Reviewer #1 (Public review):

Summary:

This paper describes a deep learning toolbox that can be used to automatically estimate functional topographic maps directly from human brain anatomy. Building on the first author's earlier work, which demonstrated the feasibility of using deep learning for this purpose, the new version of the toolbox now requires only a single anatomical MRI scan to generate predictions, eliminating the need for a myelin scan. This represents a significant practical improvement.

Strengths:

Having such a toolbox is very useful, since manual annotation and delineation of functional visual field maps is a laborious process that also requires deep expertise. The toolbox can save researchers substantial amounts of time and money, and also allows less experienced researchers to now perform this type of analysis. Notably, for certain participants and patients, the time they are able to reside in the scanner might be limited. Being able to focus on the primary research question, rather than the essential yet basic topographic information, could boost data quality and evaluation and might limit the number of participants that need to be included.

Weaknesses:

In the paper, the authors compare the performance of their new version to two previous approaches. Figure 2b shows that the new toolbox performs similarly to the previous deep-learning-based toolbox, but requires only an anatomical scan, which is a significant improvement. They also compare it to an older method that uses an atlas without requiring deep learning. For eccentricity and pRF size predictions, both deep-learning methods perform better than the older approach. For polar angle, a critical parameter for delineating visual field maps, the gain is substantially less. Moreover, the comparison to the atlas method (Benson2014) is not entirely fair, as, to our knowledge, there is also a more advanced atlas version that uses Bayesian fitting methods and already performs better than the old method. To better understand the gain of using deep learning, it would be beneficial if the authors also made the comparison to this more recent atlas-based approach. Moreover, it would be useful to know the correlations for the representative participant. Some examples of relatively "bad" maps would also be useful to have (and could be provided as supplementary information).

Figure 2b shows that the toolbox is quite good at estimating eccentricity and polar angle parameters, but less good at estimating the population receptive field (pRF) size. I will return to this latter point.

An interesting feature is that while the toolbox is trained on a specific data set (HCP), it can, "out-of-the-box", be applied to different existing data sets, without the need to retrain the model. This is quite important for the general utility of the method. The results for this are shown in Figure 3. Again, in panel b, it can be seen that the toolbox does a good job at estimating eccentricity and polar angle values, but performs rather poorly for pRF size: the deepRetinotopy toolbox has a strong tendency to only estimate very small pRFs, particularly when applying it across different datasets. For this reason, at the moment, these estimates appear hardly useful. It would be very helpful for readers if the authors could clarify or elaborate on this point, particularly regarding the limitations of pRF size predictions. They explain that this could be due to the use of different types of stimuli, but even within the same (HCP) dataset, the predictions primarily suggest tiny pRFs, even though the training dataset also contains larger ones (which can be better seen in supplementary Figure 4). Showing the predictions for higher-order brain areas, which have larger pRFs on average, could serve a similar evaluation purpose. Presumably, the underlying reasons are complex and could relate to the use of different stimuli, different analysis toolboxes, and how the deep learning model is currently being trained. Possibly, the abundance of small pRFs at lower eccentricity in the training set (which is usually the case in any empirical analysis) has given the model a very strong bias toward predicting small pRFs.

There would be various ways to verify which of these components is critical. For example, the model could be trained only on the bar stimuli of the HCP dataset, or the pRFs for all stimuli and datasets could be estimated using the same software tool. The latter seems important. For example, Supplementary Figure 4 indicates a high correlation between the Stanford and NYU cohorts that have used the same stimulus and analysis package, despite having different resolutions and scanners. Further investigation into the underlying reasons for these discrepancies would strengthen the paper. It would also provide valuable guidance for users of the toolbox on which toolbox predictions to trust and which not, as well as how well the model generalizes to other stimulus types, scanners, and image resolutions.

An aspect that is not directly apparent from the title, abstract, and introduction is that the deepRetinotopy toolbox does not by itself produce estimates of visual area labels or boundaries. It predicts only polar angle and eccentricity values. To predict labels and boundaries, the authors combine the toolbox with an atlas (the aforementioned Bayesian atlas). For visual areas V1 - V3, it does a very good job, in that the predictions are as good as the empirical ones. Notably, the authors indicate that the predictions for V2 and, in particular, V3 are worse than for V1, but Figure 4 clearly shows that predictions are as good as the empirical ones. More cannot be expected from a model that is trained on such empirical data.

Irrespective of the limitations with respect to predicting pRF size, the toolbox opens up functionally oriented analyses of very large cohorts of healthy participants, of which only anatomical data is available. The authors present an example of this by confirming the existence of differences in horizontal and vertical asymmetries in the field maps of the visual cortex of children and adults. While Figure 5 confirms the existence of differences, the analysis could be expanded to provide deeper insights, such as normalized developmental trajectories for both asymmetries, given the size of the dataset. This would better highlight the true power of their approach.

While the authors address limitations with respect to studying experience-dependent atypical functional organization, they do not address how the deepRetinotopy toolbox would handle (acquired) brain lesions. Addressing this, even if only speculative, would be welcome. Another welcome addition would be to see the predictions for additional brain areas, even if those would (presumably) be worse at present. Such information would nevertheless be essential for users considering applying this toolbox. Moreover, this could be a valuable resource serving as a benchmark for future iterations of either deepRetinotopy or other approaches.

Reviewer #2 (Public review):

Summary:

The authors introduce the deepRetinotopy toolbox, a deep learning-based software package that allows for user-friendly automatic delineation of visual areas based on anatomical (T1-weighted) MRI scans. This is an important evolution over a prior published version of the software, which required myelin maps additionally. The new version will hence allow many more users to obtain high-fidelity field-map delineations based on existing data or using standard protocols, providing a huge advance to the field. The authors exploited this strength and mapped visual field maps (for areas V1-V3) in 11060 human MRI scans covering different age classes to quantify changes of retinotopic organization across age groups, showing that previously functionally identified imbalances of early visual cortex field maps can now be identified on the basis of anatomical scans alone.

Strengths:

Overall, this is a tremendously important methodological contribution of primarily high practical and applied value. It allows functional imaging labs to delineate human cortical visual field maps with confirmed high fidelity using anatomical T1-weighted scans only. This will save expensive functional imaging and time-consuming analyses that were previously required to achieve nearly the same result and far better results than prior model-based approaches offered.

Also, the quantification of the accumulated very large dataset is meticulous and provides impressively detailed results of the field map changes for areas V1-V3 as a function of age.

Weaknesses:

(1) The weak point of the contribution is the choice to limit anatomical quality assessments and error quantifications to just three early regions, V1-V3, even though the deepRetinotopy toolbox can delineate over 20 regions (including parietal, ventral, and lateral regions, such as IPS0-5, hV4, VO1-2, V3A, PHC1-2, LO1-2, and TO1-2).

(2) The limit is fine for their large-scale application of the toolbox to age groups, as here, a clear hypothesis on early cortex variability was tested.

(3) However, the introduction of the toolbox itself warrants quality assessments and comparisons to prior models and ground truth beyond V1-V3, just like the authors did in their prior publication of the predecessor model.

(4) This is important as the vast majority of applications of this toolbox will likely go beyond V1-V3 to delineate dorsal, ventral, and lateral regions.

(5) For the present paper, this will require only 1 or 2 additional figures, or extending their present figures 2 and 4 along the lines of their previous figure 7 (Ribeiro et al 2021), which included error measures for high-level regions. Ideally, you provide sub-graphs separately for early visual, dorsal, ventral, and lateral regions.

(6) Going beyond V1-V3 is important for several reasons: first, future studies applying the software beyond V3 will need quantification for reassurance and justification. Second, for the sake of transparency, even if results are noisy or on par with prior models. Third, as a benchmark or reference point for future approaches.

Reviewer #3 (Public review):

Summary:

This valuable study presents a tool that uses brain anatomy to predict the layout and size of early visual maps, and it is strengthened by testing across a large and diverse collection of scans. The work will be useful for researchers who want to estimate likely visual map layout from standard anatomical scans and to relate anatomical differences to differences in visual organization across groups. The evidence is solid for the general usefulness of the approach, but incomplete for broader claims about prediction accuracy and use across datasets, particularly for estimates of map size and for showing that the model improves on repeated functional measurements.

Strengths:

The paper addresses a useful and important problem: estimating early visual map organization from anatomical measurements alone. Tools that predict these types of functional data from anatomical measurements were introduced more than a decade ago by Benson and colleagues, and the present authors have significantly extended that work. That is a real strength of the manuscript, because there is genuine value in having a practical tool that can estimate likely visual organization from standard anatomical scans.

Another major strength is the rigorous cross-dataset benchmarking and the accumulation of multiple datasets. The authors assembled a large and diverse set of scans and assessed model performance across different scanners, field strengths, and visual stimuli, which gives the reader a much better sense of how broadly the approach may apply. The retrospective analysis of more than 11,000 scans is especially notable and creates an unusual opportunity to ask how anatomical variation may relate to population differences in visual organization.

I also think the paper does a good job of showing why such a tool could matter in practice. A complete tool could be used in several ways. First, it could help users identify the locations of activations measured in other experiments with respect to the typical V1-V3 maps. Second, maps measured from an individual subject or patient could be compared with the predictions from the tool to ask whether they differ meaningfully from a standard anatomy-based map. Third, the tool can be used, as the authors have done here, to examine differences in anatomy across populations and interpret these differences with respect to retinotopic maps. Of these uses, the first already seems well supported by the current presentation.

Weaknesses:

(1) Quantification of the Analysis

My main concern is that the analysis relies heavily on global summary measures such as correlation and Dice score. Those measures are useful, but the paper would be more informative if it also quantified boundary differences in millimeters, especially for comparisons such as the V1/V2 boundary in Figure 2. That kind of analysis would help readers understand how large the errors are in physically meaningful terms.

(2) Model fitting methods

I also think the discussion of prediction failures for pRF size should be more explicit. The mismatch is likely influenced by the fact that the training data and several evaluation datasets were fit with different models and different analysis software. In particular, the network was trained on non-linear size estimates from the HCP data, while the comparison datasets were derived using other packages and, in some cases, different model assumptions. That likely contributes to the spread in Figure 3b and should be discussed more directly. It is important to discuss that the pRF parameters were derived using different software tools.

- HCP dataset (training data): analyzePRF (Compressive Spatial Summation model)

- NYU dataset: vistasoft

- Stanford dataset: vistasoft

- New Zealand dataset: SamSrf

- CHN dataset: Custom MATLAB software

(3) Clarifying Model Accuracy

If deepRetinotopy generates a true "noise-removed" representation of functional mapping based on anatomy, then fitting it to one fMRI measurement should predict a second, independent fMRI run better than the noisy data from the first run does.

The authors possess the exact data for this test. For the HCP dataset, the empirical fMRI data were explicitly separated into two halves: "fit 2" (the first half of the fMRI runs) and "fit 3" (the second half). They correlated these two halves to establish a "noise ceiling," the maximum possible reliability of the data. Looking at their results in Figure 2b, the correlation of the deepRetinotopy predictions falls below this noise ceiling. This means that the noisy functional Half 1 actually predicts functional Half 2 better than the anatomical model does.

The authors should state this explicitly. A side-by-side plot of Half 1 predicting Half 2 versus deepRetinotopy predicting Half 2 would show that the anatomical model regularizes map location well, but misses reliable subject-specific variation that anatomy alone cannot capture.

(4) The Hemodynamic Response Function

The assumptions used to generate the original empirical maps are permanently baked into the deep learning model. However, the authors explicitly mention the hemodynamic response function (HRF) only once, noting in the Methods that the modeled time series was "convolved with a canonical hemodynamic response function."

Beyond this single mention, there is no direct discussion of how the assumption of a single canonical HRF across all 161 HCP training subjects might have systematically impacted or biased the network's predictions. The authors address cross-dataset differences broadly under the umbrella of "experimental design" and "fMRI preprocessing pipeline" biases, but the HRF is a core biological property that mediates the connection between the anatomy and the data. The authors should explicitly discuss how this canonical assumption limits or biases the resulting deepRetinotopy network.

(5) Scoping the Input Data and Normative Use

The authors use FreeSurfer to generate a mean curvature map for the entire midthickness cortical surface. This full-hemisphere curvature map is resampled to a standard template surface space (32k_fs_LR), acting as the data frame that feeds input features into the neural network. However, while the network receives the full geometric structure of the hemisphere, it is explicitly trained to predict retinotopic parameters only within a restricted posterior ROI, based on the Wang et al. atlas and containing roughly 3,200 vertices per hemisphere.

A useful experiment to try, and perhaps the authors have already considered this, would be to restrict the input features exclusively to the posterior vertices. Including all anterior vertices may make it harder for the network to fit the localized visual data. A brief commentary on why the full hemisphere was retained as input could be highly informative for researchers adapting this geometric deep learning pipeline.

Reviewer #1 (Public review):

Summary:

In this manuscript, Emperador-Melero et al. seek to determine whether recruitment of endocytic machinery to the periactive zone is activity-dependent or tethered to delivery of active zone machinery. They use genetic knockouts and pharmacological block in two model synapses - cultured mouse hippocampal neurons and Drosophila neuromuscular junctions - to determine how well endocytic machinery localizes after chronic inhibition or acute depolarization by super-resolution imaging. They find acute depolarization in both models have minimal to no effect on the localization of endocytic machinery at the periactive zone, suggesting that these proteins are constitutively maintained rather than upregulated in response to evoked activity. Interestingly, chronic inhibition slightly increases endocytic machinery levels, implying a potential homeostatic upregulation in preparation for rebound depolarization. Using genetic knockouts, the authors show that localization of endocytic machinery to periactive zones occurs independently of proper active zone assembly, even in the absence of upstream organizers like Liprin-α.

Overall, they propose that the constitutive deployment of endocytic machinery reflects its critical role in facilitating rapid and reliable membrane internalization during synaptic functions beyond classical endocytosis, such as regulation of the exocytic fusion pore and dense-core vesicle fusion. Although many experiments reveal limited changes in the localization or abundance of endocytic machinery, the findings are thorough, and data substantially supports a model in which endocytic components are organized through a pathway distinct from that of the active zone. This work advances our understanding of synaptic dynamics by supporting a model in which endocytic machinery is constitutively recruited and regulated by distinct upstream organizers compared to active zone proteins. It also highlights the utility of super-resolution imaging across diverse synapse types to uncover functionally conserved elements of synaptic biology.

Strengths:

The study's technical strengths, particularly the use of super-resolution microscopy and rigorous image analyses developed by the group, bolster their findings.

Weaknesses:

One limitation, acknowledged by the authors, is the persistence of spontaneous activity at these synapses, which could still impact the organization of these regions.

Comments on revisions:

The authors have addressed all of my previous comments.

Reviewer #2 (Public review):

Summary:

This study examines whether the localization of endocytic proteins to presynaptic periactive zones depends on synaptic activity or active zone scaffolds. Using genetic and pharmacological perturbations in both Drosophila and mouse neurons, the authors show that key endocytic proteins remain localized to periactive zones even when evoked release or active zone architecture is disrupted. While the findings are largely negative, the study is methodologically solid and provides useful constraints for current models of synaptic vesicle recycling.

Strengths:

The experimental design is careful and systematic, spanning both fly and mammalian systems. The use of advanced genetic models, including Liprin-α quadruple knockout mice, is a notable strength. High-resolution imaging approaches (STED, Airyscan) are appropriately applied to assess nanoscale organization. The study clarifies that strict activity dependence of endocytic recruitment may not be a general principle.

Weaknesses (largely addressed in revision):

Several initial concerns have been satisfactorily addressed in the revised manuscript. In particular, the inclusion of EndoA/Dap160 experiments and the expanded discussion improve the work. Some limitations remain, including the reliance on Tetanus toxin at the Drosophila NMJ, which does not fully abolish presynaptic fusion, and the still limited insight into the mechanistic basis of periactive zone organization. The biological interpretation of small changes in protein levels upon silencing also remains somewhat unclear.

Comments on revisions:

I thank the authors for the careful revision of the manuscript. The additional experiments, in particular the inclusion of EndoA and Dap160 at the Drosophila NMJ, as well as the extended discussion of limitations, are appreciated and address important points raised in the first round.

While the principal conclusions of the study remain unchanged, and the manuscript is still largely based on negative results, I find that the authors now present these data in a more balanced and transparent manner. The discussion of activity-dependence is improved and more nuanced, especially with regard to possible contributions of spontaneous release and homeostatic effects.

In my opinion, despite the mostly negative nature of the findings, the work provides a valuable and relevant contribution, as it defines important constraints on current models of periactive zone organization. The study is technically strong, carefully executed, and systematically performed across different model systems.

Overall, the revised manuscript is clearly improved and represents a solid and well-executed piece of work that will be of interest to the field.

Reviewer #3 (Public review):

Summary:

This study examines how synaptic endocytic zones are positioned using a combination of cultured neurons and the Drosophila neuromuscular junction. The authors test whether neuronal activity, active zone assembly, or liprin-α function is required to localize endocytic zone markers, including Dynamin, Amphiphysin, Nervous Wreck, PIPK1γ, and AP-180. None of the manipulations tested caused a coordinated disruption in the localization or abundance of these markers, leading to the conclusion that endocytic zones form independently of synaptic activity and active zone scaffolds.

Strengths:

The work is systematic and carefully executed, using multiple manipulations and two complementary model systems. The authors consistently examine multiple molecular markers, strengthening the interpretation that endocytic zone positioning is robust to changes in activity and structural assembly.

Weaknesses:

The main limitation is that the study does not test whether the methods used are sensitive enough to detect subtle functional disruption, and no condition tested produces clear disorganization of the endocytic zone. As a result, the conclusion that these zones assemble independently is supported by negative data, without a strong positive control for disassembly or mislocalization.

This paper addresses a longstanding question in synaptic biology and provides a well-supported boundary on the types of mechanisms that are likely to govern endocytic zone localization. The conclusions are well justified by the data, though additional evidence would be needed to define the assembly mechanism itself.

Comments on revisions:

The authors responded to the initial review with care. They both revised the manuscript and conducted new experiments to address each reviewer's concern. The responses to the review were effective, and I think that the revised manuscript provides significant new insights. In my view, it does not require additional revisions.

Reviewer #1 (Public review):

In this paper, Solyga, Zelechowski & Keller study human visuomotor mismatch responses as an alternative instantiation of prediction errors to classic oddball paradigms. Using VR, they created a condition in which participants were moving around thereby creating a visuomotor coupling between physical movement and visual flow. To attempt to isolate the contribution of specifically movement-related predictions in this condition, they contrasted it to a condition in which participants were seated and rewatching their movement trajectory during the 'active' condition. Visuomotor mismatches were created by temporarily decoupling movement and visual experience by halting the VR display as participants continued to move.

The core finding of the paper is that participants exhibit a positively-valenced response to the visuomotor decoupling in the active but not in the passive condition. Since walking speed only insignificantly slows down following decoupling events in the active conditions, the authors argue that this difference can not be accounted for by "changes in participants' behavior or to simple visual offset responses" with the latter being equal across both conditions. The following reinstatement of the coupling in turn does not differ between the two conditions. The authors additionally show that this mismatch response differs from visual onset responses elicited by checkerboard inversions and that it's "qualitatively" stronger than more commonly studied auditory oddball mismatch responses.

The design with its focus on ecological validity is impressive, well-rationalized and the results are well illustrated. I additionally appreciate the control analyses with regards to changes in walking speed and playback DOF and, now added, additional participants who experience the passive condition before the active. I have a couple of questions/comments.

My main question in round 1 regarded the isolation of visuomotor mismatch. Although the comparison with a seated control seems like a very sensible way to control for simple visual responses, there seem to be more differences than just a break in visuomotor coupling between the conditions. I therefore wonder whether the reduced offset response in the seated condition may be, in part, explained differently. For example, given that participants always conduct the active condition before rewatching their movement in the seated condition, it seemed likely that there is a component of learning across the session that flow will sometimes be halted. This is confirmed with the analyses. The explanation that there is a visuomotor component here is given further weight by their conduction of an additional group of participants who perform the conditions in the reverse order, so this has strengthened the manuscript considerably. However, it does of course remain an imperfect control because the visual stimulus is now different between the conditions for these participants. It's the best that can be achieved with this type of paradigm though and of course it yields a great deal of ecological validity.

I was also wondering whether the authors may consider the findings in frontal electrodes more closely given that the title of the paper focuses on a specifically occipital effect. Their further analyses have confirmed that there are likely interesting frontal effects. From a theoretical point of view, the spatial dissociation in adaptation effects, which were stronger in frontal and weaker in occipital areas, seems interesting and perhaps worth discussing, especially given the interpretation that "mismatch processing may initially arise in sensory visual areas before engaging higher-order frontal regions." How come the frontal decrease in responses is not accompanied by an analogous decrease in its supposed occipital source? Could these two responses reflect different kinds of prediction error signals (i.e. objective vs subjective)?

I remain concerned that the authors fight too defensively that they have absolutely isolated visuomotor prediction mechanisms with this paradigm. It's a nice, informative study, but it seems odd to argue there are no other possible explanations. One picks a design to optimize some features but they will always come at some cost to others. Prioritising ecological validity, which is a justifiable aim, necessarily usually weakens some control over confounds.

To outline my reasoning fully: My concerns wrt generic influences of action on perception are reflected in Fig 1. The P1 is smaller when walking than sitting. It seems likely that the mismatch response reflects something about extrapolation or prediction, because it is larger when walking. However, it's not necessarily sensorimotor prediction. Even if you remove action from the equation, the flow can be extrapolated or predicted most of the time in a way it cannot so well when the video is halted. Of course the sitting condition somewhat controls for it, but when it came second the visual flow disruptions were more predictable here. A reduction in effects over time is indeed confirmed with their analyses. They now have conducted a study with the conditions in the reverse order and they find the same thing. But of course this necessitates non-identical visual flow because the sitting condition is playing the previous participant's flow. So it is likely that across all of these comparisons, it is the visuomotor mismatch that is especially salient. It's just that each comparison is a bit messy/confounded. It would strengthen the manuscript if there were some consideration given to the other processes likely at play here.

As a more minor point in response to our previous review, whether particular accounts represent an 'orthodox' view at present does not determine whether they raise logical issues in need of consideration. The authors may have missed that the papers in question consider mechanisms underlying the attenuation of particular pieces of information *from perception*. Not perceptual processing. We have one percept at any one moment in time and must understand how different population types synergistically generate that percept.

Similarly a little strange is the way in which the authors aggressively defend the position that self-generated motion is 'the strongest' type of prediction. Sure, we probably experience the effects of our actions more often than ambulances. But what about objects obeying laws of gravity or others' faces being structured and moving in systematic ways? It is hard to quantify, such that presumably many scientists would be skeptical of such a claim, and it is not needed logically to justify the importance of examining mechanisms enabling action to shape perceptual processing. I'd assume it better to fight the battles you need to (and can) fight, such that the robust claims carry more weight.

Hope these comments are helpful.

Reviewer #2 (Public review):

Summary:

This study investigates whether visuomotor mismatch responses can be detected in humans. By adapting paradigms from rodent studies, the authors report EEG evidence of mismatch responses during visuomotor conditions and compare them to visual-only stimulation and mismatch responses in other modalities.

Strengths:

- Authors use a creative experimental design to elicit visuomotor mismatch responses in humans.

- The study provides an initial dataset and analytical framework that could support future research on human visuomotor prediction errors.

Weaknesses:

- Methodological issues (e.g., volume conduction) make it difficult to confidently attribute the observed mismatch responses to activity in visual cortical regions. This could be alleviated by increasing the number of channels.

The authors successfully demonstrate that visuomotor mismatch paradigms can, in principle, be applied in human EEG. This approach provides a translational bridge between rodent and human work on predictive processing.

Reviewer #3 (Public review):

Solyga, Zelechowski, and Keller present a concise report of an innovative study demonstrating clear visuomotor mismatch responses in ambulating humans, using a mobile EEG setup and virtual reality. Human subjects walked around a virtual corridor while EEGs were recorded. Occasionally, motion and visual flow were uncoupled, and this evoked a mismatch response that was strongest in occipitally placed electrodes and had a considerable signal to noise ratio. It was robust across participants and could not be explained by the visual stimulus alone.

This is an important extension of their prior work in mice, and represents an elegant translation of those previous findings to humans, where future work can inform theories of e.g. psychiatric diseases that are believed to involve disordered predictive processing. For the most part, the authors are appropriately circumspect in their interpretations and discussions of the implications. The paper in its current form represents an important addition to the literature.

The authors have included analyses of the auditory mismatch using temporal electrodes, referenced to Cz (and therefore should exhibit a mismatch positivity). This added data clearly and convincingly shows that the sensorimotor mismatch is, indeed, stronger than the passive auditory MMN.

- The reference electrode placed at Cz makes it is difficult to interpret relative differences between frontal and occipital electrode responses, as the occipital electrodes are placed farther away from the Cz reference than the frontal electrodes. Similarly, signal occuring cortically near the Cz reference might only appear as though it is occipitally distributed in this montage. It is common in EEG research to re-montage the data to an averaged common reference in order to better interpret the scalp distributions. As the electrode coverage was sparse for some subjects, this could be challenging, and this reviewer does not feel that it is necessary to do this analysis step, or even to drastically rewrite the body of the paper. We only request that some discussion, however brief, is included in the discussion section or the methods that recommend more dense electrode coverage in the future to better interpret scalp distributions and potential meso-scale sources.

- This is just a suggestion. The authors are encouraged to analyse (and report) time-frequency power and phase locking for these mismatch responses, as is common in much of the literature (see Roach et al 2008 Schizophrenia Bulletin). This is not to say that doing so will yield insights into oscillations per se, but converting the data to the time-frequency domain provides another perspective that has some advantages. fosters translations to rodent models, as ERP peaks do not map well between species, but e.g. delta-theta power does (see Lee et al 2018 Neuropsychopharmacology; Javitt et all 2018 Schizophrenia research; Gallimore et al 2023 Cereb Ctx). Further, ERP peaks can be influenced by the actual neuroanatomy of an individual (especially for quantifying V1 responses). Time frequency analyses may aid in interpreting the "early negative deflection with a peak latency of 48 ms " finding as well. As it stands, the report is complete, and it would be acceptable if the authors chose to save this type of analysis for a future publication.

Reviewer #3 (Public review):

In this manuscript, the authors use HiC to study the 3D genome of CD14+ CD16+ monocytes from the blood of healthy and those from patients with Alcohol-associated Hepatitis.

Overall, the authors perform a cursory analysis of the HiC data and conclude that there are a large number of changes in 3D genome architecture between healthy and AH patient monocytes. They highlight some specific examples that are linked to changes in gene expression. The analysis is of such a preliminary nature that I would usually expect to see the data from all figures in just one or two figures.

In addition, I have a number of concerns regarding the experimental design and the depth of the analyses performed that I think must be addressed.

(1) There is a myriad of literature that describes the existence of cell-type-specific 3D genome architecture. In this manuscript, there is an assumption by the authors that the CD14+ CD16+ monocytes represent the same population from both the healthy and diseased patients. Therefore, the authors conclude that the differences they see in the HiC data are due to disease-related changes in the equivalent cell types. However, I am concerned that the AH patient monocytes may have differentiated due to their environment so that they are in fact akin to a different cell type and the 3D genome changes they describe reflect this. This is supported by published articles, for example: Dhanda et al., Intermediate Monocytes in Acute Alcoholic Hepatitis Are Functionally Activated and Induce IL-17 Expression in CD4+ T Cells. J Immunol (2019) 203 (12): 3190-3198, in which they show an increased frequency of CD14+ CD16+ intermediate monocytes in AH patients that are functionally distinct.

I suggest that if the authors would like to study the specific effects of AH on 3D genome architecture then they should carefully FACsort the equivalent monocyte populations from the healthy and AH patients.

(2) The analysis of the HiC data is quite preliminary. In the 3D genome field, it is usual to report the different scales of genome architecture, for example, compartments, topologically associated domains (TADs) and loops. I think that reporting this information and how it changes in AH patients in the appropriate cell types would be of great interest to the field.

Comments on revisions:

In the revision the authors did not respond to my concerns which I believe still remain valid and compromise the author's conclusions of AH-specific effects on genome architecture.

Reviewer #1 (Public review):

Summary:

This manuscript by Wang et al. describes the development of an optimized soluble ACE2-Fc fusion protein, B5-D3, for intranasal prophylaxis against SARS-CoV-2. As shown, B5-D3 conferred protection not only by acting as a neutralizing decoy, but also by redirecting virus-decoy complexes to phagocytic cells for lysosomal degradation. The authors showed complete in vivo protection in K18-hACE2 mice and investigated the underlying mechanism by a combination of Fc-mutant controls, transcriptomics, biodistribution studies, and in vitro assays.

Strengths:

The major strength of this work is the identification of a novel antiviral approach with broad-spectrum and beyond simple neutralization. Mutant ACE2 enables broad and potent binding activity with the S proteins of SARS-CoV-2 variants, while the fused Fc part mediates phagocytosis to clear the viral particles. The conceptual advance of this ACE2-Fc combination is convincingly validated by in vivo protection data and by the completely abrogated protection of Fc LALA mutant.

Additionally:

The authors include a discussion (in Discussion part) about a previously reported ACE2 decamer (DOI: 10.1080/22221751.2023.2275598) and compared with the ACE2-Fc fusion protein developed in this study. The authors also tested the off-target activity and showed no evidence of toxicity in vivo.

Reviewer #2 (Public review):

Summary:

Wang et al. engineered an ACE2 mutant by introducing two mutations (T92Q and H374N), and fused this ACE2 mutant to human IgG1-Fc (B5-D3). Experimental results suggest that B5-D3 exhibits broad-spectrum neutralization capacity and confers effective protection upon intranasal administration in SARS-CoV-2-infected K18-hACE2 mice. Transcriptomic analysis suggests that B5-D3 induces early immune activation in lung tissues of infected mice. Fluorescence-based bio-distribution assay further indicates rapid accumulation of B5-D3 in the respiratory tract, particularly in airway macrophages. Further investigation shows that B5-D3 promotes viral phagocytic clearance by macrophages via an Fc-mediated effector function, namely antibody-dependent cellular phagocytosis (ADCP), while simultaneously blocking ACE2-mediated viral infection in epithelial cells. These results provide some insights into improving decoy treatments against SARS-CoV-2 and other potential respiratory viruses.

Strengths:

The protective effect of this ACE2-Fc fusion protein against SARS-CoV-2 infection has been evaluated in a reasonable way.

Weaknesses:

(1) Some of the mice experiments suffer from insufficient sample numbers, which affect the statistical power and reliability of the results. The author acknowledged this weakness, noting that the supply of aged mice was limited, while arguing that, although the sample size is small, the data from these mice are consistent.

(2) Compared to 6 hours, intranasal administration of B5-D3 at 24 hours before viral infection results in reduced protective efficacy. However, only survival and body weight data are provided, with no supporting evidence from virological assays such as viral titer measurement. The author acknowledged that such data would be more comprehensive and attributed the limitation to constraints in animal services.

(3) The efficacy of the B5-D3-LALA group was not as good as that of the B5-D3 group. The author suggested that there might be a certain degree of viral variation, and viral infection in the lungs may be uneven in the B5-D3-LALA group.

Reviewer #3 (Public review):

Strengths:

The core strength of this study lies in its innovative demonstration that an engineered sACE2-Fc fusion redirects virus-decoy complexes to Fc-mediated phagocytosis and lysosomal clearance in macrophages, revealing a distinct antiviral mechanism beyond traditional neutralization. Its complete prophylactic protection in animal models and precise targeting of airway phagocytes establish a novel therapeutic paradigm against SARS-CoV-2 variants and future respiratory viruses.

Weaknesses:

The study attributes the complete antiviral protection to Fc-mediated phagocytic clearance, a central claim that requires more rigorous experimental validation. The observation that abrogating Fc functions compromises protection could be confounded by potential alterations in the protein's stability, half-life, or overall structure. To firmly establish this mechanism, it is crucial to include a control molecule with a mutated Fc region that lacks FcγR binding while preserving the Fc structure itself. Without this critical control, the conclusion that phagocytic clearance is the primary mechanism remains inadequately supported. The strategy of deliberately targeting virus-decoy complexes to phagocytes via Fc receptors inherently raises the question of Antibody-Dependent Enhancement (ADE) of disease. While the authors demonstrate a lack of productive infection in macrophages, this only addresses one facet of ADE. The risk of Fc-mediated exacerbation of inflammation (ADE) remains a critical concern. The manuscript would be significantly strengthened by a direct discussion of this risk and by including data, such as cytokine profiling from treated macrophages, to more comprehensively address the safety profile of this approach. The exclusive use of the K18-hACE2 mouse model, which exhibits severe disease, limits the generalizability of the findings. The "complete protection" observed may not translate to models with more robust and naturalistic immune responses or to human physiology. Furthermore, the lack of data against circulating SARS-CoV-2 variants of concern. The concept of sACE2-Fc fusion proteins as decoy receptors is not novel, and numerous similar constructs have been previously reported. The manuscript would benefit from a clearer demonstration of how the optimized B5-D3 mutant represents a significant advance over existing sACE2-Fc designs. A direct comparative analysis with previously published benchmarks, particularly in terms of neutralizing potency, Fc effector function strength, and in vivo efficacy, is necessary to establish the incremental value and novelty of this specific agent.

Comments on revised version:

The author has successfully addressed the raised issue.

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 appropriately addressed the comments raised in the previous round of review.]

Summary:

The study by Lemen et al. represents a comprehensive and unique analysis of gene networks in rat models of opioid use disorder, using multiple strains and both sexes. It provides a time-series analysis of Quantitative Trait Loci (QTLs) in response to morphine exposure.

Strengths:

A key finding is the identification of a previously unknown morphine-sensitive pathway involving Oprm1 and Fgf12, which activates a cascade through MAPK kinases in D1 medium spiny neurons (MSNs). Strengths include the large-scale, multi-strain, sex-inclusive design, the time-series QTL mapping provides dynamic insights, and the discovery of an Oprm1-Fgf12-MAPK signaling pathway in D1 MSNs, which is novel and relevant.

Reviewer #2 (Public review):

Summary:

This highly novel and significant manuscript re-analyzes behavioral QTL data derived from morphine locomotor activity in the BXD recombinant inbred panel. The combination of interacting behavioral-pharmacology (morphine and naltrexone) time course data, high-resolution mouse genetic analyses, genetic analysis of gene expression (eQTLs), cross-species analysis with human gene expression and genetic data, and molecular modeling approaches with Bayesian network analysis produces new information on loci modulating morphine locomotor activity.

Furthermore, the identification of time-wise epistatic interactions between the Oprm1 and Fgf12 loci is highly novel and points to methodological approaches for identifying other epistatic interactions using animal model genetic studies.

Strengths:

(1) Use of state-of-the art genetic tools for mapping behavioral phenotypes in mouse models.

(2) Adequately powered analysis incorporating both sexes and time course analyses.

(3) Detection of time and sex-dependent interactions of two QTL loci modulating morphine locomotor activity.

(4) Identification of putative candidate genes by combined expression and behavioral genetic analyses.

(5) Use of Bayesian analysis to model causal interactions between multiple genes and behavioral time points.

Appraisal:

The authors largely succeeded in reaching goals with novel findings and methodology.

Significance of Findings:

This study will likely spur future direct experimental studies to test hypotheses generated by this complex analysis. Additionally, the broad methodological approach incorporating time course genetic analyses may encourage other studies to identify epistatic interactions in mouse genetic studies.

Reviewer #3 (Public review):

Summary:

This is a clearly written paper that describes the reanalysis of data from a BXD study of the locomotor response to morphine and naloxone. The authors detect significant loci and an epistatic interaction between two of those loci. Single-cell data from outbred rats is used to investigate the interaction. The authors also use network methods and incorporate human data into their analysis.

Strengths:

One major strength of this work is the use of granular time-series data, enabling the identification of time-point-specific QTL. This allowed for the identification of an additional, distinct QTL (the Fgf12 locus) in this work compared to previously published analysis of these data, as well as the identification of an epistatic effect between Oprm1 (driving early stages of locomotor activation) and Fgf12 (driving later stages).

Reviewer #1 (Public review):

Summary:

Many studies have investigated adaptation to altered sensorimotor mappings or to an altered mechanical environment. This paper asks a different but also important question in motor control and neurorehabilitation: how does the brain adapt to changes in the controlled plant? The authors addressed this question by performing a tendon transfer surgery in two monkeys during which the swapped tendons flexing and extending the digits. They then monitored changes in task performance, muscle activation and kinematics post-recovery over several months, to assess changes in putative neural strategies.

Strengths:

(1) The authors performed complicated tendon transfer experiments to address their question of how the nervous system adapts to changes in the organisation of the neuromusculoskeletal system, and present very interesting data characterising neural (and in one monkey, also behavioural) changes post tendon transfer over several months.

(2) The fact that the authors had to employ to two slightly different tasks -one more artificial, the other more naturalistic- in the two monkeys and yet found qualitatively similar changes across them makes the findings more compelling. After all these are very challenging experiments!

(3) The paper is well written, the analyses are sound, and the authors interpret the data appropriately, acknowledging the key limitations.

Weaknesses:

None of note.

Reviewer #3 (Public review):

Summary:

In this study, Philipp et al. investigate how a monkey learns to compensate for a large, chronic biomechanical perturbation--a tendon transfer surgery, swapping the actions of two muscles that flex and extend the fingers. After performing the surgery and confirming that the muscle actions are swapped, the authors follow the monkeys' performance on grasping tasks over several months. There are several main findings:

- There is an initial stage of learning (around 60 days), where monkeys simply swap the activation timing of their flexors and extensors during the grasp task to compensate for the two swapped muscles.

- This is (seemingly paradoxically) followed by a stage where muscle activation timing returns almost to what it was pre-surgery, suggesting that monkeys suddenly swap to a new strategy that is better than the simple swap.

- Muscle synergies seem remarkably stable through the entire learning course, indicating that monkeys do not fractionate their muscle control to swap the activations of only the two transferred muscles.

- Muscle synergy activation shows a similar learning course, where the flexion synergy and extension synergy activations are temporarily swapped in the first learning stage and then revert to pre-surgery timing in the second learning stage.

- The second phase of learning seems to arise from making new, compensatory movements (supported by other muscle synergies) that get around the problem of swapped tendons.

Strengths:

This study is quite remarkable in scope, studying two monkeys over a period of months after a difficult tendon-transfer surgery. As the authors point out, this kind of perturbation is an excellent testbed for the kind of long-term learning that one might observe in a patient after stroke or injury, and provides unique benefits over more temporary perturbations like visuomotor transformations and over studying learning through development. Moreover, while the two-stage learning course makes sense, I found the details to be genuinely surprising--specifically the fact that: 1) muscle synergies continue to be stable for months after the surgery, despite being maladaptive; and 2) muscle activation timing reverts to pre-surgery levels by the end of the learning course. These two facts together initially make it seem like the monkey simply ignores the new biomechanics by the end of the learning course, but the authors do well to explain that this is mainly because the monkeys develop a new kind of movement to circumvent the surgical manipulation.

I found these results fascinating, especially in comparison to some recent work in motor cortex, showing that a monkey may be able to break correlations between the activities of motor cortical neurons, but only after several of coaching and training (Oby et al. PNAS 2019). Even then, it seemed like the monkey was not fully breaking correlations but rather pushing existing correlations harder to get succeed at the virtual task (a brain-computer interface with perturbed control).

Weaknesses:

I found the analysis to be reasonably well considered and relatively thorough. The authors have also suitably addressed my comments on the previous version. One minor weakness that remains (understandably so) is that the two animals in the study performed different tasks, and the results of the secondary synergy analysis seem to be quite different (Figure 10). That said, I don't think this weakness reduces the impact of the study, and though multiple replications of the same results would provide more convincing evidence, I don't think it's necessary to make the points that the authors are making.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors set up a pipeline to predict insect repellents that are pleasant and safe to humans. This is done by daisy chaining a new classification model based predicting repellents with a published model on predicting human perception. Models use a feature-engineered selection of chemical features to make their predictions. The predicted molecules are then validated against a proxy humanoid (heated brick) and its safety is tested by molecular assays of human cells. The humanistic approach to modeling these authors have taken (which consider cosmetic/aesthetic appeal and safety) is novel and a necessary step for consumer usage. However, the importance of pleasantness over effectiveness is still up for debate (DEET is unpleasant but still used often) and the generalization of safety tests is unknown and assumed. The effectiveness of the prediction models is also still warranted. They pass the authors own behavioral tests, but their contribution to the field is unknown as both models (new and published) have not been rigorously bench-marked to previous models. Moreover, the author's breadth of literature in this field is sparse, ignoring directly related studies.

Strengths:

Humanistic approach to modeling consider pleasantness and safety. Chaining models can help limit the candidate odorants from the vastness of odor space.

Weaknesses:

The current models need to be bench-marked against leading models predicting similar outcomes. Similarly, many of these papers need to be addressed and discussed in the introduction. The authors might even consider their data sources for model training to increase performance and lexical categorization for interoperability. For instance, the Dravnikes data lexicon, currently used in the human perception lexicon, has been highly criticized for its overlapping and hard to interpret descriptive terms ("FRAGRANT", "AROMATIC").

Human Perception<br /> Khan, R. M., Luk, C. H., Flinker, A., Aggarwal, A., Lapid, H., Haddad, R., & Sobel, N. (2007). Predicting odor pleasantness from odorant structure: pleasantness as a reflection of the physical world. Journal of Neuroscience, 27(37), 10015-10023.

Keller, A., Gerkin, R. C., Guan, Y., Dhurandhar, A., Turu, G., Szalai, B., ... & Meyer, P. (2017). Predicting human olfactory perception from chemical features of odor molecules. Science, 355(6327), 820-826.

Gutiérrez, E. D., Dhurandhar, A., Keller, A., Meyer, P., & Cecchi, G. A. (2018). Predicting natural language descriptions of mono-molecular odorants. Nature communications, 9(1), 4979.

Lee, B. K., Mayhew, E. J., Sanchez-Lengeling, B., Wei, J. N., Qian, W. W., Little, K. A., ... & Wiltschko, A. B. (2023). A principal odor map unifies diverse tasks in olfactory perception. Science, 381(6661), 999-1006.<br /> Related cleaned data: https://github.com/BioMachineLearning/openpom

Insect Repellents:<br /> Wright, R. H. (1956). Physical basis of insect repellency. Nature, 178(4534), 638-638.

Katritzky, A. R., Wang, Z., Slavov, S., Tsikolia, M., Dobchev, D., Akhmedov, N. G., ... & Linthicum, K. J. (2008). Synthesis and bioassay of improved mosquito repellents predicted from chemical structure. Proceedings of the National Academy of Sciences, 105(21), 7359-7364.

