Reviewer #1 (Public review):

Summary:

Many previous studies have reported inter-item biases in visual working memory tasks. These biases can be either attractive or repulsive, depending on the particular experiments. It has been difficult to explain these biases in a unifying theoretical framework. Recently, Chetverikov (the first author of the current manuscript) proposed a demixing model for explaining these biases in Ref 22. That paper shows that both attractive and repulsive biases could emerge in the demixing framework depending on the noise properties. The current manuscript seeks to test the predictions of the demixing model experimentally in a series of new experiments and find evidence supporting the demixing model.

Because previous modeling results described in reference 22 (which is a preprint) are essential in interpreting the results reported in the current manuscript, I also studied that preprint and used the results reported in that paper to help interpret the results in this paper. My comments below will also contain discussions of that modeling paper.

Strengths:

Overall, the computational model tested in the paper is novel and interesting.

The demixing framework represents an appealing hypothesis that deserves further investigation.

The current paper provides new empirical data showing that the target stimuli with the same absolute noise level can be either repelled from or attracted to non-target items, depending on the relative noise levels. The observation that biases depend on the relative noise levels is by itself an interesting one, and is consistent with the prediction of the demixing model.

Weaknesses:

While this manuscript contains interesting new experimental observations and theoretical ideas, it has several substantial problems in its current form, which limit the conclusions that can be drawn. The description of the computational model is too brief. The key modeling assumptions need to be better motivated and explained. As the computational models generate different predictions in different regimes, it is a bit difficult to evaluate how well the experimental data support the model at a more quantitative level. Also, the results focused on studying the biases in the behavior; it is unclear whether the model can fully explain the behavior data (such as error distributions or behavioral precision).

Major concerns:

(1) Concerns/suggestions regarding the computational modeling

The current paper seeks to test the predictions of the demixing-based computational model proposed in reference 22. There are several problems with the modeling component in the current paper.

(1a) The description of the model is too brief and difficult to understand. Although the model was proposed in reference 22, it would still be beneficial to provide more details of the model so that readers can understand and appreciate the strengths/limitations of the model.

The generative model and the inference procedure could be better explained to better link the model to the behavior. In particular, how was the observer's behavioral report in each trial modeled? This requires more explanation because currently the demixing procedure estimates four parameters for a given trial, yet for a given trial, only one behavioral report was produced (e.g., current Experiment 1), or two reports were produced sequentially (e.g., current Experiment 2).

(1b) Key modeling assumptions need better justification.

One such key assumption is that on a given trial, each stimulus triggers many samples (or approximately, an entire response distribution), rather than a single sample. This assumption deviates substantially from prior work on ideal observer models. It was not clear whether this assumption is realistic. For the type of stimuli used in the current experiments, perhaps one can argue that each pixel corresponds to one sample of brain activity, thus collectively each stimulus should trigger many samples of activity in the brain. If this were to be the case, it would have two implications. First, the noise parameter in the model should be directly related to the magnitude of the stimulus noise. Thus, one should be able to plug these experimentally-controlled parameter values into the model to directly generate predictions about the biases. Second, when using stimuli with no stimulus variability (e.g., simple grating stimuli), the predicted biases should change. However, it wasn't clear whether this would hold experimentally, i.e., using gratings would lead to different biases or no biases.

If the variability of the samples for a given stimulus involves neural noise, it would be useful to justify why it is reasonable to consider that many samples were generated per stimulus.

(1c) As mentioned in (1b), the model assumes that on each trial, a large number of samples was generated. It would be useful to study and report how the prediction would change when the number of samples generated per stimulus is small. In particular, what happens when each stimulus only generates one measurement? This might be useful for interpreting previous experiment results with grating stimuli.

(1d) Reference 22 studies how the predicted biases depend on the d-prime of the identifying dimension and found that the pattern of the biases varies substantially depending on the information available for the identifying dimension. However, the current paper didn't really discuss this important point. It is also unclear what parameters the authors used for the d-prime of the identifying dimension. Was it fitted directly to the data? The Methods section has some description on the "identifiability dimension", but it was a bit obscure.

Intuitively, when the d-prime of the identifying dimension is very large, the demixing problem becomes irrelevant. In this case, there should not be any biases induced by demixing. In the case of the d-prime for the identifying dimension is 0, the problem should reduce to the simplified 1-d problem studied in reference 22. If my reading of reference 22 was correct, they reported different conclusions. It would be useful to clarify these points.

In any case, the d-prime of the identifying dimension appears to be a key parameter. It would be great to constrain this parameter using the empirical data. When the d-prime of the identifying parameter is small, the observer would easily confuse the probed stimulus with the other stimulus in a given trial. This should lead to poor task performance. Thus, it may be possible to directly estimate the value of the d-prime of the identifying dimension based on the observer's performance, and then use this parameter to generate model predictions accordingly.

(1e) The current model assumes that a large number of samples are generated per stimulus and the brain can manipulate this information to perform the demixing task. It was well documented that visual working memory has a capacity limit (i.e., it can only hold information about a few items); this discrepancy needs to be clarified or addressed.

(2) How well the computational model can explain the experimental data remains not entirely clear

The authors show that there exists a parameter regime that can qualitatively explain the experimental finding. They also show that it is possible to fit the model to the data to explain the bias patterns. However, given that the model is flexible, it would be stronger if the authors could show that the same parameters that explain the biases could also explain other aspects of the behavior, for example, the magnitude of the errors.

In other words, the model is not well constrained in the way it was tested in the paper. But it should be possible to improve it. First, if the noise parameter in the model is determined by the stimulus variability, one can determine it directly based on the external noise in the stimuli (discussed also in 1b) and see what prediction it leads to. Second, from the behavioral data, it may be possible to estimate the noise for the identifying dimension. Doing so will help better constrain the model.

It would also help if the authors could report the best-fitted parameters from the experimental data. From these parameters, one can simulate synthetic data and apply the demixing model to see if the error distribution of the simulated observers is indeed similar to the experimentally measured error distribution. That way, one can check whether the fitted parameter explains the observer's behavioral performance beyond the biases.

Other comments:

(1) How does the model account for the swap errors? I am not sure I understood the way how the swap errors were treated in the paper. To me, substantial swap errors seem to be a consequence of having low d-prime values for the identifying dimension; that is, if there is only little information to discriminate the identity of the two stimuli, swap errors would be large. However, this possibility didn't seem to be mentioned in the paper.

(2) Since the solution of the demixing problem was obtained using a numerical procedure based on EM. It would be useful to check whether the initialization has affected the biases obtained.

Reviewer #2 (Public review):

Summary:

This manuscript investigates the origins of inter-item biases in visual working memory. The authors proposed a computational model where overlapping memory signals are disentangled, inducing memory biases that depend on relative noise levels across items. The key theoretical advance is the prediction that bias direction depends not only on absolute memory noise but on the relative noise levels of target and non-target representations. Using four experiments with color mosaics whose color variability manipulates memory precision, the authors report that biases reverse as a function of relative noise in a manner predicted by the model.

Strengths:

The manuscript is clearly written and theoretically motivated. The experiments are well designed and provide converging evidence for a distinctive and non-intuitive prediction of the proposed model. I found the central result compelling: independently manipulating target and non-target noise leads to qualitatively different bias patterns, consistent with the model's prediction that relative noise is a key determinant of bias direction.

Weaknesses:

The main limitation is that the evidence establishes consistency of the data with the proposed Demixing Model, but does not demonstrate that the model provides a unique explanation of the data. Although the manuscript argues that dominant theories struggle to account for the observed reversals, no formal comparison with alternative computational frameworks is presented. In addition, model fitting results are reported only briefly, making it difficult to evaluate fit quality at the level of individual observers.

Reviewer #1 (Public review):

Summary:

This paper provides interesting observations about the effects of a classical mutation in the daf-2 insulin-like receptor in male C. elegans. The observations are a contribution in and of themselves; however, the conclusions reached about these observations are not supported by the work presented. Most importantly, male-specific effects on healthspan measures are asserted without direct comparison to hermaphrodites. Perhaps more fundamentally, essential features of the methods and experimental design are lacking, which makes formal assessment of the results impossible, especially given our knowledge of negative male-male interactions, which have gone completely unacknowledged here. Indeed, there is a general lack of context for known sex differences in C. elegans, especially in terms of the core elements of longevity, which are presented here as entirely novel but in fact are not.

Major comments:

(1) The main overall criticism of the premise of the paper is that it lacks a clear hypothesis that would lead to explicit experimental tests. Instead, many of the results are observational, and the conclusions reached go beyond the actual experiments conducted. The goal should be explicit and consistent between the introduction/ discussion, and the findings should directly address the goal.

The overall focus appears to be that daf-2 males have an extended lifespan for reasons that are different from hermaphrodites. This conclusion is apparently based on the observation of lipid reserves in mutant animals. However, none of the healthspan measures were conducted in parallel with identical measures in hermaphrodites. How can the authors then claim that males are unique? This is especially problematic since other studies have demonstrated that daf-2 hermaphrodites also have altered lipid composition (Vrablik 2015 Biochim Biophys Acta; Horikawa 2010 Mol Cell Endocrin).

(2) The authors make unwarranted claims about causation from observational data that is correlative in nature. Again, they claim that male longevity is caused by increased lipid reserves. This may in fact be the case, but there is no evidence to show that this is causal, only that lipid reserves are increased in mutant animals. Causation requires an actual experiment, in this case, disrupting lipid maintenance in daf-2 males (e.g., Lapierre 2013 Autophagy). Their conclusions are consistent with their results, but their conclusions are much too strong given the nature of the evidence, especially given the concerns about proper comparisons to hermaphrodites.

(3) With these concerns in mind, all conclusions related to male-specific effects should be statistically tested using a sex-by-treatment interaction term in the statistical model. This is obviously impossible for the healthspan data, but for lifespan, this can be directly tested using (genotype x sex interaction in the CPH analysis). Further, it is unclear why each of the replicates is shown separately in Figure 1.

It is nice that the authors do not directly pool them, as most longevity studies do, but the replicate effects can be included in a more comprehensive model, which would yield an appropriate "average" effect curve.

(4) There is an inadequate review of pre-existing literature and findings that predate the observations presented here. While this is not an issue in general, the authors present their work as entirely novel when it is not.

In addition to Gems and Riddle (2000), which is tangentially cited in the discussion, the following papers should be cited and discussed in the introduction to clarify what is currently known and what remains to be explored:

Partridge and Gems (2002) Mechanisms of aging: public or private?

McCulloch and Gems (2007) Sex‐specific Effects of the DAF‐12 Steroid Receptor on Aging in Caenorhabditis elegans

Hotzi et al (2018) Sex‐specific regulation of aging in Caenorhabditis elegans

Al-Saadi et al (2025) Disruption of the insulin signaling pathway in C. elegans dramatically increases male longevity and enhances reproductive health late in life

In addition, the authors assert that the study of sex differences is unstudied. If the authors are specifically referring to the sex differences in aging research, they should explicitly state that and revise their language to reflect that it is "understudied" rather than "unstudied". But as stated below, there are many studies that look at sex-specific differences in behavior, physiology, development, etc. This is most important in the context of sexual conflict, of which there are many studies that are directly relevant to the work presented here. The authors are encouraged to review some of these papers.

(5) This is particularly important in the context of how the experiments presented here were actually conducted. The methods are inadequate to assess this, and the results would therefore be impossible to replicate in the absence of additional details. Exactly how many individuals were raised on each plate during the longevity assays (and other work) is critical to understanding the results of this study. This is because males have direct, chemically and physically mediated negative impacts on one another (see many papers from the Brunet and Murphy labs). Further, it is not even clear whether males and hermaphrodites were reared separately from one another. Males are known to leave plates without hermaphrodites, which requires appropriate inclusion of censoring criteria in studies such as these. It is unclear whether and how this was handled. Censoring is an essential feature of any longevity study and so needs to be explicitly described in the statistical methods.

The methods describe the use of heat shock to induce the production of males, but it is unclear which generation is being used here. Ordinarily, males would be induced, and then male populations would be maintained by forced mating (picking to ensure that there is a high relative frequency of males) for several generations to eliminate any carryover effects of the heatshock itself. Were the heatshock males put directly into the longevity assays? If so, were hermaphrodites subject to identical treatment? This is confusing, and a potentially critical confound is not performed correctly.

Reviewer #2 (Public review):

Summary:

The manuscript presents interesting observations regarding the exceptional longevity and improved healthspan of male daf-2 mutants. Given the comparatively limited focus on male aging in C. elegans, the study provides a potentially useful characterization of sex-specific effects associated with reduced IIS signaling.

Strengths:

The 4-fold increase in lifespan of male daf-2 mutants is a striking and unexpected observation. The altered fat metabolism between older daf-2 mutant males and hermaphrodites provides further evidence of sex-specific effects.

Weaknesses:

(1) A major limitation of the current study is that the conclusions rely primarily on a single daf-2 allele. It would strengthen the manuscript to validate at least the major observations using an independent daf-2 allele or through daf-2 RNAi. This is particularly relevant for the proposed male-specific enhancement of longevity and healthspan, as it remains unclear whether the observed effects broadly reflect reduced IIS signaling or may be influenced by allele-specific effects or background mutations.

(2) The methods for male lifespan assays require additional detail. Although the authors state that males were generated and transferred every three days, it is not clear whether males were maintained singly or in groups, how many males were placed per plate, or how many were censored by fleeing. These details are particularly important for male aging assays, as male lifespan in C. elegans is known to be influenced by social interactions. Factors such as population density can affect survival and healthspan measurements. Clarifying these procedures would improve reproducibility and interpretation of the reported male-specific lifespan effects.

(3) Because reduced IIS signaling in daf-2 mutants is known to alter metabolism, physiology, and potentially male-derived signaling, it would be interesting to determine whether the enhanced longevity of daf-2 males is influenced by altered male-male interactions or resistance to male-associated toxicity. In this context, clarification of whether lifespan assays were performed with grouped or individually maintained males would be valuable. If not already tested, lifespan analysis under isolated single-male conditions could help distinguish intrinsic longevity effects from potential contributions of population-dependent signaling or social interactions.

(4) In Figure 2D, the body-length measurements in WT males appear somewhat unexpected, particularly the apparent increase between Day 14 and Day 20. Since adult worms are not typically expected to exhibit substantial growth at advanced ages, additional clarification regarding the measurement methodology would be helpful, including confirmation that the scale bars and image scaling were applied consistently across conditions.

(5) The use of palmitic acid barriers following Beydoun et al. (2024) is appropriate; however, it would be helpful to clarify whether WT and daf-2 males exhibited comparable fleeing behavior under these assay conditions. Because male worms are highly prone to plate leaving and censoring, genotype-dependent differences in fleeing behavior could potentially influence survival analyses and the number of censored animals. In addition, as Beydoun et al. primarily characterized these barrier conditions using hermaphrodites, it would be useful to clarify whether comparable barrier effectiveness was observed in male lifespan assays.

(6) Separately, Beydoun et al. (2024) also reported that palmitic acid barrier conditions can influence body-size measurements, whereas PEG-based barriers did not show similar effects on body size. It would therefore be useful to know whether comparable body-length trends were observed under alternative barrier conditions, particularly given the unexpected increase in WT male body length at later ages.

Reviewer #3 (Public review):

This manuscript reports a striking sex-specific effect of the daf-2(e1370) mutation on C. elegans lifespan. The authors show that male daf-2 mutants exhibit dramatically extended lifespan relative to wild-type males, wild-type hermaphrodites, and daf-2 hermaphrodites. The study also demonstrates increased lipid accumulation in these long-lived males, which is increased further over time, improved late-life motility, enhanced oxidative stress resistance, and a requirement for the downstream effector of daf-2, daf-16, for the longevity phenotype.

The interest of the work is the magnitude and consistency of the lifespan effect. The authors report large increases in both median and mean lifespan in daf-2 males across independently replicated experiments. This is further supported by healthspan analyses and their finding that male daf-2 mutants maintain improved motility and stress resistance, which argues against the interpretation that lifespan extension merely reflects prolonged frailty. The genetic epistasis experiment demonstrating loss of the longevity phenotype in daf-2;daf-16 double mutants provides evidence that the effect depends on canonical insulin/IGF-1 signalling.

The main limitation is that at least the first figure is rather an incremental increase on previous work examining the lifespan of daf-2 males, although the authors do indeed show that the effects can be much larger (or more 'plastic') than those previously published. While these findings are potentially important, the manuscript would certainly benefit from a more extensive discussion of how the results compare with prior studies of daf-2 mutants and male longevity, including possible explanations for the apparent discrepancies.

The epistasis experiment shows that this exceptional longevity requires the expression of daf-16. However, in contrast to the initial experiments (Figure 1) that show three replicates of the lifespan experiment (the standard in lifespan work in this model), it appears that the daf-2;daf-16 experiment has only been performed once.

In addition, the lifespan data for hermaphrodite daf-2 mutants appear somewhat unusual. Although the mean lifespan is increased, the median lifespan is reported to be only modestly greater than that of wild-type hermaphrodites. I know that this mutant can give lifespan curves that look like this, but either the use of another allele or of the experimental conditions and how these values compare with previously published daf-2(e1370) datasets would help readers interpret the magnitude of the male-specific effect.

The lipid phenotype is intriguing. It would be interesting to expand this to examine somatic vs embryonic fat. In addition, I noted that in the methods section, the authors use palmitic acid to stop the male worms 'fleeing' the plates; is it possible to rule out the possibility that the daf-2 mutants are simply eating and metabolising/storing this fatty acid barrier differently than their wild-type counterparts? This would be worth considering and controlling for, particularly as male C. elegans have been shown to have dramatically altered metabolic transcriptional profiles. If indeed this increased lipid is responsible for the extreme longevity of the daf-2 mutant males, it would be desirable to try to link this mechanistically to the phenotype.

Overall, the evidence convincingly supports the conclusion that male daf-2(e1370) mutants are exceptionally long-lived under the conditions tested and that this phenotype requires DAF-16. The work has the potential to make an important contribution to understanding sex-specific regulation of ageing, although further contextualisation within the existing literature would strengthen the manuscript.

Reviewer #1 (Public review):

Summary

In this paper, the authors provide a systematic investigation of structural brain differences associated with congenital aphantasia (self-reported lifelong absence of voluntary visual imagery). Specifically, the authors analysed a structural neuroimaging dataset involving 18 individuals with aphantasia and 18 visualizers to test two competing hypotheses: (1) that aphantasia reflects alterations in visual pathways and early visual cortex, and (2) that it instead reflects differences in higher-order frontotemporal and cingulate systems. To test these hypotheses, the authors employed multiple analysis approaches (e.g., cortical morphometry, tractometry, graph-theoretic network analysis).

They report structural differences between the two groups in frontotemporal and cingulate systems. In contrast, they found no reliable group differences in early visual cortex or major visual tracts. On this basis, they propose that aphantasia is primarily associated with differences in higher-order systems supporting integration and conscious access to internally generated representations, rather than with deficits in sensory visual representations themselves.

Strengths

(1) The present work addresses an important gap in the mental imagery literature, providing a systematic investigation of structural neuroimaging differences in congenital aphantasia. By showing that structural differences between aphantasics and visualizers are mainly concentrated in frontotemporal and cingulate systems (rather than in visual cortex), it makes an important step toward a better understanding of individual differences in mental imagery and provides a set of candidate regions for future mechanistic work.

(2) A key strength of the study is the multimodal approach employed to address the main research question, integrating tractometry, functional region-of-interest (fROI)-based tractography, graph-theoretic network analysis, and surface-based cortical morphometry, which provide a converging assessment of structural differences between aphantasics and visualizers.

(3) The complementary use of Bayesian analyses alongside NHST to assess evidence for null results is a further strength of this work.

Weaknesses:

(1) A weakness of this work is related to aspects of the framing and, in particular, what can be confidently inferred from the results. The framing of existing accounts of aphantasia in the Introduction appears limited in that it reduces the views on aphantasia to two options (sensory strength account versus conscious access account) without acknowledging a third distinct position, namely that aphantasia reflects a specific deficit in the voluntary generation of imagery (Milton et al., 2021; Zeman et al., 2015, 2020; Whiteley, 2021; Cavedon-Taylor, 2022). Like the conscious access account, the view that aphantasia involves a deficit in the generation of sensory representation also speaks against the hypothesis of reduced sensory strength of internally generated representations. This third view could be acknowledged/discussed as it also maps quite well onto the presented results.

(2) Relatedly, I think the main weakness of the paper concerns the interpretation of results being restricted to a lack of "conscious access". The paper frames its findings as mainly evidence for a conscious access failure, the view that visual representations are generated by aphantasics but cannot be consciously accessed. However, the structural findings are equally consistent with a voluntary generation failure, especially since the same higher-order regions examined can also be implicated in the top-down generation and control of imagery. The authors themselves initially define aphantasia as "lifelong absence of voluntary visual imagery". Given the nature of structural imaging data (as opposed to functional data), it is not possible with the present study to distinguish between a lack of generation versus a lack of conscious access. As such, examining this alternative interpretation appears appropriate, and it would considerably strengthen the paper. Structural MRI alone is not sufficient to dissociate imagery generation from conscious access, as these are fundamentally functional questions.

(3) Some inconsistency and lack of clarity around the specific choice of regions/networks, which could be better motivated and explained. E.g., the "core imagery network" analysed in the white-matter connections analysis was derived from a previous 7T study (with which the sample partially overlaps) and is not necessarily the network most commonly associated with visual imagery in the literature (e.g., see Dijkstra et al., 2019; Pearson, 2019). It is, for instance, unclear why V1 was examined in the cortical thickness analysis but not in the previous one, given that both analyses are related to the visual pathway hypothesis. Related to this, in the graph-theoretic analysis, the rationale for network selection is inconsistently established in the Introduction. The attention and salience networks do have some grounding in the Introduction through the mention of specific regions such as FEF and anterior insula, though these are discussed as individual regions rather than as networks. However, the default mode network receives no motivation in the Introduction. More explicit elaboration on these choices would be appropriate.

(3) The interpretation provided in the Discussion tends to oversimplify what is in fact a heterogeneous and rich set of structural findings into a relatively coherent mechanistic account. The observed differences are spatially and directionally variable across tracts, cortical regions, and metrics: e.g., FA is reduced in the UF and posterior interparietal corpus callosum but increased in the dorsal cingulum; cortical thickness is reduced in aPFC but increased in medial temporal regions, and so forth. The Discussion acknowledges this in part (e.g., proposing increased dorsal cingulum FA as potentially compensatory) but does not address the directional heterogeneity systematically. The authors could discuss more explicitly what the opposing directions of effects mean for their overall interpretation. Relatedly, some parts of the Discussion link specific structural findings to specific imagery processes in ways that go beyond what the current data can support. The authors could more clearly distinguish between what the structural data show and what functional interpretations are taken from prior work.

Reviewer #2 (Public review):

Summary:

This paper addresses whether congenital aphantasia reflects an alteration of visual representations themselves, or rather of the systems that allow internally generated representations to reach conscious experience.

Strengths:

The study is novel and ambitious. The authors combine several complementary structural MRI approaches in a rare and well-characterised population, and the convergence of the findings toward frontotemporal and cingulate systems, with relative sparing of early visual cortex and major visual pathways, is particularly interesting because it could affect the way visual imagery is modelled and tested experimentally and clinically.

Weaknesses:

Overall, I found the manuscript conceptually and methodologically strong. My main concern regards the interpretation of the anatomical findings, rather than the findings per se. The authors discuss their results within a rich cognitive framework. However, the current dataset does not appear to include independent behavioural or neuropsychological measures that would allow the proposed cognitive interpretation to be tested in the same participants. As a result, the manuscript sometimes moves quite rapidly from 'these structural differences involve systems associated with higher-order control, salience, conscious access' to 'these structural differences may explain the cognitive mechanisms of aphantasia'. I agree that this is the most interesting interpretation, and probably the right one to explore. Although plausible, it remains indirect. The authors already acknowledge this point when discussing memory, affective control, and semantic processing. However, the same logic should be extended to the interpretation of the full set of findings. For example, if the salience/anterior insula findings are interpreted in relation to access to internally generated representations, it would be useful to know whether aphantasic participants also differ behaviourally on tasks tapping interoception or related aspects of internal monitoring. I appreciate that collecting additional behavioural data may not be feasible at this stage, especially given the difficulty of recruiting participants with such a specific manifestation. However, I think it should be acknowledged more explicitly in a dedicated limitation paragraph.

Reviewer #3 (Public review):

Summary:

The authors investigate the structural brain basis of congenital aphantasia, a condition characterised by a lifelong absence of voluntary mental imagery. They test two competing accounts: one predicting structural differences in early visual pathways, the other predicting differences in higher-order frontotemporal and cingulate systems. To do this, they combine four complementary structural imaging approaches: white-matter microstructure profiling along anatomically defined tracts, tractography seeded from functional regions of interest, whole-brain structural network analysis, and cortical thickness mapping. The main finding is that white-matter differences are selective for frontotemporal and cingulate pathways and absent in early visual pathways, which the authors interpret as support for the higher-order account.

Strengths:

The multi-modal design is a genuine strength: running four independent analyses increases the chance of detecting real effects and of identifying false positives that appear in only one stream. The statistical choices within each analysis are appropriate. Permutation-based correction with a threshold-free method is well-suited to the tract-level comparisons. The use of Bayes factors to quantify evidence for null results, rather than simply reporting non-significant tests, is particularly valuable here, since the absence of visual pathway differences is central to the argument. The robustness checks across multiple brain parcellations for the network analysis strengthen confidence in those findings.

Weaknesses:

The main limitation concerns the relationship between two of the analysis streams. The measure used to weight structural connections in the network analysis is calibrated to match fiber density estimates derived from the same diffusion signal that drives the white-matter microstructure differences. If the two groups differ in tissue organisation in certain pathways (which the microstructure analysis suggests they do), that difference will feed into both measures. The authors should acknowledge this dependency when discussing convergence across analyses.

More broadly, the imaging metrics used throughout (measures of fiber organisation and weighted connection counts) reflect what the diffusion model captures from the tissue and cannot be directly read as measures of axon number or connection strength. This is a known limitation of the field, but it is relevant to the strength of structural claims made in this paper.

The network analysis is presented without comparison to a null network. Without this, it is hard to know whether the node-level differences reflect specific network topology or simply follow from overall differences in connectivity weight or density between groups.

The study runs four separate discovery analyses on the same 36 participants, each corrected within itself but with no control across analysis streams. At 18 participants per group, this is exploratory work. Some of the language used in the abstract and discussion, like "first comprehensive characterization" and "selective structural phenotype", reads as more definitive than the data support at this sample size. Framing the results as hypotheses to be replicated would make the paper stronger.

The paper frames the results as distinguishing between two competing accounts. The positive evidence for the higher-order account is clear. The absence of differences in visual pathways is a different kind of result: it means such differences were not detected in this sample, not that visual pathways are uninvolved. The discussion at times moves toward that stronger conclusion, which the data do not support.

The cortical thickness analysis finds one cluster in the predicted direction, while the other analyses each return multiple effects. One cluster in a whole-brain search with 18 participants per group is not strong evidence and should not be presented as equivalent to the other results.

Effect sizes are reported without confidence intervals throughout. With 18 participants per group, the uncertainty around those estimates is large, and confidence intervals would give readers a more accurate sense of what can be concluded.

Reviewer #1 (Public review):

In their manuscript Arjun et al. investigate the role of the histone acetyl transferase Gcn5 in controlling drosophila blood cell homeostasis in the larval lymph gland. Using gcn5 zygotic mutants as well as targeted knock-down and over-expression of Gcn5 in various lymph gland cell populations, they show that these manipulations impact (but in a rather haphazard manner) niche cell number, blood cell progenitor maintenance, plasmatocyte differentiation, crystal cell differentiation, DNA damage accumulation. Their results suggest that Gcn5 controls autophagy and show that reducing the expression of the autophagy machinery affect blood cell differentiation. By using drugs as well as genetic approaches to modulate the mTOR pathway, they conclude that Gcn5 levels are regulated by mTOR, but that the impact of this pathway on blood cell homeostasis can override Gcn5 function.

Overall, the main conclusions are sound but interpreting several lines of experiments and results remain complicated. Consequently, the overall picture of the role of Gcn5 in Drosophila larval lymph gland development, and its relationship to mTOR and autophagy, remains unclear.

Reviewer #2 (Public review):

Summary:

Drosophila haematopoiesis has been shown to be governed by a number of signalling pathways such as JAK/STAT and Dpp. This important study shows a role for nutrient sensing and autophagy in determining blood cell differentiation. The authors show that General control non-derepressible 5 (Gcn5), a histone acetyltransferase affects blood cell differentiation. Gcn5 also negatively regulates autophagy through its effector TFEB which directly regulates autophagy genes. The authors also show that mTORC1 modulates Gcn5 levels and through it TFEB activity thus acting as a fine-tuning mechanism which maintains optimal levels of autophagy.

Strengths:

The main strength of the work lies in the interesting finding that cellular metabolic processes such as autophagy has a direct role in blood cell differentiation and has the potential to be of interest to those working on vertebrate haematopoiesis as well. The report has generated intriguing data, using promoters specific for sub sections of the lymph gland, that different cellular subsets of the lymph gland contribute differently towards haematopoiesis, but this is not followed up in detail and the final conclusions are derived from a combination of whole lymph gland perturbations as well as those from specific promoters.

Weakness:

(1) Gc5 seems to be expressed throughout the lymph gland but modulating it in the subsections do not have the same result. It is very striking that the knockdown of Gcn5 in the prohemocyte population does not have an effect on differentiation whereas overexpression does. And the modulations of Gcn5 in PSC also has variable effects across hemocyte subpopulations which is not explored in the manuscript. Interestingly, also the domain deletion constructs show differential effect on blood cell differentiation when altered solely in the prohemocytes which is not explained. While Gcn5 can be seen in all sections of the lymph gland in the first figure, under the HHLT-Gal4 and Hml-Gal4, Gcn5 looks cytoplasmic and almost completely excluded from the nucleus strikingly unlike Gcn5 expression under the Collier-Gal4 and Dome-Gal4. The rest of the experiments in the manuscript are done with multiple promoters, with autophagy flux measured by modulating Gcn5 with a pan hemocyte promoter, but the mTORC1-Gcn5 axis is explored using chemical modulators which affect the whole of the lymph gland (Fig7) or using two pro-hemocyte promoters (Fig8).

(2) The knockdown of Gcn5 seems to affect the gland size (A compared to B and C). Since mTORC1 is a central regulator of cell size, it is possible that some of the effects seen in these knockdowns are potentially through mTORC1 affecting size suggesting that the signalling axis between mTORC1 and Gcn5 might not be a one-way axis as suggested in Figure 9. Also, this would mean that in experiments where absolute cell counts of crystal cells or niche cells are used to assess blood cell differentiation, further analysis to consider total cell numbers in the lymph gland would strengthen the manuscript.

(3) A genetic manipulation of mTORC1 specifically in the pro hemocytes would strengthen the role of mTORC1 in the pathway rather than the chemical modulation which affects the whole of the lymph gland.

Comments on the revised manuscript:

Overall, the revisions make the narrative more coherent. The authors have also added data which substantiates their conclusions.

However, in some instances, the authors are not clearly able to explain the discrepancies in the data (Gen-5 depletions under the Hml-Gal4 in the whole larval lysates remove p62 completely) which is not ideal.

A query regarding the discrepancies in the immunofluorescence data: The authors have removed the IF data which suggested that there could be differences in the shuttling of Gcn5 between the nucleus and cytoplasm. The authors suggest that immunofluorescence issues are at the root of these variable results, but the reviewer wonders whether there could be further unexplored mechanisms re: shuttling that is unexplored here and would have been potentially novel.

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 weaknesses raised in the previous round of 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).

Reviewer #2 (Public review):

Summary:

Zylberberg et al. reanalyze eye-tracking and behavioral data 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):

McGaughey and Gold ask where in the decision process the flexibility of evidence accumulation arises, proposing that it is not solely a property of downstream integrators but is also supported by stimulus-specific sensory adaptation in the middle temporal area (MT). Recording single-unit activity in rhesus macaques during a motion direction-discrimination task in which an adapting stimulus of varying temporal stability precedes an identical test stimulus, they find that more rapidly changing contexts produce weaker and less discriminable MT responses to the test stimulus, which they argue accounts in part for context-dependent changes in decision-making behavior. Through session-level correlations they further identify pupil-linked arousal as a parallel, apparently separable contributor.

The main strength is the shift of perspective toward the encoding stage: rather than treating MT as a static input to flexible downstream integrators, the authors show that early sensory cortex can itself contribute adaptive, context-dependent signals that shape behavior. The conceptual advance is supported by a well-designed paradigm-total exposure to each motion direction is matched across conditions and the test stimulus is held identical-together with single-unit recordings and simultaneous pupillometry. The behavioral effect is consistent across three animals, and the fact that context-dependent differences emerge over repeated stimulus presentations within a trial, rather than as a sustained baseline offset across blocks, ties the effect convincingly to stimulus-specific adaptation.

The behavioral effect constrains the temporal dynamics of decision formation but does not uniquely identify its algorithmic basis: a leak, a saturating non-linearity, or a reduction in the gain of integration are all compatible with a shallower rise of accuracy with viewing time, and the reduced MT discriminability is itself an encoding-stage efficiency effect of this kind. The manuscript appropriately treats the algorithmic basis as unresolved, noting that distinguishing these accounts would require analyses not available here, such as reverse-correlation or motion-energy kernels with lower-coherence test stimuli.

The inference that the adaptation- and arousal-related signals operate independently rests on the absence of session-wise correlations between the neural and pupil measures and their behavioral contributions. Given the noise in the trial-wise estimates, this is best read as consistent with, rather than demonstrating, true independence, as the authors note.

Overall, the authors largely achieve their aim of showing that sensory adaptation in MT shapes the evidence available for time-dependent perceptual decisions. The evidence for a sensory-encoding contribution is convincing, while the claim of independence between adaptation and arousal is more tentative and is framed as such.

Reviewer #2 (Public review):

McGaughey and Gold trained rhesus macaque monkeys to perform a motion-direction discrimination task in which a behaviorally irrelevant adapting stimulus with either fast or slow direction alternations preceded a variable-duration test stimulus, while simultaneously recording single-unit activity in area MT and pupil diameter. They report that adaptation to the more rapidly changing stimulus was associated with reduced behavioral sensitivity, attenuated test-evoked MT responses, and larger pupil-linked arousal signals. The authors interpret these behavioral changes as evidence for context-dependent adjustments to the temporal dynamics of decision formation and argue that these adjustments are supported by both sensory adaptation in MT and arousal-related mechanisms. More broadly, they conclude that flexible evidence accumulation in dynamic environments arises from distributed adjustments across sensory encoding and neuromodulatory systems rather than solely from changes within a downstream accumulator. If correct, this interpretation has important implications not only for our understanding of perceptual decision making, but also for broader theories concerning the functional role of sensory adaptation.

The conclusions of the paper are generally supported by the data. Evidence for adaptation-induced changes in sensory encoding, behavior, and pupil dynamics is convincing, and the revised manuscript substantially strengthens the connection between the behavioral findings and the proposed decision-making framework.

Comments on revised version.

The revised manuscript provides a clearer account of how recent stimulus history influences behavioral performance. In the original version, aspects of the psychometric functions were interpreted as evidence for a more leaky evidence-accumulation process, although some of these effects could potentially have reflected alternative mechanisms, including influences of the adapting stimulus on short-duration trials. The additional analyses and discussion included in the revision clarify that information from the adapting stimulus contributes to behavior at short viewing durations and appropriately temper claims regarding the specific computational mechanism underlying the observed behavioral effects. While the data do not uniquely identify whether these effects arise from changes in leak, other nonlinearities, or related decision processes, they provide convincing evidence that recent temporal context influences the temporal dynamics of decision formation.

My original review also noted that different sections of the manuscript relied on different behavioral metrics and analytical approaches when relating behavioral changes to neural and pupil-linked measures. The revised manuscript now provides a clearer rationale for these choices, including distinctions arising from the different trial types and time windows used in the neural and pupil analyses.

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:

Kashiwagi et al. undertook a population analysis of dendritic spine nanostructure applied to the objective grouping of 8 mouse models of neuropsychiatric disorders. They report that spine morphology in cultured hippocampal neurons shows a higher similarity among schizophrenia mouse models (compared with autism spectrum disorder (ASD) mouse models) and identify an effect of Ecrg4 (encoding small secretory peptides) on spine dynamics and shape in these models.

Strengths:

The study developed a method for objectively comparing spine properties in primary hippocampal neuron cultures from 8 mouse models of psychiatric disorders at the population level using high-resolution structured illumination microscopy (SIM) imaging. This novel technique identified two distinct groups of mouse models according to the population-level spine properties: those with ASD-related gene mutations and those with schizophrenia-related gene mutations. Functional studies, including gene knockdown and overexpression experiments, identified an effect of Ecrg4 on the spine phenotype of the schizophrenia model mice.

Weaknesses:

The main weakness is that the study is wholly in vitro, using cultured hippocampal neurons. The authors present this as an advantage, however, arguing that spine morphology as measured in a reduced culture system can demonstrate direct effects of gene mutations on neuronal phenotypes in the absence of indirect influences from nonneuronal cells or specific environments.

Reviewer #2 (Public review):

Okabe and colleagues build on a super-resolution-based technique they have previously developed in cultured hippocampal neurons, improving the pipeline and using it to analyze spine nanostructure differences across 8 different mouse lines with mutations in autism or schizophrenia (Sz) risk genes/pathways. It is a worthy goal to try to use multiple models to examine potential convergent (or not) phenotypes, and the authors have made a good selection of models. They identify some key differences between the autism versus the Sz risk gene models, primarily that dendritic spines are smaller in Sz models and (mostly) larger in autism risk gene models. They then focus on three models (2 Sz - 22q11.2 deletion, Setd1a; 1 ASD - Nlgn3) for timelapse imaging of spine dynamics, and together with computational modelling provide a mechanistic rationale for the smaller spines in Sz risk models. Bulk RNA sequencing of all 8 model cultures identifies several differentially expressed genes which they go on to test in cultures, finding that ecgr4 is upregulated in several Sz models and its misexpression recapitulates spine dynamics changes seen in the Sz mutants, while knockdown rescues spine dynamics changes in the Sz mutants. Overall, these have the potential to be very interesting findings and useful for the field.

Reviewer #1 (Public review):

Summary:

This important study examines how antibiotic-resistant bacterial cells can protect neighboring sensitive cells in mixed populations that occupy both surface-associated and freely growing states. Using experiments in Enterococcus faecalis together with a mathematical model, the authors test the hypothesis that protection would be stronger in biofilm-associated populations, but instead find that resistance-mediated protection extends broadly across both population types. The work provides evidence that antibiotic efficacy depends strongly on community composition, population density, and density-dependent detoxification dynamics.

Strengths:

A major strength of the study is the close integration of experimental measurements with a relatively simple quantitative model that captures many of the observed population dynamics. In particular, the work highlights how interactions between antibiotic detoxification, cellular growth, and saturation at carrying capacity can generate nonintuitive behavior, including the reported population inversion effect. The agreement between the well-mixed model and the experimental observations is convincing, and the spatial analyses suggest that cells within the biofilm are sufficiently intermixed that large-scale spatial segregation is unlikely to dominate the observed behavior.

Weaknesses:

The mechanistic interpretation could, however, be clarified further by more explicitly emphasizing the competing timescales associated with detoxification, growth, and resource limitation. The current results suggest that when resistant cells are initially abundant, detoxification occurs rapidly relative to growth, allowing the population to approach carrying capacity after relatively few doublings, whereas slower detoxification at lower resistant fractions may permit greater expansion of sensitive cells once antibiotic concentrations decline. Additional direct measurements of antibiotic concentrations over time would also strengthen the connection between the experimental system and the modeling framework by testing whether the detoxification dynamics assumed in the model are quantitatively appropriate, although this seems very plausible.

The study also raises interesting questions regarding the role of spatial structure and exchange between planktonic and biofilm-associated populations. It would be informative to explore whether biofilm-specific protection becomes more pronounced at lower antibiotic concentrations, where local detoxification may compete more directly with antibiotic penetration into the biofilm, and in this context, the dynamics of exchange between biofilm and planktonic populations would be interesting to understand. Overall, the evidence supporting the central conclusions is convincing, and the study will likely be of broad interest to researchers studying microbial communities, antibiotic resistance, and collective population dynamics.

Reviewer #2 (Public review):

Summary:

In this manuscript, Martins et al. examined the cooperative response of E. faecalis cells to beta-lactams, in both planktonic culture and in biofilm. They found that the competition outcome between the susceptible and resistant strains is frequency dependent; they have also quantified how the competition curves change with inoculation OD and antibiotic concentration. To the authors' surprise, the competition dynamics are not that different in biofilm and in planktonic culture, which the author attributed to the unstructured nature of the thus-grown E. faecalis biofilms, quantified through correlation analysis. Using a well-mixed model capturing growth, death, and drug degradation by the resistant cells, the authors were able to quantitatively capture the experimental observation.

Strengths:

Overall, the data presented are solid. Although there is not much surprise after the understanding that the E. faecalis biofilm is unstructured, the manuscript still provides a useful "null case", so to speak, for researchers in the field when considering antibiotics in the context of biofilm. The theoretical model presented and the procedure of fitting the experimental data are useful to the research community.

Weaknesses:

One clarification the author should make is on the biofilm growth process. Specifically, could staining experiments be performed to demonstrate the secretion of the extracellular matrix? Just by looking at Figure 1b, it is hard to say. It remains a question whether the biofilm culture simply contains unstructured clusters rather than real biofilms (that are usually structured).

Reviewer #3 (Public review):

Summary:

The authors studied social aspects of antibiotic resistance by co-cultivating antibiotic-resistant and sensitive Enterococcus faecalis (an important pathogen) as biofilms to assess the extent to which sensitive cells can take advantage of the protection provided by resistant cells against both a beta-lactam antibiotic and in the presence of a B-lacatamase inhibitor. By quantifying the proportion of each cell type using fluorescence microscopy, they conclude that protection is provided equally in the biofilm and planktonically, and that the biofilm is completely unstructured with regard to the locations of the two cell types. A mathematical model is then used to show that no spatial information is needed to recapitulate the results and that the protective effect can be described completely by the growth rates of the two cell types and the affinity of the β-lactamase to the antibiotic and inhibitor. The strength of evidence is difficult to assess due to unclear descriptions of some methods, and the significance of the findings is limited by the experimental setup, where antibiotics were added very close to the time of inoculation.

Strengths:

The co-cultivation of antibiotic-resistant and sensitive bacteria allows for exploration of the social aspects of antibiotic resistance. Fluorescently-tagged strains allow for unambiguous tracking of the two cell types. The simultaneous analysis of biofilm and planktonic cells enables insight into whether these different growth modalities are influenced by social aspects of antibiotic resistance. In analyzing the structure of the biofilm, the use of a null model with randomized cell positions allows for an accurate determination of whether the observed data are due to some effect; however, as noted below, there is a caveat to this analysis. The broad observation that biofilm and planktonic populations are linked is generally supported by the data; however, this result is closely tied to the experimental setup used. The development of a mathematical model that can recapitulate results from a second set of data with values obtained from fitting a different set of data shows robustness of the model for using it to explain the results.

Weaknesses:

The observed results are tied very closely to the experimental setup of adding antibiotics very close to the time of inoculation, but this connection is not discussed. The described 'population inversion' effect is better described as frequency-dependent selection for resistant cells, but frequency-dependent selection is not discussed. Confocal microscopy was used to quantify the relative proportion of antibiotic-resistant and sensitive cells in the biofilm; however, it is unclear if the entirety of the Z stacks was used to determine these proportions. This is also the case for the analysis of whether the sensitive/resistant cells are non-randomly distributed in the biofilm: it is unclear whether the vertical distance between cells was taken into account. The authors claim that biofilm and planktonic bacteria are protected equally by the presence of resistant bacteria; however, Figure 1a and b seem to clearly show that the proportion of sensitive cells is higher in the planktonic cells compared to biofilm cells when started from an equal frequency inoculum, meaning this is not always the case. The mathematical model is used to confirm the result that no spatial components are needed to describe the results; however, this is mostly linked to the initial setup of the experiment, where antibiotics are added at the time of inoculation, and no biofilm could form before the outcome of the antibiotic-cell interactions was concluded.

Reviewer #1 (Public review):

Summary:

Lituma and colleagues investigate the role of NMD in astrocytes, an underexplored question given that prior work on NMD in the brain has focused exclusively on neurons. Using a tamoxifen-inducible, astrocyte-specific Upf2 conditional knockout (cKO) mouse, they report that loss of astrocytic NMD causes: (1) reductions in astrocyte cell volume and surface area across hippocampus, visual cortex, and prefrontal cortex; (2) decreased excitatory synapse density, reduced dendritic spine density, and impaired synaptic engulfment; (3) deficits in basal synaptic transmission and LTP, with selective impairment of mGluR-LTD; (4) elevated spontaneous calcium transients in astrocytes; and (5) anxiety-like behavior in the elevated plus maze (EPM) and contextual fear conditioning paradigms. Transcriptomic analysis of FACS-isolated astrocytes identifies 277 differentially expressed genes, ~40% of which carry canonical NMD-inducing features, implicating pathways linked to calcium signaling, phagosome formation, and glial development. A rescue experiment using the CalEx calcium extrusion pump demonstrates partial restoration of synaptic strength and anxiety behavior when astrocytic calcium is normalized.

The study addresses an important gap in our understanding of RNA regulation in glial cells, and the overall conceptual framework is well described. The experimental design is generally appropriate, and the multi-pronged approach lends the main claims a degree of validity.

Strengths:

(1) Novelty: This is the first study to systematically examine NMD function in astrocytes in vivo. The identification of astrocytic NMD targets via RNA-seq combined with an NMD-inducing feature classifier is a meaningful methodological contribution.

(2) Multi-method approach: The authors combine morphological analysis (Imaris 3D reconstruction), synaptic markers (PSD-95, LAMP2 engulfment assay), spine density measurements, acute slice electrophysiology, two-photon calcium imaging, behavioral testing, and transcriptomics. The convergence across these methods strengthens confidence in the claims.

Weaknesses:

(1) While the transcriptomic analysis is a valuable addition, the connection between specific NMD targets and the observed calcium phenotype remains largely correlational. The authors identify Gabbr2 and Adora1 as upregulated candidates with canonical NMD features and speculate that their elevated expression drives aberrant calcium signaling. However, no validation (e.g., qRT-PCR or protein-level confirmation) of these candidates is presented. The mechanistic pathway between NMD disruption and elevated calcium is thus inferred from pathway analysis rather than demonstrated. This is a significant gap between the transcriptomic and physiological arms of the study, and the authors should be more explicit about this limitation or, ideally, provide at least one validated target.

(2) The reduction in astrocyte surface area in cKO mice is interpreted as contributing to reduced synapse contact and engulfment capacity. This is a reasonable hypothesis, but the study does not directly demonstrate that reduced astrocyte territory correlates with reduced synaptic coverage at the level of individual cells or brain regions. The temporal sequence of these events is unknown. Do morphological deficits precede synaptic changes? Clarification and qualification of this causal chain in the Discussion would strengthen the manuscript.

(3) LFS-induced LTD is unaffected, while mGluR-LTD is reduced. This is intriguing and potentially informative about astrocyte contributions to distinct LTD mechanisms, but the difference receives limited discussion. Given the relevance of mGluR signaling to calcium dynamics and the identified pathway enrichments (GPCR signaling), this specificity deserves more attention.

(4) The CTRL + CalEx condition is included in the EPM experiment but not in the electrophysiology or calcium imaging experiments, making it difficult to fully assess whether CalEx itself has off-target effects on synaptic transmission or anxiety in wild-type animals. The CTRL + CalEx EPM data (Figure 7F) appears to show a modest reduction in open arm time relative to CTRL, which, if robust, would suggest that excessive calcium reduction in astrocytes is also anxiogenic. This finding would be physiologically relevant and deserves comment.

Reviewer #2 (Public review):

Astrocytes are highly responsive to their environment and play a range of critical roles in brain function. Lituma et al. theorize that one mediator of that responsiveness is the regulation of RNA stability. They therefore undertake an assessment of astrocytes missing Upf2, a protein required for mRNA degradation via nonsense-mediated decay. This is an interesting study, approaching astrocyte biology from a novel angle. The authors take on an ambitious set of experiments, spanning morphological assessment, synaptic engulfment, electrophysiology, behavior, and calcium imaging.

The authors show convincing data that knocking out Upf2 in astrocytes impairs synaptic plasticity, affects behavior, and changes the complement of astrocytic mRNA. These results, in and of themselves, are intriguing and suggest that NMD is an important biological process in astrocytes, warranting further study.

