Reviewer #1 (Public review):

In this manuscript, the authors combine single-nucleus RNA sequencing with spatial transcriptomics to generate a spatiotemporal atlas of mouse placental development and explore the role of glycogen trophoblast cells in fetal viability. The study integrates several computational approaches, including trajectory analysis, regulatory network inference, and spatial mapping, together with histology and glycogen measurements. Based on these analyses, the authors propose that glycogen trophoblast cells provide metabolic support that is important for maintaining placental function and fetal survival.

One of the main strengths of the study is the quality and scope of the dataset. The integration of snRNA-seq with Stereo-seq spatial transcriptomics provides a detailed view of placental organization across regions and developmental stages. This type of combined spatial and transcriptional analysis is still relatively rare in placental biology and represents an important contribution to the field. The atlas itself will likely be a valuable resource for future studies.

Another strength is the effort to connect transcriptional findings with tissue-level validation. The glycogen staining and biochemical measurements support the interpretation that glycogen trophoblast cells contribute to placental metabolic function. The spatial analyses identifying macrophage accumulation in the labyrinth region of mutant placentas are also interesting and illustrate how spatial approaches can reveal microenvironmental changes that are difficult to detect otherwise.

The main limitation of the study is that the conclusion that glycogen cells are essential mediators of metabolic support for fetal viability remains partly indirect. The transcriptomic and spatial data strongly suggest a role for these cells, but it is still difficult to determine whether glycogen cell dysfunction is the primary cause of fetal lethality or a consequence of broader placental abnormalities. Clarifying this point would strengthen the central message of the paper.

Similarly, the macrophage accumulation observed in the labyrinth appears consistent with a response to tissue stress or injury, but its relationship to glycogen cell function is not fully explained. A clearer discussion of whether this represents a primary mechanism or a secondary effect would improve the interpretation.

Overall, this is a strong dataset and a useful spatial atlas of placental development. The study provides convincing descriptive insight into glycogen trophoblast biology, and with some clarification of the mechanistic conclusions, the manuscript will be even stronger.

Reviewer #2 (Public review):

This manuscript constructs a spatiotemporal transcriptomic atlas (STAMP) of the mouse placenta from E9.5-E18.5 by integrating Stereo-seq and snRNA-seq, and identifies two glycogen trophoblast cell (GC) subtypes (GC-1 and GC-2), a spatial transition from the junctional zone (JZ) to the decidua, and metabolic defects in Ano6-null placentas including GC persistence, glycogen accumulation, reduced glycogenolysis metabolites, and partial rescue by maternal glucose supplementation. The breadth of the dataset and the integration of atlas construction with PAS/TEM/LC-MS analyses are impressive, and the study has the potential to provide a valuable resource for the placental biology community.

However, in its current form, the central claim that "GC-mediated metabolic support is essential/indispensable for fetal viability" is not sufficiently disentangled from the complex phenotype of a global Ano6 knockout model. In addition, the stage-level biological replication in the atlas and the claim of "single-cell resolution" require more careful presentation. Therefore, while the study is interesting and potentially impactful, substantial revisions are required, particularly to recalibrate the strength of the conclusions and causal interpretations.

Major comments

(1) The most significant concern is that the manuscript overinterprets the phenotype observed in a global Ano6 knockout as direct evidence that GC glycogen metabolism is essential for fetal viability. The authors themselves report multiple severe placental abnormalities in the knockout, including reduced placental size and weight, structural defects in the labyrinth, impaired vascularization, and accumulation of abnormal regions. Previous studies cited in the manuscript also indicate that Ano6 deficiency leads to defects in syncytiotrophoblast formation, impaired maternofetal exchange, and perinatal lethality.

In this context, the current data support an association between GC metabolic defects and fetal lethality, but do not establish that GC glycogen metabolism is the primary causal driver. The conclusion should therefore be moderated (e.g., "contributes to" rather than "is essential for"), unless additional placenta-specific or GC-specific functional validation is provided.

(2) Maternal glucose supplementation is an interesting functional experiment, but in its current form, it provides supportive rather than definitive mechanistic evidence. While survival improves (from ~3% to ~10%), the rescue remains partial. Moreover, the readouts are largely limited to metabolite restoration (glucose, G1P, G6P) in the placenta and fetal liver.

To support a stronger causal claim, the authors should assess whether glucose supplementation also rescues: placental morphology (especially labyrinth structure), GC number and PAS staining, ultrastructural glycogen features (TEM), fetal growth and developmental outcomes.

(3) The atlas is constructed from nine placentas across developmental stages, suggesting limited biological replication per stage. It remains unclear how robust the observed temporal trends are to litter effects, sex differences, or sectioning variability.

Furthermore, the "single-cell resolution" is not directly measured but inferred via image segmentation and reference-based mapping (e.g., TACCO). This should be more explicitly stated, as it represents computational inference rather than direct single-cell measurement.

The authors should:<br /> - clearly report biological replicates per stage (including litter and sex),<br /> - demonstrate reproducibility of key patterns across independent samples,<br /> - refine the wording to reflect segmentation- and reference-based single-cell inference.

(4) The proposed developmental trajectory (JZ progenitor → GC precursor → GC-1 → GC-2) and the claim of GC migration from JZ to decidua are based on spatial distribution and computational trajectory analyses (Monocle, CytoTRACE).

While this is a compelling model, it remains inferential. The language throughout the manuscript should be softened (e.g., "consistent with spatial transition" rather than "migration"). Ideally, additional experimental validation, such as stage-resolved RNAscope/immunostaining quantification or lineage tracing, would strengthen this claim.

(5) The manuscript concludes that ANO6 deficiency leads to impaired glycogen utilization, based primarily on the observation that differentiation markers and glycogenolytic enzyme transcripts are unchanged.

However, this demonstrates what is not altered rather than what is mechanistically responsible for the defect. A more direct mechanistic link is needed, such as changes in enzyme activity, altered intracellular localization, effects on ion homeostasis or membrane biology.

(6) The statistical framework requires clarification. Several analyses use n = 4-8 placentas or "independent experiments," but it is unclear whether these represent independent litters or multiple samples from the same dam.

Given the risk of pseudoreplication in placental studies, the authors should define whether n refers to placentas or litters, report the number of dams per genotype, and ensure appropriate statistical treatment (e.g., litter-based analysis or mixed-effects models).

Reviewer #1 (Public review):

Summary:

The authors present a new autofocusing method, LUNA (Locking Under Nanoscale Accuracy), designed to overcome severe focus drift, a major challenge in long-term time-lapse microscopy. Using this method, they address a fundamental question in bacterial cold shock response: whether cells halt growth and division following an abrupt temperature downshift. Through single-cell analysis, the authors uncover a multi-phase adaptation process with distinct growth deceleration dynamics, and show that bacterial cells adapt to cold shock in a largely uniform manner across the population. Overall, this work provides new insights into the bacterial cold shock response at the single-cell level, extending beyond what can be inferred from population-level measurements.

Strengths:

(1) The LUNA method shows improved performance compared to existing autofocusing systems, achieving nanoscale precision over a large focusing range. Its focusing speed is sufficient for the experiments presented, with potential for further improvement through faster motors and optimized control algorithms, suggesting broad applicability. Theoretical simulations and experimental validation together provide strong support for the method's robustness.

(2) Using LUNA, the authors address a long-standing question in bacterial physiology: whether cells arrest growth and division during the acclimation phase following cold shock. Single-cell analyses across the full course of cold adaptation reveal features that are obscured in bulk-culture studies. Cells continue to grow and divide at reduced rates while maintaining cell size regulation, and exhibit a three-phase adaptation program with distinct growth dynamics. This response appears uniform across the population, with no evidence for bet-hedging. Overall, the experiments are well designed, and the analyses are solid and support the authors' conclusions.

(3) The authors further propose a model describing how population-level optical density (OD) depends on cell dry mass density, volume, and concentration. Following cold shock, cells grow more slowly and exhibit smaller sizes, explaining the apparently unchanged OD. This model provides a valuable conceptual framework for interpreting OD-based growth measurements, a widely used method in microbiology, and will be of broad interest to the field.

Weaknesses:

No major weaknesses identified.

Comments on revisions:

The authors have thoroughly addressed all of my questions. I thank them for their clear clarifications and thoughtful revisions, and I greatly appreciate their efforts in improving the manuscript.

Reviewer #2 (Public review):

Summary:

This study presents LUNA, an autofocus method that compensates for focus drift during rapid temperature changes. Using this approach, the authors show that E. coli cells continue to grow and divide during cold shock, revealing a coordinated, multi-phase adaptation process that could not be deduced from traditional population measurements. They propose a scattering-theory-based model that reconciles the paradox between growth differences of the bacteria at the single-cell level vs population level.

Strengths:

(1) The LUNA approach is pretty creative, turning coma aberration from what is normally a nuisance into an exploit. LUNA enabled long-term single-cell imaging during rapid temperature downshifts.

(2) The authors show that the long-assumed growth arrest during cold shock from population-level measurements is misleading. At the single-cell level, bacteria do not stop growing or dividing but undergo a continuous, three-phase adaptation process. Importantly, this behavior is highly synchronized across the population and not based on bet-hedging.

(3) Finally, the authors propose a model to resolve a long-standing paradox between single-cell vs population behavior: if cells keep growing, why does optical density (OD) of the culture stop increasing? Using light-scattering theory, they show that OD depends not only on cell number but also on cell volume, which decreases after cold shock. As a result, OD can remain flat, or even decrease, despite continued biomass accumulation. This demonstrates that OD is not a reliable proxy for growth under non-steady conditions.

Weaknesses:

(1) While the authors theoretically explain the advantages of LUNA over existing autofocus methods, it is unclear whether practical head-to-head comparisons have been performed, apart from the comparison to Nikon PFS shown in Video S1. As written, the manuscript gives the impression that only LUNA can solve this problem, but such a claim would require more systematic and rigorous benchmarking against alternative approaches.

(2) No mutants/inhibitors used to test and challenge the proposed model.

(3) Cells display a high degree of synchronization, but they are grown in confined microfluidic channels under highly uniform conditions. It is unclear to what extent this synchrony reflects intrinsic biology versus effects imposed by the microfluidic environment.

(4) To further test and generalize the model, it would be informative to also examine bacterial responses at intermediate temperatures rather than focusing primarily on a single cold-shock condition.

Comments on revisions:

The authors have addressed my comments in their response, but have chosen not to incorporate most of them into the manuscript. Readers may refer to the peer review section for further details.

Reviewer #1 (Public review):

Summary:

The manuscript, titled Hippocampal Single-Cell RNA Atlas of Chronic Methamphetamine Abuse-Induced Cognitive Decline in Mice, focuses on single-cell RNA sequencing (scRNA-seq) analysis following chronic methamphetamine (METH) treatment in mice. The authors propose two hypotheses: (1) METH induces neuroinflammation involving T and NKT cells, and (2) METH alters neuronal stem cell differentiation.

Strengths:

The authors provide a substantial dataset with numerous replicates, offering valuable resources to the research community.

Weaknesses:

Concerns remain regarding the interpretation of the data and the appropriateness of the statistical analyses.

Although the authors provided detailed responses to the reviewer's concerns, I am still concerned that several key issues have not yet been fully addressed in the revised manuscript.

First, in Figure 5, the authors state that neural stem cells (NSCs) preferentially differentiate into astrocytes rather than neuroblasts following METH treatment. However, based on the presented trajectories, it is difficult to visually confirm differences in the relative proportions of astrocyte versus neuroblast differentiation between the control and METH-treated conditions. The current figures do not provide a quantitative or clearly interpretable comparison of lineage allocation that would support this conclusion.

Moreover, in Figures 5C and 5F, the inferred pseudotime trajectories differ both the starting cell populations and the intermediate and terminal cell identities. As a result, the trajectories are not directly comparable between the control and METH conditions. Under these circumstances, it is inappropriate to interpret gene expression changes as occurring along equivalent differentiation paths, and the current analysis does not convincingly support the stated conclusions regarding altered NSC differentiation.

If the authors intend to claim differential gene expression associated with altered differentiation trajectories, the analysis should at minimum present the expression of the same set of genes (e.g., Bsg, Ccl4, Fos, Sox11, Flt1, Hspb1, Igfbp7, and Tmsb10) plotted along a matched trajectory (for example, NSC-to-astrocyte or NSC-to-neuroblast lineages) in both control and METH-treated samples, so that readers can directly compare expression dynamics across conditions.

In addition, several statements throughout the manuscript describing changes in cell-type proportions are not supported by corresponding statistical analyses. For example, in Figure 2C (around line 430), the authors report changes in cell proportions of ~0.1% or 2-3%. Without appropriate statistical testing, it is unclear whether such marginal differences are biologically meaningful or reproducible. The authors should either provide statistical testing (e.g., sample-level proportion analysis with p-values or confidence intervals) or revise the text to describe these findings as descriptive rather than significant changes.

Finally, the reported decrease in astrocyte proportion following METH exposure (from 6.6% to 5.5%), together with the lack of reported changes in neuroblast proportions, appears inconsistent with the trajectory-based conclusion that NSCs preferentially differentiate into astrocytes in METH-treated mice. This apparent discrepancy should be clarified or the conclusions appropriately tempered.

Reviewer #1 (Public review):

Summary:

This study combined high-field fMRI with computational modelling (including a Bayesian population receptive field [pRF] model and functional gradient analysis) in humans to demonstrate that the architecture of the corpus callosum (CC) and its interhemispheric connections is organized into parallel ipsilateral and contralateral streams, rather than functioning as a mixed integration of inputs from both hemispheres. The human findings were validated through preclinical experiments in mice using viral axonal tracing, which revealed a non-overlapping laminar arrangement of axons carrying left and right visual field information.

These results suggest that the CC operates as a set of parallel, segregated pathways, with each stream independently conveying information from one side of the visual field. This organization preserves the spatial origin of visual signals within the white matter. Although the overall concept of interhemispheric parallel pathways is not entirely unexpected, this refined understanding of callosal organization provides important scientific and clinical insights in relation to pathway-specific perturbations and in neurological disorders.

Strengths:

The manuscript is well written, the methodology is sound, and the analyses are carefully conducted. I particularly appreciate the effort to integrate functional and structural approaches and to validate the human neuroimaging findings with more sensitive preclinical techniques, such as viral tracing.

Weaknesses:

Several points require clarification to allow a more complete interpretation of the results. In addition, some further analyses are necessary to fully substantiate the claims made in the manuscript. These are detailed below

Comment 1:

BOLD signals in white matter remain a matter of debate, although this is not the central focus of the present study. Nevertheless, it is important to establish whether the underlying data have sufficient tSNR to support robust pRF estimation in white matter. In Figure 1, the EV appears relatively robust; however, it seems that only the best-fitting examples are shown. In contrast, the group-average EV reported in Figure 2, and the individual maps in the Supplementary Information indicate very low EV values, typically below 5%. In conventional fMRI analyses, thresholds of approximately 15-20% EV are often applied to exclude poor fits that may bias pRF parameter estimates. It appears that no such threshold was applied here. Interestingly, in Figure S6, the average EV for dual pRF models appears to be approximately 17%. Do dual and triple pRF models systematically produce higher EV compared to single pRF models? Additionally, Figure 2 suggests the presence of baseline activation that is captured by the model. Could this be related to a delayed or altered hemodynamic response function (HRF) in white matter? Clarification would be helpful. To better assess the robustness of the reported findings, the authors should provide quantitative measures of tSNR within the white matter tracts where the pRF model was fitted. Furthermore, a plot showing the average BOLD signal during visual stimulation versus baseline in those tracts would greatly strengthen confidence in the signal quality.

Although the reported linear relationship between pRF size and eccentricity, as well as the test-retest reliability analyses, suggest the presence of consistent receptive field estimates, these analyses are based on distributions and may lack the sensitivity required to differentiate single, dual, and triple pRF models. Moreover, the pRF estimates within the FMA appear noisy, particularly at the individual level (Figure S4), making it difficult to clearly dissociate information originating from the left and right hemifields.

Comment 2.1:

The Bayesian modelling approach is interesting and robust. However, as I understand it, the authors must specify a priori the number of pRFs to be estimated. This introduces a strong assumption about the expected underlying receptive field structure. An alternative Bayesian approach, such as micro-probing (Carvalho et al., 2020), does not require prior assumptions regarding the number or shape of pRFs. Instead, it estimates receptive field profiles in a more data-driven manner and provides a direct visualization of the pRF structure. Implementing such an approach, or at least comparing it with the current modelling strategy, could yield more reliable and potentially less biased estimates of multiple pRFs, particularly in white matter where signal quality is limited.

Comment 2.2:

Some clarifications regarding the pRF model are needed: in the Methods section, the authors mention the use of a Difference-of-Gaussians (DoG) model. However, it appears from the Results that the analyses were performed using a single-Gaussian model. Additionally, in Section 5.6, the authors state that six different pRF models were tested. Which specific models were included in this comparison? A clear description of each model, along with justification for the final model selection criteria, would help better understand the study

Comment 3:

Throughout the manuscript, the authors repeatedly refer to laminar-specific findings. However, the reported functional resolution of 1.6 mm isotropic is insufficient to reliably resolve cortical layers. Given this limitation, the laminar interpretations appear overstated. For example, in the Discussion section titled "Integrating White Matter with Laminar-Resolved Function", the authors state: "The combination of anatomically segregated white matter pathways with functionally specific cortical laminae presents a powerful synergy for human brain circuit research." Given the spatial resolution of the functional data, how are laminar-specific functional claims justified?

Similarly, the authors suggest that: "It becomes possible to assess not just if the CC is damaged, but precisely which directional pathways are compromised-either the pathways projecting from the lesioned hemisphere, or those projecting to the other, or both." It is unclear to me how the current methodology uniquely enables this level of directional specificity, and whether this was not already feasible using existing structural and diffusion-based approaches. The authors should clarify what is genuinely novel in this study.

Comment 4:

In the Discussion, the authors state: "These findings fundamentally reframe our understanding of interhemispheric communication, moving beyond static connectivity to reveal a dynamic, directionally specific highway where spatial location encodes the origin of information. This framework provides a novel blueprint for decoding directional information flow in the living human brain." Based on the analyses presented, it is unclear how the findings of this study demonstrate dynamic connectivity or true directional specificity. The reported results appear to characterize spatial organization and segregation of callosal pathways, but they do not measure the directionality of information flow, temporal dynamics, or causal directionality between hemispheres. To substantiate claims regarding dynamic or directional communication, additional analyses, such as connective field model (Haak et al.2013), effective connectivity modelling, time-resolved approaches, or perturbation-based methods (neuromodulation) would be required. As currently presented, the findings seem to support structural and functional segregation rather than dynamic or directionally resolved interhemispheric information transfer. The authors should either provide stronger evidence for these claims or moderate them.

Comment 5:

I agree with the authors that pooling of information across hemispheres represents a plausible explanation for the presence of dual pRFs. As discussed in the manuscript, such an effect would be expected to predominantly affect pRFs located near the vertical meridian. However, Figures S6C and S6D do not appear to demonstrate that bilateral pRFs are preferentially located along the vertical meridian.

Reviewer #2 (Public review):

Summary:

The manuscript proposes a "parallel wires" architecture for the visual corpus callosum, suggesting that contralateral and ipsilateral visual streams remain spatially segregated into distinct anatomical channels. The authors use a cross-species approach, combining Bayesian population receptive field (pRF) modeling in humans with dual-color viral tracing in mice. The analysis of the publicly available human fMRI dataset indicates a 92% probability of single-hemifield representation, arguing for functional segregation. The mouse mesoscale tracing data support the idea of anatomical parallel wires by displaying dorso-ventral segregation of callosal axons post-midline crossing.

Strengths:

The primary strength of this study is its cross-species integration. Observing that functional segregation in humans is mirrored by specific anatomical pathways in the mouse provides a convincing, multimodal argument for the "parallel wires" hypothesis. The data is generally well-presented, and the Bayesian modeling of the human data is a robust methodological choice.

Weaknesses:

There are weaknesses in the description, presentation, and methodological details of the mouse tracing data. First, the authors must provide detailed information regarding spectral unmixing, intensity normalization, and threshold-sensitivity analyses. These factors are critical as they directly influence the Dice and Jaccard overlap estimates that underpin the study's primary conclusions. Second, it is unclear which cortical layers have been virally labelled as there is no quantification of the spatial extent of the injection site, and there is ambiguity regarding the dorso-ventral stereotaxic coordinates.

Reviewer #3 (Public review):

Summary:

This manuscript describes a study into the functional organization of the forceps major (FMA). The authors present a Bayesian population receptive field (pRF) analysis of group-averaged HCP fMRI retinotopic mapping data, focusing on voxels within the FMA. This is unconventional because pRF modelling is usually limited to gray matter voxels, where synaptic activity underlying neural computation is the highest. Nevertheless, some previous work suggests that meaningful fMRI signals can also be gleaned from white matter voxels, where the signals are thought to reflect metabolic activity from action potentials that travel along axons. However, these signals are generally much noisier, and possible confounding effects due to partial voluming, draining veins, and different hemodynamics must be carefully ruled out. Based on the Bayesian pRF analysis, the authors claim evidence of segregated contralateral and ipsilateral representations of the visual field in the FMA. Anatomical tract tracing based on HCP diffusion MRI data from seeds identified using the pRF analysis further suggests that these representations are underpinned by separate fiber bundles, which also appear to be consistent with the results of viral tracing in mice. The results of this study could mean an important step forward in understanding transcallosal signaling.

Strengths:

The study treads uncharted territory, leveraging multiple data modalities across species and advanced analytical approaches.

Weaknesses:

The study does not address potential confounds related to BOLD imaging in white matter structures. If the fMRI results can be explained based on neighboring grey matter responses, the evidence that remains is limited to an apparent anatomical segregation of white matter bundles that appear to be present in both mice and humans.

Further details are also missing regarding the Bayesian pRF approach, including the priors used for the pRF model. These are important as they will dominate the estimates when the data are very noisy, and the authors have adopted unconventional, more complex pRF models compared with earlier work employing Bayesian pRF analyses.

It appears that the authors have not applied any statistical thresholding to ensure that only good-quality model fits are entered into subsequent analyses (i.e., the reported probabilities pertain to model comparisons, not goodness of fit). From Figure 2, it appears that the majority of the FMA voxels, barring those adjacent to visual gray matter, do not exhibit more than a few percentage points of explained variance (EV). In fact, a common threshold is >15% EV, but it looks like none of the FMA voxels exceed this threshold.

Reviewer #1 (Public review):

Summary:

The manuscript entitled "Autonomic reflex plasticity associates with time-dependent SUDEP susceptibility in a murine model with hyperactive stress circuits" by Dr. Saunders and colleagues combined a traditional mouse model of SUDEP, ventral intrahippocampal kainite (vIHKA) injection, with a genetic model of chronic hyperactivity of central corticotropin-releasing hormone (CRH) neurons (Kcc2/Crh) that further increases the risk of SUDEP in the weeks following seizure.

Strengths:

Their results show during spontaneous seizures Kcc2/Crh mice had more pronounced reflex-like ictal bradycardias compared to WT controls that notably occurred prior (~10 sec) to seizure termination and had greater autonomic disturbances compared to WT controls, including a pronounced serotonin-mediated Bezold Jarisch reflex. These results show chronic hyperactivity of central corticotropin-releasing hormone (CRH) neurons (Kcc2/Crh) increased autonomic disturbances and risk of SUDEP in a kainic acid model of epilepsy.

Weaknesses:

This study could be improved with a more thorough assessment of heart rate, blood pressure and breathing during and following the seizures, and in particular the fatal event. It is unclear if the bradycardias were spontaneous or a result of preceding central or obstructive apneas, oxygen desaturations, hypercapnia, arrhythmias, or other possible triggers.

Considerable prior work in the literature suggests SUDEP could be mediated, in some patients, by a burst of parasympathetic activity to the heart. Were the heart rate changes in these animals during seizures inhibited or blocked by atropine or atenolol?<br /> The injection of the 5HT agonist phenylbiguanide into the right jugular is not a selective approach for activating the Bezold Jarisch Reflex (BJR), which is caused by increased activity of intracardiac sensory neurons (generally activated with ischemia or a combination of low preload with high contractility). The results should be interpreted more cautiously, as a response to systemic administration of phenylbiguanide only.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors set out to evaluate the role of hypothalamic pituitary axis hyperactivity on cardiac and autonomic changes during epileptogenesis and following seizures in a mouse model of temporal lobe epilepsy. Epilepsy is very common. It can frequently result in death from sudden unexpected death in epilepsy, or SUDEP. SUDEP is thought to be at least in part due to seizure-related cardiac and autonomic instability. Increased stress states are well known to be comorbid with epilepsy. This comorbidity is thought to increase the risk of SUDEP. Here, the authors hypothesized that a mouse model of heightened stress in which there is hyperactivity of the CRH neurons in the hypothalamus would demonstrate exaggerated cardiac and autonomic effects of seizures and epilepsy.

Strengths:

For the chronic stress model, they employed the Kcc2/Crh mice that have a genetic deletion of the potassium chloride cotransporter in CRH neurons. They treated these mice and their wild-type littermates with intra-hippocampal kainic acid or saline, as epileptic and sham-treated animals, respectively. The assessed cardiac activity, blood pressure, baroreflex, and the Bezold-Jerisch reflex during epileptogenesis. This, in general, is an interesting study. They make some interesting and potentially important observations regarding heart rate and blood pressure in seizures and epilepsy.

Weaknesses:

Some of the conclusions may be a bit overstated as is and would benefit from more discussion and perhaps additional data.

Reviewer #1 (Public review):

In this study, Szinte et al. measured the spatial selectivity of fMRI BOLD responses while subjects viewed dynamic noise stimuli vignetted by a moving bar aperture. Subjects viewed these moving bar stimuli as they fixated at one of three screen locations. This design enabled the authors to test whether fMRI responses are better explained by a model in which stimulus location is encoded relative to the retina or relative to the screen (in other words, 'retintopic' vs. 'spatiotopic' encoding). In retinotopic encoding, the pRFs should move with the eyes. In spatiotopic encoding, the pRFs should be locked to particular screen locations, regardless of eye position. The results are unambiguous: the retinotopic model wins.

A number of prior human fMRI studies have addressed this issue, and there is an overwhelming consensus in the field that spatial encoding throughout human visual cortex (and high-level cortex) is retinotopic (during fixation). All of the results shown in the present manuscript are consistent with these earlier observations. Szinte et al. also find that the degree of retinotopic selectivity is not affected by the task or locus of spatial attention. This too has been observed in multiple prior studies.

So, while this manuscript is primarily confirmatory, the study does nonetheless provide valuable measurements at 7T with a higher signal-to-noise ratio and high spatial resolution than previous studies. The authors also apply an innovative Bayesian decoding analysis (which is beautifully documented on their webpage, with a step-by-step tutorial and ample examples). So, a major strength of this paper is the methods; this study does set a high standard and is an ideal example for a rigorous, replicable analysis pipeline and cutting-edge statistical inference.

The results focus on the spatial profile of pRFs with different eye positions. However, the main idea behind eye-position gain fields is that the amplitude of the visual responses changes with eye position. I could not find any analysis testing response amplitude as a function of eye position. In the Discussion, the authors assert: "We did not find an influence of gaze position at the level of individual voxels nor at the level of visual areas." The authors speculate that this might be because gain fields have a salt-and-pepper organization in the cortex that cancel out when pooled across a voxel. While the salt-and-pepper explanation seems like perfectly fine speculation, here they are discussing a result that isn't shown in the Results!

Several prior human fMRI studies have reported eye position gain fields in humans, suggesting that the salt-and-pepper explanation is not correct. Rather, it is likely the case that the authors did not test a sufficiently wide range of eye positions to detect a gain modulation. For example, a study from Merriam et al. (J. Neurosci, 2013), which is mysteriously not cited here, measured both the spatial selectivity of visual receptive fields AND the response amplitude at 8 different eye positions that were spaced by as much as 24 degrees of visual angle (including both vertical and horizontal changes in eye position). Under these conditions, Merriam et al. did find reliable modulation in response amplitude with changes in eye position, even though the spatial selectivity of the responses did not change. Importantly, Merriam et al. found that visual response selectivity was consistent with a retinotopic reference frame (not a spatiotopic reference frame) and that this selectivity was invariant to the attention task. Consideration of these issues suggests that the experimental design used in the current experiment may have precluded the detection of eye position gain fields. The current manuscript would be much improved by a careful consideration of this prior literature, which is so closely related to what the authors report here.

Reviewer #2 (Public review):

Summary:

This manuscript describes a study using fMRI voxel-wise receptive field modeling and Bayesian decoding to assess the reference frame (spatiotopic vs retinotopic) of visual information. Participants viewed sequences of visual stimuli that moved across different screen locations. Across different conditions, participants either fixated at the screen center and viewed stimuli drifting across the full screen (full-screen condition), or fixated at a central, left, or right fixation position while stimuli drifted across a 4-deg aperture centered on that fixation (gaze-center, gaze-left, gaze-right conditions). Within each of those conditions, participants either attended to visual changes around fixation (attend-fix) or in the stimulus bar (attend-bar). First, standard population receptive field mapping was conducted on the full-screen conditions to obtain fiducial maps for each subject. Then, a variety of different analyses were performed, testing retinotopic vs spatiotopic predictions for the gaze-left and gaze-right conditions. Across the extensive set of analyses performed, and across all ROIs tested, the results always best matched the retinotopic predictions. This was the case for both attend-fix and attend-bar conditions. The authors conclude that visual representations operate in a retinotopic reference frame throughout the visual hierarchy, necessitating a "re-orienting" of the search for visual stability mechanisms.

Strengths:

The analyses are sophisticated and thorough, and the results are convincingly in favor of retinotopic representations. The attention manipulation is carefully done. And the finding that the most informative/reliable voxels are the most retinotopic is an important novel contribution.

Weaknesses:

(1) The theoretical advance of this work is unclear, because the finding that visual representations operate in a retinotopic reference frame throughout the visual hierarchy, and regardless of the deployment of spatial attention, has already been demonstrated with fMRI pattern analysis almost 15 years ago (Golomb & Kanwisher, 2012). To be clear, the techniques used in this current study are considerably more modern and sophisticated, and the attention manipulation is much better, but the finding is the same. More importantly, it is never really explained why, from a theoretical perspective, the results might have been expected to differ. Referring to this as an open question feels like a copout. The manuscript needs to engage more with the prior findings and explain the motivation for the current study. Was there something about the prior findings that caused them to doubt the retinotopic conclusion? Did they think that the 7T resolution or alternative decoding approaches might uncover something different? Was this intended as a replication test with more sophisticated techniques?

(2) I think there are definitely some new and useful things this study has to offer, but the overall theoretical contribution needs to be better clarified and contextualized within the prior literature. I would strongly recommend revisiting things like the title (not a novel contribution of this study) and the implication that the current findings "reframe" or "reorient" the search for visual stability mechanisms away from static spatiotopic maps (the field has arguably been "reoriented" in that way for some time now, and this study is certainly not the first to suggest a reframing along these lines). The discussion section, in particular, has little to no acknowledgement that these findings and ideas have been shown before.

(3) The analyses always pit retinotopic vs spatiotopic predictions. But what if both types co-existed, just with retinotopic more predominant? I think this general idea needs some discussion, if not additional analyses. Would the analyses be sensitive enough to pick up sparse spatiotopic coding if present?

Additional questions/critiques/suggestions:

(4) For the out-of-sample predictions analysis (Figure 2):

a) The spatiotopic predictions are much worse for earlier visual regions, but don't seem so different from gaze-center or retinotopic in later areas. How much might this be driven by the fact that pRF size increases along the hierarchy, and for large pRF sizes, the retinotopic and spatiotopic predictions might not be very differentiable? Is there a way to quantify this or include a control model that is neither retinotopic nor spatiotopic?

b) It looks like in some of the regions, the retinotopic (and maybe even spatiotopic) R2 change compared to the gaze center is reliably positive. Why would this be? Is there a reason the fit should be better for the gaze right or gaze left conditions compared to the gaze center?

(5) For the fitting retinotopic and spatiotopic pRF models (Figure 3) and other voxel-specific analyses:

a) For many of the statistics, results are averaged across voxels. This makes sense. But it also seems to me that taking a simple average might obscure some of the potential advantages of this voxel-wise approach. For example, what if there are sparse spatiotopic effects that are washed out by the averaging? Perhaps some way of looking at the statistical distribution of voxels' RFIs could be worth considering?

b) Are there some spatiotopic areas in the searchlight maps? It looks like there may be some blue clusters, but these cortical map figures are really hard to resolve.

(6) For the RFI as a function of model overlap and explained variance (Figure 4):

a) I like this analysis; I find it convincing and novel. Could it be further quantified by correlating on a voxelwise basis the reliability (e.g., explained variance) vs RFI?

b) I'm intrigued by the seemingly reliable blueish (spatiotopic) cells at the bottom of the V1-V3 grids. These seem to suggest that for the voxels with less spatial relevance (overlap), there might be something spatiotopic, even for relatively informative voxels (high explained variance)?

c) On a related note, is the "spatial relevance" measure the same as, or correlated with, eccentricity? It sounds like voxels with high spatial relevance (overlap with the central 4deg aperture) are the more foveal voxels. Intuitively, foveal voxels might be expected to be more retinotopic, right? In addition to clarifying this measure, it'd be nice to see a similar plot with eccentricity on the y-axis.

(7) For the Bayesian decoding (Figure 5):

a) A benefit of the Bayesian decoding (e.g., over the earlier studies using non-Bayesian decoding of retinotopic vs spatiotopic) is the uncertainty estimates. I think these analyses are interesting and should be in the main text figures, not a supplement.

b) Instead of line plots showing the decoded (best) position using the posterior distribution STD as the error shading, could you show the actual posterior distribution as heat maps (like the cartoon in B)? Is it possible there could be a second peak (or clear absence of one) at the spatiotopic prediction location?

(8) Also note that Golomb & Kanwisher also calculated the RFI measure for similar ROIs for both of their attention conditions. It may be worth comparing.

(9) Methods:

a) Is it true that 2 of the authors were actually naïve as to the purpose of the study? Regardless, given the small number of subjects and high ratio of authors as subjects, it might be nice to confirm that the results are not driven by the author-participants.

b) I think 44ms TR is a typo?

c) Why was the order of the bar movement directions always the same? Wouldn't this make the stimuli very predictable for the subjects, which could be potentially problematic?

d) I'm also curious why the gaze conditions were all presented in separate runs, as opposed to different blocks within a run.

e) The eccentricity maps for the fiducial maps (Figure 1G) seem a bit strange to me. Shouldn't the foveal representation be centered at the occipital pole, not the lateral surface?

Reviewer #1 (Public review):

Summary:

This manuscript investigates whether newborns can use speaker identity to separate verbal memories, aiming to shed light on the earliest mechanisms of language learning and memory formation. The authors employ a well-designed experimental paradigm using functional near-infrared spectroscopy (fNIRS) to measure neural responses in newborns exposed to familiar and novel words, with careful counterbalancing and acoustic controls. Their main finding is that newborns show differential neural activation to novel versus familiar words, particularly when speaker identity changes, suggesting that even at birth, infants can use indexical cues to support memory.

Strengths:

Major strengths of the work include its innovative approach to a longstanding question in developmental science, the use of appropriate and state-of-the-art neuroimaging methods for this age group, and a thoughtful experimental design that attempts to control for order and acoustic confounds. The study addresses a significant gap in our understanding of how infants process and remember speech, and the data are presented transparently, with clear reporting of both significant and non-significant results.

A previous concern was that the recognition effect appeared restricted to a subgroup of participants. The authors clarify that the bilateral STG and left IFG effects were present in both groups - it was only the right IFG modulation that was group-dependent. This is an important distinction and is now clearer in the revised manuscript. The timing of the effect emerging in a specific testing window also appears less arbitrary given the authors' explanation that prior work guided the analytical approach, and that task difficulty was expected to determine whether recognition would appear in earlier or later test blocks.

The sample size question is handled honestly. A power analysis based on a related ANOVA study produced an implausibly small estimate of N=5-7, which the authors rightly set aside. Aligning with fNIRS neonate studies - where mean sample sizes around N=24 are standard - is defensible, and the within-subject design with mixed-model analysis does improve sensitivity relative to simpler approaches. This is now explained in the manuscript.

The episodic memory framing has been scaled back appropriately. The revised discussion is clear that the study demonstrates what-who binding - an early component of episodic-like processing - rather than mature episodic memory in the Tulvingian sense. This is a more honest characterization of what the paradigm can show, and it opens a reasonable developmental question about how the remaining components (where, when) come online over the first months and years of life.

Weaknesses

The weaknesses are largely interpretive rather than fatal to the core findings. The absence of a same-speaker interference control within the current paradigm means the causal role of speaker change cannot be established entirely from internal evidence alone - the inference relies partly on comparison with Benavides-Varela et al. (2011), which used a somewhat different design. This is a reasonable approach given the ethical and practical constraints of testing newborns, and the authors are transparent about it, but readers should keep in mind that the conclusion about speaker change as the critical variable is supported by converging evidence across studies rather than a direct within-study manipulation.

Overall, the study contributes new and meaningful data on an underexplored aspect of early speech processing: the role of the speaker as a contextual dimension in word memory. The findings, taken together with the prior literature, tell a coherent story and have real implications for theories of early language acquisition and the developmental origins of episodic-like memory. The paradigm is sound and the results are worth pursuing in larger and more controlled follow-up studies.

Reviewer #2 (Public review):

Summary

Previous studies by some of the same authors of the actual manuscript showed that healthy human newborns memorize recently learned nonsense words. They exposed neonates to a familiarization period (several minutes) when multiple repetitions of a bisyllabic word were presented, uttered by the same speaker. Then they exposed neonates to an "interference period" when newborns listened to music or the same speaker uttering a different pseudoword. Finally, neonates were exposed to a test period when infants hear the familiarized word again. Interestingly, when the interference was music, the recognition of the word remained. The word recognition of the word was measured by using the NIRS technique, which estimates the regional brain oxygenation at the scalp level. Specifically, the brain response to the word in the test was reduced, unveiling a familiarity effect, while an increase in regional brain oxygenation corresponds to the detection of a "new word" due to a novelty effect. In previous studies, music does not erase the memory traces for a word (familiarity effect), while a different word uttered by the same speaker does.

The current study aims at exploring whether and how word memory is interfered with by other speech properties, specifically the changes in the speaker, while young children can distinguish speakers by processing the speech. The author's main hypothesis anticipates that new speaker recognition would produce less interference in the familiarized word because somehow neonates "separate" the processing of both words (familiarized uttered by one speaker, and interfering word, uttered by a different speaker), memorizing both words as different auditory events.

From my point of view, this hypothesis is interesting since the results would contribute to estimate the role of the speaker in word learning and speech processing early in life.

Major strengths:

(1) New data from neonates. Exploring neonates' cognitive abilities is a big challenge, and we need more data to enrich the knowledge of the early steps of language acquisition.

(2) The study contributes new data showing the role of speaker (recognition) on word learning (word memory), a quite unexplored factor. The idea that neonates include speakers in speech processing is not new, but its role in word memory has not been evaluated before. The possible interpretation is that neonates integrate the process of the linguistic and communicative aspects of speech at this early age.

(3) The study proposes a quite novel analytic approach. The new mixed models allow exploring the brain response considering an unbalanced design. More than the loss of data, which is frequent in infants' studies, the familiarization, interference and learning processes may take place at different moments of the experiment (e.g. related to changes in behavioural states along the experiment) or expressed in different regions (e.g. related to individual variations in optodes' locations and brain anatomy).

Main weaknesses:

I did not find major weaknesses. However, I would like to have more discussion or explanation in the following points.

(1) It would be fine to report the contribution of each infant to the analysis, i.e. how many good blocks, 1 to 5 in sequence 1 and 2, were provided by each infant.

(2) Why did the factor "blocknumber" range from 0 to 4? The authors should explain what block zero means and why not 1 to 5.

(3) I may suggest intending to integrate the changes in brain activity across the 3 phases. That is, whether changes in familiarization relate to changes in the test and interference phases. For instance, in Figure 2, the brain response distinguishes between same and novel words that occurred over IFG and STG in both hemispheres. However, in the right STG there was no initial increase in the brain response, and the response for the same was higher than the one for novels in the 5th block.

(4) Similarly, it is quite amazing that the brain did not increase the activity with respect to the familiarization during the interference phase, mainly over the left hemisphere, even if both the word and speaker changed. Although the discussion considers these findings, an integrated discussion of the detection of novel words and the detection of a novel speaker over time may benefit from a greater integration of the results.

Appraisal

The authors achieved their aims, because the design and analytic approaches showed significant differences. The conclusions are based on these results. Specifically, the hypothesis that neonates would memorize words after interference, when interfered speech is pronounced by a different speaker was supported by the data, in block 2 and 5 and discussed the potential mechanisms underlying these findings, such as separate processing for different speakers, likely related to the recognition of speaker identity.

I think the discussion is well structured, although I may suggest integrating the changes into the three phases of the study. Maybe comparing with other regions, not related to speech processing.

Evaluating neonates is a challenge. Because physiology is constantly changing. For instance, in 9 minutes newborns may transit from different behavioral states and experience different physiological needs.

This study offers the opportunity to inspire looking for commonalities and individual differences when investigating early memory capacities of newborns.

Comments on revisions:

The authors provided satisfactory answers to my concerns.

I recognize that, because of technical and ethical reasons, the studies with neonates are particularly challenging, however, with a well-balanced design as the one the authors applied, even with small samples the data constitute valuable sources to advance in the field.

Neonate brain works in a particularly state of intense metabolic, functional and structural changes, which we are far to understand. Current data contribute to fill this gap in knowledge.

Reviewer #1 (Public review):

Summary

The manuscript by K.H. Lee et al. presents Spyglass, a new open-source framework for building reproducible pipelines in systems neuroscience. The framework integrates the NWB (Neurodata Without Borders) data standard with the DataJoint relational database system to organize and manage analysis workflows. It enables the construction of complete pipelines, from raw data acquisition to final figures. The authors demonstrate their capabilities through examples, including spike sorting, LFP filtering, and sharp-wave ripple (SWR) detection. Additionally, the framework supports interactive visualizations via integration with Figurl, a platform for sharing neuroscience figures online.