Bernier, U. R., & Tsikolia, M. (2011). Development of Novel Repellents Using Structure− Activity Modeling of Compounds in the USDA Archival Database. In Recent Developments in Invertebrate Repellents (pp. 21-46). American Chemical Society.

Wei, J. N., Vlot, M., Sanchez-Lengeling, B., Lee, B. K., Berning, L., Vos, M. W., ... & Dechering, K. J. (2022). A deep learning and digital archaeology approach for mosquito repellent discovery. bioRxiv, 2022-09.

The current study assumes that insect repellents repel via its odor valence to the insect, but this is not accurate. Insect repellents also mask the body odor of humans making them hard to locate. The authors need to consult the literature to understand the localization and landing mechanisms of insects to their hosts. Here, they will understand that heat alone is not the attractant as their behavioral assay would have you believe. I suggest the authors test other behaviors assays to show more convincing evidence of effectiveness. See the following studies:

De Obaldia, M. E., Morita, T., Dedmon, L. C., Boehmler, D. J., Jiang, C. S., Zeledon, E. V., ... & Vosshall, L. B. (2022). Differential mosquito attraction to humans is associated with skin-derived carboxylic acid levels. Cell, 185(22), 4099-4116.

McBride, C. S., Baier, F., Omondi, A. B., Spitzer, S. A., Lutomiah, J., Sang, R., ... & Vosshall, L. B. (2014). Evolution of mosquito preference for humans linked to an odorant receptor. Nature, 515(7526), 222-227.

Wei, J. N., Vlot, M., Sanchez-Lengeling, B., Lee, B. K., Berning, L., Vos, M. W., ... & Dechering, K. J. (2022). A deep learning and digital archaeology approach for mosquito repellent discovery. bioRxiv, 2022-09.

Comments on revisions:

The revisions made to the manuscript do not fully address the concerns raised in the previous round of review. The authors are encouraged to consider the following points to strengthen the work.

The benchmarking of the human perception models against Keller et al. (2017) and Gutiérrez et al. (2018) is insufficient, as the field has progressed considerably in the last five years with newer approaches using larger data sources. Benchmarking against more recent models would better situate the contribution of this work.

The exclusion of human repellency data from preprint Boyle et al. (2016) is worth reconsidering. For a study that takes an explicitly human-centric modeling approach, human behavioral data on repellency, pleasantness, and usage intent would directly support the central claims of the manuscript.

The key claims regarding repellency and consumer acceptability would be considerably strengthened by the addition of these data.

Reviewer #2 (Public review):

Summary:

This is an interesting study that seeks to identify novel mosquito repellents that smell attractive to humans. This is the second time I have reviewed, and the authors have not done anything to address the weaknesses. Although the subject matter may provide important new information for the development of new repellents, its current breadth is limited without additional assays. Arm-in-cage assays, testing the longevity of the new repellents, other ML analyses and confusion matrices, would strengthen the manuscript and demonstrate innovation. The lack of cohesion and new experimental results weakens the manuscript.

Strengths:

The combination of standard machine learning methods with mosquito behavioral tests is a strength.

Weaknesses:

The study would be strengthened by describing how other modern ML approaches (RF, decision trees) would classify and identify other potential repellents.

A comparison of the repellent activity between DEET and the top ten hits identified in this new study indicates little change in repellent activity (~3%), suggesting that DEET remains the gold standard. Without additional toxicity tests and longevity tests, the study is arguably incremental. The study's novelty should be better clarified.

The Methods in the repellency tests are sparse, and more information would be useful. Testing the top repellents at low doses (<<1%) and for long periods (2-12 h) would strengthen the manuscript. Without this information, the manuscript is lacking in depth.

Testing human subjects on their olfactory percept of the repellents would also increase the depth and utility of the manuscript. Without additional experiments, the authors' conclusions lack support and have limited impact on the state-of-the-art.

This manuscript is a mix of different approaches, which makes it lack cohesion. There is the ML method for classifying new repellents that smell good, but no testing of the repellents on human volunteers. The repellents are not tested at realistic concentrations and durations. And the calcium mobilization test is strange, and makes little sense in the context of the other experiments and framing of the manuscript.

Comments on revisions:

The authors have a potentially strong manuscript. However, I would urge the authors to address the reviewer comments in a substantive manner.

Reviewer #1 (Public review):

Summary:

The paper describes a biologically plausible version of JEPA using recurrent neural networks called RPL for recurrent predictive learning. Given an embedding z_t, a recurrent neural network processes these inputs with the form: c_t+1 = RNN(c_t, z_t). Then the predictive network f is predicting the future inputs with the format: min || f(c_t) - stop_grad(z_t+delta t) ||^2. I understand that a prediction error is defined as: e = z_t+delta t - f(c_t) to model cortical measurements in the oddball task.

The RPL model is also shown to build an internal world model, with "real-world" data like the movement of moving animals or speech signals. The representation is then compared to V1 data and expected prediction error signals in an oddball setting. In a stacked hierarchy of RNN learning with RPL, the higher layers appear to learn high-level latent variables, although gradients are not propagated downward to the lower layers.

Strengths:

(1) The paper tackles an open question: Self-supervised learning is thought to be a fundamental principle to explain how computation is structured in the brain. Cortical data suggest qualitatively that prediction error is a core principle of representation learning in the brain, but the field is still looking for a simple yet expressive model that would explain how the cortex learns its representations. RPL contributes in that direction by making a useful link between cortical representation learning in RNN models and the JEPA learning algorithm that was demonstrated to scale to large world model learning from video data by Lecun's group. It is very useful to connect this popular deep learning algorithm to cortical data.

(2) The model formalism is relatively elegant and simple: Simple next input prediction objectives are conceptually simple but not necessarily trivial to build at scale. There is a clear benefit in comparison with contrastive or IL methods because they are free from dataset-specific data augmentation and negative samples. Thereby moving the comp neuro field towards conceptually simpler models of representation in the cortex. Yet predictive only models (and in particular predictive models in latent space instead of pixel space) are not easy to build in a stable fashion. JEPA family is basically intended to solve this question; it is very nice and timely to bring this to comp neuro.

(3) The methodology combining comp neuro and deep learning makes sense: The conceptual and qualitative analogy with cortical prediction errors is relevant and consistent with what is expected as a model of self-supervised learning in cortical models. The methodology to compare RPL with IL and CL is methodologically meaningful and grounded: showing, for instance, how some of the models fail to represent some latent structure in some toy datasets is interesting.

(4) h-RPL: The h-RPL is perhaps the most creative departure from the JEPA model family. It would be interesting to say more about what was particularly difficult to see in the latent variables emerging in the hierarchical model. I often find it magical that layer-wise learning rules of this type are not learning redundant representations. Any insights why this is not the case here would be potentially insightful.

Weaknesses:

In general, I fully support the type of question and ideas that the paper is putting forward. It is, however, very hard in this research field to gain insight into specific conceptual contributions or specific bits of experimental data that the model puts forward. In pointing to the following weaknesses, I am encouraging the authors to lay out more clearly what the unique hypothesis is or the contribution of the RPL model that we should remember it for.

(1) The devil is in the details:

1a) Comparison with JEPA variants: JEPA variants are integrating different details into the learning algorithm. Integrating, for instance, "masking" of the latent encoder targets, or EMA in the style of BYOL or Siamese networks, for the predicted representations. It is great that RPL does not seem to need any of those (next input prediction is a natural implementation of masking, and EMA does not seem to be used). It is notoriously hard for the JEPA model to work without these features. Since some of these details are sometimes surprisingly crucial for a simulation to work, it would be good to report which of the other important details were key to live without EMA and masking. Is it the difference in learning rate, for instance? Or maybe the tasks considered are simply easy enough for any model to work; if so, it could be useful to acknowledge to what extent this is true.

1b) Comparison with IL and CL: On a high level, the comparison with IL and CL algorithms is written as conclusive. I suspect that the failure modes of IL and CL that are described are not due to the algorithms themselves, but rather to the construction of invariance statistics or the choice of negative sample sets (the sets of samples among which variance 1 is requested by VICreg). For instance, if variance (or negative sample set) is taken only across time, the variance object identity is expected to collapse. Similarly, if the variance is taken across the object identity, the variance across time can collapse. So I wonder if the failure of IL and CL is induced by the construction of the variance definition.

(2) Prediction error: When compared to the recording of cortical activity in Figure 7. It is not obvious from the figure which latent space we are talking about mathematically. Is the vector z, c or the prediction error e? This is rather important from a neuroscientific point of view, because the prediction error e is expected to explain the neuronal data. On the other hand, the prediction error e is only used in the learning algorithm to define the loss function, but it is not the communication medium between the RNN units c (or with the encoder z).

In the brain, since the measurements are recorded as neural activity, they are communication channels between specific units (z or c). It is probably c or z that would already explain the oddball prediction error. I believe that other models, like Forward-forward of Nejad et al., have tried quite hard to address this apparent tension. Whether or not this is resolved by RPL, it thinks it would be beneficial to state the problem and clarify how the algorithm addresses or ignores the issue.

(3) Successor representation without value? I believe the term successor representation is historically relevant in a reinforcement learning (RL) setting and has a precise mathematical definition. Without RL, I feel that learning successor representation is conceptually identical to learning a transition matrix (aka, a primitive world model). I therefore wonder if the pitch for high-level framing of the successor representation is appropriately described or trivial.

(4) Learning in RNN: Learning with recurrent networks appears to be a key in this model presented here (it is in the algorithm name). Yet, this aspect of the model and the literature on biologically plausible learning rules for RNN is not really discussed.

Reviewer #2 (Public review):

This is a very interesting manuscript, which proposes a novel idea on how cortical networks may learn useful representations of sensory stimuli. The model implementing this idea is thoroughly tested in multiple experimental paradigms. The manuscript is very clearly written. I feel it may have a significant impact on our understanding of cortical circuitry.

Reviewer #3 (Public review):

Summary:

This paper presents Recurrent Predictive Learning (RPL), a self-supervised model conceptually similar to Joint-Embedding Predictive Architecture (JEPA) models. RPL sequentially observes dynamic scenes to predict subsequent observations. A central claim of the work is that the model's trained representations are simultaneously invariant and equivariant to transformations, such as movement properties that emerge without explicit supervision. These representational qualities are demonstrated through three experiments utilizing two simulated datasets and one naturalistic dataset. Furthermore, the latent embeddings are qualitatively compared with neural data, showing that the model reproduces the successor representation observed in human V1 and the local/global oddball effect in the monkey Prefrontal Cortex.

Strengths:

(1) The paper addresses a fundamental question relevant to both computational neuroscience and machine vision: how the brain learns representations that are simultaneously invariant and equivariant to transformations. The manuscript is well-written, easy to follow, and supported by clear visualizations.

(2) While JEPA-style models have recently gained significant traction in the artificial intelligence community, this paper nicely bridges the gap to neuroscience. By framing these architectures as a theory for visual learning in the brain, the authors provide valuable insights into how predictive frameworks can explain cortical processing.

(3) The qualitative alignment with V1 and PFC data is a particularly strong contribution, as it offers a potential mechanistic explanation for observed neural phenomena through the lens of self-supervised learning.

Weaknesses:

(1) The central claim, that both invariance and equivariance emerge spontaneously, requires further scrutiny (see Ghaemi et al., NeurIPS, 2025; Garrido et al., arXive, 2024). In particular, the synthetic "moving animal" dataset used in this paper may be too simple to fully support this claim. In latent space prediction, a model must predict both the scene content and the dynamics of movement. Because movement (whether ego-motion or external) is often highly uncertain (or multi-modal), predictive models in naturalistic settings often "collapse" toward learning purely invariant representations, ignoring the hard-to-predict dynamics. In the provided simulations, the movements are extremely predictable. In more complex scenarios, the model would likely prioritize content (invariance) over dynamics (equivariance) unless aided by action-conditioning or explicit factor estimation (Zhang et al., ICLR, 2026). The authors' results in Figure 5 using naturalistic video seem to reflect this limitation, given the lower performance on the naturalistic videos compared to the synthetic datasets.

(2) The framing of the RPL model as an entirely new theory of representation learning is slightly overstated. The focus on prediction in representation space rather than input space is the defining characteristic of JEPA and various other Self-Supervised Learning (SSL) models, even sequential prediction. While this paper clarifies the connection between these AI frameworks and cortical circuits, the work would be strengthened by more explicitly positioning RPL within the context of existing JEPA-style models and prior SSL theories of the visual system.

(3) A significant challenge in latent-space SSL is avoiding "representational collapse" (where the model provides a trivial constant output). While the paper alludes to JEPA-like solutions, it lacks a detailed explanation (in both the text and the architectural schematics) of the specific technique used to prevent collapse. Consequently, it is difficult to evaluate the authors' claim of "biological plausibility," as the biological equivalents of common machine learning techniques (such as stop gradient) are not discussed.

(4) Recent work has shown that the capacity (size) of the predictor significantly influences the learned representations in a JEPA-type world model (Gorrido et al., 2024). In simpler scenarios, a large enough predictor can allow a model to "memorize" dynamics rather than learning generalized equivariant features. It would be beneficial to see how the ratio of predictor size to encoder size affects the emergence of these features.

Methodological Clarifications:

(1) The authors mention a contrastive learning comparison but provide few details. Since contrastive learning is primarily a technique to avoid collapse, it would be a more rigorous baseline if implemented within the same architecture as RPL to isolate the effect of the predictive objective.

(2) In the PFC data comparison (Figure 7f), there appears to be a discrepancy where the local and global conditions show nearly identical results in PFC, while different dynamics in the model. It is unclear if this is a visualization error or a genuine model deviation.

(3) The criteria for selecting specific model variables for comparison with V1 versus PFC are not explicitly defined. Clarification is needed on whether the same latent variables were used for both brain regions or if different layers were selected.

Reviewer #1 (Public review):

Summary:

The authors combine discriminative auditory fear conditioning with longitudinal in vivo calcium imaging to ask how prelimbic (PL) representations of learned and generalized threat evolve across recent and remote memory time points. Using two different CS+ frequencies and a no-shock control group, they report that PL population activity tracks graded behavioral generalization, that population similarity is highest for tones eliciting strong threat responding, and that distinct subnetworks can be identified that appear to encode tone-specific sensory features versus learned threat-related response structure.

To my knowledge, this may be the first study to comprehensively examine neural encoding of fear generalization in prelimbic cortex (PL). The manuscript is ambitious and technically interesting, and several aspects are potentially important. In particular, the suggestion that neurons showing graded, learning-related response patterns become selectively stabilized over time is intriguing. The inclusion of two CS+ training conditions and a no-shock control also strengthens the case that at least some of the reported effects are related to associative learning rather than simple sensory differences. However, in its current form, the manuscript does not yet fully support the strength of the conceptual claims. Several issues limit confidence in the interpretation, including the possibility that repeated testing itself contributes to changes across days, uncertainty about the relationship between neural activity and freezing behavior, limited quantitative documentation of longitudinal cell registration, and a number of problems in figure clarity and statistical framing. Overall, the study contains promising observations, but the claims should be narrowed, and several analyses or controls would be needed to fully support the proposed framework.

Detailed Comments

(1) A general concern is that the repeated test procedure itself may contribute to extinction. Because the animals are exposed to multiple CS frequencies across multiple test days, and each tone is presented three times per session, some of the reported changes in behavior and neural activity across days could reflect extinction or repeated nonreinforced retrieval rather than the passage of time per se. This is especially relevant given that the manuscript makes claims about recent versus remote representations and representational drift over 30 days. At a minimum, the authors should discuss this limitation explicitly and temper claims about time-dependent changes. Ideally, they would include a control group in which animals are tested only once or twice (e.g., at an early and later time point with fewer CS frequencies), or a reduced-frequency testing design that minimizes extinction while still allowing evaluation of recent versus remote memory.

(2) More generally, some of the reported learning-related neural differences may be driven by behavioral differences, particularly freezing, rather than by learning or generalization per se. For example, animals that freeze more to certain frequencies may show corresponding neural response differences simply because freezing alters PL activity. The authors should examine this possibility more directly. Analyses testing whether recorded cells encode freezing behavior, or whether tone frequency-related neural differences remain robust when comparing high- and low-freezing epochs, would help determine whether the reported effects reflect learned stimulus value rather than behavioral state differences.

(3) A central feature of the manuscript is the analysis of neural response properties over an extended period of time, up to 30 days after learning. However, aside from a brief mention in the Methods that spatial registration was used, the manuscript provides very little quantitative information about this critical aspect of the study. The paper would be strengthened by including explicit metrics describing longitudinal cell tracking, such as the number and proportion of ROIs retained across all sessions, distributions of spatial-footprint correlations or centroid distances across days, and representative examples of matched imaging fields over time. Without this information, it is difficult to assess how strongly the longitudinal claims are supported.

(4) The text states that "Figs. 1c and 1d show GCaMP6f expression in PL, representative calcium footprints, and activity traces". However, the figure as presented does not clearly show all of these elements, at least not in a way that matches the description in the Results. The correspondence between text and figure should be corrected.

(5) The labeling of Figure 2a is insufficient for interpretation. The legend states that the panel shows raster plots of sound responsiveness, but the axes and scaling are not clearly defined. It is not clear from the figure what the x-axis represents, whether the y-axis corresponds to individual neurons, where the CS period occurs, or what the activity scale at the right denotes. Also, the term 'rasters' implies that spikes were analyzed. It seems that the spike inference approach (CASCADE) was only used for later analyses. Perhaps 'heat-plot' would be more accurate here? Generally, this figure should be annotated more clearly so that the reader can understand it without referring back to the Methods.

(6) In relation to Figure 3, the analysis of population-averaged responses across tone frequencies is useful, but the manuscript would be stronger with additional statistical analyses across time and across groups. For example, if the authors want to argue that learning induces graded changes in neural responses and that these evolve across time, they should directly compare within-group responses across days and also compare matched frequencies between the conditioned groups and the no-shock controls. These analyses would help establish whether the observed differences are genuinely learning dependent and whether they change significantly over time.

(7) The inclusion of two different CS+ frequencies and a no-shock control is a strength of the study and substantially improves the interpretation that graded neural responses are related to learning and generalization rather than to simple sensory processing or passage of time. That said, I am not entirely comfortable with the use of the term "inference" throughout the manuscript. What is being measured here appears closer to sensory generalization than inference in a stronger cognitive sense. The current task does not clearly require that animals infer hidden structure or stimulus value through abstract reasoning; rather, the generalized stimulus may simply be treated as similar to the conditioned cue. The terminology should therefore be reconsidered or softened.

(8) I also found the use of the term "valence" somewhat problematic. The manuscript appears to use valence to refer to graded responding across tones with different aversive significance, but valence typically refers more broadly to distinctions between appetitive and aversive value. Here, terms such as "threat value," "aversive value," may be more precise. The authors should consider revising this language throughout.

Reviewer #2 (Public review):

Summary:

The following points are those that occurred to me across readings of the paper. They are listed in what I take to be the order of their significance. Many of the points relate to the loose use of language and invocation of concepts that are not warranted, given the study design and results obtained.

Major Comments:

(1) The concept of ensemble turnover is interesting - the way it is introduced and discussed implies some type of spontaneous change in the neural underpinnings of fear discrimination and generalization in the PL. But, of course, every trial involves an opportunity to learn about the threat CS or the generalization test stimuli, and I am troubled by the thought that stability in the neural underpinnings of fear discrimination and generalization will actually reflect the level of defensive behaviours evoked on different trial types and/or the discrepancy between those behaviours and the outcome of a given trial in the generalization test. That is, stability in the neural underpinnings may be related to an animal's certainty or uncertainty in the contingency between a stimulus and danger; or, put another way, an animal's confidence that danger will or won't occur given the presence of some stimulus. This is not uninteresting. It is, however, not considered anywhere in the paper, which is overloaded with references to inferred threat values and integration of information across different types of stimuli. The protocol is not one that requires inference about anything or integration across anything.

(2) I appreciate the link to Gu and Johansen in paragraph 3 of the Introduction, but the type of generalization under investigation here is not the same as the type of 'generalization' studied by Gu and Johansen [who used a sensory preconditioning protocol]. Nonetheless, the authors have forced the language used by Gu and Johansen into their paper, and this has created tension [at least for this reader] as the concepts introduced by Gu and Johansen [inference, integration] are simply not relevant given the generalization protocol used here. Here are a few examples of points where the tension might interfere with a reader's understanding:

a. 'We hypothesized that generalization to novel stimuli depends on stable subnetwork organization that enables comparisons between learned and inferred valence, as well as population-level features that reduce variability across related representations.'

I understand the words in the hypothesis, but can't form a representation of what is being said because of the reference to terms that stand in need of clarification [inferred valence, variability across related representations], but, ultimately, won't be clarified. This needs to be re-expressed so that the reader can appreciate what is being said.

b. 'Our results show that stable cortical subnetworks integrate the emotional "gist" of memory and inferred valence for novel cues over time, despite ongoing ensemble reorganization, and that population-level firing rate similarity across stimulus presentations determines threat generalization.'

Again, what does this mean? How is the gist of a memory integrated with inferred valence for novel cues over time? The statement simply doesn't make sense. This needs to be rewritten for clarity.

c. 'In CS⁺15 mice, positively modulated sound-responsive neurons exhibited graded tone activity reflecting the contingency learned valence as well as the inferred valence of novel tones across testing days...'.

Can this be rewritten as 'In CS⁺15 mice, positively modulated sound-responsive neurons exhibited graded activity to the tone CS and its variants that were used to assess generalization.'? The overloading of the text with references to 'contingency learned valence' and 'inferred valence' is unnecessary and makes it much harder to understand what has been shown in the results.

(3) Re the same passage of text as in 2c:

Is it the case that these neurons are simply tracking the expression of freezing to the various tones? The same question applies to the results obtained for the CS+3 mice. If this is the case, then why should the results be taken to support the banner statement that 'Sound-modulated PL population responses encode learned and inferred valence' - these analyses do not support that statement. And, as indicated, I don't believe that the language of learned and inferred valence is appropriate to such statements, given the nature of the protocol used and results obtained. It is a study looking at how populations of neurons in the PL respond during presentations of auditory stimuli that were subject to discriminative conditioning, and during tests of generalized freezing to other [intermediate] auditory stimuli.

(4) It is stated that:

'In no-shock controls, although both positive and negative responses were present, population activity was not modulated by tone frequency or valence'.

What does this mean? I can understand that population activity was not modulated by tone frequency. But what does it mean to say that it was not modulated by valence? Why should it have been when none of the tones were conditioned in this group and, hence, mice were responding to all the tones equally? And given that this is true, I don't understand the use of 'valence' here, or the subsequent statements in this paragraph that 'graded responses require associative learning' and that 'PL population responses encode graded sound-valence associations that reflect both learning and inference, closely matching behavioral generalization.' The latter statement is particularly unwarranted and, again, highlights a major issue with the paper. It could and should be rewritten as 'PL population responses reflect behavioral generalization.' There is nothing in the additional language that adds to the reader's understanding of what has been shown. The reference to 'graded sound-valence associations that reflect both learning and inference' is completely unwarranted, given the nature of this study. It is anathema to the vast literature on stimulus generalization. If the authors wished to make statements of this sort, they should have taken a different approach, perhaps using protocols like those featured in Gu and Johansen.

(5) The section titled, 'Consistently active neurons preserve valence representations as newly recruited neurons sharpen remote memory traces' ends with the following summary:

'Together, these results indicate that consistently active neurons maintain stable representations of learned and inferred sound associations across time, whereas neurons recruited after conditioning progressively acquire graded tuning at later retrieval stages. This dynamic refinement suggests that cortical memory representations become increasingly selective during systems consolidation, while a stable neuronal subpopulation preserves the core emotional content of the memory.'

Once again, the summary is not in keeping with the results obtained. The 'dynamic refinement' of representations is far more likely to reflect the repeated testing across days 1, 15, and 30 rather than anything to do with systems consolidation - at the very least, it is the simplest interpretation of the results. The impact of repeated testing is evident in the sharpening of generalization gradients over time, which is contrary to what is otherwise observed in the literature - the incredibly well -documented broadening of generalization gradients with time. Given this impact of repeated testing, surely the changes in the neuronal population that underlie performance are more likely to reflect the learning that occurs on days 1, 15, and 30, which is reflected in reduced freezing to the non-conditioned tones. If this is a reasonable take on the results, then I don't see the basis for invoking systems consolidation at all, and I don't see the basis for inferring a stable neuronal subpopulation that preserves the emotional content of the memory. Rather, non-reinforced presentations of 'never-reinforced' tones result in recruitment of additional neurons that result in suppression of freezing responses to those stimuli.

(6) In the section titled, 'Population vector similarity at stimulus onset determines degree of generalization', it is stated that:

'Because population similarity peaked shortly after stimulus onset, we quantified similarity during the first 5 s after tone onset relative to the CS⁺. In CS⁺15 mice, population similarity was highest for 15/15 and 15/11 tone pairs with no differences between them.'

Isn't this consistent with the view that the population response in the PL simply reflects the level of freezing? Freezing to the 15-15 and 15-11 tones is most likely to be similar on their first presentation prior to the effects of extinction on the 11 Hz tone; hence the results obtained. That is, these results appear to clearly indicate that neuronal responses in the PL reflect the degree of stimulus generalization, as evidenced in freezing behavior. Given all that we know about the involvement of the PL in expressing fear responses, it is not appropriate to claim that 'population vector similarity at stimulus onset *determines* the degree of generalization. The PL responses simply reflect the varying levels of performance displayed to the different types of tones. What have I missed that could be taken to support additional statements?

Later in the same section, it is stated that 'population-level similarity at stimulus onset scales with behavioral threat generalization and is maximal for tones associated with robust threat responses.' For simplicity and, therefore, clarity, this should be rewritten as 'population-level similarity at stimulus onset reflects behavioral threat generalization.'

(7) In the section titled, 'Different subnetworks encode acoustic versus learned properties of sound association', it is stated that:

'Our previous analyses show that learned and inferred associations are represented at the population level. However, these results do not resolve whether graded responses arise from pooled activity of frequency-selective neurons or from subnetworks encoding integrated learned valence across tones.'

What does it mean to say 'integrated learned valence across tones'? As it presently stands, the meaning of the phrase is unclear. It only makes sense if one supposes that generalized freezing responses to the 11 and 7 kHZ tones reflect separate associations between those tones and the aversive foot shock US. This supposition is inconsistent with the rich literature on generalization of Pavlovian conditioned fear responses. Specifically, it is inconsistent with the many theories of fear generalization, which attribute the reduction in fear as one moves away from the specific conditioned stimulus to a decrement in the ability of the test stimulus to activate the trained CS-US association. My strong impression is that the authors would do well to ground their findings in theories of stimulus/fear generalization, of which there are many. This would better serve the results obtained [and the reader's appreciation of them] - at present, the unnecessary invocation of concepts does very little to enhance the reader's appreciation or understanding of what has been found in the study.

(8) Another example of what has been a common theme in this review :

'...we hypothesized that the PL active ensemble segregates into functionally distinct subnetworks: one encoding tone-specific sensory features with dynamic characteristics, and another responding to all frequencies encoding stable core memory content and inferred emotional valence.'

What does it mean to say 'all frequencies encoding stable core memory content and inferred emotional valence'? Do the authors mean to say '...and another that tracks freezing/defensive responses regardless of whether they were elicited by the trained CS or one of the generalization test stimuli'?

(9) It is stated that - 'Graded clusters encode emotional valence but constitute only a fraction of the active population; yet valence coding at the population level remains accurate and precise. This indicates that neurons newly recruited into the population-likely frequency-selective and organized within learning-independent clusters-can be shaped by associative processes through modulation of firing activity.'

What does this mean? Are the authors trying to say that - 'Some clusters of PL neurons track freezing responses. In spite of the fact that these are only a fraction of the total active neuronal population, the population-level response of PL neurons also tracks the levels of fear to the trained tone and its variants used in the test for generalization.' If this is what one wants to say, then the final statement in the reproduced section does not follow. That is, there is no indication that 'neurons newly recruited into the population-likely frequency-selective and organized within learning-independent clusters-can be shaped by associative processes through modulation of firing activity.' As noted, the characteristics of other ensembles that become active across the repeated tests on days 1, 15, and 30 are more likely to reflect learning from non-reinforcement that occurs within and across those sessions. Perhaps this is what is meant by the phrase, 'shaped by associative processes'? If so, it should be stated explicitly instead of left to the reader to work out.

(10) The following points all relate to the Discussion and reiterate many of the points above.

a. 'A subset of neurons remains consistently active across sessions, preserving core components of the memory trace and supporting inference of emotional valence for novel sounds, while neurons recruited after conditioning progressively acquire valence selectivity at remote time points.'

'Inference of emotional valence' is unclear and unwarranted for all of the reasons provided above regarding the use of language.

b. '...Our data reconcile these views by demonstrating that cortical representations of emotional valence emerge rapidly after learning and persist within stable subnetworks, even as the broader population undergoes substantial turnover. This architecture preserves core mnemonic content while allowing flexibility in the surrounding ensemble.'

These statements assume that the PL neuronal responses reflect something more than the levels of freezing behavior to the different stimuli; what are the grounds for this assumption?

c. 'Importantly, these subnetworks encode both learned contingencies and the inferred valence of novel stimuli along a graded representational axis, suggesting that strong recurrent connectivity provides a stable scaffold for emotional memory representations.'

What is a graded representational axis, and what part of the first statement suggests that 'strong recurrent connectivity provides a stable scaffold for emotional memory representations'? If the authors' goal was to make statements about emotional memory representations vis-à-vis emotional memory content, they should have used protocols that allowed them to probe such content. The auditory fear conditioning protocol used here [followed by tests for generalization to other auditory stimuli that differ in frequency from the conditioned tone] is not one that lends itself to analysis of emotional memory representations or content.

d. 'Dynamic tone-selective responsive neurons emerge independently of learning, as they are present in both control and experimental mice, reflecting pre-existing PL sensory-driven properties (Hockley & Malmierca, 2024; Zikopoulos & Barbas, 2006).'

Maybe. They are also likely to have developed as a consequence of the repeated testing on days 1, 15, and 30, which involved intermixed exposures to the tones of different frequencies. That is, rather than 'pre-existing PL sensory-driven properties', the responses of these neurons might reflect the emergence of discrimination between the various tones across testing, and greater suppression of freezing to the non-trained tones compared to the trained tone across the various test intervals.

Reviewer #3 (Public review):

Summary:

Normandin et al. explore the coding of stimuli predicting an aversive event in the prelimbic cortex. Stimuli could either be explicitly paired, explicitly unpaired, or novel but with an inferred association with the aversive event (generalization). Long-term tracking of GCaMP-positive neurons allowed them to examine how coding evolves out to a month following training. In general, they found two types of ensemble codes. One was ensembles coding for each stimulus independently, but with enhanced responding to the one eliciting a freezing response. The other was ensembles that responded to all stimuli in proportion to their similarity to the stimulus paired with the aversive event, either increasing or decreasing their activation with the degree of freezing elicited by a stimulus. Importantly, this second set of ensembles was more stable across days, potentially providing a memory trace.

Strengths:

(1) The authors track ensembles in prelimbic cortex over long time scales, providing valuable information on the consolidation of neural codes.

(2) Neural coding of generalization is examined, which is under-examined in the field.

Weaknesses:

(1) Difficult to determine if responses treated as encoding stimulus valence are driven instead by the behavior that the stimulus elicits, freezing.

(2) The study implies that the identified ensembles are causally related to valence memory, but no experimental interventions are performed to justify this.

Reviewer #1 (Public review):

The authors demonstrate an innovative approach to investigate the effect of cone dropout on visual acuity using their newly developed olo system. By systematically reducing the coverage of real-world input to the cone photoreceptor mosaic ("cone dropout condition"), the authors are able to assess how having fewer cones leads to reduced vision, in comparison to existing approaches ("pixel dropout condition").

The capture of a rich dataset, including cone imaging and eye motion, is valuable. Benchmarking with the prior literature, suggesting that good visual acuity can be maintained despite a 50% loss in cone density, is impressive. However, it is known that cone density varies dramatically from the peak cone density location in the foveal center to even a location a few degrees outside of the fovea. In addition, there is a high degree of subject-to-subject variation in peak cone density. Given that the C stimulus is hollow in the middle, the stimulus does not actually hit the location of the peak cone density but must land slightly outside of it. Therefore, considering the actual cone density of where the stimulus lands will be important to discuss and/or analyze.

The observation of visual acuity maintenance with cone dropout has been a longstanding mystery since the 2013/2018 papers by Ratnam and Foote. The authors should be commended for their approach to addressing this important question. However, there are some simplifications and assumptions being applied to make this jump (i.e., that a 50% reduction in cone stimulation in a healthy eye is comparable to a 50% reduction in cone density in a patient). It seems unlikely that, in a patient's eye, with cone dropout, there will be gaps in the mosaic. Not considering any other non-photoreceptor-related reasons for visual acuity loss, which can occur in patients, the cone aperture acceptance angle may be different due to changes in cone size or packing; the sensitivity of individual cones may also be reduced due to deficits in the visual cycle recovery, which could be affected in disease. Some of these limitations could be addressed and acknowledged more explicitly.

Overall, this is an impressive study incorporating state-of-the-art technology to probe the fundamental limits of human vision.

Reviewer #1 (Public review):

Summary:

Fujita and colleagues investigated two selective peripheral nerve voltage-gated sodium channel inhibitors targeting either Nav1.7 or Nav1.8 on the excitability of human dorsal root ganglion neurons. The authors discovered that Nav1.8 inhibition is more effective at suppressing repetitive firing of DRG neurons, and this may explain the greater clinical efficacy observed for suzetrigine.

Strengths:

The study is interesting, and the findings are conceptually satisfying in that they may explain one aspect of Nav1.7 vs Nav1.8 targeting success.

Weaknesses:

(1) The use of postmortem human DRG neurons provides translational relevance, but the use of these cells is also a liability, given their high degree of variability. Of note are the 10 to 20-fold differences in baseline properties among cells, which dwarf the effects of the test compounds. The experiments may suffer from undersampling.

(2) A potential confounder when using post-mortem human DRG neurons is heterogeneity of cell types. The methods clearly state that the cells selected for recording were of 'generally' small size, but specific criteria for what constitutes 'small' or other unstated selection criteria were not provided. A table of individual cell capacitance and input resistance values, along with information about individual donors (age, sex, ethnicity), is important to include. Additionally, some discussion of how DRG neuron heterogeneity impacts the findings. This relates to concern #1 about sample size determination and how cell heterogeneity factored into this calculation.

Reviewer #2 (Public review):

Summary:

The authors examine the functional role of Nav1.7 voltage-gated sodium channels in human sensory neuron electrogenesis using a Nav1.7 selective inhibitor and human dorsal root ganglion neurons obtained from organ donors. Patch-clamp electrophysiology is used at physiological temperature to measure the impact of Nav1.7 inhibition on sensory neurons' action potential firing. This is an important topic as Nav1.7 and Nav1.8 have been identified as therapeutic targets for the treatment of pain, but there has been mixed success with isoform-specific inhibitors in clinical trials. The data suggest that Nav1.7 and Nav1.8 have overlapping yet complementary functions in nociceptor neurons and that targeting both may be most effective for reducing nociception.

Strengths:

The data are of high quality. Action potential properties are measured at 37 degrees Celsius. Threshold is measured using brief pulses. The Nav1.7 inhibitor has been reported to be highly selective for Nav1.7 over Nav1.8 and moderately selective for Nav1.7 over Nav1.1 and Nav1.6. Data are collected using identical conditions and protocols to a previous study on the role of Nav1.8 in similar neurons.

Weaknesses:

The study relies on a single Nav1.7 inhibitor that has not been extensively characterized. One prior study indicates that the IC50 is around 140 nM, thus the 600 nM concentration used in this study could be predicted to reduce Nav1.7 currents by 80%. However, there is no voltage-clamp data in the current study to confirm this, and therefore, it is unclear if the batch of AM-2099 is as potent as reported in the paper that initially described its selectivity. The impact of Nav1.7 inhibition is compared to data from a previous study by this lab, and this is a minor concern. It would have been interesting to see if the combined inhibition of Nav1.7 and Nav1.8 completely blocked action potential generation in the human DRG neurons.

Reviewer #3 (Public review):

Summary:

In this manuscript, Fujita/Jo/Stewart/Osorno et al. investigate the contribution of Nav1.7 in regulating the excitability and firing properties of human dorsal root ganglion (hDRG) neurons in vitro. The authors characterize the effects of a previously reported Nav1.7-selective blocker AM-2099 in cultured hDRG neurons from postmortem organ donors. The authors observed modest changes in many of the properties expected by inhibiting Nav channels, including decreased action potential upstroke rate and amplitude, while increasing the voltage and current thresholds for spike generation. However, AM-2099 did not change the maximum number of APs in response to suprathreshold stimulation, leading the authors to conclude that Nav1.7 inhibition alone has limited efficacy in reducing the firing properties of hDRG neurons and that Nav1.7 blockers may have limited efficacy as analgesics. This is surprising, given that patients with loss-of-function mutations in Nav1.7 suffer from congenital insensitivity to pain. While it may indeed be true that pharmacological inhibition of Nav1.7 is unlikely to produce analgesia, the present study was limited to a single concentration of AM-2099. The manuscript would be significantly strengthened by a more careful and thorough pharmacological characterization of this compound, which has not been widely used or validated in native human DRG neurons.

Strengths:

Experiments are well-designed and executed, and the results presented are convincing. The focus on voltage-gated sodium channels in native human DRG neurons is highly relevant to recent efforts to develop safer analgesic options for chronic pain in people.

Weaknesses:

Only a single concentration of AM-2099 was used for all experiments. This compound was reported to be selective for cloned human Nav1.7 channels in heterologous systems, but has not been validated in other studies after the original publication in 2016. Since the original study reported a substantial state-dependent block of recombinant Nav1.7 channels, more detailed pharmacological characterization of AM-2099 is needed in human DRG neurons to fully support these claims. This study would be significantly strengthened by the inclusion of dose-response curves to assess how much of the sodium current is inhibited at this concentration, confirming selectivity in hDRG, and whether maximal inhibition of Nav1.7 still has limited efficacy in reducing the firing of native human sensory neurons.

Reviewer #1 (Public review):

The manuscript shows that different traits of adults and larvae correlate with Red List status. The authors argue that this shows a big gap in the conservation of amphibians and that the traits of all life stages should be taken into account in amphibian conservation. Specifically, amphibian conservation should do more for the habitats where the larvae live.

The manuscript is well written and easy to understand. The methods are sound.

While the study will make an interesting contribution to conservation science, there are many things that I disagree with.

I don't think that amphibian larvae and their requirements are a "blind spot" as the title suggests. When reading the manuscript, I didn't learn how conservation practice should change in response to the results.

I wonder whether the relationship between species traits and extinction risk is of great importance for conservation. If a species is Data Deficient on the IUCN Red List, then species traits could be used to predict its Red List category. However, for other conservation projects, I don't see how this would work. How would traits be linked to captive breeding, conservation translocation, pond construction or habitat management in general? In some cases, I can envision a link between species traits and pond hydroperiod.

Species traits are body size and morphological traits. That makes sense. However, one of the species traits was microhabitat. I find it far-fetched to call habitat a species trait. This is standard habitat ecology. It is well known that habitats matter and that different habitat types face different threats, and consequently, the species that live in those habitats. Furthermore, habitat and morphology may be confounded. For example, tadpoles in lentic and lotic habitats have very different morphologies. So is it habitat or morphology?

I don't know how the threat status of Chinese amphibians is determined. IUCN has multiple reasons why a species can be Red Listed. One reason is range size, and another reason is population decline. Personally, I don't think they should be pooled in an analysis because they are fundamentally different reasons why a species has a high extinction risk. A reduction in population size of greater than 30% in 10 years or 3 generations is not the same thing as a small distribution range. Another issue is that IUCN developed the Green Status of species. The Green Status shows that even a species which is LC on the Red List may be significantly depleted.

The species traits in Table 1 are mostly functional/morphological and body size related (and microhabitat). While there may be correlations between traits and Red List status, it is unknown whether this is correlation or causation. In addition, it is difficult to know the conservation interventions that may be necessary now that we know that relative head with and Red List status are correlated.

In the discussion, the authors explain why body size and other traits may affect extinction risk and whether there is a causal relationship. I agree that body size may have a direct effect because larger species are harvested more frequently (it was interesting to learn that tadpoles are harvested as well). However, as macroecological studies show, smaller species often have larger populations than larger species. Abundance may matter.

I found it much harder to understand why relative head length and tympanum size correlated with Red List status. I wasn't convinced by the arguments in the discussion. Typanum size may be related to hearing and anthropogenic noise. Several studies are cited which show that frogs alter their calling behaviour in response to noise. Crucially, however, they describe changes in behaviour or properties of the advertisement call, yet none show that noise has effects on population viability. If some anthropogenic stressor affects individuals, then this does not mean that it will cause a population decline. When IUCN published the second global amphibian assessment, did they list noise as a major threat to amphibians?

There are statements that the tadpole stage is the most important stage: "a critical period for amphibian survival" (line 78-79). While there is high mortality in the tadpole stage, tadpole survival is rather unlikely to affect population survival. Many population models show this. See, for example, Biek et al. 2002 in Conservation Biology. Other papers have argued that the postmetamorphic juvenile stage is most important (Petrovan and Schmidt 2009 Biological Conservation).

The authors repeatedly make the statement that amphibian conservation should focus more on the tadpole stage. I don't understand why this statement is made. For example, a major activity in amphibian conservation is the restoration and de novo construction of ponds (see Calhoun et al. 2014 PNAS, Moor et al. 2022 PNAS). Ponds are habitats for tadpoles. Others removed fish from amphibian breeding sites because fish prey on tadpoles (and adults; see Vredenburg 2004 PNAS). Semlitsch (2002 in Conservation Biology) argued that the management of pond hydroperiod is a critical element of amphibian recovery plans. Ponds should be temporary because this effectively removes predators that consume tadpoles. Clearly, the tadpole stage is not a neglected stage in amphibian conservation.

Reviewer #2 (Public review):

Summary:

In this study, the authors tried to examine whether there are differences in the association between functional traits and extinction risk in adult and tadpole stages in Chinese anurans.

Strengths:

Overall, I think the basic idea of the study is interesting and important. It can be applied to other taxa with complex life cycles throughout the animal kingdom.

Weaknesses:

I do not think the authors achieve their aims, as the results only partially support their conclusions. The study has several drawbacks that need to be clarified or revised, including the unclear threat categories for tadpoles, model selection and model averaging, the potential problem of AIC, and the omission of other important species traits.