My primary concern is whether the authors may be largely studying dying cells. The idea that NMD disruption has a dramatic effect on astrocyte morphology is an intriguing idea, but it is not fully established here. The nuclei in the example cKO morphology images appear small and/or fragmented. This raises concerns that the authors did not ensure that they had the full 3D morphology of the astrocyte in the section, and the cell is in part cut off, which would compromise any data on the morphology. The authors state that the tissue was sectioned at 70 um. The diameter of an astrocyte in the adult mouse brain is typically between 50 and 70 um. Unless astrocytes are perfectly positioned in the center of the slice, at this thickness, the majority of astrocytes will almost certainly be partially cut off. More detail on how cells were chosen and what quality control metrics were implemented would alleviate concerns here. An alternative possible explanation for these small/fragmented nuclei is that cKO astrocytes may be unhealthy to the point that they are actively dying. Using the transgenic ZsGreen label, the authors state that they observe a size change (Figure S4); this is not readily apparent and is not quantified in any way. It does appear from these images that there may be a loss of some astrocytes; cell death, which would also be an interesting finding, is a fundamentally different process than morphologic restructuring in living cells. The authors do attempt to count astrocytes (Figure S6B), but do so with GFAP. This is a fundamentally flawed approach. Because GFAP is not readily detectable in most healthy astrocytes in most gray matter regions, GFAP should not be used to quantify astrocyte numbers; this experiment should be repeated with a better marker, such as Aldh1l1, Sox9, etc.

Synaptic engulfment: This is an extraordinarily high degree of engulfment in the control animals compared to many published studies, leading to concern as to the technical approach. Indeed, the overall low level of PSD-95 signal in control conditions in adult mice is concerning as to the technical accuracy of the approach. It is unclear exactly how the investigators labeled the astrocytes; presumably via the ZsGreen label, but it is never stated, and the only images shown are the highly processed Imaris renderings. The small astrocytic processes, or leaflets, that make up the vast majority of the astrocytic arbor are on the order of 100nm in diameter. The processes shown in Figure 2B are, according to the scale bar, at least 20x that size. It is difficult to have much faith in these results as currently presented.

The signal-to-noise ratio of the GCaMP experiments is worryingly low, likely responsible for the abnormally low dF/F in all conditions and the lack of significant change between control and CalEx, when control astrocytes should show a much higher GCaMP signal than any CalEx-expressing astrocyte. That said, the higher Ca++ in Upf2 KO astrocytes is intriguing. Given the roles of elevated calcium in cell death, this may reflect cells that are unhealthy to the point that they are starting to die.

The authors conduct a FACS-based analysis of astrocytic mRNA from control vs Upf2-KO, with intriguing results. An important caveat, though, is that a large amount of astrocytic mRNA is in the processes. If mRNA stability is being actively and rapidly regulated, it seems likely that the mRNA in the processes would be the most relevant population of regulated mRNA. FACS-based approaches to astrocyte purification will, as robustly shown elsewhere, strip off those processes. Particularly given that the authors have shown that the processes may be the most actively changing astrocytic compartment with Upf2 KO, this is a strange choice of technique vs. something like Ribotag that would preserve the mRNA in processes. At least, there should be some discussion regarding using FACS for this analysis and the consequences for profiling mRNA in astrocytic processes.

Minor points:

(1) The use of the Aldh1l1-CreER mouse is a strong choice and has been shown to be highly astrocyte-specific. Combining that transgenic mouse with viruses driven by different forms of the GFAP promoter is quite bizarre in several ways. First, GFAP-dependent AAVs have been shown repeatedly to have significant neuronal leak. Second, these mice are, in all cases, receiving two different viruses, driven by different forms of the GFAP promoter, and the non-Cre virus is not Cre-dependent (vs. a much more standard approach of using a Cre-dependent second virus to ensure that all analyzed cells received both viruses). The authors mention that "this experimental design ensures that phenotypes are not caused by an acute effect of tamoxifen." It is certainly true that tamoxifen is not a biologically neutral molecule. However, the mice still receive tamoxifen, both in these morphology virus experiments and in almost all other experiments. This experimental approach is not inherently bad, nor does it necessarily invalidate the data (although the near-certain neuronal contamination due to the GFAP promoter-driven viruses is a concern). It is, however, convoluted in ways that appear unnecessary. If there is a strong rationale for this approach beyond the tepid explanation already present, it should be explicitly mentioned.

(2) The characterization of the knockout is incomplete. While the authors should be applauded for their attempts to phenotype the cells in which they observe Cre-mediated recombination, there are issues with their technical approach. Most importantly, and an issue that affects other analyses in the paper as well: the vast majority of astrocytes in the healthy cortex do not express GFAP. Therefore, using GFAP to claim high astrocyte specificity and efficiency is a fundamentally flawed approach. Second, MBP is a myelin marker, not a cytoplasmic marker, and would not successfully colocalize with a cytoplasmic marker like ZsGreen even if recombination in oligodendrocytes did occur. Third, recombination at one set of LoxP sites is not a reliable indicator of recombination at other sites. Recombination efficiency is highly dependent on the spacing between the LoxP sites and cannot be reliably extrapolated to other floxed genes without validation. Finally, the most likely culprit for off-target recombination with Aldh1l1-CreERT2 (or other astrocyte-selective Cres, and certainly the GFAP-based viral promoters) is neurons, which the investigators did not test for. Neuronal Aldh1l1-CreERT2 leak is most likely to occur in the hippocampus. With the images shown in Fig S3, it is unclear whether it is possible to convincingly colocalize Upf2 staining with a cytosolic marker of all astrocytes, such as Aldh1l1 or S100b, but such data would be more appropriate. An alternative approach to validation would be in situ hybridization.

(3) Supplementary Table 2 should include gene IDs, not just Ensemble IDs.

(4) It is not fully clear what the investigators are denoting as a spine in Figure 2E; the two images do not appear to have the large degree of difference that the quantification suggests. The oversaturation of the signal complicates assessment.

(4) A more detailed discussion of the rationale behind the timeline would be helpful. What is the half-life of Upf2, and how rapidly do NMD genes build up upon Upf2 disruption? In particular, in the case of virus experiments, the timeline is quite fast: ~2.5 weeks from injection to analysis. ssAAV expression takes over a week to reach appreciable levels.

Reviewer #3 (Public review):

Summary:

The authors investigate mRNA targets of the nonsense-mediated decay (NMD) pathway in astrocytes and link the dysfunction of NMD in astrocytes to aberrant synaptic transmission that has downstream effects on behavior. Specifically, they find a link between the aberrant synaptic transmission with elevated spontaneous calcium signaling in astrocytes, and functionally they demonstrate that manipulating astrocyte calcium signaling with CalEx modulates astrocyte calcium signaling towards wildtype levels and improves anxiety behavior. They investigate the astrocyte calcium signaling changes in Upf2 conditional knockout mice in several brain regions that have been linked to anxiety behavior, including the hippocampus and prefrontal cortex. They also observe aberrant astrocyte calcium signaling in the visual cortex, demonstrating that dysfunction of the NMD pathway in astrocytes has widespread effects on synaptic transmission in various brain regions. This work identifies, through RNA-Sequencing, potential mRNA targets of NMD in astrocytes, and shows that pathway enrichment of these targets highlights calcium signaling. Altogether, this work highlights the importance of the basic cellular process of NMD in astrocytes, which are known to have extensive local translation of proteins in their perisynaptic processes. NMD may be particularly important in astrocytes due to their intimate association of processes with neuronal synapses, and the authors suggest that alterations to NMD function in astrocytes may be an important avenue for future investigation in neurodevelopmental disorders.

Strengths:

Altogether, this work is a critical foundation for future research into astrocyte contributions to neurodevelopmental disorders. The authors do a thorough characterization of astrocyte conditional Upf2 knockout mice in several brain regions. They present a complete story that connects molecular events (NMD pathway regulation of mRNA degradation) to astrocyte regulation of circuit activity to organismal behavior. The electrophysiological analysis is thorough, and the manipulation of calcium activity ties astrocyte calcium activity to anxiety behavior. The RNA-sequencing dataset is useful to the scientific community and provides a resource of candidate molecules that might be dysregulated in neurodevelopmental disorders.

Weaknesses:

The study suffers from some overstated claims and a lack of statistical rigor in some experiments, as detailed below.

(1) The title states that "Astrocytic Nonsense-mediated mRNA decay regulates calcium signaling to support synapse function and restrain anxiety". The term "restrain anxiety" implies that the NMD pathway has a direct effect on a molecular switch to control anxiety. Anxiety behavior is a complicated process, controlled by many biological phenomena and synaptic transmission in the circuit as a whole, and is not directly linked to a specific NMD mRNA target. This title is overstating the findings of the study.

(2) In general, the first figures (1-2) suffer from low power (N = 3) and statistical rigor. The statistics are inflated by analyzing individual fields of view and per-cell data rather than performing the statistics on the average of biological replicates. It is preferable to show the biological replicate data so that readers can observe the natural biological variability between replicates.

(3) The claim that astrocytes have decreased engulfment of synapses in the Upf2 conditional knockout mice is not strongly substantiated by the data. The resolution of confocal microscopy and the static nature of histological images make it difficult to measure synaptic engulfment as an active process. Additionally, the metric of quantifying the % occupancy of PSD95 puncta within the total astrocyte volume may be skewed due to overall differences in cell size (shown in Figure 1). There is not much discussion of how a decrease in astrocyte engulfment of synapses may lead to decreased synapse number. To the contrary, one might expect decreased engulfment to result in increased synapse density.

(4) The authors use Gfap as a marker to count astrocyte cell number and assess if there are changes in cell number between genotypes (Figure S6). However, Gfap does not label all astrocytes in the cortex and, in fact, is rather an aberrantly expressed marker in conditions of inflammation, as opposed to the hippocampus, where Gfap is basally expressed in all astrocytes. In the cortex, there seems to be a trend for reduced Gfap in the conditional knockout mice, which may suggest differences in astrocyte molecular signatures rather than cell numbers. Another astrocyte marker, like Aldh1L1, will be more accurate to assess this question histologically.

(5) The authors state that "Preventing abnormally high basal calcium activity in NMD-deficient astrocytes restores normal excitatory synapse function...". However, this claim is not substantiated by the data. CalEx manipulation certainly shifts the input-output curve but does not restore to wildtype baseline levels (Figure 6E). Additionally, synapse number does not appear to be restored to wildtype levels (Figure 6D - although the p-value for this comparison is now shown). The investigators do observe improvements in anxiety phenotypes, suggesting there is some modulation of circuit activity, but the claim that CalEx manipulation restores baseline synaptic transmission is not supported.

Reviewer #1 (Public review):

Summary:

The article "Nanoscale organization of beta-II spectrin within segments of the membrane-associated periodic skeleton in mouse sciatic nerve axons" by Gazal et al. looks into the organization of the spectrin scaffold in mouse sciatic nerves using super-resolution microscopy. It is now well established that axons, across species, contain a membrane-associated periodic scaffold mainly composed of circumferential actin filaments and longitudinally arranged spectrin tetramers. While super-resolution imaging of neurons in cell culture is relatively easy, exploring the ultrastructure of myelinated axons in intact nerve fibers is a daunting task. Nevertheless, the authors have attempted this by fixing and preparing cross-sections of sciatic nerves. They have then tried to quantify the fluorescence intensity patterns of specific components, especially that of labeled beta-II spectrin and have analysed its distribution.

One of the main findings is that spectrin is distributed along the axonal periphery and along the outer part of the myelin sheath. By labelling multiple cellular components and using intensity analysis, the authors show the sequence of structural organization of a few key components. They see that, unlike in the case of axons in culture, the axonal cross-sections within the sciatic nerve deviate significantly from a circular shape. They then use 3D-dSTORM to investigate the distribution of beta-II spectrin along the axonal circumference. They see that this distribution is very heterogeneous, both in the sizes of spectrin puncta and their arrangement along the periphery. The amount of spectrin scales linearly with axonal circumference.

Strengths:

Super-resolution imaging of axons of intact nerve fibers to investigate the organization of beta-II spectrin.

Weaknesses:

While most of the findings, like the spatial distribution of spectrin and related components, are reasonably well supported by data, I have concerns regarding the subsequent claims made in the article. The detection of axial periodicity based on the observation of a peak in the inter-tetramer spacing distribution is not very convincing, and a 3D representation (or a video of 3D reconstruction) would have been better. And so are the claims on characteristic spectrin spacing of 200 nm along the axonal circumference. A peak in the distribution does not imply a periodic arrangement.

Reviewer #2 (Public review):

Summary:

This is an interesting paper by the Unsain lab looking at the nanoscale organization of the membrane-associated periodic cytoskeleton in mouse sciatic nerve axons. The precise organization of the structure remains unclear, especially in vivo, and this manuscript significantly adds to our knowledge of this important structure. While some of the findings in the study are somewhat expected (though still valuable to see in an in vivo setting), an interesting observation is the presence of discrete nanoscale clusters that scale up with the size of the axon, which challenges previous assumptions.

Strengths:

Strong, convincing data; clever combination of imaging and analytical tools to make novel points; well written; excellent composition of figures.

Weaknesses:

(1) Figure 2A/3A: The large and small clusters of spectrin, as seen in cross sections, are unexpected and novel. The authors have done a clever job of combining imaging and analyses, but some things are still unclear. First, the authors should be consistent in their language when they talk about the spectrin clusters. Recommend precise language to define the small and large clusters when they first appear in the text, and then use the definitions consistently throughout the text. Second, based on the data shown, one does not get a clear idea of how the small and large clusters are organized along the longitudinal axis of the axon. In that context, are Figure 2B and C from imaging along the longitudinal axis? If not, it's unclear how the authors can conclude that the spectrin assemblies have a distance of ~170 nm along the linear axis. In general, a perceived limitation of this study is that while the authors have done a good job looking at cross sections, there is no information on the longitudinal distribution of spectrin in these axons. Looking at both cross- and longitudinal sections would also clarify details about the large spectrin clusters. For instance, are they small sausage-like structures, or long rods of spectrin running along the length of the axon? One assumes that all the analyses in Figures 3 and 4 are from the small clusters. Can the authors do a similar analyses of the large clusters? Finally, a schematic model showing both cross- and longitudinal- sections would make things clearer, but the authors would need to show the longitudinal data for that.

(2) It is interesting to think that the larger spectrin accumulations may be similar to the condensate-like structures seen by Boyer et al., as the authors mention in the discussion. In that context, it is possible that these focal accumulations are local reservoirs of spectrin that are also seen in mature axons (indeed, these accumulations were also seen in mature axons in the Boyer et al. paper, and they also speculated that these accumulations may be local reservoirs). Can the authors check if actin/adducin is also present in these larger spectrin accumulations?

(3) While talking about the nanoscale clusters, it is important to specify that the authors are talking about circumferential clusters. Though the writing is excellent, one still does not get the precise definition of "clusters" from just reading the abstract, and it would be good if the authors could work on that more (I recognize that this is not easy to do).

Reviewer #3 (Public review):

Summary:

In the presented work, the authors investigate spectral staining in axons of the sciatic nerve, where the MPS has been detected before using STED microscopy. They employ 3D-dSTORM in tissue sections and analyze the data, measuring localization of clusters on the axon perimeter and the relative distribution of those. From these data the conclude that large gaps in spectrum localizations exist and that clusters around the axon exist that are spaced at 200nm.

Major Comments:

(1) The presented data are at times overinterpreted, and the discussion lacks a critical view of the data. For example, the statement "...Unlike previous suggestions from qualitative evidence in cultured neurons (REfs), βII‑spectrin distribution in MPS segments of peripheral nerves is discontinuous, with extensive stretches of the perimeter lacking βII‑spectrin." is quite strong, given it is based on immunofluorescence staining and dSTORM microscopy in tissue. Absence of evidence of staining is not evidence of absence.

(2) The authors claim in the abstract that "The number of these clusters scales linearly with the axonal perimeter, maintaining a constant membrane occupancy of ~20% across varying axon diameters." Again, this is from a cut through an axon, while measuring the density of clusters on the perimeter. If they claim area occupancy, an area should be imaged, and the dots (clusters) should be measured in surface coverage in a 2D projection of the axonal surface.

(3) In general, this reviewer suggests being a bit more moderate in statements such as: "These findings challenge simplified models of the MPS based on cultured systems and demonstrate that the MPS in peripheral nerves is composed of discrete structural units." These statements are bold from the relatively few measurements in a single method and a single viewpoint. Especially when considering that techniques such as dSTORM depend extremely highly on labeling density, and apparent clustering of localization is highly prone to misinterpretation. If the authors desire to make such statements, working with endogenously labeled protein would be warranted. The authors should at least hedge such statements.

(4) If the authors want to make statements about general organization, why do they not compare adjacent cuts through the axon? If there are continuous spectrin filaments, the clusters should appear at the same site across repeated cuts through the axon.

Besides this, this reviewer welcomes the effort that has been made to establish dSTORM in tissue sections and to investigate the MPS in native tissue.

Reviewer #1 (Public review):

Summary:

The predominant view on CHOP's functions during ER stress is that it promotes cell death. This is in contrast to a handful of reports in the literature that claim that CHOP is a positive regulator of protein synthesis during chronic ER stress, and therefore is part of the adaptation program to ER stress. These previous studies were performed in tissue culture cells. Velarde and co-authors have used a mouse model of induction of mild ER stress to study the function of CHOP in hepatocytes.

Major strengths and weaknesses of the methods and results:

The authors use state-of-the-art mice to manipulate (i) CHOP and (ii) ATF6, a protective factor of ER proteostasis, and address the hepatocyte responses to mild ER stress in vivo and in cultures. Validated gene expression programs are well correlated to liver pathology in the mouse models. This is a very well-done study.

The authors clearly show that CHOP transitions hepatocytes under mild ER stress to a chronic ISR state, which is phenocopied by ATF6-depleted hepatocytes. So the conclusion that CHOP exacerbates ER stress in hepatocytes during mild ER stress is correct. It is also clear that CHOP targets negatively the transcription of hepatocyte identity genes, which opens a new direction of studies on the function of CHOP in secretory cells in general.

Conclusion:

This is a significant study that will benefit different research fields, and specifically studies on proteostasis, as was recently highlighted in Nat. Str. Mol. Biol. by experts in the field.

To this reviewer, the importance of the study is that it links the function of a transcription factor (CHOP) to stress intensity (mild versus severe) in a physiological experimental model (hepatocyte function and pathology).

Reviewer #2 (Public review):

The Unfolded protein response (UPR) and related integrated stress response (ISR) are critical signaling systems for cell survival in response to acute stresses. While the UPR directs critical adaptive gene expression, certain chronic stresses switch this pathway towards cell death and disease. An important question concerns the mechanisms by which the UPR switches from being adaptive to maladaptive. Prevailing models focus on the transcription factor CHOP (DDIT3 or GADD153), whose levels are enhanced via the UPR, and extended/amplified amounts of CHOP are suggested to boost death-related gene expression. However, the literature and this manuscript point out a number of observations that do not neatly fit with this model, suggesting that there are still unresolved processes by which CHOP adjusts cell outcomes via the UPR.

This manuscript features a nice hepatocyte-targeted knockout of CHOP to discern the contribution of CHOP in the transition between adaptive and maladaptive outcomes. The key ideas presented in this study are that CHOP-directed gene expression is focused on protein synthesis, metabolism, and hepatocyte identity. In the progression of the UPR, CHOP expression can lead to resumption of protein synthesis, which can assist in the translation of the UPR-directed transcriptome, which includes ATF6/XBP1-directed genes that aid the processing capacity of the endoplasmic reticulum (ER). However, enhanced nascent protein can further stress the ER. CHOP directs gene expression in both the first phase- acute and second phase-chronic in the UPR, and the pivotal decision lies in the transition between the phases.

Overall, the manuscript includes some new ideas as well as refinements of earlier ones for CHOP-determination of UPR-directed cell fate. The CHOP-hepatocyte knockout mouse model helps to delineate the different tissue functions of CHOP, which has been a problem for some earlier studies. The manuscript progression of experiments is solid, and experimental design and documentation are rigorous. The manuscript text is largely clear, but there are portions that would benefit from fuller explanations of ideas.

There are three points of concern. First, the manuscript model (Figure 7) lays out a timeline for the progression of the UPR between two phases. The study is not always clear about the times assayed, and there appears to be a single time point for measurements. Second, there is emphasis on protein synthesis changes in the model. It is true that the literature argues that resumption of protein synthesis concurrent with stress damage (i.e., GADD34-directed gene expression) is a key reason for the potentially debilitating effects of CHOP (e.g., Marciniak et al 2004, Han et al 2013). However, the manuscript does not feature protein synthesis measurements. Inclusion of bulk protein synthesis measurements in the context of this model system would strengthen the study and support for the model. Finally, for this reviewer, some of the most interesting ideas center on CHOP-directed transcription of genes that regulate hepatocyte identity. There is solid evidence for direct CHOP regulation of these genes, but the manuscript does not really develop and test the ramifications of these networks on cell fate during ER stress.

Reviewer Concerns:

(1) The abstract packs in a lot of information. The ideas would not be clear to a general reader. Furthermore, the UPR and ISR are referred to in the second-to-last sentence, but not defined earlier in the abstract.

(2) There are some typos/grammar concerns.

(3) ATF4 diminished with CHOP-depletion (Figure S2A). What is the mechanism here? Does this complicate the analysis of CHOP-directed gene expression? How does this fit with Figure 6J? The timelines for TM treatment are critical. The authors should more fully explain the time courses in the experiments.

(4) Figures 2 and 3: There is a discussion on enhanced protein synthesis with loss of CHOP (reduced GADD34 expression). What is the time point - 8 hours TM? Emphasize, explain, and justify time points of experiments here and in later panels. It would strengthen the model with direct measurements of protein synthesis. The authors could include GADD34 protein measurements in these panels. Figure 3 - panel D - some abbreviations are not standard.

(5) Figure 4: One of the most interesting in the manuscript is the transcription factors downstream of CHOP that are linked with hepatocyte differentiation and metabolism. The manuscript would be bolstered by developing some of these target genes into the Figure 7 transition model.

(6) Figure 6: The comparison of CHOP and ATF6 target genes is a highlight of the manuscript. The literature on this topic is complex, and there are some suggestions that CHOP can be downstream of ATF6. Furthermore, there were some earlier models by Walter and others about extended induction of Perk (death) vs induction of other UPR sensors (survival) (e.g. PMID: 17991856). It would be helpful in the Discussion to delineate between these models and their critical differences.

Reviewer #3 (Public review):

In this manuscript, the authors aim to understand the function of the transcription factor CHOP, which is known to promote cell death during severe stress in the ER. The authors note that CHOP is induced during less severe stress, but its functional output is not well understood in these cases. Here, they study the effects of conditional knockouts of CHOP in hepatocytes of mice challenged with chemical inducers of ER stress.

Tunicamycin (an ER stress inducer) injection leads to the upregulation of CHOP and lipid accumulation in the liver, but no significant cell death in the experiments outlined here. Conditional knockout of CHOP results in a number of differences in the way hepatocytes respond to stress, notably resulting in lower steatosis.

There are two main findings supported by the data presented here. First, the authors show that CHOP suppresses the expression of ONECUT, a master regulator of hepatocyte differentiation and metabolism, during ER stress. They show by ChIP-seq that CHOP binds to the promoter region of this gene, and by RNA-seq that ONECUT expression is suppressed by ER stress in a CHOP-dependent manner. Many predicted targets of ONECUT1 were also suppressed by ER stress in a CHOP-dependent manner, though they were not bound directly by CHOP. The data support a model where CHOP down-regulates hepatocyte metabolism and identity via regulation of ONECUT1. This is a new and interesting finding, perhaps explaining the steatosis phenotype of livers that accompanies ER stress, although this was not tested directly.

The second main finding of this paper is that CHOP deletion leads to an interesting assortment of effects on genes related to the ER stress response and integrated stress response (ISR). As expected, based on prior work, CHOP deletion led to more phosphorylation of eIF2alpha (CHOP is known to upregulate the phosphatase for this translation factor). However, unexpectedly, this did not cause increased expression of ATF4 (a transcription factor whose upregulation during stress is dependent on eIF2alpha phosphorylation) and its downstream targets; in fact, CHOP deletion had the opposite effect on these. In other words, CHOP seems to both turn off the initiating signal for the ISR (namely, eIF2alpha phosphorylation) and also promote the downstream signaling events that rely on this initiating signal. It makes sense that cells would do this, as restoring translation would be important for realizing the effects of the massive changes in gene expression initiated by ER stress, and yet this would exacerbate stress in the short term, so it would be counterproductive to also turn off the entire stress-regulated program. Having a factor (perhaps CHOP) that coordinates these two events makes sense. It will be interesting in future work to understand the mechanisms behind this regulation.

Finally, CHOP deletion led to less activity of other aspects of the ER stress response, notably IRE1 (determined through measurement of XBP1 splicing and RIDD of Bloc1s1). This is explained by the continued phosphorylation of eIF2alpha in these knockouts, as the continued attenuation of translation would lessen the burden of misfolded proteins in the ER. Somewhat confusingly, the same pattern is not seen in downstream targets of XBP1. Less splicing, coupled with perhaps less translation of the spliced mRNA, should result in less active transcription factor and lower expression of its target genes in the CHOP KO. This is not observed in Figure 2, although the more global gene expression analysis suggests that all stress-dependent gene expression changes were weaker in the CHOP KO livers.

The authors characterize the effects of CHOP, promoting restoration of protein synthesis and the accompanying exacerbation of stress while preserving the signaling that should relieve ER stress, as a switch from an acute to chronic phase of ER stress. This is mirrored in their analysis of ATF6 in a similar series of experiments. Although this is an interesting framework for thinking about the stress response, whether CHOP is the key factor or a supporting actor in regulating this transition will require a better understanding of the mechanisms involved.

Reviewer #1 (Public review):

In the wild, bacteria can be found in a wide range of metabolic states, including states in which they are resource limited. Because phages heavily rely on the infected cell's molecular machinery to replicate, it is natural to wonder how phage-bacteria interactions depend on the metabolic state of the cell. In this work, Marantos et al. investigate specifically how the rate of infection of 5 different phages changes between cells grown in energy-rich conditions and cells grown in energy-depleted conditions. Their results clearly show that 4 out of the 5 phages studied display a significant reduction in infection rate in cells that are energetically depleted and provide a potential explanation for this observation by looking into the mechanisms that these phages use to irreversibly infect their host cells.

The work also tries to explain the observation using a mathematical/mechanistic model that describes infection as the sequence of two steps, where a phage first needs to bind to a cell receptor, from which it can potentially unbind, and then irreversibly infects by injecting its genome. The mechanistic interpretation offered by the model highlights an interesting trade-off between adsorbing to a metabolically active host and discriminating between active and inactive hosts that, somehow, a phage has to optimize. It would be interesting, in the future, to investigate how different phages optimize this task.

Comments on revised version.

I am happy with how the authors have addressed all the comments. The manuscript is much clearer and more readable and the previous overstated claims have been removed/clarified.

Reviewer #2 (Public review):

Summary:

The authors investigate the dependence of phage adsorption rates on host metabolic state, using 5 coliphages that differ in their infection cycles and host receptors. They find that four of the 5 phages showed significantly reduced infection under low metabolic states, with phage that generally have weaker adsorption being more strongly affected by low metabolism. The authors complement their findings with a 2-step infection model where phages can disengage from their hosts after initial adsorption. The paper illustrates the power of standardized experimental protocols for quantitative trait comparisons and highlights the dependence of phage infection success on host physiology.

Strengths:

The paper is well written and clearly structured.

The experiments are well designed and particularly commendable is the diligent use of control scenarios to allow for quantitative comparison between phages. This standardized protocol will be valuable for the entire phage community.

The authors convincingly show the impact of host physiology on phage adsorption success. This dependence has so far mainly been considered for intracellular phage replication and the paper shows that host physiology has to be taken into account at all steps of phage infection.

Reviewer #3 (Public review):

Marantos et al. showed that for some coliphages, the energetic state of the bacterial host cell has a strong impact on whether phage infection is initiated. The authors drew this conclusion from the observation that there are more free phages remaining in the medium after infection of arsenate-azide-treated cells as compared to after infection of untreated cells. These data were analyzed and reported both as ratios of the treated vs. untreated conditions and using a mass-action kinetic model of phage-cell collision in the infection mixture. The data supported the findings that for four phages infecting Escherichia coli bacteria, namely, phages λ, 𝜙80, m13, and T6, the phages are less likely to initiate infection if the host bacteria are energy depleted. However, for phage T5, the authors found that their infection propensity is not impacted.

As I have stated in the first submission of this manuscript, the data presented by the authors clearly supported the principal conclusion of the study. The five phages chosen by the authors represent different viral lifestyles and infection mechanisms, highlighting the potential applicability to other Escherichia coli phages. Finally, the authors successfully use a classic mass-action model of phage-cell collision to interpret their data. The simplicity of their experimental assay, combined with the use of this mathematical model, offers other investigators who study phage-bacterial interactions in other contexts a potentially useful toolkit to examine infection in general, and specifically, the dependence of phage infection on the host's metabolic state.

Comments on revised version.

In this revised version, the authors have successfully resolved all of my comments. I appreciate that the main text has been majorly revamped, which greatly helps the readers follow the motivation behind the experiment and analyses, and interpret the data. I agree that the revised terminology choice "commitment to infection", instead of the previous interchangeably used "adsorption"/"entry", is much more logical, considering the experimental data. I also commend the authors for writing the modeling part in a very clear, pedagogical, and instructive manner. Overall, I believe that this manuscript will be valuable to those who are interested in phage-bacterial interactions.

Reviewer #1 (Public review):

Summary:

This paper presents a toolkit for the transformation of Blastocystis. The authors have screened a number of selectable agents, promoters and reporter genes and present their findings. This resource will be of immense use to those in Blastocystsis field, as well as those seeking to establish transformation tools in other species where such tools do not yet exist. Establishing new transformation tools is extremely challenging, and the authors have done an excellent job.

Strengths:

The authors have carried out a systematic screen of promoters, reporter genes and selectable agents. They have screened numerous for each, and all the data is presented. It is good to see when things did not work as well as when things did - so this data set is extremely useful indeed.

Weaknesses:

The findings are reported by reporter gene assay (microscopy). No evidence is given using genetics. The authors claim that the DNA is maintained episomally. However, could it be possible that there is integration? No PCRS/RT-PCRs are shown (although it can safely be assumed that the DNA/RNA is present where the transformation was successful), nor are any Western blots. These would have been useful to show that the P2A ribosomal skipping had occurred, and that proteins were expressed individually rather than as a polyprotein.

Comments on revised version.

The authors have revised their manuscript to clarify that molecular analyses have not yet occurred and have resolved the technical/publication issues with the figures. I look forward to seeing these tools used in future publications to answer important questions in Blastocystsis research.

Reviewer #3 (Public review):

Summary:

The primary objective of this study was to establish a practical and functional framework for propagation of stable transgenic cell lines of Blastocystis, a common animal gut microeukaryote. Although the work focused on Blastocystis ST7-B, a subtype with relatively low prevalence in humans, this choice is justified by its association with more frequent negative health effects. Beyond their relevance to the medical field, the methodological advances described here have the potential to also expand cell biology studies of this anaerobic organism, including its unusual mitochondria and redox metabolism.

Strengths:

Prior to this work, genetic tools for Blastocystis were very limited, relying on a single strong promoter-terminator combination. The authors successfully expanded the available promoter set across a range of expression strengths by testing two dozen variants in luciferase-based assays. Critically, they developed an integrated workflow from a modular transgenic construct design to an expanded inventory of molecular components (promoters, reporters), optimized DNA delivery, stepwise antibiotic resistance-mediated clonal selection and propagation, and to reporter validation. The evaluation of several anaerobiosis-compatible labeling strategies for live (and fixed) cell optical imaging will be particularly useful, with the SNAP-tag system appearing especially promising for Blastocystis.

Weaknesses:

The presented data generally provide a solid support for the conclusions that the work reached, but clarification of reasoning and several inconsistencies, as well as amendments to visual presentation of the data would be highly beneficial, as detailed below.

(1) Episomal persistence of the construct:

The manuscript repeatedly assumes, including in its title, that constructs persist in Blastocystis in their episomal form, but no direct evidence is provided. Although this interpretation is plausible, it should be identified more clearly as provisional. Nuclear genomic integration (e.g., via NHEJ) remains a possible explanation unless supporting evidence or rationale is provided to exclude it. Testing whether the phenotype persists without drug-mediated selection in the generated transgenic cell lines would help strengthen the case for episomal maintenance.

(2) Promoters and terminators:

(2.1) There is a discrepancy between the claimed number of loci (14), from which promoters used to drive luciferase expression were derived, and those detailed as having been actually generated in Table 1 (11). This inconsistency should be corrected or explained, as it creates uncertainty around the accuracy of the dataset.

(2.2) Based on the presented evidence, constructs benchmarked in bioluminescence assays differed only in their promoter composition. Although terminator selection is mentioned in the Methods section, no additional details are provided; for instance, Table 1 and Figure 2 only list 23 promoters in total. Figure 2A likewise shows only promoter-dependent variation. If the terminator was held constant (LeguP1?), this should be stated explicitly. The authors may then consider revising the wording of having tested "23 promoter-terminator pairs" to better reflect that only promoters varied.

(2.3) Promoter benchmarking was done with a plasmid lacking a selection marker, so it is unclear how the maintenance of the luciferase construct was ensured. Without selection, the observed reporter intensity could reflect differential or stochastic plasmid retention rather than promoter strength alone. The luminescence assay was performed 16-18 hours after transfection, but the rationale for this particular timeframe should be explained. In this context, the authors should explicitly state whether the experiments shown in Fig.2A represent biological triplicates or technical triplicates from a single transfection.

(3) Figure 2:

(3.1) Several aspects of the current design may lead to ambiguity for the reader. The boxplots are colour-coded, but it is unclear whether the colours carry meaning or are purely decorative. Because the data are already spatially separated into bins, additional random colouring is redundant and may suggest distinctions that are not intended. In addition, the part A of Figure 2 is split into two panels with the scale for the left panel shown in the right panel and some of the boxplot colours falling in the range of the scale, but not in line with their counterparts in the left panel. Because the colour use is not consistent, it is difficult to tell whether the same scale should be applied to both panels or how it should be interpreted.

(3.2) The left panel of the part A uses a diverging blue-white-red colour scheme, which is most appropriate when the midpoint represents a meaningful central value such as zero. Because the values shown in this graph are only positive, a non-diverging 2-colour scale or a colour palette such as 'viridis' would make the plot easier to interpret.

(3.3) A black background should be avoided: 'B' and 'C' labels are invisible and it draws attention to a distracting design feature rather to the data themselves.

(4) Figure 3:

(4.1) Individual snapshots should be separated more clearly, either by using a white background or by adding visible borders to make the overall composition clearer. As currently displayed, some boundaries between fluorescent channels resemble image artifacts rather than intentional panel divisions.

(4.2) In the parts B-D, the legend should explain more clearly what each image shows and the figure itself would benefit from annotations. There seem to be three sub-panels in each 'condition' of part B (as well as C and D): while the middle and rightmost panel can be easily inferred to represent the fluorescent protein and bright-field image, what the leftmost panels represent is not specified. If DAPI was used to dye DNA, an explanation why mostly multiple labelled regions are visible should be provided.

(4.3) Cell morphology and appearance differ markedly between UnaG/smURFP and SNAP-tag images, which should be explained. A microscope issue is mentioned in the main text, but if that was the cause, the authors should consider replacing the images as the current distortions complicate interpretation.

Comments on revised version.

The revised version provides sufficient clarity and appropriate visual presentation. Some confusion evidently arose due to my misunderstanding, so I thank the authors for their comprehensive clarifications and patience.

Reviewer #2 (Public review):

Summary:

The manuscript titled "Latent gene network expression underlies partial re-evolution of a polyphenic trait in the worker caste of ants" by Vasquez-Correa et al. aimed to study genetic mechanisms underlying developmental plasticity, especially binary polyphenism in queen vs worker ant castes. This is an interesting question regarding the extent to which phenotypic traits were altered, lost or regained, and how molecular pathways (upstream vs. downstream) can facilitate this process.

In ants, reproductive castes (queens and males) develop wings as well as 3 ocelli for mating flights and other activities, while worker castes are wingless, and in some species, they have either no or a reduced number of ocelli. The phylogenetic analysis showed that in the Camponotini ant clade, the one-ocellus phenotype re-evolved in three species independently. The authors analyzed the conserved developmental pathways between Drosophila (well-established) and ants using HCR (a high-quality in situ hybridization technique). They found that although upstream genes for the development of ocelli (otd and hh) showed similar expression between castes, downstream genes (toy, eya, and so) had reduced or no expression in workers of C. floridanus, and this differential expression may lead to partial or complete loss of ocelli. Consistently, workers develop rudimentary tissues, suggesting that they initiate the ocellus developmental process but somehow stop it before adulthood.

Strengths:

Evo-devo approaches to reveal conserved molecular pathways of ocellus development. High-quality HCR provided convincing evidence of the expression of key genes in ocelli, eyes and antenna throughout larval development.

Using HCR, the authors showed differential expression of downstream genes in males vs. soldiers vs. minor workers of C. floridanus, which might explain phenotypic differences between castes.

Comments on revised version.

The authors have addressed the concerns in the revision. No further comments.

Reviewer #3 (Public review):

Summary:

This paper examines the loss and re-evolution of specific organs during the evolution of ants. The authors show that these organs, the ocelli, disappear and are re-evolved in different ant species, and in different ant castes within these species. The Authors show that this is linked to a conserved GRN discovered in Drosophila, that appears to underlie the development of the ocelli, and demonstrate that this GRN appears to remain active in the developing heads of ants that have no ocelli- implying that it is the evolutionary latency of this GRN that allows loss and subsequent evolution.

Strengths:

This manuscript has outstanding imaging of a very difficult developing organ, and the key data, fluorescence in situ hybridisation, is done well and clearly shows what the authors wish to demonstrate. The methods are well described and underpin the whole work.

The authors convincing demonstrate that gene expression patterns imply the conservation of the ocellus gene regulatory network from Drosophila to ants. They further show that this network is present even in ants that don't produce an adult ocellus, but do show that in those species, loss of a developing nascent ocellus (which they identify) occurs at the same time as an interruption in the expression of the key genes in the GRN. All of this data is beautifully presented and explained.

Weaknesses:

There is one key weakness in that there are no functional students that indicate that the GRN actually does make the ocellus, though the expression patterns are convincing. This applies to loss of the ocellus as well. It would be nice to see that transient loss of the ocelli GRN might lead to loss of ocelli in ant species that have them. These are very difficult things to achieve as the key genes have earlier developmental roles, such that CRISPr knockouts would not be interpretable, and transient RNAi in the head capsules of developing pupal ants would be challenging.

As the authors note in their response this is very difficult to achieve. While the addition of this data would raise this manuscript to an outstanding one, I think the data presented is solid, well-presented and provides novel insight.

Reviewer #1 (Public review):

Summary:

Cisplatin, a platinum-based chemotherapeutic agent, induces intra- and interstrand crosslinks, thereby blocking DNA replication and transcription and triggering apoptosis. The authors aim to demonstrate that DNA polymerase κ (Polκ), traditionally seen as a translesion synthesis (TLS) polymerase, able to synthesize DNA through DNA lesions, plays a non-catalytic, structural role in stabilizing replication forks and protecting cells from cisplatin-induced cytotoxicity. A key finding of this work is the identification of two novel molecular axes: PCNA-Polκ-Polδ, which facilitates efficient DNA replication; PCNA-Polκ-USP18, which stabilizes DNA damage response proteins. These findings provide actionable therapeutic targets for overcoming head and neck squamous cell carcinoma chemoresistance, a cancer with rising incidence and limited treatment options.

Strengths:

The study relies on a robust experimental design, including Polk allegedly CRISPR-Cas9 knockout, siRNA knockdown, and rescue experiments with wild-type, catalytically dead, and PCNA-interaction-deficient Polκ variants, supporting a non-catalytic role of Polκ. The work also reports a strong implication of Polk in cisplatin resistance, the identification of USP18 as a possible Polk partner and the consequences of Polk depletion on post-translational stabilisation of DNA damage response proteins.

Weaknesses:

The findings reported in this manuscript cannot be generalized to all cisplatin resistance mechanisms, as cells may develop multiple adaptive strategies to survive chemotherapy. Polκ's role varies across cancer types. For example, it is downregulated in stomach and colorectal cancers but upregulated in HNSCC, lung, and ovarian cancers. Thus, its use as a biomarker or drug target may be context-dependent.

Acute cisplatin exposure is sufficient to trigger Polκ upregulation to levels similar to those in resistant cells. However, it remains unclear how long this upregulation persists and to what extent it contributes to survival. Further, the sensitivity of cisplatin-naïve H357 or SCC9 cells (H357-S and SCC9-S) to Polκ knockdown has not been addressed. This is a critical question, as acute cisplatin exposure induces Polκ expression to levels similar to those in resistant cells. This could argue against a direct role for Polκ in mediating resistance and instead suggest indirect mechanisms (like Polκ-dependent mutations during adaptation).

The experimental design and results aimed at demonstrating the existence of a PCNA-Polκ-USP18 axis (Figure 9A) do not fully support the conclusion that these proteins form a stable complex. This set of experiments also lacks essential controls, such as the immunoprecipitated bait and the amount of immunoglobulins precipitated in all conditions. This also applies to the colocalization experiments in cells shown in Figure 9B. Images are poor and lack quantification. Further, Polk is seen mainly cytoplasmic in the upper panel, while it is nuclear in the lower panel. Discrepancies in Polk subcellular localization are also evident in the Supplementary data. USP18 is known to deubiquitinate ISG15-modified proteins (not just ubiquitin). The study does not rule out ISGylation as a contributing mechanism. The experimental design involving analysis of DNA synthesis dynamics at a single-molecule level is not appropriate. Overinterpretation of the data in several parts of the manuscript and lack of rigor in performing the experiments. Inappropriate consideration and absence of discussion of previously published literature directly related to the subject studied in this manuscript. Discrepancy with a previous report regarding the role of Polk in Chk1 phosphorylation (Tonzi et al., eLife 2018). Synergic effect of T2AA inhibitor and Cisplatin have been already described in « naive » cancer cells (Inoue et al, 2014). Another critical point is that the proliferation rate of Polk-depleted cells is slower than that of wild-type cells. Hence, the colony formation assay shown in Figure 2B can be misleading, since the observed differences can be interpreted only as a proliferation problem.

Reviewer #2 (Public review):

Summary:

Building on earlier studies, the authors report a role for pol kappa in mediated cisplatin resistance. Their data on dispensability of pol kappa catalytic activity for cisplatin resistance is consistent with previous reports. They further demonstrate that the PIP box of pol kappa is critical for cisplatin response. Based on these observations, the study concludes that targeting pol kappa and PCNA interaction can be a viable approach to overcome cisplatin resistance.

Strengths:

Indications that interaction between Pol kappa PIP box and PCNA can be targeted to overcome cisplatin resistance.

Weaknesses:

(1) The study has used a model of cisplatin resistance and found that the phenotype is specifically reliant on upregulation of Pol kappa. They also observe that in this model of cisplatin resistance, there is rapid degradation of multiple repair proteins, including ATM, ATR, HR and NHEJ proteins upon knocking out Pol kappa. However, it is unclear how the resistant model was derived. Also, since the data and almost all experiments in this manuscript were performed with a single model of cisplatin resistance, the conclusions should be taken with caution.

(2) There are also inconsistencies in findings. Increased G2 arrest and no change in origin firing are being observed despite a significant reduction in Chk1 protein levels.

Reviewer #3 (Public review):

This manuscript investigates the role of PolK in cisplatin repair. While in general it is considered that polK is not involved in the repair of cisplatin-induced DNA damage, the authors show that in a very specific scenario, namely cisplatin-resistant head and neck cancer cells, loss of PolK causes cisplatin sensitization, implying a role in cisplatin repair by polK in these cells. It is also implied that these cells acquire cisplatin resistance by overexpressing polK, but this is not really investigated. The authors then go on to show that DNA replication in the presence of cisplatin is affected by the loss of polK in these cells and also identify USP18 as a potential polK interactor in these cells with a similar phenotype. They claim that polK and USP18 form a pathway that allows cisplatin tolerance in these cisplatin-resistant head and neck cancer cells. The findings are interesting and useful to the field; however, the manuscript, in its current form, has several issues. Most importantly, the mechanism of USP18 has not been investigated. In addition, the manuscript does not flow fluidly, and instead, various experiments are put together without a clear logic. Some of the claims are not substantiated by the data shown.

(1) The experiments in Figure 1 using a few cell lines from various types of cancers are not enough to conclude that polK expression is specifically induced by cisplatin in some types of cancers but not others. Since the focus of this study is head and neck cancer, the authors should show the expression of PolK after cisplatin treatment in more head and neck cancer cell lines, and not just the two investigated.

(2) It is unclear to me why the authors include H357-S in their experiments. If the idea is that these cells acquire resistance because they overexpress polK, then the authors should investigate this by exogenously overexpressing PolK in H357-S cells and test if these cells are cisplatin resistant.

(3) In addition, the authors should create the polK knockout in H357-S cells as well and include it as a control in their experiments.

(4) Page 6, line 28: the comet assay does not measure DNA degradation, but rather DNA breaks.

(5) Figure 4B: How does the overexpression of PolK mutants compare to endogenous PolK expression? It is important to assess if this expression is similar or of much higher magnitude.

(6) Page 9, line 22: "For such a function, the catalytic domain of PolK becomes dispensable, whereas its interaction with PCNA is sufficient to drive efficient replication". I do not understand what data the authors used to make this claim. The interaction and colocalization studies should be performed with the PIP mutant. Similarly, this mutant should be used in the HU DNA fiber assays.

(7) It is unclear how USP18 acts. What are its substrates? Chk1/2, BRCA1, BRCA2? This needs to be investigated. The impact of PolK on this activity needs to be assessed as well (is PolK needed for USP18-mediated de-ubiquitination of these DSBR proteins?). As it stands, the manuscript does not address the mechanism of USP18 in DNA repair, which is billed as the main finding of the paper.

(8) Do PolK and USP18 interact directly? Experiments using recombinant proteins would be useful to address this.

Reviewer #1 (Public review):

Summary:

This is an important paper examining LTP induced by theta-burst stimulation in hippocampal slices from macaques and rats. While both species show theta-burst-late-LTP, only the non-human primate theta-burst-late-LTP showed synaptic tagging and capture that converts early-LTP into late-LTP in an independent synaptic pathway.

Strengths:

Synaptic tagging is a fundamental feature of repeated 100 Hz-tetanus-induced LTP, whereas theta-burst induction is arguably more physiologically relevant. Thus, synaptic tagging during theta-burst may differ in the two species, a distinction that may prove important in the mechanisms underlying the cognitive differences between the species.

Weaknesses:

Bursts repeated at the frequency (~5 Hz) of the endogenous theta rhythm induce strong LTP, primarily because this frequency disables feed-forward inhibition and allows sufficient postsynaptic depolarization to activate voltage-sensitive NMDA receptors. Therefore, the species differences may be due to differences in inhibition, rather than in molecular mechanisms of maintenance. One way to assess the relative strengths of this early induction mechanism in rats and macaques is to examine the "depolarization envelope" during the sequential bursts, which may be determined from the recordings already obtained. (Larson and Munkácsy, Theta-burst LTP, Brain Res 2015 Sep 24:1621:38-50. doi: 10.1016/j.brainres.2014.10.034)

Another issue is that the PKMzeta-antisense oligodeoxynucleotides block the synthesis of the kinase. However, Mei F, Nagappan G, Ke Y, Sacktor TC, Lu B (2011), BDNF Facilitates L-LTP Maintenance in the Absence of Protein Synthesis through PKMzeta. PLoS ONE 6(6):e21568, provided evidence that BDNF and theta-burst stimulation can act to increase PKMzeta by a protein synthesis-independent mechanism, presumably through decreased degradation. Therefore, the absence of an effect of the PKMzeta-antisense does not exclude the possibility that persistently increased PKMzeta is the mechanism of theta-burst-late-LTP maintenance in mice or macaques. This issue is worth discussing.

Reviewer #2 (Public review):

Summary:

This study compares theta-burst stimulation (TBS)-induced synaptic plasticity in hippocampal CA1 slices from rats and non-human primates (Macaca fascicularis). The authors report that while TBS induces persistent LTP in both species, only primate hippocampal slices exhibit synaptic tagging and capture (STC) under these conditions. They further show increased BDNF and PKMζ expression following TBS in primates and propose that a redundant BDNF/PKMζ signaling architecture supports persistent plasticity in primates, whereas rodent TBS-LTP depends primarily on BDNF. The work aims to identify species-specific specializations in associative plasticity with implications for translational neuroscience.