Strengths:

Reproducibility in data analysis remains a significant challenge within the neuroscience community, posing a barrier to scientific progress. While many journals now require authors to share their data and code upon publication, this alone does not ensure that the code will execute properly or reproduce the original results. Recognizing this gap, the authors aim to address the community's need for a robust tool to build reproducible pipelines in systems neuroscience.

Comments on revisions:

In this revised version, the authors have addressed the majority of the concerns raised in the initial review. The manuscript is clearer, the documentation and explanations have been strengthened, and several important practical issues-particularly regarding usability, terminology, and deployment-have been meaningfully improved. While the framework continues to position itself both as a flexible analysis environment and as a mechanism for freezing and preserving reproducible pipelines, the authors have clarified their rationale for maintaining this dual role. I have no additional comments at this stage.

Reviewer #2 (Public review):

Summary:

Lee et al. introduce Spyglass, an open-source Python framework designed to tackle the reproducibility crisis in systems neuroscience by integrating the Neurodata Without Borders (NWB) standard with DataJoint relational databases. The framework aims to standardize data ingestion, preprocessing, analysis pipelines, and data sharing for complex electrophysiological and behavioral experiments.

Strengths:

(1) Handling of Complex Workflows: The architectural design is pragmatic and robust. Features such as the "cyclic iteration" motif for spike-sorting curation and the "merge" motif for consolidating multiple data streams effectively handle the iterative nature of data processing without incurring database bloat.

(2) Ecosystem Integration: The revised manuscript clarifies that Spyglass acts as a community hub, explicitly detailing its integration with established tools like SpikeInterface, DeepLabCut, GhostiPy, MoSeq, and Pynapple.

(3) Pipeline Clarity & Practical Demonstration: The addition of Supplementary Figure 1, in conjunction with Figure 5, successfully maps out the complex, multi-step decoding workflow for both the UCSF and NYU datasets. Together, these figures tell a complete and compelling story of how this pipeline can be used in practice, providing much-needed visual clarity on how raw data moves through the database to generate final results.

Appraisal:

The authors have successfully achieved their aims. Spyglass is a highly functional system capable of handling the heavy lifting of data management. The revisions have significantly improved transparency regarding the tool's limitations and its onboarding process, making it a highly attractive blueprint for labs aiming to adhere to FAIR principles.

Reviewer #1 (Public review):

Summary:

The authors wanted to determine whether the set-19 gene, one of 38 SET-domain containing genes in C elegans, has a clear function in vivo with respect to lysine methylation. The question is not only whether it can modify this histone tail residue, but also what the impact of a loss of this locus is on the inheritance of repressive chromatin states.

Strengths:

The authors clearly achieved their goal, and it is convincingly shown that SET_19 is indeed a somatic cell histone methyltransferase with a striking specificity for H3K23. There is both recombinant protein work, quantitative mapping in vivo, of histone marks and transcriptional changes, and the authors rule out some other hypotheses that have been in the literature. Overall, this provides a compelling argument that SET-19 is indeed the major somatic cell HMT for this residue. Interestingly, the phenotypes are rather minimal, consistent with redundancy in the physiological roles of histone methylation, and redundancy as well in HMT function. For the most part, the data are not over-interpreted. The genetic alleles used, assuming they are confirmed, were revealing and well-documented.

Weaknesses:

The major weaknesses are easily fixed. The major weaknesses mainly reflect a slight overstatement of certain data (claiming insignificance, when it is not clear how that was determined) and claiming a bit too much about SET-32, which was independently claimed to be an H3K23 HMT. Clearly, the two SET domain enzymes are not redundant, nor is the claim that SET-32 has no role in H3K23 methylation completely convincing. Especially in germline or embryonic conditions. Finally, the imaging is not of very high quality, nor are the images fully quantitated. These points can be easily remedied.

Reviewer #2 (Public review):

Summary:

This manuscript identifies SET-19 as a somatic H3K23 methyltransferase in C. elegans, building on previous genetic evidence for a role of set-19 in H3K23me3 regulation. The authors combine quantitative mass spectrometry, western blotting, in vitro methyltransferase assays, ChIP-seq, and RNA-seq to show that loss of set-19 causes a strong reduction of H3K23me3, particularly in somatic tissues, and is associated with derepression of a subset of genes enriched for H3K23me3. They further conclude that SET-19 is dispensable for canonical feeding RNAi and for transgenerational or intergenerational inheritance of RNAi, distinguishing its function from other heterochromatin-associated methyltransferases such as SET-25, SET-32, and the H3K27 HMTs. Overall, the work adds an important piece to the H3K23 methylation pathway and tissue-specific chromatin regulation in C. elegans.

Strengths:

Very strong genetic and biochemical evidence for SET-19 as the major H3K23me3 HMT.

The mass spectrometry and western blot data convincingly demonstrate a strong reduction of H3K23me3 in two independent set-19 alleles and rescue by GFP::SET-19, which is a major strength (Figure 1, including Figure 1f).

The in vitro methyltransferase assays (Figure 2) showing robust H3K23me1/2/3 activity for SET-19 SET+CC and only modest H3K23me activity for SET-32, together with the SAM titration experiment in Figure 2C, are very informative and nicely support the conclusion that SET-19 is a high-activity H3K23 methyltransferase compared to SET-32.

The ChIP-seq analysis is central to the conclusions that H3K23me3 is enriched on chromosome arms, co-localizes with H3K9me3/H3K27me3, and is strongly reduced in set-19 mutants.

Weaknesses:

(1) The global reduction of H3K23me3 in Figure 3b,c and Figure S4c is convincing, but the correlation analysis between H3K23me3 loss and mRNA changes in Figure 3g could be strengthened. Currently, the analysis appears to focus on broad categories; it would be helpful to provide:

Representative genome browser tracks (e.g., exemplary gene coverage plots) for several genes that show clear H3K23me3 peaks in wild type, reduction in set-19, and concomitant upregulation of mRNA levels, and for a few genes that retain H3K23me3 and do not change expression. This would make the link between chromatin changes and transcriptional output more concrete.

(2) In Figure S4C, the authors note a pronounced reduction of H3K23me3 mainly on chromosome arms, but in the current data, it appears that the impact might be arm-specific (i.e., stronger reduction in one arm than the other in a chromosome), with a notable pattern at the X chromosome tip where H3K23me3 seems increased. This is potentially interesting and should be briefly commented on in the Results or Discussion, for example, whether this reflects compensatory activity of another HMT, changes in chromatin organization, or could be a technical artifact.

(3) Figure 3d suggests that some actively expressed genes can also display relatively high H3K23me3 levels, which complicates a simple model of H3K23me3 as exclusively repressive. If feasible, a limited additional analysis stratifying genes by both H3K23me3 and H3K9me3/H3K27me3 status might clarify whether these highly expressed, H3K23me3‑marked genes differ in other chromatin features.

(4) The authors argue that SET-19 primarily affects H3K23me3 and not other canonical repressive marks, based largely on mass spectrometry. It would significantly strengthen the mechanistic conclusions if the authors could assess H3K9me3 and H3K27me3 profiles in set-19 mutants, ideally by ChIP-seq or at least by focused ChIP-qPCR at a subset of loci that lose H3K23me3 and are derepressed at the RNA level. This would address whether H3K23me3 loss occurs independently of changes in other heterochromatin marks, or whether there is crosstalk.

Reviewer #2 (Public review):

Summary:

This study aims to examine the effects of the subcellular localization of the mammalian clock protein PER2 and its dedicated binding partners CRY1 and the kinase CK1. Using a combination of transient transfection and a Dox-inducible expression system, they show that CRY1 promotes nuclear retention of PER2, and that phosphorylation of PER2 by CK1 promotes cytoplasmic localization and release of CRY1. Changes in complex assembly and subcellular localization could impact the transcriptional repressive function of the CK1-PER2-CRY1 complex in the molecular clock.

Strengths:

The study establishes a system of transient transfection and Dox-inducible expression that allows for strict temporal control of the presence of fluorescently-tagged clock proteins. This is essential to conduct time-lapse microscopy studies that determine changes in the apparent subcellular localization and stability of associated clock proteins. With the potential caveats of overexpression set aside, the authors make use of good controls and supplement cell-based work with in vitro experiments where possible. The discovery that phosphorylation of PER2 by CK1 in the nucleus leads to cytoplasmic localization of PER2 and PER2-CRY1 complexes is a new finding. Moreover, the apparent dissociation of CRY1 from PER2 after CK1 phosphorylation provides a potentially new mechanism by which the repressive activity of this complex could be regulated.

Weaknesses:

Overexpression of circadian clock components, normally expressed at low levels, could disrupt the stoichiometry of native interactions, Although the authors provide a reasonable rationale for the Dox-inducible approach and use appropriate controls throughout the experiments, there is still concern that overexpression of the components of this transcriptional repressive complex far exceed the concentration of the transcription factor they regulate, and this has not been taken into consideration here. In addition, the interesting discovery that CK1 phosphorylation of PER2 leads to dissociation of CRY1 has not identified the phosphorylation site(s) responsible for this, so the mechanism by which this occurs is still unknown. Still, this study provides some interesting hypotheses regarding CK1 regulation of PER2 and CRY1 that could drive future work in the field.

Comments on latest version:

This manuscript has already undergone two rounds of review at a reputable journal, and we have been provided with the previous reviewers' comments and the authors' responses. I am satisfied with the responses and changes to the manuscript made in these previous rounds of review and don't have any further experiments to suggest that wouldn't represent significant additional work.

Reviewer #2 (Public review):

In this study, the authors investigate how increasing cognitive demand shapes activity patterns in the dorsal dentate gyrus (DG). Using a touchscreen-based TUNL task combined with TRAP/c-Fos tagging, birth-dating of adult-born granule cells (abDGCs), and chemogenetic inhibition, they show that higher task demand increases mature granule cell (mGC) recruitment and enhances suprapyramidal (SB) versus infrapyramidal (IB) blade bias. Functionally, mGC inhibition reduces overall activity and impairs performance without disrupting blade bias, whereas inhibition of {less than or equal to}7-week-old abDGCs increases mGC activity, abolishes blade bias, and impairs discrimination under high-demand conditions. These findings suggest that effective pattern separation depends not only on overall DG activity levels but also on the spatial organization of recruited ensembles.

The integration of touchscreen TUNL with temporally controlled activity tagging and birth-dated cohorts is technically strong. Quantification of SB-IB bias and radial/apical distributions adds anatomical precision beyond bulk activity measures. The comparison between mGC and abDGC inhibition is conceptually compelling and supports dissociable functional roles. Overall, the data convincingly demonstrate that increasing cognitive demand amplifies blade-biased DG recruitment and that mGCs and abDGCs differentially contribute to both behavioral performance and network organization.

However, how abDGCs are integrated into the mGC network under high cognitive demand remains unresolved. Additional experiments are needed to clarify how abDGCs shape spatial recruitment patterns and whether they directly inhibit or indirectly regulate mGC activity to maintain high performance.

Furthermore, the authors frame "high cognitive demand" as a multidimensional construct encompassing broad behavioral challenge. It would strengthen the work to delineate how local abDGC-mGC circuit interactions regulate specific task components in real time. This will require higher temporal resolution approaches, as TRAP and c-Fos labeling integrate activity over prolonged windows and primarily reflect sustained engagement rather than moment-to-moment computations.<br /> The central conclusion that dentate function depends on coordinated spatial recruitment rather than total activity magnitude is supported by the data, although mechanistic interpretations are tempered given methodological limitations.<br /> Overall, this work advances models of adult neurogenesis by emphasizing a critical-period modulatory role of abDGCs in organizing DG network activity during high-demand discrimination. The combined behavioral and circuit-level framework is likely to be influential in the field.

Comments on revisions:

None remaining.

Reviewer #1 (Public review):

The manuscript presents a compelling new in vitro system based on isogenic co-cultures of human iPSC-derived hepatocytes and macrophages, enabling the modelling of hepatic immune responses with unprecedented physiological relevance. The authors show that co-culture leads to enhanced maturation of hepatocytes and tissue-resident macrophage identity, which cannot be achieved through conditioned media alone. Using this system, they functionally validate immune-driven hepatotoxic responses to a panel of drugs and compare the system's predictive power to that of monocyte-derived macrophages. The results underscore the necessity of macrophage-hepatocyte crosstalk for accurate modelling of liver inflammation and drug toxicity in vitro. The manuscript is clearly written and addresses a key limitation in liver organoid systems: the lack of immune complexity and tissue-specific macrophage imprinting.

Strengths:

• Novelty and Relevance: The study presents a highly innovative co-culture system based on isogenic human iPSCs, addressing an unmet need in modelling immune-mediated hepatotoxicity.

• Mechanistic Insight: The reciprocal reprogramming between iHeps and iMacs, including induction of KC-specific pathways and hepatocyte maturation markers, is convincingly demonstrated.

• Functional Readouts: The application of the model to detect IL-6 responses to hepatotoxic compounds enhances its translational relevance.

Weaknesses:

The co-culture model with monocyte-derived macrophages is not fully characterised, making comparisons less informative.

Reviewer #3 (Public review):

Summary:

In this study, the authors establish a human in vitro liver model by co-culturing induced hepatocyte-like cells (iHEPs) with induced macrophages (iMACs). Through flow cytometry-based sorting of cell populations at days 3 and 7 of co-culture, followed by bulk RNA sequencing, they demonstrate that bidirectional interactions between these two cell types drive functional maturation. Specifically, the presence of iMACs accelerates the hepatic maturation program of iHEPs, while contact-dependent cues from iHEPs enhance the acquisition of Kupffer cell identity in iMACs, indicating that direct cell-cell interactions are critical for establishing tissue-resident macrophage characteristics.

Functionally, the authors show that iMAC-derived Kupffer-like cells respond to pathological stimuli by producing interleukin-6 (IL-6), a hallmark cytokine of hepatic immune activation. When exposed to a panel of clinically relevant hepatotoxic drugs, the co-culture system exhibited concentration-dependent modulation of IL-6 secretion consistent with reported drug-induced liver injury (DILI) phenotypes. Notably, this response was absent when hepatocytes were co-cultured with monocyte-derived macrophages from peripheral blood, underscoring the liver-specific phenotype and functional relevance of the iMAC-derived Kupffer-like cells. Collectively, the study proposes this co-culture platform as a more physiologically relevant model for interrogating macrophage-hepatocyte crosstalk and assessing immune-mediated hepatotoxicity in vitro.

Strengths:

A major strength of this study lies in its systematic dissection of cell-cell interactions within the co-culture system. By isolating each cell type following co-culture and performing comprehensive transcriptomic analyses, the authors provide direct evidence of bidirectional crosstalk between iMACs and iHEPs. The comparison with single-culture controls is particularly valuable, as it clearly demonstrates how co-culture enhances functional maturation and lineage-specific gene expression in both cell types. This approach allows for a more mechanistic understanding of how hepatocyte-macrophage interactions contribute to the acquisition of tissue-specific phenotypes

Weaknesses:

(1) Overreliance on bulk RNA-seq data:

The primary evidence supporting cell maturation is derived from bulk RNA sequencing, which has inherent limitations in resolving heterogeneous cellular states and functional maturation. The conclusions regarding hepatocyte maturation are based largely on increased expression of a subset of CYP genes and decreased AFP levels - markers that, while suggestive, are insufficient on their own to substantiate functional maturation. Additional phenotypic or functional assays (e.g., metabolic activity, protein-level validation) would significantly strengthen these claims.

(2) Insufficient characterization of input cell populations:

The manuscript lacks adequate validation of the cellular identities prior to co-culture. Although the authors reference previously published protocols for generating iHEPs and iMACs, it remains unclear whether the cells used in this study faithfully retain expected lineage characteristics. For example, hepatocyte preparations should be characterized by flow cytometry for ALB and AFP expression, while iMACs should be assessed for canonical macrophage markers such as CD45, CD11b, and CD14 before co-culture. Without these baseline data, it is difficult to interpret the magnitude or significance of any co-culture-induced changes.

(3) Quantitative assessment of IL-6 production is insufficient:

The analysis of drug-induced IL-6 responses is based primarily on relative changes compared to control conditions. However, percentage changes alone are inadequate to capture the biological relevance of these responses. Absolute cytokine production levels - particularly in response to LPS stimulation - should be reported and directly compared to PBMC-derived macrophages to determine whether iMAC-derived Kupffer-like cells exhibit enhanced cytokine output. Moreover, the Methods section should clearly describe how ELISA results were normalized or corrected to account for potential differences in cell number, viability, or culture conditions.

(4) Unclear mechanistic interpretation of IL-6 modulation:

The observed changes in IL-6 production upon drug treatment cannot be interpreted solely as evidence of Kupffer cell-specific functionality. For instance, IL-6 suppression by NSAIDs such as diclofenac is well known to result from altered prostaglandin synthesis due to COX inhibition, while leflunomide's effects are linked to metabolite-induced modulation of immune cell proliferation and broader cytokine networks. These mechanisms are distinct from Kupffer cell identity and may not directly reflect liver-specific macrophage function. Consequently, changes in IL-6 secretion alone - particularly without additional mechanistic evidence or analysis of other cytokines - are insufficient to conclude that co-culture with hepatocytes drives the acquisition of bona fide Kupffer cell maturity.

Reviewers comments to revised manuscript.

The authors successfully established an isogenic, iPSC-derived human liver co-culture model to investigate the role of hepatocyte-macrophage interactions in driving Kupffer cell (KC) identity and hepatocyte maturation. By utilizing a single genetic background, the authors effectively minimized the experimental variability often encountered in non-isogenic systems. A significant highlight of this work is the demonstration that direct co-culture-as opposed to conditioned media alone-is a primary driver for critical KC identity markers such as ID1 and ID3. Furthermore, the model's ability to recapitulate complex clinical IL-6 responses to known hepatotoxicants where standard models have failed underscores its potential utility for early-stage DILI screening. However, there are significant methodological concerns regarding the data analysis. While the study compares four or five distinct experimental groups (e.g., Day 0, Day 7, Day 3 co-culture, and Day 7 co-culture), the authors utilized Student's t-tests for these comparisons. This approach does not account for the multiple comparisons problem and increases the risk of Type I errors. Additionally, while IL-6 secretion is used as a primary functional readout, the individual mechanisms behind these drug responses were not explored experimentally. Finally, Pearson correlation analysis indicates that the iMacs remain poorly correlated with actual in vivo human embryonic liver macrophages, suggesting that the "imprinting" of true KC identity remains incomplete.

Reviewer #1 (Public review):

The authors previously reported that Heliconius, one genus of the Heliconiini butterflies, evolved to be efficient foragers to feed pollen of specific plants and have massively expanded mushroom bodies. Using the same image dataset, the authors segmented the central complex and associated brain regions and found that the volume of the central complex relative to the rest of brain are largely conserved across the Heliconiini butterflies. By performing immunostaining to label specific subset of neurons, the authors found several potential sites of evolutional divergence in the central complex neural circuits, including the numbers of GABAergic ellipsoid body ring neurons and the innervation patterns of Allatostatin A expressing neurons in the noduli. These neuroanatomical data will be helpful to guide the future studies to understand the evolution of the neural circuits for vector-based navigations.

Strength

The authors used sufficiently large scale of dataset from 307 individuals of 41 specifies of Heliconiini butterflies to solidify the quantitative conclusions, and present new microscopy data for fine neuroanatomical comparison of the central complex.

Weakness

(1) Although the figures display a concise summary of anatomical findings, it would be difficult for non-experts to learn from this manuscript to identify the same neuronal processes in the raw confocal stacks. It would be helpful to have instructive movies to show step by step guide for identifications of neurons of interests, segmentations and 3D visualizations (rotation) for several examples including ER neurons (to supplement texts in line 347-353) and Allatostatin A neurons.

(2) Related to (1), it was difficult for me to access if the data in Fig 7 support the author's conclusions that ER neuron number increased in Heliconius Melpomene. By my understanding, the resolution of this dataset isn't high enough to trace individual axons and therefore authors do not rule out that the portion of "ER ring neurons" in Heliconius may not innervate the ER, as stated in Line 635 "Importantly, we also found that some ER neurons bypass the ellipsoid body and give rise to dense branches within distinct layers in the fan-shaped body (ER-FB)". If they don't innervate the ellipsoid body, why are they named as "ER neurons"?

(3) Discussions around the line 577-584 requires the assumption that each ellipsoid body (EB) ring neuron typically arborise in a single microglomerulus to form largely one-to-one connection with TuBu neurons within the bulb (BU), and therefore the number of BU microglomeruli should provide an estimation of the number of ER neurons. Explain this key assumption or provide an alternative explanation.

(4) The details of antibody information are missing in the Key resource table. Instead of citing papers, list the catalogue numbers and identifier for commercially available antibodies, and describe the antigen and if they are monoclonal or polyclonal. Are antigens conserved across species?

(5) I did not understand why authors assume that foraging to feed on pollens is more difficult cognitive task than foraging to feed on nectars. Would it be possible that they are equality demanding tasks but pollen feeding allows Heliconius to pass more proteins and nucleic acids to their offsprings and therefore they can develop larger mushroom bodies?

Comments on revisions:

The authors fully addressed my concerns and significantly improved the accessibility of the manuscript.

Reviewer #2 (Public review):

Summary

In this study, Farnsworth et al. ask whether the previously established expansion of mushroom bodies in the pollen foraging Heliconius genus of Heliconiini butterflies co-evolved with adaptations in the central complex. Heliconius trap line foraging strategies to acquire pollen as a novel resource require advanced spatial memory mediated by larger mushroom bodies but the authors show that related navigation circuits in the central complex are highly conserved across the Heliconiini tribe, with a few interesting exceptions. Using general immunohistochemical stains and 3D reconstruction, the authors compared volumes of central complex regions and unlike the mushroom bodies, there was no evidence of expansion associated with pollen feeding. However, a second dataset of neuromodulator and neuropeptide antibody labeling reveal more subtle differences between pollen and non-pollen foragers and highlight sub-circuits that may mediate species-specific differences in behavior. Specifically, the authors found an expansion of GABAergic ER neurons projecting to the fan shaped body in Heliconius which may enhance their ability to path-integrate. They also found differences in Allatostatin A immunoreactivity, particularly increased expression in the noduli associated with pollen feeding. These differences warrant closer examination in future studies to determine their functional implication on navigation and foraging behaviors.

Strengths

The authors leveraged a large morphological data set from the Heliconiini to achieve excellent phylogenetic coverage across the tribe with 41 species represented. Their high quality histology resolves anatomical details to the level of specific, identifiable tracts and cell body clusters. They revealed differences at a circuit level, which would not be obvious from a volumetric comparison. The discussion of these adaptations in the context of central complex models is useful for generating new hypotheses for future studies on the function of ER-FB neurons and the role of Allatostatin A modulation in navigation.<br /> The conclusions drawn in this paper are measured and supported by rigorous statistics and evidence from micrographs.

Weaknesses

The majority of results in this study do not reveal adaptations in the central complex associated with pollen foraging. However, reporting conserved traits is useful and illustrates where developmental or functional constraints may be acting. The authors have now revised the introduction to set up two alternate hypotheses..

In the main text, the authors describe differences in GABAergic ER neurons between H. melpomene and an outgroup species, with additional images from other species in Figure S4. Quantification of ER cells in these other species would strengthen the claim that these are increased in Heliconius and not just the focal species, but this may hopefully be pursued in future studies.

Comments on revisions:

I am satisfied with the authors' revisions.

Reviewer #1 (Public review):

The author presents a new method for microRNA target prediction based on (1) a publicly available pretrained Sentence-BERT language model that the author fine-tunes using MeSH information and (2) downstream classification analysis for microRNA target prediction. In particular, the author's approach, named "miRTarDS", attempts to solve the microRNA target prediction problem by utilizing disease information (i.e., semantic similarity scores) from their language model. The author then compares the prediction performance with other sequence- and disease-based methods and attempts to show that miRTarDS is superior or at least comparable to existing methods. The author's general approach to this microRNA target prediction problem seems promising, but fails to demonstrate concrete computational evidence that miRTarDS outperforms other existing methods. The author's claim that disease information-based language models are sufficient is unfounded. The manuscript requires substantial rewriting and reorganization for readers with a strong background in biomedical research.

A major issue related to the author's claim of computational advance of miRTarDS: The author does not introduce existing biomedical-specific language models, and does not compare them against miRTarDS's fine-tuned model. The performance of miRTarDS is largely dependent on the semantic embedding of disease terms. The author shows in Figure 5 that MeSH-based fine-tuning leads to a substantial improvement in MeSH-based correlation compared to the publicly available pretrained SBERT model "multi-qa-MiniLM-L6-cos-v1" without sacrificing a large amount of BIOSSES-based correlation. However, the author does not compare the performance of MeSH- and BIOSSES-based correlation with existing language models such as ChatGPT, BioBERT, PubMedBERT, and more. Also, the substantial improvement in MeSH-based correlation is a mere indication that the MeSH-based fine-tuning strategy was reasonable and not that it's superior to the publicly available pretrained SBERT model "multi-qa-MiniLM-L6-cos-v1".

Another major issue is in the author's claim that disease-information from miRTarDS's language model is "sufficient" for accurate microRNA target prediction. Available microRNA targets with experimental evidence are largely biased for those with disease implications that have been reported in the biomedical literature. It's possible that their language model is biased by existing literature that has also been used to build microRNA target databases. Therefore, it is important that the author provides strong evidence that excludes the possibility of data leakage circularity. Similar concerns are prevalent across the manuscript, and so I highly recommend that the author reassess the evaluation frameworks and account for inflated performance, biased conclusions, and self-confirming results.

Last but not least, the manuscript requires a deeper and careful description and computational encoding of microRNA biology. I'd advise the author to include an expert in microRNA biology to improve the quality of this manuscript. For example, the author uses the pre-miRNA notation and replaces the mature miRNA notation to maintain computational encoding consistency across databases. However, the mature microRNA notation "the '-3p' or '-5p' is critical as the 3p and 5p mature microRNAs have different seed sequences and thus different mRNA targets. The 3p mature microRNA would most likely not target an mRNA targeted by the 5p mature microRNA.

Reviewer #2 (Public review):

Summary:

This study introduces a novel knowledge-driven approach, miRTarDS, which enables microRNA-Target Interaction (MTI) prediction by leveraging the disease association degree between a miRNA and its target gene. The core hypothesis is that this single feature is sufficient to distinguish experimentally validated functional MTIs from computationally predicted MTIs in a binary classification setting. To quantify the disease association, the authors fine-tuned a Sentence-BERT (SBERT) model to generate embeddings of disease descriptions and compute their semantic similarity. Using only this disease association feature, miRTarDS achieved an F1 score of 0.88 on the test set.

Strengths:

The primary strength is the innovative use of the disease association degree as an independent feature for MTI classification. In addition, this study successfully adapts and fine-tunes the Sentence-BERT (SBERT) model to quantify the semantic similarity between biomedical texts (disease descriptions). This approach establishes a critical pathway for integrating powerful language models and the vast growth in clinical/disease data into biochemical discovery, like MTI prediction.

Weaknesses:

The main weakness lies in its definition of the ground-truth dataset, which serves as a foundation for methodological evaluation. The study defines the Negative Set as computationally predicted MTIs that lack experimental evidence. However, the absence of experimental validation does not equate to non-functionality. Similarly, the miRAW sets are classified by whether the target and miRNA could form a stable duplex structure according to RNA structure prediction. This definition is biologically irrelevant, as duplex stability does not fully encapsulate the complex in vivo binding of miRNAs within the AGO protein complex.

Reviewer #1 (Public review):

Summary:

This study examines how traumatic brain injury (TBI) alters hippocampal network dynamics and single-unit activity in awake, behaving rats. Using laminar recordings, the authors report reductions in theta power, theta-gamma phase-amplitude coupling, and spike-field entrainment, alongside impairments in spatial memory performance.

Strengths of the study include the use of high-density laminar electrodes to localize activity across hippocampal layers and the integration of electrophysiological and behavioral measures. Analyses that consider behavioral state and account for broadband power changes improve confidence in the interpretation of oscillatory effects. Additional controls suggest that the observed differences are unlikely to be explained by gross motor or motivational deficits. The reported relationships between theta amplitude, phase-amplitude coupling, and spike entrainment provide useful insight into how network coordination is disrupted following injury.

There are a few minor weaknesses. The analyses of single-unit activity across environments are relatively limited, and more comprehensive approaches to characterizing spatial coding would strengthen conclusions about how TBI impacts hippocampal representations. The behavioral assessment relies primarily on a single task, which constrains the interpretation of the cognitive deficits. In addition, the relatively small number of animals is a limitation, although this is partially mitigated by the number of recorded units and the consistency of effects across measures.

Overall, this work provides a careful characterization of hippocampal circuit dysfunction following TBI and contributes to understanding how disruptions in oscillatory coordination and spike timing may relate to cognitive impairment.

Comments on revisions:

The authors have adequately addressed all of my concerns.

Reviewer #3 (Public review):

Summary:

In this study, authors studied the effects of traumatic brain injury created by LFPI procedure on the CA1 at network level. The major findings in this study seem to be that the TBI reduces theta and gamma powers in CA1, reduces phase amplitude coupling in between theta and gamma bands as well as disrupts the gamma entrainment of interneurons. I think the authors have made some important discoveries that could help advance the understanding of TBI effects at physiological level, however, more investigations into deciphering the relationship of the behavioral and brain states to the observed effects would help clarify the interpretations for the readers.

Strengths:

The authors in this study were able to combine behavioral verification of the TBI model with the laminar electrophysiological recordings of CA1 region to bring forward network level anomalies such as the temporal coordination of network level oscillations as well as in the firing of the interneurons. Indeed, it seems that the findings may serve future studies to functionally better understand and/or refine the therapies for the TBI.

Weaknesses:

Discoveries made in the paper and their broad interpretations can be helped with further characterization and comparison among the brain and behavioral states both during immobility and movement. The impact of brain injury in several parts of the brain can alter brain wide LFP and/or behavior. The altered behavior and/or LFP patterns might then lead to reduced spiking and unreliable LFP oscillations in the hippocampus. Hence, claims made in abstract such as "These results reveal deficits in information encoding and retrieval schemes essential to cognition that likely underlie TBI-associated learning and memory impairments, and elucidate potential targets for future neuromodulation therapies" does not have enough evidence in testing whether the disruptions were information encoding and retrieval related or due to sensory-motor and/or behavioral deficits that could also occur during TBI.

Movement velocity is already known to be correlated to the entrainment of spikes with the theta rhythm and also in some cases with the gamma oscillations. So, it is of importance to disentangle the differences in behavioral variables and the observed effects. As an example, the author's claims of disrupted temporal coding (as shown in the graphical abstract) might have suffered from these confounds. The observed results of reduced entrainment might on one hand be due to the decreased LFP power (induced by injury in different brain areas) resulting in altered behavior and/or the unreliable oscillations of the LFP bands such as theta and gamma, rather than memory encoding and retrieval related disruption of spikes synchrony to the rhythms, while on the other hand they may simply be due to reduced excitability in the neurons particularly in the behavioral and brain state in which the effects were observed, rather than disrupted temporal code. Hence, further investigations into dissociating these factors could help readers mechanistically understand the interesting results observed by the authors.

Comments on revisions:

The authors have substantially improved the manuscript in response to the previous reviews. In particular, the revisions addressing the issue of behavioral deficits that could be caused due to the TBI, which were surprisingly not present (if anything minimal) in the injured rats, have strengthened the study and improved the support for the main conclusions. Overall, the manuscript is now clearer and more rigorous. Authors have also addressed all the minor points raised in the study. As a result, the study is now solid, with the major findings broadly supported by the data.

Reviewer #1 (Public review):

Summary:

This study utilizes fNIRS to investigate the effects of undernutrition on functional connectivity patterns in infants from a rural population in Gambia. fNIRS resting-state data recording spanned ages 5 to 24 months, while growth measures were collected from birth to 24 months. Additionally, executive functioning tasks were administered at 3 or 5 years of age. The results show an increase in left and right frontal-middle and right frontal-posterior connections with age and, contrary to previous findings in high-income countries, a decrease in frontal interhemispheric connectivity. Restricted growth during the first months of life was associated with stronger frontal interhemispheric connectivity and weaker right frontal-posterior connectivity at 24 months of age. Additionally, the study describes some connectivity patterns, including stronger frontal interhemispheric connectivity, which is associated with better cognitive flexibility at preschool age.

Strengths:

- The study analyses longitudinal data from a large cohort (n = 204) of infants living in a rural area of Gambia. This already represents a large sample for most infant studies, and it is impressive, considering it was collected outside the lab in a population that is underrepresented in the literature. The research question regarding the effect of early nutritional deficiency on brain development is highly relevant and may highlight the importance of early interventions. The study may also encourage further research on different underrepresented infant populations (i.e., infants not residing in Western high-income countries) or in settings where fMRI is not feasible.

- The preprocessing and analysis steps are carefully described, which is very welcome in the fNIRS field, where well-defined standards for preprocessing and analysis are still lacking.

Weaknesses:

- The study provides a solid description of the functional connectivity changes in the first two years of life at the group level and investigates how restricted growth influences connectivity patterns at 24 months. However, it does not explore the links between adverse situations and developmental trajectories for functional connectivity. Given the longitudinal nature of the dataset, future work should expand the analysis using more sophisticated tools to link undernutrition to specific developmental trajectories in functional connectivity, and eventually incorporate additional data to increase statistical power.

- Connectivity was assessed in 6 big ROIs to reduce variability due to head size and optode placement. Nevertheless, this also implies a significant reduction in spatial resolution. Individual digitalisation and co-registration of the optodes to a head model, followed by image reconstruction, could provide better spatial resolution. This is not a weakness specific to this study but rather a limitation common to most fNIRS studies, which typically analyse data at the channel level since digitalisation and co-registration can be challenging, especially in complex setups like this. The authors made an important effort to identify subjects with major optode displacement; however, future work might use tools to digitally record the positions of optodes and head markers.

Reviewer #2 (Public review):

Strengths:

The article addresses a topic of significant importance, focusing on early life growth faltering in low-income countries-a key marker of undernutrition-and its impact on brain functional connectivity (FC) and cognitive development. The study's strengths include the laborious data collection process, as well as the rigorous data preprocessing methods employed to ensure high data quality. The use of cutting-edge preprocessing techniques further enhances the reliability and validity of the findings, making this a valuable contribution to the field of developmental neuroscience and global health.

Weaknesses:

The study lacks specificity in identifying which specific brain networks are affected by growth faltering, as the current exploratory analyses mainly provide an overall conclusion that infant brain network development is impacted without pinpointing the precise neural mechanisms or networks involved.

Reviewer #3 (Public review):

Summary

This study aimed to investigate whether the development of functional connectivity (FC) is modulated by early physical growth, and whether these might impact cognitive development in childhood. This question was investigated by studying a large group of infants (N=204) assessed in Gambia with fNIRS at 5 visits between 5 and 24 months of age. Given the complexity of data acquisition at these ages and following data processing, data could be analyzed for 53 to 97 infants per age group. FC was analyzed considering 6 ensembles of brain regions and thus 21 types of connections. Results suggested that: i) compared to previously studied groups, this group of Gambian infants have different FC trajectory, in particular with a change in frontal inter-hemispheric FC with age from positive to null values; ii) early physical growth, measured through weight-for-length z-scores from birth onwards, is associated with FC at 24 months. Some relationships were further observed between FC during the first two years and cognitive flexibility, in different ways between 4- and 5-year-old preschoolers, but results did not survive corrections for multiple comparisons.

Strengths

The question investigated in this article is important for understanding the role of early growth and undernutrition on brain and behavioral development in infants and children. The longitudinal approach considered is highly relevant to investigate neurodevelopmental trajectories. Furthermore, this study targets a little studied population from a low-/middle-income country, which was made possible by the use of fNIRS outside the lab environment. The collected dataset is thus impressive and it opens up a wide range of analytical possibilities.

Weaknesses

Data analyses were constrained by the limited number of children with longitudinal data on NIRS functional connectivity. Applying advanced statistical modeling approaches such as structural equation modelling would provide further insights on neurodevelopmental trajectories and relationships with early growth and later cognitive development.

Reviewer #1 (Public review):

Summary:

Hoverflies are renowned for their striking sexual dimorphism in eye morphology and early visual system physiology, as well as in sexually dimorphic behaviors. Surprisingly, male and female flight behaviors in response to optic flow exhibit only subtle differences. Nicholas et al. investigate the sensorimotor transformation of sexually dimorphic visual information into flight steering commands via descending neurons. Using a combination of intracellular and extracellular recordings, neuroanatomical analysis, and behavioral assays, the authors convincingly demonstrate that descending neurons-particularly at high optic flow velocities-exhibit pronounced sexual dimorphisms, while wing steering responses remain largely monomorphic. The study highlights a very interesting discrepancy between neuronal and behavioral response properties.

More specifically, the authors focused on two types of descending neurons that receive inputs from well-characterized wide-field sensitive tangential cells: OFS DN1 and OFS DN2. Their likely counterparts in Drosophila connect to neck, wing and haltere neuropils. The authors characterized the visual response properties of these two neuronal classes in both male and female hoverflies and identified several interesting differences. They then presented the same set of stimuli, tracked wing beat amplitude and analyzed the sum and the difference of right and left wing beat amplitude as a readout of lift or thrust, and yaw turning, respectively. Behavioral responses showed little to no sexual dimorphism, despite the observed neuronal differences.

Strengths:

I find the question very interesting and the results both convincing and intriguing. A fundamental goal in neuroscience is to link neuronal responses and behavior. The current study highlights that the transformations - even at the level of descending neurons to motoneurons - is complex and less straightforward than one might expect.

Weaknesses:

The authors investigated two types of descending neurons, but it was not clear to me how many other descending neurons are thought to be involved in wing steering responses to wide-field motion. I would suggest providing a more in-depth overview of what is known in hoverflies and Drosophila, since the conclusions drawn from the study would be different if these two types were the only descending neurons involved, as opposed to representing a subset of the neurons conveying visual information to the wing neuropil.

Both neuronal classes have counterparts in Drosophila that also innervate neck motor regions. The authors filled hoverfly DNs in intracellular recordings to characterize their arborization in the ventral nerve cord. In my opinion, these anatomical data could be further exploited and discussed a bit more: is the innervation in hoverflies also consistent with connecting to the neck and haltere motor regions? Are there any obvious differences and similarities to the Drosophila neurons mentioned by the authors? If the arborization also supports a role in neck movements, the authors could discuss whether they would expect any sexual dimorphism in head movements.

Revision comment:

I thank the authors for their detailed replies to my questions and the additional clarifications and analysis included in the paper. All my concerns have been addressed.

Reviewer #2 (Public review):

Summary:

Many fly species exhibit male-specific visual behaviors during courtship while little is known about the circuit underlying the dimorphic visuomotor transformations. Nicholas et al focus on two types of visual descending neurons (DNs) in hoverflies, a species in which only males exhibit high-speed pursuit of conspecifics. They combined electrophysiology and behavior analysis to identify these DNs and characterize their response to a variety of visual stimuli in both male and female flies. The results show that the neurons in both sexes have similar receptive fields but exhibit speed-dependent dimorphic responses to different optic flow stimuli.

Strengths:

Hoverflies, though not a common model system, show very interesting dimorphic behaviors and provide a unique and valuable entry point to explore the brain organization behind sexual dimorphism. The findings here are not only interesting on their own right but will also likely inspire those working in other systems, particularly Drosophila.

The authors employed rigorous morphology, electrophysiology, and behavior methods to deliver comprehensive characterization of the neurons in question. The precision of the measurements allowed for identifying a subtle and nuanced neuronal dimorphism and set a standard for future work in this area.

Weaknesses:

I'd like to thank the authors for the revised manuscript, especially the new analyses and figures. Most of my earlier concerns have been satisfactorily addressed by now. Interested readers are kindly referred to the authors' responses for the discussion of the limitations of this work.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The editors have determined that the authors adequately addressed the prior reviewer comments.]

Summary:

The author's goal was to arrest PsV capsids on the extracellular matrix using cytochalasin D. The cohort was then released and interaction with the cell surface, specifically with CD151 was assessed.

Note on previous revisions:

The authors did an excellent job in their revision to include data from the effect of proteolytic priming on their observed virion transfer to the cell body. All other minor issues were addressed adequately.

The work could be especially critical to understanding the process of in vivo infection.

Reviewer #2 (Public review):

Review of the previous version:

The study design involves infecting HaCaT cells (immortalised keratinocytes mimicking basal cells of a target tissue) and observing virus localization with and without actin polymerization inhibition by cytochalasin D (cytoD) to analyze virion transfer from the ECM to the cell via filopodial structures, using cellular proteins as markers.

In the context of the model system, the authors stress in the revised version the importance of using HaCaT cells as a relevant 'polarized' cell model for infection. The term 'polarized' is used in the cell biological literature for epithelial cells to describe a strict apical vs. basolateral demarcation of the plasma membrane with an established diffusion barrier of the tight junction. However, HaCat cells do not form tight junctions. In squamous epithelia, such barriers are only found in granular layers of the epithelium. The published work cited in support of their claims either does not refer to polarity or only in the context of other cells such as CaCo-2 cells.

Overall, the matter of polarity would be important, if indeed the virus could only access cell-associated HSPGs as primary binding receptor, or the elusive secondary receptor via the ECM in the used model system (HaCaT cells), if they would locate exclusively basolaterally. This is at least not the case for binding, as observed in several previous publications (just two examples: Becker et al, 2018, Smith et al., 2008). With only a rather weak attempt at experimental verification of their model system with regards to polarity of binding, the authors then go on to base their conclusions on this unverified assumption.

This is one example of several in the manuscript, where claims for foundational premises, observations, and/or conclusions remain undocumented or not supported by experimental data.

Another such example is the assumption of transfer of the virus from ECM to the tetraspanin CD151. Here, the conclusions are based on the poorly documented inability of the virus to bind to the cell body, which is in stark contrast to several previous publications, and raises questions. Thus, association with CD151 likely occurs both from ECM derived virus AND virus that binds to cells, so that any conclusions on the mode of association is possible only in live cell data (which is not provided). Overall, their proposed model thus remains largely unsubstantiated with regards to receptor switching.

There are a number of important additional issues with the manuscript:

First, none of the inhibitors have been tested in their system for efficacy and specificity, but rely on published work in other cell types. This considerably weakens the confidence on the conclusion drawn by the authors.