Reviewer #1 (Public review):

Summary:

This manuscript provides a comprehensive and mechanistic analysis of how tsetse flies feed on blood across a wide range of host skin types. The authors combine detailed anatomical characterization of the feeding apparatus with quantitative measurements of mechanical properties, probing forces, and blood uptake, complemented by experiments using artificial skin. They show that tsetse flies do not rely on extreme forces or uniquely specialized structures, but instead on subtle and highly efficient structural and mechanical adaptations (such as the toothed labellum and coordinated proboscis movements) to achieve effective blood pool feeding. The study successfully moves beyond descriptive anatomy to a quantitative, functional analysis that explains how feeding is accomplished across diverse substrates.

Strengths:

A major strength of the work is the impressive integration of multiple complementary approaches. Advanced imaging tools provide a convincing three-dimensional view of the proboscis, labellum, and associated structures, while direct force measurements and blood intake quantification place these observations on a solid quantitative footing. The use of artificial skin with different mechanical properties is particularly powerful, as it allows structure-function relationships to be tested under controlled and reproducible conditions. Together, these datasets provide strong and coherent support for the authors' central conclusions. The quantitative treatment of feeding mechanics represents a significant advance over largely descriptive prior work by others (e.g., Gibson W et al 2017) and establishes a valuable mechanistic insight for studying blood feeding in insect vectors more broadly.

Weaknesses:

The study focuses almost entirely on uninfected flies and does not address how infection might alter feeding mechanics or performance. Previous work has shown that trypanosome infection can affect salivary gland function and feeding time (Van Den Abbeele et al 2010), and even cause damage to mouthparts, all of which can influence feeding behavior and efficiency. While this does not detract from the technical quality or the core findings of the study, a more explicit discussion of these biological variables would help place the results in a broader transmission-relevant context and clarify how generalizable the conclusions are to natural infection settings.

Overall, this is an outstanding and carefully executed study that will have a significant impact on the fields of vector biology and parasite transmission.

Reviewer #2 (Public review):

Summary:

This manuscript presents an impressively detailed, multidisciplinary analysis of the mechanics of blood feeding in Glossina spp. Combining SEM, CLSM, µCT, FIB‑SEM, macro‑videography, and quantitative force measurements, the authors characterize the structures and biomechanics of attachment, proboscis deployment, tissue penetration, and blood uptake. They also examine interactions with diverse host‑type substrates, from human skin equivalents to cow, deer, and lizard skin, and integrate these with force measurements to quantify penetration and retraction dynamics.

The work's key conclusion is that the tsetse fly does not rely on any single exceptional morphological innovation, but rather uses a suite of subtle structural features and retractive forces to feed efficiently across diverse hosts. This result is novel, insightful, and evolutionarily compelling. Overall, this is a strong manuscript that combines methodological sophistication with biological relevance. It should be of high interest to researchers studying vector biology, biomechanics, parasite transmission, and vector-host interactions.

Strengths:

(1) The combination of SEM, CLSM, µCT, and FIB‑SEM provides an unusually comprehensive anatomical characterization of the tsetse feeding apparatus.

(2) The direct measurement of proboscis penetration and retraction forces across diverse substrates is highly original and fills a major knowledge gap in vector-host interaction mechanics.

(3) The study bridges morphology, mechanics, behavior, and host tissue properties, which strengthens the overall conclusions.

(4) Imaging of trypanosomes within the hypopharynx and surrounding tissue during feeding provides new information about parasite delivery mechanisms.

Main Comments:

(1) The authors conclude that feeding versatility arises from the sum of subtle adaptations. This interpretation is reasonable, but it would help to sharpen which findings most robustly support this statement. For example, the relative similarity of proboscis forces across skin types is compelling evidence that the proboscis is broadly tuned rather than specialized. The observation that tsetse targets softer interscale regions on lizard skin suggests behavioural selectivity, not morphological specialisation. It would strengthen the discussion to highlight which data most directly refute the hypothesis of a unique specialization.

(2) A central finding is that retraction forces exceed penetration forces across substrates, implying that backward pulling is a key component of wound creation. However, the biological interpretation could be deepened. Specifically, do the authors believe retraction serves primarily to enlarge the pool‑feeding site? How does this compare mechanically to mosquito fascicle oscillation or other blood‑feeding arthropods (especially other flies such as those in the tabanidae family)? Could retraction forces contribute to anchoring or resisting host grooming behaviors?

(3) The study analyzes a diverse set of substrates, which is a strength. However, some caveats deserve explicit discussion. Human skin equivalents and dermal equivalents lack the full mechanical complexity of real skin (e.g., innervation, perfusion, tension). Frozen or ethanol‑stored samples, particularly reptile skin, may also exhibit altered mechanical properties compared to live tissues. These limitations do not undermine the findings but should be explicitly acknowledged as they influence the interpretation of absolute force magnitudes.

(4) The SEM and FIB‑SEM images showing trypanosomes in the hypopharynx and surrounding tissue during penetration are visually striking and suggest rapid dispersal. It would be helpful to connect these observations more clearly to the kinetics of parasite deposition and whether mechanical tissue laceration is likely to increase inoculation efficiency. Without conducting additional experiments, the authors could discuss whether these findings support or modify existing models of salivary-gland-derived parasite release.

(5) The authors demonstrate that tsetse attachment abilities fall within the range of generalist insects and are far lower than those of obligate ectoparasites. However, the manuscript could discuss how attachment forces relate to the tsetse's ecological context, e.g., whether their attachment is generally brief, whether host shaking strongly selects for grip strength, etc. Is there evidence that other Glossina species or tabanids with different host preferences show variation in attachment performance? This would broaden the relevance of the findings.

(6) In video 4, could the authors clarify whether the observed maxillary vibrations are hypothesized to reduce penetration resistance or serve another function?

Reviewer #3 (Public review):

Summary:

Human and animal trypanosomiasis are fatal illnesses caused by African trypanosomes transmitted by tsetse flies during a bloodmeal. Thus, tsetse fly feeding is the key physical step in disease transmission to mammals. Tsetse fly feeding is not a new story, but it is revisited here through the application of sophisticated imaging techniques and novel biomechanical methods of analysis. The authors aim to provide a high-resolution picture of the structures and forces involved in feeding to provide mechanistic insights into the process of feeding, from attachment, penetration, drinking and retraction of the feeding parts.

Largely, the authors have achieved their aims. They (i) examine the structures and forces involved in attachment; (ii) they provide detailed multi image analysis of the proboscis providing insights into its probing ability and physical mechanism of penetration; (iii) they conduct a controlled analysis of the physical forces involved in penetration and report that they are in the low nM range, not especially strong but much higher that the mosquito bite and finally they provide a first analysis of blood uptake during feeding.

Strengths:

The study images the tsetse fly feeding structures in unprecedented detail, with resolution to the uM scale, in 3-D, and during feeding. The resulting images are dramatic and insightful (and beautiful and frightening!), so researchers interested in trypanosomes, tsetse flies, or blood feeding by flies in general will want to see.

They conclude that flies attach strongly to smooth surfaces because of interactions possible via the array of acanthae of the pulvillus pad at the ends of the tarsi. The estimated attachment forces are similar in male & female flies, in the low mM range (they look impressively strong in video 1). They provide a very striking analysis of the proboscis and labellum and associated tooth structures (Figures 4 & 5). I recall many years ago observing that tsetse flies are messy feeders, and these structures, especially the rasping teeth structures on the reverse folded labial tips, explain why! This seems more like a chainsaw than a jigsaw in action, but the authors are probably correct that these structures and the probing/retraction mechanism explain many features of tsetse fly feeding and their ability to feed on a wide range of hosts with very different skin types.

The impressive aspect of this paper is the range of imaging techniques (CLSM, SEM, uCT, FIB SEM), the quality of the images, which attests to the obvious care taken with sample preparation. The biomechanical analysis, especially the penetration analysis, is impressive. Finally, the paper is clearly written and presented; it was a very easy read and, overall, a very engaging study.

Weaknesses:

I suppose it could be said that the paper is a descriptive study; it doesn't really test a hypothesis, but that is not a prerequisite for sharing it. Perhaps the least convincing parts are the imaging of the flexible versus rigid parts of the structures, which is based on the amount of resilin (flexible) and chitin-protein (stiff), based on their autofluorescence. It seems odd that the joints would be less blue (stiffer) in Figure 1i, or what the blue structures correspond to in Figure 6B-D.

Reviewer #1 (Public review):

In this manuscript, the authors investigate the relationship between genetic codes and their robustness to single-point mutations. They construct ten alternative genetic codes by reassigning nine codons to Leu, Ser, or Ala, and assess mutational robustness using three reporter proteins subjected to error-prone PCR. This represents an interesting experimental approach to addressing the hypothesis that the standard genetic code is optimized for mutational robustness.

Major comment:

While I find the experimental design valuable, I am not fully convinced by the authors' conclusion that "alterations of the genetic code within the ranges explored in this study have no significant effect on mutational robustness". The current analysis is based on the functional output of three individual reporter proteins. Given that cellular systems involve far more complex interactions, it would be more appropriate to limit this conclusion to mutational robustness at the level of individual protein activity, rather than making broader generalizations.

Specific comments:

(1) tRNA modification and expression efficiency (Page 5, line 131).

The authors attribute the observed inefficiency to the lack of chemical modifications in the tRNAs used. However, gene expression efficiency can also be strongly influenced by DNA sequence design. To better support this claim, it would be helpful to compare luciferase activity when expressed using native E. coli tRNAs. This comparison could clarify whether the observed effects are due to tRNA modification status or other sequence-dependent factors.

(2) Discrepancy between expression level and activity (Figure S7 vs Figure S8).

Although GAL expression levels appear similar across different genetic codes (Figure S7), their activities differ substantially (Figure S8), even in the low-mutation library. This discrepancy warrants further investigation. Possible explanations include differences in protein folding efficiency or translational error rates, as mentioned by the authors in the main text.

To address this, the authors could analyze the protein products using mass spectrometry. If this is not feasible due to low expression levels, alternative approaches such as SDS-PAGE (e.g., with radiolabeling or Western blotting) would still provide valuable information. Additionally, comparing activity after in vitro refolding could help distinguish between folding defects and sequence-level errors. While I understand that the primary aim of this study is to compare mutational robustness across genetic codes, discussing these observations would significantly enhance the mechanistic insight of the work.

(3) Protein expression analysis for additional reporters.

Since protein expression levels are critical for interpreting reporter activity, similar analyses should also be performed for luciferase (Luc) and mSG in both high- and low-mutation libraries. This would ensure that differences in activity are not confounded by variations in protein abundance.

Reviewer #2 (Public review):

Summary:

The study addresses the long-standing question in molecular biology and genetics: why has nature selected the current genetic code (SGC, or standard genetic code)? The authors have tested 'error minimization theory', one of the prevailing hypotheses to explain this. Their approach is to create a minimum genetic code (MGC) and its variants (3^9 theoretical possible codes). Using three parameters to quantify the effect of mutations (Polarity, volume, and hydropathy), they computationally test the cost of these genetic codes (3^9) by simulations. Finally, they test this cost experimentally using an in vitro translation system with 10 select genetic code variants with a range of costs (low to high). They use three randomly mutated reporter genes for this purpose - beta-galactosidase, luciferase, and mSG. They find no correlation between the cost of the genetic code and the reporters' output. Based on these observations, they suggest that error-minimization theory may not explain the current egocentric code.

The question they are asking is very exciting, and their approach is solid. The authors are very careful in their analyses and conclusions.

Major Concerns:

(1) The rationale for using MGC instead of SGC: It is unclear why the authors rely on the MGC for this analysis when the central question concerns the SGC. If the goal is to evaluate whether the SGC minimizes mutational cost, a more direct approach would be to generate alternative variants of the SGC itself and compare their mutational cost distributions. At present, it is difficult to assess whether conclusions drawn from this comparison are fully relevant to the stated biological question.

(2) The mutational cost analysis appears biologically oversimplified because all amino acid substitutions are treated equivalently. The analysis assumes that all mutations contribute equally to fitness consequences, which does not reflect biological reality. In natural proteins, the impact of an amino acid substitution depends strongly on its structural and functional context. For example, substitutions affecting catalytic residues, ligand-binding interfaces, phosphorylation sites, or other regulatory motifs can severely impair protein function even when associated changes in polarity, hydropathy, or volume are minimal. Conversely, substitutions in structurally permissive or functionally dispensable regions may have little or no measurable effect despite larger physicochemical differences. Therefore, changes in polarity, hydropathy, and volume alone do not necessarily predict functional consequences.

(3) It is not clear why they increased the concentration of the two tRNAs in near-SGC. Have they maintained the same tRNA concentrations in experiments explained in Fig 5 for all 10 genetic codes tested?

Reviewer #3 (Public review):

Summary:

In this manuscript, Miyachi and Ichihashi investigate whether the arrangement of the genetic code affects mutational robustness. Using an in vitro minimal genetic code with vacant codons, they constructed 10 non-standard genetic codes by reassigning Ala, Ser, and Leu, generating codes with replacement costs that were generally higher than those of the standard genetic code across several amino acid property measures. They then tested how random mutations affected the activity of reporter proteins translated under these altered codes. Although error minimization theory predicts that higher-cost codes should make mutations more harmful, the authors report that protein function declined to a similar extent across all codes examined, suggesting that mutational robustness remains largely unchanged within the range of genetic code alterations tested here.

Strengths:

This is an interesting study that investigates one of the most fundamental and intriguing questions in molecular evolution: the emergence of the genetic code, which is nearly universal across nature. The in vitro approach is a powerful aspect of the work and provides an opportunity to examine this phenomenon experimentally at a depth that has previously been inaccessible.

Weaknesses:

However, the authors' use of random mutation libraries has certain limitations that prevent the study from realizing its full potential to uncover the mechanisms governing the molecular evolution of the genetic code.

Major points:

(1) Statistical analyses are missing for several of the manuscript's main claims. This issue applies throughout the paper, including, but not limited to, Figures 1D, 2B, 4B-D, and 5B.

(2) In Figure 2A, the authors modify the NanoLuc gene by reassigning Ala, Leu, or Ser to new codons and elegantly show that the in vitro availability of the corresponding tRNAs is important for protein function. However, the functional importance of the specific modified positions within NanoLuc is not clear. As a result, it is difficult to determine what the expected consequences of these codon changes should be, which in turn limits the interpretation of the observed changes in protein activity. To improve the interpretability of this experiment, the authors should report exactly how many codons were modified in each variant and, ideally, examine the effect of progressively increasing the number of reassigned codons.

(3) The calculations presented in Figure 3 raise an interesting conceptual question: why does the near-standard genetic code not exhibit the lowest cost? One possible explanation is that the standard genetic code evolved under multiple competing constraints and is therefore not expected to be optimal for any single cost metric, while still achieving strong overall performance. In this context, it would be informative if the authors combined the three cost measures into a single integrated index and examined whether the near-SGC performs more favorably when all three dimensions are considered together. Such an analysis could add important depth to the study.

(4) It is difficult to assess the consequences of the random mutations presented in Figure 4 on reporter gene function based solely on the reported "error rate/base" parameter. In particular, the x-axis in Figure 4B should be converted into the estimated number of mutations per gene. This would make the results more intuitive and would allow the reader to better evaluate the expected degree of disruption to protein function.

(5) A central limitation of the random mutagenesis libraries used in Figure 5, which also underlie one of the manuscript's main claims, is that the exact mutations and their distribution across the reporter genes are not reported. In addition, protein activity is measured only at the level of the entire library, without directly linking individual mutations to their functional consequences. This substantially limits mechanistic interpretation. In my view, this issue can only be addressed convincingly if the authors test a set of defined variants carrying specific mutations and directly evaluate their functional effects.

(6) Related to the previous point, in Figures 5C, 5E, and 5G, the authors present the ratio between low-mutation-rate and high-mutation-rate libraries. However, because each library contains a different collection of mutations, it is unclear what can be inferred from these comparisons. To overcome this limitation, the authors should assess the effects of altered genetic codes on specific, defined mutations rather than on heterogeneous mutation pools alone.

(7) Along the same lines, in Figures 5C, 5E, and 5G, it is unclear why the effects of random mutations would be expected to correlate with the three calculated cost metrics, given that the positions, identities, and functional relevance of the mutations within the genes are not known. Without this information, the biological meaning of these correlations remains difficult to evaluate.

(8) For each mutagenesis library, the number of variants, the average number of mutations per variant, and the distribution of mutation positions should be reported clearly and transparently. These details are important for evaluating the strength of the conclusions.

(9) Because only three amino acids were manipulated in the non-standard genetic codes, it remains unclear whether these particular amino acids occupy positions in the reporter proteins that are especially important for function and therefore likely to generate strong phenotypic effects. More broadly, it is not clear whether the assay is sufficiently sensitive to detect the effects of only a subset of deleterious variants within a pooled library. This point should be addressed more explicitly.

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HTML可以创建具有颜色编码、内联注释等高级功能的PR审查工具，这是Markdown难以实现的。

Reviewer #2 (Public review):

Summary:

This study uses dental traits of a large sample of Chinese mammals to tract evolutionary patterns through the Paleocene. It presents and argues for a 'brawn before bite' hypothesis -- mammals increased in body size disparity before evolving more specialized or adapted dentitions. The study makes use of an impressive array of analyses, including dental topographic, finite element, and integration analyses, which help to provide a unique insight into mammalian evolutionary patterns.

Strengths:

This paper helps to fill in a major gap in our knowledge of Paleocene mammal patterns in Asia, which is especially important because of the diversification of placentals at that time. The total sample of teeth is impressive and required considerable effort for scanning and analyzing. And there is a wealth of results for DTA, FEA, and integration analyses. Further, some of the results are especially interesting, such as the novel 'brawn before bite' hypothesis and the possible link between shifts in dental traits and arid environments in the Late Paleocene. Overall, I enjoyed reading the paper and I think the results will be of interest to a broad audience.

Weaknesses:

For the original draft of the manuscript, I had four major concerns with the study, especially related to the sampling, diet, and evidence for the 'brawn before bite' hypothesis. I still believe that the original issues that I raised may be weaknesses of the study. For example, there is still limited discussion on diets (even though the dental topographic analyses used in the study are designed for inferring diets). And I find the results a little challenging to interpret because teeth of multiple positions are included in the same samples, which seems problematic. That said, the authors have addressed each of my previous concerns and have made major revisions, including running new analyses, and thus I support the paper.

Reviewer #2 (Public review):

Summary:

The authors pair analysis of replication timing and allele-specific expression in clonal populations of primary human cells. They combine these data with previously published data on clones from transformed human cell lines. They identify a number of genomic regions that display asynchronous replication timing in at least one clone and correlate these regions with allele-specific expression of genes within them. They also observe that several interesting gene sets, including genes that are associated with human diseases, map to asynchronously replicating regions. This is a good experimental approach that builds on already published data demonstrating the connection between allelic imbalance and replication timing.

- This is a research topic that touches on a few sub-fields of biology, and thus to make the paper more approachable we would recommend a careful edit of the text for clarity and precision of language.

- Authors point out that this is a decades-old field; we would suggest to use terminology established within the field is possible. Allelic imbalance has been referred to as AI, MAE (monoallelic expression), RMAE (random monoallelic expression) etc. The paper whose mouse data the authors make use of uses Asynchronous Stochastic Replication Timing (ASRT) instead of VERT to refer to the same phenomenon.

- Methods do not provide fully sufficient detail to fully evaluate or reproduce these experiments.

- It is helpful to show representative loci as the authors do in Fig 1F and G and Fig 2 but these panels are very densely rendered and thus difficult to process visually - even the cartoon version (1D) is thick with overlapping lines. The point that allelic imbalance is enriched in VERTs would be enhanced if the authors could present the allelic ratio for all genes found in all VERTs, demonstrating how replication timing on either chromosome affects the allelic ratio.

- The authors make the important point that VERTs are unlikely to be shared among different cell types and tissues (Fig 1i), but then find an enrichment for neuronal and immune genes in VERT regions identified in ACPs. It follows that these same genes are unlikely to be in such regions in the tissues where they are relevant. Some of the GO terms presented are too broad to suggest any biological significance to the result, even if there is statistical significance (for example, the top term for LCL clones 'Cytoplasm' is associated with 12,000 genes, and the second term for mouse clones 'Membrane' is associated with 10,000). It would be helpful to focus on GO terms lower in the GO hierarchy.

- Figure 3 highlights the association of related gene clusters with VERTs but the VERTs are assigned based on variable replication timing in just 1 or 2 clones. This is an interesting observation, but to make the point that "VERT regions frequently coincide with gene clusters in the human genome" there needs to be a systematic assessment of replication timing at all gene clusters across all clones, and a statistical test for significance.

- It is an interesting hypothesis that VERTs are conserved between species at syntenic loci. If such regions are really conserved, one would expect that replication timing at these sites would be consistently asynchronous. However the data presented shows that in human clones these VERTs can be specific to an individual donor (as in 5A) or an individual clone (as in 5H).

- The finding that VERTs coincide with neurodevelopmental disease genes in immune and cartilage cells is at odds with the previous statements and data about the tissue specificity of VERTs. In order to support the claim that neurodevelopmental disease associated genes reside in asynchronously replicating regions, and are thus more prone to allelic imbalance, it would be helpful if the authors demonstrated this phenomenon in neuronal cells.

- The authors consistently lean on sparse samples (i.e. a single clone) within a modestly sized dataset (4 clones from 2 donors each) to propose a new model for haploinsufficiency in human disease. It may well be but the consistent focus on limited elements in the data and perhaps an overreach in the interpretation makes it difficult to appreciate the very good experiments presented.

- This section refers to the revised version of the paper.

We would like to thank the authors for the changes and explanations offered. Although we don't fully agree with a few answers offered, overall the answers and changes in the manuscript have significantly improved the work presented. As such it should be of interest to many readers.

Reviewer #1 (Public review):

Summary:

The study by Zatulovskiy et al. examined how cell size influences cell susceptibility to ferroptosis. The authors found a size dependence specifically for ferroptosis-inducing drug Era2, but not for other drugs. Using various human cell lines (HMEC, HT 1080, RPE 1), the authors generated populations of small and large G1 cells by FACS, CDK4/6 inhibition (palbociclib), or inducible cyclin D1 knockdown, and measured cell susceptibility to ferroptosis. Larger cells were more resistant than smaller cells. Mechanistically, larger cells showed reduced plasma membrane lipid peroxidation, higher glutathione concentrations, and changes in relevant cellular proteins levels, as analyzed using previously published data. Deleting ACSL4, which is involved in ferroptosis, partly eliminated the size dependence of ferroptosis. The work concludes that cell size is a key determinant of ferroptosis susceptibility. Overall, this work expands our understanding of how cell size is correlated with functional properties of cells, which can have implications for biomedical sciences.

Strengths:

The study establishes a credible link between cell size and susceptibility to ferroptosis, as induced by Era2. Experimental replication is sufficient, and key conclusions rely on data from multiple cell lines and on multiple approaches to manipulate cell size. This suggests that the conceptual findings made in this paper could reflect a more fundamental feature of mammalian cells. In addition, this work provides an interesting contrast to another recent study about size-dependency of ferroptosis (https://doi.org/10.1016/j.isci.2025.112363), where increased cell size heightened sensitivity to the GPX4 inhibitor RSL3.

Original Weaknesses:

Disentangling cell size effects from other confounding factors, such as the cell cycle or overall metabolic rate, is challenging, and the authors have managed to qualitatively prove that cell size influences Era2-induced ferroptosis. However, the quantitative nature of this link between cell size and susceptibility to ferroptosis remains somewhat unclear due to the confounding factors that are present in many of their experiments. Notably, the quantitative nature of this link could also be cell type and growth condition -dependent, which remain to be investigated in detail. It should also be noted that this work focused on cell culture studies, and it remains unclear how much the findings of this paper could influence therapeutic strategies in vivo.

Comments on revised version:

I would first like to emphasize that I find this work solid, and I think the authors have done good work with the revisions.

My only remaining recommendation is that the authors aim to more carefully examine the magnitude of the observed cell size-dependency in ferroptosis susceptibility. Their manuscript contains several experiments where the quantitative nature of this link remains unclear due to confounding factors, such as the cell cycle. For example, in Fig 2B&C, it seems that accumulation of cells in G1 (from ~60% to ~95%) decreases ferroptosis equally to the effect caused by cell volume doubling (from day 2 to day 4 of palbo treatment), suggesting that cell cycle has a much more pronounced effect on ferroptosis than cell size (especially when considering the size change from day 0 to day 2). However, the magnitude of the cell size effect is not consistent between all experiments shown. This is not surprising, as the authors use different approaches to changing cell size and different cell lines, but it makes the work more qualitative than quantitative. Notably, another confounding factor is the cell's metabolic/biosynthetic rate. It seems reasonable to assume that prolonged palbociclib treatment will decrease metabolic and protein synthesis rates (normalized to cell size), and this could make the cells less susceptible to ferroptosis. The rapamycin treatment results shown by the authors also support this notion. One approach to examining this could be to grow cells in various growth conditions to manipulate their growth & metabolic rate.

Reviewer #2 (Public review):

Summary:

The authors set out to understand how cell phenotypes differ depending on the size of the cell, specifically here how cell size affects cell death. Using human cell lines (HMEC, HT-1080, RPE-1), the authors examined cell size through FACS sorting, CDK4/6 inhibition and inducible cyclin D1 knockdown. They identify that larger cells are more resistant to ferroptosis induced by system xc^- inhibition (erastin2), but more sensitive to GPX4 inhibition (RSL3), highlighting pathway-specific size dependencies.

Mechanistically, larger cells exhibited:

- Higher glutathione levels, supporting lipid peroxide detoxification

- Increased ferritin expression, promoting iron sequestration

- Lower ACSL4 levels, reducing incorporation of peroxidation-prone lipids

The findings are supported by high-throughput microscopy, flow cytometry (BODIPY-C11 lipid peroxidation assays), and proteomic analyses. The study concludes that cell size influences proteome composition and metabolic capacity, thereby shaping cell death decisions, an insight with implications for aging, cancer, and ferroptosis-based therapies.

Major Strengths:

- use of multiple cell lines to validate their findings

- use of multiple, complimentary approaches

- well designed screen and experiments throughout

- clearly written, logical flow and easy to follow

- relevance for multiple fields

Weaknesses:

- Lack of in-depth mechanistic investigation

- Experiments are all in vitro and so, as yet, it is uncertain what the in vivo consequence would be

General Assessment:

This study presents a mechanistic link between cell size and ferroptosis susceptibility. Using high-throughput microscopy, proteomics, and genetic perturbations across multiple human cell lines, the authors demonstrate that larger cells are more resistant to ferroptosis induced by system xc^- inhibition (erastin2). This resistance is attributed to elevated glutathione production, increased ferritin-mediated iron sequestration, and reduced ACSL4-dependent lipid peroxidation. The experimental design is rigorous and multifaceted, with consistent results across cell types and size manipulation methods. While the study is limited to in vitro systems, its conceptual and mechanistic insights lay the groundwork for future in vivo and translational investigations.

Advance:

This work is the first to systematically show that cell size directly influences ferroptosis susceptibility via proteome scaling. It reconciles previous findings that large cells are sensitized to GPX4 inhibition (RSL3) by demonstrating that the ferroptosis pathway targeted system xc^- vs GPX4 determines the direction of size-dependent vulnerability. The study provides a conceptual advance by positioning cell size as a regulatory axis in cell death decisions, and a mechanistic advance by identifying size-dependent changes in glutathione metabolism, ferritin levels, and ACSL4 expression.

Audience:

This research will be of interest to specialists in cell death, ferroptosis, redox biology, and cancer biology. It also holds relevance for aging researchers and translational scientists exploring ferroptosis-based therapies. The findings may influence how cell size heterogeneity is considered in therapeutic design, particularly in oncology and senescence-targeting strategies.

Comments on revised version:

We have no additional comments after revision. Thank you for addressing our initial queries.

Reviewer #3 (Public review):

In this manuscript, Zatulovskiy and colleagues elaborate on their previous work describing cell size-dependent changes in the proteome by investigating whether these changes can be correlated in differences in cell physiology. Using a cleverly-designed high throughput screen, they searched for compounds that differently-sized cells display differential sensitivity towards. Their primary hit, Era2, is involved in the ferroptosis pathway and serves as the starting point for a detailed study of how excess cell size protects cells from ferroptosis-induced cell death via: 1) lower concentrations of ACSL4 (which produces peroxidation-prone PUFAs), 2) increased ferritin concentrations, and 3) increased GSH concentrations.

Overall, the experiments in this manuscript are well-designed and interpreted. It is an extremely well-written manuscript with a clear trajectory of logic.

Comments on the revised version:

The authors have addressed my original concerns adequately. I do not need to see it again, if there are further revisions.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Senior Editor without further input from the original reviewers. The authors have moderated their claims and discussed the limitations of their experimental design more transparently. The previous reviews are included for reference.]

Comments on previous version:

The authors investigated tactile spatial perception on the breast using discrimination, categorization, and direct localization tasks. They reach four main conclusions:

(1) The breast has poor tactile spatial resolution.<br /> This conclusion is based on comparing just noticeable differences, a marker of tactile spatial resolution, across four body regions, two on the breast. The data compellingly support the conclusion; the study outshines other studies on tactile spatial resolution that tend to use problematic measures of tactile resolution, such as two-point-discrimination thresholds. The result will interest researchers in the field and possibly in other fields due to the intriguing tension between the finding and the sexually arousing function of touching the breast.

The manuscript incorrectly describes the result as poor spatial acuity. Acuity measures the average absolute error, and acuity is good when response biases are absent. Precision relates to the error variance. It is common to see high precision with low acuity or vice versa. Just noticeable differences assess precision or spatial resolution, while points of subjective equality evaluate acuity or bias. Similar confusions between these terms appear throughout the manuscript.

A paragraph within the next section seems to follow up on this insight by examining the across-participant consistency of the differences in tactile spatial resolution between body parts. To this aim, pairwise rank correlations between body sites are conducted. This analysis raises red flags from a statistical point of view. 1) An ANOVA and its follow-up tests assume no variation in the size of the tested effect but varying base values across participants. Thus, if significant differences between conditions are confirmed by the original statistical analysis, most participants will have better spatial resolution in one condition than the other condition, and the difference between body sites will be similar across participants. 2) Correlations are power-hungry, and non-parametric tests are power-hungry. Thus, the number of participants needed for a reliable rank correlation analysis far exceeds that of the study. In sum, a correlation should emerge between body sites associated with significantly different tactile JNDs; however, these correlations might only be significant for body sites with pronounced differences due to the sample size.

(2) Larger breasts are associated with lower tactile spatial resolution<br /> This conclusion is based on a strong correlation between participants' JNDs and the size of their breasts. The depicted correlation convincingly supports the conclusion. The sample size is below that recommended for correlations based on power analyses, but simulations show that spurious correlations of the reported size are extremely unlikely at N=18. Moreover, visual inspection rules out that outliers drive these correlations. Thus, they are convincing. This result is of interest to the field, as it aligns with the hypothesis that nerve fibers are more sparsely distributed across larger body parts.

(3) The nipple is a unit<br /> The data do not support this conclusion. The conclusion that the nipple is perceived as a unit is based on poor tactile localization performance for touches on the nipple compared to the areola. The problem is that the localization task is a quadrant identification task with the center being at the nipple. Quadrants for the areola could be significantly larger due to the relative size of the areola and the nipple; the results section seems to suggest this was accounted for when placing the tactile stimuli within the quadrants, but the methods section suggests otherwise. Additionally, the areola has an advantage because of its distance from the nipple, which leads to larger Euclidean distances between the centers of the quadrants than for the nipple. Thus, participants should do better for the areola than for the nipple even if both sites have the same tactile resolution.

To justify the conclusion that the nipple is a unit, additional data would be required. 1) One could compare psychometric curves with the nipple as the center and psychometric curves with a nearby point on the areola as the center. 2) Performance in the quadrant task could be compared for the nipple and an equally sized portion of the areola and tactile locations that have the same distance to the border between quadrants in skin coordinates. 3) Tactile resolution could be directly measured for both body sites using a tactile orientation task with either a two-dot probe or a haptic grating.

Categorization accuracy in each area was tested against chance using a Monte Carlo test, which is fine, though the calculation of the test statistic, Z, should be reported in the Methods section, as there are several options. Localization accuracies are then compared between areas using a paired t-test. It is a bit confusing that once a distribution-approximating test is used, and once a test that assumes Gaussian distributions when the data is Bernoulli/Binomial distributed. Sampling-based and t-tests are very robust, so these surprising choices should have hardly any effect on the results.

A correlation based on N=4 participants is dangerously underpowered. A quick simulation shows that correlation coefficients of randomly sampled numbers are uniformly distributed at such a low sample size. This likely spurious correlation is not analyzed, but quite prominently featured in a figure and discussed in the text, which is worrisome.

(4) Localization of tactile events on the breast is biased towards the nipple<br /> The conclusion that tactile percepts are drawn toward the nipple is based on localization biases for tactile stimuli on the breast compared to the back. Unfortunately, the way participants reported the tactile locations introduces a major confound. Participants indicated the perceived locations of the tactile stimulus on 3D models of these body parts. The nipple is a highly distinctive and cognitively represented landmark, far more so than the scapula, making it very likely that responses were biased toward the nipple regardless of the actual percepts. One imperfect but better alternative would have been to ask participants to identify locations on a neutral grey patch and help them relate this patch to their skin by repeatedly tracing its outline on the skin.

Participants also saw their localization responses for the previously touched locations. This is unlikely to induce bias towards the nipple, but it renders any estimate of the size and variance of the errors unreliable. Participants will always make sure that the marked locations are sufficiently distant from each other.

The statistical analysis is again a homebrew solution and hard to follow. It remains unclear why standard and straightforward measures of bias, such as regressing reported against actual locations, were not used.

Null-hypothesis significance testing only lets scientists either reject the null hypothesis or not. The latter does NOT mean the Null hypothesis is true, i.e., it can never be concluded that there is no effect. This rule applies to every NHST test. However, it raises particular concerns with distribution tests. The only conclusion possible is that the data are unlikely from a population with the tested distribution; these tests do not provide insight into the actual distribution of the data, regardless of whether the result is significant or not.

Reviewer #2 (Public review):

Summary:

The authors tested tactile acuity on the breast of females using several tasks.

Results:

Tactile acuity, assessed by just-noticeable differences in judging whether a touch was above or below a comparison stimulus, was lower on both the lateral and medial breast than on the hand and back. Acuity also scaled inversely with breast size, echoing earlier findings that larger hands exhibit lower acuity, presumably because a similar number of tactile receptors must be distributed over larger or smaller body surfaces. Observing this principle in the breast as on the hand strengthens the view that fixed innervation is a general organizing principle of the tactile system. Both methodology and analysis appear sound.

Most participants were unable to localize touch to a specific quadrant of the nipple, suggesting it is perceived as a single tactile unit. However, the study does not address whether touches to the nipple and areola are confused; conceptualizing the nipple as a perceptual (landmark) unit would suggest that such confusion should not take place. Aside from this limitation, the methodology and analysis appear sound.

Absolute touch localization, assessed by asking participants to indicate locations on a 3D rendering of their own torso, revealed a bias toward the nipple. The authors interpret this as evidence that the nipple serves as a landmark attracting perceived touch. However, as reviewers noted during review, alternative explanations cannot be fully ruled out: because the stimulus array was centered on the nipple, the observed bias may stem from stimulus distribution rather than landmark status. Aside from this caveat, the methodology and analysis appear sound.

Overall assessment:

The study offers a welcome exception to the prevailing bias in tactile research that limits investigation to the hand and arm. Its support for the fixed innervation hypothesis and its suggestion that the nipple may serve as a potential landmark-though requiring further scrutiny-illustrate the value of extending research to other body regions. By employing multiple tasks, the authors address several key aspects of tactile perception and create links to earlier findings.

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 rounds of review.]

Giordano et al. demonstrate that yeast cells expressing separated N- and C-terminal regions of Tfb3 are viable and grow well. Using this creative and powerful tool, the authors effectively uncouple CTD Ser5 phosphorylation at promoters and assess its impact on transcription. This strategy is complementary to previous approaches, such as Kin28 depletion or the use of CDK7 inhibitors. The results are largely consistent with earlier studies, reinforcing the importance of the Tfb3 linkage in mediating CTD Ser5 phosphorylation at promoters and subsequent transcription.

Notably, the authors also observe effects attributable to the Tfb3 linker itself, beyond its role as a simple physical connection between the N- and C-terminal domains. These findings provide functional insight into the Tfb3 linker, which had previously been observed in structural studies but lacked clear functional relevance. Overall, I am very positive about the publication of this manuscript.

Reviewer #2 (Public review):

Summary:

This work advances our understanding of how TFIIH coordinates DNA melting and CTD phosphorylation during transcription initiation. The finding that untethered kinase activity becomes "unfocused," phosphorylating the CTD at ser5 throughout the coding sequence rather than being promoter-restricted, suggests that the TFIIH Core-Kinase linkage not only targets the kinase to promoters but also constrains its activity in a spatial and temporal manner.

Strengths:

The experiments presented are straightforward and the model for coupling initiation and CTD phosphorylation and for evolution of these linked processes are interesting and novel. The results have important implications for the regulation of initiation and CTD phosphorylation.

Reviewer #3 (Public review):

Summary:

Eukaryotic gene transcription requires a large assemblage of protein complexes that govern the molecular events required for RNA Polymerase II to produce mRNAs. One of these complexes, TFIIH, comprises two modules, one of which promotes DNA unwinding at promoters, while the other contains a kinase (Kin28 in yeast) that phosphorylates the repeated motif at the C-terminal domain (CTD) of the largest subunit of Pol II. Kin28 phosphorylation of Ser5 in the YSPTSPS motif of the CTD is normally highly localized at promoter regions, and marks the beginning of a cycle of phosphorylation events and accompanying protein association with the CTD during the transition from initiation to elongation.

The two modules of TFIIH are linked by Tfb3. Tfb3 consists of two globular regions, an N-terminal domain that contacts the Core module of TFIIH and a C-terminal domain that contacts the kinase module, connected by a linker. In this paper, Giordano et al. test the role of Tfb3 as a connector between the two modules of TFIIH in yeast. They show that while no or very slow growth occurs if only the C-terminal or N-terminal region of Tfb3 is present, near normal growth is observed when the two unlinked regions are expressed. Consistent with this result, the separate domains are shown to interact with the two distinct TFIIH modules. ChIP experiments show that the Core module of TFIIH maintains its localization at gene promoters when the Tfb3 domains are separated, while localization of the kinase module, and of Ser5 phosphorylation on the CTD of Pol II, is disrupted. Finally, the authors examine the effect of separating the Tfb3 domains on another function of TFIIH, namely nucleotide excision repair, and find little or no effect when only the N-terminal region of Tfb3 or the two unlinked domains are present.

Strengths:

Experiments involving expression of Tfb3 domains in yeast are well-controlled and the data regarding viability, interaction of the separate Tfb3 domains with TFIIH modules, genome-wide localization of the TFIIH modules and of phosphorylated Ser5 CTDs, and of effects on NER, are convincing. The experiments are consistent with current models of TFIIH structure and function and support a model in which Tfb3 tethers the kinase module of TFIIH close to initiation sites to prevent its promiscuous action on elongating Pol II.

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 carefully considered all the reviewers' comments. The newly added analyses, figures, and text sections are of high quality, and we commend the authors for their in-depth revision of the manuscript.]

This manuscript presents a high-quality, chromosome-level genome assembly of the European cuttlefish (Sepia officinalis), a representative species of the cephalopod lineage. Using state-of-the-art sequencing and scaffolding technologies -including PacBio HiFi long reads and Hi-C chromatin conformation capture - the authors deliver a genome assembly with exceptional contiguity and completeness, as evidenced by high BUSCO scores. This genome resource fills a significant gap in cephalopod genomics and offers a valuable foundation for studies in neurobiology, behavior, and evolutionary biology. However, there are several major aspects that need to be strengthened.

Reviewer #2 (Public review):

This paper concerns an interesting organism, Sepia officinalis. However, in the opinion of this reviewer, the paper reads somewhat like a genome report. The authors have used 23x PacBio HiFi in conjunction with relatively low coverage (11x) Hi-C to scaffold the genome into a karyotype of 47 chromosomes. They have used a combination of short and long read RNA seq to annotate the genome in what looks like a very good annotation. The paper offers basic analyses of the Busco evaluation, some descriptive analyses of gene family and repeat content, and a bit more focused analysis on synteny among sequenced squids. Generally, the data will be useful.

Reviewer #3 (Public review):

Summary:

In this study, authors Simone Rencken and co-authors present and investigate the genome of the common cuttlefish Sepia officinalis.

Strengths:

The authors explain in a detailed yet concise manner the main steps for a genome assembly, with very robust methods for validation, and according to current best practices. In addition to the chromosomal assembly, the authors confirmed the presence of 47 chromosomes using Hi-C data and multiple species synteny. They also generated a comprehensive gene annotation, with assessments of gene completeness, providing a useful resource for the community of researchers interested in cuttlefish biology and comparative genomics.

Reviewer #1 (Public review):

Summary:

This manuscript by Alonso-Caraballo et al, is a novel piece of work that examines the impact of oxycodone self-administration on neural plasticity within paraventricular thalamic (PVT) to nucleus accumbens shell (Shell) pathway - two regions shown to play a key role in cue-induced drug seeking on their own, and whether this plasticity varies based on abstinence period and biological sex.

Strengths:

The authors show using a clinically relevant long-access model of opioid self-administration promotes dependence and acute withdrawal in both male and female rats. During subsequent cue-induced relapse tests at 1 or 14-days following the conclusion of self-administration, data show that while both male and females demonstrate drug-seeking behavior at both time points, females show a further elevation in responding on day 14 versus day 1 that is not observed in the males. When accounting for past work showing elevations in drug seeking in males after 30 days, these data indicate that craving-induced relapse for opioids may develop faster and may be more pronounced in females compared to males.

These behavioral findings were paralleled by use of ex vivo acute slice electrophysiology and circuit-specific ex vivo optogenetics to examine the impact of oxycodone self-administration on synaptic strength within the paraventricular thalamus (PVT) to nucleus accumbens shell (NAcSh) pathway(s). Data support a time-dependent but sex independent strengthening of glutamatergic signaling at PVT-to-NAcSh medium spiny neurons (MSNs) that is only present following a relapse test at 14 days post abstinence in males versus females, providing the first evidence that opioid self-administration and/or cue-induced drug-seeking augments this pathway. Using an extensive set of physiological measures, the authors show that this increased synaptic strength reflects a upregulation of presynaptic release probability. Further, this upregulation of excitatory signaling aligned temporally with an increase in MSN excitability, as assessed by increases in action potential firing frequency. Finally, the authors provide the first evidence that similar to other inputs to the NAcSh, PVT projections innervate both MSN as well as local interneurons, promoting a GABA-A specific feedforward inhibitory circuit. Interestingly, unlike direct excitatory inputs to MSNs, no changes were observed ostensibly within this feedforward circuit, highlighting a selective enhancement of excitatory drive and output of MSNs with protracted abstinence.