Strengths:

The topic is potentially important because direct comparisons of hippocampal plasticity mechanisms between rodents and primates are rare.

Weaknesses:

(1) Limited biological replication in the primate experiments

The manuscript's strongest claims rely on data obtained from 36 slices from 7 monkeys, qPCR analyses with n=3 biological replicates, and Western blot analyses with n=3 biological replicates. The effective sample size for species-level conclusions is therefore not large. The manuscript frequently treats slices as independent observations while drawing conclusions about species differences. This is particularly problematic for electrophysiological experiments because multiple slices appear to originate from the same animals. The statistical unit should be the animal, not the slice, unless nested analyses are performed.

The authors should (1) report the number of animals contributing to each experiment, (2) provide animal-level analyses, (3) use mixed-effects or hierarchical models where appropriate, and (4) clarify whether multiple slices from the same monkey contributed to the same experimental condition. Without these analyses, the evidence for species-specific mechanisms remains weaker than presented.

(2) The central STC conclusion requires stronger controls

The most important result is that TBS supports STC in primates but not rats (Figures 1F-G). However, several alternative explanations are not excluded. For example, only a single interval (30 min) between TBS and WTET is examined. Classical STC studies characterize tag duration, PRP availability window, and temporal asymmetry. The current work does not determine whether primates exhibit longer tag persistence, increased PRP synthesis, altered capture efficiency, or merely a shifted temporal window. A temporal series (e.g., {plus minus}15, {plus minus}30, {plus minus}60, {plus minus}90 min) would substantially strengthen the mechanistic interpretation.

(3) Species differences may reflect tissue quality or preparation differences

The manuscript compares 5-7 week-old rats with 5-7 year-old monkeys. These are very different developmental stages. Moreover, euthanasia methods, extraction procedures, and postmortem handling are different. These factors can affect BDNF expression, protein synthesis, LTP magnitude, and transcriptional responses. The authors should discuss these caveats more explicitly.

(4) Statistical reporting is incomplete

Many comparisons report exactly Wilcoxon p = 0.0313 and U-test p = 0.0022, across numerous experiments. This suggests very small sample sizes and discrete nonparametric distributions. The manuscript should report exact n values for each comparison, effect sizes, and confidence intervals.

Second, many genes and proteins are tested. No correction for multiple testing is described. The authors should state whether corrections were applied, and if not, justify this choice.

(5) Interpretation and significance

The study addresses an important and understudied question: whether associative synaptic plasticity mechanisms differ between rodents and primates. The finding that TBS can support STC in the primate hippocampus is potentially novel and impactful. However, the mechanistic evidence remains incomplete, the molecular analyses are underpowered, and several key controls are missing. At present, the data support the conclusion that under the specific experimental conditions tested, TBS-induced plasticity in primate hippocampal slices exhibits greater associative persistence than in rat slices.

The stronger claims regarding evolutionary specialization, fundamentally distinct plasticity rules, altered STC thresholds, and redundant BDNF/PKMζ architecture require additional experimental support.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors have undertaken an investigation of differences between two mammalian species, the brown rat and the crab-eating macaque, in the mechanisms supporting a well-established model of long-term Hebbian synaptic plasticity, Schaffer collateral to CA1 Long-term potentiation (LTP) in the hippocampus. LTP has been long-studied and deeply characterised due to its potential importance in modeling a strong candidate process for the central mechanism of learning and memory. LTP was first discovered in lagomorphs (rabbits), but has since been much more widely studied in rodents (mostly rats and mice), and there has been some complementary work revealing LTP in non-human primates and even in humans, revealing largely overlapping canonical mechanisms of induction, expression, and maintenance. More specifically, this study puts a particular focus on the fascinating associative features of this form of lasting synapse-specific modification, in which a synaptic input can be stimulated with a relatively weak induction protocol that will not produce lasting plasticity on its own, but can undergo lasting LTP if paired with stronger stimulation on a separate synaptic input to the same neuron. This associativity mechanism is particularly attractive within the Hebbian synaptic plasticity framework as it provides a candidate mechanism for associative forms of learning in which stimulus-stimulus, stimulus-reward, stimulus-punishment, or action-outcome associations are formed. A particularly attractive feature of this associative LTP is that there can also be a substantial time-lag between the strong stimulation of one pathway and the weaker stimulation of the other synaptic input, which only undergoes lasting LTP by hijacking the proteins synthesized as a result of strong stimulation elsewhere. This observation has led to the famous tagging and capture hypothesis as an explanation of how such synapse-specific change can be achieved on both stimulated inputs but not on other synaptic inputs, given the potential requirement for cell-wide protein synthesis. This theory, for which there is very strong experimental evidence, posits that a protein tag is left at synapses that have been stimulated with sufficient vigor in recent history, serving as a key mechanism to ensure that those weakly stimulated synapses will undergo change when a larger-scale LTP event occurs due to stronger stimulation elsewhere within a relevant time window. Again, this idea is attractive as it can explain how we might form associations between events that occur slightly separated in time. The manuscript goes on to show that an induction protocol that is particularly physiologically relevant, theta burst stimulation, produces this tag and capture associative effect in ex vivo slices of Macaque hippocampus, much more readily than in side-by-side ex vivo slices of rat hippocampus. Moreover, the manuscript delves into the importance of well-characterised LTP maintenance mechanisms, including PKMzeta and BDNF, which are key factors that ensure that altered synaptic change is maintained for long periods of time despite substantial molecular turnover in the neuron. The observation in this manuscript is that a degree of redundancy for these mechanisms exists in the primate species but not the rodent species, as both mechanisms need to be inhibited to return LTP to baseline in the Macaque, but only one needs to be inhibited to have that effect in the rat. A major emphasis of this study is that there may be a step-wise difference in associative learning mechanisms between rodents and primates that may contribute to their differing cognitive capacities, although I believe a lot more evidence would be required to reach that conclusion.

Strengths:

The strengths of this study are that it is technically very proficient and is from a laboratory that has a long history of seminal work on synaptic tagging and capture. The cross-species comparison, particularly involving non-human primates, is also very hard to achieve, and a major strength here is the side-by-side comparison of slices from rat and monkeys. Further strengths of the study are the use of a number of experimental strategies, including both observation and intervention, to demonstrate differential involvement of LTP maintenance mechanisms. A final major strength is conceptual, as it is undoubtedly useful not only to identify shared mechanisms of plasticity between commonly used model organisms and either humans or much more closely related species such as old world monkeys, but also to reveal differences that have the potential to contribute to differences in memory/cognition.

Weaknesses:

The findings of this study are a very useful building block for understanding how generalisable mechanisms of LTP are. However, arriving at really substantial conclusions from these findings is challenging, as there are a number of variables that are unaccounted for in this study that may explain the differences that have been observed between rats and monkeys. One example of a potential confound to these interpretations is that rats are nocturnal/crepuscular animals, and macaques are diurnal animals. Thus, to undertake a like-for-like comparison, it would be necessary for the rats to be on a reversed light-dark cycle to ensure that the wake cycle of the rat (dark) is being compared with the wake cycle of the monkey (light). It is possible that the authors have done this, but it is not mentioned in the methods section. The reason this is important is that there is a substantial body of work indicating that different mechanisms are at play in hippocampal LTP during wake and sleep. Transcripts and proteins related to synaptic function are dramatically differentially regulated during sleep-wake cycles, and phosphorylation states of key proteins involved in plasticity are also altered. Moreover, synaptic tagging and capture are specifically disrupted by sleep deprivation. Perhaps the authors have already considered this factor and appropriately reversed the light-dark cycle of their rat subjects, in which case a clarification in the manuscript would be useful. Nevertheless, I have used this as an example because there is a variety of potential confounds that may explain the difference between SC-CA1 TBS LTP in rats and monkeys, e.g., circadian rhythms, degree of enrichment, natural light vs indoor lighting, diet, degree of inbreeding, strain, etc. Thus, to make strong conclusions about the potential for differences in plasticity rules/mechanisms and how those may contribute to differences in cognition, I think it would be necessary to compare a wider variety of species, including a good representation of each order (e.g., nocturnal rats and diurnal squirrels, new and old world primates) and not just a single exemplar. I understand, of course, that this is really pushing the boundaries of practicality, but I see no other way to make a strong conclusion or to generalise to mechanisms or properties of plasticity in rodents vs primates. Thus, while I believe the manuscript presents really admirable work, I am not sure the findings are at all easy to interpret.

Reviewer #1 (Public review):

Summary:

This article describes a very ambitious metascience project aimed at testing the reproducibility of a corpus of publications conducted in Brazil. The strength of the approach lies in its systematic, multicenter replication design. The authors focus on three commonly used experimental paradigms in biology: the MTT assay, RT-PCR, and the elevated plus maze.

The effort is commendable and reveals a rather low rate of reproducibility, in line with findings from fields considered less reproducible in the life sciences, such as cancer biology.

Strengths:

The study is supported by a substantial dataset, incorporating multiple independent replication attempts and the use of stringent, well-defined protocols, which strengthens confidence in the overall conclusions.

Weaknesses:

(1) Being neither an expert in metascience nor in statistics, I cannot fully judge the methodological aspects of the article or its extensive supplementary material. I will therefore focus my comments on readability. I found the manuscript difficult to digest. The authors should improve readability if they wish to reach a broad audience of experimental biologists. In particular, they should simplify the description of protocols and highlight the key findings more clearly, using accessible language. See specific points below

(2) The article appears to oscillate between:

i) a description of the approach and the inherent challenges of such a multicenter replication program.

ii) an estimation of reproducibility.

These could potentially form two separate articles: one aimed at a broad audience emphasizing key results, and another focused on methodological aspects for a more specific metascience audience. The Results section currently contains redundancies and is difficult to follow for non-experts in statistics. I also find it challenging to extract the main findings.

A possible improvement would be to include an initial section clearly describing the protocol (replication of a single experiment, across several labs, for three types of assays), followed by a concise presentation of the main results regarding reproducibility in Brazilian science with subsections. Methodological details could be moved either to a Supplementary Information or to a more specific article, while being summarized in the Discussion.

(3) This study evaluates the reproducibility of a single experiment from each article, taken out of its broader context. While this provides an estimate of reproducibility, it does not directly contribute to resolving uncertainties within a specific field. This may represent a limitation compared to other reproducibility projects that attempt to replicate multiple key claims within a given study (e.g., in cancer biology or Drosophila immunity). I found that a weakness is that it does play a role in cleaning a field of wrong statements.

(4) The observation that external observers can predict which experiments are likely to be reproducible is interesting and should be more clearly emphasized.

(5) The manuscript frequently refers to future publications. It would be helpful to clarify what is included in the present article versus what is deferred to subsequent papers

Reviewer #2 (Public review):

Summary:

This is an important contribution to science, not only because large-scale replication studies remain rare despite their value, but also because this one focuses on research that was under represented in previous large-scale efforts. The findings reveal concerningly low replicability in this field, pointing to a problem that warrants immediate attention. Particularly noteworthy is the study's sampling strategy: by randomly selecting experiments from a wide range of publications based on methods, rather than filtering by research area, importance, or citation counts, the authors have produced results that are potentially more representative of the broader literature than those of previous large-scale replication projects in this and other fields. Overall, this is a fantastic contribution that I will be recommending and using in all my open science talks, and from which I have learned a great deal. Congratulations to the team!

Strengths:

A study of this scale inevitably requires an enormous amount of work and methodological care, and this one is clearly both robust and thoughtfully designed. I want to particularly acknowledge the considerable efforts the authors have made to ensure the robustness of their findings. The use of multiple approaches to estimate replicability, combined with a substantial battery of sensitivity analyses, including a multiverse approach on top of everything else, clearly reflects the authors' genuine commitment to understanding their results and the limits of their conclusions. The transparency and sharing of all protocols, materials, and challenges and limitations encountered is also outstanding.

Weaknesses:

There were several instances during my reading of the methodology where I felt the authors relied too heavily on the external supplementary materials, at the expense of basic detail in the main manuscript. I appreciate how overwhelming it can feel to integrate more into an already substantial paper, but without some minimum integration, the reading experience and overall comprehension are too often compromised, at times posing more questions than answers. And it is unrealistic to expect most readers to engage with the extensive supplementary materials provided. Please see the comments below for specific suggestions.

Additionally, I found the discussion rather underdeveloped. There is relatively little engagement with the broader literature, not only with replicability studies from other fields, but more generally with relevant meta-research work on publication bias, blinding, risk of bias, citation practices, etc. Some of the most novel and interesting findings in the paper also receive less attention than they deserve, and the discussion at times reads as a repetition of the results section rather than a critical engagement with them. I would encourage the authors to engage more deeply here, as the study clearly has much more to say. Doing so would further highlight why this study is important for the answers it provides and the questions it can spur. Again, please see the comments below for specific suggestions.

Specific suggestions:

Page 1, abstract: "while t values for replications were positively correlated with researcher predictions about replicability, and negatively correlated with the rate of publications by the original article's last author" - I need to address the question: why t values and not effect sizes, p values, or something else? Update after reading the study: although the authors used others, they seem to place more emphasis on t values, which is not well explained. Without a clear explanation, it just left me wonder why, given that effect sizes would, in principle, be more information.

Page 2, paragraph 2: "reproducibility (defined here as reaching the same results when analyzing a set of data)" - In my opinion, this definition is vague enough that it encompasses not only reproducibility (same data, same methods) but also robustness (same data, different methods), and I would therefore recommend providing a more precise definition. The same applies to replicability (different data, same methods), since the definition used does not highlight the importance of using the same methods, and thus also encompasses generalisability (different data, different methods). Explicitly clarifying these distinctions is particularly important as the field grows and the terms become increasingly mixed up and confusing.

Page 2, paragraph 3: "All of these issues raise concerns about the replicability of published results - something that has not been evaluated systematically in the country" - I would suggest providing more information about why those factors may lead to expected lower replicability, ideally with a couple of sentences supported by references. As it stands, less experienced readers may not follow the argumentation and may consider it speculative.

Page 3, paragraph 2: "We then opened a public call for Brazilian labs that could replicate experiments using these methods and models, advertised by email, social media and lectures in conferences and institutions, to which 73 labs initially responded" - Since recruiting is an important component of this study, I would recommend providing additional details so the reader can better assess how comprehensive and unbiased the recruitment process was. AND Page 5, paragraph 2: Please provide more information about this open call: how was it advertised, where, and when? This is needed so that the reader can assess its comprehensiveness and potential biases. Even the link provided is not specific enough to understand the process, as it only states: "Calls were open to participants > 18 years old with current or previous experience in experimental research in any field and were advertised via e-mails, lectures and social media."

Page 3, paragraph 2: "Based on the expertise of respondents and a feasibility analysis by the coordinating team, we selected 3 outcome assessment methods for replication" - Since this choice determined what was ultimately studied and who could participate, I would like to see more information to understand it: was it based on the most common expertise among respondents? How was feasibility defined and estimated?

Page 3, paragraph 3: How was the manual screening performed? Was it done by one or more people? Was there double-screening to ensure reliability of the screening protocol? Did the authors use a specific decision tree or tool? How were conflicts between observers resolved? Were any other validation steps taken to ensure reliability? The same comments apply to the data extraction (who, how many, validation, protocol, etc.).

Page 3, paragraph 3: As a non-expert, I would need more context about the expected average cost of experiments in this field; otherwise, I cannot assess how representative this sample is or whether potential biases may exist (e.g., cheaper experiments perhaps being expected to be less replicable than more expensive ones). Could expected costs also have affected the reduction in geographical coverage eventually observed in this study (Figure S3)?

Page 6, paragraph 2: "(on a scale of 1 to 5)" - Could you clarify whether 1 means no deviations and 5 means everything deviated? Is that how it was phrased to participants? Was there a threshold used by the coordinating team to decide how many deviations were acceptable? (I would briefly clarify all scales mentioned below to allow easier interpretation throughout.)

Page 6, paragraph 4: How were long-text answers (e.g., justifications) reviewed? Was this done manually by one or more members of the coordinating team, or using any text interpretation tool? What steps were taken to ensure the interpretation of these answers was as objective as possible?

Page 8, paragraph 1: "If issues were found, the lab and coordinating team reviewed them via email until the sources of errors were identified and corrected (see https://osf.io/58vsx for details)." - Could you please provide information about how often these disagreements arose and briefly explain their causes? I am struggling to understand why these discrepancies occurred and how frequently. Without more detail, the error rate presented in the next paragraph is a little concerning.

Page 8, paragraph 4: Please provide the version of any package or software used throughout, and make sure to cite R appropriately (R Core Team XXX). In addition, did the authors calculate the log ratio of means (ROM/lnRR) using escalc()? If so, please report this. If not, I would recommend doing so, as escalc() implements recommended small-sample adjustments that produce slightly different values compared to a simple manual calculation of log(mean1/mean2).

Page 10, paragraph 1: "Coefficients of variation from the original study were compared to the mean coefficient of variation of its replications using Wilcoxon's signed rank test" - I wonder how these CVs were calculated - whether simply as SD/mean or using escalc() from the R package metafor, which includes a correction for small-sample size. This may affect the fairness of the comparison, particularly since CVs from original studies are expected to be slightly overestimated given their smaller sample sizes relative to the replications. I also have concerns about using the mean CV of all replications and comparing it to a single CV value, as this ignores the uncertainty around that mean. An additional check could involve calculating the log coefficient of variation ratio (lnCVR; Nakagawa et al. 2015, Methods in Ecology and Evolution; implemented in escalc()) between the original CV and each replication CV, and running a random-effects (or multilevel) meta-analysis that accounts for shared-control non-independence. I believe this would provide a more robust approach, as it does not ignore the uncertainty around the mean CV of the replications - uncertainty that, if neglected, is expected to increase the likelihood of false positive findings. This concern would also apply to the subsequent analysis on absolute means.

Page 10, paragraph 2: The change in geographical distribution shown in Figure S3 appears rather striking, with western states disappearing step by step. Should the reader be concerned about the eventual geographical representability of the sample?

Page 15, Figure 3A: I wonder whether adding 95% CIs calculated from the sampling variance of each ratio would improve interpretation and help readers appreciate the real differences between the dots (i.e., means) - along the lines of a forest plot.

Page 17, section "Predictors of replication success": It is unclear to me how the decision was made about which results from Figure 4 to present in the text. Intuitively, given that correlations were calculated for both t values and lnRR (and other metrics), I would have expected that whenever a result is highlighted in the text, the authors also report how it changes depending on the metric used - for example, the interesting result regarding the 5-year number of publications, whose correlation is notably lower when using lnRR (−0.31 vs. −0.18). Presenting this nuance in the text would reduce the risk of inadvertently giving the impression of cherry-picking.

Page 23, paragraph 1: (this comment should have come during the first % reported, but only in the discussion I realized how important this would be for comparing estimates) I wonder whether the authors should calculate 95% confidence intervals for all their percentages (and those of Errington et al.) using the Wilson method via the function binom.confint() in R, which handles extreme proportions (0% or 100%) more gracefully. This would ensure that uncertainty around these percentages is not neglected and would aid interpretation when comparisons are made. In addition, in the next sentence, the authors are comparing correlation coefficients, at least verbally, these could in principle be transformed into Pearson's r and assigned 95% confidence intervals following meta-analytic workflows, which would better allow us to assess whether these correlations are meaningfully larger or smaller, and help avoid potentially misleading arguments.

Page 24, paragraph 2: The following result is really interesting and I would love for the authors to expand on it a little. There must be other meta-research studies that, despite not studying replicability directly, have explored a similar predictor: "Other features of the original article were generally uncorrelated with replication outcome, although large rates of publications by the last author were associated with lower replicability, suggesting that incentivizing publication volume may be counterproductive for the reliability of results."

Page 25, paragraph 1: I believe the authors could explore if there is evidence for "incorrect labeling of error bars (Cumming et al., 2007; Vaux, 2004)" by plotting log(SD) vs log(mean) across all original studies, and exploring if large outliers (i.e., points largely deviating from the positive regression) exist. That should provide some insights into whether some values reported as SD in the original studies were indeed SE, which I am assuming is what the authors of the study are referring to when they say "incorrect labelling of error bars" here.

Code: I could not engage with the data and code, but I would like to highlight that the organisation and clarity of the GitHub repository is of high quality.

Reviewer #3 (Public review):

Summary:

The authors conducted a large-scale replication effort of lab-based biomedical experiments with an emphasis on the country of origin and who conducted the replication experiments. The authors aimed to understand this context in both the outcomes produced, but also in the approach. Finally, the authors aimed to conduct multi-lab replications to provide richer data from the replications. Overall, the authors find replication rates that are like other large-scale replication efforts in the biomedical space. The authors provide rich detail into the three experimental techniques that were the focus of this effort, potential moderators of replication success, and challenges in conducting replications and coordinating a large-scale crowd-sourced effort.

Strengths:

The paper is outstanding in being transparent and calibrated in how the results are presented. While the authors were challenged by mundane aspects (e.g., difficulty with logistics), unexpected aspects (e.g., COVID pandemic), and very insightful aspects unique to conducting replications (e.g., experimental issues). The authors also provide variation in how they present the results, including confirmatory, multiverse, and exploratory analysis. A unique strength for this study is the rich in-depth insights about the process and interpretation of conducting replications, including predicting replication success in the lab-based biomedical space.

Weaknesses:

The study has weaknesses that the authors acknowledge in their discussion, such as lower number of replications than originally planned that limited the intended effort to compare multiple experiments with multiple attempts against a single original experiment. Another weakness is the limited discussion connecting these findings to the Brazilian research ecosystem.

Reviewer #1 (Public review):

Summary:

The authors used a large dataset evaluating gut carriage of Enterobacterales and ESBL organisms from children aged 6-24 months as the basis for a modeling study to investigate what factors are most important for determining the prevalence of ESBL resistance. The modeling incorporated travel, a simple model of carriage duration (short and long), fitness cost of resistance on transmission and clearance, and antibiotic use. They found that antibiotic use is the primary driver of resistance prevalence, with transmissibility of resistant strains also important for setting the prevalence. Travel, while important when prevalence is very low, plays less of a role in maintaining prevalence once it is established (in keeping with other recent work). They estimated the fitness cost of resistance (terming a reduction of 14% on the rate of transmission and an increase of 23% on the rate of clearance as "low"). While the extent of assumptions and simplifications makes me skeptical of the quantitative conclusions, the qualitative ones seem reasonable and reinforce the long-held principles of the field--reducing antibiotic pressure and interrupting transmission--and highlight the importance of understanding the biological factors that shape the duration of carriage and the likelihood of colonization.

Strengths:

This study incorporates many of the factors that might influence the carriage prevalence of ESBL Enterobacterales. This builds on the work led by this group, both in primary data collection and in theory. Overall, it's such a tough problem that I commend the authors for trying to tackle it. The authors take a thoughtful, rigorous approach, acknowledging simplifications and assumptions where they need to, so as to evaluate the various factors shaping ESBL prevalence.

Weaknesses:

Part of the reason it's such a tough problem is that we have limited data to structure and parameterize a complex model.

(1) The data are not sufficiently described.

The primary data source for this modeling exercise comes from a study of 6-24-month-old children who underwent rectal swabs and evaluation of the carriage prevalence of Enterobacterales, and then whether these Enterobacterales were ESBL; moreover, the study included data on travel and on antibiotic use. Could the authors please direct us to these primary data? Could the authors also justify the parameters in their models from these data--for example, could they please provide the distribution of antibiotic use and the associated timing? Could they also explain why they decided to treat all Enterobacterales as if they were E. coli (line 307)? Is there evidence that all Enterobacterales occupy the same niche and compete with each other?

(2) The model should be more fully described and the limitations explored/explained.

- The authors should point to the code and the ODEs.<br /> - I understand the focus on the pediatric population; the authors argue that this is reasonable because ESBL colonization is similar across age groups. But presumably, antibiotic use differs across age groups, and there is colonization pressure from within households.<br /> - The authors only consider resistance to extended-spectrum beta-lactams and use of beta-lactam antibiotics, but ESBL Enterobacterales are often resistant to other antibiotics as well. How much does the use of other antibiotics also select for Enterbacterales that happen to carry ESBL resistance? "One bug/one drug" modeling, as done here, neglects the complexities of the actual patterns of resistance and range of antibiotic use.<br /> - Do the data support the T3 or S3 compartments, which, if I understand correctly, means no exposure to antibiotics can happen during three months after either treatment or travel? What do the data say about the patterns of antibiotic use? I'd imagine that the likelihood of antibiotic use is not homogenous, but instead, there are some who use repeated rounds of antibiotics.<br /> - Why do the authors exclude individuals who used antibiotics in the prior 7 days? What justifies that cutoff? The authors speculate that the impact of excluding these individuals is likely to be minimal; why exclude them, then? Did the authors evaluate the results if they were included?<br /> - What is the basis of "niche differentiation", as described starting on line 221? Why should clearance of one strain be slower when the strain co-occurs in a host with a strain of another type?

Reviewer #2 (Public review):

Overview:

This study integrates several datasets into a unified modeling framework that incorporates several mechanisms thought to impact the spread of ESBL-resistant bacterial strains. The model accounts for tradeoffs between persistor and colonizer strains, travel rates, antibiotic treatment and strain clearance, direct competitive interactions, and, most importantly, a series of distinct costs associated with the carriage of ESBL resistance. The resulting 75-compartment model is internally consistent and structurally neutral. However, the parameter estimation is flawed in many ways, compromising the interpretations of the model.

On the usage of the Swedish infant data set to estimate colonization and persistence:

First, while other papers have taken similar approaches, the Swedish infant data set is fundamentally inadequate to estimate colonization and persistence rates. This is because very few colonies were typed per sampling event (2 to 6 colonies per event). The original authors themselves argued that strains of indistinguishable morphology would not be able to be differentiated by this method. They also provided data showing that strain identity was not directly related to colony morphology (same strain often displaying distinct morphologies).

The consequence of this is that strains present in low abundance would be missed with a high likelihood. However, if they were to be stochastically sampled, this would count as a "colonization" event, and if they were missed in subsequent samplings, this would count as a "loss" event. In other words, the statistical methods described conflate within-host dynamics (which might lead to distinct within-host abundances) with between-host dynamics (colonization and loss).

Beyond this conceptual issue, some technical aspects aren't particularly sound. The mean of the inferred posterior for the lambda and mu parameters are then used to calculate the beta, gamma, d, and epsilon parameters through a linear regression. The more technically correct way of doing this would be to directly infer these parameters from the data and obtain a full posterior for these parameters.

This highlights another issue: these parameters are passed down to the next statistical model as point estimates, with no associated uncertainty. This artificially inflates the (already low) confidence of the estimates for the cost parameters.

Finally, when this procedure generated parameters that were inconsistent with their expectations (clearance is too high to explain prevalence in France), they adjusted the parameters by discarding and recalculating their beta parameters to artificially enforce neutrality between their strains and enforce the expected prevalence. This is problematic because beta and gamma were jointly estimated, and there is no particular reason why some of them should be discarded. The more natural interpretation would be that parameters inferred from Swedish infants do not translate well to French adults, which should preclude their usage in this context.

On the estimation of costs of ESBL resistance:

The core of the second statistical model is to use prevalence data, travel data, and treatment data in conjunction with the previously inferred colonization and loss parameters to infer the costs of carrying antibiotic resistance. Therefore, the accuracy of this section is contingent on an accurate estimation of the previous parameters. However, these colonization and loss parameters are inherited with no uncertainty (just point estimates are passed down), which, as previously mentioned, generates an artificially precise posterior distribution for the resistance parameters.

However, the most severe issue with the statistics lies in the choice of priors for the cost parameters. All of them are uniform in a positive range that implies a positive cost. Importantly, the average over a positive range will always be positive; therefore, this method will ALWAYS estimate a positive mean for the costs. Note that the posterior distribution of some cost parameters seems to peak around zero and abruptly decays with no mass to the left of zero. This is caused by the choice of prior. Had delta been allowed to be negative (i.e., antibiotic resistance carried a benefit, having the prior be uniform between -1 and 1), the posterior distribution would likely be much more symmetrical, and the confidence interval would have included 0.

Restating, because the prior is a continuous function between 0 and 1, it contains infinitely more mass in the region that represents there being a cost (delta>0) than in the region representing no cost (delta=0). This means that it is a mathematical impossibility for this model to infer the absence of a cost.

Therefore, the main finding of the paper ("We found that resistance is costly") is a mathematical artifact of the prior choice and of the model structure.

Reviewer #3 (Public review):

Cotto and colleagues integrated data analysis with mathematical modeling to examine extended-spectrum beta-lactamase (ESBL)-producing E. coli in France. While ESBL prevalence has risen globally, it has stabilized at approximately 6-8% across Europe. Established risk factors for ESBL carriage include prior antibiotic exposure and travel to high-prevalence regions, most notably South-East Asia. The dataset incorporated information on ESBL-producing E. coli and travel history in young children, and the model was calibrated to ECDC surveillance data on ESBL across Europe, supplemented by literature-derived parameters on antibiotic use, E. coli biology, and transmission dynamics. The authors report that ESBL-carrying strains exhibit a 14% fitness cost in community transmission relative to susceptible bacteria, yet are cleared 23% less frequently. ESBL carriage was strongly associated with factors that prolong gut colonization. Both antibiotic treatment rates and transmission efficiency were identified as key determinants of community-level ESBL prevalence.

Strengths:

The study addresses a clinically and epidemiologically important topic. The integrated modeling approach is methodologically sound and well-suited to disentangling the relative contributions of transmission and antibiotic selection pressure.

Weaknesses:

Several concerns regarding the data used in this study warrant consideration. First, model calibration relied on ECDC surveillance data pooled across multiple European countries, several of which have substantially lower antibiotic consumption than France (ECDC ESAC-Net Annual Epidemiological Report, 2024). Given that antibiotic use is a primary driver of ESBL selection, ESBL prevalence is likely to be heterogeneous across these settings. Calibrating to a geographically diverse dataset risks introducing systematic bias into parameter estimates that may not be representative of the French context. The authors should repeat the analysis using France-specific data, or, where this is not feasible, restrict the calibration dataset to countries with comparable antibiotic consumption profiles. Second, the travel exposure data may be insufficient to adequately capture importation dynamics from South-East Asia, as the cohort consisted exclusively of young children, a demographic less likely to travel to high-prevalence regions than older age groups. This may result in an underestimation of travel-associated importation as a contributor to community ESBL prevalence, and the generalizability of these findings to the broader population should be interpreted with caution.

Reviewer #1 (Public review):

Summary:

In this work, T. Wijerathne et al. investigated and reported the agonistic effect of Yoda1 and Yoda2 over PIEZO2 function using patch clamp electrophysiology, Ca2+ imaging, and molecular dynamics. They find that Yoda1 sensitizes PIEZO2 to membrane tension, can induce Ca2+ influx, and decreases its inactivation to a lesser degree than it does to PIEZO1 channels. Additionally, their data shows that Yoda2 sensitizes PIEZO2 channels to membrane indentation to a greater extent, but it has a weaker effect on channel inactivation than Yoda1. Interestingly, they report that a mutation in a conserved arginine between PIEZO channels can be used to abolish PIEZO1-mediated Ca2+ flux in response to Yoda molecules. As a whole, the results presented here should be put into perspective against previous and future works involving systems where both PIEZO1 and PIEZO2 might be expressed. This is especially true for works where Yoda1 has been used as a basis for determining the absence of PIEZO2.

Strengths:

The authors use multiple techniques to investigate how Yoda molecules affect the three most important biophysical aspects of PIEZO channels that, when changed, result in pathophysiological responses: a) sensitivity to mechanical stimuli, b) Ca2+ entry, and c) channel inactivation. Lastly, they find a specific amino acid/region that could be exploited for drug design and/or development.

Weaknesses:

The methods and discussion sections are lacking enough detail to fully evaluate the findings and put them into perspective, respectively.

Reviewer #2 (Public review):

Summary:

This manuscript challenges the long-standing assumption that Yoda1 and Yoda2 are PIEZO1-selective activators. Using patch-clamp electrophysiology and calcium imaging in HEK293TΔPZ1 cells overexpressing PIEZO2, the authors demonstrate that Yoda1 potentiates PIEZO2 stretch-activated currents to a similar extent as PIEZO1 and slows PIEZO2 poking-current inactivation (albeit with lower efficacy). They further show that the more potent analog Yoda2 affects PIEZO2 at nanomolar concentrations and use mutagenesis and molecular dynamics simulations to propose that Yoda2's benzoic acid group forms a transient salt bridge with R1724 in the putative Yoda binding pocket, explaining its enhanced potency.

Strengths:

The authors are established Piezo/biophysics experts; the study is highly important, technically competent, and carries significant implications for the reinterpretation of prior work that used Yoda compounds as PIEZO1-selective probes.

The core finding that Yoda1 modulates PIEZO2 stretch currents is convincing and important. However, several conceptual, methodological, and presentational issues need to be addressed before acceptance, as detailed below.

Weaknesses:

(1) The abstract states that Yoda1 potentiates PIEZO2 "as efficaciously as PIEZO1." This claim is accurate only for stretch currents and single-channel open probability, but the paper itself demonstrates important asymmetries: i) Yoda molecules slow PIEZO2 poking-current inactivation ~2-fold, versus ~5-10 fold for PIEZO1 (Figure 3b and ref #60). ii) Spontaneous Ca²⁺ entry via PIEZO2 requires non-physiological conditions (high extracellular Ca²⁺, hypertonic solutions) that are unlikely to occur in native cells.

The abstract should be revised to clearly qualify where equivalence holds and where efficacy differences exist. IMO, the current wording risks overcorrecting the historical bias (PIEZO1-only) by going too far in the other direction.

(2) Related concern: the PIEZO2 Ca²⁺ signal in Figure 2 is only detectable using a Ca²⁺-boosted solution (CBS ie 30 mM Ca²⁺). Physiological extracellular Ca²⁺ and cells normally do not experience sustained hypertonicity at these magnitudes. The authors should explicitly clarify that the practical implication of their findings is primarily for electrophysiological (patch-clamp) experiments and that the Ca²⁺ imaging caveat applies only under amplified conditions. Specifically, the authors should state that in standard Ca²⁺ imaging assays with physiological buffers, PIEZO2 is unlikely to confound Yoda1 results.

Related point: Can cytochalasin D (CytoD) restore a Yoda1-dependent Ca²⁺ signal in physiological saline? This would help determine whether the weak PIEZO2 response is primarily a membrane tension issue (cytoskeletal tethering) versus intrinsically lower channel expression or permeability. The authors already have tagged PIEZO1/2 constructs and could, in principle, normalize by surface expression.

(3) The mean inactivation tau values for wild-type PIEZO2 poking currents in both DMSO and Yoda1 conditions (Figure 3b, approximately 15-40 ms range) appear substantially higher than values reported in published literature (typically 5-10 ms; eg, PMID: 20813920). This discrepancy needs to be addressed.

(4) The authors perform all MD simulations on a truncated PIEZO1 model and justify this choice by noting that the Yoda binding region is highly conserved between homologs. This is a reasonable and defensible starting point given the availability of well-validated PIEZO1 simulation set ups in their lab. A few points are nonetheless worth addressing: While PIEZO2 simulations are not strictly required, the authors are encouraged to briefly discuss whether any long-range structural differences between PIEZO1 and PIEZO2 (outside the binding site itself) could influence Yoda2 binding dynamics, particularly in light of the chimera data showing that PIEZO2 sequence in repeat A abolishes Yoda1 sensitivity. This reviewer still doesn't understand the reason behind this discrepancy despite it being acknowledged in the text.

Another MD-related comment is that three simulation replicas (which is impressive for such a big system) show markedly different salt bridge occupancy (82.6%, 49.7%, 99.8%; stated in the text). This wide variation suggests incomplete sampling in at least one replica. The authors should provide RMSD plots for ligand and protein backbone to assess convergence and possibly discuss whether the 49.7% replica represents a genuinely distinct binding mode or incomplete equilibration.

(5) The Discussion proposes that PIEZO2's weaker Ca²⁺ response to Yoda1 could partly reflect lower membrane expression. Since the authors already have fluorescently tagged PIEZO1 and 2 constructs, a simple fluorescence intensity comparison between the two (acknowledging it would reflect total rather than surface expression) could provide at least indirect support for this claim. Alternatively, if such a comparison is not feasible, the authors may consider removing membrane expression from the list of proposed explanations or explicitly acknowledging that this remains unsubstantiated speculation. The max poking currents may somewhat and roughly indicate the level expression difference too, if done exactly side by side.

(6) The abstract or concluding remarks should highlight that Dooku1 is not PIEZO1-selective in its agonist-like action on PIEZO2, and that Cmpd15/Cmpd64 appear to be better PIEZO1-selective tools. This nuance is buried in the Results section.

(7) The authors should not cite PMID 31015490. Clearly, any work on MCC13 is confounded by the overwhelming expression of PIEZO1 (PMID: 42084270). Instead, the authors should also cite the literature from others who have clearly recorded stretch currents from PIEZO2 before the cited studies (eg, PMID: 37590348).

Reviewer #3 (Public review):

Summary:

The manuscript reports that Yoda1 and Yoda2 agonize PIEZO2 in a manner similar to PIEZO1, increasing open probability and stretch sensitivity, but the mechanism underlying this sensitivity is incomplete. Mutagenesis was shown exclusively in PIEZO1, with no corresponding mutagenesis in PIEZO2, so the proposed mechanism in PIEZO2 is inferred by homology rather than directly tested. All experiments use mouse PIEZO2, and the human ortholog should be used before generalizing the proposed reinterpretation of the field.

Strengths:

The pressure-clamp electrophysiology demonstrating a shift in half-activation pressure for PIEZO2 is compelling evidence in support of the central claim.

Weaknesses:

(1) In the single-channel recordings (Figure 1a), it's unclear how many channels were present in those patches. After applying -60 mmHg pressure, multiple channels would be activated (as seen in Figure 1e). The number of channels in the patch and their inactivation rate could significantly influence the open probability in such experiments. To overcome this, in the original Yoda1 article (Syeda, Ruhma, et al. eLife 2015), no additional pressure was used. Additionally, the reported open probability comparison (n=7 Yoda1 vs n=17 DMSO patches) has an SEM nearly as large as the effect itself (0.30 {plus minus} 0.11), consistent with a small number of outliers driving this. The underlying mean open and shut times are reported without any statistical test; only the derived open probability receives a p-value. Additionally, in Figure 1a, the Yoda1 condition noise is different from the control. This should be stated if noise filtering was applied and how, given that this could affect open probability analysis.

(2) The calcium imaging data in Figure 2 raise significant concerns regarding the chemical activation claim. The calcium-boosted solution (30 mM Ca2+) is not physiological and appears to be generally stressing cells rather than specifically activating PIEZO2: the control condition under CBS already shows an elevated signal, consistent with cells being unwell at this calcium concentration, and adding Yoda1 on top of this shifted baseline raises further questions about specificity rather than confirming it. Separately, it is unclear why DMSO alone produces measurable PIEZO2-associated calcium influx in HBSS, a result that is not addressed in the text. Figure 2 should clearly indicate when DMSO/Yoda1 perfusion was initiated, and y-axis labels are missing from panels A and B.

(3) In the poke experiments, an activation threshold should be calculated and reported, and amplitude data (e.g., peak current versus indentation depth) should be shown rather than only inactivation tau values. It is also unclear why mClover3- and N-GFP-tagged constructs were used in these experiments, since electrophysiological recording already confirms channel expression without requiring a fluorescent tag.

(4) For inactivation kinetics (Figure 3b), the authors use unpaired comparisons across separate cells, whereas the deactivation experiments (Figure 3c) use paired; it should be applied to the inactivation experiments as well. Deactivation kinetics for PIEZO2 itself should be shown. If the claim is that Yoda1 acts on PIEZO2 through the same mechanism proposed for PIEZO1, then a PIEZO1/2 chimera should be expected to show a corresponding effect on deactivation tau; instead, this chimera is reported as completely Yoda1-insensitive despite both parental channels being Yoda1-sensitive, as shown in this study.

(5) Given that this reflects a different experimental paradigm for Yoda EC50, PIEZO1 should be included within Figure 4b. Additionally, EC50 bar plots should be present on this figure. The inactivation time constant for PIEZO2 without Yoda1 is inconsistent across figures, below 20 ms in Figure 3b but above 20 ms in Figure 4c.

(6) Finally, the modeling is performed exclusively on PIEZO1, whereas the manuscript's central focus is PIEZO2. It is therefore unclear whether the proposed structural mechanism, including the basis for Yoda2's reduced efficacy on PIEZO2, can be directly extrapolated to PIEZO2.

Reviewer #1 (Public review):

Summary:

In this study, the authors describe an early diverging vertebrate KCNE gene present in jawless lampreys that they denote KCNE0.

Three forms of the protein are isolated from different lampreys, which have 95% homology to each other, but only moderate homology to KCNE1-6.

Co-expression with lamprey KCNQ1 produced a non-inactivating current, whereas co-expression with mammalian KCNQ1 resulted in less modulation. Introduction of a tetra-leucine motif from KCNE4 into KCNE0 reduced current on co-expression with KCNQ1, conferring an inhibitory effect.

Strengths:

This is an interesting and uncontroversial report of a new KCNE isoform from lower vertebrates that gives insight into the evolutionary progression of the sequence and functional properties of the accessory protein.

Weaknesses:

(1) No error bars visible for lamprey Q1 isoforms (open symbols) in Figure 2G. No statistical comparison was provided to indicate whether lamprey Q1 isoform V1/2s are significantly different (nor in Supplementary Table 1).

(2) There is the same issue in Figures 3 and 4. No appropriate statistical comparison is made between V1/2s for different truncations of PmKCNE0 (Figure 3), or between KCNQ1 species isoforms with and without PmE0.

Reviewer #2 (Public review):

Summary:

This study functionally characterizes a single KCNE-like gene, kcne0, from a jawless vertebrate. The authors conducted multiple experiments, including TEVC, VCF, RT-PCR, and RNA-seq to show that KCNQ1 and kcne0 exhibited a broadly overlapping organ distribution in lamprey species, and KCNE0 produced a constitutively active current when co-expressed with lamprey KCNQ1, similar to the effects of human KCNE3 on KCNQ1. This modulation was species-specific, as co-expression of KCNE0 with other species' KCNQ1 was less effective. Moreover, the authors found that truncating the N-terminal had a more significant reduction of the modulatory effects than truncating the C-terminal of KCNE0. Interestingly, the introduction of the tetra-leucine motif from human KCNE4 into KCNE0 conferred KCNE0 with comparable effects of human KCNE4 on KCNQ1.

Strengths:

The authors clearly introduced an early-diverging member of the KCNE family, and convincingly demonstrated the function of this gene, KCNE0. The results are supported by experiments of multiple approaches and are clearly written. The work is significant and will interest readers from the extended research area.

Weaknesses:

No major concerns were identified with the manuscript in general.

Reviewer #1 (Public Review):

The manuscript by Boudjema et al. describes the cellular events underlying centriole amplification and apical migration to allow the assembly of hundreds of motile cilia in multi-ciliated cells. For this, they use cell culture models in combination with fixed and live cell imaging using antibody staining and fluorescence from endogenously tagged centriole and deuterostome markers, respectively. The work is largely descriptive and functional analyses are restricted to treatment with the microtubule depolymerizing drug nocodazole. The imaging is state-of-the-art including confocal microscopy, live imaging with optical sectioning and high optical and temporal resolution, as well as super-resolution imaging by ultra-expansion microscopy.

The study does a good job of providing a very detailed description of the dynamics of centrioles and deuterostomes that lead to centriole amplification and apical migration in multiciliated cells. This detailed view was missing in previous work. It also reveals the involvement of microtubules at multiple steps: the formation of a cloud of deuterostome precursors, the nuclear envelope tethering of newly formed centrioles, their separation, and their migration to the apical surface.

It would have been useful to expand the analysis of the role of microtubules by including analyses of the requirement for specific microtubule motors, for a better understanding and additional evidence that microtubule-based transport is involved. A weak point is that there is no visualization of microtubules together with deuterosomes and centrioles at the different steps of centriole amplification and migration, to directly address how these structures may interact with and move along microtubules.

Overall, apart from experimental aspects and since this is largely a descriptive study, the manuscript would benefit from more precise language and a better description of the complex events underlying centriole amplification and movements.

Comments on revised version.

The authors have significantly improved the manuscript, by refocusing it, introducing text and figure changes, and by adding new data including functional analyses. The revised version now has convincing data that support the claims. All my remaining concerns have been addressed.

Reviewer #3 (Public review):

Summary:

In this manuscript, Boudjerna and Balagé et al. aim to elucidate the spatial origin of centriole amplification and the mechanisms behind the formation of an apical basal body patch in multiciliated cells (MCCs). To this end, they focused on the role of microtubules and developed new tools for spatiotemporal and high-resolution analysis of different stages of centriole amplification, including the centrosome stages, A-stage, G-stage, MCC-stage. Among these tools, the MEF-MCC cells grown on micropatterns stands out for its versatility as it is not tissue-specific and does not require epithelial cell-to-cell contact for differentiation. Additionally, the Cen2-GFP; mRuby-Deup1 knock-in mouse model was used to study different stages of centriole amplification in physiological brain MCCs. This model offers an advantage over the previously described Cen2-GFP model by enabling the resolution of early events in centriole amplification through the visualization of Deup1-positive structures and their dynamics. Finally, the authors leveraged powerful imaging techniques, including super-resolution microscopy, the U-ExM and high-resolution live cell imaging in order to detect and track centriole amplification, elongation, disengagement, and migration.

By combining the MEF-MCC and knock-in mouse model with spatiotemporal imaging in control and nocodazole-treated cells(treated acutely or chronically), the authors define the sequence of events during centriole amplification, revealing the critical roles of microtubules for the first time. Initially, the centrosome-mediated microtubule network forms, organizing a pericentrosomal nest from which procentrioles and deuterosomes emerge. Their findings indicate the importance of microtubules in recruiting and maintaining pericentriolar material clouds that contain DEUP1, PCNT, SAS6, PLK1, PLK4, and tubulins. Following the amplification stage, the procentrioles mature, leading to cells displaying numerous MTOCs, as demonstrated by regrowth experiments. Mature centrioles then disengage from deuterosomes, attach to the nuclear envelope, and migrate to the apical surface facilitated by microtubules.

Strengths:

The manuscript provides new insights into the regulatory function of microtubules and microtubule-based transport in different stages of differentiation in brain MCCs. Addressing the role of microtubules during different stages of centriole amplification required development of new tools to study brain MCCs, which will be useful in future studies of MCCs. A notable strength of this manuscript is the authors' thorough and quantitative spatiotemporal analysis of highly dynamic processes in MCCs. The precision and detail in describing these dynamic events are impressive and are further strengthened in the revised version through additional analysis and adoption of new methods. This comprehensive analysis advances our understanding of MCC biology regarding the involvement of microtubules.

Comments on revised version.

The revised manuscript is substantially improved, and given the scope, it is appropriate that it primarily establishes a detailed spatiotemporal framework. That said, a few points would further strengthen clarity and impact. First, several observations naturally raise follow-up mechanistic questions, for example whether additional cytoskeletal systems such as actin contribute to steps like centriole apical migration. A slightly more detailed framing of these open questions would help guide future work. Second, some terminology introduced to label observed microtubule-based structures (for example "nest") may not be essential. Finally, while the authors have increased quantification, some analyses would benefit from super plot-style displays with replicate-level comparisons, particularly for intensity-based readouts.

Reviewer #1 (Public review):

This work convincingly shows that, rather than gradually "evolving" throughout interphase, global chromatin architecture undergoes unexpectedly sharp remodeling at G1-S (and to a lesser extent, S-G2) transitions. By applying "standard" Hi-C analyses on carefully sorted cells, the authors provide an excellent temporal view of how global chromatin architecture is changed throughout the cell cycle. They show a surprisingly abrupt increase in compartmentation strength (particularly interactions between the "active" A compartments) at G1-S transition, which is slightly weakened at S-G2 transition. Follow-up experiments show convincingly that the compartment "maturation" does not require the DNA synthesis accompanying S phase per se, but the authors have not identified the responsible factors (work for future publications). The possible biological ramifications of these architectural changes (setting up potential replication "factories", and/or facilitating transcription-replication conflict resolution, both more pertinent for the active A compartments, which are most affected) have been well discussed in the article, but still remain speculative at this stage.