Second, the authors aim to study transfer from ECM to the cell body and effects thereof. However, there are still substantial amounts of viruses that bind to the cell body compared to ECM-bound viruses in close vicinity to the cells. This is in part obscured by the small subcellular regions of interest that are imaged by STED microscopy, or by the use of plasma membrane sheets. This remains an issue despite the added Supple. Fig. 1, where also only sub cellular regions are being displayed. As a consequence the obtained data from time point experiments is skewed, and remains for the most part unconvincing, largely because the origin of virions in time and space cannot be taken into account. This is particularly important when interpreting the association with HS, the tetraspanin CD151, and integral alpha 6, as the low degree of association could be originating from cell bound and ECM-transferred virions alike.

Third, the use of fixed images in a time course series also does not allow to understand the issue of a potential contribution of cell membrane retraction upon cytoD treatment due to destabilisation of cortical actin. Or, of cell spreading upon cytoD washout. The microscopic analysis uses an extension of a plasma membrane stain as marker for ECM bound virions, this may introduce a bias and skew the analysis.

Fourth, while the use of randomisation during image analysis is highly recommended to establish significance (flipping), it should be done using only ROIs that have a similar density of objects for which correlations are being established. For instance, if one flips an image with half of the image showing the cell body, and half of the image ECM, it is clear that association with cell membrane structures will only be significant in the original. But given the high density of objects on the plasma membrane, I am not convinced that doing the same by flipping only the plasma membrane will not also obtain similar numbers than the original.

Reviewer #2 (Public review):

Summary:

The authors used single-nuclei sequencing of benign fallopian tubes and ovarian cancer to delineate the plausible cell of origin of high-grade serous ovarian cancer.

Strengths:

These substantial data provide the field with significant research resources to examine additional features in normal fallopian tubes and ovarian cancers. The highly detailed bioinformatic analysis, rooted in a strong biological framework, is convincing. The methodology was appropriate and used validated methodology based on biological relevance (region selection and transcriptomics analysis).

The authors propose a convincing model of epithelial progenitor cells and their localisation in high-grade serous ovarian cancers. These findings are important and useful.

Weaknesses:

Overall, the weaknesses are clearly stated in the discussion. The study provides a novel framework for future study, and proposes a model which will require validation.

Within the ovarian cancer field, the endometrioid and clear cell histotypes are thought to arise from ciliated or secretory cells. Typically these are thought to be from the cervix or uterus. This concept was not mentioned in the work.

Further, in the ovarian cancer field, stemness is judged by some classic assays - aldehyde assays looking at ALDH1A1 and spheroid-producing ability. These were not mentioned - could these be useful in a population of fallopian tube epithelial cells, or would other assays/markers be more appropriate?

The choice of ES2 and OVCAR was not sufficiently justified, as ES2 is widely regarded as a clear cell ovarian cancer cell line in many research circles. Additionally, I did not see confirmation of gene knockdown by Western blot or qPCR.

PGR loss through copy number variant was surprising, as this was a marker. So would the marker be lost through one of these mechanisms randomly or specifically?

Reviewer #1 (Public review):

Summary:

Using comprehensive profiling of normal and cancerous tissue via bulk and single-cell RNA sequencing, the authors identified that high-grade serous ovarian cancer is likely to originate from the epithelial progenitor cells from the distal fimbrial region of the fallopian tube, where it has been previously shown to be most prone to ovulatory stress and other microenvironmental influences. The authors also included a CNV analysis to identify hotspots in HGSOCs.

The findings are preliminary, but the resource on its own has great potential and can be used for developing methods for early detection, stratification and treatment.

The main limitation of this study is that the lineage is purely inferred from bioinformatics analysis. More validation work is required, perhaps using cell models / other model organisms.

Strengths and weaknesses:

The authors investigated the origin of high-grade serous ovarian cancer, which is one of the deadliest. They performed comparative analysis using both bulk and single-nucleus RNA sequencing between cancerous and normal tissues (fallopian tube and ovaries) and identified a population of epithelial progenitor cells from the distal fimbrial region that are exposed to ovulatory stress, as the most plausible cells of origin. The extensive profiling of the molecular signatures can also be used for early detection and stratification for treating the disease.

Previous studies have shown that HGSOCs likely originated from the epithelial lining of the fallopian tubes (PMID 32349388). The bulk RNAseq data is confusing in that neither the overall correlation of the transcriptome nor the sample clustering (Figure 1) supports the idea that the HGSOCs are close to the fallopian tube. The authors could perform a more comprehensive marker gene-based analysis to demonstrate their relationship.

The authors also performed a comprehensive analysis of single-cell datasets on both normal and cancerous tissue in humans. From there, they performed a combination of RNA velocity, PAGA and pseudotime, etc, to try and delineate the relationship amongst related cell populations. It would be helpful if the authors could clarify why they applied this particular suite of tools (explaining the differences between tools and bioinformatic approaches) to assist the broader readership who may not be familiar with this type of single-cell bioinformatic analysis.

It also seems to me that the authors did not account for patient effect when they performed the data integration (this point is discussed in the text). This may explain at least partially why the clusters are segregated by patient samples. Another explanation is that it could be due to uneven sampling, as only very few cells (1000s) were captured from each of the tumour samples, and this is clear when a dramatic difference can be seen in their cellular composition.

The trajectory analysis of normal and cancer single-cell data should also include other cells to prevent confirmation bias, as these analyses would only consider relationships amongst the cells available in the model.

As the authors indicated in the limitations, the cell lineage in the studies is largely inferred from the bioinformatics analysis. Experimental lineage tracing via other experimental models (organoids/animal models) would be required.

Despite these limitations, this study will serve as an important resource for the scientific community. I would also suggest that the authors should share this resource via additional portals in addition to the GEO data deposit (e.g. the HCA, or single-cell portals such as at the Broad Institute or CellXGene Discover).

Reviewer #1 (Public review):

This work demonstrates that MORC2 undergoes phase separation (PS) in cells to form nuclear condensates, and the authors demonstrate convincingly the interactions responsible for this phase separation. Specifically, the authors make good use of crystallography and NMR to identify multiple protein:protein interactions and use EMSA to confirm protein:DNA interactions. These interactions work together to promote in vitro and in cell phase separation and boosted ATPase activity by the catalytic domain of MORC2.

Moreover, the authors show solid evidence supporting their important claim that MORC2 PS is important for MORC2-mediated gene regulation. Exploring causal links between PS and function is an important need in the phase separation field, particularly as regards the role of condensates in gene regulation, and is a non-trivial matter. It is crucial and challenging to properly explore the alternative possibility that soluble complexes, existing in the same conditions as phase-separated condensates, are the functional species. The authors have attempted to address this concern by manipulating the physical nature of the MORC2 condensates using a killswitch (KS) peptide (MORC2 +KS), finding that reducing condensates dynamics results in a cellular phenotype very similar to that of the phase separation-deficient MORC2 condensates. While not fully ruling out the alternative, soluble-complex hypothesis, this experiment suggests that function is indeed localized inside the MORC2 condensates, and that perturbing the condensate can be functionally equivalent to removing condensate formation.

The authors also look at several disease related mutants of MORC2. While most of these do not seem to have an obvious connection to the phase separation data, it is quite interesting that one mutant, E236G, displays similar intra-condensate dynamics compared to MORC2 +KS, strengthening the claim that MORC2 phase separation is important for function and suggesting that the observations in this paper may indeed have some disease relevance.

Strengths

Static light scattering and crystallography are nicely used to demonstrate the dimerization of MORC2FL and to discover the structure of the CC3 domain dimer, presumably responsible for the dimerization of MORC2FL (Figure 1).

Extensive use of deletion mutants in multiple cell lines is used to identify regions of MORC2 that are important for forming condensates in the nucleus: the IBD, IDR, and CC3 domains are found to both be essential for condensate formation, while the CW domain plays an unknown role in condensate morphology (Figure 3). The authors use NMR to further identify that the IBD domain seems to interact with the first third of the centrally located IDR, termed IDRa, but not with the latter two thirds of the IDR domain (Figure 4). This leads them to propose that phase separation is the product of IDB:IDRa interaction, CC3 dimerization, and an unknown but important role for the CW domain.

Based on the observation that removal of the NLS resulted in diffuse cytoplasmic localization, they hypothesized that DNA may play an important role in MORC2 PS. EMSA was used to demonstrate interaction between DNA and several MORC2 domains: CC1, CC2, IDR, and TCD-CC3-IBD. Further in vitro microscopy with purified MORC2 showed that DNA addition significantly reduces MORC2 saturation concentration (Figure 5).

These assays convincingly demonstrate that MORC2 phase separates in cells and identifies the protein domains and interactions responsible for this phenomenon.

Weaknesses

The connection between condensates and function, while improved from the original manuscript, still has some weak points.

The central experiment demonstrating that MORC2 condensates mediate function takes the form of RNA-Seq in MORC2 KO HeLa cells (Figure 6), rescued with WT, condensate-deficient mutants, and a KS peptide mutant that reduces dynamics by increasing homotypic protein interactions. The observation that rescuing with MORC2 +KS is ineffective, in a manner similar to rescue with condensate-deficient MORC2 mutants, suggests that unperturbed condensates are important for function. An alternative possibility, however, is that condensates are non-functional bystanders, and that the increased homotypic interactions present in MORC2 +KS result in stronger MORC2 +KS recruitment to condensates, reducing the pool of functional, dilute phase MORC2 +KS and squashing function via sequestration. Similar ideas have been explored by others for transcription factors (e.g. Chong et al, Mol Cell, 2022). This possibility is neither discussed nor ruled out. The absence of microscopy data showing similar localization of MORC2 and MORC2 +KS (particularly the amount of diffuse MORC2 outside condensates) amplifies this concern.

The RNA-Seq data presented in Figure 6h also has some concerning qualities. Inter-replicate variability is higher than ideal, particularly for MORC2 deltaCC3. This may be a product of the transient transfection system used for these experiments, which inherently results in stochasticity. Specific sets of genes regulated by MORC2 are consistent with the main conclusion (Figure 6i, individual genes in 6h, showing that all mutants are more similar to one another than to WT MORC2), but global transcription shifts seem quite different between MORC2 condensate-deficient mutants and MORC2 +KS (Figure 6h heatmap), suggesting much more than simple condensate disruption is taking place. Together, this weakens the conclusion that MORC2 condensates are the functional form of MORC2.

Reviewer #2 (Public review):

Summary:

The study by Zhang et al. focuses on how condensation of a chromatin-associated protein MORC2 regulates gene expression. Their study shows that MORC2 forms dynamic nuclear condensates in cells. In vitro, MORC2 phase separation is driven by dimerization and multivalent interactions involving the C-terminal domain but interplay with other parts of MORC2 too. A key finding is that the intrinsically disordered region (IDR) of MORC2 exhibits strong DNA binding. They report that DNA binding enhances MORC2's phase separation and its ATPase activity, offering new insights into how MORC2 contributes to chromatin organization and gene regulation. Authors correlate MORC2's condensate forming ability and material properties with its gene silencing function using a few variants. Moreover, they investigate the effect of disease-linked mutations in the N-terminal domain of MORC2 on its ability to form cellular condensates, ATPase activity and DNA-binding. Their work implies that proper material properties of MORC2 condensates may be important to their biological function.

Strengths:

The authors determined a 3.1 Å resolution crystal structure of the dimeric coiled-coil 3 (CC3) domain of MORC2, revealing a hydrophobic interface that stabilizes dimer formation. They present extensive evidence that MORC2 phase separates across multiple contexts, including in vitro, in cellulo, and in vivo. Through systematic cellular screening, they identified the C-terminal domain of MORC2 as a key driver of condensate formation. Biophysical and biochemical analyses further show that the IDR within the C-terminal domain interacts with the C-terminal end region (IBD) and also exhibit strong DNA-binding capacity (using 601 DNA), both of which promote MORC2 phase separation. Together, this study emphasizes that interactions mediated by multiple domains-CC3, IDR, and IBD- drives MORC2 phase separation. Additionally, the work uses a unique kill-switch peptide fused to the MORC2 sequence to disrupt its material properties -- this permits the authors to examine the link between material properties and transcription function. The study is overall strengthened by (1) the combination of variants tested both in vitro and in cellulo, and (2) the systematic examination of domain contributions that highlight the multivalent interactions at play mediating MORC2 condensation.

Weaknesses:

The employed MORC2 variants have enabled the beginning of an investigation linking condensation and biological function, but more work will be needed to really dissect the contribution of condensation to DNA-binding, ATPase activity, and gene silencing. A systematic investigation of differential material properties on MORC2 condensates will be needed to assess the link to biological function, especially as the authors' work is reminiscent of how the liquidity of Caulobacter crescentus PopZ condensates tunes bacterial fitness.

Reviewer #3 (Public review):

Summary:

The manuscript by Zhang et al. demonstrates that MORC2 undergoes liquid-liquid phase separation (LLPS) to form nuclear condensates critical for transcriptional repression. Using a combination of in vitro LLPS assays, cellular studies, NMR spectroscopy, and crystallography, the authors show that a dimeric scaffold formed by CC3 drives phase separation, while multivalent interactions between an intrinsically disordered region (IDR) and a newly defined IDR-binding domain (IBD) further promote condensate formation. Notably, LLPS enhances MORC2 ATPase activity in a DNA-dependent manner and contributes to transcriptional regulation, establishing a functional link between phase separation, DNA binding, and transcriptional control.

Strengths:

The manuscript is well organized and logically structured. It provides valuable mechanistic insights into MORC2 function, and the majority of the conclusions are well supported by the data presented.

Reviewer #1 (Public review):

Summary:

This study investigates how ingestive behaviors are reflected in muscle activity and how these behaviors relate to neural dynamics in the brain. By combining muscle recordings with computational analysis, the authors identify patterns of mouth movements and show that these change over time and align with changes in brain activity. The work suggests that ingestion is not defined by a single action but by coordinated changes across multiple behaviors.

Strengths:

(1) Addresses an important and underexplored question about how ingestive behavior is organized.

(2) Combines behavioral, physiological, and computational approaches creatively.

(3) Provides a novel framework for quantifying complex ingestive movements.

(4) Demonstrates a clear temporal relationship between behavior and brain activity.

Weaknesses

(1) Behavioral labels rely on video-based scoring, which may not fully capture subtle or hidden movements.

(2) The relationship between brain activity and behavior is correlational, but sometimes interpreted more strongly.

(3) The manuscript could be clearer and more accessible to readers outside the field.

Reviewer #2 (Public review):

Summary:

In this study, Baas-Thomas et al. aim to study the neural mechanisms underlying ingestive versus rejection responses to taste stimuli by developing an EMG-based approach to identify ingestion-related orofacial movements. Whereas prior work has focused primarily on detecting rejection-related gapes, the authors introduce a machine-learning classifier that uses waveform features extracted from anterior digastric (AD) EMG signals to detect mouth- and tongue-movement (MTM) events associated with ingestion. Clustering analyses further suggest that ingestive behavior consists of multiple MTM subtypes whose relative frequencies vary across trial time and taste conditions. Finally, simultaneous recordings indicate that shifts in MTM expression follow transitions in gustatory cortex (GC) population dynamics into palatability-related firing states, supporting a role for cortical ensemble activity in coordinating ingestive motor responses.

Strengths:

Overall, the scientific question addressed in this study is well motivated. A mechanistic understanding of ingestive decision-making requires a precise characterization of the motor patterns that implement ingestion, and these behaviors have remained insufficiently resolved in prior work. The authors take a reasonable and technically innovative approach by leveraging AD EMG recordings to classify distinct orofacial movement patterns. The extracted waveform features appear effective in separating gapes from ingestion-related mouth-tongue movements, and clustering analyses further suggest the presence of distinguishable MTM subtypes that show meaningful temporal structure and neural correlates. Taken together, the work provides a potentially useful framework for linking gustatory cortical dynamics to the motor expression of taste-guided decisions.

A particularly valuable aspect of this work is the attempt to move beyond a binary characterization of ingestive behavior and instead identify multiple subtypes of ingestion-related movements. This finer behavioral resolution has the potential to provide a more realistic account of how complex consummatory actions are organized. More broadly, the effort to relate structured behavioral motifs to population-level neural dynamics is conceptually interesting and could prove useful for future studies seeking to connect circuit dynamics with the motor implementation of motivated behaviors.

Weaknesses:

(1) I have several concerns regarding the methodological comparisons used to establish the superiority of the proposed XGBoost classifier. In particular, the comparison between the XGBoost classifier and previously used QDA approaches (Figure 3) may not be entirely well-matched. The QDA framework was originally designed primarily to detect gape events and does not explicitly assign labels to MTM movements. As a result, the apparent advantage of XGBoost in identifying MTMs may partly reflect differences in task formulation rather than intrinsic differences in classification performance. From visual inspection, gape detection performance appears broadly comparable across methods.

A more informative benchmark would involve comparing XGBoost to an extended pipeline in which QDA-based gape detection is combined with a secondary movement-detection stage, distinguishing MTMs from periods of no movement. Such a comparison would better isolate the contribution of classifier architecture per se. Without this control analysis, the strength of the claim that XGBoost provides superior performance for behavioral decoding remains somewhat uncertain.

(2) The presentation of the neural ensemble analyses is considerably less comprehensive and intuitive than that of the behavioral analyses. The manuscript would benefit from more direct visualization of inferred neural state transitions. For example, plotting predicted neural states in a manner analogous to the behavioral states illustrated in Figure 6B would improve interpretability and help readers understand how neural dynamics relate temporally to behavioral changes.

In addition, the interpretation that GC ensemble dynamics drive behavioral state transitions may require further clarification. If GC activity plays a causal role in initiating behavioral changes, one might expect a consistent brain-to-behavior lag across changepoints. However, Figure 6 appears to show such lag primarily at the second transition but not at the first. This raises questions about how uniformly the proposed causal interpretation applies across state boundaries, and additional analysis or discussion is needed.

(3) The neural ensemble analyses primarily focus on constructing higher-level behavioral state variables rather than directly testing how individual movement subtypes relate to neural activity. The behavioral interpretation of the inferred state structure, therefore, remains somewhat unclear. While this approach is consistent with previous work from the authors and with broader state-transition frameworks of gustatory processing, it is not immediately obvious that this is the most informative level of analysis for the present dataset.

In particular, it would strengthen the manuscript to examine whether GC neurons or ensembles also encode lower-level motor structure, such as the occurrence of gapes or specific MTM subtypes. Demonstrating selective or mixed encoding across hierarchical levels (movement motifs versus abstract behavioral states) would help clarify the functional interpretation of the reported neural dynamics. At present, the manuscript largely assumes that GC activity reflects higher-order behavioral states without directly testing alternative representational possibilities.

(4) Because direct behavioral ground truth for intra-oral ingestive movements is difficult to obtain, MTM subtypes are inferred primarily through clustering of EMG waveform features. Although the authors demonstrate statistical separability and cross-session stability of these clusters, it remains unclear whether they correspond to discrete motor programs or instead reflect a structured partitioning of a continuous behavioral space shaped by feature selection and preprocessing choices. Perhaps some additional robustness analyses or convergent validation (e.g., alternative clustering methods, feature perturbation tests, or stronger neural and behavioral dissociations) would help clarify the biological significance of the inferred subtype structure.

Reviewer #3 (Public review):

Summary:

This study examines how ingestive-related orofacial movements relate to ensemble dynamics in gustatory cortex (GC) during taste processing. Previous work has shown that GC activity evolves through a sequence of population states following taste delivery, culminating in a transition to palatability-related firing that precedes rejection-related orofacial movements (e.g., gaping). Importantly, perturbing GC activity around the time of this transition alters the timing of gaping, suggesting that these ensemble dynamics play a functional role in linking taste evaluation to behavioral responses. The present study asks whether similar neural dynamics are also associated with ingestive-related orofacial movements that occur during the consumption of palatable stimuli.

To address this question, the authors develop a machine-learning classifier to identify distinct orofacial movements from anterior digastric EMG recordings. Using a set of labeled EMG waveforms obtained from video-scored trials, a gradient-boosted (XGBoost) classifier is trained to detect gapes, mouth/tongue movements (MTMs), and periods of no movement. Applying this classifier to a larger EMG dataset reveals that ingestive-related MTMs cluster into three distinct movement subtypes whose frequencies change systematically within trials.

The authors then relate these behavioral dynamics to previously described GC ensemble transitions identified using changepoint modeling. They report that changes in MTM subtype frequencies tend to occur shortly after the transition to palatability-related activity in GC. These results suggest that GC population dynamics are temporally associated not only with rejection-related behaviors but also with ingestive motor patterns that occur as animals prepare to consume palatable tastants.

Strengths:

The study introduces an innovative framework for extracting intricate orofacial movement information from EMG recordings. The machine-learning classifier provides a scalable method for identifying specific orofacial movements and performs better than previously published algorithms designed for gape detection. This approach allows the authors to examine movement microstructure at a temporal resolution that cannot be achieved with video scoring in freely moving animals.

A second strength is the integration of orofacial movement analysis with neural population dynamics. By relating EMG-derived movement subtypes to ensemble state transitions in GC, the study builds on a substantial body of work examining the temporal evolution of taste responses in cortex. The finding that ingestive-related movement dynamics occur shortly after the emergence of palatability-related firing provides an interesting extension of previous observations linking GC state transitions to rejection behavior.

The manuscript is also commendable in its commitment to data accessibility. By providing clear information about how the datasets can be accessed and making training data for the classifier publicly available, the authors make it possible for other researchers to examine the analytical pipeline and apply similar approaches to their own datasets. This transparency provides a useful framework for extending and building upon the methods presented here.

Weaknesses:

Some aspects of the EMG-based movement classification pipeline warrant careful interpretation. The training dataset used for classifier development is relatively small and is derived from a subset of trials in which mouth movements were clearly visible in video recordings. While the classifier performs well on this labeled dataset, it is not entirely clear how representative these labeled examples are of the full range of EMG signals present in the larger dataset.

The interpretation of the three identified MTM subtypes also remains somewhat tentative. The study convincingly demonstrates that distinct waveform-defined clusters exist in the EMG data, but the functional significance of these clusters as ingestive "behaviors" is less clear. As acknowledged by the authors, the specific roles of these movement patterns in the ingestion process remain speculative.

Finally, several conclusions in the Discussion rely on relatively strong mechanistic language when describing the relationship between GC dynamics and ingestive behavior. The data clearly demonstrate a temporal association between GC state transitions and changes in the frequencies of the different MTM subtypes. However, the results primarily support the interpretation that similar cortical dynamics are associated with ingestive and rejection-related behaviors rather than definitively establishing that these behaviors "are governed by the same underlying neural mechanisms".

Reviewer #1 (Public review):

Summary:

The authors have used a macaque (two animals only) to follow the migration of 'seeded' TDP43 protein in neuronal pathways - thus mimicking the spread of ALS in the human CNS. Previous experiments in rodents failed to demonstrate this, posing interesting and important biological differences, possibly related to the UMN-LMN system in higher order apes and humans.

Strengths:

An important step forward.

Weaknesses:

No weaknesses were identified by this reviewer. Only 2 animals were used, but that is appropriate given the sensate status of the macaque. In the opinion of this reviewer, the results are entirely convincing.

Reviewer #2 (Public review):

Summary:

There are astonishingly few papers trying to reproduce the process of initiation and spreading that Braaks studies have suggested and postulated. The authors should be applauded for pioneering such a difficult experiment. They overexpressed the TDP-43 protein in the motor neuron pool of the brachioradialis muscle and showed that by this technique, motor neurons in this pool died, and the muscle got denervated. They had evidence of a spreading process from the spinal cord to the cortex, demonstrated by showing widespread deposits of phosphorylated TDP-43 bilaterally in the cervical cord and the motor cortex. By their experiment, they created a dying-backwards model, not a model of corticofugal spread, like that shown by Braak. No muscle weakness was observed, not even in the brachioradialis.

Strengths:

The strength of this innovative study is the fact that this spreading experiment uses the phylogenetically young connectome of primates (macaques). They also made the thought-provoking observation of spreading from the cord to the motor cortex, not the corticofugal spread model observed by Heiko Braak. This is thought-provoking because this enables the observer to compare their model with the findings in humans.

Weaknesses:

The following aspects are not a weakness but need to be better explained for the interested reader - and potentially improved in future studies for which the authors laid the foundation:

(1) Why do the authors use the brachioradialis motor neuron pool to overexpress TDP-43? More is known about other muscles and how they are embedded in the motor connectome of primates. Why not the biceps brachii or the hand extensors or - even better - the small muscles of the hand? These are known to be strongly monosynaptically connected with the motor cortex. The authors should explain this. I am unclear if there was a specific reason which I did not see or understand. In my view, the brachioradialis is not the best representative of the primate connectome, for example, to examine this model and compare it with the corticofugal spread.

(2) In the Braaks experiment, only (seemingly soluble) non-phoshorylated TDP-43 "crossed" synapses. Phosphorylated TDP-43 did not do this. The authors of this study saw phosphorylated TDP43 in motor neurons and the cortex. Is there any potential explanation for how it crosses synapses? If it really does, there is an obvious difference to the human situation which needs to be emphasized and explained (in the future).

(3) There were significant deposits of phosphorylated TDP-43 in oligodendrocytes in humans. Whilst I understand that one experiment cannot solve every question - I am curious about whether the authors saw anything in oligodendrocytes?

(4) Which was the pattern of damage? Of course, this pattern is not likely to have a monosynaptic pattern - like in humans........but was there a pattern? Did it have a physiologically meaningful basis? Was there any relation to the corticofugal monosynaptic pattern? What are the differences? The authors speak of "multiple waves". Does this mean that if this were a corticofugal model, for example, oculomotor neurons would also degenerate?

Reviewer #3 (Public review):

Summary:

In this paper by Jones and colleagues, a non-human primate model is described in which wild-type TDP-43 is expressed in the cervical spinal cord. This gave rise to loss of motor neurons in the ventral horn at that level in the cervical spinal cord. MRI of the muscles allowed to see increased intensity in the mostly affected brachioradialis muscle, suggesting this muscle becomes denervated. At the neuropathological level, TDP-43 and pTDP-43 staining in the cytoplasm is increased, not only at the specific level of the cervical spinal cord, but also at a distance.

Strengths:

A clear strength is the state-of-the art focal expression of the TDP-43 transgene at a focal site in the cervical spinal cord. This is achieved by combining a general expression of a flipped loxP flanked TDP-43 vector using AAV9 intrathecal administration, followed by an intramuscular AAV2 hSyn CRE-TdTomato vector in the brachioradialis muscle in order to induce focal recombination and expression of TDP-43 in motor neurons innervating this muscle on one side.

Another strength is the non-human primate background, which is much closer to the human situation.

Weaknesses:

Given the complexity and cost of the model, the n is very low.

The design of the experiments and the results shown about the toxicity induced by this focal TDP-43 expression do not allow us to conclude that it is a good model for ALS for several reasons. It is not clear that the TDP-43 overexpression results in spreading weakness or in spreading motor neuron loss. The neuropathological changes described suggest that there is a kind of stress response, which extends to regions away from the site of primary damage, but more is needed to provide convincing evidence that there is spreading of disease pathology reminiscent of human ALS.

Reviewer #4 (Public review):

Summary:

In this manuscript, the authors present data describing the development of a model of ALS in rhesus macaques. They use a viral intersectional model to overexpress TDP-43 in a population of motor neurons and then study the spread of the pathology about 7 months later. They demonstrate that both the cervical spinal cord and motor cortex (new and old M1) are full of TDP-43, suggesting that the pathology spreads from the single motor pool to presumably related neurons.

Strengths:

This is a super-important study in two main ways:

(1) This could be the birth of a really important model, one that is really needed for making progress in understanding ALS and the development of therapeutics. There are shortfalls with all the rodent models. Models dependent on cell cultures are superb for understanding cell-autonomous processes, but miss out on connectivity, particularly the long-range connectivity. Organoids may ultimately prove to be beneficial, but they would need cortex, spinal cord, and muscle, and translatability from them is not assured. So a NHP model is needed, and this may be it. Furthermore, the Methods are meticulously described and will undoubtedly facilitate reproducibility.

(2) The concept of the spread of pathology has been proposed for some time, I think, based initially on the detailed clinical observations of Ravits and colleagues. The authors have looked at this directly and provide supporting evidence for this interesting hypothesis. They show spread locally and contralaterally in the spinal cord (although a figure would be nice) and to the motor cortex.

Taking only these 2 points into account is more than sufficient for me to be enthusiastic about this work.

Weaknesses:

I'd like to make a couple of points that if addressed, could, in my view, help the authors strengthen this work.

(1) We don't know how many MNs were transduced by the rAAV. There was no tdTom expression, for whatever reason. The authors show an image of a control experiment with a single MN transduced, but there should be a red motor pool, at least in the control experiments. The impression that I get is that very few were transduced, and, in my mind, this makes the findings even more interesting - maybe you don't need many "starter" MNs.

(2) Continuing on this point, this leads the authors to conclude that all BR MNs have died. They support this by the reduced MN count (see point 3). Firstly, do we know how many BR MNs there are in the rhesus macaque, and does the reduction seen correspond to this number? Secondly, and more importantly, the muscle looks normal on MRI at 28 weeks - it does not look like a denervated muscle. The authors state that it has maybe been reinnervated, but by what, if all the BR MNs are dead? This does not seem like a plausible explanation to me. Muscle histology, NMJs, and fibre typing would have been useful to understand what's going on with the MNs. (And electrophysiology would have been wonderful, but beyond the scope of this study.)

(3) Some MN biologists, like me, fuss a lot about how to count MNs, which is almost as difficult as counting the number of angels on the head of a pin. Every method has its problems. Focusing on the two methods here: (a) ChAT immunohistochemistry is pretty good in healthy states, but we don't know what happens to ChAT expression in different diseases, particularly when you have a new model. If its expression is decreased, then it is not a good marker for MNs; (b) Identifying MNs based on the size and morphology of neurons in the ventral horn is also insufficient. For example, ~30% of neurons in a typical pool are small gamma MNs, and a significant proportion (depending on the muscle) of the remainder will be small alpha MNs. So what one is counting is, at best, the large alpha MNs, not all the MNs in a pool. And in ALS, it's these largest MNs that are affected at the earliest stages. The small ones might be fine. So results will be skewed. (Hence, it would be interesting to see if the muscle had a higher proportion of Type I fibres after being reinnervated by S-type MNs.)

(4) Statistics. These are complex experiments looking at the spread of a disease. The experimental unit is therefore the monkey, n=2. In each monkey, multiple sections are analysed, which are key technical replicates and often summative. For example, do we care about the average cell number in Figures 4D, E, 5 I, J or 6G, H, or rather the total cell number? Do the error bars mean anything? To be clear, I am by no means minimising the importance of the overall convincing findings. But I do not think this statistical analysis is particularly meaningful.

Reviewer #1 (Public review):

Summary:

The question of how or whether "extensive memory training affects neocortical memory engrams" (to use the words of the authors) is an interesting question and an area where I think there is room for advancing current knowledge. That said, I do not think the current paper succeeds in meaningfully addressing this question. At a conceptual level, I really struggled with the predictions and interpretations of the findings. There are also several elements of the experimental paradigm and analysis decisions that feel incompatible with the claims that are made. While the manuscript does demonstrate that several measures of neural pattern similarity differ between the various groups of individuals, the issue is that it is difficult to draw clear conclusions from these findings.

Strengths:

(1) This is a very unique dataset. Being able to recruit and enroll high-level memory athletes is impressive.

(2) In principle, comparing memory athletes to control subjects, active control subjects (who received working memory training), and trained subjects (who received method of loci training) is very appealing.

(3) In several ways, the authors were rigorous in their analyses.

(4) In principle, the question of how memory training influences neural similarity vs. dissimilarity is of potential interest.

Weaknesses:

(1) As far as I can tell, the training manipulation is fully confounded with instructions. That is, subjects were only instructed to use the method of loci if they had completed method of loci training (or if they were the memory athletes). For the training group, in the pre-training session, there was no strategy instruction (subjects could do whatever they wanted), but post-training, they were told to use the method of loci. I understand the argument, of course, that naïve subjects might not be very good at using the method of loci if they had no experience with it. But, it does seem entirely possible that some (or even many) of the observed fMRI results that are attributed to "extensive training" are better explained by strategy use. That is, maybe the effects can be explained by TRYING to use the method of loci as opposed to actual proficiency with the method of loci. It seems impossible to address this, given the design of the experiments. As such, any claims about the effects of memory training, per se, feel inappropriate. It feels equally plausible that the effects are due to the strategy instruction. If the same results could be obtained through a simple strategy manipulation without ANY training at all, that would radically alter the interpretation of the effects. I think the strategy use account is, in fact, quite viable because it is very easy to improve subjects' memories with a method of loci instruction (relative to no strategy instruction) without ANY practice at all. Obviously, practice does improve memory performance with the method of loci, but my point is that even without any meaningful practice, there is likely to be SOME immediate benefit to adopting the method of loci as a strategy. There is also the question of why the effects for the memory athletes weren't obviously stronger than for the trained group, given that the memory athletes have much more experience with the method of loci. Ultimately, the problem with the current design is that I don't see how one can tease apart the role of training, per se, vs. strategy use.

(2) There is no clear theoretical framework for the predictions or interpretations. The Results section is mostly a list of lots of different permutations of analyses (similarity within a group, between groups, between trials, across trials between subjects, during encoding vs. retrieval, frontal vs. hippocampal vs. parietal ROIs, etc). For each analysis, I did not have an intuition for what the prediction should be (e.g., should athletes have higher or lower pattern similarity?), and even after seeing all the results, I still do not have an intuition for how to interpret them. For the main results related to dissimilarity in prefrontal cortex, I would have, if anything, predicted the opposite: that when individuals are trained to use a common strategy, there would be MORE similarity between them. The Discussion acknowledges a very wide range of possible factors that might contribute to measures of similarity/dissimilarity, but I am ultimately left feeling that I have no idea how to interpret the results because the design and analyses were not structured such that any of these interpretations could be teased apart.

(3) Same theme: the analyses shift from frontal regions (when looking at encoding) to hippocampus and precuneus (when looking at temporal recency). This shift in ROIs is confusing. The analyses (encoding vs. recognition) are essentially confounded with the ROIs (frontal vs. hippocampal/precuneus), so it's hard to know whether different analyses yielded different patterns or different ROIs yielded different patterns. Why were the frontal regions that were important for encoding ignored for the temporal recency judgments? And the fact that medial temporal lobe regions showed opposite effects to the frontal regions during encoding did not get much attention. Given that there were opposing patterns (dissimilarity vs. similarity) across different brain regions, the framing of the paper (that "the method of loci may bolster uniqueness") feels like a very selective representation of the data.

(4) One of the more surprising aspects of the analyses (or at least one of the analyses) is that representational similarity analyses (RSA) are used to compare the average activity pattern (averaged across all trials) between different individuals. At a conceptual level, this really just reduces to a univariate analysis. It is not standard (or intuitive) to think about RSA that is essentially blind to the actual representational content. In other words, averaging across trials obviously washes out the content, and what is left are process-level effects. For process-level analyses, univariate analyses are far more common and seem more straightforward. However, these 'RSA' analyses are described as reflecting the "uniqueness of each word-location association" (an account which strongly implies content-level effects). This feels like an inappropriate description of what the analyses actually reflect.

(5) I think the analysis looking at trial-by-trial similarity during word encoding (showing greater dissimilarity among the experienced individuals) is a somewhat interesting result, but again, I think the interpretation is very difficult. It is hard (or, impossible, I think) to get a clear sense of what is driving those differences. Is it the association of a unique spatial context? Is it somehow a product of better encoding, per se (as opposed to distinct spatial contexts)? These things could be tested by actually manipulating the spatial contexts in a more controlled way. For example, the paper by Liu et al. that is cited several times - and also a just-published paper by Christopher Baldassano (Nature Human Behaviour) - each used a very controlled paradigm where the (imagined) spatial location associated with each item was known/manipulated. However, the design of the current study does not allow for these things to be teased apart.

(6) Relatedly, the training group seemed to receive instruction on a common spatial route, but, surprisingly, "Participants were free to choose which route and how many they would use to anchor the 72 items." Thus, if I understand correctly, we don't know whether the trained individuals were using common or distinct locations. And the fact that they learned a 50-location route but then studied a 72-word list is also a bit strange. Not having control or knowledge of the location that was associated with each word (sequence position) is a major limitation and also a major difference between the current study and other recent studies. For that matter, the word order was also randomized, so there was no control over whether the words and/or locations matched. These issues really complicate interpretation.

(7) Again, same theme: for the result showing lower trial-by-trial similarity (within-subject similarity), the question is why, exactly, training/experience is associated with lower trial-by-trial similarity. Does training specifically or preferentially lead to greater differentiation between temporally-adjacent trials (as in Liu et al)? Does it lead to greater differentiation IF subjects associate each word with a unique location? Or maybe there is a more abstract effect of sequence/position that is independent of spatial location? Importantly, each of these three possibilities that I mention here has a precedent in prior studies that were more tightly controlled. But here, there is no way to tease these apart because of the experimental design, limiting the conclusions.

(8) The ISC analysis described on p. 9 (line 328) is confusing. If I understand correctly, correlations between different trials were not computed (e.g., subject 1 trial 1 was not correlated with subject 2 trial 2). Rather, trial 1 was always correlated with trial 1 (in other subjects). Thus, it is not clear whether trial-level alignment matters at all. Maybe the same results would be obtained if there were no correspondence across subjects in trial number. Or if the trial order was shuffled within the subject. Given this, I simply don't know how to think about the data. And why did memory athletes show higher pattern similarity in this analysis as opposed to lower pattern similarity (as in some other analyses)? And why was this analysis performed by comparing memory athletes to each other as opposed to memory athletes to non-athletes? And, conceptually, why was this selective to the memory athletes or to the precuneus? And why was it selective to the temporal order test and not encoding? I am not asking the authors to answer each of these questions; rather, the point I am trying to make is that this analysis, and many of the analyses, seem to raise more questions than they answer.

(9) The ISC analyses are interpreted in terms of scene construction and context reinstatement, but these conclusions go (very) far beyond what the data actually shows. Again, I don't see how this analysis lends itself to a meaningful conclusion. And this general critique applies to many of the analyses reported in this paper.

(10) The fact that words were in random order per subject also makes the ISC analysis even more confusing to think about. The memory athletes had unique spatial routes (that they used for the method of loci) and unique word lists. So, why would it make sense to look at trial-level ISC? At a conceptual level, I simply don't understand what this is intended to capture.

(11) Differences in the pattern of results between the encoding and temporal memory recognition task are hard to make sense of and are not addressed in much detail. Why would it make more sense to have across-trial similarity during recognition than during encoding? I think any account of this is very speculative.

Reviewer #2 (Public review):

The authors aim to understand how intensive training with the method of loci changes the brain systems that support memory in both elite "memory athletes" and previously untrained adults. They combine a cross-sectional comparison of athletes and matched controls with a longitudinal training study including mnemonic training, active working-memory training, and passive control groups, and use fMRI pattern-similarity analyses to characterise how brain activity patterns during learning and temporal-order judgments become more distinct or more shared within and across individuals.

The dual design is a major strength. It combines findings from both real-world expertise and experimentally induced training and adds well-matched control groups. The representational similarity analyses are appropriate and reveal a clear, internally consistent picture in which learning with the method of loci leads to more idiosyncratic prefrontal and posterior cortical patterns during encoding, and more shared hippocampal-precuneus patterns during temporal-order retrieval, observed in both athletes and trained novices.

However, the study is complex and the manuscript dense, and some secondary analyses feel less central or are difficult to interpret. More importantly, while the neural evidence for training-related changes in representational format is compelling, the behavioural relevance of these changes is less clearly supported. The key per-group brain-behaviour correlations are weak and inconsistent, and the direct association between neural and behavioural change across all subjects is not clearly presented.

Overall, the work convincingly shows that extensive mnemonic practice reorganises neural representations in specific networks, but the strength and specificity of the claimed link to long-term memory improvements should be viewed as more tentative.

Reviewer #3 (Public review):

Summary:

This study sought to explore how neural representations during encoding change with expertise or proficiency in the method of loci (MoL). To do this, the authors compared three groups: memory athletes (experts in MoL), naive controls, and naive participants before and after 6 weeks of MoL training and analyzed how similar their encoding-related activity patterns were across groups and training. They found that in lateral prefrontal, inferior temporal, and posterior parietal regions, pattern similarity decreased with expertise and training. They also found that changes in similarity between pre- and post-training were associated with improvements in memory performance measured 4 months later. Additionally, in a follow-up exploratory analysis on the temporal order recognition task, neural patterns were more similar for those proficient in MoL - a contrast to the decrease seen at encoding. Taken together, the authors interpret these findings as evidence that proficiency with the method of loci is associated with distinct encoding representations: Broadly, the findings suggest that greater representational differentiation at encoding may be associated with better memory.

Strengths:

(1) The manuscript is impressively rich with analyses. Their general claim that neural differentiation increases between individuals with MoL experience is thus addressed in this work. Specifically, the authors effectively explore different levels of granularity to tackle the question of whether a participant's neural representation (with MoL experience) looks more similar to that of another (with less experience) during encoding.

(2) The authors connect their hypotheses about neural representational differences caused by training to behavioral data (and 4 months later at that).

(3) Although exploratory, they not only look at encoding-related differences, but also retrieval-related differences.

(4) The authors provide many supplementary figures with complementary and interesting findings. As I read, I found myself curious about exploratory analyses, which were then addressed in supplementary figures.

Weaknesses:

(1) The manuscript is impressively rich, but the number of analyses and levels of comparison (and how they are presented) made it difficult to follow. The paper would benefit from an anticipatory introductory paragraph (or an introductory Results paragraph) that explicitly states the hypotheses and which sections of the results addressed them. Additionally, given how this is a Methods-last formatted paper, the manuscript would benefit from a few introductory sentences at each Results section describing the methodology.

(2) One of the motivations needs strengthening. Given the introduction, the manuscript seems to be motivated by two complementary questions: (i) whether neural differentiation effects reported with short-term MoL training (as done in Liu et al., 2022) extend with longer-term training and expertise and (ii) whether training might lead individuals towards a canonical "expert" representation that can only be acquired through training as has been previously shown in other work (e.g., Meshulam et al., 2021).