Overall, these data highlight a potential role for heightened synaptic strength within the PVT-NAcSh pathway in cue-induced relapse behavior during protracted abstinence and identify a potential therapeutic target during abstinence to reduce relapse risk in abstaining individuals.

Weaknesses:

Overall, the experimental approach and data provided appear rigorous and support their overall conclusions and achieve their goal of understanding how opioid self-administration impacts synaptic strength within the PVT-NAcSh pathway. Although not undermining these data, there are a few potential weaknesses that reduce the impact of the work. For example, the inability to directly assess whether cue-induced drug-seeking is in fact augmented compared to daily intake during self-administration in the maintenance face only permits the authors to denote that reexposure to cues and the context is sufficient to promote active lever pressing without demonstrating whether seeking behavior is in fact elevated further during a cue test. This is notably understandable as drug available sessions were 6-hours versus a 1hour relapse test. Importantly, it is clearly demonstrated that drug seeking is higher on average in female mice after 14 days versus 1 day.

With regard to interpretation of electrophysiology findings, the lack of inclusion of an abstinence only group does not permit interpretations to parse out whether observed increases in synaptic strength (or the lack of) reflect abstinence or an interaction between abstinence period and re-exposure to the operant chamber, as slices were taken 30-45 min post relapse test. While much literature has shown that drug induced adaptations in the NAc requires a post drug period for plasticity to measurably emerge, studies have also shown that re-exposure to heroin-associated cues following abstinence seemingly "reverses" increases in cell excitability in prelimbic-NAc pyramidal neurons (Kokane et al., 2023) and that depotentiation of morphine-induced increases in synaptic strength in the NAc shell can be depotentiated by drug re-exopsure -- an effect also observed with cocaine re-exposure (Madayag et al., 2019). Notably, the lack of effect at 14 but not 1 day supports the likelihood that the relapse test does not in fact influence the plasticity within the PVT-NAcSh circuit.

While the lack of effect on AMPAR:NMDAR ratio and rectification indices do support the notion that enhanced EPSC amplitudes in input-output curves do not reflect a change in AMPAR subunit expression (i.e., increased GluA2-lacking receptors that exhibit inward rectification at depolarized potential) nor a change in postsynaptic sensitivity to glutamate, without direct assessment of AMPAR-specific and NMDAR-specific input-output curves, it doesn't definitively exclude the possibility that both AMPA and NMDA receptor currents are being upregulated, thus negating an observable change in postsynaptic strength.

Overall, these findings provide novel insight into how the PVT-NAcSh pathway is altered by opioid self-administration and whether this is unique based on abstinence period and sex. Importantly, these were the primary objectives stated by the author. Data highlight a potential role for the observed adaptations in relapse behavior and identify a potential therapeutic target during abstinence to reduce relapse risk in abstaining individuals. However, it should be noted that no causal link is demonstrated without experiments to reduce/prevent relapse.

Comments on revisions:

The authors addressed previous concerns brought up, specifically by clarifying data interpretation as well as text modifications related to potential caveats of these interpretations. However, I recommend that the title be changed to not focus on sex differences to avoid misunderstanding. The authors should also address the lack of difference physiologically compared to the behavior as a caveat more clearly in the discussion (i.e. likely suggests this isn't the pathway driving the difference).

Reviewer #2 (Public review):

Summary:

This is an interesting paper from Alonso-Caraballo and colleagues that examines the influence of opioid use, acute and prolonged abstinence, and sex on cue-induced relapse and paraventricular thalamus (PVT) to nucleus accumbens shell (NAcSh) medium spiny neurons circuit physiology. The study presents a valuable finding that following prolonged, but not acute abstinence from oxycodone self-administration, female rodents exhibit higher relapse rates to drug paired cues. Additionally, the study presents the useful finding that prolonged abstinence increased PVT-NAcSh MSN synaptic strength in both sexes, an effect that is likely due to presynaptic adaptations. While the evidence to support these two findings is solid, further experiments are required to determine the functional role of the PVT-NAcSh MSN circuit in relapse following prolonged oxycodone abstinence, and the mechanism underlying the heightened relapse vulnerability in females in this model of opioid use disorder.

Strengths:

The paper is interesting, well written and presented, and the experiments are well designed and conducted. The revised analysis of spike count data that models the hierarchical structure of the data is appropriate to overcome low animal numbers and the potential for oversampling. The authors are transparent in reporting the results related to this analysis in figure 5 and acknowledge the study is underpowered to confirm the trend of increased intrinsic excitability in male MSNs following prolonged oxycodone analysis.

Weaknesses:

A major weakness of this study is the disconnect between the behavioral and neurophysiological data reported. While a striking sex difference in relapse-like behavior is observed, there are no statistically significant sex differences in any of the neurophysiological data reported. Moreover, without an experiment to functionally test the role of the PVT-NAc projection in relapse-like behavior following prolonged oxycodone these two arms of the study seem divorced.

While the authors don't directly conclude that the PVT-NAc MSN circuit is required for relapse following prolonged oxycodone abstinences, in the introduction the authors state they aim to test the hypothesis that increased synaptic strength in PVT-NAcSh projections are necessary for drug-seeking. This study does not include the required experiments to test this hypothesis.

Impact:

The topic is of interest to the field of substance use disorders and gives solid evidence for the need to consider targeted therapeutics aimed at relapse prevention in opioid use disorder.

Reviewer #3 (Public review):

Summary:

Alonso-Caraballo et al. use behavioral testing and ex vivo patch-clamp electrophysiology combined with circuit-specific optogenetic stimulation of PVT terminals to examine how oxycodone self-administration and abstinence duration shape cue-induced relapse and PVT-NAcSh synaptic transmission in male and female rats. In the revision, the authors reanalyzed intrinsic excitability using nested hierarchical GLMMs, acknowledged the low power in the male prolonged-abstinence group, and expanded the discussion of relevant PVT-NAc literature. These changes improve the manuscript. That said, most of the revisions are textual and the main experimental gap remains. Both sexes show increased oxycodone seeking compared to saline at 14 days, but only females show a time-dependent incubation from 1 to 14 days, and the PVT-NAcSh synaptic strengthening is the same in both sexes. Nothing in the revision brings those two observations closer together. The excitability data also come from NAcSh MSNs with no confirmation of PVT connectivity, which limits what circuit-specific conclusions can be drawn. The study is a solid characterization of abstinence-related synaptic changes in this pathway, but some of the conclusions still go further than the data allow.

Strengths:

The behavioral characterization is thorough and well-executed, covering self-administration, somatic withdrawal, and cue-induced relapse across two abstinence durations in both sexes. The sex-specific escalation in oxycodone seeking from 1 to 14 days in females but not males is a clear and compelling finding. The use of circuit-specific ex vivo optogenetics to isolate PVT terminal inputs onto NAcSh neurons is a genuine methodological strength, and the demonstration of feedforward inhibitory recruitment through local GABAergic interneurons adds meaningful novelty to the circuit characterization. The reanalysis of intrinsic excitability using nested hierarchical GLMMs appropriately accounts for the non-independence of cells recorded within the same animal and is a real improvement over the original approach. The expanded discussion of prior PVT-NAc work, particularly the more accurate treatment of Keyes et al. (2020) and Paniccia et al. (2024), better situates the findings within the existing literature.

Weaknesses:

The core limitation of the study remains unchanged after revision. The PVT-NAcSh synaptic strengthening after prolonged abstinence is statistically indistinguishable between sexes, while females but not males show a time-dependent escalation in oxycodone seeking from 1 to 14 days of abstinence. The Discussion proposes hormonal modulation or differences in upstream inputs as possible explanations, but none of these are tested and the gap is left unresolved. The intrinsic excitability recordings come from NAcSh MSNs with no confirmation that those neurons receive direct PVT input, which was raised in the original review, acknowledged in the revision, and not experimentally addressed. The male prolonged-abstinence excitability trend has approximately 20% statistical power and is non-significant, yet the Discussion interprets it as a potential neuroadaptation that could facilitate signal flow through the PVT-NAcSh circuit and contribute to relapse, which goes well beyond what the data support. The failure to distinguish between D1 and D2 MSNs remains a significant limitation given that cell-type-specific plasticity at PVT-NAc synapses has been shown to be directly relevant to opioid seeking in prior work. Finally, the Conclusion builds a mechanistic framework around D2 MSNs, PV interneurons, and D1 MSNs that is drawn from studies using different drugs or experimental designs, and none of these cell-type-specific mechanisms are tested in the present experiments.

Reviewer #1 (Public review):

The manuscript by Ho and Schock investigates the role of the Z-disc protein Zasp52 during Drosophila flight muscle development. It was known before, mainly by findings from this group, that Zasp52 is required for normal sarcomere morphogenesis, specifically Z-disc morphogenesis in indirect flight muscles. But the exact molecular mechanism by which Zasp52 contributes, apart from the fact that it is localised there and is somehow involved in multimerization/cross-linking, was not clear. This paper proposes that an intrinsically disordered region (IDR) in Zasp52 is needed for some of its functions, by stabilising Zasp52 localisation at the Z-disc. Specifically, the IDR in Zasp52 is proposed to be required for Z-disc maintenance during the mechanical challenges of flight, while being dispensable for the initial morphogenesis during development. This hypothesis is supported by strong genetic evidence and behavioural tests, deleting Zasp's IDR impairs flight from mid-age onwards, while a block in flight activity lifts the phenotype.

However, some of the phenotypic analysis, in particular the bending of the sarcomere, likely upon mechanical challenge by muscle contractions, needs more detailed investigations to be fully convincing.

Strengths:

(1) The linker in the alternatively spliced exon 15 of Zasp52 was deleted with a state-of-the-art genetic editing strategy. Surprisingly, flies are homozygous viable, showing that this long part of the Zasp52 protein is not essential for animal survival or sarcomere morphogenesis.

(2) The observed sarcomere phenotypes with age, especially the bending Z-discs, are new and exciting.

(3) The displayed EM images document interesting phenotypes.

(4) Most of the observed phenotypes can be rescued by re-expression of the long Zasp52 isoform, which does contain the IDR region, but not by a shorter one without it, suggesting that IDR is important.

(5) FRAP data measure the local turnover of a short-ZaspGFP and show that this increased in the Zasp mutant lacking the IDR domain, suggesting that Zasp-IDR might stabilise Zasp at the Z-disc.

(6) Interestingly, flight and sarcomere morphology phenotypes can be rescued by preventing the flies from flying, suggesting that they are mechanically induced.

Weaknesses:

(1) The western blot quantifications of Zasp isoform expression are weak. No error bars are indicated in the quantifications; the quantifications appear to be more qualitative than quantitative. According to band intensities, the long Zasp isoforms seem to be less present compared to the shorter ones, even in the flight muscles.

(2) The phenotypic analysis of the sarcomere appears somewhat superficial throughout the paper. Only Zasp52 and phalloidin are shown; no other Z-disc or thick filament proteins. At least myosin stainings and overview images are important to better judge the phenotypic variations. Are the variants between individuals or regional in the same muscle?

(3) EM images would benefit from better quantification.

(4) Other proteins were not analysed with the FRAP-based turnover assay for comparison in wild type and mutant. All Z-proteins might turn over faster in the mutant with the defective Z-disc.

Reviewer #2 (Public review):

Summary and Strengths:

This in-depth genetic analysis of Zasp52 function in Drosophila indirect flight muscle (IFM) provides an interesting perspective regarding the role of a partially disordered region (IDR) in exon 15e. This exon seems to be exclusively present in IFM and contributes to the prevention of myofibril disintegration during aging, likely due to interactions of this region with Z-disc insertion and/or stability. The addition of an isoform (PR) that lacks exon 15e serves as a nice control to illustrate the necessity of exon 15e in muscle structure and function. Overall, the manuscript is exceptionally well-written, logical, with nicely controlled experiments and detailed statistical analysis that largely support the conclusions drawn by the authors. While exon 15e is clearly involved in preventing muscle degeneration, a solid role for thin filament stability is not clearly shown (as mentioned in the abstract). In addition, which regions/how the proteins of the IDR may contribute are unclear.

Weaknesses:

(1) It is not clear in Figure S1A where exon 15e fits within the Zasp52 locus schematic. This is important as a premise of this paper describes this region to be key, and proof from multiple prediction programs would lend more weight to the prediction of the exon being largely disordered. Inclusion of the discussed short linear motifs, comparison with Canoe or LBD3 for similarities and/or an Alphafold structure would help make the authors' point (colorized with known domains).

(2) Interesting that immobilization rescues the deterioration phenotypes. The authors should explain in more detail how this was done to avoid dehydration/starvation of the flies.

(3) There is a lot of discussion about the potential function of the IDR region, specifically a putative actin binding motif or other 'ordered' regions that may contain short linear motifs. It would strengthen the findings to show which of these may be essential for Zasp52 function in the IFM. The ability to bind actin could be tested biochemically, and/or smaller deletions could be made to unequivocally test the role of the ABD vs other predicted motifs using genetics. If some of these regions are more ordered, where do they lie within, and do they form a predicted fold or structure that gives insight into function?

Reviewer #1 (Public review):

The study by Escamilla del Arenal et al. utilized a conditional knockout mouse model to study the role of Mex3a in immature olfactory sensory neurons (OSN). Mex3a is a dual-functional protein that has RNA-binding function and ubiquitin-E3 ligase activity. The results revealed that Mex3a expression is critical for proper OSN differentiation and contributes to cell surface protein trafficking and translation, cilia structure, and planar cell polarity in mature neurons. Moreover, Mex3a enforces lineage fidelity, selectively repressing sustentacular programs in neurons and neuronal programs in sustentacular cells.

In addition, the authors established an in vivo HyperTRIBE mouse model to identify Mex3a RNA targets and incorporated UbiFast into the Mex3a conditional knockout (cKO) model to find its protein targets to investigate how Mex3a regulates OSN differentiation. The experimental systems are laborious and comprehensive, which allowed the authors to identify new Mex3a putative targets in OSN.

The phenotypic results derived from the conditional Mex3a cKO mice are solid. Mechanistic findings also revealed that, in addition to facilitating protein degradation, Mex3a may confer K27 ubiquitin linkage on its target proteins, which has a non-proteolytic role but affects target protein activity, other post-translational modifications, or protein-protein interactions. However, among all Mex3a putative targets, the authors decided to emphasize on the Mex3a-mediated K27 ubiquitination on stress granule protein Serbp1 and ribosome protein Rps7, and the association between Mex3a expression and Serbp1 and p-eEF2 ribosome recruitment. This Mex3a-Serbp1-p-eEF2 ribosome recruitment axis, although it can be important in Unfolded Protein Response (UPR) signaling, seems rather general and cannot explain the striking lineage-specific phenotypes observed in the mouse model. The authors need to provide more solid evidence to demonstrate that K27-Ubiquitinylation of Serbp1 is a key step of Mex3a function in OSN differentiation to strengthen the relation between the phenotypes and mechanism presented in this study.

Reviewer #2 (Public review):

Summary:

In this manuscript, Arenal and colleagues demonstrate that loss of Mex3a leads to defects in cell surface protein trafficking, translation, ciliary structure, and planar cell polarity in mature neurons. Through proteomic analyses, the authors show that Mex3a depletion alters the abundance of proteins involved in vesicular transport, lipid metabolism, and ribosome biogenesis. Using the HyperTRIBE approach, the authors further identify targets of Mex3a and provide evidence supporting a role for K27-linked ubiquitination in regulating these substrates. Mechanistically, the study suggests that Mex3a levels influence the recruitment of SERBP1 and phosphorylated eEF2 (p-eEF2) to ribosomes, contributing to translational repression.

Strengths:

Overall, this is a very interesting and well-written manuscript that significantly advances our understanding of Mex3a function and its role in neuronal development, particularly in olfactory sensory neurons. The data are clearly presented and thoughtfully interpreted.

Weaknesses:

I have a few minor comments that may further strengthen the manuscript and improve its accessibility to a broader readership.

(1) In Figure 3B, the authors describe Mex3a localization to cytoplasmic granules. However, it is unclear how these compartments were defined. It would strengthen the conclusions if the authors included co-localization experiments using established cytoplasmic granule markers (e.g., stress granule markers) to define the identity of these structures more precisely. This would clarify whether Mex3a associates with stress granules, RNA processing bodies, or another class of ribonucleoprotein granules.

(2) Functional validation of K27-linked ubiquitination on SERBP1<br /> To further define the functional significance of K27-linked ubiquitination, it would be informative to mutate the relevant lysine residue(s) on SERBP1 and examine whether this alters its recruitment to ribosomes or affects translational repression. Such an experiment would provide more direct evidence that K27-linked ubiquitination of SERBP1 mediates the observed translational effects.

(3) Discussion of vesicular trafficking and lipid metabolism targets<br /> The identification of Mex3a targets involved in vesicular trafficking and lipid metabolism, including COPII coat components such as Sec31a and lipid regulatory proteins such as Sec14 and PIP5K1A, is particularly intriguing. The authors may wish to expand the Discussion to address how regulation of these proteins could contribute to defects in plasma membrane trafficking and planar cell polarity. Integrating these findings with the observed cell surface trafficking phenotypes would further enhance the mechanistic framework of the study.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors investigate the role of the KH and RING domain-containing protein Mex3a in the differentiation and maturation of olfactory sensory neurons. Using conditional knockout of Mex3a in immature neurons, they show that mature olfactory sensory neurons display defects in membrane protein trafficking, including olfactory receptors and Adcy3, together with abnormalities in ciliary radial organization and planar cell polarity. Through single-cell RNA sequencing and quantitative proteomics, the authors further show that Mex3a-deficient neurons fail to properly resolve the unfolded protein response and exhibit transcriptomic features suggestive of lineage mixing with sustentacular cells. The study also introduces a methodological advance by adapting HyperTRIBE for use in transgenic mice, which enables the identification of in vivo Mex3a RNA targets, including components of Wnt signaling that appear to be under translational repression by Mex3a. The authors then pursue one of these targets to further explore the role of Mex3a in translational repression.

Strengths:

First, it addresses an important biological and conceptual question. Mex3a is a multifunctional protein with the potential to couple RNA regulation, protein homeostasis, and key cellular processes, yet its in vivo role in neuronal differentiation remains poorly understood. By focusing on Mex3a in olfactory sensory neurons, the manuscript asks a timely and important question of how post-transcriptional regulation contributes to the maturation of highly specialized neurons, including the establishment of ciliary architecture, membrane protein trafficking, and cell polarity. Second, the generation and validation of an inducible in vivo mouse HyperTRIBE system represents a technical advance. By incorporating the Adar deaminase domain into a transgenic mouse model, the authors establish a rigorous and useful approach for identifying Mex3a RNA targets in vivo, which is likely to be valuable to the wider RNA biology community. Third, the study integrates the Mex3a knockout model with single-cell RNA sequencing, quantitative mass spectrometry-based proteomics, ubiquitin profiling, and ribosome-related analyses, providing a broad and multilayered view of the Mex3a knockout phenotype. Finally, the imaging analyses revealing altered ciliary content and organization in olfactory sensory neurons identify an interesting and potentially important link between Mex3a, cilia biology, and vesicular trafficking. More broadly, the manuscript reflects a very substantial experimental effort, and each individual dataset has the potential to be useful for the field.

Weaknesses:

A main weakness of the manuscript is that the mechanistic links between the major findings remain somewhat correlative, and the biological narrative is not fully sustained through the later figures. The study documents defects in membrane trafficking, ciliary radial organization, and planar cell polarity, and it identifies candidate targets with clear relevance to these processes, including factors linked to vesicle trafficking. However, the manuscript then shifts its mechanistic focus toward translational regulators such as Serbp1 and Rps7, without adequately connecting these later analyses back to the core phenotypes established earlier. As a result, there is a noticeable disconnect between the phenotypic emphasis of the study and the mechanistic validation that follows.

A second weakness is that, given the breadth and potential importance of the datasets generated, validation remains limited for several of the major conclusions. This reduces confidence in the interpretation of the single-cell, proteomic, ubiquitin-related, and ribosome-associated analyses, and also limits the future value of these datasets as a resource for the field. Because the manuscript aims to address several major questions at once, stronger validation and clearer integration across the different experimental arms are needed for the conclusions to feel fully supported.

Finally, the HEK293T overexpression experiments are less solid than the in vivo analyses and do not provide equally strong support for the proposed mechanisms. In this context, some of the observed effects on cytoskeletal organization, membrane-less granule formation, and ribosome profiles may be indirect, which makes it difficult to weigh these findings alongside the much stronger in vivo phenotypes.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The revised version adequately addresses the relatively minor comments from the previous round of review.]

Summary:

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

Strengths:

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

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

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

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

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

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

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

Reviewer #1 (Public review):

Summary:

The authors describe a new database that rigorously explores protein conformations.

Strengths:

It is extremely well done, using state-of-the-art tools by a group at the top of the field of structural modeling. The evaluation of qualities and the benchmarking of the structures are outstanding, and it is expected that the new database will have a significant impact on the field.

Weaknesses:

The authors are using MD simulation to generate some of the structure, and therefore should have access to standard MD energies. I am surprised that no evaluation is provided based on these energies that can be extended to free energies.

Reviewer #2 (Public review):

Summary:

The authors developed a dataset of protein conformations by running molecular dynamics simulations starting from both native and decoy conformations for a large number of proteins. These conformations were put together as a dataset for querying and downloading, along with their energies under different force fields. The authors suggest that such conformations represent the proteins' conformational landscape, so that they will be useful for evaluating methods generating multiple conformations of proteins.

Strengths:

The dataset is online and working. It has good documentation for others to use.

Weaknesses:

The biggest weakness is that the collected conformations very likely do not represent the true conformational landscape. To represent the conformational landscape, the structures need to be sampled based on the Boltzmann distribution. However, in this study, conformations are generated by running very short (125ps to 375ps) MD simulations starting from near-native conformations and decoys. Such short simulations will produce small fluctuations around the starting conformations, so the distribution of conformations is largely dominated by the distribution of the initial conformations, which by one means are Boltzmann distributed. A conformation might be physically plausible, but it might have very small weight in the Boltzmann distribution. On the other hand, conformations with large weights might not be in the dataset.

Reviewer #3 (Public review):

Summary:

This manuscript describes a web-based tool that allows researchers to compare large numbers of representative ("plausible") conformations of proteins. It also includes energetic analysis from multiple widely used structure-prediction methods.

Strengths:

This tool will likely be useful for students who want to learn more about the ensemble properties of proteins. The resource is well organized and it represents a large amount of computing resources.

Weaknesses:

It is not entirely clear how the database may be utilized by other groups to advance research. It could be helpful if the authors add a short section that provides example use cases that illustrate how this database can support new strategies for studying protein dynamics.

Reviewer #1 (Public review):

Summary:

In this manuscript from the Levy lab, the authors investigate whether SETD6 regulates hepatic lipid accumulation through direct methylation of PPARγ. They show that SETD6 binds and mono-methylates PPARγ at K170, and provide evidence that this modification enhances PPARγ occupancy at target promoters, promotes expression of lipid metabolism genes, as well as facilitates lipid droplet accumulation in HepG2 cells. The authors also find a positive feedback loop or circuit in which PPARγ activates SETD6 transcription in a methylation-dependent manner, thereby reinforcing this lipogenic program. Overall, the work presents a novel SETD6-PPARγ regulatory axis linking lysine methylation to transcriptional control of lipid storage genes, with possible relevance to NAFLD-associated biology.

In all, I find this to be an important paper that describes and advances a new regulatory pathway that has significance to human health and disease. It would also be of interest to a broad audience. That said, there are also some concerns that the authors should address, as outlined below.

Major concerns (pertains to rigor - highest priority)

(1) Overall, the work presented is of high quality, and the data nicely support the conclusions; however, a few panels should be strengthened that have missing controls or information:<br /> a. The co-IP panel in Figure 1B lacks a lane where HA SETD6 is expressed without PPARγ. This control is needed to verify that the SEDT6-HA signal depends on PPARγ.<br /> b. In Figure 1C, the authors should show that the co-IP works in both directions (include IP for PPARγ/blot for SETD6). I am a bit confused also over the labeling with IP on the left and on top of the panel next to the beads label. More importantly, the data would be stronger if the authors took advantage of a deletion line to validate that the co-IP is specific to the presence of both.<br /> c. The same IP labeling issue exists for Figure 3B (label is on the same and on top).<br /> d. Antibody information (e.g., where the pan-methyl Ab comes from and at what dilutions they are used at) is missing.

Nice to have experiments (medium priority - strongly consider)

(2) A missing gap is how K170me1 contributes to DNA binding and gene transcription. One possibility is that methylation enhances the DNA-binding activity of PPARγ. Given that the authors have all of the reagents, it would be possible to perform a gel shift assay (or other approach) with and without SETD6-mediated methylation. Is DNA binding affected/enhanced?

(3) Along these lines, I wonder if there is another possibility: could SETD6-mediated methylation of PPARγ drive SETD6-PPARγ interaction? In other words, in the K170R, is SETD6 still even associated with PPARγ, and this interaction is required for promoter recruitment? Alternatively, would a catalytic dead version of SETD6 fail to associate with PPARγ? Currently, no experiments test the impact of an unmethylatable version of PPARγ or a catalytic dead version of SETD6 on SETD6-PPARγ interaction or SETD6 recruitment to promoters.

Minor concerns (text and figure display)

(4) The text has multiple typos and grammatical errors, and there are some issues with the figure display.

Reviewer #2 (Public review):

Summary:

In this work, the authors investigated the regulation of the transcription factor PPARγ by the post-translational modification lysine methylation. The data demonstrate that the lysine methyltransferase SETD6 targets PPARγ for methylation using biochemical and cell-based assays. Methylation of PPARγ occurs in its DNA binding domain, and the authors demonstrate that loss of methylation limits PPARγ chromatin binding, particularly to lipid storage and metabolism gene promoters. As a physiological output, the authors demonstrate that deletion of SETD6 and loss of PPARγ methylation also disrupt lipid droplet accumulation in hepatocytes. In addition, the authors uncover a positive feedback loop in which SETD6 methylation of PPARγ also regulates its binding to the SETD6 promoter and expression of the gene.

Strengths:

One of the key strengths of this manuscript is the novelty of the findings in terms of identifying a new mode of regulation of PPARγ that modulates its chromatin association in cells and thereby regulates lipid metabolism genes. The authors nicely combine biochemical studies of SETD6 activity with cell-based assays investigating PPARγ and SETD6 function in regulating lipid storage. Data supporting this conclusion is largely convincing, and frequently, multiple assays are used to provide sufficient support to the conclusions. This work therefore expands regulatory modes of PPARγ and identifies a new target for SETD6, an enzyme that targets a number of other transcription factors. Furthermore, the regulatory loop that controls SETD6 expression via PPARγ methylation is likely important for understanding SETD6 function in different cell types that have high levels of lipid accumulation or regulation. The gene expression and lipid accumulation assays are useful for testing the physiological outcome of loss of SETD6 activity or PPARγ methylation directly.

Weaknesses:

The data presented in the manuscript are largely convincing in support of the authors' conclusions; however, there are some errors in the presentation of the figures and some issues in the text that would benefit from editing. Furthermore, there are some important questions not fully addressed in the results or discussion. It would be great if the authors could speculate more on the diverse roles of SETD6 in methylated transcription factors and/or provide more context regarding the conditions that are likely to support methylation of PPARγ by SETD6. Also, while a potential cross-talk between methylation and phosphorylation is described in the discussion, it would be great to provide more structural insight into how this might regulate DNA binding of PPARγ and/or discuss whether there are other possibilities given the location of the target lysine in the DNA binding domain.

Reviewer #1 (Public review):

Summary:

In this manuscript, Yang et al expand on their previous work showing that platelet recruitment to the liver via liver macrophages is important for APAP-induced liver injury. Here, they show that platelets induce a glycolytic switch in liver non-parenchymal cells, including Kupffer cells, and that this is mediated by the protein Aldolase A produced by platelet-derived extracellular vesicles (PEV). They show that targeting Aldolase A may be a valid therapeutic strategy for severe APAP injury.

Strengths:

(1) They nicely showed that platelet effects in APAP are mediated by Aldoa via platelet-derived extracellular vesicles.

(2) Their data show that one of the effects of platelets in APAP liver injury is inducing metabolic switch to the glycolytic pathway, including in KCs.

(3) Their data points to the therapeutic potential of targeting ALDOA in severe APAP liver injury.

Weaknesses:

(1) They have not shown that the platelet-induced glycolytic switch is only in KCs.

(2) They also have not shown that KC's role in APAP injury is primarily mediated by their interaction with platelets and the subsequent glycolytic switch.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors have investigated the role of platelet-derived ALDOA in liver injury induced acetaminophen (APAP) induced acute liver injury. There are some major flaws in data interpretation as described below. While a decrease in liver injury due to platelet depletion and lower injury in platelet-specific ALDOA KO mice seems real, the claims related to EVs and Platelet-KC crosstalk are not well supported.

Strengths:

Core findings are interesting and supported by the data

Weaknesses:

(1) At least two additional timepoints, one at 6 hr and another at 24 hr should be performed in the APAP model to better understand the dynamics of liver injury, especially after platelet depletion.

(2) Interpretation of the experiments in Figure 2 with clodronate is flawed. 2-DG pretreatment and CLDN administration alone both seem to decrease liver injury substantially, so it is not surprising to see very little injury in the 2-DG+CLDN group.

(3) Since both 2-DG and CLDN were administered pre-APAP, it is possible that they may interfere with APAP metabolism. This should be checked by looking at GSH depletion at 30 min post APAP treatment. The same question goes for S2 figure data.

(4) There are no data on specific steps of APAP toxicity, such as GSH depletion, JNK activation, mitochondrial injury, etc., which are all well characterized in any of the studies. Rather, only injury endpoints are measured. It is critical to measure the mechanistic steps. This applies to all studies, but most importantly to the ALDOA-PF-KO mice in Figure 6.

(5) Interpretation of data in Figure 5F is flawed. Since depletion of platelets also decreases liver injury along with the platelets, it can not be deduced that the decrease in ALDOA is only in platelets. Many other things are changing.

Reviewer #3 (Public review):

Summary:

The authors address the possibility that platelet (PLT) derived EVs are important mediators of acute liver injury. Furthermore, KCs are important mediators of inflammation and are noted to need to undergo metabolic reprogramming to achieve their effects during injury. They use an APAP-induced liver injury model (AILI). They show that PLTs are recruited and that they interact with KCs in this model system. RNA-seq of KCs showed upregulation of glycolysis and gluconeogenesis. PLT depletion led to reduced liver injury. RNA-seq of KCs showed downregulation of glycolysis. In vitro co-culture of KCs and pets recapitulated the glycolysis findings. In vivo, 2DG inhibited liver injury, but not in the setting of KC depletion. They went on to show that PLT-derived EVs mediate this effect on KCs using a mix of in vitro and in vivo assays, although control EVs were lacking. After doing mass spec on EVs, they find that ALDOA is the critical payload of the PEVs that mediates the pro-glycolytic effect in vivo. They both delete ALDOA from PLTs, and they use an ALDOA inhibitor to show that injury in AILI requires ALDOA.

Strengths:

This is generally an interesting series of observations with an elegant mechanism. Many of the experiments are done in vivo with highly rigorous KO models. However, in many of the EV experiments, there are concerns about a lack of appropriate controls that might limit the rigor of those aspects of the study. 

Weaknesses:

(1) There is strong variability in the gene expression between mice in Figure 1B. I worry that the signals may not be statistically significant. The authors should assess the statistical significance.

(2) In Figure 2B, the necrosis areas that are circled in the image do not seem to resemble the quantitation on the right. For example, I don't see 60% necrosis in the APAP PBS group. Also, I don't see 5-10% necrosis in the CLDN APAP group. More images that are clearer are needed, and circled necrosis areas should be shown.

(3) In Figure 2D, a higher N should be shown. The number of mice (3) is different from the other experiments, so the exclusion of those mice should be explained.

(4) In general, control EVs from a non-PLT source should be used for all EV-related experiments. EVs derived from AML12 hepatocytes would seem to be a reasonable control for some of the experiments. Otherwise, it is hard to know if this is a general EV effect or one that is specific to PLT-derived EVs. In Figure 3B, EVs from non-PLTs should be used as a control. Since it is possible that all EVs express some level of TSG101 or CD63. In addition, control EVs should be used to test effects on KC metabolism, since the claim is that the effects are specific to PLT-derived EVs. Similarly, Figure 4 needs some kind of EV control that is not from PLTs.

(5) Figure 5B should include an EV control in the blot. Most of the blots need controls from AML12 EVs or from another in vivo source.

(6) It is a little difficult to imagine how enough ALDOA protein could be transmitted from PEVs to influence KC glycolysis on the gene expression level. It is possible that ALDOA is required for PLT-induced activation of KCs, or that EVs from PLTs can induce a metabolic shift in KCs. However, it has not been definitively shown that ALDOA from PEVs is directly causing the KC activation. Ultimately, it would be good to obtain PEVs from ALDOA WT and KO mice, then provide these PEVs to AILI mice without PLTs to see if they have differential effects on the AILI model. This would really demonstrate that the ALDOA in the PEVs is mediating the glycolytic, injurious effect.

Reviewer #1 (Public review):

Summary:

Kim and Parsons present a timely overview of the NTR/prodrug system and its applications in regenerative biology research, with particular emphasis on tissue-specific cell ablation. The system has substantially advanced the field by enabling non-invasive, conditional cell elimination, and has proven especially powerful in zebrafish, though applications in other classical model organisms are also noted. The review covers the historical origins of the NTR system, its use in regeneration studies, small-molecule screening, and genetic and CRISPR-based screening, as well as future directions including the development of the highly efficient NTR2 enzyme variant.

Strengths:

This is a useful and well-structured contribution. The manuscript is a valuable resource for the regeneration biology community.

Weaknesses:

The revised manuscript shows significant improvements; however, two points remain insufficiently addressed and should be resolved in the final version.

(1) The term 'suicide gene'

As noted in my first round of revisions, the term 'suicide gene' as applied to bacterial nitroreductase remains unaddressed in the revised manuscript, despite being scientifically inappropriate and a potential source of confusion regarding the NTR/Mtz mechanism.

'Suicide' implies an intrinsic, cell-autonomous programme of self-destruction. This is incompatible with the NTR/Mtz system, in which cell death is experimentally induced through exogenous administration of metronidazole (Mtz) by the investigator. While the 'suicide gene' framing may have utility in the cancer therapy literature, likely to aid communication with non-specialist and clinical audiences, however, it is not standard in the zebrafish field, where NTR is more accurately described as a conditional toxigene. Since this review focuses predominantly on zebrafish models, its terminology should reflect that of the relevant literature.

A further conceptual problem with the 'suicide gene' framing is that it obscures the pharmacological nature of Metronidazole. Mtz is a pharmaceutical agent with intrinsic baseline toxicity: extended exposure or modestly elevated concentrations cause toxic side effects and lethality even in non-transgenic (wild-type) zebrafish (PMID: 24428354). NTR-expressing cells do not self-destruct; rather, they are rendered selectively hypersensitive to Mtz relative to other eukaryotic cells by virtue of expressing the enzyme. This distinction is mechanistically important and should be reflected in the language used throughout the manuscript.

In summary, the term 'suicide gene' does not accurately capture enzyme-mediated bioactivation of an exogenous prodrug and should be removed from the manuscript.

(2) Barriers to using the NTR/Mtz system in non-aquatic model organisms

In response to my suggestion that the title should include "zebrafish" to accurately convey the scope of the review to prospective readers, the authors stated that "there is no intrinsic barrier to adopting this technique more broadly in other systems," citing the example that "NTR was first developed in mice, but with a prodrug that proved difficult to use, and it was not widely pursued." These two statements are, however, contradictory: if the prodrug proved difficult to use, this constitutes precisely the kind of practical barrier the authors claim does not exist. The authors should clarify and reconcile this inconsistency, and provide a more thorough discussion of why the NTR/Mtz system has seen limited adoption in classical model organisms, such as mice and Drosophila.

Reviewer #2 (Public review):

Summary:

Kim and Parsons reviewed the nitroreductase (NTR)/prodrug system: when engineered cells expressing the enzyme NTR are treated with prodrug (e.g. metronidazole), NTR converts the prodrug into cytotoxic compound which kill these cells. The review covers how the system has been developed, spatiotemporal control of targeted cell ablation, and its broad utility to study regenerative mechanisms, model human diseases, and screen chemicals to discover pro-regenerative and protective compounds. They further discussed the newer version of NTR, more potent prodrug, and experimental design, which not only expand the possible utility of the NTR/prodrug system, but allow the research community to develop a precise, reproducible and versatile platform.

Strengths:

The review summarized landmark work application of the NTR/prodrug system, and recent studies in model organisms, with focus on the model organism zebrafish. The review provides a good gateway to understanding the system and considering regenerative studies.

Weaknesses:

None.

Comments on revisions:

The authors have addressed the previous points, and the manuscript has been greatly improved.

Reviewer #3 (Public review):

Summary:

This manuscript by Kim and Parsons presents an overview of the nitroreductase/metronidazole (NTR/MTZ) cell ablation system.

Strengths:

This manuscript nicely places the NTR/MTZ system in context of other cell ablation methods, with a discussion of their respective advantages and disadvantages. This review is particularly useful for highlighting the many ways the NTR/MTZ system has been applied to study regeneration of multiple cell types and to model different degenerative human diseases. The review concludes with a discussion on recent improvements made to the system and practical considerations and "best practices" for NTR-based experiments. This review could be a helpful resource, especially for researchers new to regeneration or cell ablation studies.

Comments on revised version:

I thank the reviewers for revising the manuscript to expand their discussion of using the prodrug/NTR system in other model organisms while also revising the abstract to make it clear this review will be zebrafish focused. With these revisions, this review provides an informative overview of how the prodrug/NTR system has not only been an important tool for regeneration studies and but also for elevating the zebrafish as a regeneration model. That said, including other model organisms could have been a nice addition to the last section on experimental considerations, especially in the context of discussing potential barriers to wider adoption of the NTR system. However, given that the vast majority of studies using the NTR system are in zebrafish, the current scope of this review is understandable.

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:

This manuscript by Zhao et. al investigates the canonical hedgehog pathway in testis development of Nile tilapia. They used complementary approaches with genetically modified tilapia and transfected TSL cells (a clonal stem Leydig cell line) previously derived from 3-mo old tilapia. The approach is innovative and provides a means to investigate DHH and each downstream component from the ptch receptors to the gli and sf1 transcription factors. They concluded that Dhh binds Ptch2 to stimulate Gli1 to promote an increase in Sf1 expression leading to the onset of 11-ketotesterone synthesis heralding the differentiation of Leydig cells in the developing male tilapia.'

Strengths of the methods and results:

- The use of Nile tilapia is important as it is an important aquaculture species, it shares the genetic pathway for sex determination of mammalian species, and molecular differentiation pathways are highly conserved<br /> - The approach is rigorous and incorporates a novel TSL, clonal stem Leydig cell model that they developed that is relatively faithful in following endogenous developmental steps and can produce the appropriate steroid.<br /> - Tilapia are relatively amenable to CRISPR/Cas9 targeting and, with their accelerated developmental time frame, provide an excellent model system to interrogate specific signaling pathways.<br /> - The stepwise analysis from dhh-gli-sf1 is thoughtful and well done.

Achieved Aims: The authors set out to test the hypothesis that the canonical Dhh signaling pathway for Leydig cell differentiation and steroidogenic activity is mediated via ptch2 and gli1 regulation of sf1. The results are strong, there are additional steps needed to verify that redundancy/compensation is not contributing to the outcomes.

This work is important in better understanding of nuanced commonalities and differences in developmental pathways across species. Specific to Leydig cell differentiation and steroidogenesis, their work with tilapia supports conservation of the canonical Dhh pathway; however, there appear to be some differences in downstream mediators compared to mouse. Specifically, they conclude that ptch2/gli1 stimulates sf1 and steroidogenesis in tilapia where gli1 is dispensable in mouse. Instead, Gli3 has recently been shown to play an important role to stimulate Sf1 and support the hedgehog pathway.

Reviewer #1 (Public review):

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

Summary:

The authors describe co-regulated gene modules underlying stage differentiation in Leishmania donovani through a system-level analysis of multiple molecular layers. Using amastigotes isolated from infected hamster spleens and corresponding culture-derived promastigotes, they analyzed genomic variation, transcript abundance, protein levels, phosphorylation states, and metabolite profiles. By combining these, the study identified potential regulatory mechanisms associated with parasite differentiation and generated hypotheses regarding how gene expression is coordinated across different levels.

Strengths:

A major strength of the study is the breadth of the dataset generated. The integration provides an unusually comprehensive view of molecular changes associated with Leishmania differentiation in vitro. Such multi-layer datasets involving bona fide vertebrate host stages remain relatively rare in parasitology and will likely become a valuable resource for the molecular parasitology community. In addition, the use of amastigotes isolated from infected hamsters rather than relying on axenic models provided a biologically relevant framework for the analyses.

The revised manuscript improved several aspects of the original. The RNA-seq analysis is described with a clearer pipeline, and several claims regarding causal regulatory feedback associations have been appropriately toned down. Among the observations reported, the association between parasite differentiation and proteasome-mediated protein degradation is particularly remarkable. The combination of quantitative proteomics with pharmacological inhibition of the proteasome with lactacystin provides support for a role for protein turnover in developmental transitions and paves the way for future mechanistic studies.

Weaknesses:

Most regulatory interpretations remain largely inferential or indirect. The integration identifies correlations between different levels, but direct functional validation is limited/absent. Many of the descriptions should not be interpreted as validated. As highlighted by the authors in this revised version, the mechanistic studies will be part of future work and are beyond the scope of the current work. Of note, the attempt to confirm lactacystin-induced inhibition of proteasomal activity via anti-polyUb immunoblotting did not demonstrate the expected outcome of increase in overall poly-ubiquitylation.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.]

Reviewer #2 (Public review):

Pescher and colleagues present a revised manuscript detailing the multi-omic characterisation of Leishmania donovani amastigote to promastigote differentiation and integration of this data. The molecular pathways that regulate Leishmania life-stage transitions are still poorly understood, with many approaches exploring single proteins/RNAs etc in a reductionist manner. This paper takes a systems-scale approach and does a good job of integrating the disparate -omics datasets to generate hypotheses about the intersections of regulatory proteins that are associated with life-cycle progression. The differentiation step studied is from amastigote to promastigote using hamster-derived amastigotes which is a major strength. The use of hamsters permits the extraction of parasites that are host adapted and represent "normal", host-adapted Leishmania ploidy; the promastigote experiments are performed at a low passage number. Therefore, this is a strength or the work as it reduces the interference from the biological plasticity of Leishmania when it is cultured outside the host for prolonged periods. The multi-omics datasets presented are robust in their acquisition and analysis and will form an excellent resource for researchers studying the molecular events (particularly proteasomal protein degradation, and phosphorylation) during life-stage progression.