My major criticism of this article is aimed more at the state of the field in general, rather than this specific article, but it should be discussed to give a more balanced view: what actually is a chromatin compartment? Chromosomal tracing and live tracking experiments have shown that the majority of "structures" identified from Hi-C experiments are statistical phenomena, with even "strong" interactions only being infrequent and transient. A-B compartments are "built up" from multiple very low-frequency "interactions", so ascribing causal effects for genome functions is even tougher. As a result, I have very little confidence in the results of the authors' polymer simulations and their inferred "peninsula" A compartment structures without any other supporting experimental data.

Comments on revised version.

The authors have included orthogonal DNA FISH evidence to support their claims which greatly strengthens the manuscript. Their further precisions within the discussion have answered all of my previous concerns with the manuscript.

Reviewer #2 (Public review):

Summary:

This manuscript by Choubani et al presents a technically strong analysis of A/B compartment dynamics across interphase using cell-cycle-resolved Hi-C. By combining the elegant Fucci-based staging system with in situ Hi-C, the authors achieve unusually fine temporal resolution across G1, S, and G2, particularly within the short G1 phase of mESCs. The central finding that A/B compartment strength increases abruptly at the G1/S transition, stabilizes during S phase, and subsequently weakens toward G2 challenges the prevailing view that compartmentalization strengthens monotonically throughout interphase. The authors further propose that this "compartment maturation" is triggered by S-phase entry but occurs independently of active DNA synthesis, and that it involves a consolidation and large-scale reorganization of A-compartment domains.

Strengths:

Overall, this is a thoughtfully executed study that will be of broad interest to the 3D genome community. The data are of high quality, and the analyses are extensive, albeit not completely novel. In particular, previous work (Nagano et al 2017 and Zhang et al 2019) has shown that compartments are re-established after mitosis and strengthened during early interphase, and single-cell Hi-C studies have reported changes in compartment association across S phase. In particular, Nagano et al show that DNA replication correlates with a build-up of compartments, similar to what is presented here, with the authors' conclusion that compartment strength peaks in early S. The idea that it weakens toward G2, rather than continuing to strengthen, appears to be novel and differs from the prevailing framing in the literature.

Comments on revised version.

The authors have responded constructively to my major conceptual concerns. The distinction between DNA synthesis and replication initiation has been clarified appropriately. The additional insulation analysis substantially strengthens the argument that compartment maturation is not simply a consequence of changing loop extrusion dynamics, although I would encourage slightly more cautious wording regarding "independence" from cohesin-mediated extrusion. The peninsula model is now framed appropriately as a heuristic interpretation and supported by orthogonal imaging data. Finally, the discussion of conservation across cell types has been appropriately tempered. Overall, I believe the manuscript has been significantly improved.

Reviewer #1 (Public review):

Summary:

The manuscript by Lu and colleagues demonstrate convincingly that PRRT2 interacts with brain voltage-gated sodium channels to enhance slow inactivation in vitro and in vivo. The work is interesting and rigorously conducted. The relevance to normal physiology and disease pathophysiology (e.g., PRRT2-related genetic neurodevelopmental disorders) seems high. Some simple additional experiments could elevate the impact and make the study more complete.

Strengths:

Experiments are conducted rigorously including experimenter blinding and appropriate controls. Data presentation is excellent and logical. The paper is well written for a general scientific audience.

Comments on revised version.

The manuscript by Lu and colleagues has been revised sufficiently to address all my prior concerns.

Experiments are conducted rigorously including experimenter blinding and appropriate controls. Data presentation is excellent and logical. The paper is well written for a general scientific audience.

Reviewer #2 (Public review):

Summary:

As a member of DspB subfamily, PRRT2 is predominantly expressed in CNS and has been associated with various paroxysmal neurological disorders. Previous studies have shown that PRRT2 interacts with Nav and Cav channels, modulating channel properties and neuronal excitability.

In this manuscript, Lu et al. demonstrate that PRRT2 is a potent regulator of Nav channel slow inactivation, promoting the development of Nav slow inactivation and impeding the recovery from slow inactivation. This effect is highly conserved in PRRT2s across species as well as among DspB family members (TRARG1 and TMEM233). The authors further confirmed the interaction between Nav channels and PRRT2 in heterologous expression systems as well as in Prrt2-V5 knock-in mice. Prrt2-mutant mice, which lack PRRT2 expression, require lower stimulation thresholds for evoking after-discharges when compared with WT mice.

Overall, this is a well-executed and methodologically comprehensive study. This work offers valuable insight into the physiological functions of PRRT2 and reveals a potential pathogenic mechanism underlying PRRT2-associated neurological disorders.

The revised manuscript has addressed most of the concerns raised by the reviewers and has been substantially strengthened, although I still have several concerns regarding the discussion section.

Strengths:

(1) Overall, this is a well-executed and methodologically comprehensive study. The electrophysiological data strongly support the conclusion that PRRT2 is a potent regulator of Nav channel slow inactivation. The observation that this regulation is conserved in PRRT2 across species and among DspB family members raises the possibility that altered regulation of Nav channels may also contribute to the pathogenesis of TRARG1- or TMEM233-associated disorders.

(2) Co-immunoprecipitation assay performed using brain tissue from genetically modified Prrt2-V5 knock-in mice provides convincing in vivo evidence for the interaction between PRRT2 and Nav1.2 channels.

(3) Prrt2-V5 KI mice show markedly reduced PRRT2 protein expression and display phenotypes similar to those observed in Prrt2-mutant mice, supporting an important role of PRRT2 in regulating neuronal and network excitability.

Weaknesses:

(1) Nav1.6 is also highly expressed in cortical neurons and is widely regarded as a major contributor to action potential initiation and sustained high-frequency firing. Given that PRRT2 similarly regulates the fast and slow inactivation of Nav1.6 and Nav1.2 channels, the potential contribution of Nav1.6 regulation to neuronal and network excitability should be discussed.

(2) Slow inactivation is generally considered to develop over timescales ranging from hundreds of milliseconds to seconds or longer. Therefore, the statement in Discussion (Page 13, line 381-382) that "slow inactivation develops on a timescale of tens of milliseconds to seconds" may not accurately reflect the conventional kinetic definition of slow inactivation and should be clarified.

(3) Page 14, line 417-430: "question about how Nav channel slow inactivation is regulated in cells that do not express PRRT2".<br /> PRRT2 is unlikely to be the sole regulator of Nav channel slow inactivation. Other molecules and signaling pathways may regulate Nav channel and contribute to neuronal excitability. In addition, neuronal excitability can also be regulated through modulating other Nav properties, such as long-term inactivation or slow recovery from inactivation, as well as through modulating the activity of other ion channels, for example, Kv7.2 and Kv7.3 channels. Therefore, PRRT2-negative cells may utilize alternative mechanisms to fine-tune neuronal excitability. In its current form, this paragraph somewhat overstates the role of PRRT2 and would benefit from a more balanced discussion.

(4) Page 50, Figure 7-figure supplement 2: It would be helpful to include representative traces of the 1st and the last (20th) compound APs in panels B and C.

Reviewer #3 (Public review):

This paper reveals that the neuronal protein PRRT2, previously known for its association with paroxysmal dyskinesia and infantile seizures, modulates the slow inactivation of voltage-gated sodium ion (Nav) channels, a gating process that limits excitability during prolonged activity. Using electrophysiology, molecular biology, and mouse models, the authors show that PRRT2 accelerates entry of Nav channels into the slow-inactivated state and slows their recovery, effectively dampening excessive excitability. The effect seems evolutionarily conserved, requires the C-terminal region of PRRT2, and is recapitulated in cortical neurons, where PRRT2 deficiency leads to hyper-responsiveness and reduced cortical resilience in vivo. These findings extend the functional repertoire of PRRT2, identifying it as a physiological brake on neuronal excitability. The work provides a mechanistic link between PRRT2 mutations and episodic neurological phenotypes.

Comments:

(1) The precise structural interface and the molecular basis of gating modulation remain inferred rather than demonstrated.

(2) The in vivo phenotype reflects a complex circuit outcome and does not isolate slow-inactivation defects per se.

(3) Expression of PRRT2 in muscle or heart is low, so the cross-isoform claims are likely of limited physiological significance.

(4) The mechanistic separation between trafficking of PRRT2 and its gating effects is not clearly resolved.

(5) Additional studies with Nav1.6 should be carried out.

Comments on revised version.

These comments have been addressed in the revised version.

Reviewer #1 (Public review):

Summary:

This study offers a careful and technically strong look at how surface stickiness changes whisker-surface interactions and how that information reaches peripheral sensory neurons. The authors use 3D whisker tracking to capture bending, twisting, rolling, and tip motion during contact with surfaces that differ in stickiness, coarseness, and position. They show that sticky surfaces, especially silicone, broaden the range of whisker deformation, produce stronger but less frequent stick-slip events, and change firing rates in some trigeminal ganglion neurons. Overall, the study is valuable because it goes beyond standard 2D tracking and shows that out-of-plane motion and roll are important for understanding how whiskers encode texture.

Strengths:

The study is technically strong and well motivated. Its main strength is the use of 3D whisker tracking to show that surface stickiness affects whisker deformation in ways that standard 2D tracking would miss, including torsion, roll, out-of-plane motion, and stick-slip dynamics. The authors also connect these mechanical effects to TG activity, providing evidence that stickiness information is available in peripheral sensory responses. Overall, the work expands the study of whisker-based texture sensing beyond coarseness and provides a richer biomechanical framework for understanding tactile encoding.

Weaknesses:

The main weakness is that stickiness is not formally defined early in the manuscript, even though it is the central experimental variable. Several methodological choices also need clearer justification or validation, including the use of 2D measures as comparators for torsion and roll, the thresholds used for stick-slip detection, the degree-5 polynomial fit, the reference ROI, and aspects of the 3D surface reconstruction. The neural evidence should also be interpreted cautiously because the TG sample is small, only a subset of units discriminated silicone, and the correlation between strain sensitivity and silicone discrimination is suggestive rather than definitive.

Reviewer #2 (Public review):

The authors explore the sensation of stickiness from the point of view of whisker exploration and encoding in the trigeminal ganglion. In doing so, they develop methods for 3D whisker tracking to describe stick-specific parameters such as stick-slip rates and strain. Overall, the methods are strong, and the authors present the results appropriately. Overall, I think exploration of the sensation of stickiness is a great question.

My main criticism is in relation to the chosen stimuli, and I wonder whether the authors may have room to explore more naturally sticky materials and what this may mean for the animal.

(1) Chosen stimuli for stickiness:

Four different materials are used, with the aim of presenting animals with graded measures of stickiness. The results show that silicone stands out against the others; it's less clear whether the intermediate textures (Delrin and resin) may be truly intermediate in stickiness.

I wonder if the stimuli chosen were truly representative of the aim of providing a gradient of stickiness. Did the materials differ in other features, such as surface temperature, texture, etc., which could explain some results? The authors discuss this in terms of coefficients of friction and how these estimates are not quantified in relation to whiskers themselves.

Measures of stick-slip and strain with silicone vs other materials make intuitive sense. Could the authors add additional naturally sticky stimuli to exemplify the results? For example, adhesive, glue, or a sugary substance.

(2) Tracking methods and quantification:

The 3D tracking methods, which incorporate whisker twists, strain, and other fine features of whisker exploration, present an advance in terms of analysis of how whiskers may explore more complex, natural features of environments. The analyses and quantifications are all solid and robust. The technical approaches are well-prepared to take the work a step further in terms of stimulus choice.

(3) Peripheral coding of stickiness:

The authors report that some units respond preferentially to whisking on silicone and that this has to do with strain on the whisker. Is there a possibility to understand the nature or anatomy of these units and why they might be preferential for the sticky sensation? Can the location in the follicle be assigned? And/or would the methodology allow for assignment of where the specifically sticky-tuned units project centrally?

(4) Relationship to natural stimuli:

A piece missing from the paper is more discussion and exploration of why stickiness may be important for sensory coding, as well as potentially more naturally sticky stimuli. One could imagine that a mouse navigating the world could find stickiness attractive, if it were a source of sweet food, for example, or it could potentially be a sensation the animal prefers to avoid. Stickiness could also indicate contamination or a sticky trap, to be avoided. If the authors are able to add naturally sticky stimuli, the whisker exploration and encoding could potentially provide further cues towards the valence of stickiness for mice.

Reviewer #3 (Public review):

This paper tackles an underexplored dimension of whisker-based texture sensing: while surface coarseness encoding has been extensively characterized in rodents, the mechanical and neural basis for stickiness sensing has not previously been examined. The authors make two intertwined contributions that together represent a substantial advance: a methodological one - a 3D whisker tracking pipeline operating at 4000 fps, capable of capturing torsion, roll, and out-of-plane whisker motion - and a scientific one - a first characterization of how whisker mechanics and primary trigeminal afferent responses differ between surfaces of high and low stickiness. The work is technically solid, the dataset is large, and the question is well motivated both by the multidimensional nature of tactile texture perception and by the practical advantages of the whisker system for studying touch mechanics.

Strengths.:

The 3D tracking system is a timely advance over existing tools, particularly in its handling of non-planar whisker shapes and the full automation required for the sub-millisecond resolution needed to detect stick-slip events. The mechanical dataset is extensive. The finding that whisking against silicone expands the sampled whisker strain space and produces stronger but less frequent stick-slip events is clearly demonstrated and internally consistent with the proposed mechanism of greater strain accumulation before frictional release - a physically intuitive result. The open release of the tracking code considerably increases the value of this work to the broader community.

Weaknesses:

A few aspects of the paper, if sharpened, would considerably strengthen the evidence and the clarity of the conclusions.

The central claim - that "stickiness information is available to the whisker system" - does not capture the precision of what the paper demonstrates. As stated, the finding is close to guaranteed: any variation in surface friction will produce some change in whisker mechanics, so the presence of mechanical differences between materials is expected rather than surprising. The more valuable question the paper is well positioned to answer is which specific dimensions of the whisker mechanical response are most informative about surface stickiness. The paper reports effects on strain distribution breadth, stick-slip amplitude, and stick-slip rate, but does not synthesize which of these - or which sub-dimensions (bending, twisting, or rolling) - carry the most discriminating information. Identifying the salient dimensions of the mechanical response and relating them to the proposed frictional mechanism would sharpen the paper's conclusions substantially.

A related but distinct limitation is the absence of direct force measurements during whisker-surface contact. The authors acknowledge this openly, and I recognize it is not easily remedied within the current experimental setup. It does, however, constrain interpretation: without knowing the actual forces generated at the whisker-surface interface, the assumed stickiness ordering of the tested materials cannot be validated, and - importantly - the relative contribution of surface friction and material compliance to the observed mechanical differences cannot be determined. This is an important direction for future work in this area.

The paper argues carefully that 2D tracking is insufficient for capturing the full mechanical picture of whisker-surface interactions, and the figure currently in the supplementary material (Figure S2) makes this case convincingly through multiple analyses. This argument is the core justification for the paper's methodological contribution and deserves a place in the main manuscript. Furthermore, while the mechanical case for 3D over 2D tracking is well made, it has not yet been tested at the neural level: the regression model used to predict neural firing incorporates 3D variables, but its performance is not compared against an equivalent model restricted to 2D variables. Such a comparison would directly demonstrate whether torsion and roll - the signals inaccessible to 2D tracking - carry neural predictive value, and would elegantly unite the paper's methodological and scientific contributions.

Finally, the three-dimensional plots in Figure 3 are the paper's primary representation of its main mechanical result, and there is a real opportunity to make them considerably more informative. The whisker deformation probability distributions (panel B) are rendered in 3D from a single viewing angle, making it difficult to assess the shape or anisotropy of the distributions - and in particular to see which dimensions expand most for silicone relative to the other materials. This is precisely the information needed to identify the most salient dimensions of the stickiness signal, and two-dimensional representations would make it directly readable.

Reviewer #1 (Public review):

Summary:

Using Mendelian randomisation on available GWAS data, the investigators identified eGenes associated with prostate cancer and applied the data to define relevant immune cell types involved. Additional analysis was performed to explore potential candidate targets and agents from licensed medicines.

This is an interesting approach as the investigators have expertise in other research fields, applied here to prostate cancers. The use of three different datasets is significant, and the approach to further analyse implicated eGenes in drug target analysis is relevant and timely.

A particular strength is taking putative genes from Mendelian randomisation analysis to target and potential drug agents.

Some aspects of the study would need to be clarified to enable interpretation of the findings in the context of the prostate gland and prostate cancers: expanding the descriptions of the supporting Supplementary Data and Tables, explanations of the analysis for the general reader, and clarification of the selection of eGenes (Figure 5).

Reviewer #2 (Public review):

Summary:

This study integrates bulk and single-cell transcriptomic-derived eQTLs from two separate consortia (PRACTICAL and Finngen) to identify immune-cell-specific therapeutic targets in prostate cancer. Mendelian randomization and Bayesian colocalization have been used to produce druggable eGene modules through STRING and DrugBank.

This is an interesting study that is attempting to address risk-associated, immune-specific transcriptomic repertoires in prostate cancer. It is knitting together concepts of drug repurposing and prostate cancer immunogenicity. This is an entirely computational study, which would benefit from some wet lab experimental validation.

It is very tricky to attribute cell-type-specific responses, especially when the majority of genes involved represent cytoskeletal or stress responses, which are ubiquitous throughout the prostate microenvironment. This point is relevant for the drug repurposing section: if these drugs are targeting immune cell-specific repertoires, what would the response be of the entire environment? It would be useful to contextualize the validity of each proposed therapy in a specific prostate cancer context and the involvement of AR antagonism or radiotherapy.

Strengths and limitations of this study:

Strengths:

This is a scientifically interesting and potentially impactful study, particularly in its attempt to integrate immune-cell-specific transcriptomics, causal inference, and drug repurposing in prostate cancer. The methodology is well described, and the data (albeit limited) are well analyzed.

Limitations:

The central weakness is the overstatement of the conclusions regarding immune-cell-specific causality, without sufficiently contextualizing the biological meaning of the findings.

Highlighted genes, such as LMNA, XBP1, histone-related genes, and stress-response markers, are ubiquitous regulators involved in fundamental cellular processes, including ageing, unfolded protein response (UPR), integrated stress response (ISR), chromatin remodeling, proliferation, and metabolism. It is unclear whether these signatures truly represent immune mechanisms, or instead reflect broader inflammatory and age-associated biology expected within an ageing glandular organ such as the prostate.

Immune cell identity alone may not be sufficient to infer biological relevance because immune state characterization (e.g., exhausted versus functional T cells, or distinct macrophage/myeloid phenotypes) is largely absent from the current analysis. The assertion that specific immune populations are correlated with prostate cancer susceptibility is probably an overstatement unless the nature of these cells can also be characterized.

The interpretation of "causal variants" is not always specified, i.e., what phenotype is being associated: prostate cancer susceptibility, recurrence, progression, or treatment response (e.g. is there direct causality from immune-cell variants to prostate cancer?).

Overall, there is a need for stronger biological and translational contextualization: how do the identified pathways relate to ageing-associated inflammation, PIN, microbiome-driven inflammatory changes, and stress-response biology in the prostate gland? While the manuscript identifies network hubs and enriched pathways, it often stops short of explaining what these modules biologically represent or how they may influence prostate cancer development, progression, treatment resistance, or immune evasion.

There are additional publicly available spatial transcriptomic or single-cell datasets which could be used to validate whether the purported immune-cell-specific genes are genuinely enriched in immune populations adjacent to tumour cells. In the drug repurposing analyses, the current study does not explicitly handle prostate cancer subtypes such as HSPC, CRPC, NEPC, or DNPC and co-treatment with androgen receptor antagonism or radiotherapy.

Reviewer #1 (Public review):

Summary:

The manuscript- "Cell cycle-dependent variation in endocytosis drives phenotypic diversity in M. tuberculosis" by Subhash et al. demonstrates how host cell heterogeneity shapes intracellular pathogen phenotypes. The central and novel finding of this study (G2-phase cells have higher endocytic capacity and harbour more oxidised Mtb) highlights that a host cell cycle (interphase-driven) changes in endocytic capacity regulate bacterial redox states.

Strengths:

Overall, the study is well-executed and conceptually rich, establishing a causal link between host cell cycle progression, endocytic heterogeneity, and M. tuberculosis phenotypic diversity.

The combination of multiple modalities, including live-cell imaging, flow cytometry, scRNA-seq, and redox-sensitive bacterial reporters, supports these findings and substantially strengthens the biological relevance of the work.

The writing is generally clear, and the figures are well-organised.

This work will be of interest to readers across cell biology, microbiology, and infection biology

Weaknesses:

However, several central claims are only partially supported, the mechanistic depth is limited, and several experimental and analytical concerns need to be addressed.

Major Comments:

(1) The authors demonstrate a correlation between the G2 phase and elevated endocytic capacity. However, the mechanistic link (upstream molecular mechanism) between the cell cycle and endocytic upregulation remains largely unaddressed. The authors speculate that membrane biogenesis during volumetric expansion may drive increased endocytosis and note that lipid biosynthesis genes are upregulated in high-endocytic cells. It would substantially strengthen the paper to test this directly, by examining whether inhibition of lipid biosynthesis (e.g., with fatostatin or cerulenin) selectively reduces the G2-associated increase in endocytic capacity. Alternatively, cyclin-CDK axis perturbations (e.g., CDK1 inhibition with RO-3306 to specifically block G2/M entry) could be used to ask whether cells arrested in G2 maintain elevated endocytosis, helping distinguish cell-cycle-position-dependent from cell-cycle-progression-dependent effects.

(2) The current data show a clear association between high endocytic capacity and more oxidised Mtb, and the authors (consistent with their prior work) hint at lysosomal delivery as the likely mechanism. However, direct evidence for this in the current paper is limited. An experiment examining phagosomal pH or lysosomal fusion (e.g., using a pH-sensitive reporter or lysotracker) specifically in high- and low-endocytic-capacity cells after infection would help confirm this.

(3) Temporal resolution of Mtb redox dynamics. The plasticity experiment (Figure 6C-D) is elegant and shows that Mtb redox states revert as host cells divide and daughters enter G1. However, the experiment compares day 0 and day 3 post-sorting, which spans multiple cell divisions. While a finer time resolution (spanning 24h) would establish the causal relationship, the authors could discuss the possibility and consequences of multiple cell divisions between day 0 and day 3 used in the present study.

(4) Relevance of G2 percentages in differentiated macrophages. In Figure 7 and Supplementary Figure S7, only 4.4-5.7% of THP-1-derived macrophages and 5.7% of BMDMs are in G2. While the authors demonstrate statistically significant differences in Mtb redox states between G1 and G2 macrophages, the biological significance of such a small G2 fraction in a non-dividing population deserves discussion specifically with respect to: a) Are these cells re-entering the cycle? b) Is the G2 designation capturing a distinct functional state rather than active cycling? The authors should include additional markers (e.g., phospho-histone H3 for mitotic cells or BrdU incorporation to test for active S-phase) to characterise this population and clarify its identity and origin in differentiated macrophages, thereby meaningfully informing interpretation.

In conclusion, this is an important mechanism-driven study that highlights an important link in host-driven bacterial phenotypic heterogeneity. The experiments are thorough, the model is well-supported, and the study has implications for infection biology.

Reviewer #2 (Public review):

In this manuscript, the authors utilize a combination of techniques to show that macrophage endocytic capacity is partially dictated by cell-cycle stage, that Mycobacterium tuberculosis (Mtb) more readily infects macrophages that are in G2/M -phases, and that bacteria that are internalized by macrophages at different stages of the cell-cycle experience different levels of intracellular stress (as reported by the redox state of the bacteria). Furthermore, the authors provide evidence that terminally differentiated macrophages retain memory of the cell-cycle stage that they were in prior to differentiation, at least in the context of endocytic capacity.

This work provides evidence for the growing idea that fundamental heterogeneity in both host and bacterial organisms can alter the host-pathogen relationship in important ways. However, based on the current data, I am not convinced that the manuscript establishes endocytic capacity as the causal link between macrophage cell-cycle stage and bacterial state. The main issue is that fluorescence-based sorting for cell-cycle stage is likely to covary with cell size. Larger cells, including those later in the cell cycle, may be more likely to fall into the "high" fluorescence gate, while smaller cells may be enriched in the "low" population. Therefore, the observed phenotypes may still be cell-cycle-associated, but the causal determinant could be a correlated feature of cell-cycle progression rather than endocytic capacity itself. This is a significant caveat because nearly all the data, including the live-cell imaging following individual cells, rely on 'total' fluorescence, which will scale strongly with cell size.

If the authors' conclusion that endocytic capacity is cell-cycle regulated holds true after appropriate controls, this would significantly advance our understanding of the causal interplay between host cell-cycle state, endocytosis, and Mtb physiology. However, an alternative interpretation is that the observed differences in Mtb uptake and bacterial redox state are associated with cell-cycle stage but are not caused directly by differences in endocytic capacity. For example, they could instead reflect other cell-cycle-linked changes in macrophage physiology, such as cell size, intracellular volume, metabolic state, or some other mechanism important for Mtb pathogenesis. If the authors find that their data are best explained by cell-cycle stage independent of endocytic capacity, this would still represent an important advance. However, in that case, the manuscript should clearly distinguish the association with cell-cycle state from the downstream effector mechanisms, which would remain to be determined.

Strengths:

The authors utilize various macrophage models for their studies, which is important considering the variability in macrophage behavior, as well as the growing evidence that differences between mouse and human macrophages are relevant for Mtb infection.

Weaknesses:

The most important caveat is the covariance between fluorescence-based reporters and cell size. This concern applies to both the sorting experiments, which directly measure total fluorescence, and the time-lapse microscopy experiments, in which the authors show total fluorescence rather than mean, area-normalized fluorescence in Figure 3C. This could be explained by biomass accumulation alone, rather than by a specific cell-cycle-dependent increase in endocytic capacity. Without distinguishing total signal from concentration or activity per unit cell area/volume, it is difficult to conclude that endocytosis itself is regulated by cell-cycle stage rather than simply scaling with cell size.

Although the authors provide some evidence that the mean GFP intensity, which more closely reflects concentration, differs between the sorted populations in Figure 3B, they do not report statistics for this comparison. Moreover, this control is not carried through the rest of the manuscript, including in key experiments such as Figure 2B. As a result, it remains difficult to determine whether the observed differences between "high" and "low" populations reflect cell-cycle state specifically or instead reflect differences in total reporter fluorescence driven entirely by cell size.

The evidence for cell-cycle-dependent effects would be more convincing if the authors included additional controls. For example, they could:

(1) Plot both mean GFP intensity and total GFP intensity in Figure 3B, ideally alongside an unrelated fluorescent reporter that does not vary across the cell cycle. This would help distinguish changes in reporter concentration from changes driven by cell size or total fluorescence.

(2) Sort cells based on an unrelated fluorescent marker and test whether the same phenotypes - infectivity, dextran uptake, bacterial redox state, etc. - differ between high- and low-fluorescence populations. If these phenotypes are specific to the cell-cycle reporter and not observed with an unrelated marker, this would strengthen the conclusion that the effects are linked to cell-cycle state rather than to fluorescence intensity, cell size, or sorting artifacts.

Reviewer #1 (Public review):

Summary:

Torpor can be induced by chemogenetic activation of the medial preoptic area. This activation leads to protection from myocardial infarction in an isolated heart preparation despite normalization of the ambient temperature, thus, in principle, uncoupling hypothermia from torpor-induced neuroprotection. Putative pathways of protection are suggested by proteomic studies.

Strengths:

(1) Elegant strategy for inducing torpor in rats.

(2) Appropriate controls for verifying the neuron transducer.

(3) Cardiac protection is significant and appears independent of hypothermia.

(4) Interesting omic strategy to begin to find established and novel pathways mediating organ autonomous torpor-induced protection.

Weaknesses:

(1) The study would benefit from using inhibitory chemogenetics of the same neurons to demonstrate that this might make cardiac response to ischemia worse.

(2) Infecting an area of the brain not known to be involved in torpor would be a useful control.

(3) In vivo cardio protection seems essential as the validation of the strategy requires support that is in the intact animal.

(4) The assumption that the positive effects of torpor are mediated via a phosphoproteomic change rather than a translational or transcriptional control mechanism is not established.

(5) A 40 percent reduction in infarct size may work for genetically identical rats with no co-morbidities, but is unlikely to be significant enough to weather the variability that emerges in humans because of these differences and more. The question is not what the mechanism is, but how do we make it more robust? Overall, this is at best a preliminary data set that requires more experiments to deliver on its immense promise.

Reviewer #2 (Public review):

Summary:

Elley and colleagues induced a synthetic torpor-like state in rats (a non-hibernating species) by chemogenetically activating neurons in the medial preoptic area of the hypothalamus. They show that this state substantially reduced cardiac infarct size in an ex vivo ischemia-reperfusion model. They further report that protection persisted when ambient temperature was raised to prevent hypothermia, and used exploratory phosphoproteomics to identify candidate cardioprotective signaling pathways.

Strengths:

This is the first demonstration that a torpor-like state is cardioprotective in a species that does not naturally enter torpor, which meaningfully advances the potential clinical utility of synthetic torpor. The experimental design is logical, and the controls are generally appropriate. The characterisation of the responsible neuronal population using ISH against QPLOT markers adds mechanistic depth and supports the cross-species conservation argument. The phosphoproteomic analysis, though exploratory, generates plausible and biologically coherent hypotheses grounded in the hibernation literature.

Weaknesses:

The primary weakness is that the central conclusion - that hypothermia is not necessary for cardioprotection - exceeds the evidence. The thermoneutral groups were not demonstrably normothermic (36.4 vs 37.05{degree sign}C, p=0.44 with n=6), core temperature telemetry was absent in the majority of control animals contributing to the infarct endpoint, and the decisive test, i.e., a correlation between individual nadir temperature and infarct size, was never performed. Additional weaknesses include the absence of sex-stratified analysis despite known estrogenic contributions to torpor

Reviewer #3 (Public review):

Summary:

The manuscript by Elley and colleagues describes experiments on the effects of synthetic torpor on ex vivo heart ischemia. The key aspect of the study was the use of viral-vector mediated manipulation of the hypothalamic medial preoptic area (MPA) in rats. They used AAV-CaMKIIa-hM3D(Gq). The authors report that chemogenetic activation of the MPA prior to an ex vivo heart ischemia-reperfusion insult induces cardio protection against infarct size that is independent of prior in vivo hypothermia. Phosphoproteomic analysis of cardiac tissue suggested changes in cell survival and death pathways.

Strengths:

This study has important strengths. The idea is novel. The experimental design is appropriately rationalized and fascinating. The manuscript is written and presented concisely.

Weaknesses:

The study has important weaknesses in the experimental design and validation of the model.

(1) The study is based on the use of a DREADD-designed viral vector (AAV-CaMKIIa-hM3D(Gq) -mCherry) that is activated by 2 mg/kg IP injection of CNO. The rationale is to putatively activate the MPA. The authors show no evidence for chemogenetic activation of neurons in the MPA. This could be done using a variety of different approaches, even phosphoproteomics.

(2) The stereotaxic injections are difficult to precisely and locally place, particularly bilaterally. Figure 2F is only a schematic. It would be better to show actual low magnification brain sections (bregma +0.12 to -0.48) from a representative rat to show the placement of the AAV.

(3) The control rats were injected with AAV-CaMKIIa-EGFP. Why was EGFP used instead of mCherry for the control?

(4) Ideally, a mutant non-activatable variant of AAV-CaMKIIa-hM3D(Gq) should have been used for a better control.

(5) The authors should comment on whether there is any neurotoxicity in the MPA associated with the forced AAV expression of hM3D-Gq.

(6) Is there any inflammatory pathology seen in the MPA with AAV transduction?

(7) There are no experiments to show that the systemic torpor is specifically associated with the MPA region. Experiments should be done with injections of AAV-CaMKIIa-hM3D(Gq)-mCherry placed in other brain regions, for example, the nearby nucleus accumbens.

(8) The mapping of the distribution of neurons responsible for synthetic torpor is not mechanistic enough and is not directly to the point. While excitatory and inhibitory markers are examined, a more interesting and deeper approach would have been to use glutamate receptor antagonists to manipulate the torpor response.

(9) The ischemia and reperfusion aspects of the Lagendorff method need to be clarified. The isolated hearts are already ischemic after their removal from the rat. The reperfusion aspect is caused by reflow of blood to generate oxidative stress, but in the ex vivo model, is there really reperfusion injury?

(10) The authors show that whole animal oxygen consumption is reduced in the torpor state. The measurement is crude and most likely reflects the inactivity of the animal's skeletal muscle in the torpor state. A more relevant and direct experiment would be to do oxygen consumption (or Seahorse) assays on extracts of the isolated hearts.

(11) The authors report that the synthetic torpor induces bradycardia. There is no follow-up on this important observation. The MPA-heart connection is not analyzed. (A) Is the link through cardiovascular centers in the brainstem? (B) Is the torpor-induced bradycardia mediated through increased parasympathetic or decreased sympathetic autonomic tone? Pharmacological experiments could also be done.

Reviewer #1 (Public review):

The work corroborates the idea, recently suggested by Rosenthal et al. (2025), that spreading depolarization is involved in the mechanisms of electroconvulsive therapy. Using a mouse model of electroconvulsive therapy and various sophisticated approaches to visualize cortical activity, the authors provide an extensive description of traveling calcium waves induced by electroconvulsive stimulation. The study confirms that the calcium events have properties typical of cortical spreading depolarization and seeks to show that the calcium/SD waves mediate therapeutic and neuroplastic effects of electroconvulsive therapy. The authors find that after electroconvulsive stimulation associated with calcium/SD waves, Fos expression increases widely; in the cortex, this increase is localized to the hemisphere affected by calcium waves. They show that some EEG predictors of the beneficial effects of electroconvulsive therapy correlate with the occurrence of calcium/SD waves. Despite the solid methodology and the study's interesting, its conclusions are not fully supported by the data.

In particular:

(1)The title of the paper claims that "electroconvulsive stimulation drives cortical spreading depolarization dependent immediate early gene expression". However, immunohistochemical staining shows that Fos expression increases not only in the cortex but also in many subcortical regions, including the hippocampus and amygdala (Figure 5A). Really, conventional electroconvulsive therapy stimulates nearly the entire brain volume and induces generalized seizure activity that can trigger SD not only in the cortex but also in other brain sites. Therefore, regions beyond the cortex can also drive the effects of electroconvulsive therapy. Next, the authors use Fos staining as a marker of neuronal plasticity. However, Fos is also a marker of preceding neuronal activation. As electroconvulsive stimulation, seizures, and SD are associated with high neural activity, it is unclear whether the observed Fos upregulation results from the prior activation or heralds the subsequent plastic changes. Other markers of neuroplasticity (e.g., BDNF) should also be examined.

(2) Postictal EEG suppression is one of the most promising correlates of positive clinical outcomes after electroconvulsive therapy. Cortical SD is also tightly coupled with suppression of neuronal activity in affected regions. Although the authors report that postictal suppression is stronger after stimulations with cortical SDs than without SDs, the cortices affected (ipsi) and unaffected (contra) by unilateral cortical calcium/SD events exhibit identical suppression (Figure 6F). The result contradicts established knowledge in the field. If the calcium events are cortical SDs, they should induce EEG suppression only in the affected hemisphere.

(3) The study states a beneficial role of calcium/SD waves in ECS effects. However, SD alters numerous aspects of brain function, leading to a range of effects that can underlie side effects as well. Assessment of the behavioral effects of stimulation with and without calcium/SD waves can help clarify the issue.

The results of the work suggest that cortical SD can contribute to electroconvulsive therapy-related mechanisms and help to optimize the stimulation parameters to achieve maximal therapeutic effect.

Reviewer #2 (Public review):

Summary:

This manuscript addresses the question of mechanisms underlying the therapeutic effects of electroconvulsive therapy (ECT). Clinical efficacy of ECT in major depression (and other disorders) is well established and has often been assumed to be a direct consequence of seizure activity generated by the current application. However, as the authors point out, this explanation is unsatisfactory. A recent study (Rosenthal et al., 2025) provided evidence that ECT generates a wave of cortical spreading depolarization (CSD) in mice, and initial evidence that similar events were generated in patients undergoing ECT. Based on their observations, Rosenthal et al. proposed that CSD, rather than seizure, may engage plasticity mechanisms that contribute to the brain's clinical response to ECT. The current study adds to that prior work by reporting other consequences of CSD, in addition to sustained Ca2+ elevations. The current study also links EEG characteristics immediately following the ECT with the likelihood of generating a CSD, which can help optimize ECT parameters.

Strengths:

An important research topic, linking a large set of rodent studies with a limited clinical EEG data set.

The data acquisition and analyses appear to be of very high quality, and the main results are well illustrated.

Association between EEG characteristics linked to good clinical outcome matched by mouse EEG data linked to CSD.

Characterization of multiple consequences of CSD following ECT in the mouse brain.

Weaknesses:

The main characterization of CSD propagation comes from GCaMP Ca2+ measurements, as previously reported (Rosenthal et al., 2025). That prior study also provided key electrophysiological evidence of CSD with a DC shift after ECT in mice (supplemental data). Given the prior evidence for ECT-CSD, the additional measures shown in the current manuscript are fully expected. Thus, the 2-photon imaging of Ca2+ elevations following CSD (Figure 4) is consistent with prior 2-photon imaging studies of CSD, and the complex hemodynamic and pH changes are expected to contribute to propagation of EGFP fluorescence changes (Supplemental Figure 5). These data are well presented, but, contrary to the results section here, these results appear confirmatory rather than necessary to build a case that the key event generated by ECT is a CSD.

The authors state that "our conclusion that CSD is the primary driver of plasticity is based on its role in driving Fos expression" (line 472). Related to the point above, there is already a very well-established literature showing that CSD leads to rapid and robust Fos expression in rodent cortex, so this is fully consistent with prior work. The prior work, CSD-fos work, should be summarized and/or cited more clearly in the manuscript. Showing that Fos increases only in the hemisphere where there is a large CSD-Ca2+ wave is a clear demonstration of this. While Fos increases can certainly be well linked to plasticity in some experimental paradigms, the implication that Fos increases underlie CSD-induced plasticity and possibly therapeutic effects of ECT is not appropriate. Fos increases after CSD are a reliable marker of the very strong neuronal activation that occurs, but Fos increases are not specific for plasticity and can be activated by challenges that do not generate synaptic plasticity. A range of other gene expression changes have been identified with CSD and may contribute to adaptive plasticity; these could be mentioned alongside speculation about Fos. To support the main conclusions of this paper about CSD driving plasticity via Fos, Fos knockout or knockdown studies are needed, as has been used in prior plasticity studies.

Reviewer #3 (Public review):

Summary:

This manuscript combines widefield calcium imaging, electroencephalography, 2-photon imaging, and immunohistochemistry in mice to re-demonstrate that electroconvulsive stimulation (ECS) induces a seizure followed by cortical spreading depolarization, as previously shown. The putative novel finding - which is not unexpected - is that ECS is also correlated with increased expression of the immediate early gene cFOS, although this has also been shown previously. The authors speculate that CSD drives cFOS expression, which might contribute to the therapeutic effects of ECT; however, experiments performed do not provide causal evidence for this hypothesis. Instead, the authors use expression of cFOS - a nonspecific activity-dependent gene induced in various pathological and non-therapeutic contexts - as a proxy for plasticity and/or therapeutic effect. Hence, overall, the significance of the findings is limited and primarily serves to replicate prior work, with the evidence evaluated as incomplete.

Strengths:

The experiments are generally well executed from a technical perspective.

Main Weaknesses to be addressed in revision:

(1) The main findings of this paper are replication experiments of prior work, and thus, the novelty and significance of this manuscript are relatively limited.

- It is already known that the mean frequency of ECT-induced seizures decays between peak and offset in humans (Stuiver et al. Clin Neurophysiol. 2026 Jan:181:2111439. doi: 10.1016/j.clinph.2025.2111439) and mice (Murakami et al. J Pharmacol Sci 2008 Jan;106(1):78-83. 10.1254/jphs.FP0071453), which the authors re-demonstrate in Figure 1.

- It has already been demonstrated that ECT in mouse models induces lateralized CSD waves in a manner that depends on stimulation parameters and the initial evoked response during stimulation (Rosenthal et al. Nat Comm. 2025 May 18;16(1):4619. doi: 10.1038/s41467-025-59900-1); the authors replicate this in Figures 1, 2, 3, 6.

- It is already widely established that EEG and calcium signals are highly concordant in mouse brain physiology, as shown in Figure 1. It is already known that CSD propagates from supragranular to granular and infragranular layers (Zakharov et al. Epilepsia. 2019 Dec;60(12):2386-2397. doi: 10.1111/epi.16390) as shown in Figure 4.

- It is already known that CSD waves induce cFOS expression (e.g., Dell'Orco et al. Front Cell Neurosci. 2023 Dec 14:17:1292661. doi: 10.3389/fncel.2023.1292661; Hermann and Hossman. Neuroscience. 1999 Jan;88(2):599-608. doi: 10.1016/s0306-4522(98)00249-8) as the authors replicate in Figure 5.

Minimally, the authors should revise claims regarding novelty, as the manuscript, as written, is misleading to a reader not familiar with the field. There is limited innovation in re-demonstrating that these events are seizures and that they involve spreading depolarization.

(2) The authors frame their hypothesis that CSD could be a potential mediator of the therapeutic effects of ECT, but they do not measure therapeutic effects or directly test this hypothesis. The principal advancement of the paper is showing that ECT-induced CSD triggers hemisphere-specific cFOS expression as a proxy of plasticity. However, it is already known that CSD induces cFOS expression (as noted above). The observation that cFOS expression was induced only by CSD, not by the initial seizure, is likely a byproduct of the greater activity induced by CSD than by seizure. cFOS expression is nonspecific to plasticity or therapeutic effects and can be triggered by many non-therapeutic interventions. The cFOS data thus do not meaningfully measure therapeutic plasticity. The authors also selectively cite references suggesting that EEG metrics such as seizure duration predict positive therapeutic outcomes, but this link is controversial and not well established in the clinical literature.

Minor Weaknesses:

(3) For the n=3 mice used for concurrent 2P imaging with microprism implant, these animals also had ChrimsonR co-expression, but there are no optogenetic studies described in this paper, which is confusing. Yet, this co-expression introduces a significant confound, as GCaMP6 emission (525/50nm band in this study) will overlap substantially with the ChrimsonR excitation spectrum. Thus, the fluorescence emission used to image these neurons may be optogenetically activating them at the same time. Please explain.

(4) Incision of the cortex for implantation of a prism is a significant cortical injury that likely induces CSD instantaneously and may change the propensity for CSD in subsequent recordings. Please comment on this limitation and address how much time elapsed after surgery before imaging.

(5) Method details are missing or insufficiently described for location, titer, and injection strategy for 2-photon experiments.

(6) Given the wide range of parameters used for ECS in mice and ECT in humans, the authors should provide tables for what stimulation parameters were used for each recording. These protocols were chosen manually rather than randomly or systematically, which introduces confounding factors into analyses that use parameters as an independent variable.

(7) While much of the cFOS staining after unilateral CSD shows hemisphere-specific asymmetry, several regions (piriform cortex, amygdala, thalamus) do appear to have bilateral cFOS expression. Please comment on this.

(8) The discussion states: "If CSD accounts for plasticity effects, triggering a CSD in a non-seizure context may be sufficient to elicit therapeutic effects. This is supported by the clinical success of ultra-brief stimulation treatments that do not cause seizures, such as rTMS with accelerated protocols, which achieves treatment efficacy on par with ECT for major depressive disorder". Are the authors implying that TMS induces CSD? What evidence supports this idea?

(9) This statement - "Assuming psychosis is the result of thalamocortical coupling that is too weak in frontal areas of the cortex" (lines 583-585) - may be overly speculative.

Reviewer #1 (Public review):

[Editors' note: all three reviewers confirm that all initial concerns have been fully resolved through comprehensive revisions and supplementary analyses.]

Summary:

By imaging the dynamics of synaptic proteins in cultured neurons, this study presents significant findings regarding the dynamics of excitatory and inhibitory synaptic proteins during development. The evidence shows that the ratios of excitatory and inhibitory synaptic proteins are stable during synapse development. This discovery advances our understanding of the complex mechanisms governing synapse formation. The strength of the evidence is robust, as it is supported by a combination of biological assays and endogenous labeling.

Strengths:

This research sheds light on the dynamics of the excitatory and inhibitory synapses during development. It is crucial to understand that while excitatory synapses and inhibitory synapses are developed independently, the ratio of their number is relatively stable during development, maintaining a stable excitatory/inhibitory ratio.

Important findings and implications in the research include:

(1) Persistent Synapse Dynamics: Excitatory and inhibitory synapses remain highly dynamic even in mature neurons (DIV12-14), challenging the dogma that synaptic structures are stable after the synaptogenesis stage.

(2) Maintained E/I Balance: Despite ongoing synapse turnover (formation/elimination) and presynaptic terminal reduction, the overall density and ratio of excitatory-to-inhibitory synapses remain relatively stable during circuit maturation (Figure 7).

(3) Developmental Shifts: While presynaptic compartments decrease over time, postsynaptic sites increase, suggesting independent regulation of pre- and postsynaptic elements within a stable E/I framework.

Weaknesses:

This study focuses on specific synaptic proteins within synapses, which may not fully represent the dynamics of other synaptic machinery; also, whether similar observations exist in vivo is still unknown. Further research is needed to explore the implications of these findings in more complex neuronal environments.

Comments on revised version:

The authors have addressed all my questions/comments. No further questions for this manuscript.

Reviewer #2 (Public review):

Summary:

The Garbett et al. identified a critical need to begin to understand the interplay between the assembly, maturation, and elimination of excitatory and inhibitory synapses. They also detail the lack of reliable tools to address this gap in knowledge. Here, the authors developed synaptic reporters expressed by lentiviruses (mClover3-Homer1c, HaloTag-Syb2, and tdTomato-Gephyrin). They combined these reporters with resonance scanning confocal imaging to measure synapses over a 15-hour period during neuron development and in mature neurons in primary hippocampal cultures. Using these reporters in the same neuron, the authors compared the ratios of postsynaptic excitatory and inhibitory specializations that co-localize with presynaptic terminals during development and in mature neurons and found that they are stable across time points. Finally, the authors developed CRISPR/Cas9 tools (TKIT) to knock-in endogenous fluorescent tags (GFP/tdTomato-Gephyrin) or epitope tags (HA-Bassoon and HA-Homer1) to begin to study synapse dynamics using endogenous proteins. I believe this paper highlights an important gap in knowledge and begins to offer methodologies to determine the dynamic coordination between excitatory and inhibitory synapses.

Strengths:

(1) The experiments are well-designed and carefully controlled.

(2) The authors carefully validated the reporter and TKIT constructs.

(3) The authors provide strong proof-of-principle for the use of the reporter constructs to track synapse formation, maintenance, and elimination over a 15-hour period.

(4) Ingenious use of technologies (reporters, TKIT, and resonance scanning confocal microscopy) to develop a platform for future studies of synapse dynamics.

(5) Strong evidence supporting that the ratio of excitatory and inhibitory synapses (those that oppose syb2) stays constant through development.

Overall, this is a well-executed study that develops tools to simultaneously image excitatory and inhibitory synapse dynamics and represents an important first step to address the fundamental question regarding the coordination between these two types of synapses.

Comments on revised version:

The authors addressed all my questions and comments. Their edits have made this paper significantly stronger. I believe that this is an important paper for the field.

Reviewer #3 (Public review):

In the present study, the authors describe the development of new tools and imaging strategies to assess the concomitant development of excitatory and inhibitory synapses in dissociated neuron cultures. To this end, they generate fluorescently tagged constructs of excitatory and inhibitory synapse marker proteins using either conventional overexpression or CRISPR-based strategies. They then image these marker proteins over a timespan of 15 hours to assess synaptic dynamics at different developmental timepoints. Based on their data, they conclude that excitatory and inhibitory synapse development occur in concert to maintain a functional balance despite individual synapse turnover.

Overall, this study addresses an interesting question, i.e., the interplay between the development of excitatory and inhibitory synapses, which has important implications, particularly for neurodevelopmental disorders in which the balance of excitation and inhibition is disrupted. The experiments are technically solid and well-executed, and the individual images are highly compelling.

Comments on revised version:

The authors have fully addressed my concerns, and this is now a strong manuscript for the synaptic field.

Reviewer #1 (Public review):

Summary:

This study investigates how human temporal voice areas (TVA) respond to vocalizations from nonhuman primates. Using functional MRI during a species-categorization task, the authors compare neural responses to calls from humans, chimpanzees, bonobos, and macaques while modeling both acoustic and phylogenetic factors. They find that bilateral anterior TVA regions respond more strongly to chimpanzee than to other nonhuman primate vocalizations, suggesting that these regions are sensitive not only to human voices but also to acoustically and evolutionarily related sounds.