The first motivation is clear and compelling. The second one, however, does not feel as well grounded. In studies like Meshulam et al., alignment is expected because participants are exposed to the same stimulus or concept. In contrast, as the authors note, a user of the method of loci is encouraged to create unique, vivid representations of their loci and to-be-remembered items - here, neural alignment is at odds with the premise of the technique. As such, the described tension between increased pattern similarity across the studies cited in the second paragraph of the introduction and individuals proficient with MoL feels underdeveloped (despite the reference-rich second paragraph).

The authors would benefit from articulating why the counterfactual of "increased neural alignment" might be expected, specifically, in the method of loci. In other words, why should we expect trainees to become more similar to experts when the strategy itself promotes idiosyncratic representations? Perhaps, the authors could distinguish between alignment at the level of knowledge representations vs the process of encoding (e.g., the act of placing items into loci).

(3) Relatedly, terminology referencing the employed methodology is a bit unclear. In some of the papers cited that look at pattern similarity across people (like Meshulam et al., or Koch et al.), the spatial patterns of individuals are compared with 'template' patterns that reflect the canonical representation of a concept or episode. However, the manuscript does not include this type of template-based comparison. This is understandable because there may not be a representative canonical pattern when each participant has their own idiosyncratic palace. In this case, a pairwise comparison may be more fitting as it focuses on the distances between people's representations instead of the distances between them and a group template. Although both comparisons (pairwise and template-based similarities) are related, they have different interpretations. A clearer justification for why pairwise similarity, instead of template-based similarity (as in many of the cited papers), is the more appropriate metric in this paradigm early on would add to the clarity of the work. Additionally, this slight difference in methodology was confusing because some portions of the text (including the figures) say "group average", but in others, we see "pairwise".

Minor Comments:

A recent paper (Masis-Obando et al., 2026, Nat Hum Behav) shows that stable and distinctive spatial representations can support later reinstatement of items placed within those contexts. Their conclusions seem to support your hypotheses and results here. In parallel, prior work (like Robin et al., 2018, J Neurosci) emphasizes the importance of spatial contexts for the representation of events. Given how MoL encoding relies on vivid context-item binding, including these perspectives in the Introduction (and/or discussion) may help frame the current findings within the broader memory literature.

Overall, this work provides rich and valuable contributions to the field.

Reviewer #2 (Public review):

In this revised version of the manuscript, the authors have addressed many of my concerns. The representative confocal images now provided, allow for a much better assessment of the claims being made and hence the data to be understood, for example the level of protein expression of Chi3l1 in the macrophages.

There is just 1 concern remaining, which is a main claim of the manuscript, that loss of Chi3l1 drives KC death in MASLD. This claim is made based on gene expression profiles and the presence of Tunel staining in liver sections. However the KC numbers are not altered compared with WT when assessed by flow cytometry. This discrepancy is not really addressed. If the cells are not actually dying this would explain the lack of moKCs (a concern raised by reviewer 1) and would indeed suggest that the loss of these cells is, as suggested by that reviewer, trivial in this timeframe. The authors propose in their rebuttal that the KCs are in a prolonged state of stress, explaining the Tunel staining, but to make the claim that they die, the authors need to show their eventual loss from the liver. Otherwise the claims of death should be revised.

Reviewer #3 (Public review):

This paper investigates the role of Chi3l1 in regulating the fate of liver macrophages in the context of metabolic dysfunction leading to the development of MASLD.

Comments on revisions:

My comments have been addressed.

Reviewer #1 (Public review):

Ma et al. use human-chimpanzee tetraploid cells across different cell types to identify the genetic causes and then transcriptomic consequences of divergence in DNA methylation. They conclude that the evolution of DNA methylation is driven primarily by cis-regulatory changes, and that the evolution of CpG sites contributes to cis-regulation, while transcription factor expression underlies some trans changes. They then argue that divergence in DNA methylation is associated with changes in gene expression and may contribute to human phenotypes.

The tetraploid model is able to provide compelling evidence that most regulatory evolution occurs due to cis-regulatory changes. My only concern is that the extent of trans-changes may be overstated, as almost all are eliminated by changing from a nominal p-value criterion to even a 25% false discovery rate. The follow-up analyses are incomplete with major gaps. The authors focus on single potential mechanisms for cis- and trans-changes, but it is not clear to what degree these mechanisms explain the extent of cis and trans changes. There are also other mechanisms which are not investigated, such as the importance of TF binding sites for cis-regulatory evolution. While likely beyond the scope of this work, communicating these areas for future work would have helped define the niche for this manuscript.

Next, the authors seek to show that differences in DNA methylation are functionally relevant. Consistent with previous results, they show that differences in DNA methylation are (weakly) associated with changes in gene expression. They hypothesize that genes with concordant regulatory elements should exhibit greater methylation-expression coupling than other genes and show that cis-expression/cis-methylation pairs are more strongly correlated than trans/trans pairs. However, I worry that this result could be confounded by larger effect sizes for cis-changes than trans effects. I also think that looking at cis/trans or trans/cis changes would have been useful to directly test the driving hypothesis. Another limitation is that this analysis is limited to promoter regions. It is not clear how many divergent DMRs are included and how many of those genes have differences in expression. The key question is whether differences in DNA methylation are functionally important, and the answer provided by these analyses is "sometimes".

Finally, the authors make a case for lineage-specific selection on DNA methylation that is connected to human traits. This evidence was not convincing. In fact, it is even said that these tests cannot be interpreted as evidence of lineage-specific selection (lines 399-401), so I am confused why these results are framed as testing for selection. The evidence better supports an argument connecting DNA methylation to human phenotypes.

In conclusion, I think this study provides a valuable resource for differences in DNA methylation between humans and chimpanzees across tissues, and provides important insight into the relative abundance of cis and trans regulatory evolution. Additional research is necessary to investigate the underlying regulatory mechanisms, and more care needs to be taken in exploring the functional consequences.

Reviewer #2 (Public review):

Summary:

This manuscript investigates the causes and consequences of human-specific DNA methylation divergence relative to chimpanzees. The main aim of this study is to disentangle cis- and trans-regulatory contributions to DNA methylation differences, which the authors address using an innovative interspecies hybrid cell system differentiated into multiple cell types. This design allows them to control for trans-acting environments and directly compare allelic regulation.

The authors show that cis-regulatory mechanisms dominate DNA methylation divergence and that methylation-expression coupling is strongest when both are cis-regulated. They further explore potential mechanisms underlying these patterns, including CpG-disrupting mutations and transcription factor-associated trans effects, and identify pathways that may reflect lineage-specific regulatory evolution.

This study provides a valuable dataset and a compelling framework for understanding how local sequence variation contributes to epigenetic and transcriptional divergence, with likely broad impact in comparative and evolutionary genomics.

Strengths:

A major strength of this study is the use of human-chimpanzee hybrid cells, which provides a powerful system to disentangle cis- and trans-regulatory effects in a shared cellular environment. This experimental design allows for a more definitive assessment of regulatory mechanisms than traditional cross-species comparisons.

The study also benefits from the inclusion of multiple differentiated cell types, increasing the robustness and generality of the conclusions. The consistent observation that cis-regulatory mechanisms dominate methylation divergence across these contexts is well supported by both CpG-level and DMR-level analyses.

Another important contribution is the finding that methylation-expression coupling is strongest when both are cis-regulated. This provides a mechanistic explanation for previously observed weak global correlations between methylation and gene expression. Given that the nature of regulatory evolution is likely highly heterogeneous, this study adds valuable insights and guidelines for future investigations. I recommend that the authors provide a list of cis-cis-regulated promoters and their associated genes, which would be a valuable resource for the field.

The application of the two-step sign test identifies biologically relevant pathways, suggesting links between epigenetic divergence and human-specific traits.

The dataset itself, namely, comprehensive DNA methylation and gene expression across multiple cell types in shared cellular contexts, as well as a primary cell type, is a valuable resource for the field. Additionally, the application of the two-step sign test identifies biologically relevant pathways, suggesting links between epigenetic divergence and human-specific traits.

Weaknesses:

Although the authors identify transcription factors associated with differential methylation, it is unclear what proportion of differentially methylated CpGs or DMRs can be attributed to these factors. Providing a quantitative estimate would help assess the relative contribution of trans-acting regulation.

The analysis of CpG-disrupting mutations is interesting but raises two concerns. First, other classes of variants-such as transcription factor binding site-disrupting mutations-could also influence local methylation patterns and are not considered here. Second, the causal direction remains ambiguous: CpG-disrupting mutations may result from methylation-associated mutational processes (e.g., C→T transitions at methylated CpGs) rather than being the primary drivers of methylation divergence. While additional analyses may not be necessary, explicitly acknowledging these alternative explanations would strengthen the interpretation.

Regarding the discussion comparing the distance between CpG-disrupting SNVs and trans-DMRs, without information on the absolute or relative distance distributions, it was difficult to assess the magnitude of the observed differences. Moreover, trans-DMRs, by definition, are not driven by local (cis) variation, and the lack of proximity to CpG-disrupting SNVs is expected. Clarifying what additional insight this analysis provides beyond this expectation may improve this section.

One potential extension would be to examine whether the same cis-acting SNVs are consistently associated with methylation differences across multiple cell types. If these variants are mechanistically causal, one might expect their effects to be reproducible across contexts, or at least more frequent than expected by chance. Such an analysis could further support the proposed link between sequence variation and methylation divergence.

Regarding their two-step sign test analysis, because enrichment-based approaches can sometimes overemphasize statistical significance without reflecting effect size, I wonder if incorporating the magnitude of methylation change would provide additional information or strengthen these findings. While the authors highlight some cases, such as TUBB2 and GRIK, a more general overview and/or integration of effect size into the analysis or discussion would improve interpretability.

Reviewer #3 (Public review):

Summary:

Ma et al. use human-chimpanzee tetraploid cells to examine species differences in DNA methylation. They identify differentially methylated regions under cis or trans regulation. Cis-DMRs are enriched near SNVs that disrupt or create CpGs, providing a plausible mechanism for cis changes in methylation. They also seek to identify transcription factors that might affect methylation in trans, as well as gene sets with evidence for consistent changes in methylation and expression between humans and chimpanzees.

Strengths:

The authors have generated a new dataset across multiple cell types, examining differences in DNA methylation between humans and chimpanzees using human diploid cells, chimpanzee diploid cells, and human-chimpanzee tetraploid cells. Using this dataset, they identify that cis-DMRs are enriched near SNVs that disrupt or create CpGs compared to trans-DMRs, and identify transcription factors as candidate trans-acting factors. Both identified SNVs and transcription factors are good candidates for future experimentation. Further, they find that cis-DMRs are more highly correlated with cis-expressed genes than trans-DMRs with trans-expressed genes, providing evidence that methylation and expression are linked genome-wide.

Weaknesses:

The authors could greatly improve the manuscript by focusing on two issues.

(1) Strengthening their cis/trans analysis, including:<br /> a) only showing or analyzing genomic regions that pass FDR correction;<br /> b) clarifying how cis genes are defined (Figure 2B shows some genes labeled as cis where the direction-of-effect differs between hybrid and parent cells);<br /> c) assessing how well powered they are to perform each analysis.

(2) Softening claims about human evolution or human specificity for several reasons:<br /> a) Their comparison lacks tetraploid controls (e.g. human-human tetraploids and chimp-chimp tetraploids) or experimental follow-up in diploid cells, making it hard to be certain that observed effects are not due to ploidy.<br /> b) There are no outgroup species included in the analysis.<br /> c) The use of no or very loose FDR corrections with the sign test makes it difficult to draw conclusions.<br /> d) Experimental data to link SNVs to changes in cis methylation or identified transcription factors to changes in trans methylation would be needed to validate the authors' predictions.

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 satisfactorily addressed the previous concerns raised by the reviewers.]

Summary:

This study presents convincing findings that oligodendrocytes play a regulatory role in spontaneous neural activity synchronization during early postnatal development, with implications for adult brain function. Utilizing targeted genetic approaches, the authors demonstrate how oligodendrocyte depletion impacts Purkinje cell activity and behaviors dependent on cerebellar function. Delayed myelination during critical developmental windows is linked to persistent alterations in neural circuit function, underscoring the lasting impact of oligodendrocyte activity.

Strengths:

(1) The research leverages the anatomically distinct olivocerebellar circuit, a well-characterized system with known developmental timelines and inputs, strengthening the link between oligodendrocyte function and neural synchronization.

(2) Functional assessments, supported by behavioral tests, validate the findings of in vivo calcium imaging, enhancing the study's credibility.

(3) Extending the study to assess long-term effects of early life myelination disruptions adds depth to the implications for both circuit function and behavior.

Weaknesses:

(1) The study would benefit from a closer analysis of myelination during the periods when synchrony is recorded. Direct correlations between myelination and synchronized activity would substantiate the mechanistic link and clarify if observed behavioral deficits stem from altered myelination timing.

(2) Although the study focuses on Purkinje cells in the cerebellum, neural synchrony typically involves cross-regional interactions. Expanding the discussion on how localized Purkinje synchrony affects broader behaviors-such as anxiety, motor function, and sociality - would enhance the findings' functional significance.

(3) The authors discuss the possibility of oligodendrocyte-mediated synapse elimination as a possible mechanism behind their findings, drawing from relevant recent literature on oligodendrocyte precursor cells. However, there are no data presented supporting these assumptions. The authors should explain why they think the mechanism behind their observation extends beyond the contribution of myelination or remove this point from the discussion entirely.

Comment for resubmission: Although the argument on synaptic elimination has been removed, it has been replaced with similarly unclear speculation about roles for oligodendrocytes outside of conventional myelination or metabolic support, again without clear evidence. The authors measured MBP area but have not performed detailed analysis of oligodendrocyte biology to support the claims made in the discussion. Please consider removing this section or rephrasing it to align with the data presented.

(4) It would be valuable to investigate secondary effects of oligodendrocyte depletion on other glial cells, particularly astrocytes or microglia, which could influence long-term behavioral outcomes. Identifying whether the lasting effects stem from developmental oligodendrocyte function alone or also involve myelination could deepen the study's insights.

(5) The authors should explore the use of different methods to disturb myelin production for a longer time, in order to further determine if the observed effects are transient or if they could have longer-lasting effects.

(6) Throughout the paper, there are concerns about statistical analyses, particularly on the use of the Mann-Whitney test or using fields of view as biological replicates.

Reviewer #1 (Public review):

Summary:

The manuscript by Seraj et al. introduces a transformative structural biology methodology termed "in extracto cryo-EM." This approach circumvents the traditional, often destructive, purification processes by performing single-particle cryo-EM directly on crude cellular lysates. By utilizing high-resolution 2D template matching (2DTM), the authors localize ribosomal particles within a complex molecular "crowd," achieving near-atomic resolution (~2.2 Å). The biological centerpiece of the study is the characterization of the mammalian translational apparatus under varying physiological states. The authors identify elongation factor 2 (eEF2) as a nearly universal hibernation factor, remarkably present not only on non-translating 80S ribosomes but also on 60S subunits. The study provides a detailed structural atlas of how eEF2, alongside factors like SERBP1, LARP1, and IFRD2, protects the ribosome's most sensitive functional centers (the PTC, DC, and SRL) during cellular stress.

Strengths:

The "in extracto" approach is a significant leap forward. It offers the high resolution typically reserved for purified samples while maintaining the "molecular context" found in in situ studies. This addresses a major bottleneck in structural biology: the loss of transiently bound or labile factors during biochemical purification.

The finding that eEF2 binds and sequesters 60S subunits is a major biological insight. This suggests a "pre-assembly" hibernation state that allows for rapid mobilization of the translation machinery once stress is relieved, which was previously uncharacterized in mammalian cells.

The authors successfully captured eIF5A and various hibernation factors in states that are traditionally disrupted. The identification of eIF5A across nearly all translating and non-translating states highlights the power of this method to detect ubiquitous but weakly bound regulators.

The manuscript beautifully illustrates the "shielding" mechanism of the ribosome. By mapping the binding sites of eEF2 and its co-factors, the authors provide a clear chemical basis for how the cell prevents nucleolytic cleavage of ribosomal RNA during nutrient deprivation.

Weaknesses:

While 2DTM is a powerful search tool, it inherently relies on a known structural "template." There is a risk that this methodology may be "blind" to highly divergent or novel macromolecular complexes that do not share sufficient structural similarity with the search model. The authors should discuss the limitations of using a vacant 60S/80S template in identifying highly remodeled stress-induced complexes. For instance, what happens if an empty 40S subunit is used as template? In the current work, while 60S and 80S particles are picked, none are 40S. The authors should comment on this.

In the GTPase center, the authors identify density for "DRG-like" proteins. However, due to limited local resolution in that specific region, they are unable to definitively distinguish between DRG1 and DRG2. While the structural similarity is high, the functional implications differ, and the identification remains somewhat speculative. The authors should acknowledge this in the text.

While "in extracto" is superior to purified SPA, the act of cell lysis (even rapid permeabilization) still involves a change in the chemical environment (pH, ion concentration, and dilution of metabolites). The authors could strengthen the manuscript by discussing how post-lysis changes might affect the occupancy of factors like GTP vs. GDP states.

The study provides excellent snapshots of stationary states (translating vs. hibernating), but the kinetic transition-specifically how the 60S-eEF2 complex is recruited back into active translation-is not well discussed. On page 13, the authors present eEF2 bound to 60S but do not mention anything regarding which nucleotide is bound to the factor. It only becomes clear that it is GDP after looking at Figure S9. This should be clarified in the text. Similarly, the observations that eEF2 is bound to GDP in the 60S and 80S raises the questions as to how the factor dissociates from the ribosome. This could also be discussed.

Overall Assessment:

This work reported in this manuscript likely represents the future of structural proteomics. The combination of high-resolution structural biology with minimal sample perturbation provides a new standard for investigating the cellular machines that govern life. After addressing minor points regarding template bias, protein identification, and transition dynamics, this work may become a landmark in the field of translation.

Comments on revisions:

In the revised version of the manuscript, the authors have addressed my prior concerns.

Reviewer #2 (Public review):

In this manuscript, the authors describe using "in extracto" cryo-EM to obtain high-resolution structures of mammalian ribosomes from concentrated cell extracts without further purification or reconstitution. This approach aims to solve two related problems. The first is that purified ribosomes often lose cellular cofactors, which are often reconstituted in vitro; this precludes the ability to find novel interactions. The second is that while it is possible to perform cryo-EM on cellular lamella, FIB milling is a slow and laborious process, making it unfeasible to collect datasets sufficiently large to allow for high-resolution structure determination. Extracts should contain all cellular cofactors and allow for grid preparation similar to standard single-particle analysis (SPA) approaches. While cryo-EM of cell extracts is not in itself novel, this manuscript uses 2D template matching (2DTM) for particle picking prior to structure determination using more standard SPA pipelines. This should allow for improved picking over other approaches, in order to obtain in large datasets for high-resolution SPA.

This manuscript has two main results: novel structures of ribosomes in hibernating states; and a proof-of-principle for in extracto cryo-EM using 2DTM. Overall, I think the results presented here are strong and serve as a proof-of-principle for an approach that may be useful to many others.

Comments on revisions:

This current draft addresses my prior comments regarding usability for readers through the addition of text describing how parameters were optimized as well as an additional supplementary figure outlining the processing workflow. With these additions, I have no further comments.

Reviewer #3 (Public review):

Summary:

The authors describe a new structural biology framework termed "in extracto cryo-EM," which aims to bridge the gap between single-particle cryo-EM of purified complexes and in situ cryo-electron tomography (cryo-ET). By utilizing high-resolution 2D template matching (2DTM) on mammalian cell lysates, the authors sought to visualize the translational apparatus in a near-native environment while maintaining near-atomic resolution. The study identifies elongation factor 2 (eEF2) as a major hibernation factor bound to both 60S and 80S particles and describes a variety of hibernation scenarios involving factors such as SERBP1, LARP1, and CCDC124.

Strengths:

(1）The use of 2DTM effectively overcomes the signal-to-noise challenges posed by the dense and viscous nature of cellular extracts, yielding maps as high as 2.2 Å.<br /> (2）The discovery of eEF2-GDP as a ubiquitous shield for ribosomal functional centers, particularly its unexpected stabilization on the 60S subunit, provides a compelling model for ribosome preservation during stress.

Weaknesses:

(1) Representative nature of cell samples and lower detection limit

The cells used in this study (MCF-7, BSC-1, and RRL) are either fast-growing cancer cell lines or specialized protein-synthetic systems. For cells with naturally low ribosomal abundance (such as quiescent primary cells), achieving the target concentration (e.g., A260 > 1000 ng/uL) would require an exponentially larger starting cell population.

Is there a defined lower limit of ribosomal concentration in the raw lysate below which the 2DTM algorithm fails to yield high-resolution classes? In ribosome-sparse lysates, A260 becomes an unreliable proxy for ribosome density due to the high background of other RNA species and proteins. How do the authors estimate specific ribosome abundance in such heterogeneous fields?

(2) Quantitation in heterogeneous lysates and crowding effects

The authors utilize A260 as a key quality control measure before grid preparation. However, if extreme physical concentration is required to see enough particles, the background concentration of other cytoplasmic components also increases. This may lead to molecular crowding or sample viscosity that interferes with the formation of optimal thin ice. How do the authors calculate or estimate the specific abundance of ribosomes in the cryo-EM field of view when they represent a much smaller percentage of the total cellular content?

(3) Optimization of sample preparation

The authors describe lysates as dense and viscous, requiring multiple blotting steps (2-3 times) for 3-8 seconds. Have the authors tested whether a larger molecular weight cutoff (e.g., 100 kDa) during concentration could improve the ribosome-to-background ratio without losing small factors like eIF5A (approx. 17 kDa)? Could repeated blotting of a concentrated, viscous lysate introduce shearing forces or increased exposure to the air-water interface that perturbs the native conformation of the complexes?

(4) The regulatory switch and mechanism of eEF2

The finding that eEF2-GDP occupies dormant ribosomes is striking. What drives eEF2 from its canonical role in translocation to this hibernation state? Is this transition purely driven by stoichiometry (lack of mRNA/tRNA) and the GDP/GTP ratio, or is there a role for post-translational modifications? How do these eEF2-bound dormant ribosomes rapidly re-enter the translation pool upon stress relief?

(5) Hibernation diversity and LARP1 contextualization

The study reveals that hibernation strategies vary across cell types. Does the high hibernation rate in RRL reflect a physiological state, or does it hint at "preparation-induced stress" due to resource exhaustion or mRNA degradation in the cell-free system? How do the authors reconcile their discovery of LARP1 on 80S particles with recent 2024 reports that primarily describe LARP1 as an SSU-bound repressor?

Comments on revisions:

The authors have addressed the issues I had raised in my initial review. The additional data and clarifications provided in the revision are satisfactory. I have no further recommendations.<br /> Thanks to the authors for their efforts.

Reviewer #1 (Public review):

Summary:

Rolland and colleagues investigated the interaction between Vibrio bacteria and Alexandrium algae. The authors found a correlation between the abundance of the two in the Thau Lagoon and observed in the laboratory that Vibrio grows to higher numbers in the presence of the algae than in monoculture. Timelapse imaging of Alexandrium in coculture with Vibrio enabled the authors to observe Vibrio bacteria in proximity to the algae and subsequent algae death. The authors further determine the mechanism of the interaction between the two and point out similarities between the observed phenotypes and predator prey behaviours across organisms.

Strengths:

The study combines field work with mechanistic studies in the laboratory and uses a wide array of techniques ranging from co-cultivation experiments to genetic engineering, microscopy and proteomics. Further, the authors test multiple Vibrio and Alexandria species and claim a wide spread of the observed phenotypes.

Comments on revisions:

I thank the authors for their additional work on the manuscript. My comments were addressed to my satisfaction.

Reviewer #2 (Public review):

Goal summary

The authors sought to (i) demonstrate correlations between the dynamics of the dinoflagellate Alexandrium pacificum and the bacterim Vibrio atlanticus in natural populations, ii) demonstrate the occurrence of predation in laboratory experiments, iii) demonstrate that predation is induced by predator starvation, and iv) test for effects of quorum sensing and iron-uptake genes on the predation process.

Strengths include

- Data indicating correlated dynamics in a natural environment that increase the motivation for study of in vitro interactions<br /> - Experimental design allowing clear inference of predation based on population counts of both prey and predators in addition to microscopy-based evidence<br /> - Supplementation of population-level data with molecular approaches to test hypotheses regarding possible involvement of quorum sensing and iron update in predation

Weaknesses include

- A quantitative analysis of effects of manipulating V. atlanticus density on rates of predation would have been valuable<br /> - Lack of clarity in some of the methodological descriptions

Appraisal

The authors convincingly demonstrate that V. atlanticus can prey on A. pacificum, provide strongly suggestive evidence that such predation is induced by starvation and clearly demonstrate that both iron availability and correspondingly the presence of genes involved in iron uptake strongly influence the efficacy of predation.

Discussion of impact

This paper will interest those interested in the diversity of forms of microbial predation and how microbial predatory behavior responds to environmental fluctuations. It will also interest those investigating bacteria-algae interactions and potential ecological controls of algal blooms. It may also interest researchers of microbial cooperation in light of the suggestion of communication between predator cells.

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.

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?

(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).

(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.

(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.

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.

Weaknesses:

(1) Purely theoretical work, no experimental validation.

(2) Adopts previously published models more or less 'as is', without detailed re-evaluation and re-assessment, or without developing them further.

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.

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.

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.

Reviewer #1 (Public review):

Summary:

This study examines Müller glia (MG) reprogramming in the uninjured mouse retina through a combination of Notch signaling inhibition and AAV-induced proliferation. Building on their prior work showing that Cyclin D1 overexpression and p27^Kip1^ knockdown (CCA) promotes MG proliferation with very limited neurogenesis, the authors now demonstrate that Rbpj deletion alone induces a modest degree of MG-to-neuron conversion without proliferation, in agreement with recent work in the field. However, combining Rbpj deletion with CCA-mediated proliferation substantially enhances MG dedifferentiation and the generation of retinal neuron-like cells. Through genetic lineage tracing, histological analyses, and single-cell transcriptomics, the authors provide evidence that MG-derived cells acquire molecular features of bipolar (ON, OFF, and rod bipolar) and amacrine neurons. Most MG-derived cells appear to survive long-term (up to 9 months).

Strengths:

Overall, the study is carefully designed and executed, and the manuscript is clearly written with well-presented figures. While the work does not significantly expand the repertoire of neuronal types generated from mammalian MG beyond what has been previously reported in the field, it provides a valuable and improved strategy for inducing robust MG proliferation and neurogenesis in the mammalian retina.

Weaknesses:

(1) It would be better to include a negative control AAV when evaluating the effect of CCA AAV in the Rbpj KO background. This could help distinguish the specific contribution of the CCA construct from potential effects of intravitreal AAV injection itself, which can induce mild inflammation, known to influence MG reprogramming.

(2) The extent of MG transduction by the CCA AAV is not clear. As quantifications are normalized to total MG (GFP^+^ or TdTomato^+^) or retinal length, it would be useful to clarify whether near-complete transduction is assumed, or if additional information on transduction efficiency can be provided.

(3) In Figure S10, the reduced MG proliferation observed in the CCA + Rbpj deletion group could also potentially reflect decreased GFAP promoter activity in dedifferentiated MG following Rbpj deletion. Alternatively, MG-derived cells may be more fragile under these conditions.

(4) In the CCA + Rbpj deletion condition, do MG undergo single or multiple rounds of cell division?

(5) What fraction of neuron-like cells (bipolar- and amacrine-like) arises from proliferation versus direct transdifferentiation? Quantification of MG-derived cells expressing neuronal markers (e.g., Otx2, HuC/D), with and without EdU labeling, would help distinguish these mechanisms.

(6) In Figure S18a, the authors state that "while the neuron-like clusters were best classified as BC-like and AC-like based on their distinct marker gene expression, they also exhibited mixed expression of genes associated with other retinal neuronal types, including RGC markers (e.g., Tubb3, Myt1l, Grin1) and photoreceptor markers (e.g., Crx, Prom1, Epha10, Gucy2e, Scg3) (Fig. S18a), suggesting that the regenerated cells exist in a hybrid state" and "MG derived neuron like cells also expressed genes characteristic of RGCs and photoreceptors, indicating enhanced lineage". However, many of these genes are not specific to RGCs or photoreceptors and are instead broadly expressed in retinal neurons or enriched in bipolar/amacrine populations. Therefore, it is unclear whether these cells exhibit hybrid RGC or photoreceptor identity.

(7) The authors provide a thorough molecular characterization of MG-derived cells through immunostaining and single-cell sequencing. However, their morphological features, synaptic connectivity (e.g., synaptic marker expression), and electrophysiological properties remain largely uncharacterized. While these experiments may be technically challenging, this limitation should be discussed.

(8) The conclusion that CCA + Rbpj deletion induces neurogenesis without compromising MG supportive functions or retinal homeostasis appears somewhat oversold. This claim is primarily based on gross retinal morphology and ZO-1 staining. Given the extent of MG dedifferentiation and ectopic cell generation in the ONL and INL, it is likely that retinal function is affected. Functional assessments (e.g., ERG) would be required to support this conclusion. The authors should consider tempering this statement.

(9) Regarding the mechanism by which CCA-induced proliferation enhances MG reprogramming in the Rbpj knockout background, one plausible explanation is that chromatin states (e.g., histone modifications and DNA methylation) are transiently reset during DNA replication and cell division. While this alone may be insufficient to activate neurogenic programs, it could synergize with Rbpj deletion to allow neurogenic transcription factors (such as Ascl1, Otx2, NeuroD1, and NeuroD2) to access previously inaccessible chromatin regions, thereby promoting MG reprogramming.

Reviewer #2 (Public review):

Summary:

The inability of the mammalian retina to regenerate poses a major clinical challenge. Much has been learned about the regenerative potential of the retina from teleost fish, where Müller glia (MG) are able to proliferate and produce new neurons after injury. However, MG do not retain this potential in the mammalian retina. The authors showed previously that forcing MG to re-enter the cell cycle by downregulating p27 and upregulating cyclin D1 could induce MG to dedifferentiate, but the results were transient, and these cells eventually reverted back to MG and did not form neurons. Here, they expand on this to show that in MG, coupling forced cell cycle re-entry with deletion of Rbpj, which inhibits the transcriptional effects of Notch signaling, induces some MG to proliferate and take on features of multiple cell types, including MG precursor cells, amacrine-like cells, and bipolar-like cells. This work lends valuable insight into the regenerative potential of mammalian MG, particularly when Notch signaling is manipulated.

Strengths:

The major claims of the authors are well-supported. They show convincingly - and through multiple methods including immunostaining, single-nucleus RNA sequencing, and in situ hybridization - that coupling notch inhibition with cell cycle reactivation induces the expression of neuronal markers in mammalian MG. The snRNA-seq data are particularly valuable in demonstrating the induction of bipolar-cell subtypes. Edu labeling is effective in demonstrating the induction of proliferation, and the long-term viability of the generated neuron-like cells is intriguing.

Weaknesses:

Whether the newly generated neurons are functionally integrated remains unclear, and the effect of the manipulation on the function of the retina was not tested. Imaging data suggests that many of the newly generated neurons persist for months, but often appear mislocalized. It is also not clear if the manipulation of MG affects long-term MG function. Cell death was not evaluated, and although the authors evaluated the long-term effect on tight junctions, this data was not quantified, and further analysis on morphology or function was not done. Control eyes were untreated, not vehicle-injected.

Reviewer #1 (Public review):

Summary:

This interesting paper probes the problematic relationships between the classical "spiralian" taxa, i.e., annelids, molluscs, brachiopods, platyhelminths and nemerteans, and shows that the branches leading to them are so short as to be unreliable guides to their relationships. This, in turn, has important implications for how we view the origin of the animal phyla.

Strengths:

A very careful analysis of a famous old problem with quite significant results. The results seem to be robust and support their conclusions.

It often passes uncommented that many different trees are published about animal relationships, yet some parts of the tree seem extremely difficult to resolve; the spiralians are perhaps the most difficult case. More recently, problems about sponges or ctenophores as sister groups to the rest of the animals have alerted us to major areas of uncertainty in large-scale phylogenetic reconstruction; this paper is a welcome reminder that other, perhaps even harder, problems exist which may be difficult to ever resolve with the (molecular) data we have.

Weaknesses:

The paper could have perhaps drawn out some of the implications of its results in a clearer manner.

Reviewer #2 (Public review):

Summary:

The relationships among the phyla making up Spiralia - a major clade of animals including molluscs, annelids, flatworms, nemerteans and brachiopods - have been challenging from a phylogenomic perspective despite decades of molecular phylogenetic effort. Every topology uniting subsets of these phyla has been recovered with apparent support in at least one study, yet no consensus has emerged even from large-scale genomic datasets. Serra Silva and Telford set out to determine whether this instability reflects a genuine biological signal being obscured by analytical limitations, or whether it reflects a rapid, near-simultaneous origin of these phyla that has left behind in modern genomes far too little phylogenetic information to resolve. They focused deliberately on five phyla, reducing the problem to a tractable set of 15 unrooted and 105 rooted topologies, and applied a suite of complementary approaches across two independent datasets and multiple substitution models to test whether any topology is significantly preferred over alternatives.

Strengths:

(1) The conceptual framing of the problem is excellent, and the study makes a convincing case across several lines of evidence. By enumerating all possible topologies and demonstrating empirically that every one of the 15 unrooted arrangements has been recovered as the preferred solution in at least one published study, the authors make a strong argument about the state of the field. The use of two entirely independent datasets as a consistency check is great, and convergence between them, where it occur,s substantially strengthens confidence in the conclusions.

(2) It is my view that the simulation framework is a particular strength. Generating data on a fully unresolved star tree and scoring those data under both correctly-specified and misspecified substitution models provides convincing evidence that the strong preference for rooting Spiralia on the flatworm branch is, at least partly, an analytical artefact driven by the exceptionally long branch in combination with compositional heterogeneity across sites. This is an important methodological demonstration with implications beyond spiralian phylogenetics, as the same issue is likely to affect other deep, long-branched lineages in the animal tree of life.

(3) The randomised taxon-jackknifing approach is a very nice addition here. The demonstration that preferred topologies shift depending on which species happen to be sampled (even within the same phylum) is a convincing indicator of weak signal, and provides a practical caution for future studies that may report strong support for a particular spiralian arrangement based on a fixed taxon sample.

(4) The branch-length analyses, benchmarking internal interphylum branches against the already disputed and extremely short branch uniting deuterostomes (work also by this group), are well-conceived and solid.

(5) I think it is worth highlighting the notable intellectual honesty throughout the paper: the authors do not overstate their results, correctly acknowledging that while the unrooted topology grouping molluscs with brachiopods and flatworms with nemerteans emerges most consistently, this preference is not statistically significant under more adequate substitution models and may itself carry some artefactual component.

Weaknesses:

(1) The restriction to five phyla is the most significant limitation, as the authors acknowledge this and give a clear computational justification, but readers should be aware that the paper's convincing conclusions apply specifically to the five focal phyla and the evidence remains incomplete with respect to spiralian phylogeny as a whole.

(2) The treatment of substitution model adequacy, while commendably thorough for site-heterogeneous models, is necessarily bounded. The authors note that models accounting for non-stationarity, across-lineage compositional heterogeneity, or mixtures of tree histories might yield different results, and that even the most sophisticated currently available approaches have not produced consistent spiralian topologies across studies. This is not a criticism of what has been done here - the analytical scope is reasonable and well-implemented - but it means the paper cannot be read as a definitive demonstration that no model will ever resolve these relationships. The distinction between a true hard polytomy and a radiation that is effectively unresolvable given current data and methods could be drawn more sharply in the discussion.

(3) The reticulation-aware coalescent analyses are presented somewhat briefly relative to the likelihood-based topology scoring. The finding that flatworms are recovered within a paraphyletic jaw-bearing animal clade in both summary trees - interpreted as long-branch attraction - is striking, and its implications for gene-tree-based approaches to spiralian rooting deserve more discussion than they currently receive.

(4) The central conclusions - that interphylum branches in Spiralia are extraordinarily short, that topological preferences are strongly model-dependent and taxon-sampling-sensitive, and that an ancient rapid radiation is the most parsimonious explanation - are convincingly supported by the evidence presented. The identification of flatworm long-branch attraction as an important confounding factor in rooting analyses is itself an important and well-demonstrated result.

Conclusion:

This paper clearly makes an important contribution to the ongoing debate about spiralian relationships and, more broadly, to methodological discussions about how to handle anciently diversified clades where phylogenetic signal is genuinely limited. The exhaustive topology-scoring framework combined with taxon-jackknifing and simulation under unresolved trees is a valuable methodological template that could usefully be applied to other notoriously difficult nodes in the animal tree. I thoroughly enjoyed the discussion of the implications of these findings for interpreting Cambrian fossils and the evolutionary history of shells, segmentation, larval types and other characters - it is both thoughtful and thought-provoking and will be of broad interest well beyond the phylogenomics and zoology communities. From a very practical perspective, the data and scripts provided make the work useful to researchers wishing to apply similar approaches to other groups.

Reviewer #3 (Public review):

Summary:

This paper addresses the controversial internal relationships within the Spiralia, a major clade of invertebrate animals including molluscs, annelids, brachiopods and flatworms.

Strengths:

Performs a range of empirical analyses and simulations that address the core question. Although a favoured unrooted topology finds some support, this is not strongly endorsed in the paper.

Weaknesses:

(1) Only considers a subset of relevant phyla (e.g. gastrotrichs are relevant to the phylogenetic position of Platyhelminthes), although how this would change the scale of the analyses (i.e. number of topologies) is addressed in the paper.

(2) Discussion of Spiralia evolution and broader context, particularly the relevance for the fossil record. Line 448: our current understanding of the early spiralian fossil record is quite consistent with the main results of this paper. For example, there are very few claims for fossils that sit on the short branch leading to Spiralia (or Lophotrochozoa as defined here) that this paper discusses. Many of the key fossils that inform on the characters discussed in the introduction, which have unusual character combinations, have an apomorphy of one of the phyla discussed, and so are resolved as members of the stem lineages of particular phyla.

(3) This is what you would expect with long phylum stem lineages (line 148) and a short spiralia stem lineage. For example, the mollusc Wiwaxia has chaetae, but a mollusc like Radula (Smith 2012), the conchiferan mollusc Pelagiella has chaetae and a coiled shell (Thomas et al. 2020). The only fossil groups that are routinely discussed as belonging to the stem lineage of more than one phylum are the tommotiids, which have chaetae, segmentation and a complex mineralised skeleton (but not shells in the brachiopod/mollusc sense, see Guo et al 2023) but they sit on the lophophorate stem lineage, a synapomorphy rich group the monophyly of which the present paper endorses (e.g. line 435). The fossil record is consistent with the scenario presented in line 442, e.g. convergent loss or reduction of chaetae and segmentation and convergent evolution of shells in molluscs and brachiopods.

Reviewer #1 (Public review):

This study integrates Xenium spatial transcriptomics of paired inflamed and uninvolved Crohn's disease tissues with functional analyses in a csf2rb-/- larval zebrafish DSS intestinal injury model to investigate the spatial and cell-type-specific roles of GM-CSF. The work is limited mechanistically and adds little to an already disputed field: GM-CSF's role in intestinal inflammation is context-dependent and extensively studied in mice and humans, and this study does not resolve these controversies. The zebrafish appears to be a poor model for these questions: it lacks mammalian intestinal architecture, complex microbiota, and clearly validated functional ILC populations. Putative ILC1s are poorly defined based on stress-response gene modules, while ILC3s are somewhat better characterized, but overall, the system does not allow mechanistic insights into GM-CSF regulation of ILCs. The DSS experiments largely recapitulate the known protective effects of GM-CSF in epithelial injury without clarifying underlying mechanisms.

Figure 1

GM-CSF expression is extremely sparse, rarely exceeding 0.005 frequency even in inflamed regions. The authors should acknowledge this and discuss why. Xenium could be used to characterize the niche around GM-CSF-producing cells, but no new cellular circuit is revealed beyond known myeloid-lymphoid interactions.

Figure 2

Colon length in DSS colitis is not decreased in Csf2rb⁻/⁻ versus wild-type zebrafish under untreated conditions, suggesting endogenous GM-CSF has minimal impact. In Figure 2E, Tg(mpeg1:mCherry) larvae show staining in vessel- or epithelial-like structures expressing Csf2rb, which does not resemble macrophages and requires clarification. pSTAT5 is upregulated with GM-CSF treatment, but the responding cell types are unclear.

Figure 3

Putative ILC1s are defined by stress-response gene modules rather than canonical markers. Overlapping genes with human (HSP90AA1, UBB, MCL1, DOK2) do not indicate ILC1 identity, which is described by IL7R, KLRB1, or TBX21 expression in the human Xenium dataset. ILC2s were not detected, and Ifng expression is broadly distributed, making attribution to ILC1s uncertain. ILC3s are somewhat better defined, but overall, the data do not support mechanistic conclusions about GM-CSF regulation of ILC populations.

Reviewer #2 (Public review):

The authors show that GM-CSF prevents the loss of ILC3 populations and inhibits pro-inflammatory cytokine production during gut inflammation. They combine a preclinical model of gut inflammation in zebrafish with spatial transcriptomic analysis of samples from Crohn's disease patients. The data show that GM-CSF ameliorates gut inflammation by (1) curtailing the differentiation of disease-associated ILC1 and (2) by "boosting" the tissue repair function of ILC3.

The topic of the manuscript is interesting. However, there are various limitations that are summarized below.

(1) The main finding of the manuscript, that GM-CSF maintains ILC3 populations, is not analyzed in depth. Since the authors' own data and other publications show that the receptors for GM-CSF are expressed in myeloid cells, a better analysis of the transcriptional changes of these populations upon GM-CSF administration is needed.

(2) The authors could compare the transcriptome of macrophages and monocytes from inflamed and uninvolved sections in their Xenium dataset. In addition, investigating how zebrafish macrophages change due to the lack of GM-CSF and comparing them with the human findings would add to the data.

(3) Since the authors developed a novel mutation in zebrafish that is predicted to affect myeloid populations, a detailed characterization of the myeloid immune compartment in these organisms is missing.

(4) Niche analysis in the Xenium slides could provide direct evidence on how macrophages close to ILC3 are different from those closer to other cell types, like ILC1.