Overall, in the absence of follow up experiments on specific individual examples, some of the claims in the original submission were toned down and reflect a more neutral description of the data now. Significantly, the data still underpin a key role for regulation of the ribosome between the amastigote and promastigote stages (and during the differentiation process). The recursive and reciprocal links between the phosphorylation and ubiquitination systems are interesting and present many opportunities for future investigation.

Reviewer #3 (Public review):

Summary:

The authors proposed to use 5-layer systems level analysis (genomics, transcriptomics, proteomics / protein degradation, metabolomics, phosphoproteomics) to uncover how post-transcriptional mechanisms regulate stage differentiation in Leishmania donovani.<br /> This enabled the identification of several potential regulatory networks, including the regulation of stage-specific gene clusters by RNA stabilisation or decay, proteasomal degradation and protein phosphorylation.

In the new version of this manuscript, the authors have addressed all questions raised by the reviewers.

Strengths:

Although some observations in this study have already been described in the literature, the integrated analysis applied here provides a novel view on how different levels of post-transcriptional networks regulate Leishmania differentiation. This "5-layer system" represents the first analysis of this depth in kinetoplastid parasites.<br /> The revised version with an increased sample number for the RNA-seq now made the authors assumptions adequate to their obtained data.<br /> The use of a proteasomal inhibitor adds an interesting insight in how protein degradation is involved in the parasite differentiation, confirming previous observations in the literature, and help to explain the discrepancies between mRNA and protein expression in the different stages.

Weaknesses:

While this work provides an impressive and foundational dataset, it opens the door for future research to rigorously validate these initial findings and conclusions.

Significance and Impact in the field.

The different datasets generated in this study will be of great interest to the parasitology community, either to be used for hypothesis generation, to validate data from other sources, etc.

The multi-layered analysis performed here identified a series of potential feedback loops and regulatory networks to be further explored in organisms that lack transcriptional control.

Reviewer #1 (Public review):

The manuscript by Tassan-Lugrezin et al. confirms the existence of the MICOS complex in the causative agent of malaria Plasmodium falciparum. Prior to this study, only one of the two core MICOS subunits, Mic60, was found by homology search to be encoded in the apicomplexan parasite's genome. This study demonstrates the absence of the other core subunit, Mic10. It also identifies another MICOS subunit, Mic19, which co-migrates with Mic60 in a very large molecular weight complex upon blue native polyacrylamide gel electrophoresis. The authors then demonstrate that expression of both Mic60 and Mic19 is considerably upregulated during the differentiation of P. falciparum from the pathogenic asexual blood stage (ABS) to gametocytes, which correlates with the activation of oxidative phosphorylation during this process. While gene deletion of Mic19, Mic60 and both simultaneously does not affect this transition, the crista are nevertheless deformed. More significantly, crista junctions are significantly reduced, indicating that MICOS serves the same function in apicomplexans as it does in opisthokonts: maintaining crista junctions. Furthermore, the genetic interaction of mic60 and mic19 observed by augmented crista deformation when both are deleted is further evidence of their biochemical interaction, further supporting their similar complexome profiles. This study represents an important contribution to our understanding of MICOS evolution. Furthermore, the study shows that proper cristae formation is not essential for Plasmodium life cycle progression under in vitro conditions. Moreover, mutant gametocytes are still able to mate in the mosquito vector, albeit with lower efficiency.

Strengths:

The study is a result of a lot of technically challenging work in the model Plamsodium. The technically difficult life cycle progression experiments are well performed as far as I can tell. The electron microscopy is very well done and rigorously analyzed to obtain information about crista parameters. In particular, the authors were able to quantify the occurrence and diameter of crista junctions, which is very challenging in small mitochondria with small cristae. Finally, the authors provide convincing support that Mic60 and the newly discovered Mic19 act to shape crista junctions and MICOS can apparently carry out this function without the core subunit Mic10.

Weaknesses:

In its current form, there are conceptual weaknesses. The authors focus on the development of crista from a highly likely acristate state. This is true. But there can be more insight by considering their result in light of discovering the first functioning MICOS complex without one of its two core proteins, Mic10. The surprisingly large size of is also not really considered by the authors. This brings me the second weakness in my opinion. While I think the study represents a lot of work utilizing appropriate and crucial experiments, it seems the Complexome data was not explored enough. This data revealed Mic19, but what other potential subunits are co-migrating with Mic60 and Mic19 that can explain the large size of Plasmodium MICOS? Also, what is the consequence of the loss of Mic60 and Mic19 on the mitoproteome? Perhaps other MICOS subunits can be identified by their depletion in the knockouts versus the parental cell line.

Comments on latest version:

I am reviewing this manuscript again after reviewing it for Reviewers Commons. I appreciate the author's responses to my comments. The new version is improved but, in my opinion, still needs more work.

These revisions are changes to text, interpretations and obtaining more data from existing data or databases. I do still think one experimental control is necessary to substantiate the authors claim about membrane potential.

Reviewer #2 (Public review):

This manuscript reports the identification of putative orthologues of mitochondrial contact site and cristae organizing system (MICOS) proteins in Plasmodium falciparum - an organism that unusually shows an acristate mitochondrion during the asexual part of its life cycle and then develops cristae as it enters the sexual stage of its life cycle and beyond into the mosquito. The authors identify PfMIC60 and PfMIC19 as putative members and study these in detail. The authors add HA tags to both proteins and look for timing of expression during the parasite life cycle and attempt (unsuccessfully) to localise them within the parasite - lack of signal concluded to be reflect very low expression levels. They also genetically delete both genes singly and in parallel and phenotype the effect on parasite development. They show that both proteins are expressed in gametocytes and not asexuals, suggesting they are present at the same time as cristae development. They also show that the proteins are dispensable for the entire parasite life cycle investigated (asexuals through to sporozoites), however there is some reduction in mosquito transmission. Using mitotracker labelling, the authors observe differences in mitochondrial organisation in gametocytes compared to the transgenic lines. Further investigation at higher resolution using EM techniques, shows data supporting their hypothesis that PfMIC60 and PfMIC19 are important for organising the parasite mitochondrion.

The manuscript is interesting and is an intriguing use of a well-studied organism of medical importance to answer fundamental biological questions. Given the essentiality of mitochondrial respiration for parasite survival in the mosquito, it is surprising that the single and double knock-out transgenics do not give a severe phenotype. However, the authors have been rigorous in characterizing the impact of genetic deletion of both genes throughout the parasite life cycle. Subtle differences in mitochondrial organisation were observed, consistent with their hypothesis that PfMIC60 and PfMIC19 play roles in mitochondrial organisation. Therefore, these data presented give new insights into an organelle that dramatically changes during parasite development and adds to our knowledge of mitochondrial biology in a highly unusual organism.

Comments on revised version:

I previously reviewed this manuscript for Review Commons. This version is greatly improved and the authors should be commended for addressing all comments raised.

Reviewer #3 (Public review):

Summary:

MICOS is a conserved mitochondrial protein complex responsible for organising the mitochondrial inner membrane and the maintenance of cristae junctions. This study sheds first light on the role of two MICOS subunits (Mic60 and the newly annotated Mic19) in the malaria parasite Plasmodium falciparum, which forms cristae de novo during sexual development, as demonstrated by EM of thin section and electron tomography. By generating knockout lines (including a double knockout), the authors demonstrate that knockout of both MICOS subunits leads to defects in cristae morphology and a partial loss of cristae junctions. With a formidable set of parasitological assays, the authors show that despite the metabolically important role of mitochondria for gametocytes, the knockout lines can progress through the life stages and form sporozoites, albeit with diminished infection efficiency.

Major comments (from the previous round of review):

(1) The authors should improve to present their findings in the right context, in particular by:

(i) giving a clearer description in the introduction of what is already known about the role of MICOS. This starts in the introduction, where one main finding is missing: loss of MICOS leads to loss of cristae junctions and the detachment of cristae membranes, which are nevertheless formed, but become membrane vesicles. This needs to be clearly stated in the introduction to allow the reader to understand the consistency of the authors' findings in P. falciparum with previous reports in the literature.

(ii) at the end to the introduction, the motivating hypothesis is formulated ad hoc "conclusive evidence about its involvement in the initial formation of cristae is still lacking" (line 83). If there is evidence in the literature that MICOS is strictly required for cristae formation in any organism, then this should be explained, because the bona fide role of MICOS is maintenance of cristae junctions (the hypothesis is still plausible and its testing important).

(2) Line 96-97: "Interestingly, PfMIC60 is much larger than the human MICOS counterpart, with a large, poorly predicted N-terminal extension." This statement is lacking a reference and presumably refers to annotated ORFs. The authors should clarify if the true N-terminus is definitely known - a 120kDa size is shown for the P. falciparum, but this is not compared to the expected length or the size in S. cerevisiae.

(3) lines 244-245: "Furthermore, our data indicates the effect size increases with simultaneous ablation of both proteins?". The authors should explain which data they are referring to, as some of the data in Figs 3 and 4 look similar and all significance tests relate to the wild type, not between the different mutants, so it is not clear if any overserved differences are significant. The authors repeat this claim in the discussion in lines 368-369 without referring to a specific significance test. This needs to be clarified.

(4) lines 304-306: "Though well established as the cristae organizing system, the role of MICOS in initial formation of cristae remains hidden in model organisms that constitutively display cristae.". This sentence is misleading since even in organisms that display numerous cristae throughout their life cycle, new cristae are being formed as the cells proliferate. Thus, failure to produce cristae in MICOS knockout lines would have been observable but has apparently not been reported in the literature. Thus, the concerted process in P. falciparum makes it a great model organism, but not fundamentally different to what has been studied before in other organisms.

(5) lines 373-378. "where ablation of just MIC60 is sufficient to deplete functionality of the entire MICOS (11, 15),". The authors' claim appears to be contrary to what is actually stated in ref 15, which they cite:

"MICOS subunits have non-redundant functions as the absence of both MICOS subcomplexes results in more severe morphological and respiratory growth defects than deletion of single MICOS subunits or subcomplexes."

This seems in line with what the authors show, rather than "different".

(6) lines 380-385: "... thus suggesting that membrane invaginations still arise but are not properly arranged in these knockout lines. This suggests that MICOS either isn't fully depleted,...". These conclusions are incompatible with findings from ref. 15, which the authors cite. In that study, the authors generated a ∆MICOS line which still forms membrane invaginations, showing that MICOS is not required at all for this process in yeast. Hence the authors' implication that MICOS needs to be fully depleted before membrane invaginations cease to occur is not supported by the literature.

(7) The authors should consider if the first part of their title could be seen as misleading: It suggests that MICOS is "the architect" in cristae formation, but this is not consistent with the literature nor their own findings.

Significance:

The main strength of the study is that it provides the first characterisation of the MICOS complex in P. falciparum, a human parasite in which the mitochondrion has been shown to be a drug target. Mic60 and the newly annotated Mic19 are confirmed to be essential for proper cristae formation and morphology, as well as overall mitochondrial morphology. Furthermore, the mutant lines are characterised for their ability to complete the parasite life cycle and defects in infection effectivity are observed. This work is an important first step for deciphering the role of MICOS in the malaria parasite and the composition and function of this complex in this organism.

The limitation of the study stems from what is already known about MICOS and its subunits in other organisms. MICOS subunit knockouts have been characterised in great detail in yeast and humans with similar findings regarding loss of cristae and cristae defects. The findings of this study do not provide dramatic new insight on MICOS function or go substantially beyond the vast existing literature in terms of the extent of the study, which focuses on parasitological assays and morphological analysis.

Exploring the role of MICOS in an early-divergent organism and human parasite is however important given the divergence found in mitochondrial biology and P. falciparum is a uniquely suited model system. One aspect that would increase the impact of the paper would be if the authors could mechanistically link the observed morphological defects to the decreased infection efficiency, e.g. by probing effects on mitochondrial function. This will likely be challenging as the morphological defects are diverse and the fitness defects appear moderate/mild.

The advance presented in this study is to pioneer the study of MICOS in P. falciparum, thus widening our understanding of the role of this complex to different model organism. This study will likely be mainly of interest for specialised audiences such as basic research parasitologists and mitochondrial biologists. My own field of expertise is mitochondrial biology and structural biology.

Comments on revised version:

The authors have addressed my all of my previous comments in the updated manuscript version.

Reviewer #1 (Public review):

Summary:

In this manuscript, the role of the insulin receptor and the insulin growth factor receptor was investigated in podocytes. Mice, where both receptors were deleted, developed glomerular dysfunction and developed proteinuria and glomerulrosclerosis over several months. Because of concerns about incomplete KO, the authors generated and studied podocyte cell lines where both receptors were deleted. Loss of both receptors was highly deleterious with greater than 50% cell death. To elucidate the mechanism of cell death, the authors performed global proteomics and found that spliceosome proteins were downregulated. They confirmed this directly by using long-read sequencing. These results suggest a novel role for insulin and IGF1R signaling in RNA splicing in podocytes.

This is primarily a descriptive study and no technical concerns are raised. The mechanism of how insulin and IGF1 signaling regulates splicing is not directly addressed but implicates potentially the phosphorylation downstream of these receptors. In the revised manuscript, it is shown that the mouse KO is incomplete potentially explaining the slow onset of renal insufficiency. Direct measurement of GFR and serial serum creatinines might also enhance our understanding of progression of disease, proteinuria is a strong sign of renal injury. An attempt to rescue the phenotype by overexpression of SF3B4 would also be useful but may be masked by defects in other spliceosome genes. As insulin and IGF are regulators of metabolism, some assessment of metabolic parameters would be an optional add-on.

Significance:

With the GLP1 agonists providing renal protection, there is great interest in understanding the role of insulin and other incretins in kidney cell biology. It is already known that Insulin and IGFR signaling play important roles in other cells of the kidney. So, there is great interest in understanding these pathways in podocytes. The major advance is that these two pathways appear to have a role in RNA metabolism.

Latest comments:

The new reviewer raised two major points, whether the KO effect on splicing is specific to IGF1 and whether the interpretation could be developmental rather than due to splicing. The reviewer raises some important issues but the evidence to suggest that this is specific is data in the literature that IR/IGF signaling is already known to regulate splicing and that splicing defects were not detected in other models that they have analyzed. I agree with the reviewer (and authors) that the incomplete floxing of the genes is a major complication. The point that there could be a developmental defect with mice being born with fewer podocytes and perhaps the authors should caveat this point. The fact that they mice are born with normal function, that renal function can be maintained with up to 80% loss of podocytes suggest that they are likely born with a good number of podocytes and the dysfunction that occurs at 6 months is due to a process, induced by the loss of IR/IGF signaling that is detrimental to the podocyte.

Reviewer #2 (Public review):

Summary:

In this manuscript, submitted to Review Commons (journal agnostic), Coward and colleagues report on the role of insulin/IGF axis in podocyte gene transcription. They knocked out both the insulin and IGFR1 mice. Dual KO mice manifested a severe phenotype, with albuminuria, glomerulosclerosis, renal failure and death at 4-24 weeks.

Long read RNA sequencing was used to assess splicing events. Podocyte transcripts manifesting intron retention were identified. Dual knock-out podocytes manifested more transcripts with intron retention (18%) compared wild-type controls (18%), with an overlap between experiments of ~30%.

Transcript productivity was also assessed using FLAIR-mark-intron-retention software. Intron retention w seen in 18% of ciDKO podocyte transcripts compared to 14% of wild-type podocyte transcripts (P=0.004), with an overlap between experiments of ~30% (indicating the variability of results with this method). Interestingly, ciDKO podocytes showed downregulation of proteins involved in spliceosome function and RNA processing, as suggested by LC/MS and confirmed by Western blot.

Pladienolide (a spliceosome inhibitor) was cytotoxic to HeLa cells and to mouse podocytes but no toxicity was seen in murine glomerular endothelial cells.

The manuscript is generally clear and well-written. Mouse work was approved in advance. The four figures are generally well-designed, bars/superimposed dot-plots.

Methods are generally well described.

Comments on previous version:

Coward and colleagues have done an excellent job of responding to all the reviewer comments.

Reviewer #4 (Public review):

Summary and background:

This report entitled "The insulin/IGF axis is critically important (for) controlling gene transcription in the podocyte" from Hurcombe et al is based on a mouse double knockdown of the IR and IGF1R and a parallel cultured mouse podocyte model. Insulin/IGF signaling system in mammals evolved as three gene reduplicated peptides (insulin, IGF-1, and IGF-2) and their two receptors IR and IGF1R that cross-react to variable extents with the peptides, are ubiquitously expressed, and signal through parallel pathways. The major downstream effect of insulin is to regulate glucose uptake and metabolism, while that of the IGF pathways is to regulate growth and cell cycling in part through mTORC1. The GH-IGF-1-IGF1R pathway regulates post-natal growth. IGF-2 signaling is thought to play a major role in regulating intrauterine growth and development, although IGF-2 is also present at high levels in post-natal life. Thus, one would anticipate that reducing IR/IGF1R signaling in any cell would slow growth and cell cycling by reducing growth factor and metabolic mTORC1-mediated and other processes including the splicing of RNA for protein synthesis.

Comments on revised version:

The second sentence of the Summary reads "This study sought to elucidate the compound role of the insulin/IGF1 axis in podocytes using transgenic mice and cell culture models deficient in both receptors." The study design and rationale for the proteosome analysis described is predicated on the finding that podocyte-specific knockdown of the IR/IGF-1R in mice is associated with development of proteinuria and reduced eGFR by 20months of life. Since the IR/IGF-1R are critically required for normal development and growth of all cells and organs, the obvious explanation for the observation would be that the model system results in defective podocyte development and deployment (caused by reduced IR/IGF-1) that, in turn, causes subsequent development of proteinuria and glomerulosclerosis (that may be much less dependent on a normal level of IR/IGF-1R expression). Thus, the experimental design does not allow a distinction between podocyte development and steady state function which are different biologic processes. The data provided does not examine podocyte status immediately after birth to confirm that podocyte number and size and structure is normal in mice that subsequently develop proteinuria and glomerulosclerosis. The response to the reviewer suggests that since this would require additional mice it has not been undertaken in order to reduce animal usage. This is not a valid argument, particularly when the investigators have not even used state-of-the-art methods to measure podocyte number, size and density in adult mice, key parameters that would be required to interpret their data. Counting podocyte nuclear number in glomerular cross-sections is simply an inadequate method, even if it is used and reported in other journals, and particularly where the examples given to justify its use can hardly be viewed as representing first rate science.

If the absence of studies that would answer the above questions, the investigators should add a sentence to the Discussion dealing with study limitations as follows. "The study design does not allow us to determine whether the primary effect of reduced IR/IGF-1R expression on the phenotype is during in utero and post-natal podocyte development and deployment, during periods of rapid growth when IGF-1 levels are highest, in steady state adult podocytes, or under all of the above conditions".

Reviewer #1 (Public review):

Summary:

Johnston and Smith used linear electrode arrays to record from small populations of neurons in the superior colliculus (SC) of monkeys performing a memory-guided saccade (MGS) task. Dimensionality reduction (PCA) was used to reveal low-dimensional subspaces of population activity reflecting the slow drift of neuronal signals during the delay period across a recording session (similar to what they reported for parts of cortex: Cowley et al., 2020). This SC drift was correlated with a similar slow-drift subspace recorded from the prefrontal cortex, and both slow-drift subspaces tended to be associated with changes in arousal (pupil size). These relationships were driven primarily by neurons in superficial layers of the SC, where saccade sensitivity/selectivity is typically reduced. Accordingly, delay-period modulations of both spiking activity and pupil size were independent of saccade-related activity, which was most prevalent in deeper layers of the SC. The authors suggest that these findings provide evidence of a separation of arousal- and motor-related signals. The analysis techniques expand upon the group's previous work and provides useful insight into the power of large-scale neural recordings paired with dimensionality reduction. This is particularly important with the advent of recording technologies which allow for the measurement of spiking activity across hundreds of neurons simultaneously. Together, these results provide a useful framework for comparing how different populations encode signals related to cognition, arousal, and motor output in potentially different subspaces.

Comments on revised manuscript:

The authors have done a very good job of responding to all of the reviewers' concerns.

Reviewer #2 (Public review):

Summary:

Neurons in motor-related areas have increasingly shown to carry also other, non-motoric signals. This creates a problem of avoidance of interference between the motor and non-motor-related signals. This is a significant problem that likely affects many brain areas. The specific example studied here is interference between saccade-related activity and slow-changing arousal signals in the superior colliculus. The authors identify neuronal activity related to saccades and arousal. Identifying saccade-related activity is straightforward, but arousal-related activity is harder to identify. The authors first identify a potential neuronal correlate of arousal using PCA to identifying a component in the population activity corresponding to slow drift over the recording session. Next, they link this component to arousal by showing that the component is present across different brain areas (SC and PFC), and that it is correlated with pupil size, an external marker of arousal. Having identified an arousal-related component in SC, the authors show next that SC neurons with strong motor-related activity are less strongly affected by this arousal component (both SC and PFC). Lastly, they show that SC population activity pattern related to saccades and pupil size form orthogonal subspaces in the SC population.

Strengths:

A great strength of this research is the clear description of the problem, its relationship with the performed analysis and the interpretation of the results. The paper is very well written and easy to follow.

An additional strength is the use of fairly sophisticated analysis using population activity.

Weaknesses:

(1) The greatest weakness in the present research is the fact that arousal is a functionally less important non-motoric variable. The authors themself introduce the problem with a discussion of attention, which is without any doubt the most important cognitive process that needs to be functionally isolated from oculomotor processes. Given this introduction, one cannot help but wonder, why the authors did not design an experiment, in which spatial attention and oculomotor control are differentiated. Absent such an experiment, the authors should spend more time on explaining the importance of arousal and how it could interfere with oculomotor behavior.

(2) In this context, it is particularly puzzling that one actually would expect effects of arousal on oculomotor behavior. Specifically, saccade reaction time, accuracy, and speed could be influenced by arousal. The authors should include an analysis of such effects. They should also discuss the absence or presence of such effects and how they affect their other results.

(3) The authors use the analysis shown in Figure 6D to argue that across recording sessions the activity components capturing variance in pupil size and saccade tuning are uncorrelated. however, the distribution (green) seems to be non-uniform with a peak at very low and very high correlation, specifically. The authors should test if such an interpretation is correct. If yes, where are the low and high correlations respectively? Are there potentially two functional areas in SC?

Comments on the first revision:

My main concern with the paper is really two-fold. First, I think it is only incremental and adds next to no useful information about the SC. That might not be a fair criticism and certainly is purely subjective, but it affects the standards that eLife has on significance thresholds for papers. As such, this is an issue the editors should talk about.

Second, my main concern with the substance of the paper is that the authors jump immediately into an analysis of the 'arousal-related' effects on SC activity. Before that, I would like to see some behavioral indicators of arousal, such as RT differences, pupil size (the talk about this), or accuracy. The authors first need to describe the objective behavioral indicators of the level of arousal. Using these indices, they need to establish that there are meaningful differences in the level of arousal across the recording session. Having done so, they can proceed to link changes in SC activity with levels of arousal.

Instead, in its current form, the authors find changes in SC activity and describe them immediately as 'arousal-related'. I hope it is clear why that is premature. The 'slow-drift' fluctuations are presumed to be related to arousal, but they could be meaningless random fluctuations, or related to some other cognitive process.

Other than this conceptual issue, I do not have major problems with the analysis per se.

Comments on the latest version:

They have constructively responded to my concerns. I think 'incomplete' should be replaced with 'solidly supported'.

Reviewer #3 (Public review):

Summary:

This study looked at slow changes in neuronal activity (on the order of minutes to hours) in the superior colliculus (SC) and prefrontal cortex (PFC) of two monkeys. They found that SC activity shows slow drift in neuronal activity like in the cortex. They then computed a motor index in SC neurons. By definition, this index is low if the neuron has stronger visual responses than motor response, and it is high if the neuron has weaker visual responses and stronger motor responses. The authors found that the slow drift in neuronal activity was more prevalent in the low motor index SC neurons and less prevalent in the high motor index neurons. In addition, the authors measured pupil diameter and found it to correlate with slow drifts in neuronal activity, but only in the neurons with lower motor index of the SC. They concluded that arousal signals affecting slow drifts in neuronal modulations are brain-wide. They also concluded that these signals are not present in the deepest SC layers, and they interpreted this to mean that this minimizes the impact of arousal on unwanted eye movements.

Strengths:

The paper is clear and well-written.

Showing slow drifts in the SC activity is important to demonstrate that cortical slow drifts could be brain-wide.

Weaknesses:

The authors find that the SC cells with the low motor index are modulated by pupil diameter. However, this could be independent of an "arousal signal". These cells have substantial visual sensitivity. If the pupil diameter changes, then their activity should be influenced since the monkey is watching a luminous display. So, in this regard, the fact that they do not see "an arousal signal" in the most motor neurons (through the pupil diameter analyses) is not evidence that the arousal signal is filtered out from the motor neurons. It could simply be that these neurons simply do not get affected by the pupil diameter because they do not have visual sensitivity.

Comments on revisions:

The authors have given due consideration to the possibility that SC signaling of arousal could be at least in part due to changes in pupil size related responses to ambient light. Discussion of this point in the most recent revision helps to mitigate this concern.

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 noted above, which were raised in the previous round of review.]

Summary:

The manuscript investigates how exogenous attention modulates spatial frequency sensitivity within the foveola. Using high-precision eye-tracking and gaze-contingent stimulus control, the authors show that exogenous attention selectively improves contrast sensitivity for low- to mid-range spatial frequencies (4-8 cycles/degree), but not for higher frequencies (12-20 CPD). In contrast, improvements in asymptotic performance at the highest contrast levels occur across all spatial frequencies. These results suggest that, even within the foveola, exogenous attention operates through a mechanism similar to that observed in peripheral vision, preferentially enhancing lower spatial frequencies.

Strengths:

The study shows strong methodological rigor. Eye position was carefully controlled, and the stimulus generation and calibration were highly precise. The authors also situate their work well within the existing literature, providing a clear rationale for examining the fine-grained effects of exogenous attention within the foveola. The combination of high spatial precision, gaze-contingent presentation, and detailed modeling makes this a valuable technical contribution.

Weaknesses:

The manipulation of attention raises some interpretive concerns. Clarifying this issue, together with additional detail about statistics, participant profiles, other methodological elements, and further discussion in relation to oculomotor control in general, could broaden the impact of the findings.

Reviewer #2 (Public review):

Summary:

This study aims to test whether foveal and non-foveal vision share the same mechanisms for endogenous attention. Specifically, they aim to test whether they can replicate at the foveola previous results regarding the effects of exogenous attention for different spatial frequencies.

Strengths:

Monitoring the exact place where the gaze is located at this scale requires very precise eye-tracking methods and accurate and stable calibration. This study uses state-of-the-art methods to achieve this goal. The study builds on many other studies that show similarities between foveal vision and non-foveal vision, adding more data supporting this parallel.

Weaknesses:

The study lacks a discussion of the strength of the effect and how it relates to previous studies done away from the fovea. It would be valuable to know if not just the range of frequencies, but the size of the effect is also comparable.

Reviewer #3 (Public review):

Summary:

This paper explores how spatial attention affects foveal information processing across different spatial frequencies. The results indicate that exogenously directed attention enhances contrast sensitivity for low- to mid-range spatial frequencies (4-8 CPD), with no significant benefits for higher spatial frequencies (12-20 CPD). However, asymptotic performance increased as a result of spatial attention independently of spatial frequency.

Strengths:

The strengths of this article lie in its methodological approach, which combines a psychophysical experiment with precise control over the information presented in the foveola.

Weaknesses:

The authors acknowledge that they used the standard approach of analyzing observer-averaged data, but recognize that this method has limitations: it ignores the uncertainty associated with parameter estimates and the relationships between different parameters of the psychometric model. This may affect the interpretation of attentional effects. In the future, mixed-effects models at the trial level could overcome these limitations.

Reviewer #1 (Public review):

Summary:

In their manuscript entitled "Terminal tracheal cells of Drosophila are immune privileged to maintain their Foxo-dependent structural plasticity", Bossen and colleagues determine that the terminal cells of the tracheal system differ from other larval tracheal cells in that they do not typically show an Imd-dependent immune response to fungal and viral infections. Authors reach this conclusion based on the expression of a reporter line, Drs-GFP. The authors speculate that this difference may reflect differential expression of an immune pathway component, as tracheal terminal cells (ttcs) do not respond to forced expression of PRGP-LS. The authors then go on to show that, unlike the other cells of the tracheal system, terminal cells do not express PGRP-LC as reported by a GAL4 enhancer trap. Forced expression of PGRP-LC in terminal cells resulted in reduced branching, cell damage and features of the cell death program. These effects could be suppressed by depletion of AP-1 or Foxo transcription factors. Authors show that Foxo plays a negative role in branching of ttcs, with ectopic branching occurring upon RNAi (or under hypoxic conditions). The authors speculate that immune privilege of the ttcs may have evolved to permit Foxo regulation of ttc branching.

Strengths:

The authors provide compelling genetic data that support their overall conclusions.

Weaknesses:

FC do not appear to express DRS reporter in Figure 1 or elsewhere, raising the question of whether fusion cells are also immune privileged.<br /> Fig 5, TRE_RFP expression, is convincing in wt ttc, but not in ttc o/x PGRP-LCx

Reviewer #2 (Public review):

Summary:

In this study, Bossen et al. looked at the immune status of the tracheal terminal cells (TTCs) in Drosophila larvae. The authors propose that these cells do show PGFP-LCx expression and, hence, lack immune function. Artificial overexpression of the PGRP-LCx in the TTCs causes these cells to undergo apoptosis.

Strengths:

Only a few groups have tried to look at the immune status of the trachea, though we know that AMPs are expressed there after infection. This exciting study attempts to understand the differences in the tracheal cells that do not produce AMPs upon infection.

Weaknesses:

The reason why the TTCs have some immune privilege still needs to be completely clear. Whether the phenotype is cell autonomous or contributes to the cellular immune system is not evaluated. As we know, crystal cells also maintain oxygen levels in larvae; whether in the absence of a terminal trachea, the crystal cells have any role is not explored.

My particular comments on the figures are as follows:

(1) In Figure 2, the PGRP-LCx signal should be quantified as done for Drosomycin GFP, as shown in Figure 1.<br /> - The authors have now done this.

(2) In Fig 2F and G are the larvae infected? If not, what happens to PGRP-LCx expression post Ecc15 infection?<br /> - The authors have answered this question, saying infection has no effect on TTCs' Dr-GFP expression.

(3) Is the effect of overexpression of LCx exaggerated post-infection? In particular, when it comes to the escape phenotype.<br /> - This was not done; the infection experiment was done with PGRP-LE overexpression.

(4) Does overexpression of anti-apoptotic genes in TTC and PGRP-LCx rescue the TTC branching?<br /> - This was not done.

(5) Have the authors tried to rescue the larvae with shallow food?<br /> - This was not done.

(6) Is there any effect on the circulating hemocytes or lymph gland in the PGFRP-LCx overexpressing animals?<br /> - This was not done.

Reviewer #3 (Public review):

Summary:

The authors report that tracheal terminal cells (TTCs) in Drosophila do not activate innate immunity following bacterial infection, and attribute this to the absence of PGRP-LCx expression in these cells. Forced activation of the Imd pathway in TTCs leads to JNK-mediated cell death and reduced tracheal branching. The authors propose that this immune-privileged status preserves Foxo-dependent structural plasticity, which is essential for TTCs to respond to changing environmental conditions such as hypoxia.

Strengths:

The revised manuscript represents a meaningful improvement over the initial submission. The addition of multiple antimicrobial peptide reporters substantially strengthens the key observation that TTCs do not mount a humoral immune response upon infection, moving beyond reliance on the Drs-GFP reporter alone. The mechanistic dissection of the cell death pathway - demonstrating roles for JNK, AP-1, and Foxo downstream of ectopic PGRP-LCx activation - is well-executed and provides solid mechanistic insight. The inclusion of a second, independent UAS-PGRP-LCx line with a milder phenotype adds useful calibration. The hypoxia sensitivity assays provide physiological context, and the discussion of the gradient hypothesis, while based on qualitative observation, is logically reasoned and addresses a legitimate alternative interpretation.

Weaknesses:

The primary remaining concern is that the absence of PGRP-LCx expression in TTCs is supported by a single GAL4 enhancer trap line, without independent validation by complementary methods such as in situ hybridization, antibody staining, or reanalysis of publicly available single-cell transcriptomic data. The authors acknowledge this limitation transparently. While the convergent evidence from infection experiments - in which neither the Drs-GFP reporter nor the PGRP-LCx-Gal4 line shows TTC activation - lends indirect support, orthogonal confirmation would more definitively establish this mechanistic claim.

Additionally, the finding that Dcp-1 cleavage occurs in non-TTC tracheal cells as well suggests that Imd-mediated apoptotic signaling is not uniquely restricted to TTCs, and the Discussion could more explicitly address what distinguishes the TTC response in terms of degree or cellular context.

Reviewer #3 (Public review):

Agarwal et al identified the small molecule semapimod from a chemical screen of repurposed drugs with specific antimycobacterial activity against a leucine-dependent strain of M. tuberculosis. To better understand the mechanism of action of this repurposed anti-inflammatory drug, the authors used RNA-seq to reveal a leucine-deficient transcriptomic signature from semapimod challenge. The authors then measured a decreased intracellular concentration of leucine after semapimod challenge, suggesting that semapimod disrupts leucine uptake as the primary mechanism of action. Unexpectedly however, resistant mutants raised against semapimod had a mutation in the polyketide synthase gene ppsB that resulted in loss of PDIM synthesis. The authors believe growth inhibition is a consequence of decreased accumulation of leucine as a result of an impaired cell wall and a disrupted, unknown leucine transporter. This study highlights the importance of branched-chain amino acids for M. tuberculosis survival and the chemical genetic interactions between semapimod and ppsB indicate that ppsB is a conditionally essential gene in a medium deplete of leucine.

The conclusions regarding the leucine and PDIM phenotypes are moderately supported by experimental data. The authors do not provide experimental evidence to support a specific link between leucine uptake and impaired PDIM production. Additional work is needed to support these claims and strengthen this mechanism of action.

A mechanistic gap still exists for the model of semapimod antitubercular activity. The basis for semapimod activity is that the leucine auxotroph strain cannot acquire leucine from its environment, and thus the bug ceases to grow. Under normal growth conditions, the leucine auxotroph strain produces PDIM and acquires exogenous leucine through some mechanism (either through a transporter or through PDIM). Semapimod binding to PpsB causes the cell to alter its PDIM profile (lacking experimental for this), and now with the altered PDIM profile the cell cannot acquire enough exogenous leucine to sustain growth (either because the altered PDIM profile interferes with the leucine transporter activity or through PDIM uptake). Acquiring a mutation in ppsB results in cells unable to produce PDIM (some evidence supporting this) but can now acquire enough exogenous leucine to sustain growth. I cannot find the connection between cells that have normal PDIM with normal leucine uptake and cells that are missing PDIM with normal leucine uptake.

(1) The manuscript would benefit from adding additional antibiotic controls to experiments. With the current experimental approaches, it is unclear if these signatures are the result of semapimod specifically or the effect of an antimicrobial agent. Adding additional strains to the 2D TLC experiments could provide more confidence in the absence or modifications of the PDIM band.

(2) The intriguing observation that wild-type H37Rv is resistant to semapimod but the leucine-auxotroph is sensitive should be further explored. If the authors are correct and semapimod does inhibit leucine uptake through a specific transporter or modified PDIM profiles, testing semapimod activity against the leucine-auxotroph in various concentrations of BCAAs could highlight the importance of intracellular leucine. Cells might recover growth in the presence of semapimod treatment if enough leucine is provided in the media and some fraction is able to enter the cell through the impaired PDIM barrier.

Reviewer #4 (Public review):

Summary:

In this study, the authors screened an FDA-approved repurposed library of small-molecule inhibitors against the auxotrophic strain Mtb mc2 6206 and found that semapimod exclusively inhibited its growth. Further studies showed that it inhibits L-leucine uptake by interacting with PpsB, although the exact mechanism remains unknown. Interestingly, semapimod showed antibacterial activity against H37Rv only in vivo, not in vitro, suggesting a dependence on host-derived exogenous leucine during intracellular growth. This work therefore suggests that uptake of host-derived leucine can be targeted as an effective strategy to reduce intracellular survival of Mtb.

Strengths:

The authors have used different approaches to understand the mechanism of L-leucine uptake in Mtb. To start, they conducted an in vitro screen using an FDA-approved library, followed by transcriptomic and metabolic analyses of different Mtb mutants. Through whole-genome sequencing, they identified mutations conferring resistance to semapimod to gain further mechanistic understanding. This led to the analysis of semapimod-PpsB interaction by BLI-Octet and analysis of cell-wall apolar lipid, which explained how PDIM loss resulted in sensitivity to vancomycin. Finally, infection experiments in mice surprisingly showed that semapimod was effective against intracellular Mtb in vivo but not in vitro.

Weakness:

The major weakness of this study is that it is unclear what role PpsB plays in L-leucine uptake. It is also not clear why intracellular Mtb relies on exogenous leucine rather than endogenous leucine. Does intracellular Mtb lose its ability to synthesize leucine, which is why semapimod is active in vivo but not in vitro? Or semapimod has any other effect on host immunity that has not been explored. I have a few minor comments, which are as follows:

(1) Authors state that "The colony forming unit (CFU) estimation further shows a bactericidal activity of this molecule which causes 88% reduction of bacterial viability on day 2 and >99% reduction after 5 days of incubation" (Fig. 1d). However, this is only true when compared to the untreated control. Compared to the Day 0 control, treated bacteria appear to have undergone little or no change, suggesting that the compound is bacteriostatic, not bactericidal. The drug concentration used for Fig 1d is not mentioned. For Fig. 1e, there is no day 0 control, and the comparison is with the untreated control at Day 6, which again does not suggest bactericidal action of Semapimod.

(2) The authors report that "Notably, no cytotoxic effect was observed at this concentration against THP1, thus ruling out the possibility of cell lysis by semapimod," but the data are not shown. Similarly, authors state that "As a control, interaction of semapimod was also analyzed with the purified Ppe60, which fails to exhibit any binding," but the data is not shown.

(3) Line 235: change "promote" to "promoter".

Reviewer #5 (Public review):

Summary:

The authors have extensively characterized the response of the leucine and pantothenate auxotroph Mtb strain H37Rv mc26 206 to an FDA-approved compound library and identified semapimod that is, at best, bacteriostatic in its action against the pathogen. The authors have used transcriptional profiling, metabolite quantification and a screening of genetically-resistant mutants to identify changes in leucine uptake under semapimod exposure. Based on these data, the authors attribute changes in antibiotic susceptibility to differences in environmental leucine availability and bacterial PDIM architecture. While the work presents an interesting avenue of investigation of metabolite uptake and utilization in a comparative fashion between fully virulent and auxotroph Mtb strains, it lacks clear and direct evidence to link the observations with a mechanistic explanation.

Strengths:

The authors used a well-designed screening strategy for FDA-approved compounds against a metabolically defined strain and follow up characterization of semapimod exposure through RNA-seq and pathway analysis, metabolomics and time-course analysis of drug effects. The data has been interestingly interpreted to identify a phenotypic connection between PDIM and altered drug susceptibility.

Weaknesses:

The major gap in the study is the speculative nature of the mechanism underpinning the connection between PDIM architecture and changes in leucine uptake under various bacterial growth conditions.

(1) Despite claims of identifying a "novel leucine uptake mechanism", the authors only provide endpoint metabolite measurements rather than kinetic leucine transport studies.

(2) A clear explanation for the differences in susceptibility between auxotroph and fully virulent Mtb strains through changes in "PDIM architecture" is not supported by any direct evidence such as structural analysis, lipidomics, or direct measurement of PDIM architectural changes.

(3) The figures 1D (lines 110-112, "kills bacteria") and 7c (lines 283-285) are used to infer a bactericidal role of semapimod, which maybe a mischaracterization of drug activity. The trend in CFUs in both cases seems of no bacterial growth rather than a CFU reduction- therefore interpreted as "bacteriostatic" at best. These observations would in fact align with the general antibiotic/stress response signature identified by RNA-seq, where leucine transport related genes only happen to be a small subset of many dysregulated genes. How do the authors disentangle these generic signatures from the leucine transport evidence, other than endpoint metabolite quantification?

(4) Furthermore, the studies with supplementation of leuCD (and not panCD) in rescuing from semapimod susceptibility are not supported by a clear mechanistic link. The complementation of leuCD does not completely rescue growth- does this indicate differences in uptake and metabolism? The authors should test this by monitroing the growth of the strains in minimal medium in presence and absence of exogenous leucine.

(5) It remains unclear if the authors attribute leucine uptake differences to a loss of PDIM or changes in PDIM amount and architecture. No direct evidence is provided for differences in PDIM production in the WT H37Rv strain and the auxotroph mc2 6206 strains used in this study. Mulholland et al (2024) report similar PDIM levels for WT and auxotrophic Mtb (mc2 6206) in their stocks passaged to maintain PDIM. This could change for stocks maintained differently. Since the presence of PDIM has classically been used to explain a penetration barrier for small molecules and the schematic provided by the authors at the end of the manuscript (figure 8c) suggest free leucine penetration in the absence of PDIM, how do the authors explain the increased leucine uptake and sensitivity of a PDIM positive auxotroph to semapimod through direct experimental evidence? Further on the point of PDIM production, the WT auxotroph strain seems to produce limited amounts of PDIM as evidenced by the TLC data in Figure 6b. To solidify this point, the authors should test other point mutants for PDIM production (not attenuated for growth) through TLC and quantify these differences. These data should be compared with PDIM production in the WT Mtb H37Rv strain (used by the authors) under in vitro growth conditions. A comparative lipidomics of cell envelope components might be insightful in explaining these differences. I believe answering this query is crucial and within the scope of the work whose central claim is the identification of a novel leucine uptake mechanism. It would be interesting, in fact, to identify a novel transporter associated with the PDIM layer on the cell envelope.

Reviewer #1 (Public review):

Summary:

The manuscript by Rayan et al. aims to elucidate the role of RNA as a context-dependent modulator of liquid-liquid phase separation (LLPS), aggregation, and bioactivity of the amyloidogenic peptides PSMα3 and LL-37, motivated by their structural and functional similarities.