The work provides important comparative evidence for continuity in primate vocal communication and offers a strong empirical foundation for modeling how specific acoustic features drive TVA activity.

Strengths:

(1) Comparative scope: The inclusion of four primate species, including both great apes and monkeys, provides a rare and valuable cross-species perspective on voice processing.

(2) Methodological rigor: Acoustic and phylogenetic distances are carefully quantified and incorporated into the analyses.

(4) Neuroscientific significance: The finding of TVA sensitivity to chimpanzee calls supports the view that human voice-selective regions are evolutionarily tuned to certain acoustic features shared across primates.

(4) Clear presentation: The study is well organized, the stimuli well controlled, and the imaging analyses transparent and replicable.

(5) Theoretical contribution: The results advance u

Comments on revised version.

I thank the authors for having carefully considered and implemented my remarks on the first version.

Reviewer #2 (Public review):

Summary:

This study investigated how the human brain responds to vocalizations from multiple primate species, including humans, chimpanzees, bonobos, and rhesus macaques. The central finding-that subregions of the temporal voice areas (TVA), particularly in the bilateral anterior superior temporal gyrus, show enhanced responses to chimpanzee vocalizations-suggests a potential neural sensitivity to calls form phylogenetically close nonhuman primates.

Strengths:

The authors employed three analytical models to consistently demonstrate activation in the anterior superior temporal gyrus that is specific to chimpanzee calls. The methodology was logical and robust, and the results supporting these findings appear solid.

Weakness:

The authors only tested vocalizations from three non-human primate species other than humans. In this case, the species specificity of the effect does not fully represent the specificity of evolutionary relatedness.

Comments on revised version.

I have no further comments.

Reviewer #3 (Public review):

Summary:

Using fMRI, the authors demonstrate that human temporal voice areas (TVA) respond not only to human vocalizations but also to those of other primates, particularly chimpanzee calls, which share acoustic features with human voices. These findings provide compelling evidence for cross-species vocal processing in the human auditory system and carry important theoretical implications for understanding the evolutionary underpinnings of speech perception.

Strengths:

The study offers a valuable comparative design, rigorous acoustic and phylogenetic modeling, and consistent evidence that bilateral anterior TVA regions respond more strongly to chimpanzee vocalizations than to other species' calls. The inclusion of both great apes and monkeys provides a rare cross-species perspective.

Weaknesses:

Minor limitations include the acoustic-phylogenetic confound (which the authors partially address with additional analyses), the lack of non-vocal controls to establish true selectivity.

Overall, the methods, data, and analyses broadly support the claims, with only minor weaknesses that do not undermine the main conclusions. The findings are valuable for the subfield of auditory neuroscience and comparative cognition, with solid evidence supporting the primary claims.

Comments on revised version.

After revision, this work has shown great improvement in data analysis, figure organization, and writing. I have no further suggestions.

Reviewer #1 (Public review):

Summary:

Argunşah et al. describe and investigate the mechanisms underlying the differential response dynamics of barrel vs septa domains in the whisker-related primary somatosensory cortex (S1). Upon repeated stimulation, the authors report that the response ratio between multi- and single-whisker stimulation increases in layer (L) 4 neurons of the septal domain, while remaining constant in barrel L4 neurons. The authors attribute this divergence to differences in short-term synaptic plasticity, particularly within somatostatin-expressing (SST⁺) interneurons. This interpretation is supported by 1) the increased density of SST+ neurons in L4 of the septa compared to barrel domain, 2) the stronger response of (L2/3) SST+ neurons to repeated multi- vs single-whisker stimulation and 3) the reduced functional difference in single- versus multi-whisker response ratios across barrel and septal domains in Elfn1 KO mice, which lack a synaptic protein that confers characteristic short-term plasticity, notably in SST+ neurons. Consistently, a decoder trained on WT data fails to generalize to Elfn1 KO responses. Finally, the authors report a relative enrichment of S2- and M1-projecting cell densities in L4 of the septal domain compared to the barrel domain, suggesting that septal and barrel circuits may differentially route information about single vs multi-whisker stimulation downstream of S1.

Strengths:

This paper describes and aims to study a circuit underlying differential response between barrel columns and septal domains of the primary somatosensory cortex. This work supports the view these two domains contribute distinctly to the processing single versus multi-whisker inputs and highlight the role of SST+ neuron and their short-term plasticity. Together, this study suggests that the barrel cortex multiplexes whisker-derived sensory information across its domains, enabling parallel processing within S1.

Weaknesses:

Although the divergence in responses to repeated single- versus multi-whisker stimulation between barrel and septal domains is consistent with a role for SST⁺ neuron short-term plasticity, the evidence presented does not conclusively demonstrate that this mechanism is the critical driver of the difference. The lack of targeted recordings and manipulations limits the strength of this conclusion: SST⁺ neuron activity is not measured in L4, nor is it assessed in a domain-specific manner. The Elfn1 knockout manipulation does not appear to selectively affect either stimulus condition, domain or interneuron subtype. Finally, all experiments were performed under anesthesia, which raises concerns about how well the reported dynamics generalize to awake cortical processing.

Reviewer #3 (Public review):

Summary:

This study investigates the functional differences between barrel and septal columns in the mouse somatosensory cortex, focusing on how local inhibitory dynamics (particularly involving SST⁺ interneurons) may mediate temporal integration of multi-whisker (MW) stimuli in septa. Using a combination of in vivo multi-unit recordings, calcium imaging, and anatomical tracing, the authors propose a model in which Elfn1-dependent synaptic facilitation onto SST⁺ interneurons contribute to the distinct sensory responses to MW input in barrels and septa, enabling functional segregation between these domains.

Strengths:

The study presents a thought-provoking and useful conceptual model for understanding sensory processing in the somatosensory cortex. While barrel columns have been widely studied, septal regions remain relatively understudied in mice. If septa indeed act as selective integrators of distributed sensory input, this would suggest a novel computational role for cortical microcircuits beyond the classical view focused on barrels. Although still hypothetical, the proposed model in which SST⁺ interneurons contribute to domain-specific sensory responses between barrel and septal domains is intriguing and opens new avenues for investigating inhibitory circuit mechanisms.

Weaknesses:

The primary limitation of this study lies in the spatial and cellular specificity of the recording techniques. The physiological data rely predominantly on unsorted multi-unit activity (MUA) recorded with low-channel-count silicon probes. Because MUA aggregates signals from multiple neurons over a radius of approximately 50-100 µm (comparable to or larger than the width of septal domains in mice), it remains difficult to confidently attribute the recorded activity exclusively to septal versus barrel populations. The authors have now addressed this concern more carefully by reframing their interpretation in terms of "septal-enriched" populations and by providing additional threshold-based analyses suggesting that the principal effects are more robust in Layer 4. These additions substantially improve the manuscript and support a more cautious interpretation of the findings. Nevertheless, the proposed Elfn1/SST⁺ mechanism remains supported primarily by indirect evidence. Although the calcium imaging data provide useful support for stimulus-dependent SST⁺ recruitment, these experiments were restricted to L2/3 interneurons and therefore do not directly test the Layer 4 circuit mechanism proposed to underlie the electrophysiological observations. Direct in vivo cell-type-specific recordings and manipulations in Layer 4 would ultimately be required to establish the proposed mechanism more conclusively.

Comments on revised version.

I have read the revised manuscript and overall, I think the authors have addressed my major concerns appropriately. I appreciate the substantially moderated interpretation of the findings and the additional analyses clarifying the limitations of the MUA recordings.

Reviewer #1 (Public review):

The paper uses a passive whisker detection task in mice to identify a behavioral phenomenon that can reasonably be interpreted as spatial attentional capture. The attentional effect occurs transiently after a successful whisker stimulus detection yields reward, and lasts for a few trials before subsiding. The attentional effect is to the right or left whiskers, depending on whether right or left whiskers are rewarded; no finer spatial resolution for attention was tested. By recording whisker-evoked spiking from single units in S1, the authors show that this form of spatial attention increases the gain of whisker-evoked neuronal responses in S1 for a large subset of S1 units. In contrast, neural responses are not modulated by overall task engagement. Together, these findings show a neural signature of spatial attention in S1 cortex. Because whisker or facial movements were not tracked, it is not clear whether this represents covert attention or whisker movement in response to previously rewarded stimuli, which would be a form of overt attention.

Substantial attentional modulation of neural responses was observed for a subset of whisker-responsive S1 units, but the effect size was small on average for the total unit population. The top 25% of units showed a ~12% attentional response modulation (relative to firing rate range for each unit), but the median unit showed only a 1.3% response modulation. It would have been useful to analyze the magnitude or prevalence of attentional modulation across layers or in fast-spiking vs. regular spiking units, but this was not reported.

Major

(1) It is hard to interpret the underlying causes of the attentional modulation of neural activity without having measured whisker and facial movement. This is a particular issue in S1, where whisker movement against the stimulation grid can alter the mechanical efficiency of stimulus delivery. Such movements would represent overt attention, which would engage an entirely different neural mechanism than covert attention.

(2) An interesting debate is whether the behavioral phenomenon is best described as attention or as dynamic learning of the stimulus-response association for that block. In Posner-type cued attention tasks, and also in many block-type attention tasks in rodents, animals receive reward for successfully detecting either cued or uncued stimuli, and thus attention (higher response probability or improved psychometric sensitivity for cued stimuli) is at least partially dissociated from the stimulus-reward contingency. That is not the case here. The fact that mice have difficulty learning the contingency reversal suggests that the phenomenon is better explained by attention than by learning the contingency; however, to prove this clearly, the existence of the attentional effect on neural activity in Block 1 vs. Block 2 would have to be shown.

(3) Some of the graphical representations of the attentional modulation of neural activity are unclear. The single-unit example of attentional modulation is quite strong (Figure 3d). The mean response for the top 25% of units is also visually clear (Figure 3f). But the effect is not apparent at all in Figure 3e, which the figure legend says shows every unit. What is the yellow point and line in this figure? Why isn't the attentional effect visible in this panel? Perhaps I am misunderstanding Figure 3e, but it is not clear to me why it compares Pref>0.5 to Pref<0.5, when the intended analysis suggests it should be Pref>0 to Pref<0? Also in Figure 3, it is critical for the reader to know whether panels 3g-3h represent the top 25% of units or all units. Neither the results text nor the legend is clear on this.

(4) There is a missed opportunity to quantify attentional modulation across cortical layers, since laminar probes and Neuropixels probes were used for the recordings. In addition, there is no separation of fast-spiking from regular-spiking units, and no quantitative metrics are provided to assess the quality of single units. This could reveal key aspects of cortical processing of attentional signals.

Reviewer #2 (Public review):

Summary:

Dyce et al investigate the modulation of sensory responses in the somatosensory 'barrel' cortex during a novel whisker vibration detection task in head-fixed mice, aiming to find correlates of spatial attention in both the animals' behavior and their neuronal activity.

Strengths:

The authors produced an extensive and parameterized dataset of both behavioral responses and neuronal activity, with >3000 single units of which >1400 were responsive.

Weaknesses:

In my view, the main conclusions of the manuscript are not currently well supported by the data.

The authors effectively define "spatial attention" as a state where an animal responds more to a stimulus that gives more rewards (out of two possible stimuli presented on different sides of the snout, i.e., segregated spatially). If one defines spatial attention purely in these terms, then their findings do show neuronal correlates of spatial attention. However, those neuronal correlates can be explained by known aspects of neuronal responses in the barrel cortex.

This plays out in several different ways:

From the behavioral point of view, greater attention may correlate with an increased hit rate to stimuli on the rewarded side, but in the absence of other supporting measurements, the relationship could well be the opposite: an animal could pay more (rather than less) attention to the stimulus delivered on the unrewarded side, to make sure it suppresses the incorrect response. It is impossible to tell, as the data don't provide an independent measurement of whether the animal is paying greater attention to, or is more aware of, one side than the other, nor do they provide an independent measurement of neuronal tuning on either side. There is no separate measurement of arousal either (e.g., via pupillometry or locomotion).

The experimental design involved two blocks on each daily task session, with the second block reversing the side on which rewarded stimuli were delivered. Reinforcing one's doubts about the behavior and its interpretation, mice had much poorer performance on each day's second block, to the extent that perceptual sensitivity (d') was the same for both sides: d' did not increase after reward reversal for stimuli on the initially unrewarded side. This further emphasizes the lack of a separate demonstration of focused "spatial attention".

Much of the data (both behavioral and neuronal) could be accounted for, e.g., by a strategy where the mouse keeps a token in working memory of what side seems to be driving rewards, while maintaining equally strong sensory drive on both sides, but with no attentional shift at all. The policy would be to respond more whenever the stimulated side matches the token in memory (thus also reinforcing the token, thus enhancing performance next time). This would be easily implemented with a disinhibitory reward-modulation signal such as the one multiple researchers have found carried by VIP neurons (e.g., Szadai et al DOI: 10.7554/eLife.78815).

Similarly, the fact that "attended trials" (Pref > 0) produced greater responses than "unattended trials" appears to be explainable as follows. Here, "attended" trials are those where the contralateral stimulus is presented (and, if responded to, is rewarded), "unattended" trials are those where the stimulus is ipsilateral (and not rewarded). The animal responds more (at least in the first block) to stimuli delivered to the contralateral pad - i.e., rewarded as opposed to unrewarded ones. Beyond the knowledge mentioned above that cortex-wide VIP sensitivity to rewards can drive disinhibition in general, activity modulation dependent on rewards and outcomes (and stimulus value) has been established specifically in the barrel cortex (e.g., Lacefield et al DOI: 10.1016/j.celrep.2019.01.093, Bale et al DOI: 10.1016/j.cub.2020.10.059, Banerjee et al DOI: 10.1038/s41586-020-2704-z, Chereau et al 10.1038/s41467-020-17005-x). The reward- and value-evoked activity demonstrated in those papers would suffice to predict more activity at the contralateral electrode on "attended" trials, along the lines of the findings in Ramamurthy et al (DOI: 10.1038/s41467-025-60592-w) and consistent also with the enhanced "attentional modulation" on hit trials.

Other aspects of the analysis and terminology lead to confusing outcomes. For example, in the analysis in Figure 3, Performance averaged in a set of trials around a given trial is defined as the mean rate of responses to stimulation on either side - regardless of whether those responses are correct (since the stimuli can be on either side, but only one side is correct and gets rewarded and putatively reinforced). Thus, this definition of "Performance" can increase with the rate of incorrect licks to the wrong side and is at odds with the normal use of the word. On trials where this Perf = 1 and the stimuli are balanced on either side, this corresponds to a true performance (and reward rate) of only 0.5 - what one would normally consider random discrimination between the sides. Thus, Perf = 1 trials may still give a low reward rate and, if responses scale with reward, a small effect of reward. Hence, based on known properties of reward dependence, greater correlation of neuronal activity with "Preference" than with "Performance" would be expected, rather than reflecting a new aspect of "spatial attention". A definition of performance more in line with established practice and measuring side-to-side discrimination (corresponding more closely to the authors' "Preference" parameter) would have shown this more clearly.

Reviewer #1 (Public review):

Summary:

The authors studied the development of hippocampal connectivity gradients based on open datasets and performed correlation analyses with other MRI features as well as gene expression information from other datasets. Although the main findings are correlational and cross-sectional, the analyses are overall sophisticated and replicated in several datasets.

Strengths:

The hippocampus is a key region in understanding large-scale brain organization and cognition, and the authors applied advanced and suitable analytics to study its development. The paper is overall well-organized and well-written, and the findings are relevant for studying large-scale brain development.

Weaknesses:

While sophisticated, several of the analyses appear mainly correlational, cross-sectional, and rely on cross-dataset contextualization, which should also be stated as a limitation of the current work.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors aim to assess how the functional organisation of the hippocampus is related to the geometry and neurobiological differences of the hippocampus. In particular, the authors focus on the first three eigenvectors of hippocampal-cortical functional connectivity, based on non-linear dimensionality reduction on resting-state functional MRI data. Furthermore, the work aims to describe changes in these functional axes and their relation to other factors throughout youth and evaluate whether they are predictive of individual variations in cognition.

Strengths:

A major strength of this study is the attempt to replicate key findings across multiple developmental cohorts.

Weaknesses:

The major weaknesses of the manuscript center on gaps in technical transparency and several conceptual inaccuracies. The machine learning methodology used for cognitive prediction is scarce, leaving little means to evaluate whether the behavioral results suffer from data leakage or overfitting. The introduction sets up an oversimplified historical premise regarding the field's understanding and appreciation of hippocampal connectivity, and contains several incorrect references that throw doubt on the argumentation. Additionally, T1w/T2w signal intensity is incorrectly used as synonymous with myelin, despite gold-standard histological validation showing a non-significant correlation between T1w/T2w and myelin staining (Sandrone et al., 2013).

Appraisal of Aims and Conclusions:

The authors partially achieve their aims by illustrating certain age-related changes in hippocampal function; however, the correlative study design is not equipped to examine how these changes are "shaped" by geometry, myelination, or gene expression (especially the latter two). Furthermore, conclusions were often overstated based on small effect sizes.

Context and Field Impact:

This work adds to a growing body of literature focused on gradient-based representations of hippocampal topology. By applying these methods across a wide developmental age bracket, it provides a useful reference point for how the hippocampus and wider cortex interact during maturation. To improve utility to the neuroimaging and cognitive neuroscience communities, the nesting of subfields within the eigenvector topology should be addressed, too.

Reviewer #1 (Public review):

Summary:

Mudunuri et al. investigate the foraging response of Drosophila larvae in response to patchy resources of distinct value (concentration of nutrient or valence). They show that larvae adjust their behavior according to both the quality and valence of available resources. Interestingly, previous exposure to resources of lower value increases the permanence time in resources of greater value. This suggests that larvae can value, remember and adapt their behaviour in response to previous foraging experience.

They perform a simple integration model that recapitulates the larval behaviour.

Strengths:

This paper uses a very well-controlled foraging set-up where larvae are tested individually and for 3 hours, allowing for a good statistical analysis of their behaviour.

They investigate for the first time the ability of Drosophila larvae to perceive, remember and compare the quality and valence of distinct resources. It is very exciting, as it will open up the field of foraging decision studies using the fruitfly larvae.

Weaknesses:

(1) Most of the analysis depends on the thresholding, but it is not clear what increasing the radius of analysis means in terms of foraging. There are two issues here:

a) What is the behaviour of the larvae on the edges of the patch? It is obvious that the fructose or the NaCl will diffuse at the edge, so are they remaining in the proximity because they are actively feeding (exploiting) on this decaying concentration, or are they sensing the lower gradient and they are actually looking (chemosensing) for the higher concentration? The behaviour at the edge is really different (check sucrose in Wosniack et al. 2022), and there might be a way of avoiding the diffusion by actually adding a plastic ring and pouring the agar + resource in there. The effect of the ring, per se, would still have to be tested.

b) How was the threshold selected? It is very likely that the concentration at the patch boundary will be very different for 1M and 0.1 M. Could the authors explain why they chose such a distance? What does majority of larvae mean? Is the "majority" the same for 0.1M and 1M? Is there a relationship between the threshold chosen and the diffusion of fructose and NaCl?

(2) The word exploitation is used in the paper, but there are many instances where it is unclear whether that is the case. This should be clarified since there are no controls for exploitation.

(3) In the experiments analysing the adaptation of foraging behaviour, it is not clear if the first and second patch means that only 2 patches were analysed per larva or the first and second in a sequence of patches visited. I think it is the second option (because of Figure S3D), but the authors should clarify this. Also, we do not know how many animals were tested. The number of data points in 4C (4G) compared to 4D (4H) seems very different.<br /> Regarding the results, which are very interesting, why aren't the larvae spending less time in the 0.1M sucrose patch after having fed on a 1M patch, while they spend more time in a 1M after a 0.1M? Could it be that the difference in residence time is correlated with their hunger rather than the comparison between conditions?

(4) I am not an expert in this type of model, and I would appreciate it if the authors could explain how the values of the drift and leak have been fitted in Figure 5H. If possible, I would recommend adding a graph showing the parameter exploration of distinct possible combinations of values.

Reviewer #2 (Public review):

Summary:

This manuscript investigates how Drosophila larvae make foraging decisions in patchy environments with controlled resource density and valence. Using movement tracking in bounded arenas, the authors show that larvae's patch residence time (PRT) differs depending on resource type, environmental context, and prior experience.

The authors vary whether the environment is homogenous (all patches are equal) or heterogenous (mixed patches) and whether a higher density of the resource is appetitive (food) or aversive (salt). The most salient results are that in heterogeneous environments, larvae remain longer on higher-density patches of fructose, while they stay shorter in higher-density salt patches. The study further demonstrates that prior foraging experience influences subsequent patch residence time (PRT).

A drift-diffusion model is used to describe patch-leaving behavior, suggesting that an integration process may underlie stay-leave decisions during foraging. Overall, the work provides a useful behavioral system for studying foraging behaviour and highlights the role of context and experience in shaping larval foraging strategies.

Strengths:

A major strength of the manuscript is the behavioral system. The assay is simple, well-controlled, and suitable for realistic spatial and temporal scale tracking of individual larvae. The use of non-volatile resources and embedded patches minimizes confounds from olfactory navigation and allows the authors to focus on local patch exploitation, return behavior, and experience-dependent decisions.

The results regarding patch resident time (how long larvae stay in patches of different resource density) are convincing. In homogeneous environments, larvae spend more time on patches with a higher density of food (0.1M > 0.01M) and less time in patches with a lower density of salt (0.01M > 0.1M), indicating that their behaviour is sensitive to the valence of the resource. Further, larvae do not simply respond to current circumstances, since PRT in a given patch is sensitive to the quality of the preceding one encountered, showing some kind of memory.

Weaknesses:

(1) The theoretical background of the experiment, as exposed in the Introduction, is somewhat misleading. The experiment is based on patches of sufficient size for the individual larvae not to deplete them through their activity, so that the intake rate is constant while exploiting a given patch. In those circumstances, the theoretical rate-maximizing strategy would be to either reject a patch on encounter or stay in it indefinitely (until pupation). The threshold for rejection or acceptance will depend on travel time, but patch residence time would be either zero (or minimal identification time) or lifelong. In the introduction, it appears as if the system follows the classical Marginal Value Theorem assumptions as used in classical foraging theory. In that case, patch residence time is fundamentally sensitive to a decline in intake rate while in a patch. This raises questions about what factors drive patch-leaving in the present protocol. A better theoretical framework would focus on behavioural variables that can be expected to depend on the circumstances of the experiment, as discussed below.

(2) Rather than make predictions about time in the patch, which as explained above do not reflect the present system, larval behaviour could be modelled and described as a function of observable properties such as: (a) speed of locomotion; (b) tendency to deviate from straight progress (area restricted searching); (c) probability of return after leaving a patch, possibly controlled through rea restricted searching; (d) a response to concentration gradient, since patch boundaries are probably gradual through diffusion. There is a useful literature in this regard in studies of parasitic wasps such as Venturia canescens (formerly Nemeritis canescens, see Waage 1979). Larva may respond directly to local resource concentration (see van Alphen, J. J., Bernstein, C., & Driessen, G., 2003), where higher concentration leads to increased feeding rate, reduced locomotion, and consequently results in longer time in each patch. This could still be a normative model, but based on realistic driving inputs. The dimensions of the system make it unlikely that larvae have the opportunity to adjust to travel time, or patch composition, on which classical foraging models are based. The original versions of the marginal value theorem were thought for cases where birds exploited pine cones, so that each bird had multiple encounters, and also on dung flies that mated in dung patches, which also dried out. A system with heritable optimised parameters could work for other natural systems where the parameters can be heritable, but not here.

(3) The previous argument indicates that patch time, while it is a real quantitative consequence, is not ideal as the major dependent variable for this system. Given that the authors have the full trajectories, they could treat movement in discrete time bins and ask if the tendency to depart from linear progression (i.e. from moving straight ahead) is a function of the density of the resource. It would appear as if all the results, including return to patches (but not memory), could be explained by area-restricted searching (see Dorfman, A., Hills, T. T., & Scharf, I. (2022). A guide to area‐restricted search: a foundational foraging behaviour. Biological Reviews, 97(6), 2076-2089.). Slower movement (perhaps directly caused by eating) and more twisted progress could generate longer times in higher food densities.

(4) The evidence for an effect of prior experience is interesting but could be strengthened. The authors state that PRT on the second patch depends on the concentration in the first patch. However, statistically significant modulation of prior experience was only found when the second food patch was richer, namely 1M fructose (Figure 4C). If the change in patch time is due to a form of learning and contrast, one might expect significantly shorter times in any second patch if the first one was richer, which is not the case. One difficulty is that the 'patchy' nature of the environment may not be evident to the larvae, because they are much smaller than the patches. From a larva's perspective, a patch is an environment, potentially suitable to remain in until pupation (which is what they ought to do in richer food patches).

(5) The modelling section is promising but currently somewhat underdeveloped relative to the strength of the claims. The authors fit a drift-diffusion model to data and report that a drift-only model captures homogeneous environments, whereas adding a leak term improves the fit in heterogeneous environments. This provides a useful quantitative summary of behavior but the biological interpretation of the leak parameter is not clear. In addition, the valence condition was not modelled.

Reviewer #3 (Public review):

Summary:

The work investigates how the foraging behaviour of Drosophila larvae depends on resource quality, valence, and heterogeneity in the foraging environment. A specific focus of the work was to study how foraging decisions depend on the prior experience of alternative resource patches in the same environment. Moreover, the work presents computational models (drift diffusion models) that recapitulate foraging decisions, and whose parameters appear to depend on resource quality and environment statistics, providing potential insights into the dynamics of the decision-making process.

I am not familiar with previous literature on foraging decisions in Drosophila, but I was specifically consulted to comment on the computational modelling. Therefore, my comments will mostly focus on the modelling aspects.

Strengths:

In my understanding, the two strengths of the current study are that:<br /> (1) it uses non-volatile resources, providing better control of the available cues that could guide foraging decisions, and<br /> (2) it tracks foraging behaviour over an extended period of time (3h), generating a rich dataset of foraging behaviour in the same environment.

Overall, the study appears to have been carefully conducted.

Weaknesses:

The computational modelling currently provides limited additional value beyond the empirical results. There are no prior hypotheses that are addressed by the computational models. Given the flexibility of DDMs, fitting foraging times is expected to be feasible. The question is whether the fits provide mechanistic insight. The main insight appears to be that describing foraging times in a homogeneous environment requires a single free parameter (drift rate), while the heterogenous environment requires a second parameter (leak). However, the effective complexity of the model is higher than the stated parameter count suggests, as each patch quality is fit with a different drift rate, which does not generalise across environments: in the heterogeneous environment, the drift rate differs substantially across fructose concentrations, whereas in the homogeneous environment, the same concentrations yield nearly identical drift rates. Counter their claims, the authors also do not systematically explore the effect of specific prior foraging experience on computational parameters, but only contrast model fits to environments with different statistics, in which prior experiences will be generally different. Overall, at the moment these modelling results have a rather descriptive character, and provide very little insight into the underlying computational principles that drive foraging decisions.

A second weakness is that the study does not report the detailed results of the statistical tests, and it seems that the authors interpret several differences that are not marked as statistically significant in the figures. Furthermore, the model comparisons do not account for different degrees of freedom of the models, and the goodness of fit values alone are insufficient to conclude that one model is better than the other (rather than overfitting).

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors address the question of working memory maintenance, starting from the experimental observation that recordings of neural activity during the delay period of working memory tasks are sometimes observed to be dynamic. They introduce a new combination of metrics (noise-robustness and energy efficiency) to quantify the performance of various network mechanisms of memory maintenance, in linear networks. They compared attractor networks, feed-forward networks, and networks trained with a loss that includes a robustness and an energy-efficiency component. They show, by plotting state-space trajectories, that networks optimized with this loss exhibit a form of rotational dynamics. They analyzed the data recorded during the delay of a working memory task in PFC, and observed state-space trajectories similar to those of the trained networks.

The comparison with other network mechanisms is interesting in principle, but limited by the fact that only linear networks are considered. This led to counter-intuitive and misleading statements, like the fact that attractor networks are not robust to noise, or that feed-forward networks have energy consumption that is exponential in the number of neurons.

Strengths:

(1) The idea to use both robustness to noise and energy efficiency to assess the performance of networks on working memory tasks is interesting.

(2) The manuscript is clearly written.

(3) There is an interesting combination of methodologies: theory on simple models, network training, and data analysis.

Weaknesses:

(1) Linear networks only.

The main feature of attractor networks is their robustness to noise, which is typically allowed by the non-linearity of neural responses. To fit their modeling framework, the authors focused only on continuous attractor neural networks (e.g., Seung 1996) and ignored point-attractor models such as the Hopfield model, which are typically used to model WM tasks, and which would presumably lead to very different results, e.g., in Figure 1D.

The linearity assumption is also problematic for the comparison with feed-forward models. It seems that the authors obtained runaway firing rates, explaining Figure 1F middle, which are typically prevented in non-linear networks.

The choice of parameters for the attractor network in Figure 1 is not explained. Why is t_slow = 10^4 chosen, and what does it correspond to? We expect in linear networks that activity goes back to zero or diverges as an exponential, but in principle, the time constant can be chosen to be of the same order as the time delay, with approximately linearly decreasing SNR.

Regarding the comparison of the different mechanisms, it would have been nice to better define the notion of rotational dynamics, beyond only considering state-space analysis, which is limited to providing mechanistic interpretations.

(2) Fixed duration of delay periods.

I have understood that for a given network, the duration of the delay period is fixed, as opposed to a delay duration that would fluctuate from trial to trial. This would be an important assumption to relax as well, to better match common experimental paradigms, as well as to expose a fairer comparison with other network mechanisms. See Orhan and Ma (2023) for such a discussion.

(3) Relationship with previous works

Many other works addressed the question of dynamic firing rates during maintenance periods of WM tasks; they should be discussed and compared to the mechanism proposed here. This includes: Barak et al, Progress in Neurobio. 2013, Pereira-Obilinovic, Aljadeff, Brunel, PRX 2023, Hansel, Mato, 2013, or works pertaining to the activity-silent neural states (allowed by short-term plasticity), the framework in which the data of Panichello et al are interpreted in the original publication.

Reviewer #2 (Public review):

In this manuscript, Ritter et al. propose a model of working memory (WM) that combines feedforward and rotational dynamics. The model is discovered by optimizing a linear RNN using a loss function that encourages maximization of signal-to-noise ratio (SNR) and minimization of activation magnitude. The authors argue that the optimized model outperforms other WM models in terms of SNR and energetic efficiency, while also better replicating key features of neural responses recorded in monkey pre-frontal cortex (PFC) during a WM task. The authors also draw connections to state space models (SSM) used for other machine learning applications.

My main issue with this manuscript is that it does not appear to convincingly demonstrate that rotational dynamics offer any advantage over purely feedforward dynamics. The authors adopt three criteria according to which they compare models:<br /> (1) SNR.<br /> (2) Energy efficiency.<br /> (3) Similarity to neural data.

In terms of SNR, purely feedforward models seem to perform similarly to the optimized models (Figure 1). Figure 1 does seem to show that the optimized network produces responses of smaller magnitude when the number of units is large, but the authors do not explain why adding rotational dynamics would produce such a relationship. In fact, the responses that are plotted for the feedforward network in Figures 1B, 2C, and 5E look similar, if not smaller in magnitude than those of the optimized model. Lastly, while the authors claim in the body of the text that the optimized model replicates key features of monkey PFC responses better than the purely feedforward model, this is not apparent to me from the comparisons plotted in Figure 5E-J. The authors thus do not show strong evidence that the model they propose beats what they claim is an established baseline on any of the three criteria.

Another weakness of the manuscript is that the comparison to attractor and feedforward models seems somewhat unfair. In Figure 1, the rotational model is optimized, while the parameters for the attractor and feedforward models seem to have been at least partially chosen by hand. Figure 5C again shows the three models side by side, but the fact that it compares the same network at different stages during training complicates the comparison. Instead, one should compare the rotational solution to the optimal attractor and feedforward models, respectively (obtained by constrained optimization). From looking at the flow-fields, it seems that a feedforward network with an optimized level of amplification may work just as well. On a mechanistic level, it is unclear what computational advantage rotations offer over feedforward dynamics in the WM context.

The choice of baseline models to compare against might be questionable. The simple line attractor model by Seung et al. (1996) was initially designed to explain oculomotor integration. It is true that a line attractor has been suggested as a mechanism for working memory, e.g., in the seminal work by Machens et al (2005). However, it seems fair to say that most studies employing non-linear networks have focused on point attractors as mechanisms of working memory (e.g., Wong & Wang, 2006; Driscoll, Shenoy, Sussillo, 2024). A point attractor arguably does not suffer the SNR issues of a line attractor, because it does not lead to integration of the noise over time. However, non-trivial point attractors cannot be implemented in linear networks of the kind studied by the authors of the present study.

The authors should expand their discussion to include other, potentially closely related work proposing rotation-like dynamics in artificial neural networks during working memory. In particular, the manuscript does not discuss Sharma, Proca, et al, ICML 2026, which describes a rotational solution to a similar WM task obtained by optimizing linear RNNs (Sharma et al., 2026, Fig. 6). Notably, Sharma et al. arrive at a similar rotational (and likely also non-normal) mechanism without using either noisy inputs or a constraint on energy efficiency. The authors of the present manuscript should discuss to what extent this finding contradicts their claim that "normative pressures on noise-robustness and energetic cost shape the complex dynamics of WM circuits." (present manuscript, Introduction). Given the obvious parallels between the two studies, a comparison between the present work and Sharma et al. (2026) would add necessary context to the Discussion.

The authors should also clarify the significance of the "novel method for optimization of continuous-time RNNs driven by noisy inputs" (see Discussion) that the authors propose. This method is mentioned in the first line of the Discussion section but is barely discussed, let alone sufficiently explained, in the previous Sections. The only time a comparison to BPTT with a simple MSE loss is mentioned, it is stated that the two procedures produce the same results. The novel method appears to consist of a loss with two terms, the second of which is a well-known L2-penalty on unit activations (Sussillo et al., 2015). It is not clear that the method is either novel or necessary to obtain the reported results.

Except for the fact that higher-dimensional networks also converge on rotational solutions, Figure 3 does not add much to the reader's understanding of the optimized model (except for panel F). I find the comparison to SSMs too superficial to provide real insight.

Figure 4 claims to show that the optimized model recapitulates "a range of properties observed in prefrontal cortex and other brain areas during WM tasks" (p. 7) but does not show neural data for comparison.

Reviewer #3 (Public review):

Summary:

The authors optimize continuous-time linear recurrent networks driven by noisy input, computing the gradient of decoding performance numerically and analytically. Optimizing for stimulus discriminability after a delay, with a penalty on firing rate, they find networks that adopt what they call high-dimensional rotational dynamics. They argue that these outperform attractor and feedforward models on noise robustness and energetic cost, and resemble state-of-the-art state-space models. They then fit a targeted dimensionality reduction model to prefrontal recordings from monkeys performing a spatial working memory task and argue that the population structure matches the rotational solution.

Strengths:

The evolution of the dynamics throughout learning is a nice observation, as are the analytical calculations, although I am not sure they are new since there is a fair share of work on the learning dynamics of linear networks.

Weakness:

I see many weaknesses. I will classify them into five groups.

(1) Strawman comparison and no clear definition of what is rotational. The paper is centered on comparing a trained model with two models meant to represent "attractor dynamics" and non-normal dynamics. Both are picked as the weakest member of their class.

I use quotation marks for "attractor dynamics" because I am not sure a linear system with an eigenvalue equal to zero is a representative model for the class. This is a particular linear instantiation of the line attractor from Seung 1996, but most attractor models are nonlinear and far more robust to noise, and they are robust through error correction that this linear model does not have. Even modern continuous attractors (Rivkind and Darshan) are very robust to noise through multiple mechanisms. So what the authors picked as an "attractor model" is a limited zero-eigenvalue case that, of course, will drift. "Attractor networks are highly susceptible to noise" is therefore true only of the toy they built, not of the class.

Second, what they call a non-normal model is in fact a feedforward chain, the extreme of non-normality. There are degrees of non-normality in any matrix, and the homogeneous delay line is the corner that requires the largest firing rates. This is not representative. See Daie et al., which has a skip and recurrent structure, or Stroud, which is not a pure chain. So the feedforward chain was also picked as a strawman, chosen so that the energetic cost they then complain about is guaranteed.

This brings me to the real problem in this section. "Rotational" is never defined. If it means complex eigenvalues, then it is a spectral property of any non-normal matrix, and "rotational versus feedforward" is not a dichotomy; it is two regions of the same continuous space of non-normal connectivity. Their own Figure 2C shows the network passing continuously through an attractor, then feedforward, then rotational during optimization. If these are points on a continuum, then "rotational dynamics is optimal" is just a statement about where the optimizer lands under this particular loss and input normalization, not the discovery of a new dynamical class. They need to define the term operationally and show the solution is qualitatively, not just quantitatively, different from non-normal feedforward. I do not think it survives that test.

This brings me to the references.

(2) The dynamical mechanisms of working memory have been studied for more than two decades, and I am surprised how much directly relevant work is missing. First, Druckmann and Chklovskii 2012, where a linear system produces stable encoding from oscillating modes. This is essentially their result more than a decade earlier, and it is not cited. They also miss Murray et al. on stable encoding and heterogeneous timescales in data. They oversimplify the attractor picture; for example, Pereira-Obilinovic et al. 2023 show you can have genuinely stable attractors. They do cite Daie et al., but they ignore its central claim, that non-normality is the underlying mechanism, which is more troubling than not citing it because it means they read it and did not engage. Overall, the references are idiosyncratic, missing relevant work, and not engaging the results of papers they cite.

This brings me to the third point.

(3) Novelty and the relationship to Stroud and Orhan. Those papers take a similar optimization approach and find that, depending on the task parameters, the optimal solution is non-normal, non-normal plus attractor, or attractor. My impression is that what this work calls rotational is just the dynamics of a strongly non-normal A, selected here by the firing-rate regularizer. They never clarify the connection with Stroud. Is the only difference the energy penalty?

The way to settle this is quantitative, and they have the handle and do not use it: report the Henrici departure-from-normality of their optimized A and place the solution inside Stroud's regime structure.

There is also a tension they leave implicit. In Stroud, the early loading direction is orthogonal to the late persistent readout, and that orthogonality is the source of dynamic coding. This paper's subspace alignment result (Figure 5G, H) shows exactly this early-to-late orthogonalization in both model and data, and then presents it as evidence for the rotational account and against Stroud's hybrid. You cannot reproduce a Strout's stim vs. decoder orthogonality and claim it against Strout's without doing more work.

(4) I did not understand the SSM section, and I think it should be cut. Is this a result? Either "SSM" just means a linear dynamical system, in which case it is trivial since every linear network here, including the LMU is an SSM, or it means the network matches a fixed-connectivity model like the LMU, which it does not seem to either. So in what sense is it a result?

(5) The data analysis is one section, and the analysis could be described as feeling somewhat like an afterthought on a very rich dataset. The coding structure they show for the rotational model also looks like the Stroud non-normal-plus-attractor model to me. They even state that the hybrid reproduces the cross-temporal subspace. What are the quantitative, cross-session metric that discriminates rotational from the non-normal-plus-attractor hybrid? Is it eyeballed trajectories?

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:

In this manuscript, the authors present comprehensive experimental observations and a theoretical framework to explain the heterogeneous behaviour of sarcomeres in cardiomyocytes. They show that a stochastic component exists in their contractile activity, which may act as a feedback mechanism regulating physiological function.

Strengths:

Experiments and data analysis are robust and valid. The rigorous statistical analysis and unbiased methods enable the authors to draw well-supported conclusions that go beyond the existing literature. Their outcomes inform about cellular activity at the individual level and the authors explain how the transient dynamics of single sarcomeres are governed by a force-velocity relationship and lead to the complex contractile patterns. The similarity of the results to the study cited in [24] demonstrates the validity of the in vitro setup for answering these questions and the feasibility of such in-vitro systems to extend our knowledge of out-of-equilibrium dynamics in cardiac cells.

Very interesting the suggestion that the interplay between intrinsic fluctuations and the dynamic instability are part of a feedback mechanism for maintaining structural and functional homeostasis.

The addition of the theoretical model and the new text of the manuscript improves the clarity of the study.

Reviewer #2 (Public review):

Summary:

Sarcomeres, the contractile units of skeletal and cardiac muscle, contract in a concerted fashion to power myofibril and thus muscle fiber contraction.

Muscle fiber contraction depends on the stiffness of the elastic substrate of the cell, yet it is not known how this dependence emerges from the collective dynamics of sarcomeres. Here, the authors analyze contraction time series of individual sarcomeres using live imaging of fluorescently labeled cardiomyocytes cultured on elastic substrates of different stiffness. They find that a reduced collective contractility of muscle fibers on unphysiologically stiff substrates is partially explained by a lack of synchronization in the contraction of individual sarcomeres.

This lack of synchronization is at least partially stochastic, consistent with the notion of a tug-of-war between sarcomeres on stiff sarcomeres. A particular irregularity of sarcomere contraction cycles is 'popping', the extension of sarcomers beyond their rest length. The statistics of 'popping' suggest that this is a purely random process.

Strengths:

This study thus marks an important shift of perspective from whole-cell analysis towards an understanding the collective dynamics of coupled stochastic sarcomeres.

Reviewer #3 (Public review):

The manuscript of Haertter and coworkers studied the variation of the length of a single sarcomere and the response of microfibrils made by sarcomeres of cardiomyocytes on soft gel substrates of varying stiffness.

The measurements at the level of a single sarcomere are an important new result of this manuscript. They are done by combining the labeling of the sarcomeres z line using genetic manipulation and a sophisticated tracking program using machine learning. This single sarcomere analysis shows strong heterogeneities of the sarcomeres that can show fast oscillations not synchronized with the average behavior of the cell and what the authors call popping events which are large amplitude oscillations. Another important result is the fact that cardiomyocyte contractility decreases with the substrate stiffness, although the properties of single sarcomeres do not seem to depend on substrate stiffness.

The authors suggest that the cardiomyocyte cell behavior is dominated by sarcomere heterogeneity. They show that the heterogeneity between sarcomere is stochastic and that the contribution of static heterogeneity (such as composition differences between sarcomeres) is small.

Strengths:

All the results are, to my knowledge, new and original. The authors also made a theoretical model where each sarcomere is described by a Langevin equation based on a non-linear coupling between force and velocity of the sarcomeres. This model accounts well for the experimental results including the observation of what the authors call popping events.

Reviewer #1 (Public review):

Summary:

Dad et al. explored the roles of cytosolic carboxypeptidase 5（CCP5）in the development of ependymal multicilia in the brain. CCP family are erasers of polyglutamylation of ciliary-axoneme microtubules. The authors generated a new mutant mouse of Agbl5 gene, which encodes CCP5, with deletion of its N-terminus and partial carboxypeptidase (CP) domain (named AGBL5M1/M1).

Strengths:

The mutant mice revealed lethal hydrocephalus due to degeneration of ependymal multicilia. Interestingly, this is in contrast with the phenotype of Agbl5 mutants with disruption solely in the CP domain of CCP5 (named AGBL5M2/M2) that did not develop hydrocephalus despite increased glutamylation levels in ependymal cilia as observed for AGBL5M1/M1 mutants. The study has been well-performed and the findings suggest a unique function of the N-domain of CCP5 in ependymal multicilia stability.

Weaknesses:

The content of this article is relatively descriptive and lacks molecular insights, regarding the function of the CCP5 N-domain.

Comments on revised version.

The authors have appropriately revised the manuscript in response to most of my comments.

Reviewer #2 (Public review):

Summary:

This study analyzed consequences of Agbl5 mutation on ependymal cells development and function. Authors first characterize their mutant mouse line reporting a reduced lifespan and severe hydrocephalus. Next, they report defect in ependymal cell cilia number and motility. They provide evidence for impaired basal bodies organisation, cilia glutamylation.

Strengths:

Description of a mutant mouse which implicate Cytosolic Carboxypeptidase 5 (the product of Agbl5 gene) for proper ependymal cells.

Weaknesses:

Description of phenotype are incomplete:

Previous comment: Microtubules are involved in the local organization of ciliary basal bodies (see Werner et al., Vladar et al.,2011; Boutin et al., 2014). It would be interesting that the author checks whether the subapical network of microtubule is glutamylated or not during ependymal cells differentiation and how this network is affected in their mutants.

Although authors now provide images of glutamylation in figure S8 their conclusion claiming that GT335 signal is increased in cilia of Agbl5M1/M1 mutant is not supported convincingly by those pictures. Quantification would be needed.

Reviewer #3 (Public review):

Summary:

The authors developed a new Agbl5 KO allele by extending the deletion to the N-terminus of CCP5 to investigate its function in mouse ependymal cells and trachea.

Strengths:

They show that the KO mice exhibit severe hydrocephalus due to disorganized and mislocated basal bodies. Additionally, they present evidence of both impaired beating coordination and a reduction in ciliary beating.

The manuscript is well-written, and the experiments are convincing.

Comments on revised version.

The authors have taken all of my comments into account and have revised their manuscript to my satisfaction.

Reviewer #1 (Public review):

Summary:

Gruskin and colleagues use twin data from a movie-watching fMRI paradigm to show how genetic control of cortical function intersects with the processing of naturalistic audiovisual stimuli. They use hyperalignment to dissect heritability into the components that can be explained local differences in cortical-functional topography and those that cannot. They show that heritability is strongest at slower-evolving neural time scales, and more evident in functional connectivity estimates than in response time series.

Strengths:

This is a very thorough paper that tackles this question from several different angles. I very much appreciate the use of hyperalignment to factor our topographic differences and found the relationship between heritability and neural time scales very interesting. The writing is clear and the results are compelling. In general, I don't have many complaints after a couple reads through the manuscript; most of my comments below are relatively minor suggestions and points of clarification.

Weaknesses:

The only "weaknesses" I identified were some points where I think the methods, interpretation, or visualization could be clarified:

On page 16, you compare heritability in functional connectivity (FC) and response time series and find that the heritability effect is larger in FC. In general, I agree with your diagnosis that this is in large part due to the fact that FC captures the covariance structure across parcels, whereas response time series only diverge in terms of univariate time-point-by-time-point differences. Another important factor here is that (within-subject) FC can be driven by intrinsic fluctuations that occur with idiosyncratic timing across subjects and are unrelated to the stimulus (whereas time-locked metrics like ISC and time-series differences cannot, by definition). This makes me wonder how this connectivity result would change if you used intersubject functional connectivity (ISFC) analysis to specifically isolate the stimulus-driven components of functional connectivity (Simony et al., 2016). This, to me, would provide a closer comparison to the ISC and response time series results, and could allow the authors to quantify how much of the heritability in FC is intrinsic versus stimulus-driven. I'm not asking that the authors actually perform this analysis, as I don't think it's critical for the message of the manuscript-but it could be an interesting future direction. As the authors discuss on page 17, I also suspect there's something fundamentally shared between response time series and connectivity as they relate to functional topography (Busch et al., 2021) that drives part of the heritability effect.

The observation that regions with intermediate ISC have the largest differences between MZ, DZ, and UR is very interesting, but it's kind of hard to see in Figure 1B. Is there any other way to plot this that might make the effect more obvious? For example, I could imagine three scatter plots where the x- and y-axes are, e.g., MZ ISC and UR ISC, and each data point is a parcel. In this kind of plot, I would expect to see the middle values lifted visibly off the diagonal/unity line toward MZ. You could even color the data points according to networks like in Figure 3C. (You also might not need to scale the ISC axis all the way to r = 1, which would make the differences more visible.)

On page 9, if I understand correctly, you regress the vector of ISC values across parcels out of the vector of heritability values across parcels and then plot the residual heritability values. Do you center the heritability values (or include some kind of intercept) in the process? I'm trying to understand why the heritability values go from all positive (Figure 2A) to roughly balanced between positive and negative (Figure 2B). Important question for me: How should we interpret negative values in this plot? Can you explain this explicitly in the text? (I also wonder if there's a more intuitive way to control for ISC. For example, instead of regressing out ISC at the parcel/map level, could you go into a single parcel and then regress the subject-level pairwise ISC values out when computing the heritability score?)

On page 4 (line 155), you say "we shuffled dyad labels"-is this equivalent to shuffling rows and columns of the pairwise subject-by-subject matrix combined across groups? I'm trying to make sure your approach here is consistent with recommendations by Chen et al., 2016. Is this the same kind of shuffling used for the kinship matrix mentioned at line 189?