Reviewer #1 (Public review):

Summary:

The authors sought to define the molecular mechanism by which the adaptor protein Egalitarian (Egl) recognizes and binds specific mRNA localization signals -- in particular, the K10 transport and localization signal (TLS) -- to initiate dynein-based transport in Drosophila. In doing so, they identified the minimal Egl domains required for RNA binding, determined the atomistic structure of the Egl-RNA complex, and explored the recognition mechanism (shape vs. structure). They furthermore performed in vivo functional validation using CRISPR-mediated genome editing in Drosophila that showed that the identified binding residues are biologically essential.

Strengths:

The authors provided a detailed crystal structure of the Egl-RNA complex at high resolution. In particular, they used a MBP-fusion crystallization driver to be able to resolve the flexible C-terminal domain of Egl (EHD). The authors' use of an integrative approach combining X-ray crystallography with binding assays and in vivo functional validation provides compelling evidence for their claims.

The work provides a detailed interaction mapping that identifies the protein residues responsible for the electrostatic interaction with the RNA. In doing so, the work explains how Egl can recognize diverse RNA sequences by demonstrating that Egl binds primarily to the phosphate backbone and specific structural bulges, providing a plausible model for how one protein can recognize many different localization signals that share little sequence similarity.

Weaknesses:

Discrepancy in the stoichiometric Egl-to-RNA ratio (the structural data in the paper indicate a 1:1 ratio, whereas previous single-molecule transport studies suggest a 2:1 ratio) remains unanswered, with the likely explanation that the truncated version of the protein might not capture the full (native) assembly. While the authors acknowledge this in the Discussion, the paper would benefit from this issue being raised earlier, already in the Results section. Moreover, there is a notable omission of a recent preprint on a very similar topic [https://www.biorxiv.org/content/10.1101/2025.08.02.668268v1.full].

In vitro, Egl shows a relatively high affinity for non-target RNAs such as the MS2 loop, whereas it is highly selective in vivo. Is it possible that other cofactors are required for the high-fidelity sorting not present in the study? Testing binding in the presence of co-factors (BicD or Dlc) could indicate whether they increase the specificity for target RNAs over non-target ones.

Including a more diverse set of size-matched RNA controls would have significantly strengthened the paper's claims regarding specificity. Using RNAs that mimic K10 TLS would have provided a more rigorous test of the shape-recognition by Egl - using, for instance, decoy RNAs of the same length but with differently positioned bulges (or no bulges at all) or testing other known localization signals (like bicoid or hairy) of similar length.

Appraisal of aims:

The authors successfully determined the crystal structure of the Egl-RNA complex, identifying a modular binding surface composed of the EXO domain, a helical linker, and the EHD. They effectively demonstrated that Egl uses a combination of shape-specific recognition (targeting RNA bulges) and sequence-specific interactions (bonding with specific bases), and confirmed the biological necessity of these findings by showing that mutating the identified residues in living flies leads to infertility and oocyte differentiation defects. These results provide robust evidence for the authors' claims that they have defined a minimal RNA localization signal. In particular, the correlation between the L-Triple mutation's binding defect and its total sterility in flies provides proof that the identified binding surface is the functional one. While the 1:1 stoichiometry remains a point for further investigation, the authors transparently address that full-length transport may require a 2:1 assembly, suggesting their structure represents the fundamental building block of that larger complex.

Impact of the work on the field:

This study provides a high-resolution picture of how a dynein adaptor recognizes its cargo. It moves the field from predictive models to atomic-level certainty, setting a benchmark for studying other similar transport complexes. By proving that Egl recognizes RNA shape (bulges) as much as sequence, the work changes the outlook on the search for localization signals in other genomes, moving beyond simple sequence motifs to 3D structural signatures. The coordinates deposited in the EBI (IDs: 9UJU, 9UJY, 9UUG) provide a resource for the modelling of higher-order transport complexes. The identification of specific residues (e.g., the L-Triple) provides the community with tools to disrupt RNA transport in Drosophila without destroying the entire protein, allowing for more nuanced studies of development.

Reviewer #2 (Public review):

Summary:

Hong et. al. aimed to elucidate the structural basis of the Egalitarian recognition of the K10 mRNA. Using X-ray crystallography and several biochemical, biophysical, and cellular techniques, they were able to shed light on the formation, stability, and basis of interaction of the complex. The authors successfully accomplished their goal.

Strengths:

The experiments are well-performed and convincing. The manuscript is well-written.

Weaknesses:

(1) Some statistical analysis would improve the manuscript. In particular, the manuscript has several results that are based on comparisons, such as Kd. Adding p-values for significance is recommended, and this would improve the treatment of data.

(2) When showing interactions (dotted lines) in structural figures, adding the distance would be useful and is recommended.

(3) Additional SI Figure. It would enrich the manuscript to have the composite simulated annealing-omit 2|Fo| - |Fc | electron density maps for the structures contoured at a given sigma, superimposed on the final refined model. This would represent how well the data fits into the model.

Reviewer #1 (Public review):

Summary:

Zare‑Eelanjegh et al. investigate how the endoplasmic reticulum, the nucleus, and the cell periphery are mechanically linked by indenting intact cells with specially shaped atomic‑force probes that double as drug injection devices. Fluorescence‑lifetime imaging of the membrane tension reporter Flipper‑TR reveals that these three compartments are mechanically linked and that the actin cytoskeleton, microtubules, and lamins modulate this coupling in complex ways.

Strengths:

* The study makes an important advance by applying FluidFM to probe organelle mechanics in living cells, a technically demanding but powerful approach.

* Experimental design is quantitative, the data are clearly presented, and the conclusions are broadly consistent with the measurements.

Weaknesses:

* Calcium‑dependent effects: Indentation can evoke cytoplasmic Ca²⁺ elevations that drive myosin contraction and reshape the internal membrane network (e.g., vesiculation: PMID : 9200614, 32179693) possibly confounding the Flipper-TR responses; without simultaneous/matching Ca²⁺ imaging, cell viability assays (e.g., Sytox), and intracellular Ca²⁺ sequestration or myosin inhibition experiments, a more complex mechanochemical coupling cannot be excluded, weakening conclusions.

* Baseline measurements: Flipper‑TR lifetime images acquired without indentation do not exclude potential light‑induced or time‑dependent changes, which weakens the conclusions.

* Indentation depth versus nuclear stiffness/tension: Because lamin‑A/C depletion softens nuclei, a given force may produce a deeper pit and thus greater membrane stretch. It is unclear how the cytoskeletal perturbations affect indentation depth, which weakens the conclusions.

Comments on revisions:

With their responses, the authors have relieved my initial concerns.

Reviewer #2 (Public review):

Summary

This valuable study combines atomic force microscopy with genetic manipulations of the lamin meshwork and microinjection of cytoskeletal depolymerizing drugs to probe the mechanical responses of intracellular organelles to combinations of cytoskeletal perturbations. This study demonstrates both local and distal responses of intracellular organelles to mechanical forces, and shows that these responses are affected by disruption of the actin, microtubule, and lamin cytoskeletal systems.

Strengths:

This study uses a sensitive micromanipulation system to apply and visualize the effects of force on intracellular organelles.

Reviewer #1 (Public review):

Summary:

In the manuscript entitled 'The Role of ATP Synthase Subunit e (ATP5I) in 1 Mediating the Metabolic and Antiproliferative 2 Effects of Biguanides', Lefrancois G et al. identifies ATP5I, a subunit of F1Fo-ATP synthase, as a key target of medicinal biguanides. ATP5I stabilizes F1Fo-ATP synthase dimers, essential for cristae morphology, but its role in cancer metabolism is understudied. The research shows ATP5I interacts with a biguanide analogue, and its knockout in pancreatic cancer cells mimics biguanide treatment effects, including altered mitochondria, reduced OXPHOS, and increased glycolysis. ATP5I knockout cells resist biguanide-induced antiproliferative effects, but reintroducing ATP5I restores the effects of metformin and phenformin. These findings highlight ATP5I as a promising mitochondrial target for cancer therapies. The manuscript is well written.

Strengths:

Demonstrated the experiments in a systematic and well accepted methods

Weaknesses:

Significance of the target molecule and mechanisms may help in understanding the molecular mechanisms of metformin.

Comments on revisions:

In the revised manuscript, the authors addressed all the queries.

Reviewer #2 (Public review):

Summary:

The mechanism(s) by which the therapeutic drug metformin lowers blood glucose in type 2 diabetes and inhibits cell proliferation at higher concentrations remain contentious. Inhibition of complex 1 of the mitochondrial respiratory chain with consequent changes in cellular metabolites which favour allosteric activation of phosphofructokinase-1, allosteric inhibition of fructose bisphosphatase-1 and cAMP signalling and activation of AMPK which phosphorylates transcription factors are candidate mechanisms. The current manuscript proposes the e-subunit of ATP-synthase as a putative binding protein of biguanides and demonstrates that it regulates the expressivity of the Complex 1 protein NDUFB8.

Strengths:

(1) The metformin conjugate and metformin show comparable efficacy on inhibition of cell proliferation in the millimolar range.

(2) Demonstration of compromised expression of the Complex I protein NDUFB8 by the ATP5I knock out and its reversal by ATP5I expression is an important strength of the study. This shows that the decreased "sensitivity" to metformin in the ATP5I knock out cells could be due to various proteins.

(3) Demonstration of converse effects of ATP5I KO and re-expression ATP5I on the NAD/NADH ratio.

Weaknesses:

(1) The interpretation of the cellular co-localization of the biotin-biguanide conjugate with TOMM20 (Figure 1-D) as mitochondrial "accumulation" of the conjugate is overstated because it cannot exclude binding of the conjugate to the mitochondrial membrane. It would have been more convincing if additional incubations with the biotin-biguanide conjugate in combination with metformin had shown that metformin is competitive with the biotin-conjugate.

(2) The manuscript reports the identification of 69 proteins by mass spectrometry of the pull-down assay of which 31 proteins were eluted by metformin. However, no Mass Spectrometry data is presented of the peptides identified. The methodology does not state the minimum number of peptides (1, 2?) that were used for the identification of the 31/69 proteins.

(3) The validation of ATP5I was based on the use of recombinant protein (which was 90% pure) for the SPR and use of a single antibody to ATP5I. The validity of the immunoblotting rests on the assumption that there is no "non-specific" immunoactivity in the relevant mol wt range. Information on the validation of the antibody would be helpful.

(4) Knock-out of ATP5I markedly compromised the NAD/NADH ratio (Fig.3A) and cell proliferation (Fig.3D). These effects may be associated with decreased mitochondrial membrane potential which could explain the low efficacy for metformin (and most of the data in Figs 3-5). This possibility should be discussed. Effects of [metformin] on the NAD/NADH ratio in control cells and ATP5I-KO would have been helpful because the metformin data on cell growth is normalized as fold change relative to control, whereas the NAD/NADH ratio would represent a direct absolute measurement enabling comparison of the absolute effect in control cells with ATP5I KO.

(5) Figure-6 CRISPR/Cas9 KO at 16mM metformin in comparison with 70nM rotenone and 2 micromolar oligomycin (in serum containing medium). The rationale for use of such a high concentration of metformin has not been explained. In liver cells metformin concentrations above 1mM cause severe ATP depletion, whereas therapeutic (micromolar) concentrations have minimal effects on cellular ATP status. The 16mM concentration is ~2 orders of magnitude higher than therapeutic concentrations and likely linked to compromised energy status. The stronger inhibition of cell proliferation by 16mM metformin compared with rotenone or oligomycin raises the issue whether the changes in gene expression may be linked to the greater inhibition of mitochondrial metabolism. Validation of the cellular ATP status and NAD/NADH with metformin as compared with the two inhibitors could help the interpretation of this data.

Comments on revisions:

No further comments.

Reviewer #3 (Public review):

Most of the data are based on measurements of the oxygen consumption rate (OCR) and extracellular acidification rate (ECAR) measured by the Seahorse analyser in control and ATP5l KO cells. However, these measurements are conducted by a single injection of a biguanide, followed over time and presented as fold change. By doing so, the individual information of the effect to of metformin and derivate on control and KO cells are lost. In addition, the usual measurement of OCR is coupled with certain inhibitors and uncouplers, such as oligomycin, FCCP and Antimycin A/rotenone, to understand the contribution of individual complexes to the respiration. Since biguanides and ATP5l KO affect protein levels of components of complex I and IV, it would be informative to measure their individual contributions/effects in the Seahorse. To further strengthen the data, it would be helpful to obtain measurements of actual ATP levels in these cells, as this would explain the activation of AMPK.

The authors report on alterations in mitochondrial morphology upon ATP5l KO, which is measured by subjective quantifications of filamentous versus puncta structures. Fiji offers great tools to quantify the mitochondrial network unbiased and with more accuracy using deconvolution and skeletonization of the mitochondria, providing the opportunity to measure length, shape and number quantitatively. This will help to understand better, whether mitochondria are really fragmented upon ATP5l KO and rescued by its re-introduction.

Finally, the authors report in the last part of the paper a genetic CRISPR/Cas9 KO screen in NALM-6 cells cultured with high amounts of metformin to identify potential new mediators of metformin action. It is difficult to connect that to the rest of the paper, because a) different concentrations of metformin are used and b) the metabolic effects on energy consumption are not defined. They argue about molecular function of the obtained hits based on literature, and on comparison the pattern of genetic alterations based on treatments with known inhibitors such as oligomycin and rotenone. However, a direct connection is not provided, thus the interpretation at the end of the results that "the OMA1-DEL1-HRI pathway mediates the antiproliferative activity of both biguanides and the F1ATPase inhibitor oligomycin" while increasing glycolysis, needs to be tuned down. This is an interesting observation, but no causality is provided. In general, this part stands alone and needs to be better connected to the rest of the paper.

Comments on revisions:

Thanks to the authors for addressing the concerns raised during the review of the original manuscript. The data now include proper measurements of OCR and quantifications of the mitochondria network. The screening data is better connected to the rest of the paper and provide compelling evidence for mitochondria and in particular the ATP synthase as potential targets of metformin.

Joint Public Review:

Summary

Riva et al. introduce a semi-automatic setup for measuring Drosophila melanogaster oviposition rhythms and use it to map the timekeeping function underlying egg laying rhythms to a subset of clock cells. Using a combination of neurogenetic manipulations and referencing the publicly available female hemi-brain connectome dataset, they narrow the critical circuit down to two of the three CRYPTOCHROME expressing lateral-dorsal neurons (CRY[+] LNds). Their findings suggest that different overlapping sets of clock neurons may control different behavioral rhythms in D. melanogaster.

This work will be of interest to researchers interested in the circadian regulation of oviposition in D. melanogaster (and possibly other insects), a phenomenon which has been left relatively under-explored. The construction of a semi-automated setup which can be made relatively cheaply using available motors and 3D printed molds provides a useful model for obtaining longer records of oviposition activity.

Strengths

The authors use a semi-automated monitoring system to detect circadian egg laying rhythms in spite of inherently noisy data. Using this approach they use a variety of different genetic tools to show that CRY+ LNds play a role in generating the circadian rhythm of oviposition, that PDF-expressing neurons seem to be important for maintaining the circadian period of egg laying, and that period locus function is required for the circadian rhythmicity of oviposition. The authors also point to some potentially interesting connectome data that suggest hypotheses regarding the neuronal circuit linking daily timekeeping to oviposition, which will require further validation in future studies.

Weaknesses:

The major weaknesses of this work result from the noisy nature of the data, and the need to average the individual records of many animals in order to extract significant rhythmicity values. The predicted neural output pathways will require validation in future studies.

Reviewer #2 (Public review):

Summary:

Shahbazi et al. trained recurrent neural networks (RNNs) to simulate human upper limb movement during adaptation to a force field perturbation. They demonstrated that throughout adaptation, the pattern of motor commands to the muscles of the simulated arm changed, allowing the perturbed movements to regain their typical, perturbation-free straight-line paths. After this initial learning block (FF1), the network encountered null-fields to wash out the adaptation, before re-experiencing the force in a second learning block (FF2). Upon re-exposure, the network learned faster than during initial learning, consistent with the savings observed in behavioral studies of adaptation. They also found that as the number of hidden units in the RNN increased, so did the probability of exhibiting savings. The authors concluded that these results propose a neural basis for savings that is independent of context and strategic processes.

Strengths:

The paper addresses an important and controversial topic in motor adaptation: the mechanism underlying motor memory. The RNN simulation reproduces behavioral hallmarks of adaptation, and it provides a useful illustration of the pattern of muscle activity underlying human-like movements under both normal and perturbing conditions. While the savings effect produced by the network, though significant, appears somewhat small, the simulation demonstrating an increase in savings with a greater number of hidden units is particularly intriguing.

Main weakness:

The introduction details the ongoing debate in the literature regarding the mechanisms underlying savings, particularly whether it stems from explicit or implicit learning processes. However, it remains unclear how the current work addresses this debate. There is already a considerable body of research, particularly in visuomotor adaptation, demonstrating that savings is predominantly driven by explicit strategies (e.g., Morehead et al. 2015, Haith et al., 2015; Huberdeau et al., 2019; Avraham et al., 2021). Furthermore, there have been multiple reports that implicit adaptation exhibits attenuation upon relearning (Avraham et al., 2021, Leow et al., 2020; Yin and Wei, 2020; Hamel et al., 2021; Hamel et al., 2022; Wang and Ivry, 2023; Hadjiosif et al., 2023). In the discussion, the authors acknowledge that their goal was not to model a complete explicit-implicit system, but rather to probe how savings may emerge from a purely implicit mechanism. Given the central debate introduced by the authors, the manuscript would benefit from a more detailed discussion explaining how their findings elucidate the specific conditions under which savings emerge from purely implicit mechanisms versus when cognitive strategies predominate.

Reviewer #1 (Public review):

[Editors' note: The Reviewing Editor has assessed the revised manuscript without seeking further input from the original reviewers. The authors have addressed the main points raised during peer review, including clarifying methodological differences with prior work, providing additional analysis, and expanding the discussion of potential mechanisms. These revisions strengthen the interpretation and presentation of the findings, and the conclusions remain supported by the data.]

Summary:

Ritzau-Jost et al. investigate the potential contribution of AP broadening in homeostatic upregulation of neuronal network activity with a specific focus on dissociated neuronal cultures. In cultures obtained from a few brain regions from mice or rats using different culture conditions and examined by different laboratories, AP half-width remained stable despite chronic activity block with TTX. The finding suggests that AP width is not significantly modulated by changes in sodium channel activity.

Strengths:

The collaborative nature of the study amongst the neuronal culture experts and the rigorous electrophysiological assessments provides for a compelling support of the main conclusion.

Reviewer #2 (Public review):

Summary:

This study reexamined the idea that action potential broadening serves as a homeostatic mechanism to compensate for changes in network activity. The key finding was that, while action potential broadening does occur in certain neurons - such as CA3 pyramidal cells-it is far from a universal response. This is important because it helps resolve longstanding discrepancies in the field, thereby contributing to a better understanding of network dynamics. The replication of these findings across multiple laboratories further strengthened the study's rigor.

Strengths:

Mechanisms of network homeostasis are essential to understand network dynamics.

Reviewer #3 (Public review):

Summary:

The manuscript "Unreliable homeostatic action potential broadening in cultured dissociated neurons" by Ritzau-Jost et al. investigates action potential (AP) broadening as a mechanism underlying homeostatic synaptic plasticity. Given the existing variability in the literature concerning AP broadening, the authors address an important and timely research question of considerable interest to the field.

The study systematically demonstrates cell-type- and model-specific AP broadening in hippocampal neurons after chronic treatment with either tetrodotoxin (TTX) or glutamatergic transmission blockers. The findings indicate AP broadening in CA3 pyramidal neurons in organotypic cultures after TTX treatment, but notably not in dissociated hippocampal neurons under identical conditions. However, blocking glutamatergic neurotransmission caused AP broadening in dissociated hippocampal neurons. Moreover, extensive evaluations in neocortical dissociated cultures robustly challenge previous findings by revealing a lack of AP broadening following TTX treatment. Additionally, the proposed role of BK-type potassium channels in mediating AP broadening is convincingly questioned through complementary electrophysiological and voltage-imaging experiments.

Strengths:

The manuscript exhibits an outstanding experimental design, employing state-of-the-art techniques and a rigorous multi-lab validation approach that greatly enhances scientific reliability. The experimental results are meticulously illustrated, and the conclusions drawn are justified and supported by the presented data. Furthermore, the manuscript is comprehensively and clearly written.

Reviewer #1 (Public review):

Summary:

The authors investigated the role of an E3 ubiquitin ligase ITCH in regulating the viral life cycle of SARS-CoV-2. The authors showed that ITCH mediates ubiquitination of the membrane (M) and envelope (E) proteins of SARS-CoV-2. Ubiquitination of E and M result in enhanced interactions between the structural proteins and redistribution of the structural proteins into autophagosomes. The authors claim that the enhanced interactions between structural proteins and trafficking of the structural proteins into autophagosomes contribute to SARS-CoV-2 replication and egress, prompting ITCH as a potential antiviral target. ITCH also alters the cellular distribution of host proteases important for spike cleavage which protect and stabilize spike with cleavage. The authors also demonstrated that SARS-CoV-2 replication is augmented by ITCH in which virus replication is significantly impaired in cells lacking ITCH expression.

Strengths:

The authors provided high quality data with appropriate experimental controls to justify their claims and conclusions. The mechanistic analyses are excellent and presented in a logical manner. The investigation of the role of ubiquitination in coronavirus assembly and egress is novel as most previous studies focused on its role in mediating innate immune responses.

Comments on revisions:

The authors have addressed my previous concerns.

Reviewer #1 (Public review):

Summary:

In this remarkable study, the authors use some of their recently-developed oxytocin receptor knockout voles (Oxtr1-/- KOs) to re-examine how oxytocin might influence partner preference. They show that shorter cohabitation times leads to decreased huddling time and partner preference in the KO voles, but with longer periods preference is still established, i.e., the KO animals have a slower rate of forming preference, or are less sensitive to whatever cues or experiences lead to the formation of the pair bond as measured by this assay. This helps relate the authors recent study to the rest of the literature on oxytocin and partner preference in prairie voles. To better understand what might lead to slower partner preference, they quantified changes to the durations and frequency of huddling. In separate assays they also found that Oxtr1-/- KOs interacted more with stranger males than wild-type females. In a partner choice assay they found that wild-type males prefer wild-type females more than Oxtr1-/- KO females. They then performed bulk RNA-Seq profiling of nucleus accumbens of both wild-type and Oxtr1-/- KO males and females, either housed with animals of the same sex or paired with a wild-type of opposite sex. 13 differentially expressed genes were identified, mostly due to downregulation in wild-type females. These genes were also identified in a module lost in the Oxtr1-/- voles by correlated expression profiling. They also compared results of transcriptional profiling in female and male wild-type vs Oxtr1-/- voles (independently of bonding state), and found hundreds of differentially expressed genes in nucleus accumbens, mostly in females and often with some relation to neural development and/or autism. Some of the reduction in transcript was confirmed with in situs, as well as compared to changes in transcription in the lateral septum and paraventricular nucleus (PVN) of the hypothalamus. Finally they find fewer oxytocin+ and AVP+ neurons in the anterior PVN.

Strengths:

This is an important study helping to reveal the effects of oxytocin receptor knockout on behavior and gene expression. The experiments are thorough and reveal a surprising number of genetic and anatomical differences, with some sexual dimorphism as well, and the authors have more carefully examined the behavioral changes after shorter and longer periods of partner preference formation.

Weaknesses:

It is surprising that given all the genetic changes identified by the authors, that the behavioral phenotypes are fairly mild. The extent of gene changes also might be under-reported given the variability in the behavior and relative low number of animals profiled.

Comments on revisions:

No further recommendations. I commend the authors for finding the typos in their first version and correcting the manuscript.

Reviewer #1 (Public review):

The authors investigated the response of worms to the odorant 1-octanol (1-oct) using a combination of microfluidics-based behavioral analysis and whole-network calcium imaging. They hypothesized that 1-oct may be encoded through two simultaneous, opposing afferent pathways: a repulsive pathway driven by ASH, and an attractive pathway driven by AWC. And the ultimate chemotactic outcome is likely determined by the balance between these two pathways.

It is not surprising that 1-octanol is encoded as attractive at low concentrations and repulsive at higher concentrations. However, the novel aspect of this study is the discovery of the combinatorial coding of 1-oct in the periphery, where it serves as both an attractant and a repellent. Furthermore, the study uses this dual encoding as a model to explore the neural basis of sensory-driven behaviors at a whole-network scale in this organism. The basic conclusions of this study are well supported by the behavioral and imaging experiments, though there are certain aspects of the manuscript that would benefit from further clarification.

A key issue is that several previous studies have demonstrated a combinatorial and concentration-dependent coding of odorant sensing in the nematode peripheral nervous system. Specifically, ASH and AWC are the primary receptors for repellent and attractive responses, respectively. However, other neurons such as AWB, AWA, and ADL are also involved in the coding process. These neurons likely communicate with different interneurons to contribute to 1-oct-induced outputs. The authors' conclusion that loss of tax-4 reduces attractive responses and that osm-9 mutants reduce repulsive responses is not entirely convincing. TAX-4 is required for both AWC (an attractive neuron) and AWB (a repulsive neuron), and osm-9 is essential for ASH, ADL, and AWA (attraction-associated). Therefore, the observed effects on the attractive and repulsive responses could be more complex. Additionally, the interpretation of results involving the use of IAA to reduce the contribution of AWC at lower concentrations lacks clarity.

The authors did not observe any increased correlation between motor command interneurons and sensory neurons, which is consistent with the absence of a consistent relationship between state transitions and 1-oct application. Furthermore, they did not observe significant entrainment of AIB activity with the 2.2 mM 1-oct application. This might be due to the animals being anesthetized with 1 mM tetramisole hydrochloride, which could affect neural activity and/or feedback from locomotion.

Comments on revisions:

The authors have addressed all my previously raised concerns.

Reviewer #2 (Public review):

Summary:

The authors used whole-network imaging to identify sensory neurons that responded to the repellant 1-octanol. While several olfactory neurons responded to the initial onset of odor pulses, two neurons consistently responded to all the pulses, ASH and AWC. ASH typically activates in response to repellants, and AWC typically activates in response to the removal of attractants. However in this case, AWC activated in response to the removal of 1-octanol, which was unexpected because 1-octanol is a harmful repellant to the worm. The authors further investigated this phenomenon by testing different concentrations of 1-octanol in a chemotaxis assay, and found that at lower (less harmful) concentrations the odor is actually an attractant, but becomes repulsive at higher concentrations. The amplitude of the ASH response appeared to be modulated by concentration, but this was not true for AWC. The authors propose a model where the behavioral response of the worm is the result of integrating these two opposing drives, where repulsion is a result of the increased ASH activity over-riding the positive drive from AWC. The authors further tested this theory by testing mutants that ablated the AWC response (tax-4 or AWC::HisCl) or ASH response (osm-9 or ASH::HisCl). The chemo-silencing (HisCl) and tax-4 experiments were consistent with their hypothesis, while the osm-9 mutation had a limited impact on chemotaxis behavior, highlighting the potential role of osm-9-independent signaling in ASH in response to 1-octanol. While the interneuron(s) that integrate these signals to influence behavior were not identified, the authors did find that increasing concentrations of 1-octanol did increase the likelihood of AVA activity, a neuron which drives reversals (and hence, behavioral repulsion).

Strengths:

This was simple and elegant work that identified specific neurons of interest which generated a hypothesis, which was further tested with mutants that altered neuronal activity. The authors performed both neuronal imaging and behavioral experiments to verify their claims.

Weaknesses:

The authors note that other sensory neurons likely contribute to 1-octanol chemotaxis. Given the NeuroPAL data, it would have been nice to identify these other neurons as well. However, the reviewer is aware that this is tangential to the primary focus of this study.

Reviewer #3 (Public review):

Summary:

This work describes how two chemosensory neurons in C. elegans drive opposite behaviors in response to a volatile cue. Because they have different concentration dependencies, this leads to different behavioral responses (attraction at low concentration and repulsion at high concentration). It has been known that many odorants that are attractive at low concentrations are aversive at high concentrations, and the implicated neurons (at least AWC for attraction and ASH for repulsion) have been well established. None the less, by studying behavior and neural responses in a common context (odor pulses, as opposed to gradients) this provides a clear picture of how these sensory neurons may guide the dose dependent response by separately modulating odor entry and odor exit behaviors.

Strengths:

(1) This work provides good evidence that worms are attracted to low concentrations and repelled by high concentrations of 1-oct. Calcium imaging also makes it clear that dose-dependence of this response is stronger for ASH than AWC.

(2) This work presents calcium imaging and behavior with the same stimulus (sudden pulses in volatile odor concentration), while previous studies often focus on using neuronal responses to pulses to understand navigation of gentle gradients.

Weaknesses:

(1) As a whole it is not clear precisely how important AWC is (compared to other cells) for the attractive response (as the authors correctly acknowledge).

(2) The evidence that AIB minus AVA contains relevant information is weak. It appears the entrainment index in Fig. 6H for AIB-AVA could easily be explained by the negative entrainment between AVA and the stimulus (along with no effect or role for AIB). This is suggested by the similar p-values and similar distribution of random EIs (stretched and mirrored) between the first and last rows of this figure.

(3) The model in Figure 7 would be strengthened if it was demonstrated that IAA is attractive when worms are saturated in a 1/10^4 concentration. Panel 7G (and ref. 39) indicate that 10^-4 IAA activates ASH, which would suggest a different explanation for the change from attraction to repulsion in 7C.

Reviewer #1 (Public review):

[Editors' 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:

The Authors test the hypotheses, using and effort-exertion and an effort-based decision-making task, while recording brain dynamics with EEG, that the brain processes reward outcomes for effort differentially when they earned for themselves versus others.

Strengths:

The strengths of this experiment include what appears to be a novel finding of opposite signed effects of effort on the processing of reward outcomes when the recipient is self versus others. Also, the experiment is well-designed, the study seems sufficiently powered, and the data and code are publicly available.

Weaknesses:

There is some concern about the fact that participants report feeling less subjective effort, but also more disliking of tasks when they were earning rewards for others versus self. The concern is that participants worked with less vigor during self-versus-others trials and this may partly account for a key two-way Recipient x Effort interaction on the size of the Reward Positivity EEG component. Of note, participants took longer to complete tasks when working for others. While it is true that, in all cases, participants met the requisite task demands (they pressed the required number of buttons) they did so more sluggishly when earning rewards for others. The Authors argue that this reflects less motivation when working for others, which is a plausible explanation. The Authors also try to rule out this diminished vigor as a confounding explanation by showing that the two way interaction remains even when including reaction times (and also self-reported task liking) as a covariate. Nevertheless, it is possible that covariates do not fully account for the effects of differential motivation levels which would otherwise explain the two-way interaction. As such, I think a caveat is warranted regarding this particular result.

Reviewer #2 (Public review):

Summary:

Measurements of the reward positivity, an electrophysiological component elicited during reward evaluation, have previously been used to understand how self-benefitting effort expenditure influences processing of rewards. The present study is the first to complement those measurements with electrophysiological reward after-effects of effort expenditure during prosocial acts. The results provide solid evidence that effort adds reward value when the recipient of the reward is the self but discounts reward value when the beneficiary is another individual.

Strengths:

An important strength of the study is that amount of effort, the prospective reward, the recipient of the reward, and whether the reward was actually gained or not were parametrically and orthogonally varied. In addition, the researchers examined whether the pattern of results generalized to decisions about future efforts. The sample size (N=40) and mixed-effects regression models are also appropriate for addressing the key research questions. Those conclusions are plausible and adequately supported by statistical analyses.

Reviewer #1 (Public review):

Summary:

This is a wonderful and landmark study in the field of human embryo modeling that uses patterned human gastruloids and conducts a functional screen on neural tube closure and identified positive and negative regulators and defines the epistasis among them.

Strengths:

This was achieved following optimization of micro-pattern based gastruloid protocol to achieve high efficiency, and then optimize was to conduct and deliver CRISPRi without disrupting the protocol. This is a technical tour de force as well as one of the first studies to reveal new knowledge on human development through embryo models which has not been done before.

Weaknesses:

A minor one. One can never find out if findings in human embryo models can be in vitro revalidated in humans in vivo for obvious and justified ethical reasons. However, the authors indicate that in the "limitations of study" section.

Comments on revisions:

The authors have adequately addressed all comments raised.

Reviewer #1 (Public review):

Summary:

This study investigates the role of the medial prefrontal cortex (mPFC) in generating goal-directed actions under threat, using a progressive behavioral paradigm, neural recordings, and optogenetic inhibition in mice. The authors demonstrate that while mPFC GABAergic neurons strongly encode cues, actions, and errors, particularly under high cognitive demand, this neural activity is not causally required for executing avoidance behaviors. By rigorously controlling for movement and arousal, the researchers found that much of the observed mPFC signaling actually reflects baseline behavioral states rather than the generation of the actions themselves. This dissociation between encoding and causality challenges traditional views of mPFC as an executive controller of action and provides a nuanced understanding of its role in evaluative and contextual processing.

Strengths:

The behavioral paradigm employed in this study is one of its greatest strengths, offering a rigorous, progressive, and well-controlled framework to dissect the neural mechanisms underlying avoidance under threat. This three-phase task design is particularly well-suited to tease apart the contributions of learning, discrimination, and cognitive load to both behavior and neural activity.

By tracking movement (speed, rotations) and including it as a covariate in statistical models, the authors also underscore the need to control for movement and baseline activity when interpreting cortical signals, which is relevant for all studies of brain-behavior relationships, ensuring that behavioral changes are not due to general arousal or motor activity.

Finally, the study combines multiple advanced techniques-fiber photometry, single-cell calcium imaging (miniscopes), and two distinct optogenetic inhibition methods-to provide a comprehensive look at both neural encoding and causal necessity.

Weaknesses:

The authors conclude that mPFC is not required for avoidance, based on the minimal behavioral effects of optogenetic inhibition. While this interpretation is supported by the data, the choice of viral constructs could lead to an underestimation of the mPFC's role for other reasons. First, the choice of viral constructs could lead to an underestimation of the mPFC's role for several reasons. Specifically, the efficacy of eArch3.0 inhibition was not verified beyond histology, and its non-cell-type-specific nature could lead to disinhibition or compensatory activity in downstream regions. Although the authors' use of visual cortex (VI) inhibition as a control suggests that broad cortical inhibition does not impair avoidance, subcortical compensation cannot be ruled out. Additionally, Vgat-ChR2 targets only GABAergic neurons, potentially missing glutamatergic contributions. Addressing these limitations in the Discussion section would strengthen the manuscript.

Reviewer #2 (Public review):

Summary:

The manuscript by Sajid et al. describes a comprehensive behavioral, imaging, and optogenetic dataset investigating the role of the mPFC in avoidance and escape behaviors. Although many movement- and task-related variables are encoded by mPFC GABAergic neurons, the main conclusion is that they are unlikely to control behavioral output.

Strengths:

The manuscript is generally well executed and plausible in its conclusions. It provides an alternative viewpoint to many articles describing the involvement of mPFC in behavior, based on a complex multi-stage behavioral paradigm acquired and analyzed in an unbiased way.

Weaknesses:

This reviewer sees three main weaknesses.

(1) There are few details on the linear mixed models in the methods. This section could be improved by including a mathematical description. More importantly, the reader never learns how accurately the models capture the data. Given that most conclusions rely on the models, it seems central to address this point carefully. For example, what is the explained variance, marginal, and conditional? Were the nested models compared to non-nested ones (e.g., AIC), what are the specific outputs of the likelihood ratio tests briefly mentioned in the methods?

(2) For several figures, there is a disconnect with the main text, in the sense that it is difficult to understand how statements in the main text connect with specific figure panels or bars in their graphs. This is particularly the case for the most complex figures, e.g., Figures 3, 4, and their supplements. It would be beneficial to introduce subfigure labels (A1, etc) and state explicitly in the main text what figure panel is described (in parentheses). Alternatively breakdown the figures into multiple ones, decreasing ambiguity. This is important because it will help the reader better assess the strength of the results.

(3) It does not appear that the code and data used to produce the figures are made available. That would be very beneficial, given the complexity of the analysis and dataset collection procedures. It would also help readers better understand the results and probe their validity.

Reviewer #3 (Public review):

I first want to state that I am not an expert in the field, making it hard for me to provide informed comments on the value of the scientific results. But from where I stand, the study seems very carefully designed, very well controlled, and the statistical methodology used across the manuscript is strong and sound.

Summary:

The authors investigated the role of PFC interneurons in cue-guided behaviour under threat. They designed a behavioural task with increasing levels of difficulty that allows them not only to correlate the activation of cortical interneurons with different parameters of the tasks, but also to assess if this correlation changes with increasing cognitive load. They carefully take into account confounding factors such as movement and show that indeed neuronal activity is strongly driven by movement. Using generalised linear models throughout their manuscript, the authors could include movement as a confounding factor in their statistical analysis, thus allowing them to next correlate interneuron activity with task-specific parameters. Using first fibre photometry to image bulk activity of the interneurons and by comparing the responses in the PFC and in the visual cortex, they identify that PFC neurons show stronger activation related to punishment compared to the sensory cortex. Interestingly, under high cognitive demand, PFC interneurons show cue-specific activation, which could reflect the involvement of the PFC in cue-selective action selection.

In a second set of experiments, they use Miniscope to image individual interneurons. They classified interneurons, not based on their expression of specific markers as usually done, but based on their correlation with movement. Using this classification, they identify clusters of neurons that show activity modulation related to various behavioural parameters.

Lastly, they performed optogenetic manipulations to silence the PFC during cue-guided behaviour and showed little behavioural effect of the manipulation, which they suggest means the PFC is not involved in taking action in this task.

Strengths:

The design of the study is backed by convincing arguments from the authors. The confounding factors are carefully taken into account and integrated into state-of-the-art statistics. The results thus appear robust and reliable. The authors do not overinterpret their results; quite the contrary, they are prone to toning down the interpretation of statistically significant results and they warn the readers about potential misinterpretation or confounding factors. The discussion makes for a very interesting and informative reading.

Weaknesses:

The main weakness, in my view, lies in the Results section. In the figures, the authors do not present any raw data, and the plots are shown as mean {plus minus} SEM without displaying the distribution of individual data points. It is both a strength and a weakness that the authors do not attempt to guide the reader through the Results section and instead present the findings with very little emphasis on the key outcomes of the GLM. While this approach is arguably the most transparent way to report results, it also makes the section quite difficult to follow and may discourage readers.

I would recommend rewriting the Results section to make it more accessible to a broader audience. A similar issue applies to the figures: presenting all plots reflects a commendable commitment to transparency, but it would greatly benefit from a clearer narrative. As it stands, it is difficult to grasp the message of each figure by simply browsing through them.

Reviewer #1 (Public review):

Summary:

Liao et al. present SCOPE (Spatial reConstruction via Oligonucleotide Proximity Encoding), a method for reconstructing spatial organization from diffusion-defined DNA barcode interactions without the use of optical imaging. In SCOPE, hydrogel beads bearing unique DNA barcodes contain both "sender" and "receiver" oligonucleotides. Upon enzymatic release, sender oligos diffuse locally and hybridize to receiver oligos on neighboring beads, forming chimeric molecules that encode spatial proximity. Sequencing these products yields an interaction matrix, which is then used to reconstruct a spatial coordinate map.<br /> The authors demonstrate reconstruction of synthetic two-dimensional shapes, a large multicolor Snellen eye chart, and the interior surface of three-dimensional molds. The work expands the conceptual and experimental landscape of optics-free spatial sequencing.

Strengths:

SCOPE employs bidirectional sender and receiver oligonucleotides on every bead, rather than using asymmetric transmitter-receiver architectures found in other diffusion-based methods. The symmetric design may improve detection sensitivity and reconstruction strategies, and represents a meaningful variation on optics-free spatial encoding.

A notable strength of this study is the physical scale achieved. The authors reconstruct a Snellen chart spanning approximately 704 mm² and demonstrate molded 3D structures on the order of 75-100 mm³. Although some larger-scale warping is evident, and is discussed as potentially due to non-uniform diffusion, the relative local positioning across these large areas appears impressively accurate.

The authors extend reconstruction beyond two-dimensional arrays to three-dimensional molded surfaces. This demonstrates that the assay and the computational methods for interpreting proximity graphs can support non-planar spatial relationships, expanding the scope of optics-free spatial inference.

Weaknesses:

Although the method is discussed in the context of spatial genomics and potential tissue applications, it is currently demonstrated only on engineered two-dimensional bead arrays and three-dimensional shapes fabricated in molds. It remains unclear how SCOPE would perform in heterogeneous biological environments, where diffusion may exhibit additional non-uniformities. A biological proof-of-concept, even limited in scope, would help define the method's strengths and limitations more clearly.

The reconstruction of three-dimensional structures lacks strong sampling from volume interiors. This is speculated to be due to several possible factors; however, this limitation constrains the method to reconstruction of volume surfaces rather than comprehensive three-dimensional profiling.

The reconstruction workflow involves multiple preprocessing steps and embedding choices. While these appear to work well for synthetic shapes with known geometry, it is less clear how parameter choices would be made in contexts where ground truth is unknown. Clarifying how reconstruction robustness is assessed without prior knowledge of spatial structure would help readers understand how the method could be practically deployed, particularly in more heterogeneous tissue contexts.

Reviewer #1 (Public review):

Summary:

This study demonstrates, through a series of EEG and MEG experiments, that the human brain automatically categorizes words from alphabetic and non-alphabetic languages, and it unpacks the neural mechanisms of this process from multiple angles. The work examines not only univariate repetition-suppression (RS) effects, but also how repeating or alternating languages influences the representational similarity of words within and across language categories.

Strengths:

The univariate RS effects across multiple experiments lend support to some of the main conclusions

Weaknesses:

I have reservations about the logic underlying the multivariate analyses, and I believe the implications of the control experiments merit fuller discussion.

(1) Question 1: Logic of the multivariate analyses

The original text states:

"The processing of intra-language similarity was quantified as correlation distances between neural responses to two words of the same language, which occurred more frequently and would be inhibited in the Rep-Cond (vs. Alt-Cond) due to habituation (Fig. 1c)...".