Strengths:

The authors combine extensive biophysical characterization with cell-based assays to investigate how RNA differentially regulates peptide aggregation states and associated cytotoxic and antimicrobial functions.

Weaknesses:

While the study addresses an interesting and timely question with potentially broad implications for host-pathogen interactions and amyloid biology, some aspects of the experimental design and data analysis require further clarification and strengthening.

Reviewer #2 (Public review):

In this paper, Rayan et al. report that RNA influences cytotoxic activity of the staphylococcal secreted peptide cytolysin PSMalpha3 versus human cells and E. coli by impacting its aggregation. The authors used sophisticated methods of structural analysis and describe the associated liquid-liquid phase separation. They also compare to the influence of RNA on aggregation and activity of LL-37, which shows differences to that on PSMalpha3.

That RNA impacts PSM cytotoxicity when co-incubated in vitro becomes clear. However, I have two major problems with this study:

(1) The premise, as stated in the introduction and elsewhere, that PSMalpha3 amyloids are biologically functional, is highly debatable and has never been conclusively substantiated. The property that matters most for the present study, cytotoxicity, is generally attributed to PSM monomers, not amyloids. The likely erroneous notion that PSM amyloids are the predominant cytotoxic form is derived from an earlier study by the authors that has described a specific amyloid structure of aggregated PSMalpha3. Other authors have later produced evidence that, quite unsurprisingly, indicated that aggregation into amyloids decreases, rather than increases, PSM cytotoxicity. Unfortunately, yet other groups have in the meantime published in-vitro studies on "functional amyloids" by PSMs without critically challenging the concept of PSM amyloid "functionality". Of note, the authors' own data in the present study that show strongly decreased cytotoxicity of PSMalpha3 after prolonged incubation are in agreement with monomer-associated cytotoxicity as they can be easily explained by the removal of biologically active monomers from the solution.

In their revision and in the rebuttal, the authors have further described their concept regarding what they call "functionality" of PSMalpha3 amyloids. They now admit that monomers are the active cytolytic form, like other researchers have stressed, whereas amyloids are not. This represents a considerable difference to earlier papers in which they ascribed functionality, i.e. cytolytic capacity, to PSMalpha3 amyloids, a claim that has raised considerable controversy. Now, they use the term "functional " to describe that PSMalpha3 amyloids, while not cytolytic, can be reversed to a cytolytic monomeric state, calling them a "dynamic reservoir". There is no evidence that such a reservoir is necessary for the cytolytic activity of the monomers to be established; also, there is no evidence that in a biological system, such an amyloid reservoir exists. To continue calling PSMalpha3 amyloids "functional" based on this - considerably changed - concept of the authors appears inappropriate, given the finally admitted absence of cytolytic activity of the PSM amyloids in addition to the continuing complete lack of evidence of any biological relevance of PSM amyloid formation.

(2) That RNA may interfere with PSM aggregation and influence activity is not very surprising, given that PSM attachment to nucleic acids - while not studied in as much detail as here - has been described. Importantly, it does not become clear whether this effect has biologically significant consequences beyond influencing, again not surprisingly, cytotoxicity in vitro. The authors do show in nice microscopic analyses that labeled PSMalpha3 attaches to nuclei when incubated with HeLa cells. However, given that the cells are killed rapidly by membrane perturbation by the applied PSM concentrations, it remains unclear and untested whether the attachment to nucleic acids in dying cells makes any contribution to PSM-induced cell death or has any other biological significance.

Overall, the findings can be explained in a much more straightforward way with the common concept of cytotoxicity being due to monomeric PSMs, and the impact of nucleic acids on cytotoxicity being due to lowering of the concentration of that active form by RNA attachment. Further limiting the significance of the findings, whether this interaction has any biological significance on the physiology or infectivity of the PSM producer remains largely unexplored.

Further remarks:

• Circumstantial evidence based on the "amyloid inhibitor", EGCG: The results with EGCG, which has been shown to have a moderate amyloid-reducing effect on PSMalpha 1 and PSMalpha4, should not be taken as evidence for amyloid-based cytotoxicity. While increased concentrations of EGCG reduced the cytotoxic effect of PSMalpha3, it is not convincingly shown that this is due to a lower concentration of amyloid vs. monomeric PSM.

• It is appreciated that the authors refrain from presenting the unsubstantiated concept of "functional" PSM amyloids in the discussion. However, wording in that direction must also be removed from other parts of the manuscript (e.g. "bioactive fibrillar polymorphs". "The formation of cross-alpha amyloids has been correlated with toxic activity", etc.), generally refraining from uncritically implying that amyloid formation underlies PSM biological activity, and rather discussing that the much more likely explanation of the findings is a lowering of cytolytically active, monomeric PSM concentration.

• Discussion: "PSM alpha3 interaction with nucleic acids within human cells ...supports a comparable mechanism...". Delete. Unsubstantiated.

• The authors should cite papers that have argued against their hypothesis and not only their own manuscripts.

Reviewer #2 (Public review):

Summary:

This study presents a detailed single-cell transcriptomic analysis of the post-natal development of mouse anterior chamber tissues. The dataset is robust, consisting of ~130,000 cells collected across seven time points from early post-natal development to adult. Analysis focused on the development of cells that comprise Schlemm's Canal (SC) and trabecular meshwork (TM).

Comments on revisions:

My critiques have been adequately addressed.

Reviewer #1 (Public review):

Summary:

The authors show that if they generate a weighted multi-conformer ensemble of structural models to fit crystallographic electron density data, the application of statistical mechanical methodologies to that ensemble can provide reasonable estimates of configurational entropy terms related to protein-ligand binding.

Strengths:

A fair range of proteins (12) and ligands (70) is included in the study. The analytical methodologies are well described. Both successful and less successful analytical approaches are discussed, and the latter are frequently as insightful as the former.

Weaknesses:

Compared to the universe of protein-ligand complexes, this dataset is inevitably very limited, so the generality of the observations made here remains speculative. Though a fair range of proteins is studied, the dynamic range in the binding affinity data is limited. The practical utility of the approach is never really commented on.

Reviewer #2 (Public review):

The manuscript by Miller and Wankowicz (M&W) develops a crystallographic approach to predict the contribution of protein conformational entropy to the total binding entropy using multi-conformer ensemble models. The approach loosely follows the path developed by Wand using NMR relaxation methods. Their approach is to generate local crystallographic order parameters (analogous to NMR order parameters) to estimate protein conformational entropy and then combine this with statements about water entropy. The static view of the ensemble is perhaps easier to grasp, with respect to entropy, than the NMR-based dynamical view. This approach is potentially ground-breaking and of great importance given the ease, relative to NMR, with which the source data can be obtained. However, the approach has several deficiencies, only some of which are noted by the authors.

Like the initial Wand approach (Frederick et al Nature, 2007), M&W develop a simple counting relationship between members of the ensemble and a statement about conformational entropy. For reasons that are not clear, M&W utilize "per residue" scaling, which was initially introduced by Wand but later discarded for the more physically meaningful "per torsion angle" scaling. As noted in the Nature 2007 paper, this assumes uncorrelated occupancy. The current Wand approach (Caro et al PNAS, 2017) subsumes correlated occupancy and potentially incomplete sampling of the ensemble into an empirically determined scaling parameter (sd). This is likely a major contributor to the mysterious 1/4 scaling factor that is introduced. It is not clear to me how discrete conformational states are counted from the qFit models. Using the B-factor, as opposed to a thermal factor, to account for motion in a rotamer well seems suspect. With some irony, M&W only look at chi-1 rotamers in distinct contrast to the NMR approach, which looks at the end of the side chain, which captures the entire disorder. On the other hand, the crystallographic approach "sees" all side chains, whereas the NMR approach, as currently rendered, looks only at methyl-bearing side chains and requires coupling to neighbors to report on all side chains (see Kasinath JACS 2013 and Wand & Sharp ARB 2018).

Nevertheless, as noted by Nature 2007, the fact that a linear relationship is seen between the apparent conformational entropy and total binding entropy suggests that the former is a major component of the latter. It also reinforces the idea that dSrt is constant for higher affinity complexes, i.e., residual rigid-body motion of protein relative to ligand is limited (a conclusion reached in PNAS 2017) but not mentioned. This is an important result.

The classic hydrophobic effect is potentially a significant component of total binding entropy. Here, the manuscript falls flat by focusing on crystallographically resolved waters. As shown in site-resolved detail (Nucci et al, NSMB 2011 and others), hydration water has a range of residual motion (entropy) that will modulate contributions to water entropy upon displacement from an interface. A very clear example of the potential for large contributions was demonstrated in the wet interface of a barnase-DNA complex (PNAS 2017). The fact that the classic dASA treatment failed, I think, points to problems elsewhere in the approach.

I note that the range of ligand types explored by M&W is quite limited as compared to PNAS 2017, making generalization somewhat difficult (see Wand Cur. Opin. Struct. Biol, 2013 for why this is important). Finally, it is disappointing that the authors chose not to examine systems common to PNAS 2017, making direct comparison to the NMR method impossible.

In summary, this manuscript sets the field in a new direction. It is a first serious look at conformational entropy using crystallographic approaches. If fully validated, this approach would permit an explosion of insight since the crystallography is now straightforward, very fast and capable of approaching larger systems, relative to the NMR approach. However, there are missing quantitative elements represented by a formal relationship that is fitted by the data. I do not think this is a fatal flaw for this manuscript, however. If the supplementary material is improved for clarity and completeness (e.g, include tables of thermodynamic data; conformer analysis; B-factors) such that all figures could be independently reproduced and therefore analyzed in different ways, and the comments made above are addressed, if not resolved, then I think this manuscript could become a keystone for this new direction.

Reviewer #1 (Public review):

Matsumoto et al. identify Com2, a C2H2-type zinc finger transcription factor not previously linked to sphingolipid metabolism, as a regulator of this pathway in budding yeast. They show that depletion of sphingolipids by myriocin, an inhibitor of serine palmitoyl transferase, increases Com2 expression. This, in turn, promotes the expression of the protein kinase Ypk1 and enhances TORC2-dependent phosphorylation of Ypk1. The authors identify a Com2-binding site in the YPK1 promoter and provide evidence that Com2 functions upstream of Ypk1 to regulate its<br /> expression. They further report that Com2 abundance is controlled by the ubiquitin-proteasome system: degradation of Com2 is inhibited by myriocin treatment and enhanced by phytosphingosine. Mutational analyses of putative phosphorylation and ubiquitination sites support a role for these modifications in regulating Com2 stability. Based on these findings, the authors propose that Com2 acts as a transcriptional regulator of sphingolipid metabolism that responds to sphingolipid levels and promotes Ypk1 expression.

Strengths:

This study provides a valuable finding on the regulation of sphingolipid synthesis by the transcription factor Com2 in budding yeast. The evidence supporting the authors' claims is solid, although additional evidence clarifying the mechanisms and biological significance of ubiquitin-proteasome-mediated degradation of Com2 would strengthen the work. This work will be of interest to microbiologists studying budding yeast.

Weaknesses:

The biological significance of Com2 degradation is not sufficiently clear, which represents an important limitation of the study. It would also be important to determine whether Com2 is actively degraded under normal growth conditions, such as during logarithmic growth in the absence of drug treatment.

Reviewer #2 (Public review):

Summary:

In this study, Matsumoto and co-workers use budding yeast as a model organism to identify and characterize transcriptional mechanisms that homeostatically regulate sphingolipid metabolism. Through a genetic suppressor screen and a series of genetic, molecular, and biochemical analyses, they identify the transcription factor Com2 as a key regulator that responds to sphingolipid levels and regulates the expression of genes such as YPK1, which in turn controls the activity of several enzymes in the yeast sphingolipid biosynthetic pathway.

Com2 itself is further regulated by the ubiquitin proteasome system in response to sphingolipid levels. High sphingolipid levels promote proteasomal degradation of Com2, whereas low sphingolipid levels stabilize Com2. These findings suggest that Com2 is a central component of a feedback system that helps maintain sphingolipid homeostasis.

Strengths:

The identification of Com2 as an upstream regulator of the TORC2-Ypk1 pathway is supported by multiple orthogonal lines of evidence. The authors also provide mechanistic insight into how Com2 protein levels are dynamically controlled through phosphorylation and ubiquitin-mediated degradation. Stabilization of Com2 in response to sphingolipid depletion appears to be required for the transcriptional upregulation of YPK1 expression.

Weaknesses:

Although several important questions remain unresolved, such as which kinases function upstream of Com2 and which ubiquitin ligase(s) target Com2, this work is nevertheless likely to have a meaningful impact on the field of sphingolipid metabolism. The identification of a regulated transcription factor that responds to sphingolipid levels may also be of broader interest to researchers studying membrane homeostasis.

Reviewer #3 (Public review):

This paper extends the authors' 2022 studies of how the synthesis of membrane sphingolipids is regulated in budding yeast. Here, they hypothesized that overexpression of a protein involved in sphingolipid (SL) biosynthesis would confer resistance of lip1-1 cells, which are Dox-inducibly defective in expression of a ceramide synthase regulatory subunit, to myriocin (Myr), a serine palmitoyltransferase inhibitor that inhibits SL synthesis. To test this idea, they transformed lip1-1 cells with a multi-copy genomic library, selecting for Myr resistance. Apart from LIP1 itself and YPK1, a protein kinase downstream of TORC2, COM2, which encodes the Com2 C2H2-type zinc finger transcription factor, was the most frequent hit in the screen. They went on to show that com2Δ cells exhibited Myr sensitivity, and that Com2 protein expression was induced under conditions that reduced complex sphingolipid synthesis, such as Myr-treatment. Using ypk1-as ypk2Δ cells and the 3-MB-PP1 Ypk1as a selective Ypk1as kinase inhibitor, they showed that Com2 phosphorylation was independent of Ypk1 activity, suggesting that Ypk1 lies downstream of Com2. Consistently, Myr treatment, which reduces SL synthesis, resulted in an increase in both Com2 and Ypk1 proteins. By generating a Ptet-off-GFP-COM2 strain they showed that when Dox was removed to induce GFP-Com2 overexpression, Myr resistance was increased. They went on to show that Com2 binds to a Com2 response element in the YPK1 promoter and drives expression of Ypk1. This was confirmed by showing that expression of a YPK1-driven lacZ reporter gene was also elevated when GFP-Com2 overexpression was induced. CRISPR deletion of the putative Com2-binding site (CBS) from the endogenous YPK1 promoter was used to generate PYPK1-ΔCBS cells, which showed a significant reduction in Ypk1 expression and exhibited intermediate Myr sensitivity, suggesting that Com2 is important for but not the only regulator of Ypk1 expression. Analysis of SL levels showed that they largely paralleled the levels of Ypk1 protein and active pT662 Ypk1. Using deletion analysis of the COM2 gene, they showed that residues 2-190 and the C-terminal DNA binding domain of Com2 were essential for Com2 function in the SL synthesis pathway. Deletion of {greater than or equal to}40 amino acids from the N-terminus increased expression of Com2 protein irrespective of Myr treatment, suggesting that Com2 protein levels are regulated by protein stability. Consistently, they found the high level of Com2 protein induced by Myr was rapidly reversed by treatment with phytosphingosine (PHS), a ceramide precursor that bypasses the Myr-blocked step and restores SL synthesis. The reduction in Com2 protein plus PHS was prevented by MG132 proteasome inhibitor treatment and led to the accumulation of polyUb-Com2 species, consistent with Com2 being negatively regulated by SL-induced UPS-mediated degradation. Based on the use of selective inhibitors of different steps in SL synthesis, they showed that SL biosynthesis up to the level of MIPC (mannnosyldiinositol phosphorylceramide) is required for the SL-mediated degradation response. Based on individual and combined K to R mutagenesis of the three Lys in Com2 1-49, they showed that K23, K35 and K51 in combination are needed for PHS-induced Com2 degradation, and therefore are likely to be the main Com2 Ub sites. Finally, they observed that PHS induced an increase in K3R Com2 phosphorylation, finding that an S/T10A mutant was only weakly phosphorylated and was resistant to PHS-induced degradation, suggesting that phosphorylation of Com2 is required for PHS-dependent degradation.

The paper is clearly written, and the data in Figures 1-6 show convincingly that the Com2 zinc finger protein, by inducing the expression of a set of genes, including YPK1 and LCB1, plays an important role in sphingolipid (SL) homeostasis in yeast under conditions when sphingolipid levels are low. However, the data in Figures 7 and 8, where the authors provide evidence that the Com2 protein was rapidly degraded in a proteasome-dependent manner in response to phytosphingosine (PHS) treatment, dependent on the N-terminal 40 residues of Com2 and a combination of three Lys residues in this region, are intriguing but incomplete. There are a number of issues, including the identity of the Com2 ubiquitylation sites. They showed that the K23/35/51R Com2 mutant was stabilized, but did they provide direct evidence that these three Lys are in fact ubiquitylated (e.g. GG-K peptide enrichment based MS analysis of Ub-Com2 from PHS-treated, MG132-treated cells). They showed that PHS treatment increased Myc13-tagged Com2 ubiquitylation in the presence of MG132, but did not show that the K3R Com2 mutant (or the S/T10A phosphorylation site Com2 mutant) failed to be ubiquitylated. They also found that the WT Com2 and particularly the K3R Com2 mutant protein exhibited hyperphosphorylation in response to PHS treatment, and that mutation of 10 potential pSer sites to Ala abolished this effect, and stabilized the Com2 protein. However, it is unclear whether the K3R mutation led to increased Com2 hyperphosphorylation per se following PHS treatment, or whether this is because there is more K3R protein, as they suggest might be the case. It is also not clear what protein kinase is responsible or how it might be activated when SL levels are high. In addition, the E3 Ub ligase needed for Com2 degradation was not identified, and it is not clear whether Com2 phosphorylation is directly involved in its recognition by a phosphodependent E3 Ub ligase, as they propose in the model shown in Figure 9. Finally, and perhaps most importantly. It is unclear how elevated levels of phytosphingosine or any sphingolipid are sensed by the Com2 pathway in order to switch on the degradation response as a negative feedback event. The model depicted in Figure 9 exposes all of these unknowns. The paper would be significantly strengthened by additional experiments defining how complex SL levels are sensed, how Com2 is phosphorylated in response to SL sensor signals, and how (phospho)Com1 is recognized for ubiquitylation and degradation.

In summary, the finding that the Com2 zinc finger transcription factor is an upstream regulator of the sphingolipid biosynthesis pathway in budding yeast, acting as part of an SL sensor system to maintain sphingolipid homeostasis, is new and potentially important. However, more mechanistic work needs to be done to address the unanswered questions raised by the data in Figures 7 and 8.

Reviewer #1 (Public review):

Summary:

This paper asks how the NK cell receptor KIR2DL4 binds HLA-G and undergoes endocytosis. The authors propose that an allosteric disulfide-bond switch controls whether the receptor is in a ligand-binding or non-binding state, and they support this model using mutagenesis, imaging, mass spectrometry, and structural prediction.

Strengths:

A major strength is the use of diverse, complementary approaches to validate the central claim. The authors combined unbiased random mutagenesis to identify key residues, confocal microscopy to track cellular localization , and mass spectrometry to quantify the redox states of specific disulfide bonds. These methods consistently support a single model: an allosteric disulfide switch. The transition between a Cys10-Cys28 bond and a Cys28-Cys74 bond serves as a functional switch that controls whether the receptor resides at the plasma membrane to bind ligand or remains inactive in endosomes.

Weaknesses:

The core model is interesting, but some of the strongest mechanistic claims still rely heavily on structure prediction rather than direct structural evidence, especially the proposed HLA-G contact surface in Figure 6.

The paper supports an effect of the disulfide state on trafficking and uptake, but the case for direct KIR2DL4-HLA-G binding still feels somewhat indirect. The manuscript itself notes that direct binding had not been previously shown, and the current explanation partly depends on inference about which disulfide state is present.

Most of the main experiments are done in transfected 293T cells, so it is still not fully clear how strongly this mechanism carries over to the more relevant NK-cell setting discussed in the paper.

The cellular evidence for the PDI story is not specific, since it depends a lot on inhibitor and blocking experiments that could affect the broader extracellular redox environment.

Reviewer #2 (Public review):

Summary:

Rajagopalan et al show how extracellular domain features regulate KIR2DL4 internalization. The trafficking phenotypes of cysteine mutants are logically organized, and well-summarized in a Table. The disulfide mapping and differential alkylation strategy are appropriate and provide strong support for alternative disulfide configurations in D0. The higher accessibility or more selective reduction of Cys10-Cys28 as compared to Cys28-Cys74 by PDI is a key mechanistic anchor.

Strengths:

The identification of a conformational switch in KIR2DL4 is conceptually novel. Experimental elegance, detailed and well-written.

Weaknesses:

Most of the mechanistic work was shown in HEK293. The authors should exhibit relevance using primary NK cells (using primary NK)

Reviewer #1 (Public review):

Summary:

Sun et al. generated germline-specific cKO mice for the Znhit1 gene and examined its effect on male meiosis. The authors found that the loss of Znhit1 affects the transcriptional activation of pachytene. Znhit1 is a subunit of the SRCAP chromatin remodeling complex and a depositor of H2AZ, and in cKO spermatocytes, H2AZ is not deposited into the gene region. The authors claim that this is why the PGA was not activated. These findings provide important insights into the mechanisms of transcriptional regulation during the meiotic prophase.

Strengths:

The authors used samples from their original mouse model, analyzing both the epigenome and the transcriptome in detail using diverse NGS analyses to gain new insights into PGA. The quality of the results appeared excellent.

Comments on revisions:

Sun et al. have responded to each comment with great care and sincerity, and substantial improvements are evident.

In particular, the addition of scRNA-seq data from P35 samples appears to play an important role in supporting the authors' claims.

However, there is still room for improvement in the reanalysis of the data and in the Discussion section.

From the data perspective, for example, the authors state in line 347 of the revised manuscript that "We found that Znhit1-deficient spermatocytes phenocopied abnormal meiotic phenotypes observed in A-MYB mutants." However, the corresponding descriptions in the main text and figure legends are not sufficiently detailed, and therefore do not fully support or substantiate this interpretation. Incorporating a statistical comparison between DEGs in Znhit1-sKO and A-myb KO would likely strengthen this point.

Regarding the overall structure of the Discussion, the connections among delayed DSB repair, MSCI, and PGA regulation via H2A.Z remain somewhat descriptive and difficult to follow. This may reflect a lack of direct evidence linking these processes; however, a more logically structured and clearly articulated Discussion would improve clarity.

Reviewer #2 (Public review):

Summary:

The study demonstrates that Znhit1 regulates male meiosis, with deletion causing pachytene failure associated with defective expression of pachytene genes and subtle effects on X-Y pairing and DSB repair. The authors attribute this phenotype to the defective incorporation of the Znhit1 target H2A.Z into chromatin.

Strengths:

The paper and the figures are well presented and the narrative is clear. Evidence that the conditional deletion strategy removes Znhit1 is strong, with multiple orthogonal approaches used. Most of the meiotic phenotyping is well performed, and the omics analysis clearly identifies a dramatic effect on the meiotic gene expression program. The link to H2A.Z and A-MYB adds a mechanistic angle to the study.

Comments on revisions:

In the revision, the authors have addressed most of my comments. The only incomplete one is comment 1, where I asked them to define the stage of germ cell arrest by histology. I requested this because the stage of arrest they identified is so unique. They didn't do it, and instead used the scRNAseq to show a depletion at the late pachytene stage onwards. I guess it supports their main findings, but it's a bit disappointing.

Reviewer #1 (Public review):

Summary:

Al Asafen and colleagues here apply a set of scanning fluorescence correlation spectroscopic approaches (Raster Image Correlation Spectroscopy (RICS), cross-correlation RICS, and pair correlation function spectroscopy) to address the nucleo-cytoplasmic kinetics of the Dorsal (Dl) transcription factor in early Drosophila embryos. The Toll/Dl system has long been appreciated to establish dorsal-ventral polarity of the embryo through Toll-dependent control of Dl nuclear localization, and represents one of a handful of model morphogen gradients produced with high enough precision to yield robust biophysical measurements of general transcription factor activity and function. By measurement of GFP-tagged Dl protein, either in wild-type embryos, or in mutant embryos with low/medium/high levels of Toll signaling, the authors report diffusivity of Dl in nuclear and cytoplasmic compartments, as well as the fraction of mobile and immobile Dl, which can be correlated with DNA binding through cross-correlation RICS. A model is presented where Cactus/IkB is implicated in preventing Dl from binding to DNA.

Strengths:

The study uses raster image correlation spectroscopy approaches to measure biophysical components of the Dl gradient in Drosophila embryos. It convincingly demonstrates a positive correlation between Toll pathway activity and the fraction of bound Dl in the nucleus. RICS methodology has widespread potential applications in cell and developmental biology, and this study will contribute to its adoption.

Weaknesses:

The study seeks to test a hypothesis for how the Toll pathway may limit Dl DNA binding in the nucleus. This experiment, while producing initial support for a role of nuclear Cactus, is confounded by co-expression of wild-type Dl, thus limiting the interpretation of the experimental results.

Reviewer #2 (Public review):

Summary:

In this manuscript, Al Asafen, Clark et al. use fluorescence correlation spectroscopy (FCS) to quantitatively analyze the mobility of Dl along the DV axis of the early Drosophila embryo. Dl is essential for dorsal-ventral (DV) patterning and its gradient initiates the activation of several genes and thereby orchestrates the formation of the Drosophila body plan. While the mechanisms underlying Dl gradient formation have been extensively studied, there are some observations for which there is not yet a mechanistic explanation. For example, the peak of the Dl gradient grows continuously during nuclear cycles 10-14. This is likely due to Cact-dependent Dl diffusion and Dl binding to DNA. But the biophysical parameters governing Dl nuclear dynamics that would support these claims have not been previously measured. In this work, the authors separated GFP-tagged Dl into a mobile and an immobile pools. Interestingly, the fraction of immobile Dl is position-dependent, revealing more binding to DNA in ventral than in dorsal nuclei. This is either due to higher binding affinity in ventral locations (due to Toll-dependent Dl phosphorylation) or to higher Dl-Cact binding in dorsal nuclei that would prevent Dl to bind DNA. Using specific dl alleles, authors support the latter hypothesis.

Strengths:

The manuscript is well written and their conclusions are convincingly supported by their methodology and analysis. As a quantitative study, the biophysical analysis seems rigorous, in general.

Although this is not the first study that employs FSC to investigate the dynamics of a morphogen, it further exemplifies how these quantitative tools can be used to uncover mechanistic aspects of morphogen dynamics during development. In particular, the manuscript reports novel biophysical parameters of Dl dynamics that will be helpful in future hypotheses-driven modeling studies.

Weaknesses:

The main weakness of the manuscript is that the main biological implication of the study, namely that the asymmetry in the fraction of immobile Dl is a result of nuclear Dl-Cact binding which prevents Dl to bind DNA (Figure 5), occurs in a region of the embryo where there is very little Dl anyways (Figure 1A). While it is interesting that a small fraction of immobile Dl significantly increases in dorsal nuclei in mutants expressing a form of Dl with reduced Cact binding it is unclear what is the biological impact of this effect in a location where Dl is nearly absent.

Another weakness of the study, is that experiments are performed in the presence of a wild-type GFP-tagged Dl (unfortunately, the Dl gradient does not form without it; Supplemental Figure 4). This is an unfortunate technical limitation, because it cannot allow to test how important Cact binding is for determining the amount of Dl that could bind DNA in more biologically-relevant locations of the embryo (e.g., in lateral regions).

Overall, I feel that the manuscript exemplify how FSC methods and analysis can be used for the estimation of biophysical parameters and test biological hypothesis, even under very low concentrations (such as Dl in dorsal-most nuclei). However, due to technical limitations, it falls short in offering a real quantitative understanding of their proposed mechanisms. The authors did not report in Figure 5, what happens to the fraction of Dl bound to DNA in lateral regions in the reduced Cact binding and reduced Toll phosphorylation mutants.

Reviewer #1 (Public review):

Summary:

In this manuscript, Chen, Tu, and Lu focused on how brain-wide dopamine release dynamically changes during sleep/wake state transitions. Using multi-site fiber photometry to monitor DA release, alongside simultaneous EEG and EMG recordings, the authors show distinct DA dynamics during transitions from NREM to WAKE, REM to WAKE, WAKE to NREM, and NREM to REM. Next, they analyze temporal coordination between regions using cross-correlation analysis. Finally, chemogenetic activation of VTA or DRN but not SNc dopamine neurons is shown to promote wakefulness.

Strengths:

The manuscript addresses an interesting question: how brainwide dopamine activity evolves across sleep/wake transitions. The combination of multi-site DA recordings with simultaneous EEG/EMG monitoring is technically sophisticated. The experimental logic is generally clear, and the dataset is rich. The result has several interesting observations.

Weaknesses:

The authors used the GRAB-DA2m sensor to monitor dopamine release. Although DA2m exhibits higher affinity for dopamine compared to NE (around 15-fold difference in EC50 in HEK cell assays), it is still possible that NE contributes to the recorded signals, particularly during sleep/wake transitions when locus coeruleus activity is strongly modulated. Given the widespread and state-dependent dynamics of NE, this potentially needs to be addressed.

Similarly, the chemogenetic experiments rely on CNO to activate hM3Dq-expressing dopamine neurons. However, it is well established that CNO can be converted to clozapine in rodents, and clozapine itself is known to influence sleep/wake. Although the authors included non-hM3Dq-expressing mice as controls, the potential confounding effects of clozapine on sleep regulation remain a concern.

Midbrain dopamine neurons exhibit both tonic and phasic firing patterns. In Figure 1, most reported dopamine transitions appear relatively slow. However, some faster, phasic-like components are observable. For example, in NAc-L during REM-to-WAKE transitions, there are 2 phasic-like decreases between −20 and 0 s. The authors used laser-evoked stimulation experiments in the VTA and DRN and showed that 2 s versus 10 s stimulation produces distinct dopamine kinetics, suggesting that different firing patterns generate distinct DA dynamics. Moreover, the temporal profiles vary not only across regions but also across transitions within the same region. For example, in CeA, the NREM-to-WAKE transition shows a relatively rapid decrease, whereas REM-to-WAKE displays a much slower decline. Similarly, some regions (e.g., NAc-L NREM-to-WAKE, DRN REM-to-WAKE) show faster changes, while others (e.g., mPFC WAKE-to-NREM, VTA NREM-to-WAKE) show slower kinetics. These observations argue against a simple region-specific explanation and instead suggest that distinct firing modes may differentially contribute depending on transition type.

While cross-correlation analysis provides insight into the temporal coordination of DA signals across regions, several limitations should be considered. Sleep/wake transitions are inherently non-stationary events, whereas cross-correlation assumes relatively stable signal properties within the analysis window. This mismatch may bias lag estimates and obscure transient lead-lag relationships. Moreover, the temporal resolution of fiber photometry and the kinetics of genetically encoded DA sensors limit the precision with which timing relationships can be interpreted, particularly for sub-second lags.

In the Introduction, the authors state that they aim to address 'which dopaminergic populations causally drive these patterns.' However, the chemogenetic approach used operates on a relatively slow timescale: CNO-induced activation takes 15-30 minutes to produce effects, and the induced changes are long-lasting. In contrast, the dopamine transitions described in Figure 1 occur on a much faster timescale compared to CNO manipulation. Thus, while chemogenetic activation demonstrates that stimulating VTA or DRN dopamine neurons promotes wakefulness, it does not directly establish that these populations causally drive the rapid transition-related DA dynamics observed in the photometry recordings.

Reviewer #2 (Public review):

In "Brainwide dopamine dynamics across sleep-wake transitions", Chen et al. provide a thorough description of how dopamine dynamics fluctuate across sleep-wake transitions and in transitions between sleep states. To achieve this, the authors used multi-channel fiber photometry and a genetically encoded fluorescent dopamine reporter to simultaneously measure dopamine dynamics in 8 brain regions. They also used EEG measurements to precisely quantify and time transitions between sleep states and wakefulness. Finally, the authors used channelrhodopsin to examine dopamine dynamics following subregion stimulation and chemogenetics to test the causal relationship between activation of distinct dopamine neuron populations and their effects on sleep state.

The conclusions made by the authors in this study are modest and appropriate given the largely observational nature of the principal findings. The use of optogenetics to probe regional dopamine signaling following activation of distinct nuclei is interesting, but not entirely novel and constrained in interpretability. Similarly, the chemogenetics experiment largely confirms previous studies, which the authors correctly cited in the text.

The principal findings of this study are based on strong methodological and analytical methods. Implanting 8 optical fibers in a single mouse, along with EEG/EMG electrodes, is technically challenging, providing valuable, simultaneous measurements of dopamine fluctuations across the brain. This enables the strong correlational and time-locked analyses performed by the authors in Figure 2. What's more, the use of EEG/EMG electrodes provides time-locked descriptions of sleep states, enabling precise comparisons between the dopamine signal and sleep state transitions.

The paper has some weaknesses that the authors could address. The analyses in Figure 1 could be strengthened to show how dopamine changes during transitions between specific sleep states. The injection sites for channelrhodopsin and chemogenetic viruses could be validated to strengthen the interpretation of those results. Also, a stronger justification for the experiments conducted in Figure 3 could be provided, as they seem unrelated to the present study.

Overall, this study has strong descriptive power, convincingly showing how dopamine fluctuates across sleep states. Some of the other aspects of the paper, however, are somewhat limited in novelty and interpretation.

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. The 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.

Weaknesses:

The scientific study needs a bit of in-depth analysis with respect to consistency in Kd and its implications on the mechanism.

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 have three major points and a few minor criticisms.

Major points:

(1) The main weakness is that the authors base their conclusions on a very limited set of FRET pairs. While TmrAB has been extensively studied in terms of its structure, the authors should at least acknowledge this limitation more clearly.

(2) Most smFRET distributions were fitted with one, two, or three Gaussians. However, in several cases, additional populations with noticeable amplitudes appear to be present (e.g., Figure 3c at 0.1 mM and 3 mM ATP; Figure 4a, apo; Figure 4c, 0.3 mM R9L). Could the authors clarify why these populations were not included in the analysis?

(3) Figure 3c (3 mM ATP): Is it truly possible to distinguish the two states in this distribution?

Reviewer #2 (Public review):

Summary:

Chen and colleagues conducted a cross-sectional longitudinal study, administering high-definition transcranial direct stimulation (HD-tDCS) targeting the left DLPFC to examine the effect of HD-tDCS on real-world procrastination behavior. They find that seven sessions of active neuromodulation to the left DLPFC elicited greater modulation of procrastination measures (e.g., task-execution willingness, procrastination rates, task aversiveness, outcome value) relative to sham. They show that HD-tDCS reduces task aversiveness and increases task-execution willingness on real-world tasks as quantified by intensive experience sampling methods, providing causal evidence for the role of DLPFC in modulating contextual features to delaying or completing one's goals.

Strengths:

• This is a well-designed protocol with rigorous administration of high-definition transcranial direct current stimulation across multiple sessions. The intensive experience sampling approach which probes and assesses self-relevant task goals is innovative and aims to address an important question regarding the specific role of DLPFC in modulating specific features of chronic procrastination behavior (e.g., task-execution willingness, task aversiveness).

• The quantification of task aversiveness through AUC metrics is a clever approach to account for the temporal dynamics of task aversiveness, which is notoriously difficult to quantify.

Weaknesses:

• While the findings that neurostimulation reduces procrastination behavior is compelling, there remain several alternative interpretations for these effects. For example, it could be that the task-execution willingness isn't increased per se, but rather that the goal completion becomes more valuable as participants learn from feedback or become more aware of their successful attainment of or failure to complete task goals. It is unclear whether the effects could be driven by improved working memory or attention to the reported tasks (and this limitation is addressed by the authors). In short, it is also difficult to examine the temporal dynamics of how these goals are selected across time.

• It is unclear whether the current evidence support long-retention of this neurostimulation intervention. The study includes one 6-month timepoint after the study to examine the long-term retention of the neural stimulation effect. Future studies that evaluate the long-term effects across multiple time points would strengthen the evidence for the robustness of this intervention.

Reviewer #1 (Public review):

Summary:

This is an interesting study describing intensity changes of lamellipodial Arp2/3 complex incorporation dependent on the substratum the cells are spreading on (PLL vs fibronectin), but also on manipulation of either contractility or osmotic pressure or even external mechanical load exerted onto cells, e.g., by increasing medium viscosity. The authors use quite fancy cell systems for their studies, first of all, a CRISPR-engineered fibroblast cell line in which both endogenous loci of the Arp2/3 complex subunit Arpc2 are tagged with mScarlet, but at the same time, conditionally removable using tamoxifen. These lines, optionally also harboring Pxn-GFP and Lifeact-miRFP670, have previously been described by the authors (Chandra et al, 2022, PMID: 34861242). In addition, they use cells allowing local photoactivation of Rac signalling through a Tiam1 activation module combined with Halo-tagged Arpc2, apparently stably co-expressed in tamoxifen-treated Arpc2-KO fibroblasts. These cells may or may not have been published previously.

Overall, the study provides convincing evidence that Arp2/3 complex accumulation in the lamellipodium negatively correlates with its width and perhaps the mechanical load these actin networks are exposed to at the leading edge membrane, shown initially through allowing cells to spread on substrates in which the formation of integrin-based adhesions is poor (PLL) or stimulated (through fibronectin). In the latter case, lamellipodia are comparably narrow, perhaps reasonably well clutched, and thus feel sufficient counter-force at the leading edge membrane to build a dense, Arp2/3-dependent actin network. Albeit interesting and important to show as the authors did, these results are not entirely surprising given the literature published on actin remodeling in cells in conditions similar to those used by the authors (i.e., on PLL). Thus, the results should be better embedded into the context of this previous literature to more precisely reveal which aspects are new and interesting and which ones are more or less intuitive and expected.

However, the authors also show yet another result, which is quite spectacular indeed, revealing dramatic local protrusion of a Rac-dependent lamellipodium on PLL only in the presence of methylcellulose, but not on PLL alone. Although the authors cannot fully explain the mechanisms causing these results, they are thought-provoking and will certainly stimulate future, relevant research on this topic and new insights. Altogether, I think this is an interesting study that can be shared rapidly, given that the authors provide more experimental detail and transparency concerning their used cell model systems. Aside from a few other suggestions for amendments and corrections, I would also recommend citing classical literature that has provided the basis for the interpretation of the results shown here, as specified below.

Specific criticism and comments:

(1) I feel the paper is interesting for actin remodeling and Arp2/3 complex aficionados, but quite difficult to read and to understand in places for non-experts in the field, so I think the text requires more detailed explanation of specific terms, model systems used, and overall correction of either grammatical or semantic errors, or colloquial language.

(2) In general, I think the characterization of Arp2/3 complex incorporation into the lamellipodia of cells spreading on PLL versus FN is interesting, as it has not been done previously in such a systematic fashion to my knowledge. However, I think the authors could emphasize better how this relates to previously established structural features of actin filament networks, published on PLL. So more than 3 decades ago, Hotchin & Hall published clear evidence that starved fibroblasts can only form focal complexes or adhesions downstream of PDGF or LPA-stimulation if seeded on FN, but not on PLL (see Figure 1 in PMID: 8557752). Around the same time, Flinn and Ridley showed this virtual absence of classical, Rac-dependent focal complexes to be accompanied by the formation of beautiful, broad lamellipodia (see Fig. 1A in PMID: 8743960), which only formed in the absence of excess RhoA activity and thus contractility by the way (see also below). A few years later, Small et al summarized all these phenotypes in a comprehensive review and also showed that cells on PLL (similar to the rapidly migrating keratocytes) combined large, flat lamellipodia with tiny, nascent adhesions scattered throughout these structures (see Figure 2 in PMID: 10047522). These authors also noted that the sole inhibitor-mediated reduction of contractility could switch FN-phenotypes with narrow, ruffling lamellipodia and peripheral focal complexes back to a PLL-type phenotype of broad lamellipodia (see Figure 1 in PMID: 10047522). In the following decade then, different labs (Verkhovsky, Bershadsky, Vavylonis, Watanabe et al) showed beautiful phase contrast or fluorescence movies illustrating that the broad lamellipodial phenotype of cells plated on PLL was accompanied by low frequency membrane ruffling and instead a rapid, continuous rearward flow of continuously assembling actin filament networks, partly also directly shown with actin networks labeled with both LifeAct and Arp2/3 complex subunits (see e.g. PMIDs 18800171 and 22500749). In Alexandrova et al, 2008 (PMID 18800171), authors showed that the formation of adhesions in spreading cells triggers the transition from fast to slow flow (which is of course relevant to the current study and conclusions), whereas Ryan et al, 2012 (PMID 22500749) already established the broad incorporation of actin and Arp2/3 complex into the very broad lamellipodia formed on PLL by Xenopus fibroblasts and the rapid flow of both components from distal to proximal lamellipodial regions. None of these seminal studies has been cited, although they are highly relevant for the interpretation and conclusions of the results presented. I would strongly recommend specifically referring to these studies, as this will actually support the conclusions and interpretations drawn.

(3) On the subject of literature, on the second page of the intro, end of 2nd paragraph, the authors describe Rac signaling to Arp2/3 complex through WRC considered essential for Arp2/3-mediated actin assembly at lamellipodial leading edges, but aside from one of their own papers cite none of the seminal studies by Insall, Scita, Stradal, Rottner, Bogdan labs having published seminal aspects on this pathway.

Considering the rapid F-actin flow in lamellipodia, obviously accompanied by admittedly sparse but continuous Arp2/3 complex incorporation, it is not so surprising that the latter will be obligatory here, and also the accumulation of its prominent activator WRC, as well as the branch stabilizer cortactin. Thus, the data described on page 3 of the Results section could also be framed in the context of all this previously published knowledge, providing a more comprehensive and realistic view of the relevance and novelty of the described data.

(4) In the abstract, the authors state in the context of the force-feedback mechanism established in vitro for the formation of Arp2/3 complex-dependent actin networks that "this phenomenon has not been explored through the examination of real-time responses of endogenous actin networks in cells". In my view, this is not correct, as in their prominent Cell paper, the Sixt laboratory has done exactly that (Mueller et al, 2017, PMID: 18800171). Although Mueller et al have not looked at Arp2/3 complex dynamics as far as I recall, they have still connected the extent and hence intensity of actin networks at the leading edges of keratocyte lamellipodia with the forces exerted onto them, including direct experimental manipulation of those forces. Although the study has been cited in an independent context, this point should be made clear, and the corresponding sentence in the abstract should be amended.