I found panel A in Figure 4 to be a little bit misleading because your parcel-wise approach to hyperalignment won't actually resolve topographic idiosyncrasies across a large cortical distance like what's depicted in the illustration (at the scale of the parcels you're performing hyperalignment within). Maybe just move the green and purple brain areas a bit closer to each other so they could feasibly be "aligned" within a large parcel. Worth keeping in mind when writing that hyperalignment is also not actually going to yield a one-to-one mapping of functionally homologous voxels across individuals: it's effectively going to model any given voxel time series as a linear combination of time series across other voxels in the parcel.

References:

Busch, E. L., Slipski, L., Feilong, M., Guntupalli, J. S., di Oleggio Castello, M. V., Huckins, J. F., Nastase, S. A., Gobbini, M. I., Wager, T. D., & Haxby, J. V. (2021). Hybrid hyperalignment: a single high-dimensional model of shared information embedded in cortical patterns of response and functional connectivity. NeuroImage, 233, 117975. https://doi.org/10.1016/j.neuroimage.2021.117975

Chen, G., Shin, Y. W., Taylor, P. A., Glen, D. R., Reynolds, R. C., Israel, R. B., & Cox, R. W. (2016). Untangling the relatedness among correlations, part I: nonparametric approaches to inter-subject correlation analysis at the group level. NeuroImage, 142, 248-259. https://doi.org/10.1016/j.neuroimage.2016.05.023

Simony, E., Honey, C. J., Chen, J., Lositsky, O., Yeshurun, Y., Wiesel, A., & Hasson, U. (2016). Dynamic reconfiguration of the default mode network during narrative comprehension. Nature Communications, 7, 12141. https://doi.org/10.1038/ncomms12141

Comments on revised version.

The authors have adequately addressed my previous comments. This is a strong contribution: the methods are sophisticated, the statistical treatment is rigorous, and the results are quite interesting/compelling. I'm happy to endorse the revised manuscript as a finalized version.

Just to confirm: The subjects watched all different movies across the two days, right? For a moment I was wondering "are Day 1 and Day 2 repetitions of the same movies?" Given that Day 1 and Day 2 are an organizational feature of several figures, it might be worth making this very explicit in the Methods and reminding the reader in the Results section.

Reviewer #3 (Public review):

Strengths:

It's sort of novel to study the heritability of movie-watching fMRI data. The methodology the authors used in the paper is also supportive of their findings. Figures are nicely organized and plotted. They finally found that sensory processing in the human brain is under genetic control over stable aspects of brain function (here referring to neural timescale and resting state connectivity).

Weaknesses:

What I am worried about most is the sample size and interpretation of heritability.

(1) Figure 1. I assumed that the authors just calculated the ISC within each group (MZ, DZ, and UR). Of course, you can get different variations between each group. Therefore, there is heritability. Why not calculate ISC across the whole sample, then separate MZ, DZ, and UR?

(2) Heritability scores in the paper are sort of small. If the sample size is small, please consider p-values, which will tell more about the trustworthiness of your heritability.

(3) I don't understand the high-frequency signals in fMRI data. It's always regarded as noise, the band 1 here in particular.

(4) The statement "we show that the heritability of brain activity patterns can be partially explained by the heritability of the neural timescale" should come from Figure 5. However, after controlling for NT, the heritability decreased max. 0.025 in temporal areas. I am not sure this change supports the statement. If the visual cortex is outlined, and combining ISC changes in the visual cortex, I think this would somehow be answered. Instead of delta h2, adding a new model h2 would be obvious to the readers.

(5) Figures 7 and 8, when getting the difference of heritability, please also consider the standard errors of the heritability estimates. Then you can compare across networks/regions.

(6) I think movie VS resting state is a really important result in this paper. However, there is almost no discussion. Discussing this part would be more beneficial for understanding the genetic control over the neuron arousal and excitation circuits.

Comments on revised version.

The whole manuscript has been improved a lot, and the concerns have been clarified.

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 some of comments raised in the previous round of review and have opted to proceed to a Version of Record without additional review.]

Summary:

This is an excellent and strong paper. The authors not only show the mechanisms of action of destabilizing mutations in VHL, but notably, they also go on to computationally design and experimentally test an inhibitor that restores wild-type pVHL function, offering starting points for a new class of kidney cancer drugs. The approach that the authors take here can be used to target destabilizing mutations in repressor proteins, common in diseases, including cancer.

Strengths:

This paper is the culmination of an extraordinary amount of work, over years, including method development and testing by a broad range of tools and experiments. It is thorough and comprehensive. It is also well-written and easy to follow.

Reviewer #2 (Public review):

Summary:

Inactivating VHL mutations are common in clear cell renal cell carcinoma, and about half of those mutations unfold/destabilize the protein rather than directly interfering with critical protein-protein interactions. The authors identify a compound that can stabilize/refold mutant VHL and seemingly restore its ability to downregulate its major downstream targets.

Strengths:

The authors use a clever combination of virtual and cell-based screens, followed by suitable biophysical and cell-based validation assays, to arrive at a VHL refolder. This compound is suboptimal from an ADME point of view, but could be a starting point for further medicinal chemistry optimization. Success would have implications for other diseases linked to similar loss-of-function mutations.

Weaknesses:

In going from CP4 to CP4.29 the authors screened based on downregulation of HIF. This is logical but also introduces the danger of identifying chemicals that can downregulate HIF in an "off-target" manner i.e. non-specifically. It therefore essential to clearly show that CP4.29 downregulates steady-state levels of HIF and HIF target genes in cells with suitable (hydrophobic core) VHL mutants but not in isogenic cells lacking VHL.

Reviewer #1 (Public review):

Summary:

The authors quantified and compared the 3D kinematics of bill and tongue movements between two seed-eating bird species: one that specializes on soft seeds, and one that is more adapted to feeding on hard seeds. Their goal was to determine specifically what the role of the tongue was for processing (e.g., dehusking) seeds, and to understand how differences in biting strength between species affect other aspects of seed processing. The authors provided intricate (visual) details of seed processing movements, and showed how coordination between the tongue and cranial kinesis (i.e., mobility of the upper bill relative to the cranium) is both critically important for properly positioning seeds to enhance feeding efficiency. Many studies have detailed how seed-eating birds process seeds, but this study has elevated those to a new level of quantification and visualization for readers to fully experience firsthand. Furthermore, the authors established that the force-velocity trade-off that has been observed between bill functions (e.g., feeding and singing) is largely driven by the contractile properties of the muscles. The conclusions are well supported by the results, and the authors placed the results more broadly into the context of manual grasping, making the argument that these birds achieve high levels of dexterity with far fewer degrees of freedom, which could have potential biomimetic applications.

Strengths:

This study builds upon - and advances - our understanding of the feeding mechanics of seed-eating birds using cutting-edge 3-dimensional modeling and kinematics. Their quantitative analyses of upper and lower bill, tongue, and seed displacements are complemented by elegant visualizations of seed processing in each species. Their comprehensive Bayesian modeling statistical framework tackles the issue of small sample sizes (i.e., few subjects) with volumes of data for each (i.e., lots of sequential kinematic variables) that plague comparative biomechanics studies, principally because (a) it is difficult to gather these high resolution XROMM and muscle contractile data on more than just a few subjects, and (b) these data streams are inherently very large, as they are gathered at high frame and sampling rates. Furthermore, I believe their approach to statistically testing for differences between species sets a new standard for our field that could (perhaps should?) be implemented in other similar types of studies. Another strength is in how the results were packaged: each subsection indicated how the objectives were addressed, and there were concluding statements trailing each subsection that helped deliver the key takeaways.

Weaknesses:

A potential weakness is one that the authors themselves mentioned, regarding the body (and skull) size differences between species. Because gape size limits bite force, and given the force-velocity tradeoff in muscle function, there could be limitations on the rapid manipulation of relatively large seeds for similar reasons in the smaller finches. I see that the small finches appear to overcompensate in their beak rotations, but it's not clear how those compensatory movements might affect their seed processing kinematics with their preferred seed sizes. This does not nullify the authors' conclusions, but the results for the smaller finches might not be entirely representative of seed processing mechanics in smaller species.

Reviewer #2 (Public review):

Summary:

This study investigates coordinated beak-tongue movements in seed manipulation, biting, and dehusking in songbirds. A comparative analysis of the seed-eating process in two songbird species with different biting forces, the domestic canary and Java sparrow, was conducted using high-speed XROMM with anatomical marker tracking and quantitative behavioral analysis. The authors have done a great job analyzing upper and lower beak rotation and translation, seed orientation and movement speed, and tongue kinematics.

Strengths:

The methodological approach of using high-speed (500 fps) X-ray reconstruction for 3D kinematic tracking in small animals is novel and powerful. It enables high temporal resolution tracking of orofacial movements and could potentially inspire future orofacial research in mammals, including mice and marmosets. Moreover, this study encompasses a wide range of anatomical components involved in seed manipulation behavior, including the upper and lower beak, the tongue, and jaw muscles. The behavioral quantification of these components is solid. The findings that both the upper and lower beaks contribute to seed processing, that the lower beak exhibits greater up-and-down and left-to-right flexibility than the upper beak during seed processing, and that the tongue plays an important role in transporting seeds into the mouth are all solid conclusions consistent with observations of bird feeding behavior. Nevertheless, it is valuable to confirm and quantitatively characterize these observations experimentally. The videos are excellent and very informative.

Weaknesses:

(1) The paper often resorts to qualitative descriptions (e.g., "a high positive correlation of tongue velocity and seed velocity", "Compared to positioning, the measured velocities of both seed and tongue were much lower") instead of providing exact quantitative measurements or statistical results. The authors stated that temporal autocorrelation biases standard statistical analyses (lines 205-210), but this rationale does not justify the absence of statistical validation. Suggestion: use appropriate methods for time-series data, such as a permutation test, to test the significance of correlations between variables and avoid false positives.

(2) (Minor) The marker-tracking image shown in Figure 1B could benefit from the inclusion of a higher-contrast, zoomed-in frame of the head showing the metal markers without the red tracking points, alongside the same frame with the red tracking points overlaid, to provide readers with a clearer view of the X-ray image and the methodology and its precision.

(3) (Minor: possibly soften the mechanistic claim). The proposed mechanism of lingual papillae on the tongue surface may aid food manipulation and food movement towards the posterior region of the mouth is interesting, yet the evidence describing their morphology is not strong enough to support the claim about their functional roles. Furthermore, the claim that papillae orientation affects food transport in lines 294-296 lacks supporting experimental evidence. In addition, the roles of extrinsic and intrinsic tongue muscles in controlling dexterous tongue shape changes and movements are not discussed.

Reviewer #1 (Public review):

Summary:

The authors seek to understand and identify the neural plasticity that underlies recovery from precise unilateral hemi-pyramidotomy. The corticospinal tract is severed on one side in the pyramids below the exit of corticoreticular projections. Recovery from the injury is achieved with an intensive wheel running rehabilitation regime. The anatomical sites of plasticity, the importance of plasticity in different reticular areas<br /> to recovery, and the impact of the degree of plasticity observed on recovery as correlated predictors, are shown.

Strengths:

Refined anatomical analysis using mouse line and genetic and viral intersectional tracing identifies specific reticular targets of likely enhanced cortical control that correlate with recovery of locomotor skill.

Weaknesses:

(1) The study is correlational at this time. This does not undercut the value of the data and the identification of targets of plasticity achieved in the work.

(2) Generalization of motor gains beyond locomotion was not tested. Reach-to-grasp tasks for feeding were not tested.

(3) Some discussions and use of the terms fine motor and skilled motor are fuzzy, and the limitations of the study are not sufficiently clearly stated.

Reviewer #2 (Public review):

Summary:

Bonanno and colleagues combine unilateral pyramidotomy, continuous voluntary complex-wheel running, whole-brain intersectional CSN tracing, and c-Fos mapping to ask whether rehabilitation reorganizes the supraspinal collaterals of the intact corticospinal tract neurons. The study is technically ambitious and competent, the uPyX + complex-wheel + intersectional-tracing + BrainJ combination is smart and interesting, the behavioral effect is convincing, and the blinding and exclusion criteria are explicit. The central anatomical finding - a CSN-specific, whole-brain projectome comparison with subregional LPGi/GiA/MdV granularity - is a legitimate contribution that builds on Asboth 2018. However, the strength of evidence does not support the strongest causal wording in the current abstract, significance statement, and parts of the discussion: the results remain correlational, the MdV-behavior correlation is modest, and its significance is sensitive to the unit of analysis. A major revision is recommended, primarily of framing and quantitative robustness, rather than because the central dataset is unconvincing.

Strengths:

(1) Technically ambitious and technically competent study addressing a relevant gap: brain-wide mapping of intact-CSN reorganization under continuous voluntary rehabilitation.

(2) The combination of uPyX, complex-wheel running, intersectional tracing, and BrainJ whole-brain projection analysis is novel and well integrated.

(3) Behavioral effect is convincing, blinding, and exclusion criteria are explicit.

(4) The central anatomical finding (CSN-specific whole-brain projectome under rehab, with LPGi/GiA/MdV subregional resolution) is a legitimate contribution that builds on Asboth 2018. The closest recent works (Lemieux et al. 2024, Jeleva et al. 2026) study reticulospinal rather than CSN plasticity and are complementary rather than competing.

Weaknesses:

(1) Causal framing extends beyond what the current evidence supports.

The abstract and significance statement present MdV as a potential mediator, or even a central locus, through which rehabilitation re-establishes descending control of the impaired limb. This is stronger than the evidence. What the paper shows is that CSN collateral projection density in MdV has a mild-to-medium correlation with behavioral recovery, and that this region is already known from prior work (Esposito 2014) to be relevant for skilled forelimb function. That is an interesting anatomical correlation, not a demonstration of mediation. No manipulation of MdV or of MdV-projecting CST terminals is performed; there is no silencing, no pathway-specific perturbation during rehabilitation, and no test showing that the identified sprouting is necessary for recovery. The limitations section acknowledges this, but the prominent claims do not.

(2) The behavioral caveat on what is actually novel.

The cleanest way to state what is genuinely new, clearer than the abstract itself, is this: when a CSN population loses part of its spinal target domain (via contralateral uPyX denervating the opposite cord), some CSNs from the opposite cortex appear to redirect growth into brainstem collaterals (LPGi, GiA, MdV). The compensation is plausibly sufficient to restore gross descending drive to the impaired forelimb, but most probably inadequate for the fractionated, cortico-motoneuronal fine-grain control that the direct CST normally provides. That distinction - recovery of drive and even skilled locomotor control vs. recovery of fine precision - is consistent with the ladder-rung improvements the paper reports (footfall counts are an integrated gross-placement metric) and with the skilled-reaching literature (Esposito 2014 and similar), which suggests precision grip and digit individuation would not be fully recovered by an MdV-centered detour. This note is also translationally important when we ask what humans consider fine motor control, which is mostly object manipulation. Relatedly, the ladder task is "skilled" in the operational sense that it requires cortical control, but the motor output measured (gross paw placement, overreach) is not fine motor function in the sense of digit individuation, grip force modulation, or pellet manipulation. "Skilled" here does not even mean *acquired* skill: classical skilled reaching in rodents involves explicit training to acquire a novel motor program, whereas here mice are only habituated. The brainstem-compensation hypothesis is more comfortable with restoring cortex-dependent gross placement than with restoring acquired fine-motor skills.

(3) The anatomy sample is modest for the precision of the claims.

Projection analysis rests on n = 9 pooled controls, n = 5 uPyX−Rehab, and n = 5 uPyX+Rehab. For a whole-brain subregion analysis, this is not a large dataset, even with the sensible restriction to the Wang et al. spinally-projecting set. The three medullary hits are plausible, but some of the most specific conclusions rely on a relatively small number of animals for its most specific claims. This matters especially for the MdV-behavior correlation.

(4) Normalization enforces a zero-sum structure.

Projection density is normalized to the total CST tract signal. This is a reasonable way to control for tracing variability, but it imposes a relative structure on the data: an apparent increase in one region may partly force an apparent decrease elsewhere. This may matter and has to be looked into by the authors, because the manuscript interprets decreased density in some other targets as meaningful redistribution.

(5) The decision to merge PMn and MdV under a single "MdV" label needs more justification.

Since the discussion relies on prior literature assigning skilled forelimb function to MdV proper, the reader needs to know whether the signal truly localizes there or whether it may partly reflect a neighboring region grouped under the same atlas label. Related to this, laterality would be very informative: since the proposed compensatory route is anatomically directional, showing whether the increased signal is preferentially located on the expected side of the medulla would strengthen the interpretation.

(6) The c-Fos / Fig. 3 section goes beyond what the data directly support.

The section "Complex-wheel running recruits intact corticospinal neurons" and the figure title "Rehabilitation functionally recruits intact CSNs" go beyond the actual observation, which is that a higher fraction of CSNs in M1 and M2 are c-Fos+ in runners than in non-runners. "Functionally" is not supported: c-Fos is a transcriptional marker of recent activity, not a functional readout; it does not show that the CSN's output is used to drive behavior. "Rehabilitation" is not supported either: the contrast is runners vs non-runners, applied uniformly across Sham and uPyX groups - healthy Sham+Rehab animals are on wheels for leisure, and the c-Fos effect is present in them too. The finding is difficult to interpret without thinking of the simpler framing ("moving mice have more motor cortex activity than resting mice"), with no control for generic arousal or ambulation. This section is the softest link in the causal chain running - CSN activity - medullary sprouting - recovery.

(7) MdV-recovery correlation: unstated multiple-comparison correction and possible pseudoreplication.

The correlation (R² ≈ 0.33, p ≈ 0.01) is the backbone of the paper's "causal" claim. Panels L/M/N test three correlations (LPGi, GiA, MdV vs forelimb footfall recovery); only MdV is reported as significant. The Figure 5 legend applies Tukey adjustment to the t-tests in A-C but makes no analogous statement for the correlations in L-N. A 3-test Bonferroni (α = 0.017) would not flip the MdV result, but disclosure is warranted, and the three tested regions were pre-selected from the significant group contrasts in A-C, which, to a statistician, would further shrink effective α. More importantly, the figure legend states that closed and open circles represent CFA- and RFA-traced values, respectively, which suggests the correlation treats the two tracer channels per mouse as independent datapoints - doubling the apparent n (≈ 20 from 10 uPyX mice), with the result of a higher significance than one would have at the mouse level.

(8) Reporting issues.

The reader would benefit from judging statistical choices such as those above directly from a data table rather than interpreting the authors' choices. The SciScore rightfully flags multiple missing components of transparent reporting: missing RRIDs, no code availability, limited data availability, and no power calculation, among others.

Almost all these weaknesses can be addressed with a revision of the manuscript, especially in the framing of results.

Conclusion:

The core message - that rehabilitation is associated with a selective pattern of CSN collateral remodeling in the motor medulla, and that MdV projection density covaries with behavioral recovery - is defensible from the data and already a useful result. The current wording in parts of the abstract, significance statement, and discussion goes beyond this and implies a mechanistic conclusion (mediation, central locus, re-establishment of descending control) that the data do not yet establish. The manuscript would better match its evidence with "associated with", "correlates with", or "candidate locus" framing, unless a causal experiment is added.

Reviewer #3 (Public review):

Summary:

In this study, Bonanno et al. show that after a lesion of the corticospinal tract (CST), rehabilitation running in a complex wheel drives improvement in skilled forelimb performance in mice. Mice with unilateral CST injury can perform gross motor tasks (locomotion) at the same level as the non-injured mice, but injured mice still have deficits in another task involving fine motor control. Thus, it is well-suited to test the efficacy of locomotion-based rehabilitation in fine motor control. Mice that voluntarily engaged in the rehabilitation protocol improved in the fine motor control task more than those mice that did not perform any rehabilitation. Highlighting the role of rehabilitation in the recovery of motor function after the lesion.

The authors aimed to study rehabilitation-driven intact CST sprouting to supraspinal areas. They identified one area in the motor medulla where rehabilitation significantly changes the projection density from the intact cortical spinal neurons. Interestingly, this area has ipsilateral connections and thus could be a pathway to convey motor commands from the intact corticospinal tract to the denervated area. However, as the authors acknowledge in the discussion, they only found a correlation between the change in the synaptic projections from intact CST to the medulla and the recovery. Future work should study if indeed the area of the motor medulla identified here increases its ipsilateral projections to the denervated area, confirming the re-routing of motor commands from the intact cortico spinal tract to the denervated area. The paper is strong and, in general, claims are supported by the data.

Strengths:

In this study, Bonanno et al. show that after a unilateral corticospinal tract lesion (CST), locomotion rehabilitation can improve motor function and improvements generalized to tasks that require fine motor control. Moreover, it identifies a potential pathway that could be used for the intact corticospinal tract to convey motor commands to the denervated area. The pathway identified here could become a target for rehabilitation therapies.

Weaknesses:

As the authors acknowledge in the discussion of the study, the main limitation of this study is that the reorganization observed at the motor medulla is only correlational. Thus, it is possible that the adaptation to running with an injured limb of the intact CST to adapt to an injured limb rather than a re-routing of the intact CST inputs to the denervated area underlies the synaptic changes observed in the motor medulla.

The statistical analysis could be better described.

The generalization of skilled movement is limited to only locomotion tasks.

Reviewer #1 (Public review):

Summary:

Microbialization (bacterial overgrowth) is a recognized component of degraded, eutrophied coral reefs where there is a shift from coral to algal dominance on the benthos. In addition, previous work has demonstrated that virus communities shift from a lytic strategy dominated (kill-the-winner) to a temperate (lysogenic) strategy dominated with reef microbialization. Kelman et al. sought to leverage previously published virus metagenomes produced from the water column of healthy and degraded coral reefs to assess virus community metabolic shifts. The authors also produce a conceptual model to demonstrate the potential impact of the observed metabolism shifts on reef fates.

Strengths:

The main strength of the manuscript is the findings from their metagenomic analyses and results. The virus metagenomes were produced using established approaches in the field and yield sufficient data per sample for their analyses. Interesting results regarding the shift in the types of genes from anaplerotic to cataplerotic provide the foundation for testable hypotheses to determine the magnitude of impact virus strategies have on reef health. The introduction is also well written and sets up the scene very well.

Weaknesses:

(1) The methods text currently omits important information related to the sampling design. It is not clear how many metagenomes are from healthy and degraded communities. This impacts the interpretability and robustness of the statistical results. Furthermore, it is unclear if analyses are based on assembled contigs or read-based alignments. Improving the clarity and organization of the Methods is essential for reproducibility.

(2) Regarding the bioinformatics approach, normalization using the "percent known" approach within samples may not fully account for discovery bias related to sequencing depth. While Supplementary Table 1 shows variability in read counts, the lack of community-level metadata makes it difficult to determine if sequencing depth covaries with community type (healthy vs. degraded). The study would benefit from a rarefaction analysis or subsampling to ensure that gene frequency trends and Spearman correlations are biological signals rather than artifacts of sequencing effort.

(3) The qualitative model in Figure 5 is positioned as evidence for the role of viruses in reef health, but it does not provide independent support for the authors' hypotheses. Since the model is parameterized using "arbitrary units" to reflect the authors' assumptions rather than being derived from the empirical metagenomic data, it serves as a helpful illustration of a hypothesis but not as a validation of the findings.

(4) Results and discussion require revisions to improve readability and connectivity across sections. Ensuring a clear distinction between empirical data and model-based speculation would help the audience better appreciate the science.

Reviewer #2 (Public review):

Summary:

The manuscript by Kelman and coauthors investigates how viral communities differ in the genes they encode in healthy and degraded coral reef ecosystems. Across 19 viral metagenomes from Central Pacific reefs, the authors assess the frequency of integration/excision genes as a proxy for viral community temperateness and ask whether genes associated with central carbon metabolism covary with signatures of temperateness. The main finding is that viral communities with more temperate-related genes encode more genes from the Entner-Doudoroff pathway and other reactions interpreted as anaplerotic, whereas more lytic-associated viral communities show greater representation of some pentose phosphate pathway, TCA, and redox-associated genes interpreted as cataplerotic. The authors propose a model based on these patterns in which lytic viral metabolism helps suppress bacterial overgrowth on healthy reefs, while temperate viral metabolism may promote microbialization on degraded reefs. The study addresses an interesting and potentially important concept - that viral auxiliary metabolic genes are important components of microbial communities and can affect ecosystem functioning. Linking viral metabolism to coral reef microbialization is a creative conceptual advance. The manuscript is clearly written, and the reported enrichment of anaplerotic genes in temperate-associated viromes is an interesting pattern that could motivate future work on how viral metabolic potential varies across reef states.

Strengths:

(1) The study connects viral lifestyle, central carbon metabolism, bacterial overgrowth, and reef degradation in a framework that could be useful for future studies of coral reef ecosystems and viral ecology. This is an interesting synthesis that links viral auxiliary metabolism to broader questions about microbialization and reef state.

(2) The manuscript is generally clearly organized around a testable prediction: viral metabolic gene content should vary along a lytic-to-temperate viral community gradient. The reported enrichment of anaplerotic genes in viromes with a larger fraction of temperate viruses is a compelling result.

(3) The authors highlight several virus-encoded metabolic genes that may not have been previously reported in viral datasets or genomes. If supported by further validation, these observations could expand the known repertoire of viral metabolic potential.

(4) The modeling helps clarify the feedbacks the authors propose may connect viral lifestyle, bacterial metabolism, and coral reef degradation. It provides a foundation for generating hypotheses about how viral metabolic genes could influence reef microbial dynamics.

Weaknesses:

(1) The main limitation is that the evidence for several key claims remains indirect. The core analysis is based on correlations between metabolic gene frequencies and integration/excision-related genes. This does not demonstrate that the metabolic genes occur in temperate viral genomes, are physically linked to lysogeny genes, are expressed during infection, or alter host metabolism. Thus, the data support an association between VLP-associated metabolic annotations and a community-level temperateness proxy, but not a direct link between temperate phages and these metabolic functions.

(2) It is important not to equate community-level gene frequencies with genome-level or infection-level metabolic programs. A virome may contain more anaplerotic genes overall, but that does not demonstrate that individual viruses reprogram their hosts in an anaplerotic manner nor that infection produces a net anaplerotic effect. Individual viruses may encode both anaplerotic and cataplerotic genes, and a smaller number of cataplerotic genes could have stronger metabolic consequences depending on expression, enzyme efficiency, pathway position, and host context. This is an important limitation that should be acknowledged and, if possible, addressed with contig- or genome-level analyses.

(3) The ecological interpretation assumes that viral infection is strong enough to influence reef-scale bacterial population dynamics. However, the study does not directly measure infection frequency, lysis rates, viral production, burst size, lysogeny frequency, prophage induction, gene expression, or bacterial mortality. If viral mortality or lysogenic conversion were rare in these systems, the observed gene-frequency patterns could have limited ecosystem-level consequences. This makes claims about viral metabolism suppressing bacterial overgrowth, accelerating microbialization, or acting as a conservation lever more speculative than suggested.

(4) There are statistical limitations related to the use of relative gene frequencies. Because genes are normalized as percentages of known genes, the data are compositional. Apparent increases in some categories may partly reflect decreases in others. Bootstrapped Spearman correlations are useful for assessing the robustness of these associations, but they do not address compositionality or multiple testing.

(5) The anaplerotic/cataplerotic classification is central to the manuscript's conclusions and would benefit from more support. The framework is useful, but it depends on both annotation confidence and biochemical context. Sequence-similarity annotations alone may be vulnerable to misannotation, especially for central metabolic enzymes that share conserved domains across functionally distinct proteins. Stronger evidence that key genes contain key functional domains and/or are phylogenetically related to characterized enzymes would help support the proposed functions. In addition, many central carbon enzymes are reversible or context-dependent, so a clearer rationale for each classification would strengthen the interpretation.

Overall, the manuscript presents a valuable hypothesis and highlights new ecological patterns in coral reef viral metagenomes, but falls short of the evidence needed for the strongest claims. The work would be strengthened by analyses that directly link metabolic genes to viral genomes or lysogeny markers, address compositional effects, validate key annotations, and more clearly distinguish observed gene-frequency associations from hypothesized effects on infection, host metabolism, and reef state.

The John & Calvin Podcast has just published a pretty critical review of the article.

Reviewer #1 (Public review):

Summary:

The review by Dorrell and Whittington synthesizes the progress made over the past few years with respect to a normative theory of grid cells. The core question addressed by normative frameworks of grid cells is what primary computational function grid cells serve. The review discusses evidence from mechanistic models and experimental data that point to path integration as the computational function of grid cells, consistent with results from normative models. The main goal of the review is to clarify the normative grid cell theory literature. However, the current version of the article reads at times more like a perspective or opinion article in support of the path integration hypothesis rather than a critical review of normative frameworks in the grid cell literature that contrasts the benefits and limitations, as well as pitfalls and caveats, with other modelling approaches.

Some specific comments are as follows:

(1) Abstract: "The first question quickly attracted an answer: grid cells subserve path integration ..." - I am not sure if this statement is correct. The first grid cell paper by Hafting and Fyhn in 2005 suggested that grid cells are part of a path integration-based map, and the paper emphasizes the map part. It remained unclear, and is still debated, whether grid cells are part of a system performing path integration or whether grid maps reflect the output/result of a path integration process. Other theories about the function of grid cells were brought forward as well. Although the main competing theory is discussed in this review, this review article at times appears more as a perspective or opinion article with a clear bias toward the path integration hypothesis rather than objectively discussing the evidence.

(2) Grid cells may serve multiple functions. What would be the implications for our understanding of grid cells and for interpreting the results of normative models? In general, the review could discuss some pitfalls or caveats of normative models in more detail.

(3) A normative framework can be helpful in two ways: (a) Given sufficient details on biological constraints, a normative model can help identify the computational function of grid cells. If a computational function is given and - under the given simulated biological constraints - grid cells were part of the solution, the results of the model would support the hypothesis that grid cells serve the computational function in question. (b) If a computational function were identified beyond any doubt (e.g., assume experimental data demonstrated that grid cells are necessary and sufficient for path integration), a normative model would help identify biological parameters necessary to produce grid cell firing. Unfortunately, the review falls short in making this clear distinction between (a) and (b) and in discussing important caveats regarding mixing up these two ways. E.g., the neural network model approaches by Sorscher et al. and others have been criticized because they try to achieve two things at the same time: find support for the computational function of grid cells and identify optimal parameters that result in grid cells. But doing both at the same time provides a strong bias in tweaking the parameters in exactly the way you need for the model to produce grid cells as a solution (other solutions may be possible given other parameters), preventing strong conclusions regarding the computational function of grid cells and preventing conclusions about what the parameter choices mean for biological connectivity motifs. These caveats in setting up normative models and interpreting them could be discussed in greater detail.

(4) A common assumption underlying most grid cell models is that head direction is viewed as identical to movement direction. However, head direction can differ at times from movement direction, and entorhinal head direction cells code head direction rather than movement direction (Raudies et al., 2015; 10.1016/j.brainres.2014.10.053). This missing link in how movement direction signals reach and inform grid cells could be discussed.

(5) "Knowing that one neuron in a module is active and that you make a movement north uniquely determines which neuron in that module should be active next" - I agree that this rule follows from the fact that grid cells within one module differ in phase but share spacing and orientation. However, I am surprised that the authors do not also make the argument here for the value of a normative model. Rebecca R.G. et al. (10.7554/eLife.96627) use exactly the rule cited above as a normative function. They demonstrate that this rule begets grid cells. Isn't this a prime example of how a normative approach can contribute to scientific inquiry? First, a hypothesis about a computational function is derived from experimental data. And in turn, using a normative framework, the experimental data are derived from the computational function (under appropriate biological results). The paper is discussed later together with Nicolai Waniek's work (10.1162/neco_a_01255). However, in my opinion, their work seems to be somewhat misrepresented in that later paragraph. E.g., velocity is still required as an input to determine which neuron should be active next, neurons do not need to be binary units, and space is not discretized beyond the fact that space is encoded by neurons with spatial firing fields.

Reviewer #2 (Public review):

Summary:

This review by Dorrell and Whittington covers a number of aspects related to normative modeling of grid cells. They begin by discussing key experimental insights on grid cell phenomenology. Then, they discuss how grid cells can be used to perform path integration and how they size up as efficient codes of space. These two sections then lead the authors to discuss how combining path integration and efficient coding objectives leads to models of axis-aligned grid cells in a single module. Discussion on non-linear objectives leading to multi-modules is presented. The review ends with several outstanding questions and an optimistic outlook of how normative models (particularly, task-optimized RNNs) can be used as tools for advancing understanding in neuroscience.

Strengths:

(1) The review is timely and covers an area that has seen a lot of recent activity. This discussion around many of the different results (and kinds of models), I think, will be generally helpful for the field.

(2) Although I think the story could be a little more coherently made (see below), in general I enjoyed the author's flow from efficient coding -> efficient coding + path integration -> efficient coding + path integration + non-linear objective. This framing supports the specific conclusion the authors arrive at.

(3) I also really liked the message that the review made of how normative modeling, despite some of its challenges/limitations, can be used effectively in neuroscience. The discussion of cycling between "experimental" modeling (e.g., vanilla RNNs) and theoretically-grounded models was nice, and I think it helps demonstrate the value of this approach.

(4) Showing how the metric loss could be seen as a bandpass filter (Figure 3C) was nice and a contribution of the review.

(5) While the focus of P4 (conjunctive HD-grid cells) felt initially a little cast aside, the discussion around "brain and task-optimised RNNs with standard architectural choices use fundamentally different path-integration mechanism" was nice and I think helpful for steering the community to an interesting open problem.

(6) Identifying how "non-linear functionality" can lead to multi-modules was nice and not something that I have seen as clearly presented before.

Weaknesses:

(1) The authors view the experimental evidence for grid cells being linked to path integration as "specific and strong" and that the " key computational feature that defines entorhinal cortex [is] path-integration". I think experimentalists (at least the ones I work with) would push back on that. First, it's hard to isolate path integration in rodent experiments. So while Gil et al. (2018) did about as good a job as you could do, there are still other interpretations of the results that are not purely path integration dependent. And second, as the authors point out later in the review, there is experimental work finding that grid cells are disrupted in large environments and 3D. Path integration certainly happens (to some extent) in these spaces, which begs the question of how it is achieved with weakened grid coding. Thus, I think reducing the claims about how strongly grid cells are experimentally linked to path integration is called for.

(2) The authors introduce the idea of efficient coding of space and discuss how grid cells are not optimal. It is later clarified (Sec. 5.3) that multi-module codes can be efficient (even if not the most optimal). I was confused reading Section 3, because in Section 2 the multiple modules are discussed, but then in Section 3, they are dropped, and only a single module is being considered. Equation 2 was also a little confusing to me. Alpha is not defined, and I would have thought that it would be x^Tx' - g(x)^T g(x') and not x^Tx' g(x)^T g(x'). Given that there is no page limit here, I think a little more detail in Section 3 would be helpful.

(3) In Section 3, the authors make use of P2 (translation invariance within a module) to rule out (or, at least, question) certain models/approaches. While this is certainly a standard assumption made in theoretical work, it is not very well supported by experimental findings. In particular, Diehl et al. (2017), Ismakov et al. (2017), and Dunn et al. (2017) all found that individual grid fields systematically vary in their peak firing rate. In addition, Redman et al. (2025) found that, within a given module, there was a small but robust diversity of grid orientations and spacings. These suggest that grid cells within a single module may actually be able to encode properties of local space and give some support to normative models that find efficient space coding with grid cells by finding non-axis-aligned grid fields. I think this is all important to mention because: a) it provides more biological nuance to the question about spatial coding; b) it provides more ways in which to test models. For instance, in Redman et al. (2025), the Sorscher et al. (2022) model was shown to produce variability in grid properties that loosely matched what was found in real data. For tests like this (e.g., how much does a model reproduce variability in grid firing field peak rates), I think it is going to be important for continuing to evaluate models.

(4) The focus of the review, I know, is grid cells, but of course, grid cells are part of the MEC and the larger hippocampal network. I totally understand, at some level, you have to make a decision of what to model, but it seems that there are other functional classes of neurons (border cells, head direction cells) that all play an important role in path integration. And while the models the authors consider at the end of the review capture properties of grid cells really well, they do so at the cost of not modeling anything else. The authors mention this in the context of the models not capturing conjunctive grid-head direction cells, but I think the point is a deeper one, and more discussion of at what level it makes sense to consider grid cells only is important.

(5) As I mentioned in the Strengths section, I did enjoy the flow of the paper on how path integration + efficiency is needed to get grid single modules and path integration + efficiency + non-linearity is needed to get multiple grid modules. This creates the story that adding more of these theory-driven constraints helps lead to more "accurate" models of grid cells. But one alternative view is that, if path integration + efficiency is enough to get a single grid module (but only a single grid module), then maybe the utility (or need) of multiple grid modules comes from something else. That is, instead of saying "we need more constraints to get multiple modules", it could be evidence for "we need to re-think whether multiple modules might need a different theory to explain". While I understand this is a big picture question that maybe isn't entirely fair to ask of the authors, I think: 1) the authors do a nice job of positioning their review as a kind of discussion on what normative modeling can provide to neuroscience, so having this discussion on when the failure of a model to capture ALL aspects of the biological features motivates further constraints as opposed to a new approach, would be useful; 2) this question connects with the title of the paper, i.e. "what is the question?"

Reviewer #3 (Public review):

Summary:

The authors present an extensive review of the literature on normative grid cell theory, asking what kind of cost function might be minimized by the entorhinal grid cell code. The authors show which of the main features of grid cells emerge from combinations of terms in a cost function that optimizes for spatial fidelity, biological plausibility, and path integration. They conclude by outlining potential future directions for the field.

Strengths:

The structure of the review makes it particularly useful for researchers who are familiar with grid cells but not necessarily with normative models. Equations are kept to a minimum and are usually explained conceptually.

Weaknesses:

I identified one main weakness, related to the fact that the introduction to experimental results around grid cells and what they allow us to conclude is less nuanced than the rest of the review. However, since this is not the main focus of the manuscript, I consider this a secondary limitation.

The review organizes the current literature on the subject within a coherent conceptual framework, helping to define possible paths forward for the field.

Reviewer #1 (Public review):

Summary:

Extracellular electrophysiology datasets are growing in both number and size, and recordings with thousands of sites per animal are now commonplace. Analyzing these datasets to extract the activity of single neurons (spike sorting) is challenging: signal to noise is low, the analysis is computationally expensive, and small changes in analysis parameters and code can alter the output. The authors address the problem of volume by packaging the well-characterized SpikeInterface pipeline in a framework that can distribute individual sorting jobs across many workers in a compute cluster or cloud environment. Reproducibility is ensured by running containerized versions of the processing components.

The authors apply the pipeline in two important examples. The first is a thorough study comparing the performance of two widely used spike-sorting algorithms (Kilosort 2.5 and Kilosort 4). They use hybrid datasets created by injecting measured spike waveforms (templates) into existing recordings, adjusting those waveforms according to the measured drift in the recording. These hybrid ground truth datasets preserve the complex noise and background of the original recording. Similar to the original Kilosort 4 paper, which uses a different method for creating ground truth datasets that include drift, the authors find Kilosort 4 significantly outperforms Kilosort 2.5. The second example measures the impact of compression of raw data on spike sorting with Kilosort 4, showing that accuracy, precision, and recall of the ground truth units is not significantly impacted even by lossy compression. As important as the individual results, these studies provide good models for measuring the impact of particular processing steps on the output of spike sorting.

Strengths:

The pipeline uses the Nextflow framework, which makes it adaptable to different job schedulers and environments. The high-level documentation is useful, and the GitHub code is well organized. The two example studies are thorough and well-designed and address important questions in the analysis of extracellular electrophysiology data.

Weaknesses:

There are no major weaknesses in the revised manuscript. While no data analysis pipeline can cover the needs of all experiments, the authors have added and significant flexibility in the pipeline. Even experimenters who might opt for a simpler pipeline will benefit from this work as a model.

Reviewer #2 (Public review):

Summary:

This work presents a reproducible, scalable workflow for spike sorting that leverages parallelization to handle large neural recording datasets. The authors introduce both a processing pipeline and a benchmarking framework that can run across different computing environments (workstations, HPC clusters, cloud). Key findings include demonstrating that Kilosort4 outperforms Kilosort2.5 and that 7× lossy compression has minimal impact on spike sorting performance while substantially reducing storage costs.

Strengths:

(1)Extremely high-quality figures with clear captions that effectively communicate complex workflow information.

(2) Very detailed, well-written methods section providing thorough documentation.

(3) Strong focus on reproducibility, scalability, modularity, and portability using established technologies (Nextflow, SpikeInterface, Code Ocean)

(4) Pipeline publicly available on GitHub with documentation.

(5) Clear cost analysis showing ~$5/hour for AWS processing with transparent breakdown.

(6) Good overview of previous spike sorting benchmarking attempts in the introduction

(7) Practical value for the community by lowering barriers to processing large datasets.

Weaknesses

No significant weaknesses. The authors have responded to all my review critiques and suggestions.

Reviewer #3 (Public review):

Summary:

The authors provide a highly valuable and thoroughly documented pipeline to accelerate the processing and spike sorting of high-density electrophysiology data, particularly from Neuropixels probes. The scale of data collection is increasing across the field, and processing times and data storage are a growing concern. This pipeline provides parallelization and benchmarking of performance after data compression that helps address these concerns. The authors also use their pipeline to benchmark different spike sorting algorithms, providing useful evidence that Kilosort4 performs the best of out the tested options. This work, and the ability to implement this pipeline with minimal effort to standardize and speed up data processing across the field, will be of great interest to many researchers in systems neuroscience.

Strengths:

The paper is very well written and clear. The accompanying GitHub and ReadTheDocs are well organized and thorough. Benchmarks are exceptionally well applied to support the authors' claims, and it is clear that the pipeline has been very thoroughly tested and optimized by users at the Allen Institute for Neural Dynamics. The pipeline incorporates existing software and platforms that have also been thoroughly tested (such as SpikeInterface), so the authors are not reinventing the wheel, but rather putting together the best of many worlds. In the latest revision, the authors add a nice analysis showing that compression mostly affects the lowest SNR units. This is a great contribution to the field and it is clear the authors have put a lot of thought into making the pipeline as accessible as possible.

Weaknesses:

None noted. The authors have addressed all previous questions and requests for clarification.

Reviewer #1 (Public review):

Summary:

This manuscript examines how Streptococcus pyogenes regulates expression of the virulence factor SpeB in response to both bacterial and host-derived cues. The authors propose that Vfr acts as a repressor of speB expression and that degradation of Vfr by SpeB or by neutrophil-derived proteases relieves this repression. This creates a model in which S. pyogenes can sense proteolytic activity during infection and use that information to tune virulence factor expression.

Strengths:

The main strength of the study is the bacterial regulatory mechanism. The dual reporter system provides a useful way to follow speB and hasABC expression, and the genetic analysis of known regulators helps validate the system. The media-swap experiments, recombinant Vfr experiments, and SpeB-mediated degradation of Vfr support the conclusion that Vfr represses speB and that proteolysis can relieve this repression. The finding that SpeB can degrade Vfr is particularly interesting because it suggests an autoregulatory mechanism that could reinforce SpeB expression once it has been initiated.

Weaknesses:

The host side of the model is less completely supported. The authors show that neutrophil lysates and protease-containing fractions can induce the speB reporter and degrade Vfr, which supports the idea that neutrophil-derived proteases can affect this circuit. However, the in vivo interpretation relies heavily on PAD4-deficient mice to implicate neutrophil extracellular traps. PAD4 deficiency is a useful perturbation, but it does not by itself distinguish loss of extracellular trap formation from changes in neutrophil recruitment, survival, degranulation, phagocytosis, oxidative killing, or other neutrophil death pathways. As a result, the current data support a role for neutrophil-associated proteolytic activity more strongly than they support a specific role for extracellular traps. This distinction is important for interpreting the central model. The bacterial circuit is well developed, but the host-derived cue remains somewhat underdefined. If the relevant signal is extracellular protease activity more broadly, then the model is still interesting, but the conclusion should be framed around neutrophil-derived proteolytic stress rather than extracellular traps specifically. If extracellular traps are the key in vivo source of protease exposure, then additional evidence would be needed to separate that mechanism from other neutrophil effector functions that remain intact in PAD4-deficient cells.

Overall:

This is a valuable study with solid evidence for a bacterial protease-sensing regulatory mechanism controlling SpeB expression. The work should be useful to investigators interested in bacterial virulence regulation, host-pathogen interactions, and how pathogens integrate immune-derived cues during infection. The impact of the study would be stronger if the host-derived signal were defined more precisely, but the bacterial Vfr-SpeB circuit provides a compelling framework for thinking about how S. pyogenes links proteolytic activity to virulence gene expression.

Reviewer #2 (Public review):

Summary:

The study examines how Streptococcus pyogenes integrates bacterial and host-derived signals to regulate SpeB, proposing that Vfr acts as a protease-sensitive repressor whose degradation relieves repression of speB. The authors further suggest that neutrophil-derived serine proteases, including those associated with inflammatory conditions, may promote this transition, and thereby counterbalance LL-37/CovRS-associated suppression of speB. The conceptual framework is interesting and potentially important for understanding how host inflammation feeds into bacterial virulence regulation.

Strengths:

The work addresses a biologically significant question and does so using a broad and generally well-integrated experimental approach, including bacterial genetics, reporter assays, recombinant protein analyses, neutrophil-derived material, human blood infection, and mouse infection models. A particular strength is the effort to connect host inflammatory processes to bacterial regulatory behavior, which gives the study conceptual reach beyond a narrow mechanistic observation. The data support the view that Vfr is relevant to speB control and that neutrophil-associated protease activity may influence this pathway.

Weaknesses:

The main limitations are mechanistic. The physiological form, localization, and abundance of Vfr are not sufficiently defined to support the proposed model at full strength, and the evidence that Vfr functions as a SpeB-labile repressor under biologically relevant conditions remains incomplete. The relationship between Vfr and the broader RopB/SIP regulatory framework is also not yet firmly established. In addition, the reporter system is not yet benchmarked closely enough against endogenous SpeB protein output, and its growth-phase dependence is insufficiently resolved, which makes it difficult in some settings to distinguish promoter activity from mature protease production. The neutrophil protease component is likewise not defined beyond a general serine protease signal, and the potentially important LL-37/CovRS/Vfr connection is underdeveloped in the main text. Overall, the conceptual advance is promising, but several of the central mechanistic claims would benefit from more direct experimental support and more cautious framing.

Reviewer #3 (Public review):

Summary:

SpeB is a cysteine protease secreted during infection by Streptococcus pyogenes (Spy). SpeB has been extensively investigated for its role in pathogenesis, which involves proteolytic processing of both Spy virulence factors and host proteins. Regulation of speB expression is complex and includes growth phase regulation, a quorum-sensing system, the transcription factor RopB, and the global regulatory system CovRS (CsrRS). Guerra et al now attempt to refine the current model of regulation of SpeB expression, focusing on the Spy protein Vfr, which has been suggested previously to act as a negative regulator of SpeB expression. In the current study, neutrophil lysates (representing proteases released during NETosis) are shown to degrade Vfr and to relieve repression of SpeB. At high cell density, SpeB itself also degrades Vfr, which may allow autoregulation of SpeB expression. These observations are unsurprising as the broad protease activities of both neutrophil proteases and SpeB are well known. Nonetheless, the data presented fill in additional details in our understanding of the complex regulation of an important Spy virulence factor.

Strengths:

(1) Construction of a GFP reporter strain provided a facile methodology for tracking speB promoter activity in a variety of experimental setups.

(2) A Vfr deletion mutant was a useful tool to investigate the role of Vfr in SpeB regulation, and mutants in speB and ropB were important controls.

(3) Experiments using neutrophil lysates in vitro, as well as in vivo studies of mice depleted of neutrophils with anti-Ly6G or in PAD4-/- mice (that cannot form NETs) support the hypothesis that neutrophil proteases derepress speB expression by degrading Vfr.

Weaknesses:

(1) The introduction and all the experiments in Figure 1 focus on CovRS, which turns out to be largely tangential to the overall story developed by the rest of the study. On the other hand, the complex and well-studied regulation of speB expression by RopB and the SIP quorum-sensing system is only minimally described. A better framing would be a more detailed introduction to the current model of speB/RopB/SIP/quorum sensing/growth phase regulation. CovRS could be introduced later as its relevance is really just to show that neutrophil lysates or NETs do more than simply providing LL-37, which signals through CsrS, as another regulator of speB expression.