I argue that this passage conflates two levels. Building a representational dissimilarity matrix (RDM) is a data-analysis step; it cannot be equated with a cognitive computation. Hence, there is no sense in which this computation occurs "more frequently" in one condition. RDM construction rests on the pairwise similarity of activity patterns, so even if a task engaged no cognitive computation of representational similarity, we could still compute an RDM. Conversely, if a task factor alters the RDM, we must explain how that factor changes the underlying neural patterns, not claim that it triggers specific cognitive processing. Therefore, I neither understand what "more frequent processing" the authors refer to, nor accept their account of the multivariate results.

The multivariate result pattern, briefly, is that distances between words, both within and across languages, are larger under the repetition condition. One plausible interpretation is that a word representation comprises two parts: language-type (alphabetic vs. non-alphabetic) and fine-grained identity features (visual shape, orthography, semantics, phonology, etc.). Repetition of language type may, via RS, reduce the weight of the first component, thereby increasing the relative contribution of fine-grained features and amplifying inter-word differences. This could explain the multivariate findings.

(2) Question 2:

For unlearned languages, people cannot distinguish lexical from sub-lexical levels. What, then, determines (i) the RS-effect difference between letters and radicals in familiar languages and words in unlearned ones, and (ii) the similarity of repetition effects between words in unlearned and familiar languages? An explicit account is needed.

Reviewer #2 (Public review):

Summary:

This study investigates how the human brain categorizes visual words from distinct writing systems (alphabetic vs. non-alphabetic) as a neural basis for the social-categorization function of language. Using a repetition suppression paradigm combined with electroencephalography and magnetoencephalography, the authors conducted nine experiments with independent participants to identify the neural network underlying language-based categorization, characterize its temporal dynamics, and test whether this process operates independently of linguistic properties such as semantic meaning and pronunciation.

Strengths:

(1) The study employs a well-validated design with clear control conditions and systematically manipulates key variables, including writing system, language familiarity, and native language background. The use of nine experiments with independent participant samples strengthens the reliability and replicability of the results.

(2) The work combines EEG and MEG, cross-validating findings across imaging modalities to support the reported neural effects. A combination of univariate, multivariate, and connectivity analyses is used to characterize neural responses and network interactions.

(3) Results are consistent across multiple language groups and for both familiar and unfamiliar languages, supporting the generalizability of the identified neural mechanism beyond specific languages or prior experience.

Weaknesses:

The authors provide compelling evidence that the identified neural network supports the categorization of words by language, including computations of intra-language similarity and inter-language difference. However, the conceptual framing of this finding as directly reflecting the social-categorization function of language may be premature. While the task captures spontaneous language categorization, it does not involve social evaluation or intergroup processes. The connection to social categorization is inferred from prior literature rather than demonstrated within the current experimental design. Clarifying this distinction would strengthen the conceptual precision of the manuscript.

Reviewer #1 (Public review):

Summary:

The behaviour of cells expressing constitutively active HRas is examined in mosaic monolayers, both in MCF10a breast epithelial and Beas2b bronchial epithelial cell lines, mimicking the potential initial phase of development of carcinoma. Single HRas-positive cells are excluded from MCF10a but not Beas2b monolayers. Most interestingly, however, when in groups, these cells are not excluded, but rather sharply segregated within a MCF10a monolayer. In contrast, they freely mix with wt Beas2b cells. Biophysical analysis identifies high tension at heterotypic interfaces between HRas and wild-type cells as the likely reason for segregation of MCF10a cells. The hypothesis is supported experimentally, as myosin inhibition abolishes segregation. The probable reason for lack of segregation in the bronchial epithelium is to be found in the different intrinsic properties of these cells, which form a looser tissue with lower basal actomyosin activity. The behaviour of single cells and groups is recapitulated in a vortex model based on the principle of differential interfacial tension, under the condition of high heterotypic interfacial tension.

Strengths:

Despite being long recognized as a crucial event during cancer development, segregation of oncogenic cells has been a largely understudied question. This nice work addresses the mechanics of this phenomenon through a straightforward experimental design, applying the biophysical analytical approaches established in the field of morphogenesis. Comparison between two cell types provides some preliminary clues on the diversity of effects in various cancers.

Weaknesses:

Although not calling into question the main message of this study, there are a few issues that one may want to address:

(1) One may be careful in interpreting the comparison between MCF10a and Beas2b cells as used in this study. The conditions may not necessarily be representative of the actual properties of breast and bronchial epithelia. How much of the epithelial organization is reconstituted under these experimental conditions remains to be established. This is particularly obvious for bronchial cells, which would need quite specific culture conditions to build a proper bronchial layer. In this study, they seemed to be on the verge of a mesenchymal phenotype (large gaps, huge protrusions, cells growing on top of each other, as mentioned in the manuscript).

As an alternative to Beas2b, comparison of MCF10a with another cell line capable of more robust in vitro epithelial organization, but ideally with different adhesive and/or tensile properties, would be highly interesting, as it may narrow down the parameters involved in segregation of oncogenic cells.

(2) While the seminal description of tissue properties based on interfacial tensions (Brodland 2002) is clearly key to interpreting these data, the actual "Differential Interfacial Tension Hypothesis" poses that segregation results from global differences, i.e., juxtaposition of two tissues displaying different intrinsic tensions. On the contrary, the results of the present work support a different scenario, where what counts is the actual difference in tension ALONG the tissue boundary, in other words, that segregation is driven by high HETEROTYPIC interfacial tension. This is an important distinction that should be clarified.

(3) Related: The fact that actomyosin accumulates at the heterotypic interface is key here. It would be quite informative to better document the pattern of this accumulation, which is not clear enough from the images of the current manuscript: Are we talking about the actual interface between mutant and wt cells (membrane/cortex of heterotypic contacts)? Or is it more globally overactivated in the whole cell layer along the border? Some better images and some quantification would help.

(4) In the case of Beas2b cells, mutant cells show higher actin than wt cells, while actin is, on the contrary, lower in mutant MCF10a cells (Figure 2b). Has this been taken into account in the model? It may be in line with the idea that HRas may have a different action on the two cell types, a possibility that would certainly be worth considering and discussing.

Comments on revisions:

There is still one last point that should be made even clearer:

The system is being modelled based on the principle of INTERFACIAL TENSION, a description pioneered by the works of Steinberg and of Harris, and nicely conceptualized by Brodland (2002). Now the observed behaviour is a perfect case of sorting based on higher interfacial tension AT the boundary between cell types (with nice additional documentation of local actin and myosin enrichment in the revised manuscript). What needs to be made crystal clear it that this is NOT equivalent to the model of DITH ("DIFFERENTIAL INTERFACIAL TENSION HYPOTHESIS)" (Brodland 2002, Krieg et al 2008). It is important to stop using DITH in this context, as it leads to confusion and misinterpretations. Indeed, DITH predicts cell/tissue sorting based on differences in interfacial tension WITHIN the two cell types. While DITH accounts for relative POSITIONING (one tissue engulfing the other), it is now established that this is not the motor for cell sorting and tissue segregation, the key parameter is being heterotypic tension at the heterotypic interface. I thus invite the authors to avoid the terms "differential"/DITH, and rather use either "interfacial tension", or specifically to "HIGH HETEROTYPIC INTERFACIAL TENSION".

Related: the authors correctly cite Canty et al NatComm2017 when discussing this phenomenon. I suggest to add an additional key supporting reference "D.M. Sussman, J.M. Schwarz, M.C. Marchetti, M.L. Manning, Soft yet sharp interfaces in a vertex model of confluent tissue, Phys. Rev. Letters 120 (2018) 058001". One may also include another pioneer work in Drosophila is "M. Aliee, J.C. Roper, K.P. Landsberg, C. Pentzold, T.J. Widmann, F. Julicher, C. Dahmann, Physical mechanisms shaping the Drosophila dorsoventral compartment boundary, Curr. Biol. 22 (2012) 967-976."

Reviewer #2 (Public review):

Summary:

The authors investigate the behavior of oncogenic cells in mammary and bronchial epithelia. They observe that individual oncogenic cells are preferentially excluded from the mammary epithelium, but they remain integrated in the bronchial epithelium. They also observe that clusters of oncogenic cells form a compact cluster in mammary epithelium, but they disperse in the bronchial epithelium. The authors demonstrate experimentally and in the vertex model simulations that the difference in observed behavior is due to the differential tension between the mutant and wild-type cells due to a differential expression of actin and myosin.

Strengths:

* Very detailed analysis of experiments to systematically characterize and quantify differences between mammary and bronchial epithelia

* Detailed comparison between the experiments and vertex model simulations to identify the differential cell line tension between the oncogenic and wild-type cells as one of the key parameters that are responsible for the different behavior of oncogenic cells in mammary and bronchial epithelia

Weaknesses:

* It is unclear what is the mechanistic origin of the shape-tension coupling, which is used in the vertex model, and how important that coupling is for the presented results. Authors claim that the shape-tension coupling is due to the anisotropic distribution of stress fibers when cells are under external stress. It is unclear why the stress fibers should affect an effective line tension on the cell boundaries and why the stress fibers should be sensitive to the magnitude of the internal isotropic cell pressure. In experiments, it makes sense that stress fibers form when cells are stretched. Similar stress fibers form when cytoskeleton or polymer networks are stretched. It is unclear why the stress fibers should be sensitive to the magnitude of internal isotropic cell pressure. If all the surrounding cells have the same internal pressure, then the cell would not be significantly deformed due to that pressure and stress fibers would not form. Authors should better justify the use of the shape-tension coupling in the model, since most of the observed behavior is already captured by the differential tension even if there is no shape-tension coupling.

* The observed difference of shape indices between the interfacial and bulk cells in simulations in the absence of differential line tension is concerning. This suggests that either there are not enough statistics from the simulations or that something is wrong with the simulations. For all presented simulation results, the authors should repeat multiple simulations and then present both averages and standard deviations. This way it would be easier to determine whether the observed differences in simulations are statistically significant.

Reviewer #1 (Public review):

Summary:

The aim of this work is to directly image collagen in tissue using a new MRI method with positive contrast. The work presents a new MRI method that allows very short, powerful radio frequency (RF) pulses and very short switching times between transmission and reception of radio frequency signals.

Strengths:

The experiments with and without removal of 1H hydrogen, which is not firmly bound to collagen, on tissue samples from tendons and bones are very well suited to prove the detection of direct hydrogen signals from collagen. The new method has great potential value in medicine, as it allows for better investigation of ageing processes and many degenerative diseases in which functional tissue is replaced by connective tissue (collagen).

Comments on revisions:

All points of criticism in the reviews were answered very well and led to further improvement of the article.

Reviewer #2 (Public review):

Summary:

This work presents direct magnetic resonance imaging (MRI) of collagen, which is not possible with conventional MRI or other tomographic imaging modalities.

Strengths:

The experimental work is impressive, and the presentation of results is clear and convincing.

Reviewer #3 (Public review):

The paper is well written and well presented. The topic is important, and its significance is explained succinctly and accurately. I am only capable of reviewing the clinical aspects of this work which is very largely technical in nature. Several clinical points are worth considering:

(1) Tendons typically display large magic angle effects as a result of their highly ordered collagen structure (cortical bone much less so) and so it would have been of interest to know what orientation the tendons had to B 0 (in vitro and in vivo). This could affect the signal level at the longer echo time and thus the signal on the subtracted images.

(2) The in vivo transverse image looks about mid-forearm where tendons are not prominent. A transverse image of the lower forearm where there is an abundance of tendons might have been preferable.

(3) The in vivo images show the interosseous membrane as high signal on both the shorter and longer TE images. The structure contains ordered collagen with fibres at different oblique angles to the radius and ulnar and thus potentially to B 0. Collagen fibres may have been at an orientation towards the magic angle and this may account for the high signal on the longer TE image, and the low signal on the subtracted image.

(4) Some of the signals attributed to muscle may be from an attachment of the muscle to aponeurosis.

(5) There is significant collagen in subcutaneous tissues so the designation "skin" may more correctly be "skin and subcutaneous tissue".

(6) Cortical bone is very heterogeneous with boundaries between hard bone and soft tissue with significant susceptibility differences between the two across a small distance. This might be another mechanism for ultrashort T 2 * tissue values in addition to the presence of collagen. The two effects might be distinguished by also including a longer TE spin echo acquisition.

Solid cortical bone may also have an ultrashort T 2 * in its own right.

(7) It may be worth noting that in disease T 2 * may be increased. As a result, the subtraction image may make abnormal tissue less obvious than normal tissue. Magic angle effects may also produce this appearance.

(8) It may be worth distinguishing fibrous connective tissue (loose or dense) which may be normal or abnormal, from fibrosis which is abnormal accumulation of fibrous connective tissue in damaged tissue. Fibrosis typically has a longer T 2 initially and decreases its T 2 * over time. In places, the context suggests that fibrous connective tissue may be more appropriate than fibrosis.

Overall, the paper appears very well constructed and describes thoughtful and important work.

Comments on revisions:

The responses to my criticisms are well thought out and are fine as far as I am concerned.

I suggest in Figure 5 line 6 changing "trabecular bone" to "trabecular bone marrow".

Reviewer #1 (Public review):

Summary:

In this study, Angla et al investigate the basis of observations made from previous studies where loss of Onecut (OC) transcription factors leads to changes in spinal interneuron populations that do not themselves normally express OC. The authors hypothesize that OC expression in spinal motor neurons has non-cell-autonomous effects on pre-motor interneuron (V1, V2a/b/c) population size and distribution. By knocking out OC in the motor neuron lineage (i.e., downstream of Olig2, a motor neuron progenitor marker gene), they indeed show that motor neuron-specific loss of OC expression decreases V2c interneuron number and alters the spatial distribution of V1, V2a, V2b, and V2c populations. Using bulk RNA-sequencing of WT and OC conditional knockout (cKO) motor neurons, the authors identify that the neurotrophic factor Ntf3 is downregulated by OC expression. They subsequently hypothesize that the non-cell-autonomous effects observed by loss of OC expression in motor neurons can be explained by de-repression of Ntf3. To test this, the authors conditionally knock out Ntf3 downstream of Olig2 and show that this leads to increased interneuron numbers and alters their spatial distribution, ultimately leading to dysregulation of spinal motor circuits and motor activity.

Strengths:

The authors use sophisticated genetic tools to precisely remove OC and Ntf3 expression in a lineage-specific manner and comprehensively assess the downstream effects across brachial, thoracic, lumbar levels of the spinal cord, as well as at two developmental timepoints, E12.5 and E14.5.

Weaknesses:

There are two main concerns that are not fully addressed:

(1) Based on the effects observed with OC vs. Ntf3 cKO, it is unclear whether OC is indeed exerting its non-cell-autonomous effects via Ntf3. Knocking out both Ntf3 and OC and comparing the effects to those seen with just OC cKO alone could provide more insight on this point. Also, a quantitative summary of the effects of Ntf3 overexpression in motor neurons in the chick is lacking.

(2) How the authors assess changes in the spatial distribution of interneurons is unclear. In Figures 2 and 4, the control distributions (despite reporting the same populations in the same regions) look different, suggesting large sample-to-sample variance in distribution. Although the authors report that several sections in each level were taken from at least three animals for each condition, it's unclear how variance within WT or cKO sections was accounted for in the final statistical evaluation. It seems at a glance that a comparison between control samples in Figure 2 and Figure 4 could report statistically significant differences, which would be problematic. A more rigorous report of sample-to-sample variance and a more in-depth explanation of the statistical methods are needed.

Reviewer #2 (Public review):

The study by Angla et al. proposes a model in which NT-3 produced by motor neurons regulates interneuron numbers and distribution in a non-cell autonomous manner. The authors demonstrate that ablation of motor neurons (MNs) and global and conditional deletion of OC transcription factors lead to changes in interneuron distribution. They identify that NT3 is upregulated after MN-specific OC deletion in RNA-seq experiments and show that olig2-cre mediated NT3 deletion leads to increased ventral interneuron numbers, altered distribution, and defects in locomotor behavior. The authors conclude that MN-derived NT3, under OC control, regulates interneuron development. While this is an intriguing hypothesis, additional experiments are needed to support it and strengthen the link between the different experiments described here.

(1) The study primarily quantifies interneuron numbers and distribution at different levels of the spinal cord and under different genetic manipulations. Experimental details are lacking, defining how many sections were analyzed (several are noted in the methods) and how the rostrocaudal levels of the spinal cord were precisely aligned. In different figures, the values and distributions shown for controls vary quite a lot. For example, in Figure 2B vs Figure 4B, the number of FoxP2+ V1 neurons at brachial levels is ~350 vs 125. Similarly, the control distributions in 2I and 4I are quite different. This makes it challenging to determine whether the conclusions regarding the impact of each genetic manipulation on interneuron numbers and distribution are valid.

(2) The relationship between OC and NT3 deletion data is not entirely clear. Both deletions presumably lead to changes in interneuron distribution, but is there any reverse relationship between the two that relates to relative changes in NT3 levels? The authors do not directly compare NT3 and OC KO IN distributions. Similarly, one might expect a decrease in interneuron numbers in OC mutants, which is only reported for V2c neurons. However, the image presented in Figure 2G shows an equal number of V2c INs in control and mutant.

(3) It is not clear that the behavioral phenotypes seen in the olig2-cre mediated deletion of NT3 can be attributed to changes in interneuron development. How about a role of NT3 in oligodendrocytes? There is a big gap between the embryonic changes shown here and behavior, with no in-between circuit-level changes in locomotor circuits shown. A more restricted manipulation would be deleting TrkC from specific interneuron populations. Related to this, although TrkC is shown to be broadly expressed in ventral interneurons, it is not shown specifically to colocalize with any of the interneuron markers. The authors should validate that the receptor is expressed in the subsets that they are investigating.

(4) The rationale for following up on NT3 seems to be the chick electroporation experiments; however, no changes in distribution are shown in those experiments, and only a very minor decrease in Chx10 interneurons. Shouldn't NT3 overexpression lead to substantial decreases in IN numbers according to the authors' model? The "data not shown", which presumably refers to distribution, would be important to show here, to further support this rationale.

(5) The idea that NT3 downregulation causes an increase in IN numbers is not intuitive. Also, considering the DTA experiments in Figure 1, showing that MN ablation leads to a decrease in several IN subtypes and no changes in V2a neurons. It would be helpful for the reader if the authors could synthesize their results in the discussion and reconcile their experimental findings.

Reviewer #3 (Public review):

This manuscript aims to investigate cell extrinsic mechanisms that regulate the differentiation and distribution of interneuron types in the spinal cord. The authors demonstrate that the loss of motor neurons leads to changes in the number and distribution of different interneuron types, specifically V0v, V1, and V2b (but not V2a). The authors then hypothesize that this phenotype may be controlled by the action of Onecut (OC) transcription factors in motor neurons. Conditional knockout of OC1 + OC2 in motor neurons using Olig2-Cre, however, does not lead to significant changes in the numbers of V1, V2a, and V2b interneurons, although there is a change in their spatial distribution. While the authors do not check V0v neurons in OC mutants, they do check V2c, which show a reduction in number and change in distribution. Why the same neurons are not checked across experiments is unclear. The authors then analyze existing RNA-seq data to identify factors that could be mediating the effects of the OC factors in motor neurons. They identify Ntf3 as a candidate and confirm that it is upregulated in OC mutants. Conditional loss of function of Ntf3 (Olig2-Cre) leads to increases in V1, V2a, and V2b (but not V2c) interneurons and changes in the distribution of all four interneuron types. Finally, the authors demonstrate that these Ntf3 conditional mutants have major defects in motor function.

The conclusions of this manuscript are not well supported by the data for the reasons listed below, making it difficult to assess the impact of this work on the field.

(1) The manuscript relies heavily on quantifying numbers and the spatial distribution of interneuron populations. However, these do not seem to be consistent in control animals across experiments, making it difficult to interpret any changes observed in genetic manipulations. Specifically, in Figures 2 and 4, the same markers are being used to quantify V1, V2a, V2b, and V2c interneurons in controls vs. OC (Figure 2) or Ntf3 (Figure 4) conditional knockouts, but the numbers of neurons and their distribution in control animals are variable between these two figures. For example, there seems to be a mean of >300 V1 neurons in E12.5 brachial sections of Fig. 2 controls, but this number is <150 in Fig. 4 controls. The cell distribution scoring is similarly variable between these controls without any explanation. The same is true for E14.5 controls used in Figure S1 vs. Figure S3.

(2) Neurotrophic factors generally promote neuronal survival. However, in this study, the loss of Ntf3 leads to increased numbers of interneurons. This finding is in disagreement with previous observations in slice cultures of spinal cords, as stated in the discussion. This discrepancy makes it even more important that the cell counts reported in the figures discussed above are robust.

(3) The claim that phenotypes are non-cell autonomously driven by motor neurons is not well supported. In Olig2-Cre conditional knockouts of Onecut and Ntf3, there is no confirmation that the loss of these factors is specific to motor neurons. Therefore, it cannot be ruled out that other cell populations may be mediating the phenotypes.

(4) The claim that interneuron development is regulated by OC control of Ntf3 expression in motor neurons is not well supported. The authors show that loss of OC1/2 leads to an increase in Ntf3 expression in motor neurons. If this pathway were controlling interneurons, loss of OC function and overexpression of Ntf3 would have the same phenotype, which is not the case. Additionally, it would also be expected that loss of OC function and loss of Ntf3 function would have inverse phenotypes, which is also not the case. The phenotypes from OC loss of function and Ntf3 loss of function seem distinct from one another. The authors state that too little and too much Ntf3 are both bad for interneuron development, but there is no data to support their claim that OC1/2 mutants have altered interneuron development because of higher Ntf3 expression.

(5) It is not clear that interneurons being studied express the Ntf3 receptor TrkC, which makes it difficult to assess whether changes in Ntf3 signaling are directly responsible for the phenotype.

(6) While the behavioral phenotypes are consistent with Ntf3 playing a role in motor circuits, there is no evidence to suggest that Ntf3's influence on premotor interneurons being studied is driving or contributing to this phenotype, as discussed by the authors.

Reviewer #1 (Public review):

Summary:

In this manuscript, Zmojdzian et al. provide an analysis of ryanodine receptor (RyR) expression and function in Drosophila. They also use CRISPR to engineer into flies a RyR variant of unknown significance (VUS) found in a human myopathy patient and demonstrate that it is likely a pathogenic mutation. From studies of RyR expression in embryonic and larval stages, and effects of RyR knockdown or overexpression in various muscle groups, the authors show that, in addition to its known actions in calcium-dependent excitation-contraction coupling, RyR promotes myogenesis during development.

The key conclusions of the paper are convincing. I do not have suggestions for necessary additional experimental work, and my comments are minor. One conclusion, that RyR dysfunction may be involved in aging, is stated in multiple places, sometimes speculatively but once very forcefully. The latter is in the final paragraph of the Discussion, which states RyR "plays an instrumental anti-aging role in differentiated striated muscle". This conclusion must be tempered, as even if RyR knockdown phenotypes resemble some of those seen in aging flies, the study does not examine aged flies, and there is no mechanistic analysis that might link the two. I assume the authors would prefer to modify that sentence than initiate work with aging flies to prove the assertion. Finally, the use of CRISPR to test a VUS is excellent and suggests a good way for testing of additional RyR variants in the future.

Significance:

The paper is significant in that RyR is known to be a critical protein in calcium-dependent excitation-contraction coupling but its role in developmental myogenesis is poorly studied. This study demonstrates that it is expressed during, and is important for, embryonic and larval myogenesis in the fly. RyR is also understudied in this valuable model organism, even though a P element-based mutant has been available since 2000. The mechanistic basis for the functional observations is not explored here but the work is well performed and will be of interest to investigators studying muscle development (my own field) and diseases caused by RyR mutations.

Reviewer #2 (Public review):

Summary:

This paper presents data using the Drosophila model to analyze the effects of a rare human mutation in the gene encoding the ryanodine receptor (ryr). The authors present a nice, comprehensive phylogenetic analysis that shows the Drosophila version of Ryr to be most similar to human RYR2 and that the known "hot spots" for mutations in RYR2 coincide with highly conserved regions of the Drosophila Ryr. They characterize the functional effects of ryr knockdown and overexpression on both adult heart function and larval body wall muscle. They identified embryonic ryr expression in association with actin-stained muscle precursor cells and provide beautiful stains, which clearly showed that embryonic muscle cell development was disrupted in ryr mutants. In support of these findings, KD of Calmodulin in larva (an Ryr inhibitor) phenocopied Ryr OE. They recreated a human variant of unknown function (RyR1 p.Met4881Ile ) in the conserved region of the fly gene and tested the effect on larval muscle. Their data suggested that this variant was likely deleterious as it negatively affected most muscle parameters.

Major comments:

(1) Fig, 1 In G there is no data for the RNAi KD situation.

(2) Fig. 2 Authors should include Diastolic Diameters; they mention dilated cardiomyopathy but don't show the dilation. The authors should also show staining in hearts with RYR OE and RNAi. It would be nice to have some kind of quantification of disorganized myofibrils.

(3) To evaluate and reproduce the data on the larva muscle parameters the authors should provide more details on how sarcomere length was quantified in each larva (replicates, ROI size, etc). Similarly, how were # of nuclei quantified / normalized? Importantly for these measurements, did the authors know what the contraction state of the muscles were when fixed?

(4) Fig. 3, Are RNAi and OE in the same background? I only see one control in the graphs for the RNAi line background.

(5) Fig. 3 How VL3 length was determined needs more detail, the Zhang ref is not adequate.

(6) In order to be able to evaluate the data, the statistical tests used should be cited in the figure legends along with what *, ** ,*** stand for (or just provide p values).

Significance:

The authors nicely characterized the role of Ryr in muscle development and function and recreated a human variant of unknown function (RyR1 p.Met4881Ile ) in the conserved region of the fly gene. Their data suggested that this variant was likely deleterious as it negatively affected most muscle parameters. This work supports a role for the fly model in testing potential human disease gene variants.

Comments on Revised Version:

The authors have very adequately addressed the points raised by all reviewers.

Reviewer #1 (Public review):

This is a very interesting paper. The research question is intriguing, allowing the authors to address commonly observed comorbidities between depression and anxiety and their dissociable and opposite relationship to mood fluctuations and sensitivity to reward prediction errors. The computational analyses are very in-depth, including many state-of-the-art checks and validations. Another strength is the inclusion of several large or very large samples, including a patient sample in addition to the general population sample.

I have the following questions:

(1) Factor analysis I found the hierarchical organization of the factors interesting. While this is a very common procedure in, for example, the field of intelligence (producing sub-scores and a general g factor), it is not yet very commonly used in the field of computational psychiatry (though it has been validated before for anxiety/depression, so it is used here with good reason). I was also impressed by the methodological depth. In particular, it was of note how thoroughly done it was (for example, repeating the EFA on the second half of the data set). I have one question though: is the sample size too small for the exploratory analyses, given the number of items? Given the stability across the half-split, I imagine it is not. Perhaps the authors could spell out how many items, what would be the recommended standard for a subject-to-item ratio, and comment on this. A very technical point, the authors should specify how they extracted the factor scores from the other data sets (is it using the Thurstone or Bartlett method)? From experience (though not doing a hierarchical factor analysis), Bartlett can be somewhat better compared to the default (Thurstone) - better as in the resulting factors more closely recapitulating the factor correlations in the original sample (and independence of responses of other participants in a sample for computing a person's factor score). Could you also comment on similarities or divergences in this hierarchical factor analysis approach from another one recently used transdiagnostically in Wise et al. (2026, Translational Psychiatry)?

(2) Linking factors to task parameters As I understand it, the authors relate the orthogonalized depression/anxiety to task parameters (sensitivity to RPEs on mood and mood variations) using correlations. In order to have a better understanding of how this relates to other commonly used approaches, I would pose two questions:

(i) What are the correlations when the full (non-orthogonalized) factor scores for depression and anxiety are used? Are the signs the same? (ii) What are the results when, instead of the independent correlations, the authors perform b_RPE ~ anxiety + depression (again using the non-orthogonalized factors)?

I'm assuming all of these analyses should give the same results if the authors' hypothesis of opposing effects of anxiety and depression holds true.

Minor comments:

(1) The authors should write down when the data were collected for each study. This is because AI capabilities have massively increased since ~2020 in quite specific steps (with the public release of new AI models), meaning that AI is likely to have been able to do tasks and questionnaires without detection if data were collected recently.

(2) The authors should include a statement in the methods section that checks for AI were done. If none yet, could you do any? Recent papers (Westwood, PNAS 2025; van der Stigchel PNAS, 2026) point to the risk since at least the release of o4-mini (used in the cited paper to create very human-like behaviour).

(3) It would have been good to collect questionnaires of other, thought to be unrelated psychiatric traits, like compulsivity or schizophrenia symptoms, to check the specificity of the results, also under the assumption that higher scores on either of these skewed questionnaires can pick up individual differences in 'bad questionnaire completion'. The authors should comment on the absence of other questionnaires in the discussion in the limitations section.

(4) The authors could include a more explicit sentence in the abstract stating that the anxiety result did not hold up in the clinical population.

Reviewer #2 (Public review):

Summary:

Despite their common co-occurrence, depression and anxiety are known to alter mood fluctuations in opposite ways. Here, the authors aimed at distinguishing depression-specific from anxiety-specific from psychopathology-general effects of reward processing on mood fluctuations, focusing on reward prediction errors (RPEs), which are known to be linked to mood fluctuations. This mechanistic study aims at uncovering the process through which these psychopathologies are associated with mood modulations. The authors were able to appropriately test their hypothesis and obtained results corroborating their conclusions.

This work provides a convincing demonstration of the relevance of computational psychiatry (Huys et al, 2016) and the use of decision neuroscience to shed light on the interplay of anxiety, depression, and mood.

Strengths:

The authors used a tripartite model to distinguish depression vs anxiety, as well as a computational model distinguishing reward expectation (EV in the model) from outcome processing through RPE, which are two sequential cognitive processes.

The manuscript adequately addresses the concerns one would have regarding risk-attitudes and regarding referring to trending statistical results.

Weaknesses:

The sample size of the clinical sample (N=116) may not be sufficient to detect anxiety-specific effects due to the high rate of comorbid anxious depression. It would be beneficial to include the number of MDD vs GAD vs anxious depression diagnoses in the clinical population, as this would likely shine light on the power limitations.

Reviewer #3 (Public review):

Summary:

In this submission, Wang and colleagues jointly examine the association between depression and anxiety symptoms and individuals' affective reactivity to reward prediction errors in Ruttledge et al.'s gambling paradigm. Taking a bifactor approach to anxiety and depression in several non-clinical (and one clinical sample), the authors find that anxiety-specific symptoms relate to over-reactivity of mood to reward prediction errors (RPEs) as well as heightened mood variability, while depression-specific symptoms relate to blunted mood sensitivity to RPEs. These depression- but not anxiety-specific relationships replicated in patient samples.

Strengths:

I was impressed that the data-driven, transdiagnostic approach employed by the authors uncovered specific relationships between anxiety and depression-specific factors and RPE reactivity in a well characterized task and computational model, especially in a non-clinical sample. This sheds new light on how these affective processes may be perturbed-and importantly, in different ways-by anxiety and depression symptoms. Likewise, the replication of the depression-specific finding (RPE hypo-reactivity) in a clinical sample was nice to see.

Weaknesses:

(1) While the anxiety- and depression-specific factors had differential effects on mood variability (Figure 2A-D) and RPE reactivity (Figure 2E-G) in all samples, such that the correlations between the two factors and these mood parameters were significantly different, the anxiety factor was not consistently (significantly) associated with either mood-related parameter across samples. However, the authors resolve anxiety-specific predictive effects when they collapse across datasets. While it is intuitive that achieving a larger effective sample size would afford the power necessary to detect such individual differences, this struck me as a major caveat for this set of results.

(2) The authors observe associations between the 'common factor' of depression and anxiety and risk-attitude tendencies, presumably the alpha (exponent) parameter in a prospect theory-type subjective value model. But where is this analysis explained? (i.e. how was this model formulated and how were risk attitude parameters estimated?) And what is the interpretation of this finding - is there precedent for looking at risk attitudes in this task? And why would these predictive effects only be observed in relation to the common, but not unique, factors of anxiety and depression?

Reviewer #1 (Public review):

Summary:

This is a study utilizing several types of analyses (computational modeling, neuronal cultures, rodent epilepsy model, and human intracranial multi-scale recordings) to address a highly relevant conceptual question: Are fast ripples (FRs) distinct pathological entities or largely emergent products of stochastic spike clustering? The results can potentially reshape current approaches to incorporating fast ripples into the epilepsy surgery evaluation.

Strengths:

The conceptualization of fast ripples as potentially arising by chance is highly novel and builds effectively on questions raised in prior studies that have never been satisfactorily resolved.

The integration across biological scales and models is a major strength. The state dependency analysis provides additional, strong support. The methodology and statistical approaches used are thoughtfully presented and rigorously applied.

In particular, this paper provides a strong response to the findings from Gliske et al, Nat Commun 2018. This study utilized long-term data analysis to uncover low rates of FRs detected from most recording sites, suggesting spurious detections, although FRs were concentrated within seizure onset areas.

Weaknesses:

The authors clearly aimed to use a statistical rather than a mechanism-based approach in this work. However, the paper's framing of true fast ripples as oscillatory events with stochastic fast ripples considered as confounders does not take prior investigations into biological mechanisms, particularly prior studies that point to an important role for stochastic fast ripples in some contexts. Incorporating recognition of these mechanisms would strengthen the manuscript and provide a more complete and nuanced characterization.

Some examples from the literature:

Eissa et al, eNeuro 2016, a paper that closely parallels this manuscript but took a mechanistic rather than statistical approach, showed that fast ripples can arise from population paroxysmal depolarizations - a key feature of epileptiform discharges - as temporally clustered, jittered population firing, with FRs appearing in LFP or EEG due to summated postsynaptic potentials (which are slower than action potentials and can generate signals in the high gamma range).

Foffani et al., 2007, Neuron, and Ibarz et al., 2010, J Neurosci, argue that FRs are pseudo-oscillations created by jittered neuronal populations in the setting of altered spike timing.

Smith et al., 2020, Sci Rep, contrasts FR characteristics in different regimes, i.e., intact inhibition early in a seizure vs. implied collapse of inhibition after recruitment. Schlingloff et al., 2025, J Neurosci, reported analogous findings in an animal model.

The computational model and subtraction approach provide a strong case for the random emergence of clustered activity in the high gamma band, given its assumptions. However, any such modeling effort needs to account for inhibitory activity, including impaired inhibitory function that is expected in epileptic brain regions, which has a strong modulating effect on excitatory firing and is thought to play a significant role in FR generation.

The shuffling procedure aims to preserve the power spectrum but randomizes high frequency phase (>200 Hz). However, this procedure removes biologically meaningful spike timing correlations, as well as structured cross-frequency coupling. The subtraction method thus likely underestimates the incidence of structured "distinct" FRs, while perhaps overestimating "chance" FRs due to biologically infeasible activity, making the statement that most FRs are due to chance correlation too strong.

The kainate findings underscore this point: the increase in the number of FR detections could be, as the authors state, an increase in chance clustering due to increased network excitability generally. However, the likelihood of a parallel increase in pathological FRs cannot be ruled out, given likely pro-epileptic alterations in spike timing and circuit function.

Reviewer #2 (Public review):

Summary:

This paper asks an important question that has not been discussed much in the extensive literature on the High Frequency Oscillations (HFOs) that have been extensively studied in patients with epilepsy and experimental models of epilepsy. The question is whether the Fast Ripples (FRs), the HFOs in the 250-500 Hz frequency band, represent a pathological phenomenon or represent a physiological phenomenon that occurs in the healthy brain but happens to be more frequent in epileptic tissue. It is an important question that has not been systematically addressed until now. The authors conclude, from very extensive simulations, from extensive experimental animal studies (the systemic kianate model of epilepsy in rats), and from a modest amount of human data, that FRs occur in healthy brains as a result of the chance occurrence of bursts of action potentials, and that in epileptic tissue, their frequency of occurrence is approximately 30% higher than what is expected by chance. They conclude that FRs are not a separate phenomenon of epileptic tissue. This finding is reinforced by the recent findings of FRs in experimental models of Alzheimer's disease.

Strengths:

This is a valuable study because it asks an important and original question and because it evaluates it from several angles (simulation, tissue culture, experimental animals, and human patients). The simulations and the analyses of real data are performed very carefully and with original and solidly documented approaches, using extensive simulations and extensive data sets in the cultured cell data and in the in vivo experiments. The paper is clearly written and well-illustrated.

Weaknesses:

I found only one serious weakness in this study, but it is one that is of importance. Although the original work on FRs was done in an experimental model of epilepsy, the field really became prominent when ripples and fast ripples were found first in microelectrode recordings of epileptic patients and then in the intracerebral EEG of such patients. Numerous studies have been performed since then, with a valuable meta-analysis including 700 patients (Wang Z, Guo J, van 't Klooster M, Hoogteijling S, Jacobs J, Zijlmans M. Prognostic Value of Complete Resection of the High-Frequency Oscillation Area in Intracranial EEG: A Systematic Review and Meta-Analysis. Neurology. 2024 May 14;102(9). Although the consensus at this point is that FRs are not the ideal and totally specific marker of epileptic tissue that many thought it could be, FRs are nevertheless much more frequent in epileptic tissue than in non-epileptic tissue and are a solid biomarker. It is also well established that they are much more frequent in NREM sleep than in wakefulness, as reported in the original paper of Staba et al (Staba RJ, Wilson CL, Bragin A, Jhung D, Fried I, Engel J Jr. High-frequency oscillations recorded in human medial temporal lobe during sleep. Ann Neurol. 2004 Jul;56(1):108-15., not mentioned in this paper) and in the study of Bagshaw et al (2009). In this last paper, using SEEG in various brain regions, the average rate of FRs in NREM sleep is about 6 times that in wakefulness. In the paper by Staba, with microelectrodes in mesial temporal structures, it is about twice. As a separate issue, the paper of Fraucher et al (Frauscher B, von Ellenrieder N, Zelmann R, Rogers C, Nguyen DK, Kahane P, Dubeau F, Gotman J. High-Frequency Oscillations in the Normal Human Brain. Ann Neurol. 2018 Sep;84(3):374-385), which is not quoted, found that, in an extensive sample, non-epileptic human tissue sampled with SEEG generated extremely rare FRs (an average rate of 0.04/min/channel, i.e. 1 every 25 min).

The results above are mentioned because they do not fit with the data provided in the present study: FRs are much more frequent in NREM sleep than in wakefulness in human epileptic patients, and they are much more frequent (not 30% more, but many hundreds of percent more) in epileptic tissue than in non-epileptic human tissue. The fundamental phenomenon of interest is, I believe, the FRs in epileptic patients. The animal experiments, tissue studies, and simulations are models to study the human phenomenon. With respect to the modulation by sleep and the differentiation between epileptic and non-epileptic tissue, it seems that the systems studied in this paper are not good models of the human condition. The human results presented in the study only reflect wakefulness recordings, which is not the condition in which most HFO studies have been done and in which most HFOs occur. The authors refer to the study of long-term fluctuations in HFO rates by Gliske et al. (2018) to say that one has to be careful with the results regarding sleep, for example, Bagshaw et al (2009), but the clear predominance in of HFOs in NREM sleep has been observed by many studies. The cautions regarding fluctuations over extended periods also apply to the awake human data analyzed in this study.

The study's conclusions regarding the generation of FRs are therefore questionably applicable to the human condition. I do not dispute their validity for the models and situations in which they were studied.

Reviewer #3 (Public review):

Summary:

An outstanding question in the field of high-frequency oscillations (HFOs) in the context of epilepsy is how these oscillations emerge, considering that they occur at such high frequencies, i.e., 250Hz, well above the firing ability of single neurons. One hypothesis that has been suggested in the past is that neurons that fire in an out-of-phase fashion, or rather at random intervals,s may contribute to a spectrum of HFOs ranging from 250-500Hz that are observed in epilepsy. However, how possible it is that random action potentials could aggregate to the extent that they could give rise to HFOs in the so-called fast ripple (FRs) frequency range (>200 according to the authors) remains unclear. To test this hypothesis, they used computational modeling to randomly insert action potentials in a signal, and they found that this approach is sufficient to generate FRs. Some of the predictors of whether FRs could occur were neuronal count, firing rate, and synchronization. Besides computational modeling, they used different model systems to test whether that would be possible to be observed in neuronal cultures, in epileptic rats (intrahippocampal kainic acid model), and human data. Neuronal cultures treated with picrotoxin did not show evidence that FRs could be generated beyond chance aggregation of action potentials. They then asked whether synchronization and firing rate could play a role in the emergence of FRs. They found that changes in neural firing and synchronization, such as those occurring during differences phase of the sleep-wake cycle, could affect the number of FRs occurring by chance aggregation, with more FRs seen during periods of wakefulness, a result that they replicated in human data.

The authors largely achieve their proposed aims of demonstrating that random neuronal firing can, in principle, generate FRs. Results from this study could influence current thinking around mechanisms generating FRs in epilepsy. The use of different computational approaches and model systems could offer new analytical methodologies for the study of FRs in the context of brain disease.

Strengths:

(1) The authors used a multi-level approach combining computational modeling with experimental datasets, including neuronal cultures, a rat model of temporal lobe epilepsy, and human data.

(2) Identification of key parameters such as neuronal count, firing rate, synchronization, and brain state in observed incidence of FRs generated through random aggregation of neural firing.

(3) Cross-species validation increases the likelihood of generalizability of the findings.

Weaknesses:

(1) Some of the simulated FRs appear short in duration and may not meet standard detection and definition criteria, potentially influencing validity.

(2) The neuronal culture approach does not directly test random insertion of action potentials, limiting interpretation.

(3) Sleep is treated as a homogeneous state in the rat dataset, without accounting for stage-specific differences in synchronization, which may affect the results and interpretation.

(4) The analyses conducted in human data lack direct comparison with sleep data.

Reviewer #1 (Public review):

Summary:

This study examines whether gaze direction actively shapes choice during food preference decisions or whether gaze and choice evolve largely independently until the moment of commitment. The established framework in this context, the aDDM, assumes that gaze causally biases the accumulation of evidence in favour of the fixated item. The authors show convincingly that this model fails to fit key behavioural patterns across several datasets, as do other published models that make the same assumption. The authors propose an alternative model (Post-Decision-Gaze or PDG) in which gaze and decision formation are decoupled: gaze does not influence the decision process, nor is it drawn toward the ultimately chosen item, until after the decision threshold is reached. Only during the motor execution period (after commitment) is gaze directed to the chosen option. They demonstrate that this model fits several observed patterns better than the aDDM and related variants.