(5) One point that struck me a little bit was the authors' detailed description of cell spreading on PLL and the quite strong variability of Arp2/3 incorporation dependent on the timing after spreading (as for instance the very strong and quite narrow Arp2/3 leading edge intensity at 2 hours post-seeding in Figure 3S2D). In the authors' view, they have worked with a very clean system, as they emphasized to even have eliminated the FN-locus in their cells, excluding the secretion of endogenous FN (PMID: 34861242), but how about ECM components potentially present in serum, such as, for instance, vitronectin? Indeed, it looks like the authors have done all experiments in the presence of 10% serum as far as I can see, although most of the classical PLL-experiments mentioned above have been performed with starved cells in the absence of serum. I think it would generate a more complete picture of the phenotypes and results as compared to the literature if the authors performed a subset of the key experiments on PLL without serum. I don't think the starving of cells as such is important and could be counteracted by simply lamellipodia-inducing growth factors adding into the spreading medium, traditionally perhaps PDGF or EGF (dependent on the receptor distribution of those fibroblasts), but the absence of serum would have two advantages: it would not only exclude any potential impact of serum-containing ECM components, but also alleviate the hyperstimulation of the Rho-pathway through LPA-bound BSA, the major serum-protein, which has previously been shown to counteract the "undisturbed" formation of PLL-type lamellipodia (see Figure 1B in Flinn & Ridley, PMID: 8743960).

(6) Regarding the scanning EM-images shown in the Supplement, currently called Figure 3S2A and -B (in the text erroneously termed Figures 3S1A and-B, see above). I am not sure how representative these individual EM-images of the cell plated on PLL are, given the data of rapid rearward flow of actin and Arp2/3 complex subunits, at least at early stages of spreading. Again, the classical literature on PLL-type lamellipodia and, in particular, previously published movies of such lamellipodia suggest broad lamellipodia with few ruffles, and the opposite with cells plated on FN. So in this context, the scanning EM-data shown on both PLL and FN do neither fit the authors' own data very well nor the literature, and I would recommend making sure that the individual cells selected were (i) correctly annotated and (ii) representative of a specific time point of spreading actually fitting the previously described data.

(7) It also surprised me to see that the authors describe the spreading process on PLL to actually be much slower than on FN (see Figure 3S2C - in the text Figure 3S1C). It is tempting to speculate that this might change if plating the cells in serum-free medium, as traditionally, full spreading and lamellipodia formation downstream of PDGF-stimulation (at least in 3T3 fibroblasts) is described to occur in the range of 10-30 minutes at maximum, and not several hours as shown here. This point could also be considered, or at least discussed.

(8) The movies are of very high quality and beautiful to look at, but it would help the reader to get a bit more information in the legends (like the meaning of the time-stamps, which will display elapsed time in minutes:seconds I assume, but this info is missing from the legends as far as I can see. Also, it would help the reader to better mark in the movies when a specific treatment kicks in. For instance, in movie 10, the legend states treatment starts at 10:00 (minutes:seconds?), but it would help very much if the authors could paste the term "blebbistatin" directly into the movie, beginning with the frame of treatment start.

Reviewer #2 (Public review):

The authors work with endogenously labeled Arp2/3 complexes in mouse fibroblast cell lines plated on surfaces coated with fibronectin or poly-L-lysine. They observe increased retrograde flow, but decreased actin and Arp2/3 densities, in the absence of integrin-based adhesions. Interestingly, they further find that an increase in branching density can be achieved in the absence of adhesion by a diverse set of perturbations, including blebbistatin, physical compression under agarose, and methylcellulose-mediated increases in extracellular viscosity. Although all of these conditions are likely to have pleiotropic effects on cell physiology and signaling, one plausible common denominator is that they promote cell spreading and may thereby increase membrane tension.

This study addresses a question of broad interest. The relationship between protrusive actin assembly, resisting forces, and membrane tension has received considerable attention in recent years (for a recent overview, see PMID: 38991476). Earlier work established that branched actin networks can respond to force by increasing network density in vitro (PMID: 26771487; PMID: 35748355), and pioneering work from the Sixt laboratory showed that keratocyte lamellipodia adapt to resisting forces by increasing actin density in cells (PMID: 28867286). Against that background, the manuscript contains novel and insightful observations. At the same time, the current version would be strengthened by a more rigorous mechanistic analysis and by clearer reporting of experimental systems and statistics.

Major points:

(1) Engagement with prior work on membrane tension and protrusion.

The relationship between protrusive actin assembly and membrane tension is a subject of major current interest (PMID: 38991476), and it is unfortunate that the authors do not engage more fully with seminal prior work on this subject. In particular, work from the Weiner laboratory showed that membrane tension can act as an inhibitor of cell protrusion and branched actin assembly, at least in some cell types (PMID: 22265410; PMID: 37311454). In addition, a membrane-tension-sensitive signaling pathway involving PLD2 and mTORC2 has been proposed to mediate this negative feedback (PMID: 27280401). These findings appear, at least at first glance, to contrast with the model advanced here, in which elevated membrane tension is associated with increased branching density. A more explicit discussion of these findings and of the apparent differences between systems would be essential. Testing the relevance of some of the proposed negative-feedback regulators, for example, mTORC2 or PLD2, under at least some conditions expected to increase membrane tension would substantially strengthen the manuscript.

(2) The central assumption regarding membrane tension should be tested directly.

Part of the model put forward by the authors rests on the assumption that most of the perturbations used to promote cell spreading, with the exception of hyperosmotic treatment, also increase membrane tension. This is a testable hypothesis. Multiple mechanical and optical methods have been established for this purpose, including tether pulling, micropipette aspiration, and fluorescent membrane-tension probes. Directly measuring membrane tension under at least a subset of the key perturbations would significantly strengthen the manuscript.

(3) WAVE and cortactin localization should be quantified.

The claim that WAVE and cortactin localization are independent of fibronectin-integrin engagement (Figure 2A-B) deserves to be established quantitatively. I appreciate that some variability is expected because these experiments use exogenous fluorescently tagged constructs, but the current presentation relies too heavily on representative kymographs. Quantitative analysis would make this conclusion more convincing.

(4) The interpretation of the increased-viscosity experiments needs stronger physical justification.

I am aware of the recent high-profile work showing that elevated extracellular viscosity can promote migration (PMID: 36323783), and the present manuscript is clearly supporting this. However, the physical basis for this perturbation is neither well reasoned nor explained clearly enough here. The authors use 0.6% methylcellulose of the 1500 cP grade (the relevant viscosity of the final medium should be stated explicitly btw!). Estimating the added viscosity at 7 cP = 0.007 Pa·s (up from 1 to 8 cP), one can formulate the rough back-of-the-envelope calculation for the added viscous stress:

delta τ = delta η v/h

where τ= viscous stress (Pa = pN/µm²), η = viscosity, v= protrusion speed, h = characteristic shear length scale. For cells protruding at 1 um/min, this resistance will be 0.00001-0.001 Pa. Even if the cells would protrude 100 times faster, the resistance would not exceed one pascal! Hence, the added bulk viscous stress opposing protrusion at this viscosity appears negligible relative to the known force-generating capacity of lamellipodia. This does not invalidate the biological phenotype, but it does suggest that the interpretation should be much more careful.

(5) Cell lines and experimental systems are insufficiently described.

Most biological experiments in this manuscript appear to have been performed in engineered mouse fibroblast lines, but the Methods do not provide sufficient clarity about which specific cell lines were used in which experiments. More concerning, the manuscript refers inconsistently to the base model as both a mouse dermal fibroblast line and MEFs, while the only clearly distinct named line appears to be JR20 fibroblasts used for traction-force microscopy. Along similar lines, the Arp2/3 knockout cells in Figure 2 are not adequately explained in the Results, Methods, or figure legends, regarding how these cells were generated or how the knockout was validated. The authors only later note in the Discussion that these conditional knockouts were described in an earlier paper. In general, the manuscript would benefit from much more explicit reporting of which cell line or derivative was used in each experiment.

(6) Some experiments and quantifications appear to suffer from limited replication.

For example, the optogenetic Rac activation experiment in Figure 2E appears to have been performed possibly only for a single cell per condition, since the raw intensity traces are shown without clear indicators of variability. If that reading is correct, this is below the standard typically expected for mechanistic support and seriously reduces confidence in the strength of this particular conclusion.

(7) Statistical reporting needs clarification.

Although the Methods state that the graphs show 95% confidence intervals, the manuscript does not clearly define the underlying statistical unit for many quantified datasets. In several figures, sample sizes are reported as numbers of cells pooled across only two or three independent experiments, but it is not clear whether the authors performed statistical analyses on pooled single-cell measurements or on experiment-level means. The authors should explicitly state for each quantified panel what n represents, what the error bars denote, which statistical test was used, and whether the analyses were performed on per-cell values or on independent experimental replicates.

(8) The Discussion is rather expansive relative to the amount of experimental evidence presented.

Parts of the Discussion feel more speculative and interpretive than necessary, and the manuscript would be strengthened by focusing the Discussion more tightly on the principal findings, limitations, and immediate implications of the work.

Reviewer #3 (Public review):

Summary:

Butler et al. investigated how different force mechanisms influence Arp2/3-related branched actin networks at the leading edge of lamellipodial protrusions in mouse dermal fibroblasts. In particular, their study aimed at characterizing the specific contribution and interplay between load force and adhesion signaling on the regulation of branched actin networks in live-cell experiments using endogenously one-labeled Arp2/3 subunit. A key finding of their work is that by plating fibroblasts on two different substrates supporting or not integrin engagement, they observe striking differences in branched network architectures that cannot be explained solely by integrin signaling. Instead, several of their results point to mechanical feedback resulting from changes in membrane tension during spreading, regulating the density of branched actin networks. Finally, by modifying the extracellular viscosity, the authors suggest that the stress generated at the actin-membrane interface would play a key role in regulating branched actin density in protrusions.

Major Strengths:

(1) The combination of methods used in this paper (endogenous labeling of Arp2/3, Arp2/3 genetic knockout, optogenetic activation of Rac) provides a unique opportunity to monitor spatial and temporal reorganization of endogenous branched networks generated by Arp2/3 in live cells in response to different biochemical and mechanical manipulations.

(2) The authors provide a deep characterization of the actin-network organization and dynamics observed when plating cells on different substrates, engaging or not integrins (Figure 1 and associated supplementary: intensity and width of the signal in protrusions, retrograde flow, incorporation of actin to the edge, nascent focal adhesions), which serves as a strong basis to build the rest of the paper. They also offer a comprehensive analysis of the different parameters that could explain the lack of dense branched actin network at the leading edge of fibroblasts grown on PLL-coated surfaces (they exclude the contribution of reduced branch nucleation by NPF or insufficient branch stabilization in Figure 2, the insufficient integrin-mediated signaling activating NPF in Figure 2).

(3) After having ruled out the influence of adhesion signaling in the regulation of branched actin-network density at the leading edge of the cells, the authors demonstrate that the enrichment of Arp2/3 at the leading edge is evolving together with cell spreading, suggesting a possible role of membrane tension in the process (Figure 3 and associated supplementary). To prove their point, they tested numerous methods to promote adhesion-independent cell spreading (Figures 4 to 6), while describing well the limitations of each of these techniques. These methods included promoting rapid spreading on PLL-coated substrate using blebbistatin or physical compression under agarose, and finally increasing extracellular viscosity by treating cells with methylcellulose. All of these treatments led to very consistent results upon the increase in membrane tension, supporting the idea of membrane tension controlling the branched actin organization of cells. This conclusion was further supported by an experiment (Figure 4 S1) in which a hyper-osmotic shock was performed, increasing the actin-membrane interface stress while keeping the spreading area of cells, which led to a drastic increase in Arp2/3 density at the protrusions.

(4) By activating Rac optogenetically in cells plated on PLL treated with methylcellulose (Figure 8), the authors observe the formation of robust protrusions enriched in Arp2/3, showing that increased extracellular viscosity can bypass the requirement for ECM proteins to activate protrusion driven by signaling.

Weaknesses:

(1) Although the lamellipodial architecture in cells plated on PLL appears very different from the one developed by cells grown on fibronectin (Figure 1, wider and less homogenous), the branched network is still present, and one may wonder how these differences can affect the functionality of the lamellipodia (for example, by measuring the impact on migration in 2D and 3D systems).

(2) To explain the differences observed in the branched actin networks developed by cells on PLL and FN, the authors envision several hypotheses, among which signaling factors or branched-promoting factors would be decreased in the absence of integrin adhesions. They could have, in addition, assessed actin network dynamics and turnover (we could imagine that competition between Arp2/3- and non-Arp2/3- driven structures could be different in the presence or absence of adhesions, the competition being nicely visible from Figure 2B and 2C, where, in the absence of Arp2/3, cells form prominent filopodia).

(3) All of the methods used to apply physical forces on barbed ends have their own caveats and alter not only membrane tension (but the limitations are discussed in the paper). The paper may have benefited from micropatterning the cells to either reduce or force the spreading of cells in a controlled fashion. In addition, the conclusions on levels of interface stress between plasma-membrane and the barbed-ends of actin lamellipodial networks rely on an estimate of the effect of perturbations rather than on actual measurements of these stress levels.

Likely impact of the work on the field, and the utility of the methods and data to the community:

Although the finding that branched actin networks respond to the application of physical force by increasing their density was already known from previous in vitro studies, this paper offers a detailed and compelling characterization of the reorganization of endogenously labelled branched actin networks upon different mechanical perturbations. In addition to showing the effect of increased extracellular viscosity on promoting branched actin network densification in the absence of ECM, this paper sheds new light on the interplay between signaling and mechanics in regulating protrusion and spreading. While the authors show that both signaling and mechanical feedback are important regulators of branched actin regulation and cell spreading, they demonstrate that optogenetic Rac activation is not sufficient to trigger branch network formation in the absence of sufficient mechanical support. They thus propose that biochemical signaling would act at a different level than mechanics by promoting protrusion persistence and coherence. This work will therefore impact the field of cell biology in offering a new perspective to understand the interplay between mechanical and biochemical feedback in 2D and 3D migration. It may also have broader implications as the formation of branched actin networks under the regulation by mechanical loads has been shown to be involved in other processes such as endocytosis.

Reviewer #1 (Public review):

Summary:

Yuan and colleagues present a thorough study of gene activation before and during metamorphosis in sponge larvae, combining in-depth analyses of staged transcriptomes and chromatin accessibility profiling (ATACseq). Amongst several very interesting findings, the study reveals that the acquisition of settlement competence, which arises in response to decreasing light at sunset, is characterized by changes in chromatin accessibility that anticipate strong transcriptional shifts occurring as metamorphosis starts. Another notable finding is a set of transcription factors amongst the genes strongly up-regulated at the onset of metamorphosis. In addition, larvae exposed to constant light, a condition that stalls metamorphosis, were found to activate metabolic pathways that are not normally expressed in swimming larvae. Together, the findings provide a rare level of understanding into how environmental conditions can promote deployment of alternative developmental programs in planktonic larvae.

Strengths:

This is a very comprehensive, well-documented and rigorous study of a phenomenon of wide interest. It will inspire researchers working on other species to look for similar, environmentally-driven "anticipatory" epigenetic mechanisms. It also provides a wealth of detailed information on genes, notably transcription factors, that are candidates for involvement in regulating specific metamorphosis transitions - and beyond. The data presented here are thus undoubtedly a rich and valuable resource.

Weaknesses:

I see no significant weaknesses; however, the documentation of the data is very compressed, with all the findings contained in 4 multi-panel figures with succinct legends. It is not always straightforward to connect the conclusion statements in the text to the figures. Although the relevant data is available in supplementary files, I would appreciate more help in navigating the data to assess the support for key conclusions, if possible, illustrating each text conclusion explicitly in the main figures.

Reviewer #2 (Public review):

Summary:

It is demonstrated that sponge larvae prepare for receiving the environmental cue (sunset) by extensively modifying their chromatin accessibility in the vicinity of genes that are going to be regulated during metamorphosis, in the absence of large gene expression changes. This program can be offset by modifying the cue (making light constant), leading to a novel molecular state.

Strengths:

This is a top-notch study of a key lifecycle transition in an organism of great phylogenetic importance, involving concurrent gene expression and chromatic accessibility profiling (to the best of my knowledge, this has never been done in non-bilaterians and likely anywhere outside Vertebrata). The result is highly non-trivial. There is also an additional experiment modifying the key environmental cue (constant light), adding additional insight.

Weaknesses:

I have only a couple of suggestions.

(1) Not all new pre-emptively opened OCR regions are associated with genes that are going to be regulated during metamorphosis. Is their association with such genes statistically significant? (Fisher's exact test?)

(2) Re: extended discussion on possible reasons for activation of specific transcription factor families. I feel it is not terribly useful since it is hardly more than guesswork. The authors should consider condensing this part to better emphasize the major (and most unexpected) large-scale regulation patterns.

(3) Re: enrichment analysis based on significant genes (Figure 1H): Even though it is a common practice, there is nuance: as we all know very well, many genes pass a significance threshold not because they are highly differentially regulated (i.e., show large fold-change), but because they are more abundantly expressed overall and so the statistical power for them is greater. A good example is ribosomes - before we realized what was happening, they would show up as enriched in almost every experiment of ours, which was not very useful since their fold-change was quite trivial. I see the authors have ribosome enrichment too, and I suspect there are a few more functional groups that made it because they tend to express highly on average. Ideally, we want to see what is enriched among highly regulated genes, not among abundantly expressed genes. Because of this we moved to compute enrichment based only on fold-change, using the GO_MWU package (https://github.com/z0on/GO_MWU). I suggest authors give it a shot, to see if the enrichment results become more interpretable. GO_MWU is also very powerful to analyze enrichment in WGCNA modules, in case the authors want to try that.

Reviewer #3 (Public review):

Summary:

In their manuscript, Huifang Yan and colleagues perform RNA-seq (CEL-seq) and ATAC-seq experiments to profile the transcriptome and chromatin accessibility of sponge larvae across larval competence, settlement and early postlarval development. Amphimedon, the sponge species that they use, is amenable to lab experiments and can therefore be a convenient model for experimenting with this otherwise difficult to assay ecological parameters and cues. They had previously observed that light conditions (diminished light) at sunset are critical for larvae to enter a pre-settlement stage and prime them for settlement and metamorphosis. In this paper, they report that these conditions induce a gain of accessibility in many genes, including transcription factors, and that altering these conditions by providing continuous light at sunset affects this reprogramming event.

Strengths:

The above is a very interesting observation, one that the authors speculate could have a broader significance and be a theme in many more larvae. I agree with the authors that this is an important finding, and I think that the paper will be interesting for a broad readership. If this is the case, the authors open up a new theme of chromatin regulation, extensively studied in mammalian contexts, but severely understudied in pretty much every other context.

Weaknesses:

I think, however, that their paper often reports the data in a difficult-to-follow way, and that other sorts of analyses would have made the results more accessible for a broad readership. Here, I present some suggestions that the authors might want to take into account to improve their results.

Reviewer #1 (Public review):

Objectives of the study and impact of the work:

The authors of this article primarily aim to reconstruct the evolutionary history of the insect odorant receptor (OR) family, which is responsible for the detection of odorant signals by olfactory neurons. Due to the lack of phylogenetic signal present in the sequences of this multigene family, which evolves very rapidly, phylogenetic analyses have so far never made it possible to precisely retrace how ORs diversified prior to the appearance of present-day insect orders, and what the drivers of this diversification were. For example, one may suspect that the adaptation of ORs to odors emitted by plants constituted a critical step in insect evolution during the "angiosperm terrestrial revolution," which occurred at the end of the Cretaceous, but nothing currently allows this to be asserted.

There are very nice examples, notably in Drosophilids, derived from comparisons between closely related species and documenting mechanisms of OR adaptation to certain signals. However, what the authors attempt to do in this work is to produce a macroevolutionary analysis at the scale of insects as a whole, based almost exclusively on bioinformatic analyses. To do this, they annotated OR genes in about one hundred insect species and developed pipelines for analyzing sequence similarity, structural similarity, and functional similarity, the latter being estimated through a molecular docking approach. An important feature in the evolution of insect ORs is the emergence of a unique co-receptor, called Orco, which appears to be an OR that has lost the ability to bind odorants. In addition to the large-scale bioinformatic analysis, the authors also aim to explore more specifically the factors that favored the emergence of Orco and the selective advantage conferred by the existence of OR-Orco complexes.

Given the importance of odorant receptors in insect biology and in their adaptation to different environments and lifestyles, retracing their evolutionary history is indeed a major question in evolutionary biology. In principle, this type of work therefore has the potential to become a reference in the field and to provide a basis for significant scientific advances.

Major strengths and weaknesses:

The sampling chosen for collecting OR sequences is very impressive, with more than 100 insect families represented, covering most of the major orders. This sampling appears appropriate for the question being addressed. The analysis pipeline used to collect the sequences makes sense, relying on homology-based annotation tools coupled with a structure-based filter. Nevertheless, one can note aberrant numbers of ORs for certain species (much lower than reality), which indicates that the pipeline probably did not function correctly for all genomes. In the absence of a validation step comparing the results with already known OR repertoires, it is difficult to estimate the overall quality of the data. The authors chose to apply a fairly stringent filter on sequence quality (based on predicted 3D structure), which reduces the number from 14,000 to 9,000. This choice seems logical given the subsequent use of these data, but it inevitably leads to data loss. The fact that some OR genes may be missing and that the total number may not be exact for each species is not prohibitive for studying the evolution of the family at a broad scale; however, it calls into question certain results that rely on this total number, such as the correlation between the number of ORs and genome size, lifestyle, and diet.

From the dataset collected, the authors attempted to categorize ORs in several ways, starting with the reconstruction of sequence similarity networks. The approach is interesting, but in the end, the results do not seem to be sufficiently exploited, and it is not obvious what the advantage of this approach is compared with the "classical" phylogenetic approach, which generally fails to reveal homology relationships between ORs from species belonging to different insect orders. Here again, the majority of the clusters identified are "order-specific," and when this is not the case, the authors did not attempt to exploit the results. For example, clusters SeqC26 or SeqC28, which appear to be shared by many insects, are potentially very interesting. It might have been relevant to combine this similarity-based clustering approach with phylogenetic reconstructions within each shared cluster.

The clustering based on structure also leads to the identification of a majority of "order-specific" clusters, but once again, the clusters shared by several orders are not truly exploited, which does not provide new insight into the evolution of ORs. However, the authors highlight a group of ORs in flies that appear to possess an unusual intracellular region. This is interesting, although it is a result more relevant to OR structure than to their evolution. The function of these ORs in Drosophila melanogaster, if it is known, is not discussed.

The analysis of structural diversity then leads the authors to focus on the Orco co-receptors, which are characterized by modifications of the binding pocket and the emergence of an extracellular loop that could explain the loss of the ability to bind odorant molecules. This part, which relies on in vitro experiments, is interesting and constitutes the most striking result of the study, which could in itself have been the subject of a separate manuscript. However, the molecular dynamics modelling does not add anything in the way it is conducted (5 ns is too short).

The rest of the manuscript is based on the prediction of OR response spectra using molecular docking. The work that has been carried out is extremely substantial, and the objective of linking clusters based on sequence similarity or 3D structural similarity with functional categories is entirely relevant. Nevertheless, I see two major problems with this in silico functional analysis:

(1) The docking score threshold used was chosen thoughtfully, which is very good, and according to the calculation performed, should ensure a true positive rate of more than 20%, which is excellent in such a docking analysis. But in the absence of functional validation, this 20% true positive rate is not sufficient to extrapolate OR function as the authors do in the remainder of the manuscript. The risk of error remains too high to compare in such detail the function of ORs from insects with different lifestyles or diets.

(2) The six functional clusters identified are only slightly different from one another, with similar detection of all chemical families except acids and amines (which was expected, given that these families are a priori detected by IRs rather than ORs). This shows that even though the approach is relevant and deserves to be tested, it cannot be used to establish a link between groups/lineages of ORs and response spectra at the scale of insects as a whole. This is reflected in the final analysis by the fact that there is no visible link between sequence or structural clusters and functional clusters. Given the uncertainty surrounding the docking results, the entire subsequent analysis of the relationship between the Binding Breadth Index and ecological variables is highly questionable.

Finally, the evolutionary analysis proposed to conclude that the work suffers from an incorrect interpretation: ORs of non-holometabolous insects cannot be considered equivalent to those of species that existed before the Permian-Triassic extinction. The fact that a locust or a cockroach has more narrowly tuned ORs than holometabolous insects does not mean that this was also the case for ancestral insects. To advance this type of conclusion, it would be necessary to conduct a phylogenetic analysis and reconstruct ancestral states, which is not the case here.

In summary, despite the large number of analyses performed, the authors do not succeed in achieving the stated objective of reconstructing the evolutionary history of insect ORs, and the results obtained do not sufficiently support the conclusions regarding the links between OR repertoires and environment or lifestyle.

Reviewer #2 (Public review):

The remarkable evolvability of the olfactory system enables animals to rapidly adapt to dynamic and chemically complex environments. Over the past two decades, substantial effort has been devoted to uncovering the evolutionary principles that drive the diversification of odorant receptors (ORs), yielding key insights into the forces shaping their striking variability in both vertebrates and insects. In this manuscript, Zhang and colleagues analyze the OR repertoires of over 100 insect species, leveraging sequence and structural similarity to infer patterns of gene family evolution within this diverse and ecologically important clade. By integrating sequence-based and structure-based comparisons, their study builds on a compelling and recently emerging line of research made possible by the advent of AlphaFold, which has previously clarified the phylogenetic relationship between insect Ors and the gustatory receptor gene family and revealed the unexpectedly deep evolutionary origins of this ancient structural fold.

Applying this approach to a large set of ORs derived from species throughout the insect phylogeny, the authors confirm many previously reported patterns of OR evolution. Unfortunately, the way these results are presented lacks clarity in what is already known from previous work in the field versus what is a novel finding based on the analysis of this dataset.

It is unclear how complete the odorant receptor sets are. I recommend benchmarking the pipeline by comparing its output to a gold standard and a frequently vetted complete OR set, such as that of Robertson and Wanner 2006 or similar.

Using their structural clustering approach, the authors identify a structural feature mostly unique to the OR co-receptor ORco, a beta-sheet in EL2, which they functionally show reduces odorant binding affinity - a key aspect of ORco, which does not bind ligands in the ancestral ligand-binding site. This is a particularly strong part of the manuscript, since the authors support their in silico-derived hypothesis with functional data.

Lastly, in an attempt to assess the relationship between sequence identity and structure on one hand and function on the other, the authors perform an in silico structure prediction and chemical docking analysis. As it stands, this part is on the more speculative side since the docking approach has not been verified with available functional datasets.

Reviewer #1 (Public review):

Summary:

Dancausse et al. investigate behavioral responses to nicotine exposure in Drosophila larvae. They discover that high concentrations of nicotine lead to less movement and twitching, which recover slowly after several hours. Exposure to lower concentrations, however, increases locomotion and leads to hyperactive behavior. The authors also perform pharmacological and genetic manipulations to address the role of dopamine for these behavioral changes. Additionally, they test the role of MB intrinsic neurons by genetic silencing. Both Dopamine and MB manipulations affect responses to nicotine exposure. Finally, they investigate how larvae respond to repeated exposures to nicotine and find that they do not habituate. Additionally, repeated exposure to nicotine leads to a preference towards higher concentrations in a gradient assay.

Strengths:

The authors use rigorous behavioral analysis and discover interesting concentration and experience-dependent effects of nicotine exposure on locomotion in fly larvae, which will be worth investigating in the future to decipher the underlying neural mechanism.

Weaknesses:

As the manuscript currently stands, the results of genetic manipulations are hard to interpret and rather inconclusive. The genetic manipulations have been performed using broadly expressing genetic driver lines, which weakens the conclusions drawn by the authors. Thus, no specific neural populations or brain regions have been discovered, and there is little insight into the underlying neural mechanism.

Based on gradient experiments, the authors suggest that fly larvae could serve as a model organism for addiction. This claim is quite strong, but no control experiments are shown for shorter exposure or a single exposure with a longer resting period before the gradient test. To compare this to addiction-like behaviors, more control experiments should be performed.

The authors should clarify better how experiments were performed in Materials and Methods. Generally, the authors perform novel behavioral analysis, which is not explained in enough detail. The nicotine concentration that has been used for most experiments is this a relevant concentration comparable to other studies? This information would be useful to put into context with other findings.

Reviewer #2 (Public review):

Summary:

CNS function relies on a balance of excitatory and inhibitory activity. Use of addictive stimulants such as nicotine results in a chronic imbalance of these activities, and often this activity acts through dopamine pathways. To address how stimulants cause dysfunctional signaling in the DA neurotransmitter system and how this impacts neural circuit activity and behavior, the authors of this study begin to establish Drosophila larvae as a model for studying nicotine exposure.

They focus on three questions:<br /> (1) In what ways does nicotine-driven hyperactivation modulate behavior?<br /> (2) What roles do neural circuits play in these responses?<br /> (3) What are the mechanisms of drug dependence and addiction-like plasticity?

To this end, the authors use high-resolution behavioral, genetic, and pharmacological methods.

The authors show that exposure to nicotine alters the behavioral repertoire of larval Drosophila, with effects that are long-lasting (hours) and dose-dependent. Most of the study uses a 5-minute exposure to "moderate" levels of nicotine because this dosage produces the greatest potentiation of larval crawling speed. Concomitant with increases in crawling speed, they find alterations in other behavioral parameters-crawl "efficiency" and turn rate are reduced; whereas head swings are faster and more likely to be accepted. They find that reducing the activity of dopaminergic neurons reverses the valence of behavioral change upon exposure to nicotine. For example, crawling speed is decreased upon nicotine exposure in a Ple>Kir2.1 manipulation in comparison to controls. Moreover, they demonstrate that the effect of nicotine on the quantified set of behaviors depends on dopamine signaling. Beyond implicating dopamine signaling, they implicate the mushroom body, and particularly the gamma-neurons, in mediating exposure to nicotine.

The authors further probe how nicotine exposure alters larval behavior. First, they determine what happens to crawling speed with multiple exposures, finding sustained higher crawling speeds relative to controls. Second, as a model for addition-like behavior, they examine larval behavior on a nicotine gradient after repeated nicotine exposure. The data in Figure 7D are particularly compelling, showing that after nicotine exposure, larvae prefer high concentrations of nicotine.

Strengths:

In a concise set of experiments, the authors demonstrate a nicotine-induced behavioral change, its interaction with a neurotransmitter system, and a locus of action within the CNS. Thus, the authors set the stage for the use of Drosophila larvae as a model to better understand addiction-related behaviors.

Weaknesses:

This is a clear advance for the field of larval neurogenetics, but the extent to which it changes the way we think about nicotine exposure more generally is less clear. Nonetheless, the authors clearly achieved the goal they set out to attain.

Reviewer #3 (Public review):

Summary:

Dancausse et al. examine behavioral responses to nicotine administration in larvae. The study first distinguishes between spasms and extreme hyperexcitability elicited at high doses from a hyperactivity state triggered at lower (~1 mM feeding) doses. They then focus on the hyperactivity state and examine if dopaminergic neuron function is involved (via transgenic and pharmacological manipulations). Next, the role of the Mushroom body, a site of integration in the larval brain, is interrogated. In these studies, the authors use multiple approaches to draw complementary conclusions. The last section examines the effect of repeated nicotine exposure and of nicotine preference following repeated exposure. The findings are foundational for future studies looking to use Drosophila larvae as a system to study nicotine addiction.

Strengths:

Overall, I think the study is of broad importance. The neurogenetics community gets valuable insight into how ACh excitation interplays with DA signaling to regulate movement. For the addiction community, the work describes a valuable system to further interrogate genetic and environmental factors potentially driving addiction under well-controlled conditions. The quantitative analysis is generally well done, and the use of multiple experimental strategies to buttress conclusions is commendable.

Weaknesses:

(1) Conceptual point. Insects use ACh as the primary excitatory neurotransmitter, with nAChRs broadly expressed, while vertebrates use Glutamate in this role. (Arguably, nicotine expression in tobacco plants evolved as an insecticide, broadly disrupting the central excitatory neurotransmitter.) In vertebrates, central ACh neurons are relatively sparse - primarily originating from the basal forebrain.

Based on these distinctions, it is important to consider/contrast nicotine-driven hyperexcitation from other methods to produce broad hyperexcitation (e.g., inhibition of GABA, high K+, elevated temperature, etc). Many of these methods to induce hyperexcitability would also modulate DA circuitry.

A discussion of the role of ACh in insect vs. vertebrate brains is necessary to interpret the experimental design and findings with regard to addiction. These points should be addressed in the intro and discussion.

(2) (Figure 1) Relatedly, how do the behaviors elicited in Figure 1B (30 or 60 mM) compare to the convulsions described following electroshock stimulation to induce a seizure? My suspicion is that you're essentially triggering a seizure (or seizures) in these larvae.

(3) (Figure 4) Is a statistical analysis between the CS, Ple>Kir, Ple, and Kir locomotion at baseline done? Presumably, these manipulations would alter the intrinsic activity levels of the larvae?

(4) (General quantitative question) How do the parameters co-vary across individuals following nicotine admin? Crawl speed and peristalsis frequency are analyzed. Turning doesn't seem to be considered. Do individuals that show large increases in velocity also show the largest reductions in turn rate? Are these relations preserved following the DA metabolism and MB function interventions?

(5) (Discussion / general question) Beyond DA, other monoamines are involved in regulating larval locomotion - OA and TA are a clear example from Fox et al. (2006). Could the authors comment on whether they would expect similar findings in other neurotransmitter systems or if these neurotransmitter systems are involved in the ACh -> DA interplay studied here?

(6) (Discussion) Following the establishment of nicotine preference, do larvae exhibit signs of 'withdrawal' or changes in baseline behavior when deprived of nicotine? For example, in Figure 6, does the speed following nic administration ever 'go below' the H2O line?

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors investigate how the anterior claustrum may integrate temporally separated task-relevant signals to guide behavior in a delayed escape paradigm. Because in vivo neural recordings from claustrum during this task are extremely limited-comprising single-trial data with small neuronal samples-the authors adopt a modeling-driven approach. They train recurrent neural networks (RNNs) using only behavioral data (escape latency) to reproduce task performance and then analyze the internal dynamics of the trained networks. Within these networks, they identify a subset of units whose activity exhibits persistent responses and strong correlations with behavior, which the authors label as "claustrum-like." Using dimensionality reduction, decoding, and information-theoretic analyses, they argue that these units dynamically integrate conditioned stimulus (CS) and door-opening signals via nonlinear, trajectory-based population dynamics rather than fixed-point attractor states.

To bridge model predictions and biology, the authors complement the modeling with in vitro slice experiments demonstrating recurrent excitatory connectivity and prolonged activity in the anterior claustrum that depends on glutamatergic transmission. They further compare latent neural trajectories derived from previously published in vivo claustrum recordings to those observed in the RNN, reporting qualitative similarities. Based on these results, the authors propose that the claustrum implements temporal signal integration through recurrent excitatory circuitry and dynamic population trajectories, potentially supporting broader theories of integrative brain function.

Strengths:

This study addresses an important and challenging problem: how to infer population-level computation in a brain structure for which in vivo data are sparse and experimentally constrained. The authors are commendably transparent about these limitations and seek to overcome them through a principled modeling framework. The integration of behavioral modeling, RNN analysis, and slice electrophysiology is ambitious and technically sophisticated.

Several aspects stand out as strengths. First, the behavioral RNN is carefully trained and interrogated using a rich set of modern analytical tools, including cross-temporal decoding, trajectory analysis, and partial information decomposition, providing multiple complementary views of network dynamics. Second, the slice experiments convincingly demonstrate recurrent excitatory connectivity in anterior claustrum, lending biological plausibility to the model's reliance on recurrent dynamics. Third, the manuscript is clearly written, logically organized, and conceptually engaging, and it offers a coherent mechanistic hypothesis that could guide future large-scale recording experiments.

Importantly, the work has significant heuristic value: rather than merely fitting data, it attempts to generate testable computational ideas about claustral function in a regime where direct empirical access is currently limited.

Weaknesses:

Despite these strengths, the manuscript suffers from a recurring and substantial conceptual issue: systematic over-interpretation of model-data correspondence. While the modeling results are potentially insightful, the extent to which they are presented as recapitulating real claustral neural mechanisms goes beyond what the available data can support.

A fundamental limitation is that the RNN is trained solely on behavioral output, without being constrained by neural data at either single-unit or population levels. As a result, the internal network dynamics are underdetermined and non-unique. Many distinct internal solutions could plausibly generate identical behavior. However, the manuscript frequently treats the specific internal solution discovered in the RNN as if it were a close approximation of the actual claustrum circuit.

This issue is compounded by the sparse nature of the in vivo data used for comparison. The GPFA-based trajectory analyses rely on pseudo-populations and single-trial recordings, yet are interpreted as evidence for robust population-level dynamics. Because neurons were not recorded simultaneously, the inferred trajectories necessarily lack true population covariance and shared trial-to-trial variability, limiting their interpretability as genuine population dynamics. Similarly, conclusions about trajectory-based versus attractor-based computation are drawn almost exclusively from model analyses and then generalized to the biological system.

Overall, while the modeling framework is appropriate as a hypothesis-generating tool, the manuscript repeatedly crosses the line from proposing plausible mechanisms to asserting explanatory or even causal equivalence between the model and the brain. This undermines the otherwise strong contributions of the work.

Below are several specific points that warrant further clarification or revision:

(1) Tone of model-data correspondence

Numerous statements describe the RNN as "closely mimicking," "recapitulating," or being "nearly identical" to claustral neural dynamics, sometimes extending to claims about causal relationships between neural activity and behavior. Given that neural data were not used to train the model, and that only a small subset of trained networks showed the reported dynamics, these statements should be substantially softened throughout the manuscript. The RNN should be framed as providing one possible computational realization consistent with existing data, not as a close instantiation of the biological circuit.

(2) Non-uniqueness of RNN solutions

The fact that only a small fraction of trained networks exhibited "claustrum-like" clusters deserves deeper discussion. This observation raises the possibility that the identified solution is fragile or highly specific rather than canonical. The authors should explicitly discuss the non-uniqueness of internal solutions in behavior-trained RNNs, including the range of alternative network dynamics that can reproduce the same behavior. In particular, it should be clarified why the specific network exhibiting "claustrum-like" clusters is informative about claustral computation, rather than representing one arbitrary solution among many.

(3) GPFA trajectory comparisons

The qualitative similarity between RNN trajectories and GPFA-derived trajectories from sparse in vivo data is interesting but insufficient to support claims of robustness or population-level structure. Statements suggesting that these patterns are unlikely to arise from noise or random fluctuations are not justified given the single-trial, pseudo-population nature of the data. Either additional quantitative controls should be added, or the interpretation should be substantially tempered.

(4) Scope of functional claims

The discussion connecting the findings to broad theories of claustral function, global workspace, or consciousness extends well beyond the data presented. These speculative links should be clearly labeled as such and significantly reduced in strength and prominence.

The manuscript repeatedly describes the delayed escape task as an "inference-based behavioral paradigm" and states that animals "infer that a value-neutral alternative space is likely to be safer" when the CS is presented in a novel environment. While I appreciate that the US-CS association was established in a different context and that the CS is then presented in a new environment, I am not convinced that the current behavioral evidence uniquely supports an inference interpretation.

First, it is not clear that this task is widely recognized in the literature as a canonical inference task, in the sense of, for example, sensory preconditioning, transitive inference, or model-based inference paradigms. Rather, the observed effect-that CS animals escape faster to a neutral compartment than neutral-CS controls-can be parsimoniously interpreted in terms of generalized threat value, heightened fear/anxiety, or a bias toward avoidance/escape under elevated threat, without requiring an explicit inferential step about the specific safety of the alternative compartment. The fact that no prior training is needed is compatible with flexible generalization, but does not by itself demonstrate inference in a more formal computational sense.

Second, the inference claim becomes central to the manuscript's conceptual framing (e.g., the idea that rsCla supports "inference-based escape"), yet the behavioral analyses presented here and in the cited prior work do not clearly rule out simpler accounts. Clarifying this distinction would help avoid overstating both the inferential nature of the behavior and the specific role of rsCla and the RNN's "claustrum-like" cluster in supporting inference per se, as opposed to more general integration of threat-related signals with an opportunity for escape.

This manuscript presents an interesting and potentially valuable modeling-based framework for thinking about temporal integration in the claustrum, supported by solid slice physiology. However, in its current form, it overstates the degree to which the proposed RNN dynamics reflect actual claustral neural mechanisms. With substantial revision-especially a more cautious interpretation of model-data similarity and a clearer articulation of modeling limitations-the study could make a meaningful contribution as a hypothesis-generating work rather than a definitive mechanistic account.

Comments on revisions:

The authors have carefully addressed the concerns raised in the initial review. In particular, the manuscript has been substantially improved in terms of tone, conceptual clarity, and the interpretation of the modeling results. The revised version now presents a well-balanced and appropriately framed account of the work.

The study offers a compelling and useful hypothesis-generating framework for understanding temporal integration in the claustrum, and I support its publication. As a minor point, given the acknowledged limitations of pseudo-population and single-trial data, it would be preferable to slightly soften a few remaining statements that describe trajectory structure as directly "reflecting" population-level dynamics (e.g., using "consistent with" instead).

Reviewer #2 (Public review):

This manuscript reports the behavior of a computational model of rat claustral neurons during the performance of a behavioral task known as the delayed escape task (in this reviewer's understanding, this behavioral task was created and implemented by this group only). These authors have argued in a prior manuscript (Han et al.) that a group of neurons located "rostral to striatum" are part of the claustrum. The group names the region the "rostral to striatum claustrum." Additionally, in the Han et al. paper, the authors argue that these cells are responsible for maintaining a signal that lasts through the delay period.

The main findings of the current paper are:

(1) The authors have built a model network that was trained to show firing similar to what was reported for rats in their prior paper.

(2) The authors' analysis of model behavior is used to suggest that the model network recapitulates biological activity, including the existence of a cluster of cells mainly responsible for the delay period firing.

(3) The authors offer evidence from patch clamp recordings for excitatory interconnections among claustral neurons that are an essential feature of the model network.

A major value of the computational network is that "trials" of the network can be performed. In experiments on animals, only single trials can be used.

Concerns:

(1) This paper is based on behavioral results and neural recordings from their prior paper (Han et al.), but data, e.g. in figure 1, are not clearly identified as new or as coming from that source. Figure 1A, for example, appears to be taken directly from Han et al. No methods are given in this manuscript for the behavioral testing or the in vivo electrophysiology.

(2) Many other details are unclear. Examples include model training, the weight matrices and how these changed with training (p. 13), the equations 2 and 3 (p. 13), the sources for the constants in the equations (p. 14), the methods (anesthesia, stereotaxic coordinates, injection specifics and details for "sparse expression") for the ChrimsonR injections.