(2) Vfr, as the central focus of the paper, also deserves a more thorough introduction to provide context for the study. For example, reference 19 (Shelburne et al, 2011) showed reduced transcription of speB in a vfr mutant, an effect that could be complemented by expressing vfr or a 39-aa N-terminal fragment in trans. That study presented evidence that the N-terminal peptide binds to RopB, which may prevent RopB from upregulating SpeB expression. Do the authors concur with that model? As it stands, the discussion and model in Figure 1A imply a direct regulatory effect of Vfr on speB expression rather than an indirect one through regulation of RopB. If direct regulation of speB by Vfr is a consideration, it should be investigated more thoroughly, e.g., by promoter-binding assays, CHIP-seq, etc.

(3) Use of single-cell flow cytometry generally confirmed results observed in batch culture. The authors also comment repeatedly on the heterogeneity of individual cell fluorescence representing both speB and has operon expression. However, the reason(s) for heterogeneity in gene expression are not explored, e.g., differences in individual cell growth rate in batch culture, variable loss of reporter plasmid during infection experiments, etc).

(4) Lines 116-118 and Figure 3C: Incubation of recombinant Vfr with Spy Dvfr reduced SpeB expression, but the degree of suppression is modest compared to that seen in wild-type Spy. How does the concentration of rVfr added compare to that present in the culture fluid of wild-type Spy? (Also, the concentration of rVfr used is unclear: the figure says 3 µg/ml and the legend says 0.3 mg/ml, i.e., 300 µg/ml).

(5) Lines 125-126: "...the Vfr structure contains several potential protease SpeB cleavage sites..." The role of Vfr in degrading SpeB could be clarified by identifying the predicted cleavage products, e.g., by mass spec, after co-incubation of the two recombinant proteins.

(6) Lines 122-124: "Notably, speB expression in Spy Dvfr is unaffected by LL-37 or MgCl2, further validating its [Vfr's?] dominance over CovRS regulation." This statement is an oversimplification and is potentially misleading: LL-37 is degraded by SpeB (Nyberg et al, JBC 2004), which likely explains why the addition of LL-37 fails to signal through CovRS to repress SpeB in Spy Dvfr since SpeB is produced continuously in that strain. By contrast, SpeB is only produced during the stationary phase in the wild type, so LL-37 remains active throughout the exponential phase and represses SpeB expression. The response to the CovRS ligand MgCl2 is similar (or greater) in Spy Dvfr compared to wild type (Figure S2C).

(7) Lines 153-154 and Figure 6E: Growing wild type Spy in the presence of neutrophil lysates with or without a protease inhibitor stimulated or repressed speB expression in a manner consistent with degradation (or not) of Vfr. It would be confirmatory and informative to do the same experiment with the Spy Dvfr strain.

(8) Clarity of writing could be improved, particularly by eliminating pronouns of indefinite reference (it, its, this) in contexts in which the subject is ambiguous (examples at lines 62, 89, 111, 114, 115, 123, 183, 190, 193, 204, 205, 210, 217, 221, 222, 224).

Reviewer #1 (Public review):

Summary:

The authors presented a simplified E. coli cell-free protein synthesis (eCFPS) system reduces core reaction components from 35 to 7, improving protein expression levels. They also presented a "fast lysate" protocol that simplifies extract preparation, enhancing accessibility and robustness for diverse applications.

Strengths:

The authors present a valuable new protocol for eCFPS, which simplifies its application.

Weaknesses:

The authors provide data for optimization but offer insufficient explanation of the fundamental mechanisms underlying the phenomenon based on data.

Comments on revised version.

The authors have satisfactorily addressed the concerns raised by the reviewers. However, the mechanistic basis of the observed performance gain remains insufficiently substantiated. The attribution of this improvement to enhanced transcription is currently speculative. This point could be directly tested by quantifying mRNA levels, for example, using real-time PCR, in both the initial and optimized systems. Such analysis would significantly strengthen the mechanistic interpretation of the results.

Reviewer #2 (Public review):

Summary:

The authors have made a convincing argument that the current system of in vitro translation using E. coli extracts can be significantly optimized to work with much lesser components, while maintaining activity. They have showcased their improved activity using not only physical but also functional readouts.

Strengths:

The experiments are designed in a very logical and easy to understand manner, which makes it easier not only to follow the paper, but also reproduce the results. Functional assays with the synthesized proteins are a good way to demonstrate functionality and applicability of the system. They also benchmark their system against a commercial kit to show superior performance of their system.

Weaknesses:

The production of the lysate requires special instrumentation, limiting accessibility.

Comments on revised version:

Thank you to the authors for addressing the concerns both textually and experimentally. This work has significant value.

Reviewer #3 (Public review):

Summary:

The authors aimed to overcome the challenges associated with complex, conventional prokaryotic cell-free protein synthesis (CFPS) systems, which require up to thirty-five components, by developing a streamlined and efficient E. coli CFPS platform to encourage broader adoption. The main objective was to reduce the number of reaction components from thirty-five to seven, while also developing an accessible 'fast lysate' preparation protocol that eliminates time-consuming runoff and dialysis steps. The authors also sought to demonstrate the robustness and translational quality of this streamlined system by efficiently synthesising challenging functional proteins, including the cytotoxic restriction endonuclease BsaI and the self-assembling intermediate filament protein vimentin.

Strengths:

This study presents several key strengths of the optimised E. coli cell-free protein synthesis system in terms of its design, performance and accessibility.

- The reaction mixture has been dramatically simplified, with the number of essential core components successfully reduced from up to thirty-five in conventional systems to just seven.

- The "fast lysate" protocol is a significant advance in terms of procedure.

- The system's ability to synthesise challenging, functional proteins is evidence of its robustness.

Weaknesses:

(1) Title: "A simplified and highly efficient cell-free protein synthesis system for prokaryotes".

- This title is misleading since one would expect a simplified and highly efficient cell-free protein synthesis system to yield similar protein levels compared to current cell-free protein synthesis systems. What this study shows is that the composition of cell-free protein synthesis systems can be simplified while maintaining a certain level of protein synthesis. Here, optimisation does not involve maintaining protein synthesis yield while simplifying the cell-free protein synthesis system; rather, it involves developing a simplified cell-free protein synthesis system. As mentioned in my comments below, this study lacks a comparison of protein levels with a typical cell-free protein synthesis system.

- What do the authors mean by "highly efficient"? Highly efficient compared to what experimental conditions? If one is interested by the yield of protein synthesis, is this simplified system highly efficient compared to current systems?

(2) Figure 1, 3-5:

- What do relative luciferase units represent? How are these units calculated?

- In this system, the level of expression depends mainly on the level of NLuc transcripts and the efficiency of NLuc translation. How did the authors ensure that the chemical composition of the different eCFPS buffers only affected protein translation and not transcript levels? In other words, are luciferase units solely an indicator of protein synthesis efficiency, or do they also depend on transcription efficiency, which could vary depending on the experimental conditions?

- How long were the eCFPS reactions allowed to proceed before performing the luciferase activity measurement? Depending on the reaction time, the absence or presence of certain compounds may or may not impact NLuc expression. For example, it can be assumed that tRNA does not significantly affect NLuc levels over a short period of time, and that endogenous tRNA in the lysate is present at sufficient concentrations. However, over a longer period of time, the addition of tRNA could be essential to achieve optimal NLuc levels.

- The authors show that tRNA and amino acids are not strictly essential for the expression of NLuc, likely due to residual amounts within the cell lysate. However, are the protein levels achieved without added amino acids and tRNA sufficient for biochemical assays that require a certain amount of protein? It is important to note that the focus here is on optimising the simplicity of the buffer rather than the level of protein expression. In fact, the simplicity of the buffer is prioritised over the amount of protein produced. This should be made clear.

- How would the NLuc level compare if all the components were optimised individually and present in an optimised buffer, compared to a buffer optimised for simplicity as described by the authors?

(3) Line 71, Streamlining eCFPS: removal of dispensable components. This title is misleading because it creates the false impression that proteins can be produced in vitro without the addition of certain compounds. While this is true, the level of protein produced may not be sufficient for subsequent biochemical analyses. This should be made clear.

(4) Figure 2: In the legend, change "(A) Protein expression levels of the eCFPS system measured at varying concentrations of KGlu and MgGlu2" to "(A) Protein expression levels of the eCFPS system using an Nanoluciferase (NLuc) reporter DNA measured at varying concentrations of KGlu and MgGlu2".

(5) Lanes 302-303: "The thorough optimization of the seven core components was a critical step in achieving high protein expression levels". What are "high expression levels"? Compared to what?

Comments on revised version.

The authors have adequately addressed my previous concerns.

Reviewer #1 (Public review):

Summary:

Pecak et al have deciphered the conformational dynamics of a heterodimeric model ABC transporter, TmrAB, a functional homolog of the human antigen transporter TAP, using single molecule Forster resonance energy and fluorophores attached to residues at either nucleotide binding domains or periplasmic gate. The analysis not only differentiated ATP-free and bound states, but also enabled the real time monitoring of protein conformational changes precisely dissecting transport cycles and resolving transient intermediates. This study is absolutely significant in providing and establishing a general pipeline delineating the conformational dynamics in heterodimeric ABC transporters.

Strengths:

The scientific study is very well documented for experimental design, results and conclusions supported by the experimental data. Authors have determined the conformational dynamics of TmrAB across different ATP concentrations including physiological ones and resolved an outward open state and other conformational states consistent with previous cryoEM and DEER studies. Authors have also mentioned limitations in the study.

Comments on revised version.

Authors have worked on most of the revisions stated in previous feedback and included in the newer version, which has been significantly improved. Other comments have been described to be out of scope from this study.

Reviewer #2 (Public review):

In their manuscript entitled 'ATP-driven conformational dynamics reveal hidden intermediates in a heterodimeric ABC transporter', Pečak et al. use elegant single-molecule FRET experiments in detergent to investigate the heterodimeric ABC transporter TmrAB. By combining simulations of the transporter's accessible volume with elegant trapping strategies, the authors identify an unresolved outward-facing open state and conclude that it is usually obscured by a rapidly interconverting ATP-bound ensemble. Overall, the study demonstrates that smFRET can resolve the short-lived intermediate states of TmrAB and potentially other ABC transporters that are obscured in ensemble measurements.

It is a very interesting study that highlights the power of combining high-resolution structural information with spectroscopic approaches. I had three major concerns with the original version, all of which have been addressed by the authors in this revised version.

Reviewer #1 (Public review):

WIPI1 is a PROPPIN family protein that has been implicated in Retromer-mediated membrane fission events. Although the cargos that it has been tested to be important for are diverse, one of the cargos that is unaffected is Beta1-Integrin. This leads the authors to assess another PROPPIN family protein - WIPI2, which is a homolog of WIPI1. KD using siRNA is effective and had no consequences on LAMP1, EGFR trafficking or GLUT1 trafficking. Integrin-B1, however, had a large and significant defect in its recycling from the endosome, with a clear endosomal colocalisation. Complementation experiments with WT WIPI2 recovered the phenotype, but various mutant WIPI2 complements resulted in elongated tubules, and there was also a dominant negative effect of the mutant. Integrin is a classic retriever cargo, so the authors rationalise that WIPI2 may be playing a role with retriever that WIPI1 plays with retromer. To assess this, they perform a set of immunoprecipitations. SNX17, the retriever-associated sorting nexin, co-IPs with WIPI2 in a VPS26C-dependent manner. VPS26C but not VPS26 co-IPs with WIPI2, and the reciprocal with WIPI1. These interactions were not present for the FSSS mutation of WIPI2. WIPI2 localises to Rab11 endosomes mainly, as does retriever. Mutations of WIPI2 not only affected WIPI2 localisation, but also VPS35L mutations, indicating that there is a functional relationship between the two.

Comments on revised version.

The reviewers have responded appropriately to all the points. I have no remaining concerns.

Reviewer #3 (Public review):

Summary:

The manuscript of Mayer and colleagues analyzes the function of WIPI proteins in mammalian cells. The authors identified previously CROP as a complex consisting of WIPI1 and the retromer complex, primarily in yeast cells. In mammalian cells, both WIPI1 and WIPI2 exist, whereas retromer has a homologous complex termed retriever. The now find that WIPI2 can form a complex with retriever subunits. They name this complex CROP2. Their data further indicate that CROP2 and CROP1 have distinct substrate specificities as knock down of CROP2 subunits affect beta1 integrin sorting, whereas knock down of CROP1 affects EGFR and GLUT1. The further identify a similar sequence (FSSS) in both WIPI1 and WIPI2, which is required for their specific binding to retromer and retriever.

Strengths:

CROP1 and CROP2 seem to use similar features for their formation, and have different substrates, which is convincingly shown.

Weaknesses:

The analysis lacks information that this is a complex as claimed. It can be deduced from the immunoprecipitation analysis.

Comments on revised version.

The authors answered my questions and adjusted the text accordingly. Figure 10 was not part of the submitted version. It should be checked by the editor.

Reviewer #1 (Public review):

Summary:

This paper reports the findings of a neuroimaging experiment that tested the hypothesis that the cortex, specifically early visual areas, reinstates the content from single events during our lives. The researchers tested this hypothesis by presenting to-be-remembered pictures of objects at spatial locations on the computer screen and then testing subjects with both recall and recognition. They show that during memory testing, the spatial location of the object can be decoded from the pattern of cortical BOLD responses measured with fMRI. They go on to show that the spatial tuning is higher during recognition than recall, that the tuning is correlated with memory retrieval accuracy, and that the retrieved precision is predicted by the encoded precision, particularly in the higher-level visual areas. Thus, the paper finds evidence of cortical reinstatement of details from a single event in a human life.

Strengths:

This is a strong manuscript that I have had the luxury of commenting on during a round of review at another prestigious journal. As a result, the authors have already made changes to address previous comments about highlighting the complementary learning systems approach more to motivate the alternative prediction that the cortex should only show evidence of reinstatement after repeated presentations. In addition, the authors have fleshed out the discussion of working memory in this task. They also revised their review of the literature to include citations suggesting spatial locations are normal parts of our episodic representations, likely obligatory in nature, as my group and others have argued in completely unrelated work. I applaud the authors for being responsive to a previous round of review and using the comments to address relatively minor issues with the paper, even though they moved on to a different journal. Thus, I found the paper even stronger than at first approach, and at first blush, the results were intriguing and the paper well written.

Weaknesses:

There is a logical perspective in the narrative that seems to unnecessarily weaken the paper. The paper shows evidence consistent with the conclusion that mnemonic representations are contained in early visual cortex, but then argues that those representations are not actually stored therein. For example, the first half of the last sentence of the conclusions (see page 19 of the manuscript). I understand the perspective that subcortical mechanisms must be involved in the act of retrieval, given the neuropsychology and other evidence. But if storage is elsewhere with the same fidelity so as to code this information, then how would such a memory system work? The MTL neurons would need to have the real, precise representation of all the orientations encoded at all the retinotopic locations, a mirror to V1 in terms of precision, because that's the actual memory representation being retrieved, so its fidelity will be limited by what is stored in the file, so to speak. Then, at retrieval, the paper proposes that the brain just reactivates the encoding context in V1 to help with the response output and ensure the precision of the behavioral responses. This must mean that the hippocampus/MTL has cells and networks with tuning functions that match the precision in all the cortical sensory systems that they are integrating context across, given the episodic memory models like Polyn and colleagues (2009, Psych Rev). So, there are little MTL maps that are completely redundant with V1, M1, A1, S1, etc.? Why such redundancy?

Why not propose that what the subcortical systems do is to encode a unique pattern for that episode, that is separated from others, that just links (or provides pointers to, in computer science jargon) the contextual details stored in the cortical networks themselves? In this way, we can explain why neglected patients also neglect their memories of the town square. This has always been my interpretation of the results of the Polyn et al. (2006, Science) paper and the models tested with those whole-brain results. That is, you see widespread cortical context reinstatement during (one-shot) free recall events that included visual selective cortex for faces when faces were being recalled, but included a broad network, probably V1, and activating sounds in A1, body posture in M1, etc., though the latter three examples did not discriminate between categories of memoranda, in their experiments. Given that you show that activity in V1 during retrieval looks like it is being used, you should propose that the early cortex really participates in memory storage functions. V1 neurons are wired up to neurons of other selectivities in a competitive network with plastic synaptic connections. How would experience be prevented from changing activity in the cortex? Yes, cortical changes slow after the critical periods, as studied in the classic eye suturing experiments to study ocular dominance, but changes in cortical representations do not stop with maturity, with the pinwheel centers looking like they are context sensitive, thus, changing rapidly to events across time (Okamoto, Ikezoe, et al., 2011, Sci Reports). The brain would need a no-plasticity mechanism, and instead, it looks like the cortex can completely rewire even in adulthood (Buonomano & Merzenich, 1998, Annu Rev Neuro).

I believe that the paper needs to describe the strong/radical interpretation of the current findings; that they are consistent with the view that the entire brain may be a memory structure, with encoding linking representations across sensory cortices. But also activating semantic and lexical systems, emotional networks encoding those aspects of context which we know can sometimes strongly drive effects, a nice prediction that could be made in the discussion/conclusions. Here you are looking at how precise the visual reinstatement is in V1 during retrieval following one exposure. One parsimonious mechanism to explain this effect is that the brain stores details of events using the neurons that do the high-fidelity perception of the event. Given that our goal is to stimulate thinking among fellow scientists so that this paper can be a citation classic, I think the paper should be revised so that it paints a complete picture of the theoretical possibilities of its findings.

Reviewer #2 (Public review):

Summary:

The study aims to show that the early visual cortex is not merely a sensory-perceptual region that encodes stimuli while they are physically present, but also supports the formation and retrieval of long-term episodic memories. Instead, the authors demonstrate that spatially tuned reactivation of early visual cortex after a single encoding event supports memory-guided behavior, such as recalling an object's original location.

Strengths:

The study provides solid evidence that location information for single, trial-unique objects is reinstated in early visual cortex during both recognition and recall, even without explicit spatial demands, and the remembered vs. forgotten analyses link spatial tuning to behavior. The one-shot design and absence of explicit spatial instructions are important strengths that bring the paradigm closer to everyday, incidental episodic experiences and go beyond highly trained cue-target associations.

Weaknesses:

(1) Conceptually, the main findings would appear less surprising without a sharper theoretical contrast. Given basic retinotopic coding, it is natural that object identity and location are jointly encoded when an object is presented at a particular position, so spatially tuned reinstatement in V1-V3 can be interpreted as a reconfirmation of known properties unless more clearly contrasted with theories that emphasize more abstract, position-invariant cortical representations following hippocampal-cortical recoding. As currently framed, the introduction does not fully articulate what existing accounts might predict, or what pattern of results would have challenged those accounts, which somewhat weakens the perceived theoretical payoff.

(2) It also remains somewhat unclear why early visual cortex (V1-V3), specifically, is the critical locus for the spatial information of interest, as opposed to higher-level visual or parietal regions that could also provide a spatial scaffold; clearer rationale and, if possible, control analyses in additional regions would help here.

(3) Since gaze behavior is central to any spatial account, it would be helpful to report basic eye-tracking analyses comparing remembered versus forgotten trials, especially at encoding, to rule out systematic differences in fixation patterns that could contribute to the spatial tuning results.

Reviewer #3 (Public review):

Summary and Overall Evaluation:

This is an elegant paper addressing an important question: whether spatial location is automatically activated during the recall of object memories. Building on prior work that relied on trained or repeated stimuli, the present study uses unique objects with one-time encoding across four spatial locations - a meaningful advance in ecological validity. The experimental design is clean, the data analysis is well-executed, and the reported effects, while small, are intriguing and open up interesting questions about the role of spatial structure in visual memory. Overall, this is a solid contribution, and my comments below are intended to help the authors strengthen the paper further.

Major Comments

(1) Incidental encoding.<br /> Was the memory task fully incidental - that is, were participants unaware that a subsequent memory test would follow encoding? This seems important for interpreting the automaticity claim that is central to the paper's contribution, and should be clarified explicitly.

(2) Spatial extent of the analysis - higher visual regions and negative pRFs.<br /> The analysis appears restricted to regions V1-V3. Have the authors examined higher visual areas as well? This seems like an important omission given that object memory likely engages regions well beyond the early visual cortex. Relatedly, recent work by Adam Steel and colleagues suggests that spatially tuned negative pRFs may play an important role in memory. Have the authors considered examining these? Expanding the analysis in these directions could substantially enrich the findings.

(3) Mechanism - retinotopic or spatiotopic?<br /> The paper makes a compelling case that spatial structure supports memory, but the nature of that spatial structure deserves more discussion. Are the effects retinotopic or spatiotopic in nature? The current design may not be able to fully dissociate these possibilities, but this distinction is theoretically important, and the authors should engage with it directly. Even a careful discussion of what the current data can and cannot tell us on this point would be valuable.

(4) Relationship between encoding failure and retrieval failure.<br /> For trials where memory performance is worse, and the encoding models fail, is there a systematic relationship between how the pRFs fail at object retrieval versus spatial retrieval? In other words, are the pRFs wrongly tuned in the same way at both stages? This analysis could provide meaningful insight into whether object and location retrieval draw on shared spatial representations.

(5) Object shape and spatial mapping.<br /> Real-world objects vary considerably in surface structure and shape, which may affect how cleanly they map onto a specific spatial location. Was this considered in the analysis? What was taken as the correct or peak location for each object, and how was this defined when objects extended across space? Apologies if this was addressed in the methods and I missed it.

(6) Time course of pRF activation.<br /> Is there a way to examine the time course of pRF activation within a trial? Do the spatially tuned responses arise immediately upon retrieval, or do they build up over time? Even a preliminary analysis of this would be of considerable theoretical interest, as it would speak to whether spatial reinstatement is an early automatic process or a later, more deliberate one.

(7) Effect size and functional significance.<br /> The authors acknowledge that the reported effects are very small, which I appreciate. However, this does raise genuine questions about functional significance that I think deserve a more direct response. One approach that would help contextualize the spatial effects would be to compare their magnitude to that of another feature - object identity, for example - to give readers a sense of the relative importance of spatial versus non-spatial information in memory representations. I recognize this may not be straightforward with the current design, but even a brief discussion of how one might benchmark the spatial effects would be helpful.

(8) The attention account.<br /> I found the discussion of attention less than fully convincing. The authors appear to argue against an attentional interpretation of the spatial effects, but it is not clear why participants wouldn't attend to the encoded location during retrieval - particularly in a design with relatively few retrieval cues, where spatial location may be one of the most useful available. The attention account thus seems difficult to rule out on the basis of the current data, and the discussion should engage more seriously with this alternative rather than setting it aside.

(9) Later-remembered versus later-forgotten objects - BOLD signal.<br /> Were later-remembered objects associated with stronger overall BOLD responses during encoding compared to later-forgotten objects, or was the effect specific to the pRF modelling? Clarifying this would help readers understand whether the spatial effects are part of a broader pattern of stronger encoding or something more specific to the spatial reinstatement mechanism.

Reviewer #1 (Public review):

This study examines the mechanisms underlying retinal toxicity associated with certain AAV gene therapy vectors, particularly in the retinal pigment epithelium (RPE) and photoreceptors following expression of transgenes such as GFP. The findings suggest that AAV-related retinal toxicity is driven less by transgene identity itself and more by distinct pathogenic mechanisms, including stress-induced injury in RPE cells and interferon-mediated damage in photoreceptors. The comments are as follows:

(1) The AAV vectors were manufactured in-house, and the production method is described in sufficient detail. However, were any characterization assays performed beyond qPCR-based titer determination, such as vector genome titer, capsid titer, empty/full capsid ratio, sterility, bioburden, endotoxin, mycoplasma, residual host cell DNA, residual plasmid DNA, or residual host cell protein testing? These analyses, particularly those assessing residual impurities and microbial contamination, are critical, as such contaminants may provoke inflammatory responses following subretinal injection. This, in turn, could confound the interpretation of the results, including the identification of the molecular pathways contributing to toxicity as well as the specific role of GFP-associated toxicity. Please provide any characterization information for the AAV vectors.

(2) The study uses contralateral or uninjected eyes as controls, but this choice may not adequately account for changes induced by the subretinal injection procedure itself. Because the earliest assessment of RPE toxicity was performed at 2 weeks post-injection, any injury, inflammation, retinal detachment-related stress, or wound-healing responses triggered by the surgical procedure could have contributed to the observed phenotype. As a result, comparisons to uninjected eyes alone make it difficult to distinguish vector or transgene-specific toxicity from procedure related effects. Inclusion of a more appropriate procedural control, such as sham-injected eyes or eyes injected with vehicle/buffer alone, would have strengthened the study by enabling clearer discrimination between injection-related retinal responses and toxicity attributable to the AAV construct or transgene expression.

(3) The authors used phalloidin staining on RPE-choroid flatmounts to evaluate RPE toxicity, which provides useful information on RPE morphology and structural disruption. However, it would be highly informative to also assess the presence and distribution of subretinal microglia/macrophages, for example, by Iba1 immunostaining, in the same preparations. Specifically, determining whether Iba1-positive cells accumulate in or around areas of RPE dystrophy would help clarify the contribution of local inflammatory responses to the observed pathology. Such analysis could strengthen the interpretation of the toxicity phenotype by revealing whether RPE degeneration is accompanied by focal immune cell recruitment and whether these cells spatially associate with regions of tissue damage. This would also provide additional insight into whether inflammation is likely to be a downstream consequence of RPE injury or a more direct contributor to disease progression, especially in light of publications by Danial Saban's group regarding the characterization of microglia phenotypes using RNA-seq analysis.

(4) The Discussion should also address the anatomical and procedural differences between neonatal and adult mouse eyes, particularly with respect to retinal thickness and the potential impact of subretinal injection-related injury. Because the RPE toxic effects appeared less severe in adult mice, it would be valuable for the authors to consider whether this difference reflects true age-dependent biological susceptibility or, at least in part, differences in the mechanical consequences of the injection procedure. Neonatal retinas are thinner and structurally less mature than adult retinas, which may render them more vulnerable to injection-associated stress, retinal detachment, or secondary tissue injury following subretinal delivery. In contrast, the greater retinal thickness and maturity of the adult eye may provide some degree of resilience to procedural trauma, thereby reducing the apparent severity of RPE damage. Expanding the Discussion to consider these factors would strengthen the interpretation of the age-related differences observed in toxicity and help distinguish vector- or transgene-driven effects from potential confounding effects introduced by the delivery method itself.

Overall, this manuscript presents a detailed and comprehensive analysis of transgene-induced retinal toxicity and makes effective use of multiple mouse models to dissect the contribution of relevant molecular pathways. The study is particularly strengthened by its systematic approach, combining histologic, transcriptomic, and genetic loss-of-function strategies to distinguish the mechanisms underlying toxicity in the RPE versus photoreceptors. By evaluating several knockout mouse lines, the authors can move beyond descriptive observations and begin to assign causality to specific stress and immune signaling pathways, thereby providing important mechanistic insight into AAV-associated retinal injury. These findings are timely and relevant to the broader field of ocular gene therapy, as they highlight the complexity of vector- and transgene-related toxicity and underscore the need for careful pathway-level evaluation during preclinical development.

Reviewer #2 (Public review):

Summary:

Adeno-associated viruses (AAVs) are popular gene therapy vectors, but AAVs can cause toxicity. This is particularly evident following expression of some transgenes, e.g., GFP, in the retinal pigment epithelium (RPE), which leads to loss of RPE cells and photoreceptors. Here, we sought to unravel the toxicity mechanism(s). Several transgenes, self and non-self, were tested for toxicity, with no clear correlation for this variable. RPE RNA-sequencing revealed upregulation of translational processes, cell stress, cytokine release, antiviral responses, and leukocyte infiltration pathways. Toxicity-inducing pathways were explored for causality by injecting toxic AAVs into mice deficient for intrinsic, innate, or adaptive immune pathways. The CHOP KO partially alleviated toxicity for RPE but not photoreceptors, whereas the type I interferon receptor KO partially alleviated toxicity for photoreceptors but not RPE. In situ hybridization of interferon pathway transcripts (IFNB1, IFNAR1) revealed that the RPE and retina can produce and potentially respond to interferon. These data suggest that transgene-induced cell stress responses in the RPE lead to RPE cell death, while interferon signaling contributes to the death of photoreceptors.

Strengths:

This manuscript used numerous KO mouse models to evaluate the interferon pathway, inflammatory cytokine pathways, the complement pathway, toll-like receptor signaling, cytosolic DNA sensing, double-stranded RNA sensing strain, intrinsic cellular stress pathways, as well as strains deficient for B cells and T cells or B cells, T cells, and natural killer cells. This is a robust piece of work with rigorous controls, groups, and timepoints tested. The RNA-sequencing data provided helpful guidance on the pathways that should be assessed when analyzing AAV toxicity to the retina.

Weaknesses:

The main weakness of the study is that it focuses on subretinal administration to neonatal mice, and the canonical TLR9-MyD88 was not found to have an impact on the AAV toxicity measured. More information could have been provided to understand the discrepancy.

强调了客户端的安全性审查的重要性，尤其是对于拥有广泛权限的编码代理，提醒开发者不要忽视客户端的安全性。

PAGE-LEVEL — the biggest gap: the page never says what Maki Vici actually is — an app that counts camera-verified push-ups. Since we're promoting the app (not the sweepstakes), the most differentiating, trust-building fact is absent. One clause fixes it — best home is Pillar I: "Complete your daily press-up quota, camera-verified." It answers the visitor's silent objection ("how would you know I did them?") and separates this from every habit tracker on earth.

Deliberately left alone: the headline (parallel, punchy, earns its size), "Earn Your Stripes," the warrior@empire.com / Britannia placeholders (charm, zero comprehension cost), and "No spam, just pure discipline" — best microcopy on the page.

Flag — I added this legal line, so judge it with that in mind: it names sweepstakes explicitly in the footer. If the direction is to promote the app and keep rewards vague (and the lede + Pillar III drop "sweepstakes" per the other notes), this can slim down to: "Full rules published at launch. Must be 18+." Keeping the fuller version is also defensible as forward legal cover — coupled decision with those two notes.

Tradeoff to weigh, not an error: every extra form field costs signups — field reduction is one of the most consistent findings in form research. If country only matters for prize eligibility, capture email alone here and ask location in-app at onboarding (which already collects country + state). Counter-argument: eligibility data on the list from day one. It is correctly marked Optional today.

Suggest: "Enter before the gates open. Test the first mechanics and shape what gets built."

Why: three registers collide in one sentence — military HR ("priority deployment access"), aviation ("test-fly"), agile ("product iterations") — and none of them are Roman, or human. "Before the gates open" keeps the world; "shape what gets built" keeps the real promise.

Suggest: "Lock in the founding price for anything premium we ever ship. Forever."

Why: "eternal grandfathered price tier" stacks jargon on jargon — "grandfathered" is US insurance-speak, and "eternal" already does its job. A page asking for email before the product exists is selling trust; plain promises read more trustworthy than clever ones.

Suggest: "A permanent mark on your profile that no one after you can earn. Proof you rode ahead."

Why: "profile distinction identifying you as part of" is HR language. "No one after you can earn" states the actual exclusivity mechanism plainly — and "rode ahead" teaches what a procursator is by using it. Pairs with the CTA note.

Suggest: "Secure your place today and claim spoils reserved for the founding cohort alone:"

Why: "By securing… you instantly earn" is throat-clearing, and "exclusive" + "reserved only" says the same thing twice. One imperative, one scarcity claim, said harder.

Suggest: "Every completed quota earns its spoils. Real reps, real rewards."

Why (per YT's direction): the page promotes the app, not the sweepstakes — and this sentence is currently the most explicit prize-mechanics line on the page. Keep The Spoils mythic, echo the tagline where the value lands, and save mechanics for onboarding. ("Translates directly into" is spreadsheet language either way.)

If some concreteness is wanted: "Every completed quota earns entries toward real rewards."

Suggest: "Daily Stoic wisdom, from Marcus Aurelius to Seneca. An iron mind to match the body."

Why: "Unlock curated daily doses" is app-store filler, and "anchor your physical progression" is brochure-speak. Naming Marcus Aurelius and Seneca is instant credibility with exactly this audience — and "iron mind" deliberately repeats the hero's "forge an iron mind." Repeating your key phrase is a feature, not a bug.

Suggest: "build your empire brick by brick."

Why: empires aren't layered; bricks are countable and physical, like reps — and it echoes Augustus finding Rome a city of brick and leaving it marble. Tiny change, more Roman, more muscle.

Keep this heading. Change the BUTTON below to "Enlist in the Vanguard" and add one line under the heading: "The procursatores rode ahead of the legion. So will you."

Why: the button is the moment of commitment, and right now it asks a cold visitor to become a word they can't parse. Clarity beats cleverness at the CTA — one of the most replicated findings in conversion work. The one-line definition turns the Latin from an obstacle into world-building: you keep the mystique and the signup. Trivial to implement, easy to A/B later.

Suggest: "turn your discipline into real rewards."

Why (per YT's direction): we're promoting the app, not the sweepstakes — "Real Reps. Real Rewards." is vague on purpose. So the hero shouldn't be where the mechanic gets named. Drop "sweepstake" here and let the rewards stay mythic.

(If the word does stay anywhere: "sweepstakes" with the s — that's the standard US term.)

Decide once: press-up or push-up. My vote: push-up.

Why: the app itself says push-up everywhere (Ludus, calibration, camera flow), and YouTube traffic will skew American. Ad → page → app should use one word; every synonym is a tiny "wait, is this the same thing?" If the British voice is a deliberate brand choice, keep press-up — but then use it in-app too. The ask is consistency, not dialect.

Suggest: "pairs daily Stoic philosophy with calisthenics."

Why: "Stoic" is the word this audience already follows (Daily Stoic, Ryan Holiday — an audience millions deep). "Roman philosophy" owns none of that pull, and Pillar II already says "The Stoic Mind," so this also makes the page agree with itself. Rule of thumb: Stoic for the ideas, Roman for the world.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. In the latest version, the authors have made textual revisions that note caveats about the quality of the chromatin accessibility data.]

In the manuscript entitled "Flexible and high-throughput simultaneous profiling of gene expression and chromatin accessibility in single cells," Soltys and colleagues present easySHARE-seq, a method described as an improvement upon SHARE-seq for the simultaneous measurement of RNA transcripts and chromatin accessibility.

The authors demonstrate the utility of easySHARE-seq by profiling approximately 20,000 nuclei from the murine liver, successfully annotating cell types and linking cis-regulatory elements to target genes. The authors claim that easySHARE-seq supports longer read lengths potentially enabling better variant discovery or allele-specific signal assessment, though they do not provide direct evidence to support these specific claims.

A key strength of the protocol is enhanced sequencing efficiency, achieved by shortening the Index 1 read from 99 to 17 nucleotides. This reduction does not come at a significant cost to barcode diversity, retaining approximately 3.5 million combinations. Additionally, the approach allows for the sequencing of a sub-library to assess quality prior to final barcoding and sequencing which seems quite clever.

While the increase in RNA transcript recovery is substantial, it appears to come at a cost: there is a notable decrease in ATAC fragments per cell compared to the original SHARE-seq (and other platforms). Likely as a result, the dimensionality reduction (UMAP) shows good resolution for RNA profiles but relatively poor resolution for accessibility profiles. Furthermore, the presented data suggests potential ambient RNA contamination; specifically, the detection of Albumin in HSCs and B cells is likely an artifact of the protocol rather than a biological signal.

Overall, the study is well-presented and represents a promising advance.

Reviewer #2 (Public review):

Aims:

The authors sought to optimize SHARE-seq, a multimodal single-cell method, to improve the simultaneous profiling of gene expression and chromatin accessibility. Their goal was to enhance barcode design for better sequencing efficiency and cost savings, while improving overall data quality. They then applied their optimized method, easySHARE-seq, to study liver sinusoidal endothelial cells (LSECs) to demonstrate its utility in examining gene regulation and spatial zonation.

Strengths:

The improved barcode design is an advance, increasing the proportion of sequencing reads dedicated to biological information rather than barcode identification. This modification offers practical benefits in terms of sequencing costs and read length, potentially reducing alignment errors. The method also demonstrates improved RNA detection compared to the original SHARE-seq protocol. The biological applications showcase how simultaneous measurement of both modalities enables analyses that would be practically impossible with single-modality approaches, particularly in examining how chromatin states change along developmental or spatial trajectories.

Weaknesses:

There is a notable reduction in chromatin accessibility detection compared to the original SHARE-seq method, likely limiting the use of the method in certain situations.

Overall:

The authors achieve their aim of creating an optimized protocol with improved barcode design and enhanced RNA detection. The method represents a useful advance for specific experimental contexts where the trade-offs are appropriate.

Reviewer #1 (Public review):

Summary:

NPAS4 is an activity-dependent transcription factor that regulates inhibitory synapses onto active pyramidal neurons. In this study, the authors examined whether this molecular mechanism influences neural coding in awake animals. To accomplish this, they generated a sparse, CA1-specific NPAS4 knockout in mice and compared knockout neurons with neighboring wild-type neurons recorded from the same animals during navigation. They found that, although neurons lacking NPAS4, which received diminished somatic inhibition and enhanced dendritic inhibition, still encoded location, their spatial firing was less precise: place fields were broader and less stable, showed weaker firing within the field, and exhibited more firing outside the field. KO neurons also exhibited poorer temporal organization with weaker coupling to theta oscillations and reduced phase precession, two signatures of precise spike timing in the hippocampus. Overall, the study suggests that NPAS4 links the balance of somatic and dendritic inhibition to the quality of circuit-level coding by refining the spatial and temporal precision of neuronal firing.

Strengths:

Using a sparse CA1-specific knockout, the authors compared NPAS4-deficient neurons with neighboring wild-type neurons within the same animal and network. This is a significant advantage because it minimizes confounding factors arising from global circuit disruption, providing a clearer comparison of genotypes. Furthermore, the rigorous optogenetic tagging strategy used to distinguish KO from WT neurons in vivo makes the single-cell comparisons much more convincing. Electrophysiological recordings from intermingled WT and KO neurons enable precise spike-timing measurements relative to a shared local field potential, which would be challenging to obtain with calcium imaging.

Weaknesses:

Rather than an acute manipulation, the authors rely on a chronic, sparse knockout, and NPAS4 had been deleted for at least one month before recording. Consequently, while the paper demonstrates a robust long-term phenotype, it is less definitive about the immediate causal sequence by which NPAS4 induction alters inhibition and reshapes spatial and temporal coding. Furthermore, the study focuses on single-neuron coding during navigation and does not test whether the observed degradation in coding precision leads to corresponding impairments in learning or memory in the same animals. In the discussion, the authors suggest that NPAS4 may be especially important for ripple-associated activity during sleep; however, the paper does not test this possibility.

Reviewer #2 (Public review):

Summary:

The manuscript by Payne and colleagues examines how cell-autonomous loss of the activity-dependent transcription factor NPAS4 reshapes spatial and temporal coding in CA1 pyramidal neurons of behaving mice. The work builds on the Bloodgood lab's established framework in which NPAS4 reorganizes inhibition along the somatodendritic axis of CA1 pyramidal cells, principally by regulating CCK+ basket cell synapses, and asks whether this transcriptionally driven reconfiguration of inhibition propagates into the spike-train statistics that underlie hippocampal function. The combination of sparse Cre delivery with channelrhodopsin-mediated optotagging in Npas4 fl/fl:Ai32 mice is technically elegant, as it permits within-animal comparisons of intermingled wild-type and knockout pyramidal neurons sharing a common LFP, which is a significant analytical advantage for spike-timing analyses and for controlling network-level confounds. The reported phenotype is internally consistent and converges on a coherent story: knockout neurons exhibit broader and less stable place fields, lower signal-to-noise within fields, increased out-of-field activity, weaker theta-phase coupling, and shallower phase precession slopes, with the temporal deficits at least partly explained by enlargement of the spatial receptive field.

Strengths:

Several aspects of the work deserve explicit recognition. The validation of the optotagging strategy is thorough, including the high-power stimulation control to corroborate WT classification and the post hoc histological alignment of GFP+ density with electrophysiologically identified KO fractions. The decision to test NPAS4 function in adult mice maintained in long-term enriched environments addresses an important gap, since most prior work has focused on juveniles or short-term induction paradigms. The acute slice recordings recapitulating the somatodendritic inhibition phenotype reassure the reader that the in vivo measurements are interpreted against a known synaptic substrate. The analytical framework, especially the difference maps across epochs and the linear regression decomposition of phase precession slope into genotype, field size, and theta modulation strength, is rigorous and goes beyond simple group-level comparisons. The conceptual contribution, namely the demonstration that an activity-dependent transcription factor can be tied to single-neuron coding properties in vivo, is meaningful, although it is fair to note that the direction of the effect, given that the CCK to place cell link and the NPAS4 to CCK link have each been established in prior independent studies, is largely along the lines one would predict.

Weaknesses:

The most consequential concern, in my view, is the experimental context in which the entire study is conducted. Every animal is housed in an enriched environment for two to three months, and Figure 1A itself shows that NPAS4 expression in CA1 is essentially undetectable in standard-environment conditions and only emerges with enrichment. This raises the question of whether the manuscript is in fact describing the function of NPAS4 in general, or the function of NPAS4 specifically as recruited by chronic enrichment. The paper, in its current framing, elides this distinction and presents the EE state as if it were the baseline, which it is not. EE is known to alter hippocampal connectivity, the dynamics of place cell ensembles, and the expression of many activity-dependent genes; the CCK to pyramidal cell connectivity that the authors invoke as the mechanistic anchor is also dense in standard housing, so the absence of detectable NPAS4 in SE conditions raises the further conceptual problem of how NPAS4-negative neurons would normally be innervated by CCK+ basket cells in the first place. A direct comparison of WT and KO neurons in standard-environment animals, even on a smaller scale, would discriminate between two very different interpretations, namely that NPAS4 has a constitutive role in tuning CA1 firing versus that it is specifically engaged by enrichment-driven activity and contributes to an EE-specific reorganization of coding. Recent work, including Chiaruttini and colleagues (2025), reports baseline NPAS4 expression in CA1, so the SE result in Figure 1A may itself underestimate normal expression and deserves further scrutiny. Without an SE comparison, the generality of the conclusions cannot be assessed, and the title and abstract risk overstating the scope of the findings, particularly when one considers that NPAS4 is also induced by contextual fear conditioning and other paradigms, which would predict context-specific effects rather than a uniform refinement function.

A closely related concern is the meaning of the knockout itself. Even under EE, only a few percent of CA1 pyramidal neurons express detectable NPAS4 at any given moment (Figure 1A), yet the AAV strategy deletes the gene in 30 to 60 percent of pyramidal neurons. In effect, the majority of cells classified as KO in this study would not have been expressing the protein under the relevant conditions, so the population that is statistically driving the WT versus KO differences must include a non-trivial fraction of neurons in which the deletion has no protein-level consequence. This dilutes the expected effect and raises a more interesting biological question: are the observed phenotypes carried by the few KO neurons that would have expressed NPAS4, or do they emerge from a constitutive function of the gene that is broader than the IHC signal suggests? An additional, related possibility is that NPAS4 expression segregates non-uniformly across functional classes, for example, concentrating in cells with particular firing-rate or spatial-tuning profiles, in which case the "KO" label is binary at the level of the manipulation but graded at the level of biological consequence. Stratifying the KO population by some proxy of activity history, or relating the magnitude of the phenotype to per-cell measures of recent firing, would help address this. As written, the manuscript treats the KO designation as homogeneous, while the underlying biology is almost certainly not.

A third concern, more conventionally statistical, is the treatment of cells as independent observations. The analyses rely almost uniformly on Kolmogorov-Smirnov tests applied to individual units pooled across animals, but cells recorded in the same animal share not only a common subject but a common network, since WT and KO neurons here are intermingled in the same CA1 microcircuit. Cell numbers per animal range widely, so a mixed-effects framework treating animal as a random factor, or a hierarchical bootstrap, would clarify which effects are robust against animal-level and session-level variability and protect against pseudo-replication. This concern is particularly acute for the smaller effects in Figure 2C-E, where the cumulative distributions overlap substantially, and the differences could plausibly be driven by a small number of mice or sessions. In several figures, the individual dots in supplementary panels are not labeled by animal or session, and that information would be useful for assessing how much of each effect is carried by which subset of the cohort.

The absence of a Cre/ChR2 expression control is a separate gap. The comparison throughout the manuscript pits Cre+ ChR2+ neurons (NPAS4 KO) against neighboring non-transduced neurons (WT). This is internally elegant, but leaves open the possibility that part of the phenotype arises from chronic ChR2 expression or constitutive Cre activity rather than from NPAS4 loss, especially given that most of the readouts are subtle. A small companion cohort of Ai32 mice without the floxed Npas4 allele, injected with the same AAV and processed through identical optotagging and electrophysiology pipelines, would address this definitively and is, in my view, a near-essential addition.

Several of the downstream phenotypes would benefit from stratified comparisons that hold first-order properties constant. Many of the downstream differences (stability across epochs, theta coupling, phase precession) could, in principle, be inherited from the upstream difference in firing rate, since the high-firing and high-spatial-information cells in the WT pool are likely contributing disproportionately to the group statistics. The authors do perform firing-rate-matched controls in Figure S4D-G, which is helpful, but the analysis should be extended in two ways: a parallel stratification by spatial information for the stability analyses in Figure 4, and matched comparisons of theta coupling (Figure 5) and phase precession (Figure 6) on neurons drawn from overlapping firing-rate and spatial-information distributions. The regression decomposition for phase precession is a step in this direction and shows that field size, not genotype, is the dominant predictor of slope; this finding, in my reading, deserves more prominent framing in the discussion than it currently receives, since it implies that the temporal precision phenotype is largely downstream of the spatial one rather than a parallel deficit.

The place field stability analysis is interesting but somewhat under-analyzed. The authors show that KO fields shift toward the field entrance more rapidly than WT fields and propose that this reflects an accelerated or dysregulated Mehta-effect-like dynamic. The framing is attractive, but the analysis does not establish that the shifts are systematic in the same way the classical Mehta effect is. An alternative reading is that the elevated out-of-field firing creates spurious local maxima that the peak-finding procedure occasionally classifies as field shifts, especially when in-field firing is reduced. A control analysis using a fixed reference window around the original peak, rather than re-identifying the peak each epoch, would help distinguish a genuine plasticity-like shift from instability driven by noise. The behavior of the WT population in epoch 4 also raises a question: would the drift intensify over longer recording windows, and to what extent is the apparent drift imposed by the repetitive structure of the task itself, in which animals are effectively running on a constrained linear /circular track that may impose drift-like dynamics across the population independently of genotype?

A final note on mechanism. The manuscript leans on prior work showing that NPAS4 regulates CCK+ basket cell synapses, and uses this as the mechanistic anchor for the coding deficits. The connection is reasonable but remains indirect within this study, since the authors do not measure CCK+ interneuron activity, perisomatic inhibition, or local circuit dynamics in the same animals. The discussion already acknowledges some of this, but the speculative framing of dendritic versus somatic inhibition contributions could be tightened, especially given that competing inhibitory sources (PV+ basket cells, axo-axonic cells, OLM interneurons) also shape the spatial and temporal features measured here. A more cautious mechanistic framing, distinguishing what is demonstrated from what is inferred from prior work, would be appropriate.

In summary, this is an ambitious and technically demanding study that makes a meaningful contribution by linking activity-dependent transcriptional regulation of inhibition to the spatial and temporal organization of CA1 spike trains in awake, behaving mice. The within-animal optotagging design is a real strength, the phenotype is internally consistent across multiple coding metrics, and the conceptual implications for how experience tunes single-neuron coding are significant. The principal concerns, namely the unaddressed enrichment confound that pervades the entire dataset, the conceptual ambiguity around what a KO designation actually means at the cell level when only a small fraction of CA1 neurons express the protein, the statistical treatment of nested observations from a shared microcircuit, the missing transgene control, the absence of stratified comparisons by firing rate and spatial information for the secondary phenotypes, and the somewhat overreaching mechanistic framing of the discussion, are all addressable, and if handled carefully would substantially strengthen the manuscript. With these revisions, the work would be a valuable contribution to the literature on how the molecular memory of activity shapes circuit-level coding.

Reviewer #1 (Public review):

This revised manuscript represents a partial response to the concerns raised in the first round of review. The authors have made one genuine mechanistic addition in the form of the semi-permeabilized cell reconstitution assay, removed the most overreaching conclusions regarding the contribution of cytoplasmic TDP-43 aggregation to disease, and made several minor presentational improvements. However, the central weaknesses of the original submission remain substantially unaddressed. The exclusive reliance on non-physiological TDP-43 variants, the incompletely resolved mechanism linking XPO1 to TDP-43 phase behavior, and the limited organoid validation continue to limit confidence in the major claims. The authors have, in several instances, responded by removing contested data rather than by providing the additional evidence that was requested.

(1) The justification for the 2KQ acetylation-mimetic system remains inadequate.