Strengths:

The work thoroughly considers multiple models and datasets. It advances an interesting alternative perspective on gaze-decision interactions and highlights meaningful shortcomings in existing models. The authors take the time to explain how modelling assumptions produce specific patterns in the data, which is certainly insightful to readers interested in the modelling of value-based decision making.

Weaknesses:

It is unclear to what extent the model's success relies on the way non-decision time is formalised in the model. In the proposed PDG model, non-decision time is decomposed into separate visual encoding, saccadic execution, and manual execution components. Several values (assumed or recovered) do not match known physiological or behavioural ranges. This is a common issue in the literature, and the authors may want to address it in light of broader work discussing what non-decision time consists of in both manual and saccadic actions (e.g., Bompas et al., 2024, Non decision time: the Higgs boson of decision, Psychological Review).

In particular, the "saccadic execution" parameter appears far too long and too variable to reflect merely execution; instead, it likely includes decisional components. This would make more sense since manual and saccadic planning essentially rely on distinct brain areas, hence it seems unrealistic that crossing a single threshold would trigger both manual and saccadic execution. Similarly, recovered manual non-decision times are substantially longer (though not more variable) than expected motor execution durations for button presses. These patterns suggest that parts of what the model treats as non-decision time are likely decisional in nature, although perhaps related to "action decision" rather than the "value-based decision" of interest to the authors. To what extent these two processes neatly follow each other or overlap could be usefully considered.

Reviewer #2 (Public review):

Summary:

Zylberberg et al. reanalyze eye-tracking and behavioral data (mostly from Krajbich et al., 2010) to test two predictions of the attentional Drift Diffusion Model, finding that these predictions are not met. Similarly, predictions of normative models (inspired by rational inattention) are not in line with the data, and the authors propose a post-choice model of attention. This model better accounts for the two effects but also does not account for all patterns, so the authors conclude that eye movements most likely reflect both pre- and post-decisional processes.

Strengths:

A clear strength is the systematic falsification-based approach of the paper, establishing (partially) new predictions and testing to what extent these are met by extant models and by a newly developed theory. The authors do a good job in providing intuitions behind the effects and the reasons why models such as the aDDM predict them. The paper is of substantial relevance for the field, as it shows that effects pertaining to the last fixation(s) should be interpreted with caution. Another strength is the paper's transparency as the authors clearly acknowledge that their new model does not do a perfect job either.

Weaknesses:

The paper focuses on analyzing the Krajbich 2010 data, but shows that the second effect replicates in many other datasets. A more principled approach, in which both effects are analyzed and presented for all datasets, would be more convincing. The results should then be shown together for clarity/readability.

Similarly, it would be nice to show to what extent the models' predictions depend (not depend) on using the best-fitting parameter values (are there any parameter settings under which the two effects are not predicted?)

Reviewer #3 (Public review):

Summary:

In this study, the authors reanalyzed choice, RT and gaze datasets collected from human subjects performing a food-choice task. They show that models that posit a causal role for attention in shaping the decision-making process fail to account for empirical observations in the data. These include the attentional drift diffusion model (aDDM) and models that derive attention-choice associations from an optimal policy. The authors show that a model that assumes that gazes are directed towards the chosen option after decision commitment captures more (but not all) empirical findings, suggesting that attention may reflect decisions once they are made instead of contributing to their formation. However, this post-decision-gaze (PDG) model failed to capture all aspects of the data, suggesting that gaze may reflect both decisional and post-decisional operations, and existing models are still missing some features of the gaze-directing process. The authors provide convincing evidence that post-decision gaze explains a number of empirical findings in this task.

Strengths:

(1) The analyses are generally appropriate, and the conclusions are supported by the data.

(2) The study was rigorous, as the authors considered a number of alternative possible models for behavior, and evaluated their performance based on a wide range of qualitative predictions (as opposed to exclusively relying on model comparison).

(3) The proposal that gaze may largely reflect post-decisional processes is interesting, and as far as I am aware, novel.

Weaknesses:

There was limited discussion about why one might allocate attention post-decision. I would have appreciated more discussion on the potential functional consequences or implications of post-decision gaze.

Reviewer #1 (Public review):

Summary:

This study examines whether gaze direction actively shapes choice during food preference decisions or whether gaze and choice evolve largely independently until the moment of commitment. The established framework in this context, the aDDM, assumes that gaze causally biases the accumulation of evidence in favour of the fixated item. The authors show convincingly that this model fails to fit key behavioural patterns across several datasets, as do other published models that make the same assumption. The authors propose an alternative model (Post-Decision-Gaze or PDG) in which gaze and decision formation are decoupled: gaze does not influence the decision process, nor is it drawn toward the ultimately chosen item, until after the decision threshold is reached. Only during the motor execution period (after commitment) is gaze directed to the chosen option. They demonstrate that this model fits several observed patterns better than the aDDM and related variants.

Strengths:

The work thoroughly considers multiple models and datasets. It advances an interesting alternative perspective on gaze-decision interactions and highlights meaningful shortcomings in existing models. The authors take the time to explain how modelling assumptions produce specific patterns in the data, which is certainly insightful to readers interested in the modelling of value-based decision making.

Weaknesses:

It is unclear to what extent the model's success relies on the way non-decision time is formalised in the model. In the proposed PDG model, non-decision time is decomposed into separate visual encoding, saccadic execution, and manual execution components. Several values (assumed or recovered) do not match known physiological or behavioural ranges. This is a common issue in the literature, and the authors may want to address it in light of broader work discussing what non-decision time consists of in both manual and saccadic actions (e.g., Bompas et al., 2024, Non decision time: the Higgs boson of decision, Psychological Review).

In particular, the "saccadic execution" parameter appears far too long and too variable to reflect merely execution; instead, it likely includes decisional components. This would make more sense since manual and saccadic planning essentially rely on distinct brain areas, hence it seems unrealistic that crossing a single threshold would trigger both manual and saccadic execution. Similarly, recovered manual non-decision times are substantially longer (though not more variable) than expected motor execution durations for button presses. These patterns suggest that parts of what the model treats as non-decision time are likely decisional in nature, although perhaps related to "action decision" rather than the "value-based decision" of interest to the authors. To what extent these two processes neatly follow each other or overlap could be usefully considered.

Reviewer #2 (Public review):

Summary:

Zylberberg et al. reanalyze eye-tracking and behavioral data (mostly from Krajbich et al., 2010) to test two predictions of the attentional Drift Diffusion Model, finding that these predictions are not met. Similarly, predictions of normative models (inspired by rational inattention) are not in line with the data, and the authors propose a post-choice model of attention. This model better accounts for the two effects but also does not account for all patterns, so the authors conclude that eye movements most likely reflect both pre- and post-decisional processes.

Strengths:

A clear strength is the systematic falsification-based approach of the paper, establishing (partially) new predictions and testing to what extent these are met by extant models and by a newly developed theory. The authors do a good job in providing intuitions behind the effects and the reasons why models such as the aDDM predict them. The paper is of substantial relevance for the field, as it shows that effects pertaining to the last fixation(s) should be interpreted with caution. Another strength is the paper's transparency as the authors clearly acknowledge that their new model does not do a perfect job either.

Weaknesses:

The paper focuses on analyzing the Krajbich 2010 data, but shows that the second effect replicates in many other datasets. A more principled approach, in which both effects are analyzed and presented for all datasets, would be more convincing. The results should then be shown together for clarity/readability.

Similarly, it would be nice to show to what extent the models' predictions depend (not depend) on using the best-fitting parameter values (are there any parameter settings under which the two effects are not predicted?)

Reviewer #3 (Public review):

Summary:

In this study, the authors reanalyzed choice, RT and gaze datasets collected from human subjects performing a food-choice task. They show that models that posit a causal role for attention in shaping the decision-making process fail to account for empirical observations in the data. These include the attentional drift diffusion model (aDDM) and models that derive attention-choice associations from an optimal policy. The authors show that a model that assumes that gazes are directed towards the chosen option after decision commitment captures more (but not all) empirical findings, suggesting that attention may reflect decisions once they are made instead of contributing to their formation. However, this post-decision-gaze (PDG) model failed to capture all aspects of the data, suggesting that gaze may reflect both decisional and post-decisional operations, and existing models are still missing some features of the gaze-directing process. The authors provide convincing evidence that post-decision gaze explains a number of empirical findings in this task.

Strengths:

(1) The analyses are generally appropriate, and the conclusions are supported by the data.

(2) The study was rigorous, as the authors considered a number of alternative possible models for behavior, and evaluated their performance based on a wide range of qualitative predictions (as opposed to exclusively relying on model comparison).

(3) The proposal that gaze may largely reflect post-decisional processes is interesting, and as far as I am aware, novel.

Weaknesses:

There was limited discussion about why one might allocate attention post-decision. I would have appreciated more discussion on the potential functional consequences or implications of post-decision gaze.

Reviewer #1 (Public review):

This manuscript investigates how chemogenetic depolarization of medial entorhinal cortex layer II stellate cells reshapes spatial coding in downstream hippocampal CA1. Building on the authors' prior work (Kanter et al., Neuron 2017), the study examines changes in grid cell subfield firing rates and CA1 place cell firing patterns after CNO administration. A central advance of the present work is the use of the same manipulation on two consecutive days. The authors show that the induced grid subfield rate changes are highly similar across days and that CA1 place field reorganization is likewise reproducible across days. In addition, they report that CA1 remapping after CNO is not arbitrary. The new main place field often emerges at a location that can be anticipated from the baseline rate map of the same cell, typically corresponding to a weak secondary peak outside the primary field. Finally, the authors demonstrate that these experimental findings can be recapitulated in a feedforward grid to place cell model by selectively redistributing grid subfield firing rates, supporting the interpretation that grid subfield rate changes are sufficient to drive predictable and reproducible place field reorganization.

Overall, this study is positioned as a follow-up to the authors' previous report in which the main phenomenon (grid subfield rate remapping and accompanying CA1 place cell remapping following chemogenetic depolarization of MEC layer II neurons) was already established. While the conceptual novelty is therefore incremental, the present manuscript adds important and convincing evidence about two key properties of this phenomenon, including its reproducibility across days and the extent to which the direction of place field reorganization is predictable from baseline activity. The experimental approach and analyses appear generally appropriate and carefully executed, and the inclusion of modeling strengthens the mechanistic interpretation. These results provide useful new insight into stable input-output relationships within the entorhinal hippocampal system, and the work will be of interest to researchers studying remapping and the grid to place cell transformation.

Reviewer #2 (Public review):

Summary:

Hippocampal remapping - the collective reorganization of neural tuning properties - is thought to be a crucial determinant of memory outcomes. Understanding its mechanistic bases is a fundamental goal of neuroscience and likely to be critical to understanding memory in health and disease. Here, Lykken et al. 2025 leverage a unique empirical manipulation paired with computational modeling to investigate how one mechanism - reorganization of grid cell subfield firing rates - impacts hippocampal remapping. The authors find that repeated chemogenetic excitation of MEC stellate cells induces reliable reorganization of grid cell subfield firing rates, which is in turn coupled with reliable hippocampal remapping. Notably, the authors show that this hippocampal remapping is not random but predictable, with changes in field location that can be predicted based on weak out-of-field firing observed during control sessions. These findings were well-replicated by a simple model of grid-to-place transformation.

Strengths:

This work has many strengths. One key strength of this work is its compelling demonstration that chemogenetic activation of stellate cells induces changes to the grid and place cell representations, which are reliable across repeated activations. This reliability means that the functional changes induced by this manipulation are not merely noise but rather contain a consistent structure that can be investigated to gain insight into the entorhinal-hippocampal transformation. Similarly, the demonstration that hippocampal remapping during this manipulation is not random, but predictable at the single-cell level, is also a strength. This predictability can help us distinguish competing mechanisms of remapping and place field formation more generally. Finally, by reproducing key experimental outcomes with a straightforward grid-to-place computational model, the authors show that this relatively simple model is sufficient to understand their results.

Weaknesses:

This work also has limitations that leave some relevant questions open at this time. One such set of questions which might be addressable with the author's data and modeling concerns population analyses. Do grid fields at similar locations exhibit similar changes in field properties, or do these fields change independently? Are changes in field location consistent or inconsistent among simultaneously recorded place cells? Would we expect or not expect such a structure given the model? These results might help discriminate between different mechanisms possibly at play.

Another limitation of this work is its reliance on a single measure of predictability. While this is a great start, and the various controls and modeling are appreciated, I wonder whether the modeling could be used to generate additional verifiable predictions. For example, perhaps analyzing whether there is or is not structure to unpredictable errors (are these distributed around predictions but further away, or are they random)?

Finally, one limitation comes from the between-group nature of the recordings. Because the MEC and hippocampus are recorded in separate groups of animals, the authors lose the ability to test whether each mouse's particular grid field reorganization predicts its particular pattern of remapping. If the author's model is correct, then one might hope to be able to predict with even higher accuracy the particular patterns of remapping in CA1 given sufficiently well-characterized grid field changes. This ambitious goal would require simultaneous recordings from the hippocampus and entorhinal cortex, which are beyond the scope of the current work, but would ultimately yield even more compelling evidence of the grid-to-place transformation underlying this form of remapping.

Christopher Buckley: “Steaming to Bamboola” and Other Journeys

Bill Buckley's Royal HH from the National Review.

Almost hilarious that a gloved assistant brings it out and then removes it once they're done discussing it. Something so effete-ist about this that would be befitting Buckley himself.

Reviewer #1 (Public review):

This study by Riegman & George et al. investigates the roles of the chromatin remodeling factor CHD7 and the proneural transcription factor Atoh1 at enhancers in cerebellar granule cells (GCs). Enhancers were categorized based on epigenetic marks and cross-referenced with promoter capture-HiC, ATAC-seq, and expression datasets to identify their long-range target genes, which were found to be enriched for critical neurodevelopmental processes. Differential expression and chromatin accessibility analyses in CHD7 knockout (KO) conditions suggest that this factor regulates a significant number of enhancers. These same enhancers are enriched for proneural transcription factor motifs, with Atoh1 being the most frequently present and likely the most affected. Finally, the direct interaction between CHD7 and Atoh1 was assessed via co-immunoprecipitation in co-transfected cells.

While the paper presents an interesting aspect of enhancer regulation in neurodevelopment, several points warrant attention:

Major Strengths:

The use of chromatin marks increases the resolution of promoter-interacting enhancer regions when integrated with capture-HiC, refining the identification of distal enhancers. Additionally, performing promoter capture-HiC experiments for the first time in this cell type constitutes a valuable resource for the community working on 3D genome organization and neurodevelopment.

Major Weaknesses:

As noted by the authors, limited sequencing depth reduces confidence in the conclusions and may result in missed weaker long-range interactions. Furthermore, the absence of capture-HiC and Atoh1 ChIP-seq experiments in the KO condition prevents direct comparison, thereby limiting the strength of the conclusions.

Additional Consideration:

Caution should be exercised regarding the assumption that every enhancer must physically contact its target promoter. While true for many enhancers, some act in trans through eRNAs or lncRNAs without direct physical contact.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors aim to identify active, long-range regulatory interactions in cerebellar granule cell progenitors (GCps). As such, the authors perform promoter capture Hi-C to map long-range interactions for all gene promoters, using cells isolated from P7 mouse brain samples. While the resolution of these maps is limited by the relatively large fragment sizes generated from a 6-bp cutter, the authors combine these interactions with other available published datasets, including from their own previous work, (e.g. ATAC-seq and ChIP-seq) to more precisely map putative enhancers within the long-range interacting regions of captured promoters. The paper further focuses on the importance of transcription factor Atoh1 and chromatin remodeller CHD7 in regulation of these putative enhancers in GCps. The authors suggest a direct interaction between CHD7 and Atoh1 by overexpression and co-immunoprecipitation in human embryonic kidney cells.

As stated by the authors, this study represents a valuable resource for researchers interested in the identification of enhancers in GCps cells, and their linked target genes. While broadly descriptive, the study does highlight some gene loci of interest and of biological relevance. For example, through integration of previously published datasets, the study resolves which putative regulatory elements at the Reln locus may regulate its activity.

This manuscript will be of interest to researchers interested in analysing long-distance targets of as well as researchers trying to understand the precise gene regulation in cerebellar development. It may also be of interest to clinical geneticists to interpret novel putative non-coding disease mutations.

Strengths:

The strengths of this manuscript are the integrated approach to identify cell-type specific enhancers utilizing available epigenomic datasets, and leveraging 3D genome topology to directly link them to their target genes. For example for the Reln gene previously implicated in cerebellar phenotypes for CHD7 mutants. The pcHi-C dataset generated in this study provides a valuable reference for the community of enhancer-promoter pairs for a specific cell-type of interest with human disease relevance.

Weaknesses:

The limitations of the study are partially addressed in the text by the authors, including the resolution from the pcHi-C using a 6-bp cutter, the limitation of sequencing depth (more interactions may have been identified with more depth), and the limited of correlation between replicates (likely due to undersampling the library). Page 9 "some additional interactions with the nearest gene promoters might be identified in our pcHi-C dataset with deeper sequencing".

Reviewer #3 (Public review):

Summary:

In this work, Riegman et al. establish the promoter interactome of cerebellar granule cell progenitors (CGPs) and identify thousands of putative enhancers regulating key genes in this cell population. The authors isolate primary CGps cells from the mouse cerebellum and perform promoter capture Hi-C in order to reanalyse previously generated epigenomic datasets (ATAC-seq, H3K4me1/3, H3K27ac) in these cells. They identify 22'797 enhancers interacting with gene promoters. The authors then use CHD7 ChIP-seq experiments to better annotate regulatory regions linked to genes deregulated upon CHD7 loss of function. After observing that CHD7 is frequently co-bound with ATOH1, they compare the binding profiles of ATOH1 and CHD7 together with genes deregulated in loss-of-function datasets, and refine the regulatory elements associated with each of these proteins.

Strengths:

The work is well designed and carefully executed, leading to an enhancer-promoter (E-P) interaction cartography that largely surpasses the current standard in the field. The pc-HiC dataset enables a deeper analysis of previously generated datasets (ChIP-seq and loss-of-function), which clearly improves the understanding of the mechanisms underlying CGps proliferation and differentiation. Moreover, the integration of published loss-of-function datasets for CHD7 and ATOH1 is relatively novel in this type of study and helps reduce the purely descriptive nature of the work. In particular, the analysis sheds light on genes with potential functions in CGps that had not previously been identified, as well as their regulatory connections. Overall, the study is convincing and supports the conclusions presented by the authors.

Weaknesses:

(1) A substantial part of the manuscript focuses on E-P interactions in CGPs, which gives the impression that this is primarily a genome organisation study. However, in this regard the manuscript does not bring major conceptual novelties. In contrast, the biological insights related to CGPs and the identification of new candidate genes likely represent the most novel aspect of the work. The authors should clarify the central message of the manuscript and reorganise the presentation of the results accordingly.

(2) The numbers presented throughout the manuscript are sometimes confusing. For instance, the authors initially report 106'589 PIF (line 175), but later only 61'928 (line 243) when calling enhancers. The relationship between these numbers is not straightforward. More generally, simplifying the nomenclature used to describe interaction analyses would help emphasise the biological insights rather than the computational framework.

(3) ATAC-seq alone is a relatively poor predictor of enhancers. In this context, H3K27ac would provide a more accurate marker of enhancer activity. This point is particularly important because the authors' data suggest that CHD7 does not function as a pioneer factor capable of opening chromatin. Instead, this role appears to be more closely associated with ATOH1. Therefore, alterations in CHD7 are more likely to affect enhancer activity (reflected by H3K27ac) rather than chromatin accessibility itself. If the authors do not have access to H3K27ac ChIP-seq data, this limitation should be explicitly acknowledged.

(4) The authors do not functionally test most enhancers and instead discuss primarily putative enhancers (with the exception of VISTA-tested elements). Although the term "putative enhancer" appears in some subsections, it is not consistently applied throughout the manuscript. This limitation should be clearly stated early in the manuscript with a sentence such as: "As these regions have not been functionally validated, they should be considered putative enhancers. However, for simplicity, we will refer to them as enhancers throughout the manuscript."

(5) Where feasible, the enhancer identified at the Reln gene should be functionally tested to demonstrate the added value of the approach.

Reviewer #1 (Public review):

Summary:

Overall, this is an interesting paper. The authors identify several experimental knobs that can perturb mechanical wave behavior driven by pili feedback. They frame these effects in terms of nonreciprocal interactions. While nonreciprocity could indeed play a role, it raises the question of whether mechanical feedback might also contribute. Phenomenological models can be useful, but the model currently lack direct mechanistic insight. It would be more compelling to formulate the model around potential mechanochemical feedback, which could help clarify the underlying microscopic mechanisms.

Strengths:

Report of mechanical waves in bacterial collectives, mechanism has potential application in multicellular context such as morphogenesis.

Weaknesses:

A minor concern about the language of 'left-right asymmetry.' I believe the correct term is simply 'radial asymmetry' which is a distinct concept. Left-right is not well defined in the current context.

Reviewer #3 (Public review):

Summary:

The revised manuscript presents a compelling study of radially propagating metachronal waves on the surface of Pseudomonas nitroreducens biofilms, combining experiments with two theoretical descriptions (a local phase-oscillator model and an active solid/active gel model). The central experimental findings-spiral/target/planar wave patterns, their controllability via water/PEG/temperature perturbations, and the correlation between frequency gradients and propagation direction-remain highly interesting and relevant to both bacterial biophysics and active-matter physics. The revised manuscript also adds substantial new material, including additional analyses of defect dynamics and clearer discussion of the relationship between the two models. The study continues to have a strong interdisciplinary appeal and the potential to stimulate further work on collective oscillations in biological active media.

Strengths:

The authors have substantially addressed the major conceptual issue raised in the previous round by clearly distinguishing between nonreciprocity and frequency gradients / global asymmetry. This clarification significantly improves the theoretical interpretation and resolves an important source of confusion in the original version.

The revised manuscript also improves the connection between the phase-oscillator and active-solid descriptions. In particular, the authors now explain more explicitly how the phase variable is defined in the reduced oscillatory dynamics of confined biofilm motion, and they state that they added a schematic illustration and simulation details (including parameter values and the elastic-force definition) to improve reproducibility. This directly addresses one of my previous major concerns.

A notable improvement is the newly added defect-based analysis of waveform transitions (spiral -> target -> planar). The revised text argues that defect motility is a key control parameter, linked experimentally to moisture-dependent elasticity and theoretically to nonreciprocity / defect-pair stability. This provides a more concrete mechanistic bridge between experimental perturbations and the modeling framework than in the previous version.

The manuscript now gives a clearer experimental-theoretical narrative for how environmental manipulations (drying, water addition, PEG, heating) affect wave patterns through changes in effective elasticity and activity, including a useful distinction between short-timescale and long-timescale temperature effects. This added discussion strengthens the biological interpretation and makes the modeling assumptions easier to follow.

Weaknesses:

The main remaining limitation is the level of quantitative correspondence between theory and experiment. The revised manuscript now provides a stronger qualitative/mechanistic link, but the mapping between model parameters (e.g., effective coupling terms / elasto-active parameters) and directly measurable biofilm properties is still limited. The authors acknowledge this point, and I agree that it is technically challenging in the present system. However, this means the theoretical framework is currently most convincing as an effective mechanistic model rather than a quantitatively predictive one.

Relatedly, some conclusions about parameter-level control (especially in connecting moisture/temperature manipulations to specific model parameters) remain qualitative. I do not view this as fatal, but I recommend that the manuscript clearly state this scope and avoid overstating the quantitative predictive power of the theory.

Although the terminology has improved compared with the original version, the revised manuscript still uses "left-right asymmetry" in places where the underlying geometry and symmetry are more general (e.g., radial inward propagation in circular colonies). Since this wording was one of the original points of confusion, I suggest one final pass to ensure the symmetry language is consistently precise throughout the main text and figure captions.

Reviewer #1 (Public review):

Summary:

Sullivan and colleagues examined the modulation of reflexive visuomotor responses during collaboration between pairs of participants performing a joint reaching movement to a target. In their experiments, the players jointly controlled a cursor that they had to move towards narrow or wide targets. In each experimental block, each participant had a different type of target they had to move the joint cursor to. During the experiment, the authors used lateral perturbation of the cursor to test participants' fast feedback responses to the different target types. The authors suggest participants integrate the target type and related cost of their partner into their own movements, which suggests that visuomotor gains are affected by the partner's task.

Strengths:

The topic of the manuscript is very interesting, and the authors are using well-established methodology to test their hypothesis. They combine experimental studies with optimal control models to further support their work. Overall, the manuscript is very timely and shows important findings - that the feedback responses reflect both our and our partners tasks.

Reviewer #2 (Public review):

Summary:

Sullivan and colleagues studied the fast, involuntary, sensorimotor feedback control in interpersonal coordination. Using a cleverly designed joint-reaching experiment that separately manipulated the accuracy demands for a pair of participants, they demonstrated that the rapid visuomotor feedback response of a human participant to a sudden visual perturbation is modulated by his/her partner's control policy and cost. The behavioral results are well matched with the predictions of the optimal feedback control framework implemented with the dynamic game theory model. Overall, the study provides an important and novel set of results on the fast, involuntary feedback response in human motor control in the context of interpersonal coordination.

Review:

Sullivan and colleagues investigated whether fast, involuntary sensorimotor feedback control is modulated by the partner's state (e.g., cost and control policy) during interpersonal coordination. They asked a pair of participants to make a reaching movement to control a cursor and hit a target, where the cursor's position was a combination of each participant's hand position. To examine fast visuomotor feedback response, the authors applied a sudden shift in either the cursor (experiment 1) or the target (experiment 2) position in the middle of movement. To test the involvement of partner's information in the feedback response, they independently manipulated the accuracy demand for each participant by varying the lateral length of the target (i.e., a wider/narrower target has a lower/higher demand for correction when movement is perturbed). Because participants could also see their partner's target, they could theoretically take this information (e.g., whether their partner would correct, whether their correction would help their partner, etc.) into account when responding to the sudden visual shift. Computationally, the task structure can be handled using dynamic game theory, and the partner's feedback control policy and cost function are integrated into the optimal feedback control framework. As predicted by the model, the authors demonstrated that the rapid visuomotor feedback response to a sudden visual perturbation is modulated by the partner's control policy and cost. When their partner's target was narrow, they made rapid feedback corrections even when their own target was wide (no need for correction), suggesting integration of their partner's cost function. Similarly, they made corrections to a lesser degree when both targets were narrower than when the partner's target was wider, suggesting that the feedback correction takes the partner's correction (i.e., feedback control policy) into account.

The strength of the current paper lies in the combination of clever behavioral experiments that independently manipulate each participant's accuracy demand and a sophisticated computational approach that integrates optimal feedback control and dynamic game theory. Both the experimental design and data analysis sound good and the main claim is well supported by the results.

A future direction would be to investigate how this mechanism is implemented in the CNS and to examine whether the same cooperative mechanism also applies to human-AI interactions.

Reviewer #1 (Public review):

Summary:

This study investigates how collective navigation improvements arise in homing pigeons. Building on the Sasaki & Biro (2017) experiment on homing pigeons, the authors use simulations to test seven candidate social learning strategies of varying cognitive complexity, ranging from simple route averaging to potentially cognitively demanding selective propagation of superior routes. They show that only the simplest strategy-equal route averaging-quantitatively matches the experimental data in both route efficiency and social weighting. More complex strategies, while potentially more effective, fail to align with the observed data. The authors also introduce the concept of "effective group size," showing that the chaining design leads to a strong dilution of earlier individuals' contributions. Overall, they conclude that cognitive simplicity rather than cumulative cultural evolution explains collective route improvements in pigeons.

Strengths:

The manuscript provides a compelling argument that a simpler hypothesis is necessary and sufficient to explain the findings of a recent study on improvements to pigeon routes, through a rigorous, systematic comparison of seven alternative hypotheses. The authors should be commended for their willingness to critically re-examine established interpretations. The introduction and discussion are broad and link pigeon navigation to general debates on social learning, wisdom of crowds, and CCE.

Weaknesses:

The authors' method focuses on trajectory-level average behaviour rather than the fine-scale decision-making processes of organisms. This is acknowledged in the manuscript by the authors.

Comments on revision:

The authors have addressed most of the comments by me as well as the other reviewer.

Reviewer #2 (Public review):

Summary:

The manuscript investigates which social navigation mechanisms, with different cognitive demands, can explain experimental data collected from homing pigeons. Interestingly, the results indicate that the simplest strategy - route averaging - aligns best with the experimental data, while the most demanding strategy - selectively propagating the best route - offers no advantage. Further, the results suggest that a mixed strategy of weighted averaging may provide significant improvements.

The manuscript addresses the important problem of identifying possible mechanisms that could explain observed animal behavior by systematically comparing different candidate models. A core aspect of the study is the calculation of collective routes from individual bird routes using different models that were hypothesized to be employed by the animals but which differ in their cognitive demands.

The manuscript is well written, with high-quality figures supporting both the description of the approach taken and the presentation of results. The results should be of interest to a broad community of researchers investigating (collective) animal behavior, ranging from experiment to theory. The general approach and mathematical methods appear reasonable and show no obvious flaws. The statistical methods also appear.

Strengths:

The main strength of the manuscript is the systematic comparison of different meta-mechanisms for social navigation by modeling social trajectories from solitary trajectories and directly comparing them with experimental results on social navigation. The results show that the experimentally observed behavior could, in principle, arise from simple route averaging without the need to identify "knowledgeable" individuals. Another strength of the work is the establishment of a connection between social navigation behavior and the broader literature on the wisdom of crowds through the concept of effective group size.

Comments on revision:

The authors made substantial revisions to the manuscript, addressing my comments. While I do think that regarding my second comment on CCE the authors could be a bit more bold, I am overall satisfied with the revisions made.

Reviewer #1 (Public review):

[Editors' 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.]

Original review:

Summary:

This manuscript reports a very interesting, novel and important research angle to add to the now enormous interest in how pesticides can be toxic to beneficial insects like the honey bee. Many studies have reported on how pesticides in standard use formulations show both lethality as well as sublethal negative effects on behavior and reproduction. The authors propose to use machine learning algorithms to identify new volatile compounds that can be tested for repellency. They use as input chemical structures that are derived from chemicals that have known repellent effects as identified in their initial behavioral assays.

Strengths:

The conclusion is that such chemicals specific to repelling bees and not pest insects (using the fruit fly as a model for the latter) can be identified using the ML approach. Have a list of such chemicals that can be rotated among in any field application would be a benefit because of the honey bees' ability to learn its way around any kind of stimulus designed to keep it from nectar and pollen, even when they may be tainted by pesticide.

Weaknesses:

The use of machine learning seems well-executed and legitimate. But this is beyond my expertise. So other reviewers can maybe comment more on that.

The behavioral data report on the use of a two-choice assay for bees in small Petrie plates. Bess can feed from two small wells place of filter paper impregnated with control or the control containing a chemical. The primary behavior, for ex in Fig 2C, is the first choice by one of the five bees in the plate of which well to feed from. For some chemical compound, there seems to be a 50:50 choice, indicating no repellent effects. In other cases the first bee making the choice chose the control, indicating possible repellent effects of the test chemical. Choices in this assay were validated in a free flying assay.

Concerns with the choice assay:

- 50-70 microliters amounts to what one hungry bee will drink. Did the first bee drink most of it, such that measures of bait consumed reflect a single bee or multiple bees?<br /> - How many bees were repelled to the control side? Was it just the one bee? Were other measures considered? E.g. time to first approach; the number of bees feeding at different time points; the total number of bees observed feeding per unit time.

Reviewer #2 (Public review):

Original review:

Summary:

The search for new repellent odors for honey bees has significant practical implications. The authors developed an iterative pipeline through machine learning to predict honey bee-repellent odors based on molecular structures. By screening a large number of candidate compounds, they identified a series of novel repellents. Behavioral tests were then conducted to validate the effectiveness of these repellents. Both the discovery and the methodological approach hold value for related fields.

Strengths:

* The study demonstrates that using molecular structures and a relatively small training dataset, the model could predict repellents with a reasonably high success rate. If the iterative approach works as described, it could benefit a wide range of olfaction-related fields.<br /> * The effectiveness of the predicted repellents was validated through both laboratory and field behavioral tests.

Weaknesses:

The small size of the training dataset poses a common challenge for machine learning applications. However, the authors did not clearly explain how their iterative approach addresses this limitation in this study. Quantitative evidence demonstrating improvements achieved in the second round of training would strengthen their claims. For instance, details on whether the success rate of predictions or the identification of higher-affinity components would be helpful. Furthermore, given that only 15 new components were added for the second round of training, it is surprising that such a small dataset could result in significant improvements.

Reviewer #3 (Public review):

Original summary:

The manuscript of Kowalewski et al. titled "Machine learning of honey bee olfactory behavior identifies repellent odorants in free flying bees in the field" did machine learning to predict potential candidates for honeybee repellents, which may keep foraging bees from pesticides. This is a pilot research with strong significance in the research of olfactory behavior and in pest control.

Reviewer #1 (Public review):

Summary:

Goicoechea et al. conducted a timely and thorough meta-analysis on the potential for indirect hippocampal targeted transcranial magnetic stimulation (TMS) to improve episodic memory. The authors included additional factors of interest in their meta-analysis which can be used to inform the next generation of studies using this intervention. Their analysis revealed critical factors for consideration: TMS should be applied pre-encoding, individualized spatial targeting improves efficacy, and improvement of recollection was stronger than recognition.

Strengths:

As mentioned previously, the meta-analysis is timely and summarizes an emerging set of studies (over the past decade since Wang et al., Science 2014). Those outside of the field may not be aware of the robustness in improvements in episodic memory from hippocampal targeted TMS. The authors were quite thorough in including additional factors which are important for the interpretation of these findings. These factors also address the differences in approach across studies. The evidence that individualized spatial targeting improves TMS efficacy is consistent with recent advances in TMS for major depressive disorder. The specificity of the cognitive improvements to recollection of episodic memory and not for other cognitive domains is consistent with hippocampal targeting. The authors also plan to post the complete dataset on an open-source repository which enables additional analysis by other researchers.

Weaknesses:

The write-up is succinct and emphasizes the scientific decisions that underly key differences in the various experimental designs. While the manuscript is written for a scientific audience, the authors are likely aware that findings like this will be of broad appeal to the field of neurology where treatments for memory loss are desperately needed. For this reason, the authors could consider including a statement regarding an interpretation of this meta-analysis from a clinical standpoint. Statements such as 'safe and effective' imply a clinical indication and yet the manuscript does not engage with clinical trials terminology such as blinding, parallel arm versus crossover design, and trial phase. While the authors might prefer not to engage with this terminology, it can be confusing when studies delivering intervention-like five-days of consecutive TMS (e.g., Wang et al., 2014) are clustered with studies that delivered online rhythmic TMS which tests target engagement (e.g., Hermiller et al., 2020). While the 'sessions' variable somewhat addresses the basic-science versus intervention-like approach, adding an explicit statement regarding this in the discussion might help the reader to navigate the broad scope of approaches that are utilized in the meta-analysis.

Following revision: The authors have adequately addressed my concerns.

Reviewer #2 (Public review):

Parietal lobe TMS, targeted to the episodic memory network via connections with the structures in the medial temporal lobe, improves episodic memory. This is one of very few robustly reproduced cognitive findings in noninvasive brain stimulation. The comprehensive review and detailed meta-analysis by Goicoechea et al. makes a convincing case for efficacy in healthy people and will be important for neuroscientists and clinical researchers in memory and dementia.

In 2014, Wang et al. showed that noninvasive stimulation of a parietal site, connected functionally to the hippocampus, increased resting state functional connectivity throughout a canonical network associated with episodic memory. It also caused a memory boost which was proportional to the connectivity increase within subjects. Their discovery that an imaging biomarker could (1) be used to target a functional network with critical nodes too deep to reach directly with TMS, (2) enable individualized, functionally confirmed, targeting, and (3) provide a scaling measure of target engagement, is one of the signal advances in noninvasive brain stimulation.

The meta-analytical methodology used by these authors is rigorous, and the central finding, viz. that high-frequency, network-targeted stimulation reproducibly improves event recall, is amply supported. The question of whether to stimulate before or after memory encoding is also answered. While there is a hint that individualized anatomical or functional MRI-based targeting may be superior to atlas or group average-based techniques, the finding did not survive correction for multiple comparisons. Additional studies will be needed to resolve this issue, optimize the stimulation delivery parameters, and further define the behavioral effect.

While the authors appropriately emphasize the associated network rather than the hippocampus itself, naming the target after a single node could suggest a primary role for the hippocampus in the observed outcomes, a conclusion not supported by the data reviewed here. Other nodes in the network are be equally important to aspects of episodic memory and could be useful targets for stimulation.

Despite encouraging results from small clinical samples, the question of efficacy in patients with static lesions and ongoing neurodegeneration remains open. The information gathered here, including the absence of reported adverse events, should spur Phase 2 clinical trials in patients with disorders of memory.

Reviewer #3 (Public review):

Summary:

The manuscript by Goicoechea et al. assesses the influence of hippocampal-network targeted TMS to parietal cortex on episodic memory using a meta-analytic approach. This is an important contribution to the literature, as the number of studies using this approach to modulate memory/hippocampal function has clearly increased since the initial publication by Wang et al. 2014. This manuscript makes an important contribution to the literature. In general, the analysis is straightforward and the conclusions are well-supported by the results.

Strengths:

(1) A meta-analysis across published work is used to evaluate the influence of hippocampal-network-targeted TMS in parietal cortex on episodic memory. By pooling results across studies, the meta-analytic effects demonstrate an influence of TMS on memory across the diversity of many details in study design (specific tasks, stimuli, TMS protocols, study populations).

(2) Selectivity with regard to episodic memory vs. non-episodic memory tasks is evaluated directly in the meta-analysis.

(3) The investigation into supplemental factors as predictors of TMS's influence on memory was tested. This is helpful given the diversity of study designs in the literature. This analysis helps to shed light on which study designs, e.g., TMS protocols, etc., are most effective in memory modulation.

Weaknesses:

The authors thoroughly addressed and responded to the prior comments in the revision. The only minor weakness I see is acknowledged in terms of how null effects for particular design or TMS features should be interpreted (i.e., with caution given the regression approach used).

Reviewer #1 (Public review):

Summary:

This work provides structural and mechanistic insights into the disordered protein recognition process inside the endoplasmic reticulum by the inositol-requiring enzyme 1. Using state-of-the-art molecular dynamics simulation tools, the authors propose a mechanism of disordered protein recognition that reconciles contradictory findings of biochemical and structural biology experiments.

Strengths:

(1) All MD simulations have been carried out in triplicates, and several different folded conformations were generated using alphafold2. This provides adequate statistics to draw meaningful conclusions from the simulations.

(2) Potential limitations of the disordered protein force fields and water models have been taken into consideration. Particularly, performing the simulation in both TIP3P and TIP4PD water models ensures that the conclusions drawn are not influenced by the force field choice.

(3) The binding of a large number of disordered peptides was investigated, ensuring that the conclusions drawn about disordered peptide recognition are sufficiently general.

Weaknesses:

(1) The timescales of the peptide recognition and unbinding process are much longer than what can be sampled from unbiased simulations. Therefore, the proposed mechanism of recognition should only be considered a hypothesis based on the results presented here. For example, peptides that do not dissociate within one microsecond MD simulation are considered to be stable binders. However, they may not have a viable way to bind to the narrow protein cleft in the first place.

(2) Oftentimes, representative structures sampled from MD simulation are used to draw conclusions (e.g., Figure 4 about the role of R161 mutation in binding affinity). This is not appropriate as one unbinding event being observed or not observed in a microsecond-long trajectory does not provide sufficient information about the binding strength of free energy difference.

Comments on revisions:

The authors have adequately addressed my comments. I have no further comments.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors investigated the interactions between IRE and unfolded peptides using all-atom molecular dynamics simulations. The interactions between a couple of unfolded peptides and IRE provide mechanistic insight on the activation of the UPR.

Strengths:

- Well-written manuscript accessible for a broad biological audience

- State-of-art structural predictions and all-atom simulations

- Validation with existing experimental data<br /> - Clear schematic diagram summarizing mechanisms learned from simulations

- Error estimate included

- Shared simulation data and code in public repository

Weakness:

No major concerns remain after revision.

Comments on revisions:

The authors have addressed all my questions from the previous assessment. I do not have more suggestions.

Reviewer #3 (Public review):

Summary:

In this important work, the authors use extensive MD simulations to study how the IRE1 protein can detect unfolded peptides. Their study consolidates contradictory experimental results and offers a unique view of the different sensing models proposed in the literature. Overall, it is an excellent study that is quite extensive. The research is solid, meticulous, and carefully performed, leading to convincing conclusions.

Strengths:

The strength of this work is the extensive and meticulous molecular dynamics simulations. The authors use and investigate different structural models, for example carefully comparing a model based a PDB structure with reconstructed loops with a AlphaFold 2 Multimer model. The authors also investigate a wide range of different protein structural models that probe different aspects of the peptide-sensing process. Additionally, the authors experimentally validate a part of the simulation results. These solid and meticulous MD simulations allow the authors to obtain convincing conclusions concerning the peptide-sensing process of the IRE1 protein.

Weaknesses:

A potential weakness of the study is the use of equilibrium (unbiased) molecular dynamics simulations, which means only processes and conformational changes on the microsecond timescale can be probed. Furthermore, there can be inaccuracies and biases in the description of unfolded peptides and protein segments due to the protein force fields. Here, it should be noted that the authors do acknowledge these possible limitations of their study in the conclusions. Furthermore, in the revised version, the authors partly address this weakness by employing orthogonal simulation methods and experimental techniques.

Comments on revisions:

The authors have addressed all the issues that I raised in my previous report.

Reviewer #1 (Public review):

Summary:

Thach et al. report on the structure and function of trimethylamine N-oxide demethylase (TDM). They identify a novel complex assembly composed of multiple TDM monomers and obtain high-resolution structural information for the catalytic site, including an analysis of its metal composition, which leads them to propose a mechanism for the catalytic reaction.