The authors respond to the concern about the non-physiological nature of the 2KQ mutant by citing published evidence that TDP-43 acetylation occurs in ALS patient spinal cord and is upregulated under oxidative and proteotoxic stress conditions. While these references are real and support the relevance of acetylation as a pathological post-translational modification, they do not resolve the central concern: there is no quantification of how much endogenous TDP-43 is acetylated at the specific lysine residues mimicked by 2KQ in degenerating human neurons, and no evidence that the degree of RNA-binding disruption imposed by the double glutamine substitution is ever achieved by endogenous acetylation in vivo. The 2KQ mutant eliminates RNA binding essentially completely, whereas physiological acetylation events are graded, reversible, and likely partial. The response conflates the existence of TDP-43 acetylation as a phenomenon with validation that 2KQ is a physiologically accurate model of that phenomenon. None of the new experiments address the request to test whether wild-type TDP-43 expressed at near-physiological levels, or a bona fide heterozygous ALS-linked TARDBP mutant in iPSC-derived neurons, responds to XPO1 modulation in a qualitatively similar fashion. Until this is shown, the mechanistic conclusions of this paper remain constrained to a highly artificial overexpression system and cannot be extrapolated to physiological or pathological TDP-43 biology with confidence.

(2) The homozygous K181E organoid model is still not adequately justified, and no heterozygous comparison has been provided.

The authors acknowledge that the homozygous background is "more sensitive for detecting phospho-TDP-43" and argue that homozygous conditions are commonly used in experimental TDP-43 research. However, the critical issue is not whether homozygous models are used in general, but whether the homozygous background specifically alters the relative contribution of cytoplasmic aggregation versus nuclear RNA-processing dysfunction in this study. In a homozygous K181E model, both alleles produce an RNA-binding-defective TDP-43, meaning that every molecule of endogenous TDP-43 in the cell is dysfunctional. This is categorically different from the patient situation in which one wild-type allele is present, and it may substantially exaggerate nuclear loss-of-function relative to cytoplasmic gain-of-function phenotypes. The authors have not performed the requested comparison with heterozygous K181E/+ organoids, nor have they acknowledged that the organoid genotype itself could bias the interpretation of what KPT-276 treatment rescues. Given that the organoid section is now the sole in-disease-model validation of the XPO1 mechanism, this limitation is more consequential than it was in the original submission.

(3) The new semi-permeabilized cell data is a genuine contribution, but the mechanistic interpretation remains insufficiently constrained.

The development of the streptolysin O semi-permeabilized cell reconstitution system is the most substantive new addition to this revision. The finding that LMB-stabilized anisosomes resist cytosol washout but dissolve upon RNase T1 treatment is interesting and provides a plausible indirect mechanism: XPO1 inhibition retains nuclear RNA, and this elevated nuclear RNA availability contributes to maintaining the liquid LLPS state of the TDP-43 2KQ condensate. This is a meaningful mechanistic advance and deserves credit. However, several important limitations of this new data are not adequately discussed. First, RNase T1 degrades single-stranded RNA globally during permeabilization, so the experiment does not identify which specific RNA species stabilize the anisosome, nor whether these are pre-mRNA splicing intermediates, mature mRNA, non-coding RNA, or another class. Second, the same nuclear export blockade that retains RNA will also retain the nuclear concentrations of many RNA-binding proteins, splicing factors, and other XPO1-dependent cargos. The RNase T1 experiment does not exclude the possibility that the relevant effect is mediated by an RNA-binding protein whose nuclear concentration increases upon LMB treatment and which, upon RNase digestion, can no longer engage TDP-43 or the anisosome shell. Third, the permeabilized cell system is by definition not intact and has lost cytosolic factors; whether the RNA-dependent stabilization of anisosomes operates in the same way in intact cells during physiological or pathological nuclear export perturbation is an assumption, not a demonstrated fact. The authors should more carefully frame these data as hypothesis-generating and explicitly note these alternative interpretations in the Discussion.

(4) The conceptual asymmetry between XPO1 inhibition and XPO1 overexpression phenotypes is not resolved by the new mechanism.<br /> The paper continues to present two XPO1 perturbation phenotypes that are difficult to reconcile within a single mechanistic model. XPO1 inhibition enlarges anisosomes, maintains their liquid character by FRAP, and retains them in the nucleus. XPO1 overexpression also enlarges TDP-43 puncta, but these are FRAP-impaired, gel-like, and appear in the cytoplasm. The RNA-retention model proposed by the new semi-permeabilized data explains why XPO1 inhibition stabilizes the liquid state, but it does not explain why XPO1 overexpression drives the opposite outcome: gel-like hardening and cytoplasmic redistribution. If increased nuclear RNA availability is the key variable downstream of XPO1 inhibition, then XPO1 overexpression would be expected to decrease nuclear RNA and thereby destabilize anisosomes toward dissolution or hardening. The paper does not test whether nuclear RNA levels are indeed altered by XPO1 overexpression, nor whether the cytoplasmic gel-like puncta seen in XPO1-overexpressing cells are RNA-poor relative to control anisosomes. The revised Discussion does not engage with this asymmetry in a satisfying way, and the figure model remains qualitative. A quantitative or at least semi-quantitative model that accounts for both arms of the XPO1 perturbation is needed.

(5) The removal of RNA-seq data weakens rather than strengthens the organoid section.

The authors have removed the bulk RNA-seq analysis from the revised manuscript in response to concerns that the modest transcriptional rescue was being over-interpreted. While the decision to remove over-interpretation is appropriate, the result is that the organoid section now rests entirely on pTDP-43 immunostaining as its sole readout. The revised paper thus uses reduction in immunofluorescent pTDP-43 puncta in homozygous K181E organoids as the only evidence that nuclear export inhibition mitigates TDP-43 proteinopathy in a disease-relevant context. This is a weaker evidentiary base than before the revision, not an improvement. The originally requested more sensitive orthogonal readouts, including biochemical fractionation for SDS-insoluble TDP-43, filter-trap assays, or RNA aptamer-based detection of TDP-43 aggregates, remain absent. Without at least one additional independent measure confirming that cytoplasmic TDP-43 aggregation is genuinely reduced rather than simply rendered antigenically undetectable, the organoid conclusion is not adequately supported. At minimum, the authors should provide total and cytoplasmic TDP-43 fractionation data from organoid lysates to corroborate the immunostaining result.

(6) No functional neuronal readout has been provided for the organoid model.

The organoid section now makes the claim that "nuclear export is required for the formation of p-TDP-43-containing aggregates in a disease-relevant organoid model," but no measure of neuronal health, integrity, or function is reported in association with this. Even a simple assessment of neuron survival by TUJ1 or MAP2 quantification, neurite complexity, or cleaved caspase-3 staining before and after KPT-276 treatment would substantially strengthen the biological significance of the pTDP-43 reduction. The current data establish a pharmacological effect on a pathological marker but do not demonstrate that this has any consequence for neuronal biology in the organoid, which is what the disease-relevance framing implies.

(7) The abstract and title continue to overstate the mechanistic conclusions.<br /> Despite the stated intent to reframe the study as a screening study and to temper the conclusions, the revised abstract retains the language: "These findings establish nuclear export as a key regulator of TDP-43 phase transitions and define a mechanistic framework that links altered nuclear transport and phase dynamics to TDP-43 aggregation potential." Similarly, the Discussion still states: "a particularly compelling aspect of our study is the discovery that the nuclear export receptor XPO1 governs TDP-43 liquid-to-solid transitions and subcellular localization." The word "governs" and the phrase "establish nuclear export as a key regulator" are not warranted by data that derive entirely from an overexpressed acetylation-mimetic mutant in a colon cancer cell line and a homozygous K181E organoid model. A more accurate framing would describe these findings as identifying nuclear export as one of several cellular processes that modulate TDP-43 phase behavior in a sensitized model system, with an indirect RNA-mediated mechanism that remains to be defined at the molecular level. The title change from "governs" to "modulates" is appreciated but does not extend into the abstract and Discussion, where the strong causal language persists.

(8) Individual siRNA knockdown validation for XPO1 has not been provided.

The authors argue that validation with 6 independent siRNAs across two rounds of screening, combined with convergent pharmacological data, is sufficient to establish XPO1 as a genuine hit. While the convergence of chemical and genetic evidence is reassuring, the specific request was for protein-level confirmation of XPO1 knockdown efficiency in the DLD1 TDP-43 2KQ cells used for mechanistic follow-up, together with demonstration that the anisosome phenotype is specifically caused by loss of XPO1 and not by off-target effects. This is a straightforward experiment, and its absence is particularly notable given that the entire mechanistic XPO1 narrative hinges on this specificity. At minimum, an immunoblot confirming XPO1 protein depletion in cells treated with the siRNA pool identified in the screen, in the same cell background and induction conditions as the follow-up experiments, should be provided.

(9) The identity of XPO1-dependent cargos that regulate anisosome dynamics remains entirely unknown.

The authors acknowledge that XPO1 does not directly bind TDP-43 and that the mechanism is likely indirect. The new RNA data provides one plausible indirect pathway. However, the possibility that one or more specific RNA-binding proteins or splicing factors, whose nuclear levels rise upon XPO1 inhibition, are the proximate drivers of anisosome stabilization has not been addressed. This matters because if the relevant mechanism operates through a specific cargo rather than bulk RNA retention, the model for how nuclear export connects to TDP-43 aggregation in disease would be fundamentally different. The authors decline to pursue adaptor identification on grounds of scope, which is a defensible position for future work. However, the framing should explicitly state that the current data cannot distinguish between bulk RNA retention and cargo-specific effects, and that the conclusion that nuclear export modulates TDP-43 phase behavior via RNA accumulation is a working hypothesis supported by but not proven by the RNase T1 experiment.

Minor remaining issues.

The number of independent iPSC clones and organoid batches used for the KPT-276 treatment experiment is now stated as two batches per condition, which is minimal for a 3D organoid study and does not fully address the concern about clone-level variability. Ideally, organoids from at least two independently derived isogenic clones per genotype would be used. The mCherry overexpression control added in Supplemental Figure 4 is a useful addition and is acknowledged. The immunoblotting confirmation that drug treatments do not alter total TDP-43 levels addresses a prior concern adequately. The addition of the sentence noting that anisosomes have not been validated in human patient samples is appreciated and appropriate. Statistical detail has been improved in figure legends. These minor improvements are noted positively but do not compensate for the major unresolved concerns above.

Reviewer #2 (Public review):

This manuscript addresses an important and timely question in TDP-43 biology by systematically identifying regulators of TDP-43 anisosome formation, with a particular focus on nuclear export via XPO1. Using a combination of unbiased chemical screening, genetic perturbation, and advanced imaging approaches, the authors propose that inhibition of nuclear export modulates the abundance and biophysical properties of TDP-43 anisosomes. They further strengthen their findings by introducing an additional model system, a semi-permeabilized in vitro assay, which provides mechanistic evidence that XPO1 activity prevents anisosome dissolution by retaining nuclear RNAs. The study is conceptually innovative and has potential relevance for neurodegenerative diseases characterized by TDP-43 pathology. Some minor concerns remain, mostly about experimental design of the newly added data.

Strengths:

(1) The study employs an unbiased, hypothesis-free compound screen to identify regulators of TDP-43 anisosome formation, which is a major strength and reduces confirmation bias.

(2) The authors combine chemical and genetic screening approaches, providing orthogonal validation of key pathways and increasing confidence in the biological relevance of top hits.

(3) The focus on biophysical properties of TDP-43 assemblies, assessed through imaging and FRAP, moves beyond simple presence/absence of aggregates and provides mechanistic insight into the biophysical states of TDP-43.

(4) The use of multiple experimental modalities, including live-cell imaging, FRAP, pharmacological perturbation, and transcriptomic analysis, reflects a technically sophisticated and ambitious study design.

(5) The authors attempt to extend findings beyond immortalized cancer cell lines by incorporating organoid models, demonstrating awareness of disease relevance and translational importance.

(6) The authors extend their study by incorporating a semi-permeabilized in vitro system, which provides compelling evidence that inhibition of nuclear export promotes the retention of nuclear anisosomes, an effect driven by the accumulation of nuclear RNAs.

Overall, the manuscript is clearly written and logically structured, making complex experimental workflows accessible and the central hypotheses easy to follow.

Weaknesses:

(1) The manuscript has significantly improved with the revisions. Some experimental procedures and method details, as well has statements remain incompletely described:

a) What is the smear in Figure S1 after VLX treatment?

b) The authors state that "The reduction in TDP-43 signal was not due to protein elimination.", however no data is provided to support that statement.

c) The authors state that "TDP-43 shifts from phase-separated state to a soluble state ...", however no data is provided to support that statement.

d) Why did the authors choose cow lover cytosol for this study?

e) The experimental setup for supplementing with cytosol/ATP/GTP is unclear. A more detailed schematic would be helpful to understand at what stage in the experiment these factors were added. Which step of the protocol was performed at 37 {degree sign}C, which is indicated in the figure schematic but not described in the methods.

f) In the organoid model, the authors mention that they observe similar levels of total TDP-43, however they do not provide quantification. Instead, they provide a graph that shows highly significant changes in nuclear TDP-43, which was not addressed in the text.

Additionally, some questions remain unclear:

(1) The anisosomes induced by ATP/GTP or cytosol are insufficiently characterized. It remains unclear whether these structures correspond to canonical ring-shaped anisosomes, and whether they exhibit dynamic (liquid-like) or more static (gel-like) properties.

(2) The contribution of the cytosol and ATP/GTP supplementation experiments to the overall narrative is unclear. While the findings are intriguing, their interpretation within the context of the study is not well articulated. In particular, the rationale for including cytosol is not sufficiently justified, given that ATP/GTP alone induces a pronounced effect, whereas cytosol alone does not.

(3) The authors should address why endogenous XPO1 does not co-localize with anisosomes, whereas overexpressed XPO1 does. This raises the possibility that the observed co-localization may be an artifact of non-physiological protein levels, which should be discussed.

(4) The iPSC-based model remains insufficiently characterized. While the authors propose that this system recapitulates the accumulation of liquid and solid aggregates resembling anisosomes, it is unclear whether this phenotype is robustly observed and whether KPT treatment effectively modulates it.

(5) The rationale for the selected treatment durations is unclear, and the timing appears inconsistent across experiments (ranging from 3 to 16 hours), including within experiments involving the same compound. This variability should be justified or standardized.

(6) Several figure legends require clarification:

a) In the section stating "Collectively, our results suggest that the stability and dynamics of anisosomes are modulated by XPO1-mediated nuclear export ...", the cited figure appears to be incorrect. This should refer to Figure 5L rather than Figure 5J.

b) Figure 1B: Please specify the number of replicates per concentration, the number of cells analyzed, and the model used for regression analysis. Additionally, the legend indicates a treatment duration of 15 hours, whereas Figure 1A states 24 hours.

c) Figure 2G: The authors state "7 anisosomes per condition," but the graph displays only 4-6 data points. Please clarify what each data point represents.

d) Figures 3B and 3G: Please clarify whether a defined threshold was used to determine a "reduction in anisosome number."

e) Figure 4B: These do not represent biological replicates, as all samples derive from a single cell line; rather, they constitute independent experimental replicates.

f) Figures 5B and 5H: The legend states "n = 3 biological repeats," but the number of data points shown appears higher. Please clarify.<br /> g) Figures 5K, 6C, and 6E: "Mean Fluorescence Intensity (MPI)" should be corrected to "MFI."

h) Figure 6C: Please include the number of cells analyzed and provide relevant statistical measures (e.g., R², p-value).

i) Figure 6D: The experimental timeline is unclear. Please specify the duration of incubation and the timing of each step.

j) Figure 7B: Improved labeling is needed (e.g., clarification of "mean spot volume") to better align with the figure legend.

Reviewer #3 (Public review):

Summary:

TDP-43 proteinopathy is broadly found in neurodegenerative diseases. This manuscript investigates how nuclear export influences the biophysical properties of TDP-43. The authors use a combination of chemical screening and genome-wide siRNA screening to identify pathways that modulate TDP-43 liquid-to-solid transitions. Overall, the study employs a broad array of approaches and addresses an important question in TDP-43 pathobiology. The identification of nuclear export as a central regulator is compelling and conceptually aligns with the emerging view that TDP-43 nucleocytoplasmic trafficking is a major defect in neurodegeneration.

Strengths:

This work integrates chemical and genetic screening to identify novel modifiers. The candidates were validated in both reporter cell lines and iPS-differentiated organoids. The findings support the nucleocytoplasmic transport is important for the biophysical properties of TDP-43.

Comments on revised version.

The manuscript has been improved with more data and clarification. The RNase T1 treatment experiment suggests that RNA is required for anisosome integrity. However, this does not directly demonstrate LMB increases nuclear RNA availability as changes in protein composition or other RNA-dependent mechanisms may also contribute. The conclusion and discussion need to be edited to consider these alternative scenarios. Overall, as most of the evidence remains indirect, the manuscript should avoid overinterpretation regarding the mechanisms underlying TDP-43 phase transition and aggregation.

Reviewer #1 (Public review):

Summary:

This preprint investigates the molecular mechanism by which warm temperature induces female-to-male sex reversal in the ricefield eel (Monopterus albus), a protogynous hermaphroditic fish of significant aquacultural value in China. The study identifies Trpv4 - a temperature-sensitive Ca²⁺ channel - as a putative thermosensor linking environmental temperature to sex determination. The authors propose that Trpv4 causes Ca²⁺ influx, leading to activation of Stat3 (pStat3). pStat3 then transcriptionally upregulates the histone demethylase Kdm6b (aka Jmjd3), leading to increased dmrt1 gene expression and ovo-testes development. This work aims to bridge ecological cues with molecular and epigenetic regulators of sex change and has potential implications for sex control in aquaculture.

This revision is an improvement to the manuscript. However, there are still several remaining issues that are not resolved and that limit enthusiasm.

(1) The Supplementary File 1 contains a compilation of Western blots. However, the control protein (for example GAPDH) is on a *different gel* in all of the tabs. For best practices, the protein that is used as the "loading control" needs to be on the same membrane (same Western blot), not on a different blot. It is not compelling to normalize a loading control protein on a separate blot. This reduces enthusiasm for all of the protein data in the manuscript.<br /> a. The blots under the tab "Fig. 5D" are dirty and the blot the GAPDH is over-exposed.

(2) The images provided in the response to authors have no legends and are not explained in the text. As such, they are not supportive data in their current form.

(3) The antibodies that were listed as "home-made" need to be described in great details. For example, we need to know the species that the antibodies were generated in. Additionally, we need to know the antigen (amino acid residues of the recombinant protein).

(4) The reference genes for the qRT-PCR are not listed in the Materials and Methods. The authors need to list the reference gene and tell us why they selected those genes.

(5) The comparison of the turtle and ricefield eel of kdm6b should be shown as a supplementary file and not listed as data not shown.

Reviewer #1 (Public review):

Summary:

This work investigates the membrane insertion of aromatic-centered sequences in IDPs. Using a combination of all-atom MD simulations, the PPM method, and development of the sequence-based predictor AroMIP, the authors aim to establish a quantitative membrane insertion role for aromatic-centered motifs. The study demonstrates that flanking aliphatic and basic residues promote membrane insertion, whereas acidic and polar residues suppress insertion, and further reveals a difference between F/W-centered motifs and Y-centered motifs. The resulting AroMIP model achieves high predictive accuracy on human IDPs and is implemented as a publicly accessible web server.

Strengths:

This work addresses an important biological problem, as aromatic-driven membrane insertion remains poorly characterized despite mediating diverse functions like membrane remodeling and signaling. A key strength is the combination of complementary approaches, e.g., MD simulations provide mechanistic insight into insertion pathways, while PPM enables exhaustive sequence space exploration. The large-scale analysis clearly establishes L and R as promoters and E, N, and G as suppressors. The work also provides valuable mechanistic insight into how aromatic, aliphatic, and basic residues cooperate to stabilize membrane insertion states. Another important strength is the development of AroMIP as a practical prediction tool with a user-friendly online server that appears computationally efficient and broadly accessible to the community. The work is also well connected to prior experimental and computational literature, and the authors carefully position their findings within existing knowledge of membrane-associated IDPs.

Weaknesses:

A primary limitation is the heavy reliance on computational modeling. Training for AroMIP is generated using PPM rather than direct experimental measurements, and so the model may primarily reproduce PPM behavior rather than true membrane insertion thermodynamics. Moreover, all simulations use a single lipid composition (POPC:POPS:PIP₂ 70:25:5), but biological membranes vary substantially in cholesterol, cardiolipin, and acidic lipid content. Whether AroMIP's predictions transfer to diverse lipid environments remains untested. The 5% PIP₂ concentration used in the simulations is higher than that of a normal mammalian cell and may therefore overemphasize electrostatic contributions. Applicability beyond short 9-residue motifs is unclear, as longer-range interactions or secondary structure in full-length IDRs could modulate insertion in ways the current model does not capture. This could be considered for future development.

Reviewer #2 (Public review):

Summary:

The paper addresses an interesting problem. The authors develop a method to assess the probability of insertion of aromatic residues in intrinsically disordered regions of proteins, to insert in the interfacial regions of membranes.

Strengths:

(1) The idea of the article seems very interesting. The problem of membrane association mediated by aromatic residues is definitely worth studying. Aromatic residues, especially Tryptophan (W), but also, albeit to a lesser extent, Phenylalanine (F), and Tyrosine (Y), are well known to partition preferentially to the headgroup region of the lipid bilayer.

(2) The authors propose to decipher the sequence code for insertion of sequences containing aromatic residues in the membrane employing three types of calculation methods with decreasing order of detail and complexity, but increasing order of efficiency. First, all-atom MD simulations; second, the PPM method (protein positioning in membranes) from Lomize et al (2006), Protein Sci 15, 1318; and third, AroMIP, a mathematical model developed by the authors. The results obtained with the different simulations and mathematical methods are internally consistent.

Weaknesses:

(1) Aromatic residues have been shown to partition preferentially to the headgroup region of the lipid bilayer. Most of the papers on this problem were published in the mid 1990s to early 2000s. Some of the most important papers in this regard are the following: von Heijne, Annu. Rev. Biophys. Biomol. Struct. 1994, 23, 167-192; Doyle et al. Science 1998, 280, 69-77; Landolt-Marticorena, et al. J. Mol. Biol. 1993, 229, 602-608; Killian & von Heijne, TIBS 2000, 25, 429-434; Marx & Fleming J. Am. Chem. Soc. 2021, 143, 764-772. Strangely enough, none of these articles is cited.

(2) This is the most important point and the most serious weakness. The authors find that the PPM method is able to reproduce the results from MD simulations, and the AroMIP model is able to perform well in comparison with PPM and MD, after training AroMIP on a large set of IDR sequences (intrinsically disordered protein regions) of the human proteome. The defining feature of the AroMIP calculation is the recognition of the importance of flanking residues in the membrane-insertion propensity of a sequence containing a central aromatic residue. All this sounds good. However, this is all theoretical. There is no connection to experiment or to any method that draws from experiment. The entire approach relies on the assumption that the MD simulations produce the correct results. There is no proof of the correctness of anything. As one of the greatest physicists of our times, Richard Feynman, wrote, "The test of all knowledge is experiment. Experiment is the sole judge of scientific "truth"."

(3) The drawings in Figures 2 and 3 are incorrect and misleading. The size of the Tryptophan side chain is about 5.5 Å, whereas one-half of the bilayer ("a monolayer") thickness is about 15 Å. But in the figures, the lipid length and the Trp side chain seem about the same size. This is incorrect even in a qualitative sense.

Reviewer #3 (Public review):

Summary:

This is a well-written manuscript that describes three robust and complementary computational approaches to unravel the sequence determinants of membrane insertion, specifically of intrinsically disordered regions (IDRs) containing aromatic-centered insertion motifs.

Strengths:

A robust, multifaceted computational approach employing aromatic-centered model membrane-insertion peptides, which provides critical insights into the determinants of membrane insertion.

Weaknesses:

I only have specific concerns about some of the models used for this purpose.

(1) Membrane composition and lipid shape characteristics: The authors chose to use a model membrane bilayer of a distinct lipid composition, POPC: POPS: PI4,5P2 (70:25:5 molar ratio), for their all-atom simulations of the various model peptides. While this may be pertinent for some of these peptides, it is not for many, such as sequence 2 derived from Drp1, which preferentially binds target conical lipids such as cardiolipin (CL) and phosphatidic acid (PA). The rationale behind using PI4,5P2, which can induce positive membrane curvature when sequestered, versus CL and PA, which both induce negative membrane curvature, is not explained.

(2) Parallel vs. perpendicular peptide orientation of sequence 2 in peripheral Drp1-lipid interactions: On page 11, the authors state that their simulation results of sequence 2 derived from Drp1 "contrasts with a transmembrane orientation proposed by Mahajan et al." However, upon review, a transmembrane orientation for this region has never been proposed anywhere. Drp1 is a peripheral membrane protein that reversibly binds CL- and PA-containing membranes via its intrinsically disordered variable domain containing an aromatic-centered WRG motif. Indeed, the model presented in Figure 9 of Mahajan et al. displays a peripheral and parallel orientation of the transiently helical WRG-containing motif rather than a transmembrane (i.e., across the bilayer) orientation. While the authors can distinguish between a parallel vs. perpendicular orientation of this sequence relative to the plane of the membrane bilayer surface from their simulations, suggesting that previous studies indicated a transmembrane orientation for Drp1 is disingenuous and misleading. The term "transmembrane" should be removed or replaced, as it presents a wrong image.

(3) Mutational analysis of W vs. F in membrane insertion of W-centered insertion motifs and vice versa: The PPM-based workflow suggests that F-centered sequences have the highest membrane insertion properties as opposed to W-centered ones. A W552F mutation in the WRGML sequence of Drp1 was, however, found to impair function. How do the authors rationalize this? A cross-mutational analysis of W vs. F in W-centered motifs and F-centered motifs is warranted.

Reviewer #1 (Public review):

Summary:

Forbes et al. developed an integrated approach to identify cis-regulatory elements (CREs) in the large (3.6 Gbp) genome of the crustacean Parhyale hawaiensis, addressing the challenge of pinpointing these regions among large regions of non-coding sequences. They combined ATAC-seq chromatin accessibility profiling (both bulk and single-nucleus) across embryonic and adult tissues with low-coverage genome sequencing of three congeneric species (P. aquilina, P. darvishi, P. plumicornis). Without assembling congener genomes, they mapped reads with low stringency to the P. hawaiensis reference, identifying about 55k conserved islands that overlap ATAC peaks more than expected by chance. This dual filter was used to select CRE candidates for transgenic reporter validation, yielding 6 functional elements (out of 11 tested) driving ubiquitous, neuronal, or muscle-specific expression, a major advance for non-model systems with large genomes.

Strengths:

Forbes et al. generated high-quality ATAC data across multiple scales. Using bulk ATAC-seq (from whole embryos, developing and adult legs), they identified tens of thousands of open chromatin peaks across the assembled P. hawaiensis large genome. Moreover, using single-nucleus ATAC-seq from adult legs, they could resolve differentially accessible chromatin profiles across over 15 cell types previously identified by scRNA-seq, enabling cell-type-specific candidate selection.

Furthermore, their innovative low-coverage comparative genomics method mapped 0.46-6.4% of congener reads to P. hawaiensis without genome assembly, revealing hundreds of thousands of conserved non-coding islands, including about 55k showing conservation in all four species, far exceeding random expectation.

Using the developed approach, the authors could validate 6 (out of 11 candidates) reporter constructs, driving robust ubiquitous and tissue-specific expression, succeeding where prior promoter-only screening failed and providing immediately useful genetic tools for the Parhyale community.

Weaknesses:

The primary limitation is that functional CRE testing was performed only in P. hawaiensis. While conservation maps are valuable resources, the manuscript lacks functional validation in congener species, limiting claims about broad applicability across related genomes/species.

The approach also failed to validate developmental CREs. None of the candidates from combined ATAC and conservation filtering drove reporter expression matching endogenous patterns. The authors appropriately hypothesize technical limits (low expression) or biological factors (long-range enhancers, shadow enhancers).

Overall Assessment:

Forbes et al. fully succeed with their integrated approach to (1) generate an ATAC-seq atlas plus functional CRE discovery and (2) innovative low-coverage sequencing for conservation mapping in the large 3.6 Gbp genome of Parhyale hawaiensis. Their combination of ATAC-seq chromatin accessibility profiling (bulk and single-nucleus) across embryonic and adult tissues with low-coverage genome sequencing of three congeneric species (P. aquilina, P. darvishi, P. plumicornis), without congener genome assembly, drastically shrank the CRE search space. Using this approach, the authors could validate six out of 11 candidate transgenic reporters (ubiquitous, neuronal, and muscle-specific), where prior promoter-only screening failed.

The low-coverage mapping innovation cuts cost and labour while snATAC-seq provides cell-type resolution, making these resources valuable for building new genetic and imaging tools in Parhyale.

This compelling method also has the potential to enable labs with limited resources to identify and characterize regulatory elements in more non-model organisms, advancing our understanding of their evolution while establishing a scalable pipeline for large-genome systems.

Reviewer #2 (Public review):

The manuscript by Forbes, Skafida, Karapidaki et al. concerns the in silico identification of cis-regulatory elements (CREs) in large genomes using chromatin accessibility (ATAC-seq) and sequence conservation (genomic DNA sequencing) data. They exemplify this method by applying it to identify novel CREs in Parhyale hawaiensis, which they validated using reporter constructs.

The results are convincing and are well supported by the data and validations. Identified CREs are valuable for researchers interested in the regulation of the expression of genes they control.

The methodology on the whole is also valid, as suggested by the results and previous publications on various taxa. Sequence conservation, as stated by the authors, was long used as a method to identify regions of non-coding DNA with functional and evolutionary constraints. The same applies to ATAC-seq data, which has also been used as a proxy for functional regions in different animals such as sea urchins and amphioxus. The methodology proposed is likely to be successfully used by researchers working on a variety of experimental organisms.

The authors do not use existing genome assemblies and use short-read sequencing to identify conserved regions, and while it is not conceptually novel, such an approach is becoming more and more viable and useful considering the recent advances in next-generation sequencing technology and the decrease in price of short-read sequencing.

Two major weaknesses are:

(1) The novelty of the approach and its advantages should be more explicitly stated.

(2) The authors do not discuss in depth the strength of using a combination of two methods rather than either of the two, especially considering that previously known CREs do not overlap with conserved sequences.

Reviewer #3 (Public review):

Summary:

Forbes et al. present a new approach for identifying cis-regulatory elements in large genomes. Using Parhyale hawaiensis, a crustacean with a large genome (~3.6 Gb, comparable in size to the human genome), the authors show that current methods for identifying cis-regulatory elements, effective in smaller genomes, are markedly inefficient in organisms with large genomes. To address this limitation, they combine bulk ATAC-seq and single-cell (sc) ATAC-seq to identify chromatin regions that are either ubiquitously accessible or specifically accessible in particular cell types. They further integrate comparative genomics across multiple Parhyale species (P. hawaiensis, P. aquilina, and P. darvishi), selected at appropriate phylogenetic distances (20-95 million years divergence), to pinpoint conserved open chromatin regions likely under functional constraint.

Using this strategy, the authors predict a set of ubiquitous and cell-type-specific cis-regulatory elements. Importantly, they validate these predictions using rigorous transgenic reporter assays, convincingly demonstrating that their approach can successfully identify functional regulatory elements where previous methods had failed.

Strengths:

The approach introduced by Forbes et al. is conceptually straightforward, efficient, and readily transferable to other organisms. The validation experiments show not only that a substantial proportion of the predicted elements are functional, but also that the method is capable of identifying both ubiquitous and cell-type-specific regulatory elements. Given that the identification of regulatory regions remains a major bottleneck in understanding the molecular mechanisms underlying processes of development and regeneration, this work has the potential to make a significant impact in developmental and regeneration biology, particularly for studies involving non-model organisms with large genomes.

An additional strength is the demonstration that only the genome of the focal species requires high-quality sequencing and assembly. In contrast, species used solely for comparative analysis can be sequenced at low coverage without assembly, substantially reducing costs and increasing the accessibility of the approach.

Weaknesses:

While the method is effective in identifying regulatory elements that are active ubiquitously or in differentiated cell types, it failed in detecting elements associated with developmentally regulated genes. This may be due to trivial reasons, such as a very low level of expression of the selected genes. However, as acknowledged by the authors, it may also indicate inherent challenges in identifying regulatory elements associated with developmentally dynamic gene regulation, compared to those associated with genes expressed in differentiated cell types.

A second limitation, also acknowledged by the authors, is the absence of chromatin conformation capture data, which would help link distal regulatory elements to their target genes. This limitation may be particularly relevant for developmentally regulated genes, where long-range regulatory interactions may be critical.

Addressing these limitations will be an important direction for future work. Nonetheless, the approach as presented in this manuscript represents a key contribution that sets the stage for further methodological advances in the identification of cis-regulatory elements in large genomes.

Joint Public Review:

Summary:

This study uses state-of-the-art imaging approaches to show that membrane contact site (MCS) markers and the ER-resident tyrosine phosphatase PTP1B accumulate on phagocytic membranes within actin-devoid zones during frustrated phagocytosis in RAW264.7 macrophages. The authors convincingly show that PTP1B interacts with Syk, an Fcγ receptor-associated tyrosine kinase that plays a critical role in phagocytosis, and that ablation of PTP1B results in hyperphosphorylation of Syk and increased superoxide production, without impacting phagocytic efficiency. Using a phosphoproteomic approach, the authors identify the adaptor protein Shc1 as a strongly phosphorylated protein during stimulation of immunoglobulin receptors by aggregated IgG. In the absence of PTP1B, the authors demonstrate an increased interaction between Shc1 and the NADPH oxidase NOX2 subunit p47phox, suggesting that PTP1B controls superoxide production by inhibiting a Syk-Shc1-NOX2 axis.

Strengths:

This is a well-reasoned and cogently developed study that uses contemporary methods, including high-quality TIRF microscopy combined with MAPPER (Membrane-Attached Peripheral ER) or SPLICS (split-GFP-based contact site sensors), to describe how membrane contact site markers and the ER-resident tyrosine phosphatase PTP1B accumulate in the phagocytic cup as cortical actin depolymerizes. The genetic data also convincingly show that PTP1B ablation increases Syk and Shc1 phosphorylation, enhances the Shc1/p47phox interaction, and elevates superoxide production, whereas depletion of Shc1 reduces superoxide levels. Overall, the work outlines an interesting interplay between membrane contact sites, signaling, and the phagocytic machinery of broad interest.

Weaknesses:

While the authors indicate that the PTP1B phosphatase downregulates superoxide production via the Syk-Shc1-NOX2 axis and present a summary model depicting the proposed sequence of events, the supporting data are currently mostly circumstantial. For example, although it is clear that PTP1B depletion increases superoxide production as well as Syk and Shc1 phosphorylation in vivo, there are no data directly demonstrating that the effects of PTP1B depletion on superoxide production require enhanced Syk or Shc1 phosphorylation. Likewise, although PTP1B depletion increases the interaction between Shc1 and p47phox, a soluble component of NOX2, there is no compelling demonstration that superoxide production in PTP1B-depleted cells truly depends on the NOX2 complex or on the Shc1/p47phox interaction.<br /> In addition, while the authors elegantly demonstrate the formation of ER-PM contact sites during frustrated phagocytosis within the actin clearance zone, as well as the localization of the PTP1B phosphatase in the same region, it remains unclear whether the presence of the phosphatase at membrane contact sites is required for its regulatory effect on superoxide production.

Finally, it would be interesting to investigate these phenomena in other macrophage cell lines and perhaps also in more physiological contexts than frustrated phagocytosis. This would help evaluate the broader generalizability of the results and conclusions.

Reviewer #1 (Public review):

Summary:

The authors use a gambling task with momentary mood ratings from Rutledge et al. and compare computational models of choice and mood to identify markers of decisional and affective impairments underlying risk-prone behavior in adolescents with suicidal thoughts and behaviors (STB). The results show that adolescents with STB show enhanced gambling behavior (choosing the gamble rather than the sure amount), and this is driven by a bias towards the largest possible win rather than insensitivity to possible losses. Moreover, this group shows a diminished effect of receiving a certain reward (in the non-gambling trials) on mood. The results were replicated in a general online sample where participants were divided into groups with or without STB based on their self-report of suicidal ideation on one question in the Beck Depression Inventory self-report instrument. The authors suggest, therefore, that adolescents diagnosed with depression or anxiety with decreased sensitivity to certain rewards may need to be monitored more closely for STB due to their increased propensity to take risky decisions aimed at (expected) gains (such as relief from an unbearable situation through suicide) regardless of the potential losses. However, such a result was only found in the clinical sample and cannot be generalized more broadly based on the current findings.

Strengths:

● The study uses a previously validated task design and replicates previously found results through well-explained model-free and model-based analyses.

● Sampling of adolescents at high risk can help target early preventative diagnoses and treatments for suicide.

● Replication of the results in an online cohort increases confidence in the findings.

● The models considered for comparison are thorough and well-motivated. The chosen models allow for teasing apart which decision and mood sensitivity parameters relate to risky decision-making across groups based on their hypotheses.

● Novel finding of mood (in)sensitivity to non-risky rewards and its relationship with risk behavior in STB.

Weaknesses:

● Sample size of 25 for S- group is low-powered, which is explicitly mentioned as a study limitation.

● Modeling in the mediation analysis focused on predicting risk behavior in this task from the model-derived bias for gains and suicidal symptom scores. Thus, the implications of this work are more relevant to a basic-science understanding of the etiology of suicidal behavior than they are useful as a predictor of suicidal behavior, and it is not clear that a psychiatrist or psychologist could use this task to potentially determine who is at higher risk of attempting suicide and must be more closely monitored. Indeed, relationships between task parameters and behavior and suicidal behavior was limited to the clinical sample with a diagnosis of depression or anxiety disorder, and did not extend to the online sample. Therefore, the claim that these findings provide "computational markers for general suicidal tendency among adolescents" is unwarranted.

Reviewer #2 (Public review):

Summary:

This article addresses a very pertinent question - what are the computational mechanisms underlying risky behaviour in patients having attempted suicide. In particular, it is impressive how the authors find a broad behavioral effect whose mechanisms they can then explain and refine through computational modeling. This work is important because currently, beyond previous suicide attempts, there has been a lack of predictive measures. This study is the first step towards that: understanding the cognition on a group level. Before then being able to include it in future predictive studies (based on the cross-sectional data, this study by itself cannot assess the predictive validity of the measure).

Strengths:

- Large sample size

- Replication of their own findings

- Well-controlled task with measures of behaviour and mood + precise and well-validated computational modeling

Questions, based on revised manuscript and replies to other reviewers:

(1) Replies to reviewers in general: Bayes Factors have been added, it would be good to also use common verbal terms to describe them (e.g. 'anecdotal', 'moderate' etc). For example, my reading of table S8 would be that for gambling rate there is only anecdotal evidence that it does not relate to PSWQ, BDI, and moderate evidence it does not relate to TAI.

(2) Reply to reviewer 1 Q2 (Predicting STB):

For the regression predicting suicidal ideation, it seems to me that what you did was a regression STB ~ gambling behaviour + approach + mood? Could you clarify? I had expected as a test of whether the task can predict STB risk something slightly different - a cross-validation (LOO or maybe 5-fold in the large sample): STB ~ gambling behaviour + approach [parameter from model] + mood [parameter from model]; and then computing in the left out participants: predicted STB. Then checking correlation between STB and predicted STB. This would allow testing whether the diverse task measures together predict STB (with the caveat, that it's cross-validated, rather than hold-out sample, unless you could train on one sample (in lab) and test on the other (online).

(3) Reply to reviewer 2 Q1 (parameter recovery): I'm looking at S3, it seems to still show only the scatter plots and not the correlation matrices, which are now added as text notes. Can you actually show these matrices? An off-diagonal correlation of 0.63 appears quite high. I think it needs to be discussed exactly which parameters those are, and whether that impacts the interpretation of the results.

(4) Reply to reviewer 3 Q3 (mood model): I would have imagined that the response would involve changing the mood equations (equation 8 main text) to include a term for whether the participant gambled or not, independent of the gamble value.

Reviewer #3 (Public review):

This manuscript investigates computational mechanisms underlying increased risk-taking behavior in adolescent patients with suicidal thoughts and behaviors. Using a well-established gambling task that incorporates momentary mood ratings and previously established computational modeling approaches, the authors identify particular aspects of choice behavior (which they term approach bias) and mood responsivity (to certain rewards) that differ as a function of suicidality. The authors replicate their findings on both clinical and large-scale non-clinical samples.

The main problem, however, is that the results do not seem to support a specific conclusion with regard to suicidality. The S+ and S- groups differ substantially in the severity of symptoms, as can be seen by all symptom questionnaires and the baseline and mean mood, where S- is closer to HC than it is to S+. The main analyses control for illness duration and medication but not for symptom severity. The supplementary analysis in Figure S11 is insufficient as it mistakes the absence of evidence (i.e., p > 0.05) for evidence of absence. Therefore, the results do not adequately deconfound suicidality from general symptom severity.

The second main issue is that the relationship between an increased approach bias and decreased mood response to CR is conceptually unclear. In this respect, it would be natural to test whether mood responses influence subsequent gambling choices. This could be done either within the model by having mood moderate the approach bias or outside the model using model-agnostic analyses.

Additionally, there is a conceptual inconsistency between the choice and mood findings that partly results from the analytic strategy. The approach bias is implemented in choice as a categorical value-independent effect, whereas the mood responses always scale linearly with the magnitude of outcomes. One way to make the models more conceptually related would be to include a categorical value-independent mood response to choosing to gamble/not to gamble.

The manuscript requires editing to improve clarity and precision. The use of terms such as "mood" and "approach motivation" is often inaccurate or not sufficiently specific. There are also many grammatical errors throughout the text.

Claims of clinical relevance should be toned down, given that the findings are based on noisy parameter estimates whose clinical utility for the treatment of an individual patient is doubtful at best.

Comments on revisions:'

The authors adequately addressed my comments and I find the manuscript substantially strengthened.

Reviewer #2 (Public review):

Summary:

The authors present a computational framework for generating "cell-specific" digital twins of human iPSC-CMs from a single optimized voltage clamp recording. Using deep learning trained on > 1 million artificial cells, the authors demonstrate that the model can infer 52 biophysical parameters governing 6 major ionic currents, and the resulting digital twins can reproduce experimentally recorded action potentials.

Comments on revised version:

The authors propose an interesting platform for digital twin construction of iPSC-CMs using an AI-based approach. However, regarding the fundamental concerns raised in the previous review round "lack of experimental validation" and "overstatement of the claims", the authors have merely added text to the "Limitations" in the Discussion, without providing any new wet-lab experimental data. This cosmetic revision fails to demonstrate the scientific validity of the platform, and the core issues remain completely unresolved.

I think the authors need to either provide substantial additional experimental data or drastically tone down the claims throughout the manuscript based on the following three major concerns.

(1) Lack of wet validation

The authors show that their AI model can infer 52 parameters from a single patch-clamp recording and reproduce the overall action potential waveform. However, the most critical validation (whether the individual ion channel parameters, such as IKr/ICaL, inferred by the AI actually match the true parameters of that specific cell) is still missing. Without a direct head-to-head comparison between the parameters inferred by the model and the exact values measured using conventional wet experiments, it is impossible to determine whether the platform is providing accurate prediction (or merely performing a curve-fitting).

(2) Absence of experimental validation for drug response simulations (Cell 1 vs. Cell 2)

In Figure 6, the authors present a simulation result where the administration of an IKr blocker (E-4031) induces EADs in the digital twin of Cell 1, but not Cell 2. However, there is absolutely no wet-lab validation for this prediction. Unless the authors actually administer the same drug to the live Cell 1 and Cell 2 from which the recordings were taken, this "computational drug response prediction" remains purely hypothetical. There is no evidence provided that the prediction accurately reflects real biological responses.

(3) Significant overstatement regarding "inter-individual variability" and "personalized medicine"

The authors state in the very first sentence of the Abstract: "Individual variability shapes how diseases manifest, how patients respond to therapy, and how rare phenotypes arise". However, this opening sentence is severely disconnected from the actual conclusions and data presented in this study. The platform can capture only "cell-to-cell variability within the same dish" (which is not even validated), and thus claiming "patient-to-patient differences" is an overstatement.

Reviewer #3 (Public review):

Summary:

This work use convolution neural network to optimize a voltage clamp protocol to identify features and parameters from human pluripotent stem cell-derived cardiomyocytes.

Strengths:

The major strength is the methodology used to bridge in silico prediction of cell behavior and mechanistic insights from experimental dataset.

Comments on revised version.

As highlighted by the authors, due to the variability of the hPSC-CM model, to increase the applicability of this method, additional experimental dataset from different hPSC-CM lines would increase the translation of this approach.

I personally found that the detailed description of the methods, including the rationale of including/excluding some parameters, is extremely helpful to whoever would like to use this approach in their research.

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:

In the manuscript by Winke et al, the authors present evidence that fear-induced analgesia is mediated by somatostatin projection cells from the vlPAG to the RVM. This study uses a mouse model of fear-induced analgesia, and incorporates optogenetic circuit manipulation with behaviour and electrophysiology to gain a meaningful insight into a novel circuit involved in fear-induced analgesia.

Strengths:

(1) This is a well-constructed study with appropriate controls and analyses.

(2) Alternative interpretations of the data are systematically considered and eliminated via rational experiments. The authors are commended for a nice piece of experimental work.

(3) The vlPAG is a known region of pain modulation, and this study adds valuable insight to the circuit involved in fear-associated analgesia.

Weaknesses:

Only male mice are included in this study. [This has been explained and noted as a limitation.]

Reviewer #2 (Public review):

Summary:

Wenke et al. investigated the role of vlPAG somatostatin-expressing neurons in the mediation of analgesia during defensive states. A newly developed paradigm of cued fear-conditioned analgesia, which consists of a combination of an auditory fear retrieval session and a pain test, was used to evaluate this cell population's contribution to fear-mediated analgesia. Optogenetic manipulation of vlPAG SST+ neurons modulated the responses to a nociceptive cue (Hot Plate) presented concomitantly with an aversively conditioned tone. At the same time, alterations in the freezing levels could be observed during optogenetic activation of vlPAG SST+ neurons. In order to disentangle the impact of these cells on analgesia from their impact on the expression of defensive behaviors, the authors performed electrophysiological recordings from the dorsal horn in the spinal cord of anesthetized mice. A vlPAG-RVM-DH pathway was identified to trigger nociceptive C-fibers upon optic activation of the RVM. Finally, pathway-specific activation of SST+ vlPAG-RVM neurons could abolish CS-induced analgesia.

Strengths:

The study addresses a relevant topic, that is, brainstem circuits for pain-modulatory mechanisms as part of defensive states evoked by threat. This is important because the circuit mechanisms underlying pain are still not fully understood, and defining molecular markers of cellular circuit substrates may support the identification of potential pharmaceutical targets in treating pain. The authors confirm a previous study in that a somatostatin-positive cellular population presents a crucial vlPAG circuit element mediating anti-nociceptive effects. Key novelty aspects of the present study are the demonstration that these neurons seem to play a role specifically in threat-induced analgesia. This was possible by the elegant design and application of a novel fear analgesia paradigm, combined with cell- and pathway-specific optogenetics.

Reviewer #3 (Public review):

Summary:

Conditioned analgesia refers to the ability of a learned fear cue to suppress pain-related behavior and neural activity. Understudied, the authors developed a novel conditioned analgesia procedure in which a cue that had been paired or unpaired with shock was played while a hot plate increased temperature. Compared to several control conditions, the authors found increased latency to a nociceptive response (paw licking). The authors identified somatostatin neurons in the periaqueductal gray as a likely mediator of the behavior. They then showed that: (1) stimulating vlPAG-SST neurons blocked nociceptive response latency increases to the CS+, (2) stimulating vlPAG-SST neurons suppressed fear retrieval freezing, (3) stimulating vs. inhibiting vlPAG-SST neurons drove opposing modulation of c-fibers and Aδ-fibers, (4) direct-projecting vlPAG SST neurons modulate freezing while RVM-projecting vlPAG SST neurons modulate conditioned analgesia.

Strengths:

These experiments have many strengths. The behavioral assay is chief among them. The assay is robust and controls for confounding factors to reveal a repeatable effect of a shock-paired cue to delay nociceptive responding. The optogenetic experiments provide the correct level of temporal precision, given the authors' time-specific interest in cued responding. Combining neuronal manipulations with spinal recordings is particularly innovative, especially in the context of more behavioral neuroscience-based assays. All-in-all, I found this to be an exceptionally strong set of experiments.

Weaknesses:

No obvious weaknesses were identified by this reviewer.