In addition, the authors describe a novel substrate channel within the TDM complex that connects the N-terminal ZnZn²⁺-dependent TMAO demethylation domain with the C-terminal tetrahydrofolate (THF)-binding domain. This continuous intramolecular tunnel appears highly optimized for shuttling formaldehyde (HCHO), based on its negative electrostatic properties and restricted width. The authors propose that this channel facilitates the safe transfer of HCHO, enabling its efficient conversion to methylenetetrahydrofolate (MTHF) at the C-terminal domain as a microbial detoxification strategy. Experimental data that shows an involvement of TDM in the reaction of HCHO with THF is less convincing.

Strengths:

The authors provide convincing high-resolution cryo-EM structural evidence (up to 2 Å) revealing an intriguing complex composed of two full monomers and two half-domains. They further present evidence for the metal ion bound at the active site and articulate a hypothesis for the catalytic cycle. Substantial effort is devoted to optimizing and characterizing enzyme activity, including detailed kinetic analyses across a range of pH values, temperatures, and substrate concentrations. Furthermore, the authors validate their structural insights through functional analysis of active-site point mutants.

In addition, the authors identify a continuous channel for formaldehyde (HCHO) passage within the structure and support this interpretation through molecular dynamics simulations. These analyses suggest an exciting mechanism of specific, dynamic, and gated channelling of HCHO. This finding is particularly appealing, as it implies the existence of a unique, completely enclosed conduit that may be of broad interest, including potential applications in bioengineering.

Weaknesses:

Although the idea of an enclosed channel for HCHO is compelling, the experimental evidence supporting enzymatic assistance in the reaction of HCHO with THF is less convincing. The linear regression analysis shown in Figure 1C demonstrates a THF concentration-dependent decrease in HCHO; however, it is well established that HCHO and THF can react spontaneously in a non-enzymatic manner, raising the possibility that the observed effect does not require enzymatic involvement. I appreciate the authors' clarification that the data in Figure 1 were not intended to demonstrate enzymatic channelling or catalytic involvement in the HCHO-THF reaction, and that the assay does not distinguish between changes in HCHO production and downstream consumption. However, the statement "these findings show that TDM carries out two linked reactions: TMAO demethylation at one active site, and the HCHO produced can condense with THF at the C-terminal domain, connecting TMAO breakdown to one-carbon metabolism" (page 2) still implies a mechanistic and functional coupling that is not supported by the presented data and appears inconsistent with the authors' clarification. In light of this, I recommend revising this statement to avoid implying mechanistic or functional coupling between the two reactions unless additional experimental evidence is provided.

Overall, the authors were successful in advancing our structural and functional understanding of the TDM complex. They suggest an interesting oligomeric complex composition which should be investigated with additional biophysical techniques.

Additionally, they provide an intriguing hypothesis for a new type of substrate channelling. Additional kinetic experiments focusing on HCHO and THF turnover by enzymatic proximity effects would strengthen this potentially fundamental finding. If this channelling mechanism can be supported by stronger experimental evidence, it would substantially advance our understanding and knowledge of biologic conduits and enable future efforts in the design of artificial cascade catalysis systems with high conversion rate and efficiency, as well as detoxification pathways.

Reviewer #2 (Public review):

Summary:

The manuscript reports a cryo-EM structure of TMAO demethylase from Paracoccus sp. This is an important enzyme in the metabolism of trimethylamine oxide (TMAO) and trimethylamine (TMA) in human gut microbiota, so new information about this enzyme would certainly be of interest.

Strengths:

The cryo-EM structure for this enzyme is new and provides new insights into the function of the different protein domains, and a channel for formaldehyde between the two domains.

Weaknesses:

(1) The proposed catalytic mechanism in this manuscript does not make sense. Previous mechanistic studies on the Methylocella silvestris TMAO demethylase (FEBS Journal 2016, 283, 3979-3993, reference 7) reported that, as well as a Zn2+ cofactor, there was a dependence upon non-heme Fe2+, and proposed a catalytic mechanism involving deoxygenation to form TMA and an iron(IV)-oxo species, followed by oxidative demethylation to form DMA and formaldehyde.

In this work, the authors do not mention the previously proposed mechanism, but instead just say that elemental analysis "excluded iron". This is alarming, since the previous work has a key role for non-heme iron in the mechanism. The elemental analysis here gives a Zn content of about 0.5 mol/mol protein (and no Fe), whereas the Methylocella TMAO demethylase was reported to contain 0.97 mol Zn/mol protein, and 0.35-0.38 mol Fe/mol protein. It does, therefore, appear that their enzyme is depleted in Zn, and the absence of Fe impacts on the mechanism, as explained below.

The proposed catalytic mechanism in this manuscript, I am sorry to say, does not make sense, for several reasons:

i) Demethylation to form formaldehyde is not a hydrolytic process; it is an oxidative process (normally accomplished by either cytochrome P450 or non-heme iron-dependent oxygenase). The authors propose that a zinc (II) hydroxide attacks the methyl group, which (a) is unprecedented, (b) even if it were possible, would generate methanol, not formaldehyde.

ii) The amine oxide is proposed to deoxygenate, with hydroxide appearing on the Zn - unfortunately, amine oxide deoxygenation is a reductive process, for which a reducing agent is needed, and Zn2+ is not a redox active metal ion;

iii) The authors say "forming a tetrahedral intermediate, as described for metalloprotease" but zinc metalloproteases attack an amide carbonyl to form an oxyanion intermediate, whereas in this mechanism there is no carbonyl to attack, so this statement is just wrong.

So on several counts the proposed mechanism cannot be correct. Some redox cofactor is needed in order to carry out amine oxide deoxygenation, and Zn2+ cannot fulfil that role. Fe2+ could do, which is why the previously proposed mechanism involving an iron(IV)-oxo intermediate is feasible. But the authors claim that their enzyme has no Fe. If so then there must be some other redox cofactor present. Therefore, the authors need to re-analyse their enzyme carefully and look either for Fe or for some other redox-active metal ion, and then provide convincing experimental evidence for a feasible catalytic mechanism. As it stands the proposed catalytic mechanism is unacceptable.

Revised version. The authors have essentially not changed the proposed mechanism. They have removed the reference to zinc metalloproteases, but still propose a mechanism mediated only by Zn2+. As explained above, attack by zinc (II) hydroxide is unprecedented and would generate methanol, not formaldehyde, and amine deoxygenation is a reductive process that cannot be fulfilled by Zn2+. So the proposed mechanism is still not feasible at all. The authors now say that "oxidative chemistry....remains unresolved", I'm sorry, but that is not acceptable.

I have urged the authors to re-examine the metal content of their enzyme, In the Supporting Information (Figure S5) they give ICPMS data that indicates a Zn stoichiometry of 0.5 mol Zn/mol protein, and Fe is not detected. Have the authors analysed for other redox active metals? The authors say that there is no evidence for any other metal binding site, but there is only 50% occupancy of Zn in their protein, so could there be a different metal ion present in place of Zn in the other 50% of the protein, that accounts for the observed activity?

Since there is clearly a major discrepancy here, the onus is on the authors to explain the discrepancy, rather than just returning with the same data. For example, they could treat the enzyme with EDTA to remove all metals (and check the treated enzyme by ICPMS), and then add different metal ions to test activity with different metals (could even titrate with different molar equivalents of metal ions). They could then test a range of different redox-active metal ions.

(2) Given the metal content reported here, it is important to be able to compare the specific activity of the enzyme reported here with earlier preparations. The authors have now done this in the revised version.

(3) The consumption of formaldehyde to form methylene-THF is potentially interesting, but the authors say "HCHO levels decreased in the presence of THF", which could potentially be due to enzyme inhibition by THF. Is there evidence that this is a time-dependent and protein-dependent reaction? Not yet addressed.

Also in Figure 1C, HCHO reduction (%) is not very helpful, because we don't know what concentration of formaldehyde is formed under these conditions; it would be better to quote in units of concentration, rather than %. This point has been addressed by the authors in the revised version.

(4) Has this particular TMAO demethylase been reported before? It's not clear which Paracoccus strain the enzyme is from; the Experimental Section just says "Paracoccus sp.", which is not very precise. There has been published work on the Paracoccus PS1 enzyme, is that the strain used? Details about the strain are needed, and the accession for the protein sequence. Addressed in the revised version.

Reviewer #2 (Public review):

[Editors' 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:

Ito and Toyoizumi present a computational model of context-dependent action selection. They propose a "hippocampus" network that learns sequences based on which the agent chooses actions. The hippocampus network receives both stimulus and context information from an attractor network that learns new contexts based on experience. The model is consistent with a variety of experiments both from the rodent and the human literature such as splitter cells, lap cells, the dependence of sequence expression on behavioral statistics. Moreover, the authors suggest that psychiatric disorders can be interpreted in terms of over/under representation of context information.

My general assessment of the work is unchanged, and I still have some questions requesting methodological clarification

Strengths:

This ambitious work links diverse physiological and behavioral findings into a self-organizing neural network framework. All functional aspects of the network arise from plastic synaptic connections: Sequences, contexts, action selection. The model also nicely links ideas from reinforcement learning to a neuronally interpretable mechanisms, e.g. learning a value function from hippocampal activity.

Reviewer #3 (Public review):

Summary:

This paper develops a model to account for flexible and context-dependent behaviors, such as where the same input must generate different responses or representations depending on context. The approach is anchored in the hippocampal place cell literature. The model consists of a module X, which represents context, and a module H (hippocampus), which generates "sequences". X is a binary attractor RNN, and H appears to be a discrete binary network, which is called recurrent but seems to operate primarily in a feedforward mode. H has two types of units (those that are directly activated by context, and transition/sequence units). An input from X drives a winner-take-all activation of a single unit H_context unit, which can trigger a sequence in the H_transition units. When a new/unpredicted context arises, a new stable context in X is generated, which in turn can trigger a new sequence in H. The authors use this model to account for some experimental findings, and on a more speculative note, propose to capture key aspects of contextual processing associated with schizophrenia and autism.

Strengths:

Context-dependency is an important problem. And for this reason, there are many papers that address context-dependency - some of this work is cited. To the best of my knowledge, the approach of using an attractor network to represent and detect changes in context is novel and potentially valuable.

Reviewer #1 (Public review):

Studies investigating global gene expression changes induced by a single morphine administration have previously been conducted in several rodent brain regions. In this work, the authors focused on the ventral tegmental area (VTA), a key structure of the reward system that has not been extensively characterized in this context. To examine genome-wide transcriptional responses, they employed single-nucleus RNA sequencing (snRNA seq), a method well-suited for profiling gene expression in VTA cells, which are otherwise difficult to isolate.

The effects of morphine on gene expression in VTA cells were assessed in naive animals, in rats exposed to chronic inflammatory pain induced by local CFA injection into the paw, and in animals subjected to both conditions. The study revealed widespread transcriptional changes following morphine administration, whereas inflammation alone produced only limited alterations-an outcome that may reflect the sensitivity or resolution of the sequencing approach used.

Further in vitro experiments conducted in multiple astrocyte models demonstrated that the increase in Fkbp5 expression observed in the VTA is unlikely to result from opioid receptor activation. Instead, the data indicate that this effect is mediated by glucocorticoid receptor stimulation. These findings suggest that the elevated Fkbp5 expression in the rat VTA represents a secondary response rather than a direct consequence of morphine exposure. Comparable transcriptional changes, as well as similar mechanistic interpretations, have been reported in previous studies examining the nucleus accumbens (NAc), reinforcing the view that glucocorticoid-dependent regulation of Fkbp5 may be a broader feature of opioid related neuroadaptations.

The present paper showed largely similar morphine-induced gene changes in both male and female VTA samples. On the other hand, several studies indicate that males and females exhibit differences in dopaminergic activation and distinct gene expression profiles in response to opioids in the reward system. Preclinical studies have found marked sex differences in Fkbp5 expression in the dorsal striatum. This issue should be better addressed both experimentally and theoretically.

Reviewer #2 (Public review):

Summary:

This study addresses an important gap in our understanding of how pain‑related neuroadaptations interact with opioid exposure at the cellular and molecular levels, particularly in terms of cell‑type-specific responses within reward‑related brain regions. By applying single‑nucleus RNA sequencing, the authors generate a comprehensive atlas of transcriptional changes in the rat VTA associated with chronic inflammatory pain and acute morphine administration.

Strengths:

Overall, the study is important, and the experiments are carefully designed and executed. The manuscript is logically structured and well written. The sample size is appropriate: nuclei were collected from 14 male and 14 female Sprague‑Dawley rats, with 6-8 animals per experimental group. The inclusion of both sexes further strengthens the study by enhancing the generalizability of the findings.

To increase translational relevance, the authors also employ a human‑derived astrocyte culture model, which helps bridge findings from rodent tissue to human‑related cellular mechanisms.

Weaknesses:

A limitation is that the study examines only a single time point after morphine administration. However, this is balanced by the use of state‑of‑the‑art , and inherently expensive, molecular tools that allow deep transcriptional profiling.

One area requiring clarification is compliance with methodological standards. The manuscript does not specify whether ARRIVE guidelines were followed, whether a power analysis was performed to justify the number of animals used, or how randomization and blinding procedures were implemented.

Reviewer #3 (Public review):

Summary:

This work examined the transcriptional response to pain induction by CFA and/or morphine treatment in rat VTA at the level of single cells. This builds on prior work using bulk-tissue RNA-seq to evaluate response to SNI pain and/or oxycodone treatment. Here, authors find few lasting gene expression changes with CFA, but a robust transcriptional response to acute morphine, particularly in non-neuronal cells, where an increase in Fkbp5 stood out. The authors validated corticosterone-induced elevations in Fkbp5 in rat glial cell culture and human astrocyte cell culture, which are blocked by the GR antagonist mifepristone and inhibition of Nr3c1, but are not independently induced by the µOR agonist DAMGO.

Strengths:

The authors started with somewhat surprising transcriptional observations and followed the science appropriately to investigate the functional relevance of one particular finding. This work is well-powered and uses state-of-the-art snRNA-seq and CRISPR-based manipulations in both rat glia and human astrocyte cell preparations to determine the functional relevance of Fkbp5-regulated transcriptional activity.

Weaknesses:

(1) It was somewhat surprising that the CFA-Morphine group was not taken at a time point when the morphine treatment was found to be behaviorally effective.

(2) The final conclusion that Nr3c1 repression reduces the response to cort is not novel or surprising, even if it is within human astrocyte culture (which is cool).

(3) This work falls short of bringing the research full circle by applying their Nr3c1-CRISPRi approach in vivo to alter behavioral response to morphine and/or pain.

Joint Public Review:

In this manuscript, the authors proposed an approach to systematically characterise how heterogeneity in a protein signalling network affects its emergent dynamics, with particular emphasis on drug-response signalling dynamics in cancer treatments. They named this approach Meta Dynamic Network (MDN) modelling, as it aims to consider the potential dynamic responses globally, varying both initial conditions (i.e., expression levels) and biophysical parameters (i.e., protein interaction parameters). By characterising the "meta" response of the network, the authors propose that the method can provide insights not only into the possible dynamic behaviours of the system of interest but also into the likelihood and frequency of observing these dynamic behaviours in the natural system.

The authors study the Early Cell Cycle (ECC) network as a proof of concept, focusing on pathways involving PI3K, EGFR, and CDK4/6 with the aim of identifying mechanisms that may underlie resistance to CDK4/6 inhibition in cancer. The biochemical reaction model comprises 50 state variables and 94 kinetic parameters, implemented in SBML and simulated in Matlab. A central component of the study is the generation of large ensembles of model instances, including 100,000 randomly sampled parameter sets intended to represent intra-tumour heterogeneity. On the basis of these simulations, the authors conclude that heterogeneity in kinetic rate parameters plays a stronger role in driving adaptive resistance than variation in baseline protein expression levels, and that resistance emerges as a network-level property rather than from individual components alone. The revised manuscript provides additional clarification regarding aspects of the simulation and filtering procedures and frames the comparison with experimental data as qualitative. Nonetheless, the study is best interpreted as a theoretical and exploratory analysis of the model's behaviour under heterogeneous conditions. Consequently, questions remain regarding the biological grounding of the sampled parameter regimes and the extent to which the reported frequencies of resistance-associated behaviours can be directly interpreted in physiological terms.

While the authors propose a potentially useful computational framework to explore how heterogeneity shapes dynamic responses to drug perturbation, a number of important conceptual and methodological concerns remain to be addressed:

(1) The sampling of kinetic parameters constitutes the backbone of the manuscript, yet important concerns remain regarding its biological grounding and transparency. Although the revised version provides additional clarification on the exploration of "model instances", it is still not sufficiently clear how parameter values and initial conditions are generated, nor how the chosen ranges relate to biological measurements. The kinetic rates are sampled over broad intervals without explicit justification in terms of experimentally measured bounds or inferred distributions. As a consequence, it remains uncertain whether the ensemble of simulated behaviours reflects physiologically plausible cellular regimes or primarily the properties of the assumed parameter space. In this context, the large-scale sampling (100,000 parameter sets) resembles a Monte Carlo exploration of the model rather than a biologically calibrated representation of tumour heterogeneity.

Furthermore, the adequacy of the sampling strategy in such a high-dimensional space (94 free parameters) remains open to question. In the absence of biologically informed constraints, the combinatorial space of possible parameter configurations is vast, and it is unclear to what extent the sampled ensembles can be considered representative. This issue is particularly relevant because the manuscript interprets the frequency of resistance-associated behaviours as indicative of their likelihood.

The validation presented in Figure 7 does not fully resolve these concerns. The comparison with experimental data is qualitative, and the simulations are performed in arbitrary time units, which complicates direct interpretation alongside time-resolved experimental measurements. Moreover, certain qualitative discrepancies between simulated and experimental trends (e.g., persistent versus decreasing CDK4/6 activity) are not thoroughly discussed. As this figure represents the primary empirical reference point in the manuscript, the extent to which the model captures experimentally observed dynamics remains uncertain.

Finally, aspects of presentation continue to limit transparency. Parameter ranges are described at different points in the manuscript but are not consolidated clearly in the Methods, and the definition of initial conditions remains ambiguous - particularly whether these correspond to conserved quantities or to the dynamic variables used to initialise simulations. In addition, the exact number of model instances underlying specific analyses and figures is not always explicit. Greater clarity on these issues is essential for assessing reproducibility and for interpreting the quantitative claims of the study.

(2) A central conclusion of the manuscript is that heterogeneity in protein-protein interaction kinetics is a stronger driver of adaptive resistance than heterogeneity in protein expression levels. To assess the latter, the authors fix a nominal set of kinetic parameters and generate 100,000 random initial concentrations for the 50 model species. However, according to the simulation protocol described in the manuscript, each trajectory includes three phases: (i) simulation under starvation conditions to equilibrium, (ii) mitogenic stimulation to a second ("fed") equilibrium, and (iii) application of drug treatment. The equilibrium concentrations reached in phases (i) and (ii) are determined by the kinetic parameters of the model and are independent of the initial concentrations, provided the system converges to a stable steady state. In dynamical systems terms, stable equilibria are defined by the parameter set and attract all initial conditions within their basin of attraction. Since the kinetic parameters are fixed in this experiment, the pre-treatment equilibrium that serves as the starting point for drug application should likewise be fixed. Under these conditions, it is therefore not unexpected that sampling a large number of initial concentrations has limited influence on the treated dynamics.

This raises conceptual questions about the interpretation of the comparison between kinetic and expression heterogeneity. If the system converges to a unique stable steady state prior to treatment, then variability in initial concentrations does not propagate into variability in drug response, and the observed dominance of kinetic heterogeneity may partly reflect this structural property of the model rather than a biological principle. Clarification is needed regarding whether multiple steady states exist under the nominal parameter set, and if so, how basins of attraction are explored.

More broadly, it remains unclear why initial protein concentrations can be sampled independently of the kinetic parameters. In biological systems, steady-state expression levels are typically determined by the underlying kinetic rates. A more consistent approach might require constraining initial concentrations to correspond to equilibrium states of the chosen parameter set, thereby introducing relationships between at least some of the 50 initial conditions and the 94 kinetic parameters. Finally, the manuscript employs a non-standard terminology regarding "initial conditions," which may further obscure interpretation of these results and would benefit from clarification.

(3) The technical implementation of the modelling and simulation framework remains difficult to evaluate due to insufficient methodological detail. Although the authors state that kinetic parameters are randomly sampled, the manuscript does not specify the distributions from which parameters are drawn, nor whether potential correlations between parameters are considered or explicitly ignored. Without this information, it is not possible to assess how implicit modelling assumptions shape the ensemble of simulated behaviours. Given that the conclusions rely on frequency-based interpretations across sampled parameter sets, greater transparency regarding the sampling procedure is essential.

A further concern relates to the parameter filtering step. The authors report that the "vast majority" of sampled parameter sets produced systems that were "too stiff," and that these were excluded on the grounds that stiff dynamics are not biologically plausible. However, the manuscript does not clearly define how stiffness is assessed, nor why stiffness is interpreted as biologically unrealistic rather than as a numerical property of the formulation. In standard practice, stiff systems are typically handled using appropriate implicit solvers rather than being discarded. Similarly, parameter sets that produce negative state values are excluded, yet such behaviour may arise from numerical artefacts rather than from intrinsic model inconsistency. The rationale for excluding these parameter sets, rather than adapting the numerical scheme, is not sufficiently justified.

The reported rejection rate - approximately 90% of sampled parameter sets - is substantial and raises questions regarding the interplay between model structure, parameter ranges, and numerical methods. As currently described, the filtering step appears to select parameter sets based primarily on computational tractability rather than on experimentally motivated biological criteria. The manuscript would be strengthened by clarifying whether the retained parameter sets are representative of biologically meaningful regimes, and by distinguishing clearly between exclusions based on biological plausibility and those arising from numerical considerations.

Finally, important aspects of the simulation protocol require clarification. The model is simulated under "fasted" and "fed" conditions until equilibrium is reached, yet the criterion used to determine convergence is not specified. It would be important to describe how equilibrium is assessed (e.g., based on the norm of the time derivatives). Additionally, it remains unclear whether the mitogenic stimulus applied in the "fed" phase is assumed to be constant over time and, if so, how this assumption relates to biological experimental conditions. Greater detail on these implementation choices is necessary to ensure interpretability and reproducibility.

(4) The manuscript states that the modelling conclusions are strongly supported by existing literature; however, the validation presented does not fully substantiate this claim. As noted above, the comparison with CDK2 and CDK4/6 experimental data remains qualitative, and the use of arbitrary simulation time units complicates interpretation of temporal agreement. The extent to which the model quantitatively or mechanistically recapitulates experimentally observed dynamics therefore remains uncertain.

The claim that the model reproduces known resistance mechanisms is also difficult to assess in light of Figure S10, where a large fraction of network nodes (~80%) appear implicated in resistance under some conditions. If most components of the network can, in at least some parameter regimes, be associated with resistance phenotypes, the resulting lack of selectivity weakens the strength of model-based validation. It becomes challenging to distinguish specific mechanistic insights from generic consequences of network connectivity.<br /> In addition, the Supplementary Information notes that certain components of the mitogenic and cell-cycle pathways were abstracted or excluded in order to maintain computational tractability. While such abstraction is understandable in a large ODE framework, it raises interpretative questions. Proteins identified as potential resistance drivers within the model may, in some cases, represent aggregated or simplified pathway effects. Clarifying in the main text how such abstractions may influence the attribution of resistance mechanisms would strengthen the biological interpretation of the results.

Drug inhibition is central to the manuscript's conclusions. The revised version clarifies that inhibition is implemented as a fixed fractional modification of specific kinetic rate laws. This abstraction is appropriate for exploring network-level responses, but it represents a stylised perturbation rather than a pharmacologically calibrated model of drug action. For full interpretability and reproducibility, the mathematical form of the modified rate laws, as well as the timing of inhibition relative to network equilibration, should be specified unambiguously. The biological implications of the findings depend critically on understanding this modelling choice.

The one-at-a-time perturbation analysis presented in Figure 5 provides an interpretable ranking of first-order control points across the ensemble and offers mechanistic insight into primary sensitivities of the network. However, many targeted therapies act on multiple components, and resistance frequently arises through combinatorial mechanisms. The reported rankings should therefore be interpreted as identifying primary influences under isolated perturbations, rather than as a comprehensive account of multi-target drug behaviour.

Overall, the manuscript succeeds in presenting a conceptual and exploratory framework for analysing how signalling network topology can shape the qualitative landscape of adaptive responses under heterogeneous kinetic conditions. Its principal contribution lies in establishing a systematic platform for large-scale in silico exploration. At the same time, the current limitations in biological calibration, parameter grounding, and validation constrain the extent to which the conclusions can be interpreted as predictive or quantitatively representative of specific tumour contexts. Addressing these issues would further strengthen the connection between the theoretical landscape described here and experimentally observed resistance dynamics.

Reviewer #1 (Public review):

[Editors' note: The Reviewing Editor has assessed the work without involving the previous reviewers, updating the eLife Assessment accordingly. The authors did an excellent job of addressing the reviewers' comments and suggestions. The manuscript is now in line with the minor suggestions from the original reviewers, who were already enthusiastic about the first version.]

Summary:

This manuscript by Xiong and colleagues presents a compelling validation of UniDesign, a fully computational protein design framework, by using it to engineer a novel, PAM-relaxed variant of Staphylococcus aureus Cas9 (SaCas9) named KRH. The core achievement is the successful de novo generation of a high-performance nuclease (E782K/N968R/R1015H) solely through in silico modeling, without any subsequent experimental optimization or directed evolution. The authors demonstrate that KRH expands the SaCas9 PAM specificity from NNGRRT to NNNRRT, achieving genome editing and base editing efficiencies across multiple human cell types that are comparable to, and sometimes exceed, the well-known evolution-derived KKH variant. The work positions UniDesign not merely as an analytical tool, but as a powerful engine for the generative design of complex molecular functions, offering a scalable and mechanistically insightful alternative to traditional experimental screening.

Strengths:

This is an outstanding manuscript that serves as a powerful proof-of-concept for the next generation of computational protein design. The primary selling point-the raw predictive and generative power of UniDesign-is convincingly demonstrated throughout.

The manuscript shows that the tool can:

(1) successfully navigate a complex sequence landscape to identify a minimal set of three mutations (KRH) that remodel a critical protein-DNA interface;

(2) accurately model and balance the delicate interplay between specific base contacts and non-specific backbone interactions to achieve relaxed PAM specificity;

(3) deliver a final product whose performance is indistinguishable from, and in some cases superior to, a variant that required extensive wet-lab evolution.

The experimental validation is rigorous, thorough, and directly supports the computational predictions. This work will stand as a landmark study for the field, illustrating that computational design has matured to the point where it can reliably generate sophisticated tools for genome engineering.

(1) Demonstration of Generative Power:

The most significant finding is that UniDesign, without any experimental feedback, generated a variant (KRH) that matches the performance of the evolution-derived KKH. This is a remarkable achievement. The iterative design strategy-first reducing PAM bias (R1015H), then restoring binding through non-specific interactions (e.g., N968R, E782K)-is a textbook example of rational design, but it is executed entirely by the algorithm. This validates UniDesign's energy function and search algorithm as capable of capturing the subtle biophysical principles governing PAM recognition.

(2) Mechanistic Insight as a Built-in Feature:

A key advantage of UniDesign highlighted by this work is its inherent ability to provide mechanistic explanations. The computational models not only predicted which mutations would work (e.g., N968R over N968K in the KRH variant) but also why they work. The structural and energetic analyses showing the bidentate salt bridge formed by Arg968 versus the single bond formed by Lys968 (Figure 4A) is a perfect example of how the tool's output can rationalize functional differences, a level of insight that is rarely attainable from directed evolution campaigns alone.

(3) Scalability and Accessibility for Engineering:

The authors explicitly contrast UniDesign's efficiency (minutes to hours per design run) with the computational expense of methods like COMET and the experimental overhead of directed evolution. The improvements to UniDesign v1.2, specifically the mutation-count and sequence-uniqueness penalties, directly address a key challenge in computational design (generating diverse, low-energy point-mutant libraries). This positions the tool as a highly accessible and scalable platform for engineering other CRISPR systems, a point that will be of immense interest to the community.

Reviewer #2 (Public review):

Summary:

This manuscript describes the fully in silico design of a new variant of Staphylococcus aureus Cas9 (SaCas9) using an improved UniDesign workflow.

The design strategy consists of three sequential steps:

(1) Reducing positional bias at PAM position 3;<br /> (2) Restoring DNA binding through nonspecific interactions;<br /> (3) Combining individually favorable substitutions.

The overall pipeline is conceptually elegant and logically structured, and the genome-editing activity of the designed variants is comprehensively characterized. The resulting KRH variant exhibits relaxed PAM specificity, expanding the targeting range of SaCas9 across diverse cell types. Notably, the KRH variant demonstrates performance comparable to that of the evolution-derived KKH variant, underscoring the effectiveness of the proposed computational design framework.

Reviewer #3 (Public review):

Summary:

This study reports KRH, a SaCas9 variant computationally engineered via UniDesign to recognize an expanded NNNRRT PAM with substantially enhanced editing efficiency at non-canonical sites. KRH achieves genome- and base-editing efficiencies comparable to or exceeding the evolution-derived KKH variant across multiple human cell types, demonstrating that computational design can effectively remodel PAM specificity while preserving nuclease activity.

Strengths:

The research follows a clear line of reasoning, and the results appear sound. The computational design strategy presented offers a valuable alternative to directed evolution, with potential applicability beyond Cas9 engineering.

Reviewer #1 (Public review):

Summary:

The authors build a network model of the olfactory bulb and the piriform cortex and use it to run simulations and test their hypotheses. Given the the model's settings, the authors observe drift across days in the responses to the same odors of both the mitral/tufted cells, as well as of piriform cortex neurons. When representing the M/T and PCx responses within a lower dimensional space, the apparent drift is more prominent in the PCx, while the M/T responses appear in comparison more stable. The authors further note that introducing spike-time dependent plasticity (STDP) at bulb synapses involving abGCs slows down the drift in the PCx representations, and further link this to the observation that repeated exposure to the same odorant slows down drift in the piriform cortex.

The model is clearly explained and relies on several assumptions and observations: 1) random projections of MTC from the olfactory bulb to the piriform cortex, random intra-piriform connectivity and random piriform to bulb connectivity; 3) higher dimensionality of piriform cortex representations compared to M/T responses which enables superior decoding of odor identity in the piriform cortex; 2) spike time dependent plasticity (STDP) at synapses involving the abGCs.

The authors address an open topical problem and model is elegant in its simplicity. The authors addressed many of my concerns by plotting new analyses and by adding clarifying statements and discussion points, as well as testable predictions to the revised manuscript. In the revised manuscript, a few points remain unclear and I am listing them below for further potential discussion.

(1) Given the large in response (variability) across trials reported by Shani-Narkiss, Kay & Laurent - the question remains open: what fraction of the variability in response across days can be really accounted by adult born neurogenesis (the main topic of this study) vs. other mechanisms. I think the answer to this question is key for interpreting the results presented by the authors on the impact of adult neurogenesis on changes of mitral cell responses. Unfortunately, I could not find the answer in the revised version of the manuscript.

(2) Yamada indeed reported a "drastic reorganization of ensemble odor representation" in their manuscript (Figure 3D), but my understanding is that this was observed in the context of passive exposure to the same odor across several days in a row. This does not appear to contradict the findings of Kato et al., 2012 that when an odor is presented seldom, across days the mitral cell responses are stable. Also, data from Yamada et al. appears to show some degree of overall sparsening of odor responses in mitral cells at least at the level of a decrease in response amplitude between day 1 to day 7 of repeated passive exposure (Figure 3A, Yamada et al., 2017).

(3) There was mistake on my part on one of the papers referenced with respect to random vs. structured projections from the olfactory bulb to the piriform cortex. The one I was referring to is Chen et al., Cell, 2022 (not Chae et al., Neuron, 2022). The authors discussed the implications from the latter, while I was commenting in fact on the findings from Chen et al., 2022. This study identified structured projections of individual mitral cells along the A-P axis of the piriform cortex in conjunction with collaterals to specific subsets of extra-piriform target regions.

Reviewer #3 (Public review):

Summary

The authors set out to explore the potential relationship between adult neurogenesis of inhibitory granule cells in the olfactory bulb and cumulative changes over days in odor-evoked spiking activity (representational drift) in the olfactory stream. They developed a richly detailed spiking neuronal network model based on Izhikevich (2003), allowing them to capture the diversity of spiking behaviors of multiple neuron types within the olfactory system. This model recapitulates the circuit organization of both the main olfactory bulb (MOB) and the piriform cortex (PCx), including connections between the two (both feedforward and corticofugal). Adult neurogenesis was captured by shuffling the weights of the model's granule cells, preserving the distribution of synaptic weights. Shuffling of granule cell connectivity resulted in cumulative changes in stimulus-evoked spiking of the model's M/T cells. Individual M/T cell tuning changed with time, and ensemble correlations dropped sharply over the temporal interval examined (long enough that almost all granule cells in the model had shuffled their weights). Interestingly, these changes in responsiveness did not disrupt low-dimensional stability of olfactory representations: when projected into a low-dimensional subspace, population vector correlations in this subspace remained elevated across the temporal interval examined. Importantly, in the model's downstream piriform layer this was not the case. There, shuffled GC connectivity in the bulb resulted in a complete shift in piriform odor coding, including for low-dimensional projections. This is in contrast to what the model exhibited in the M/T input layer. Interestingly, these changes in PCx extended to the geometrical structure of the odor representations themselves. Finally, the authors examined the effect of experience on representational drift. Using an STDP rule, they allowed the inputs to and outputs from adult-born granule cells to change during repeated presentations of the same odor. This stabilized stimulus-evoked activity in the model's piriform layer.

Strengths

This paper suggests a link between adult neurogenesis in the olfactory bulb and representational drift in the piriform cortex. Using an elegant spiking network that faithfully recapitulates the basic physiological properties of the olfactory stream, the authors tackle a question of longstanding interest in a creative and interesting manner. As a purely theoretical study of drift, this paper presents important insights: synaptic turnover of recurrent inhibitory input can destabilize stimulus-evoked activity, but only to a degree, as representations in the bulb (the model's recurrent input layer) retain their basic geometrical form. However, this destabilized input results in profound drift in the model's second (piriform) layer, where both the tuning of individual neurons and the layer's overall functional geometry are restructured. This is a useful and important idea in the drift field and to my knowledge is novel. The bulb is not the only setting where inhibitory synapses exhibit turnover (whether through neurogenesis or synaptic dynamics), and so this exploration of the consequences of such plasticity on drift is valuable. The authors also elegantly explore a potential mechanism to stabilize representations through experience, using an STDP rule specific to the inhibitory neurons in the input layer. This has an interesting parallel with other recent theoretical work on drift in the piriform (Morales et al., 2025 PNAS), in which STDP in the piriform layer was also shown to stabilize stimulus representations there. It is fascinating to see that this same rule also stabilizes piriform representations when implemented in the bulb's granule cells.

The authors also provide a thoughtful discussion regarding differential roles of mitral and tufted cells in drift in piriform and AON and potential roles of neurogenesis in archicortex.

In general, this paper puts an important and much-needed spotlight on the role of neurogenesis and inhibitory plasticity in drift. In this light, it is a valuable and exciting contribution to the drift conversation.

Comments on revisions:

I appreciate the substantial revisions the authors have made to the manuscript. The paper is clearly improved and addresses an important and timely question: the relationship between adult neurogenesis and drift. In particular, the effort to link adult neurogenesis in the olfactory bulb to the long-term stability of odor representations downstream is valuable, and the modeling provides useful mechanistic intuition about how inhibitory circuit remodeling could influence representational drift across layers.

That said, I remain concerned that the manuscript, as currently framed, risks giving readers the incorrect impression that experimental work has established progressive, time-dependent drift in the odor tuning of olfactory bulb neurons. Experimental studies do show that ongoing experience with a set of odors can profoundly alter bulbar responses to those odors, but longitudinal measurements in which the tested odors are not repeatedly presented between sessions have instead emphasized remarkable stability of mitral/tufted tuning over days to months across multiple groups. I also think it would strengthen the manuscript to avoid anchoring the empirical comparison too heavily on a single paradigm (Yamada et al., 2017). The experimental literature spans multiple regimes, including daily odor exposure with ongoing experience and longitudinal measurements in which the tested odors are not repeatedly presented between sessions, and these regimes can yield qualitatively different degrees of reorganization. Situating the model explicitly within this broader landscape, rather than emphasizing one dataset, would make the interpretation clearer and prevent readers from overgeneralizing the Yamada findings to baseline bulbar stability. This distinction is especially important because it contrasts with what has been reported in piriform cortex, where representational drift is observed even in the absence of ongoing experience with a given odor set, and where repeated daily encounters with the same odors can slow or arrest that drift.

Reviewer #1 (Public review):

This work develops a simple, rapid, low-cost methodology for assembling combinatorially complete microbial consortia using basic laboratory equipment. The motivation behind this work is to make the study of microbial community interactions more accessible to laboratories that lack specialized equipment such as robotic liquid handlers or microfluidic devices. The method was tested on a library of Pseudomonas aeruginosa strains to demonstrate its practicality and effectiveness. It provided a means to explore the complex functional interactions within microbial communities and identify optimal consortia for specific functions, such as biomass production.

The primary strength of this manuscript lies in its accessibility and practicality. The method proposed by the authors allows any laboratory with standard equipment, such as multichannel pipettes and 96-well plates, to readily construct all possible combinations of microbial consortia from a given set of species. This greatly enhances access to full factorial designs, which were previously limited to labs with advanced technology.

Another strength of the manuscript is the measurement and analysis of the biomass of all possible combinations of 8 strains of P. aeruginosa. This analysis provides a concrete example of how the authors' new methodology can be used to identify the best-performing communities and map pairwise and higher-order functional interactions.

Notably, the authors do exceptionally well in providing a thorough description of the methodology, including detailed protocols and an R script for customizing the method to different experimental needs. This enhances the reproducibility and adaptability of the methodology, making it a valuable resource for researchers wishing to adopt this methodology.

Comments on revisions:

I thank the authors for their response. The revisions have addressed all of the issues raised in my original review, and I believe they have improved the clarity of the manuscript.

Reviewer #3 (Public review):

The author developed a useful methodology for generating all combinations of multiple reagents using standard lab equipment. This methodology has clear uses in for studying of microbial ecology as they demonstrated. The methodology will likely be useful for other types of experiments that required exhaustive testing of all possible combinations of a given set of reagents (e.g., drug-drug antagonism and synergy).

The authors provided a useful R script that generates a detailed experimental protocol for building desired combination from any number of reagents. The produced document is useful and has clear instructions. The output of the computer script will be strengthened if graphical output is also provided (similar to the one provided in Figure 1C).

The authors show that the error rate of the method doesn't go up with the number of combinations using dyes (Figure 2).

The authors demonstrate the value of their methodology for studying interactions within microbial consortia by assembling all possible combinations of eight strains of Pseudomonas aeruginosa. The value of their methodology for this application is well founded. However, it is also unclear why specific experimental choices were made for this application. It is unclear why authors continue to show the absorbance measurements of strain assemblies over the entire wavelength spectrum and not just for ABS 600 nm (figures 3 and 4). It is also unclear why the authors provided information on the "sum of the three spectra" as this reference line is meaningless and not a reasonable null model for estimating how well specific strain combinations will grow together.

Figure 5 illustrates the various analysis types that can be performed on the data collected from growing combinations of eight Pseudomonas aeruginosa strains. It is a very informative figure since it provides a "roadmap" on the various ways in which the dataset produced can be explored. The information in Figure 5 and S6 will likely be very useful for a wide audience.

Comments on revisions:

We thank the author for considering the review and providing additional clarifications. The authors disagree with some of the points we raised and decided to reject some of our recommendations. All the points of disagreement are minor and clearly subjective (e.g., stylistic). Congratulations again for this elegant manuscript.

Reviewer #1 (Public review):

The manuscript analyzes previously published MEG and ECoG datasets to examine pre-onset neural encoding effects during language processing, replicating effects that have been reported in earlier work and demonstrating that they persist even after controlling for correlations in the stimulus sequence. Replication of these effects across recording modalities and datasets is a valuable contribution, as it strengthens confidence in the robustness of anticipatory neural activity related to upcoming linguistic input. However, I have significant concerns regarding the interpretation of these findings, particularly the conclusion that the absence of temporal generalization between pre- and post-onset activity implies that pre-onset activity does not reflect predictive pre-activation of the upcoming word.

The central inferential step in this argument relies on an implicit assumption: that if the brain were predicting an upcoming word, the neural representation prior to word onset should resemble, or generalize to, the representation observed after word onset. This assumption is not theoretically necessary and is not supported by a substantial body of work on predictive processing. Many contemporary models posit that predictions are represented in abstract, compressed, or probabilistic formats that differ from sensory-evoked representations, particularly in hierarchical systems such as language (e.g., Rao & Ballard, 1999; Friston, 2005; Federmeier, 2007; Kuperberg & Jaeger, 2016; de Lange et al., 2018). Under such accounts, predictive representations may encode expectations over latent semantic features or probability distributions rather than reinstating the neural code associated with perceptual input.

In this context, the temporal generalization analyses presented here convincingly demonstrate that pre-onset and post-onset activity do not share a stable representational code. However, this result does not rule out predictive processing per se. Rather, it rules out a specific and relatively strong hypothesis: that prediction takes the form of early reinstatement of the same neural representation used during post-onset word processing. The data are equally consistent with the interpretation that pre-onset activity reflects predictive information expressed in a different representational format that is transformed upon stimulus onset.

I therefore recommend that the authors substantially soften and clarify their conclusions regarding prediction. Statements suggesting that pre-onset activity does not reflect prediction should be revised to more precisely reflect what is directly supported by the analyses, namely, the absence of representational identity or stable overlap between pre- and post-onset activity. Explicit acknowledgement of alternative interpretations grounded in established predictive processing frameworks would improve theoretical alignment and avoid overstating the implications of the temporal generalization results.

Overall, the empirical analyses are carefully executed, and the replication across datasets is a strength. However, the current framing risks over-interpreting what the data can rule out about prediction. A clearer distinction between representational equivalence and predictive processing would significantly strengthen the manuscript's theoretical contribution.