(3) The explorations of model behavior are a catalog of everything tried rather than an organized demonstration of what the model can and cannot do. The figures could be reduced in number to emphasize the key comparisons of the different clusters and the model's behavior under different conditions intended to "test" the model.

(4) On page 6, the E-E connectivity is argued from Shelton et al. (2025) and against Kim et al. (2016), but ignores Orman (2015), which to this reviewer's knowledge was the first to demonstrate such connectivity, including the long duration events and impact of planes of section.

(5) Whereas the authors are entitled to their own opinion of prior work (references 3-8), it is inappropriate to misrepresent prior work as only demonstrating a "limited function" of claustum. Additional papers by Mathur's group and Citri's group are ignored.

In summary, the authors have made a computational model that recapitulates the firing of a subset of potentially claustral neurons during a particular behavioral task (delayed escape is certainly not the only behavior that involves claustrum - see e.g., attention, salience, sleep). If the conclusion is that excitatory claustral cells must be connected to other excitatory claustral cells, such a conclusion is not new and the electrophysiological E-E metrics are not well quantified (e.g., connectivity frequency, strength of connection). If the model is intended to predict how claustrum might accomplish any other task, there is insufficient detail to evaluate the model beyond the evidence that the model creates a subset of cells that can sustain firing during the delay period in the delayed escape task.

All relevant work must be appropriately cited throughout the manuscript.

Comments on revisions:

The authors have adequately addressed the concerns that were raised in response to the first version of the manuscript.

Reviewer #1 (Public review):

Summary:

This study presents a novel toolkit for visualizing and manipulating neurotransmitter-specific vesicles in C. elegans neurons, addressing the challenge of tracking neurotransmitter dynamics at the level of individual synapses. The authors engineered endogenously tagged vesicular transporters for glutamate, GABA, acetylcholine, and monoamines, enabling cell-specific labeling while maintaining physiological function. Additionally, they developed conditional knockout strains to disrupt neurotransmitter synthesis in single neurons. The study reveals that over 10% of neurons in C. elegans exhibit co-transmission, with a detailed case study on the ADF sensory neuron, where serotonin and acetylcholine are trafficked in distinct vesicle pools. The approach provides a powerful platform for studying neurotransmitter identity, synaptic architecture, and co-transmission.

Strengths:

(1) This toolkit offers a generalizable framework that can be applied to other model organisms, advancing the ability to investigate synaptic plasticity and neural circuit logic with molecular precision.

(2) The use of this toolkit, the authors uncover molecular heterogeneity at individual synapses, revealing co-transmission in over 10% of neurons, and offers new insights into neurotransmitter trafficking and synaptic plasticity, advancing our understanding of synaptic organization.

Weaknesses:

(1) While the article introduces valuable tools for visualizing neurotransmitter vesicles in vivo, the core techniques are based on previously established methods. The study does not present significant technological breakthroughs, limiting the novelty of the methodological advancements.

(2) The article does not fully explore the potential implications or the underlying mechanisms governing this process, while the discovery of co-transmission in over 10% of neurons is an intriguing finding. A deeper investigation into the functional uniqueness and interactions of neurotransmitters released from individual co-transmitting neurons-perhaps through case study example-would strengthen the study's impact.

Comments on revisions:

I have no further questions regarding this work. I would like to congratulate the authors on the forthcoming publication of their manuscript. This study presents a versatile methodological framework with strong potential to advance the field of neuroscience, particularly in dissecting neural circuit function and neurotransmission dynamics in vivo.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors developed fluorescent reporters to visualize the subcellular localization of vesicular transporters for glutamate, GABA, acetylcholine, and monoamines in vivo. They also developed cell-specific knockout methods for these vesicular transporters. To my knowledge, this is the first comprehensive toolkit to label and ablate vesicular transporters in C. elegans. They carefully and strategically designed the reporters, and clearly explained the rationale behind their construct designs. Meanwhile, they used previously established functional assays to confirm that the reporters are functional. They also tested and confirmed the effect of cell-specific and pan-neuronal knockout of several of these transporters.

Strengths:

The tools developed are versatile: they generated both green and red fluorescent reporters for easy combination with other reporters; they established the method for cell-type specific KO to analyze function of the neurotransmitter in different cell types. The reagents allow visualization of specific synapses among other processes and cell bodies. In addition, they also developed a binary expression method to detect co-transmission "We reasoned that if two neurotransmitters were co-expressed in the same neuron, driving Flippase under the promoter of one transmitter would activate the conditional reporter-resulting in fluorescence-only in cells also expressing a second neurotransmitter identity". Overall, this is a versatile and valuable toolkit with well-designed and carefully validated reagents. This toolkit will likely be widely used by the C. elegans community.

Comments on revisions:

The authors addressed my questions in the revised manuscript.

Reviewer #3 (Public review):

Summary:

Cuentas-Condori et al. generate cell-specific tools for visualizing the endogenous expression of, as well as knocking out, four different classes of neurotransmitter vesicular transporters (glutamatergic, cholinergic, gabaergic and monoaminergic) in C. elegans. They then use these tools in an intersectional strategy to provide evidence for the co-expression of these transporters in individual neurons, suggesting co-transmission of the associated neurotransmitters.

Strengths:

A major strength of the work is the generation of several endogenous tools that will be of use to the community. Additionally, this adds to accumulating evidence of co-transmission of different classes of neurotransmitters in the nervous system.

Another strength is the comparison to previously published single cell sequencing data and other previously published data.

Weaknesses:

Co-expression of these transporters is not in and of itself sufficient to establish neurotransmitter co-release, but this caveat is acknowledged by the authors.

Comments on revisions:

The authors have addressed all of my previous concerns.

Reviewer #1 (Public review):

Summary:

Ma et al. show that melanoma cells induce an EMT-like state in nearby keratinocytes and that when this state is induced experimentally by Twist-overexpression the resulting alteration in keratinocytes is inhibitory for melanoma invasion. These conclusions are based on experiments in vivo with zebrafish and, in vitro, with human cells. The work is carefully done and provides new insights into the interactions between melanoma cells and their environment.

Strengths:

Use of both zebrafish and human cells adds confidence that findings are relevant to human melanomas while also further demonstrating utility of the zebrafish system for discovering important new features of melanoma biology that could ultimately have clinical impacts. The work also combines a nice suite of approaches including different models for induced melanomagenesis in zebrafish, single cell RNA-sequencing, and more. Some of the final observations are intriguing as well, especially the possibility of EMT induced melanocyte-keratinocyte interactions via Jam3 expression; it will be interesting to see if these is indeed a mechanism for restraining melanoma invasion. The paper is clearly written and the inferences appropriate for the results obtained. Overall the work makes a solid contribution to our understanding of important, but too often neglected, roles of the tumor microenvironment in promoting or inhibiting tumor progression and outcome.

Weaknesses:

No critical weaknesses noted.

Comments on revisions:

The authors have adequately addressed my comments and concerns.

Reviewer #2 (Public review):

Summary:

Manuscript by Ma et. al. utilizes a zebrafish melanoma model, single-cell RNA sequencing (scRNA-seq), a mammalian in vitro co-culture system, and quantitative PCR (Q-PCR) gene expression analysis to investigate the role keratinocytes might play within the melanoma microenvironment. Convincing evidence is presented from scRNA-seq analysis showing that a small cluster of melanoma-associated keratinocytes upregulate the master EMT regulator, transcription factor, Twist1a. To investigate how Twist-expressing keratinocytes might influence melanoma development, the authors use an in vivo zebrafish model to induce melanoma initiation while overexpressing Twist in keratinocytes through somatic transgene expression. This approach reveals that Twist overexpression in keratinocytes suppresses invasive melanoma growth. Using a complementary in vitro human cell line co-culture model, the authors demonstrate reduced migration of melanoma cells into the keratinocyte monolayer when keratinocytes overexpress Twist. Further scRNA-seq analysis of zebrafish melanoma tissues reveal that, in the presence of Twist-expressing keratinocytes, subpopulations of melanoma cells show altered gene expression, with one unique melanoma cell cluster appearing more terminally differentiated. The authors use computational methods to predict putative receptor-ligand pairs that might mediate the interaction between Twist-expressing keratinocytes and melanoma cells. Finally the authors established that similar keratinocyte phentypical changes also occurs in human melanoma tissues, setting a scene for future clinically relevant studies.

Strengths:

The scRNA-seq approach reveals a small proportion of keratinocytes undergoing EMT within melanoma tissue. The use of a zebrafish somatic transgenic model to study melanoma initiation and progression provides an opportunity to manipulate host cells within the melanoma microenvironment and evaluate their impact on tumour progression. Solid data demonstrate that Twist-expressing keratinocytes can constrain melanoma invasive development in vivo and reduce melanoma cell migration in vitro, establishing that Twist-overexpressing keratinocytes can suppress at least one aspect of tumour progression. Using GeoMX spatial transcriptomics platform to interrogate a series of early melanoma precursor lesions, enabled the authors to demonstrate similar EMT phenotype in keratinocytes also occurs in humans.

Weaknesses:

Due to limitations of the current model, no EMT marker gene expression was examined in melanoma tissue sections to determine the proportion and localization of Twist+ve keratinocytes within the melanoma microenvironment. However the authors compensated this through using spatial transcriptomics platform to interrogate a series of early melanoma precursor lesions in humans.

Due to technical limitations, it remain to be determined whether blocking EMT through down-regulation of Twist in keratinocytes may influence melanoma development.

Due to technical limitations, none of the gene expression changes detected through Q-PCR or scRNA-seq were examined using immunostaining or in situ hybridization, hence cellular resolution spatial information is lacking.

Overall, the data presented in this report draw attention to a less-studied host cell type within the tumour microenvironment, the keratinocytes, which, similar to well-studied immune cells and fibroblasts, could play important roles in either promoting or constraining melanoma development. Counterintuitively, the authors show that Twist-expressing EMT keratinocytes can constrain melanoma progression. While the detailed mechanisms remain to be uncovered, this is an exciting new line of research that warrant future studies.

Comments on revisions:

The authors have provided additional evidence to support their original conclusions, and the inclusion of spatial transcriptomic analysis using human samples strengthens the study. I did not identify any further issues that require attention.

Reviewer #3 (Public review):

Summary:

In this study the authors use the zebrafish model and in vitro co-cultures with human cell lines, to study how keratinocytes modulate the early stages of melanoma development/migration. The authors demonstrate that keratinocytes undergo an EMT-like transformation in the presence of melanoma cells which lead to a reduction in melanoma cell migration. This EMT transformation occurs via Twist; and resulted in an improvement in OS in zebrafish melanoma models. Authors suggest that the limitation of melanoma cell migration by Twist-overexpressing keratinocytes was through altered cell-cell interactions (Jam3b) that caused a physical blockage of melanoma cell migration.

Strengths:

Authors describe a new cross-talk between melanoma and its major initial microenvironment: the keratinocytes and how instructed by melanoma cells keratinocytes undergo an EMT transformation, which then controls melanoma migration.<br /> Overall, the paper is very well written, and the results are clearly organized and presented.

Weaknesses:

(1) To really show their last point it would be important to CRISPR KO Jam3b in melanoma with twist OE keratinocytes, in vivo or in vitro.

(2) Use of patient biopsies from early-stage melanomas vs healthy tissue to assess if there is a similar alteration of morphology of adjacent keratinocytes and increase in vimentin in human samples would strengthen the author's findings.

(3) Characterise better the cell-cell junctions and borders between cells (melanoma/ keratinocytes) with cellular and sub-cellular resolution. Since melanocytes can "touch" with their dendrites ~40 keratinocytes - can authors expand and explain better their model? Can this explain that in some images we cannot observe a direct interface between the cells?

Comments on revisions:

The authors answered most of the concerns raised.

Reviewer #1 (Public review):

The manuscript provides several important findings that advance our current knowledge about the function of the gustatory cortex (GC). The authors used high density electrophysiology to record neural activity during a sucrose/NaCl mixture discrimination task. They observed population-based activity capable of representing different mixtures in a linear fashion during the initial stimulus sampling period as well as representing the behavioral decision (i.e., lick left or right) at a later time point. Analyzing this data at the single neuron level, they observed functional subpopulations capable of encoding the specific mixture (e.g., 45/55), tastant (e.g., sucrose), and behavioral choice (e.g., lick left). To test the functional consequences of these subpopulations, they built a recurrent neural network model in order to "silence" specific functional subpopulations of GC neurons. The virtual ablation of these functional subpopulations altered virtual behavioral performance in a manner predicted by the subpopulation's presumed contribution.

Strengths:

Building a recurrent neural network model of the gustatory cortex allows the impact of the temporal sequence of functionally identifiable populations of neurons to be tested in a manner not otherwise possible. Specifically, the author's model links neural activity at the single neuron and population level with perceptual ability. The electrophysiology methods and analyses used to shape the network model are appropriate. Overall, the conclusions of the manuscript are well supported.

Weaknesses:

One minor weakness is the mismatch between the neural analyses and behavioral data. Neural analyses (i.e. population activity trajectories) indicate a separation of the neural activity associated with each mixture. Given this analysis, one might expect the psychometric curve to have a significantly steeper slope. One potential explanation is the concentration of the stimuli utilized in the mixture discrimination task. The authors utilize equivalent concentrations, rather than intensity matched concentrations. In this case, a single stimulus can (theoretically) dominant the perception of a mixture resulting in a biased behavioral response despite accurate concentration coding. Given the difficulty of iso-intensity matching concentrations, this concern is not paramount.

Reviewer #2 (Public review):

Lang et al. investigate the contribution of individual neuronal encoding of specific task features to population dynamics and behavior. Using a taste based decision-making behavioral task with electrophysiology from the mouse gustatory cortex and computational modeling, the authors reveal that neurons encoding sensory, perceptual, and decision-related information with linear and categorical patterns are essential for driving neural population dynamics and behavioral performance. Their findings suggest that individual linear and categorical coding units have a significant role in cortical dynamics and perceptual decision-making behavior.

Overall, the experimental and analytical work is of very high quality, and the findings are of great interest to the taste coding field, as well as to the broader systems neuroscience field.

I initially had some suggestions for further analyses to clarify the contribution of constrained and unconstrained units. In the revised version, the authors have performed all the suggested analyses, further strengthening their conclusions.

Reviewer #3 (Public review):

Primary taste cortex neurons show a variety of dynamic response profiles during taste decision making tasks, reflecting both sensory and decision variables. In the present study, Lang et al., set out to determine how neurons with distinct response profiles contribute to perceptual decisions about taste stimuli.

The methods with regard to the behavioral task and electrophysiological recordings/data analysis are straightforward, solid and appropriate. The computational model is presented in a clear and conceptually intuitive manner, although the details are outside of my area of expertise.

The experimental design features a simple 2-alternative forced choice task that yielded clear psychometric curves across a range of stimuli. In vivo recordings were performed using neuropixels and yielded an appropriate sample of single neuron responses. The strength of the model lies in the fact that it consists of single neurons whose response profiles mimic those recorded in vivo, and allows neuron-selective manipulation.

By virtually lesioning specific subsets of neurons in the network, the authors demonstrate that a relatively small populations of neurons with specific tuning profiles were sufficient to produce the observed neural dynamics and behavioral responses. This effect was selective as lesioning other responsive neurons did not affect overall response dynamics or performance.

These findings provide new insight into the relation between the response profiles of single neurons in sensory cortex, their population-level activity dynamics, and the perceptual decisions they inform.

The approach is particularly innovative as it uses computational modeling to target functionally-defined "cell types", which cannot necessarily be targeted by more conventional genetic approaches.

Reviewer #1 (Public review):

Summary:

This paper characterises the physiological and computational underpinnings of the accumulation of intermittent glimpses of sensory evidence, with a focus on the centroparietal positivity and motor beta lateralization. The main finding is that the centroparietal positivity builds up during evidence accumulation but falls back to baseline during gaps, while motor beta lateralization maintains a continuous a sustained representation throughout the gap and until response.

Strengths:

- Elegant combination of electroencephalography and computational modelling.

- Innovative task design, including parametric manipulation of gap duration.

- The authors describe results of two separate experiments, with very similar results, in effect providing an internal replication.

Weaknesses:

- A direct characterization of how the centroparietal positivity and motor beta lateralization interact is missing, which limits the novelty. In their reply to reviewers, the authors argue that the signal-to-noise ratio of EEG signals is insufficient for such analyses at the single-trial level. If so, a binned or trial-averaged approach could still be attempted.

- An exhaustive characterisation of sensors and frequency bands is also missing. In their reply to reviewers, the authors suggest that this would detract from their hypothesis-driven focus. I disagree: the main hypothesis and figures could remain centred on the centroparietal positivity and motor beta lateralization, with a more comprehensive mapping of sensors and frequencies placed in supplementary material. Since the purpose of the paper is to examine EEG-based decision signals in a novel behavioural context, a broader characterisation of the underlying EEG landscape would seem appropriate.

Reviewer #2 (Public review):

Summary:

This manuscript examines decision-making in a context where the information for the decision is not continuous, but separated by a short temporal gap. The authors use a standard motion direction discrimination task over two discrete dot motion pulses (but unlike previous experiments, fill the gaps in evidence with 0-coherence random dot motion of differently coloured dots). Previous studies using this task (Kiani et al., 2013; Tohidi-Moghaddam et al., 2019; Azizi et al., 2021; 2023) or other discrete sample stimuli (Cheadle et al., 2014; Wyart et al., 2015; Golmohamadian et al., 2025) have shown decision-makers to integrate evidence from multiple samples (although with some flexible weighting on each sample). In this experiment, decision-makers tended not to use the second motion pulse for their decision. This allows the separation of neural signatures of momentary decision-evidence samples from the accumulated decision-evidence. In this context, classic electroencephalography signatures of accumulated decision-evidence (central-parietal positivity) are shown to reflect the momentary decision-evidence samples.

Strengths:

The authors present an excellent analysis of the data in support of their findings. In terms of proportion correct, participants show poorer performance than predicted if assuming both evidence samples were integrated perfectly. A regression analysis suggested a weaker weight on the second pulse, and in line with this, the authors show an effect of the order of pulse strength that is reversed compared to previous studies: A stronger second pulse resulted in worse performance than a stronger first pulse (this is in line with the visual condition reported in Golmohamadian et al., 2025). The authors also show smaller changes in electrophysiological signatures of decision-making (central parietal positivity, and lateralised motor beta power) in response to the second pulse. The authors describe these findings with a computational model which allows for early decision-commitment, meaning the second pulse is ignored on the majority of trials. The model-predicted electrophysiological components describe the data well. In particular, this analysis of model-predicted electrophysiology is impressive in providing simple and clear predictions for understanding the data.

Weaknesses:

Some readers may be left questioning why behaviour in this experiment is so different from previous experiments which use almost exactly the same design (Kiani et al., 2013; Tohidi-Moghaddam et al., 2019; Azizi et al., 2021; 2023). Overall performance in this experiment was much worse than previous experiments: Participants achieved ~85% correct following 400 ms of 33 - 45% coherent motion. In previous work, performance was ~90% correct following 240ms of 12.8% coherent motion. A second weakness is that, while the authors present a model which describes the data based on pre-mature decision-commitment, they do not examine explanations from the existing literature, that evidence is flexibly weighted, and do not provide any analyses which could be used to compare these descriptions. While their model can describe the data in this manuscript, it cannot explain the data from previous experiments showing a stronger weight on the second pulse.

Reviewer #1 (Public review):

Summary:

The authors report the results of a tDCS brain stimulation study (verum vs sham stimulation of left DLPFC; between-subjects) in 46 participants, using an intense stimulation protocol over 2 weeks, combined with an experience-sampling approach, plus follow-up measures after 6 months.

Strengths:

The authors are studying a relevant and interesting research question using an intriguing design, following participants quite intensely over time and even at a follow-up time point. The use of an experience-sampling approach is another strength of the work.

Comments on revisions:

Overall, I think the authors made many improvements to their manuscript. There are, however, still a number of concerns that first need to be addressed, since it is still not currently possible to fully evaluate the analyses, results, and conclusions presented in the paper. I list these points below:

(1) The authors still use causal language where they must not use causal language. This is true for many places in the manuscript; I am highlighting here just a few places, but the authors nevertheless have to go carefully through the whole manuscript to change these instances.

Some examples:

(a) In response to my comment (1) in the previous round, where the authors adjusted their text, the authors still use causal language in their last sentence "... procrastination behavior has been observed to impair general health..." Unless the cited study truly allowed causal conclusions, the causal language should be removed here as well.

(b) The authors still make (causal) claims about the involvement of self-control in their observed results. To reiterate from the previous round of revisions: The authors cannot make any strong claims about the role of self-control processes because they do not directly measure self-control nor do they directly manipulate self-control or have a design that would rule out alternative mechanisms other than self-control. Therefore, their claims about self-control have to be toned down. It is laudable that the authors have added a statement towards the end of their discussion about not being able to make strong conclusions about the role of self-control. But the authors need to use similar careful wording not just at the end of the discussion but throughout the manuscript.

(i) In the abstract, the authors use the formulation "...conceptualized roles of self-control on procrastination..." -- this wording is still too strong, suggesting that you actually studied self-control.

(ii) In the introduction (page 4, lines162-169), the way the authors formulate these sentences suggests that they directly measured self-control. Again, the authors need to make it explicit that they are not directly measuring self-control but its hypothesized down-stream consequences on valuations/behavior.

(iii) In the discussion, for example, on page 11, lines 555 and following, the authors write:

"One major contribution this study has made is to disentangle the neurocognitive mechanism of procrastination by demonstrating that self-control could increase task-outcome value so as to reduce procrastination."

Again, please be aware that you are NOT demonstrating that self-control does anything, since you only measure procrastination rates, outcome values, and task aversiveness. It is possible that mechanisms other than self-control might be relevant for this. Perhaps neuromodulation directly increases outcome values, without involvement of self-control processes. You simply cannot know that and therefore you cannot make those claims in the form that you are making them. You can write that the observed results are consistent with the idea that neuromodulation might have had an effect on self-control and this in turn might have affected outcome values. But you also need to make it explicit that, to substantiate these claims, you would need more direct evidence that indeed self-control was involved. These more careful formulations would not at all reduce the value of your work, but indeed they would rather demonstrate your carefulness in interpreting the results you obtained.

(2) I am still puzzled by the power analysis. In the text, you write that a sample size of 18 participants (i.e., 9 per group) would be sufficient to achieve 80% power. I still feel this seems far too optimistic and hard to believe, but that is not my point here. While in the text, you write that you need 18 participants, the G*power output seems to suggest a sample size of 34, not 18. Why this contradiction? Or is it not contradictory? If it is not, then please explain it more fully.

(3) I have several comments about the mixed-effects analysis.

First of all, I want to thank the authors for adding more details, things have become much clearer now. However, I still have a few questions and comments related to these analyses:

(a) The variable Emotions was within-subjects, as far as I understood. Accordingly, Emotions should most likely be modelled with random slopes varying over participants (in addition to being modelled as a fixed effect).

(b) The analyses still cannot fully be evaluated as I cannot access the scripts and data. The authors mention that the scripts and data should be available via a link they provide (https://doi.org/10.57760/sciencedb.35140). However, when I try to access these materials via this link, no page opens; it seems the link is dead?

(c) What are the results and conclusions if you do not include the covariates of no interest? I.e., please re-run your main models without age, gender, SES, Emotions.

(d) The authors mention that they use GLMMs, which would suggest generalized mixed-effects models, but they do not describe what family/distribution they used. Since they mention lmerTest and seem to report F-tests, my guess is that they used Gaussian models. However, both their DVs (procrastination rates and their ratings) are bounded variables and at least procrastination rates hit the lower boundary. That can mean that their analyses suffer from inflated Type 1 and/or Type 2 rates. Therefore, please repeat the analyses with an appropriate generalized mixed-effects model (perhaps a beta regression type of model?).

(e) When reporting the results of the mixed-effects models, the authors report the regression coefficient, standard error, DFs and p value, but not the actual test statistic. Please add the information about the test statistic and report all degrees of freedom (in case of F tests that would be the degrees of freedom of the test and the residual degrees of freedom).

(f) Thank you for adding the analysis where you remove the last two sessions. But currently you present them in the manuscript without explaining/motivating why you do this. Please add this motivation, as otherwise it will be puzzling for the reader why you conduct these analyses.

(4) Mediation analysis

In your manuscript, you present some mediation analyses. Please be aware that such mediation analyses cannot establish causality and they suffer from extremely high Type 1 error rates (see, e.g., https://datacolada.org/103).

My suggestion would be to completely remove all mediation analyses. However, if you want to keep them, then you need to be extremely careful in how you present the results. You need to explicitly mention that you cannot derive any causal conclusions from them and that simulation studies have shown that such mediation analyses suffer from extremely high Type 1 errors.

As an example (but the mediation results are mentioned in several places, for example, also in the abstract):

On page 10, lines 501-503: What you can causally conclude is that neuromodulation affects your measured variables (outcome values, procrastination rates, task aversiveness), but you cannot conclude that the effect of neuromodulation on procrastination rates causally operates via outcome values. Thus, please adjust the formulation accordingly. The same applies to the mediation section that follows right afterwards (page 10, lines 505-522).

(5) In the introduction, the authors introduce several theoretical procrastination frameworks (TMT, mood repair, TDM). Do the results of the current paper help to decide which framework might be the most appropriate, at least for the authors data set? It might be of interest to address this explicitly.

(6) The language is sometimes hard to understand and seems in quite some places grammatically incorrect. Thus, I think the paper would profit very much from thorough English proofreading.

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:

This study addresses the important question of how top-down cognitive processes affect tactile perception in autism - specifically, in the Fmr1-/y genetic mouse model of autism. Using a 2AFC tactile task in behaving mice, the study investigated multiple aspects of perceptual processing, including perceptual learning, stimulus categorization and discrimination, as well as the influence of prior experience and attention.

Strengths:

The experiments seem well performed, with interesting results. Thus, this study can/will advance our understanding of atypical tactile perception and its relation to cognitive factors in autism.

Reviewer #2 (Public review):

Summary:

This manuscript presents a tactile categorization task in head-fixed mice to test whether Fmr1 knockout mice display differences in vibrotactile discrimination using the forepaw. Tactile discrimination differences have been previously observed in humans with Fragile X Syndrome, autistic individuals, as well as mice with loss of Fmr1 across multiple studies. The authors show that during training, Fmr1 mutant mice display subtle deficits in perceptual learning of "low salience" stimuli, but not "high salience" stimuli, during the task. Following training, Fmr1 mutant mice displayed an enhanced tactile sensitivity under low-salience conditions but not high-salience stimulus conditions. The authors suggest that, under 'high cognitive load' conditions, Fmr1 mutant mouse performance during the lowest indentation stimuli presentations was affected, proposing an interplay of sensory and cognitive system disruptions that dynamically affect behavioral performance during the task.

Strengths:

The study employs a well-controlled vibrotactile discrimination task for head-fixed mice, which could serve as a platform for future mechanistic investigations. By examining performance across both training stages and stimulus "salience/difficulty" levels, the study provides a more nuanced view of how tactile processing deficits may emerge under different cognitive and sensory demands.

Weaknesses:

The study is primarily descriptive. The authors collect behavioral data and fit simple psychometric functions, but provide no neural recordings, causal manipulations, or computational modeling. Without mechanistic evidence, the conclusions remain speculative.

Reviewer #3 (Public review):

Summary:

Developing consistent and reliable biomarkers is critically important for developing new pharmacological therapies in autism spectrum disorders (ASDs). Altered sensory perception is one of the hallmarks of autism and has been recently added to DSM-5 as one of the core symptoms of autism. Touch is one of the fundamental sensory modalities, yet it is currently understudied. Furthermore, there seems to be a discrepancy between different studies from different groups focusing on tactile discrimination. It is not clear if this discrepancy can be explained by different experimental setups, inconsistent terminology, or the heterogeneity of sensory processing alterations in ASDs. The authors aim to investigate the interplay between tactile discrimination and cognitive processes during perceptual decisions. They have developed a forepaw-based 2-alternative choice task for mice and investigated tactile perception and learning in Fmr1-/y mice

Strengths:

There are several strengths of this task: translational relevance to human psychophysical protocols, including controlled vibrotactile stimulation. In addition to the experimental setup, there are also several interesting findings: Fmr1-/y mice demonstrated choice consistency bias, which may result in impaired perceptual learning, and enhanced tactile discrimination in low-salience conditions, as well as attentional deficits with increased cognitive load. The increase in the error rates for low salience stimuli is interesting. These observations, together with the behavioral design, may have a promising translational potential and, if confirmed in humans, may be potentially used as biomarkers in ASD.

Reviewer #1 (Public review):

Summary:

It is well known that neurons in the medial prefrontal cortex (mPFC) are involved in higher cognitive functions such as executive planning, motivational processing and internal state mediated decision-making. These internal states often correlate with the emotional states of the brain. While several studies point to the role of mPFC in regulating behavior based on such emotional states, the diversity of information processing in its sub-populations remains a less explored territory. In this study, the authors try to address this gap by identifying and characterizing some of these sub-populations in mice using a combination of projection-specific imaging, function-based tagging of neurons, multiple behavioral assays and ex-vivo patch clamp recordings.

Strengths:

The authors targeted mPFC projections to the nucleus accumbens (NAc) and basolateral amygdala (BLA). Using the open field task (OFT), the authors identified four relevant behavioral states as well as neurons active while the animal was in the center region ("center-ON neurons"). By characterizing single unit activity and using dimensionality reduction, the authors show differentiated coding of behavioral events at both the projection and functional levels. They further substantiate this effect by showing higher sensitivity of mPFC-BLA center-ON neurons during time spent in the open arms of the elevated plus maze (EPM). The authors then pivoted to the three-chamber social interaction (SI) assay to show the different subsets of neurons encode preference of social stimulus over non-social. This reveals an interesting diversity in the function of these sub-populations on multiple levels. Lastly, the authors used the tube test as a manipulation of the anxiety state of mice and compared behavioral differences before/after in the OFT and social interaction tasks. This experiment revealed that "losers" of the tube test spend less time in the center of the open field while "winners" show a stronger preference for the familiar mouse over the object. Using patch-clamp experiments, the authors also found that "winners" exhibit stronger synaptic transmission in the mPFC-NAc projection while "losers" exhibit stronger synaptic transmission in the mPFC-BLA projection. Given the popularity of the tube test assay in rank determination, this provides useful insights into possible effects on anxiety levels and synaptic plasticity. Overall, the many experiments performed by the authors reveal interesting differences in mPFC neurons relative to their involvement in high or low anxiety behaviors, social preference and social rank.

Weaknesses:

The authors have addressed all comments.

Reviewer #2 (Public review):

Summary:

The goal of this proposal was to understand how two separate projection neurons from the medial prefrontal cortex, those innervating the basolateral amygdala (BLA ) and nucleus accumbens (NAc), contribute to the encoding of emotional behaviors. The authors record the activity of these different neuron classes across three different behavioral environments. They propose that, although both populations are involved in emotional behavior, the two populations have diverging activity patterns in certain contexts. A subset of projections to the NAc appear particularly important for social behavior. They then attempt to link these changes to the emotional state of the animal and changes in synaptic connectivity.

Strengths:

The behavioral data builds on previous studies of these projection neurons supporting distinct roles in behavior and extend upon previous work by looking at the heterogeneity within different projection neurons across contexts, this is important to understand the "neural code" within the PFC that contributes to such behaviours and how it is relayed to other brain structures.

Weaknesses:

The diversity of neurons mediating these projections and their targeting within the BLA and NAc is not explored. These are not homogeneous structures and so one possibility is that some of the diversity within their findings may relate to targeting of different sub-structures within BLA or NAc or the diversity of projection neuron subtypes that mediate these pathways. This is an important future direction for this work but does not detract from the main finding as reported. The electrophysiological data in Figure 7 have some experimental confounds that makes their interpretation challenging.

Comments on revisions:

The authors have improved the manuscript somewhat by refining their description of the results. However, the normalized EPSC experiments still do not make much sense. If you have a higher light intensity or LED duration the curve of the EPSC response will saturate earlier. Similarly, if you are in a highly, or poorly labeled slice or subregion of a slice then you will see responses emerge at different intensities based on the number of synapses labelled. There is no standardization in the way these experiments were performed, so performing some arbitrary post hoc normalisation does not correct for this. Similarly, they also place the fibreoptic manually above the slice each time. This makes it much harder to determine the actual light intensity delivered to the slice on a cell by cell and group by group basis.

I have reduced my public statement from significant experimental confounds, to some experimental confounds. But the way the experiments were performed does not allow the normalized data to really be interpretable. They still argue that normalized EPSCs are relatively larger. I don't even really understand what this means biologically.

The subsequent rise/decay and other measures is now better described. However, they note that the decay constant is larger. This means that the kinetics are slower, not enhanced, as they describe.

Reviewer #1 (Public review):

Summary:

This manuscript examines the evolution of molluscan shells using single-cell analyses of the adult mantle of Crassostrea gigas and compares these data with previous datasets from embryonic and larval stages of this species and other spiralians. The authors provide support for a scenario in which secretory cells are broadly conserved across spiralians, and the incorporation of lineage-restricted genes contributes to the evolution of molluscan shells.

Strengths:

High-quality datasets for mantle tissue in Crassostrea gigas and thorough comparisons with existing datasets for this species and other spiralians. Balanced discussion.

Weaknesses:

No major weaknesses. The analyses follow fairly standard approaches in the field that have been previously applied and developed in similar systems.

Reviewer #2 (Public review):

Summary:

Bai et al. present in their study three single-cell RNA seq datasets derived from gastrulae, trochophores, and adults of the bivalve Crassostrea gigas. While a dataset on the oyster trochophore has already been published previously (Piovani et al. 2023), the gastrula and adult datasets have not been published yet. The authors conclude that cell types secreting the oyster shell valves use a genetic repertoire that is also used by epithelial and secretory cell types of very different spiralians, such as annelids, chaetognaths and flatworms.

Strengths:

The study provides new single-cell datasets from multiple developmental stages of an oyster, offering a valuable resource for the field. It takes a broad comparative approach using state-of-the-art techniques across diverse animal groups and addresses an important question regarding the origin and evolution of shell-forming cell types.

Weaknesses & suggestions to improve the manuscript:

(1) Validation of cell types

Cell type identities are not convincingly validated. Although the authors cite previous studies (l. 92), the referenced marker genes are largely not used, and the cited works do not provide sufficient spatial validation. Without in situ data, the inferred locations of cell types (e.g. Figure 2A) are not supported. Spatial validation of marker genes (e.g. via HCR) is essential, particularly for a study addressing shell field evolution. In addition, the gastrula dataset is not meaningfully analyzed, and its inclusion remains unclear.

(2) Robustness of cell type classification

Several proposed cell types may not represent distinct entities (not individuated) but rather reflect over-clustering. Marker genes are often not specific and are shared across clusters (e.g. Sec1/Sec2), making it difficult to distinguish cell types reliably.

(3) Comparative analysis of secretory cells

The comparative framework is not sufficiently supported. Secretory cells are highly diverse, and without proper validation, their comparison across taxa is not meaningful. The transcription factor analysis is limited, as only a few genes are shared and many are inconsistently expressed (Figure 3E). The conclusion of a conserved regulatory program across spiralians is therefore overstated.

(4) Clarity and interpretation of results

Results are at times difficult to follow and remain superficial. Marker genes are insufficiently annotated (especially for Crassostrea), and comparisons across taxa lack functional interpretation. Unvalidated and heterogeneous cell types are grouped together, and transcriptional similarities are overinterpreted. Overall, key conclusions are not adequately supported by the presented data.

Reviewer #3 (Public review):

Summary:

This manuscript by Bai et al. reports single-cell transcriptomics of the oyster mantle to elucidate the respective contributions of ancient conserved programmes and lineage-specific genes to the origin of the molluscan shell. The authors compare their dataset with other oyster larval datasets as well as data from other organisms (annelids, chaetognaths) and find evidence of evolutionary conservation and functional similarity with secretory cell types. They also observe that cells involved in secreting the larval skeleton express predominantly recent genes, whereas the adult skeleton-secreting programme is evolutionarily more conserved.

Strengths:

The manuscript is well written and clearly presented, and the results are interesting, particularly the distinction between larval and adult skeleton secretion, which is placed in a thoughtful evolutionary context.

Weaknesses:

(1) My main concern is that the authors rely primarily on previous studies for the experimental and functional characterisation of the identified cell types. The cited papers (Piovani, 2023 and de la Forest Divonne et al., 2025) deal with distinct stages or tissues (larvae and hemocytes, respectively), which limits their direct relevance. The authors also cite other papers for in situ expression data; it would be helpful to summarise somewhere (e.g. in a table) which genes have been experimentally characterised and what their expression domains are, or alternatively to provide HCR or in situ staining on the mantle. For instance, what is the rationale for the claim that proliferative cells give rise to the mantle? The trajectory inference approach used (Monocle) would likely yield a similar result regardless of the reference cell type, so additional justification is needed.

(2) More broadly, I find that the functional properties of the identified cell types and their relationship to the expressed genes deserve more detailed discussion. For example, at L100, several genes are mentioned, but their functional roles are not discussed. Similarly, the basis for annotating the proliferative cells is not explained. How was gene orthology assessed? Throughout the manuscript, vertebrate-style gene names are used without explicitly establishing orthology status in oyster, which should be addressed.

(3) More detail is needed on the methods and quality control for the single-cell data. The authors should clarify that the platform used (BMKMANU) is a droplet-based technology comparable in principle to Drop-seq. BMKMANU is not widely used in the field. How does it compare to 10x Genomics in terms of sensitivity and cell recovery? The authors appear to use the 10x Chromium cellranger pipeline for data analysis, which suggests compatibility, but this should be stated explicitly. Additionally, no information is provided on the number of sequencing runs or biological replicates, nor on how reproducible the results are across samples.

(4) A limitation of the phylostratigraphic analysis is that it is restricted to mantle tissue, making it difficult to place the results in a whole-organism context. How do the age profiles of mantle-expressed genes compare to those of more evolutionarily conserved tissues, such as the nervous system? I appreciate the methodological and experimental constraints, but this is a genuine limitation of the study. The authors could at least discuss it explicitly, and ideally consider generating a broader single-cell atlas of the oyster to provide this comparative baseline.

(5) Have the authors considered the potential importance of lineage-specific gene duplication? It is well established that spiralians, including oysters, have undergone extensive lineage-specific duplication of transcription factors such as homeobox genes, and many structural shell-associated proteins may similarly have been duplicated. This could be relevant to interpreting both the phylostratigraphic results and the expansion of secretory gene families.

Reviewer #1 (Public review):

This paper reports a previously unrecognized mechanism by which platelets compact fibrin fibers during clot retraction. Rather than simply pulling on fibers, the authors propose that platelets generate swirling motions that wind and loop fibrin into dense structures.

While the results are intriguing, the underlying physical mechanism remains unexplained. In particular, it is unclear how platelets generate swirling motion capable of inducing fibrin coiling, especially when suspended in 3d fibrin mesh. This raises concerns about the conclusions. Also, does fibrin have inherent chirality or structural asymmetry that could promote coiling independently of platelet activity? Furthermore, platelet retraction typically involves platelet aggregation rather than isolated cells, and it is unclear how fibrin coiling would proceed in clustered platelets.

Reviewer #2 (Public review):<br /> <br /> Summary:

Grichine et al. investigate platelet-mediated fibrin compaction using human donor platelets and propose a novel mechanistic model in which platelets generate contractile forces and wind fibrin fibers into compact coiled structures. Using a combination of 2D spread assays, 3D clot imaging via expansion microscopy, live-cell imaging, and computational modelling, the authors present evidence of cage-like fibrin architectures, coiled-fibre morphologies, and platelet-centred "rosette" structures present during fibre compaction. They further suggest that actomyosin-driven cytoskeletal dynamics, potentially involving rotational or swirling motion, underlie this proposed winding mechanism, analogous to DNA looping and compaction. The study addresses an important and longstanding question in thrombosis and hemostasis and offers a conceptually novel perspective on clot compaction.

Strengths:

The integration of multiple imaging modalities is a notable strength of this paper. In particular, the 2D fiber-retraction assay provides a useful model for understanding the spatio-temporal dynamics of platelet-mediated fibrin compaction, which can be applied to other systems and may yield detailed mechanistic insights into biological processes. The live-imaging approaches are particularly well executed and offer valuable dynamic insight.

Weaknesses:

The primary weakness of this paper lies in its descriptive nature and its reliance on correlative rather than causal evidence. Several interpretations are not uniquely supported by the data presented. For example, the categorisation of fibrin accumulation in 2D assays as "fiber winding" and "fibre compaction" remains descriptive without establishing winding as a mechanism. Alternative mechanisms, such as circular bundling, stacked fibers under tension, or fibrin crosslinking-induced aggregation, are neither excluded nor investigated. Although the authors present compelling live imaging, establishing winding as a dynamic phenotype would require quantitative analyses, such as measuring angular velocities and coiling rates. The use of a second fluorophore-labelled fibrin population could further strengthen evidence for rotational dynamics. Similarly, the inference of rotational contractility or actomyosin "swirling", based on chiral actin organisation and blebbistatin treatment, is not sufficiently supported to conclude that platelets actively wind or loop fibrin fibers. The mathematical model, while complementary and well-constructed, relies on multiple assumptions and lacks predictive validation.

Appraisal:

While the authors successfully document intriguing fibrin architectures and provide a compelling descriptive framework, they do not fully demonstrate a mechanistic model of active fibrin winding by platelets. The conclusions regarding platelet-driven winding and rotational dynamics are not sufficiently supported by direct or quantitative evidence. To substantiate these claims, the study would benefit from experiments that directly link platelet dynamics to fibrin organisation, including coordinated measurements of platelet motion and fibre rearrangement. As it stands, the results are suggestive but do not definitively support the proposed mechanism.

Discussion and Impact:

Despite these limitations, the study addresses an important question in thrombosis and hemostasis and introduces a potentially impactful conceptual framework for understanding clot compaction. The imaging approaches and datasets presented will be valuable to the community, particularly for researchers interested in platelet mechanics and fibrin organisation. However, the overall impact will depend on whether the proposed mechanism can be more rigorously validated. In its current form, the study presents an interesting and thought-provoking model, but would benefit from either stronger experimental support for the proposed mechanisms or a more cautious interpretation of the findings.

Reviewer #3 (Public review):

Summary:

This work aims to understand the mechanisms that platelets use to interact with and compact fibrin fibers during clot formation. This is an important process during wound healing, and recent work has demonstrated that platelets play a critical role in generating the force required to drive the accumulation of fibrin. The authors argue that current models are insufficient to account for the observed reduction in clot volume and propose that platelets actively 'wind up' these fibers by undergoing myosin-dependent rotation. While interesting, the experiments performed by the authors do not directly test this mechanism, and further evidence is required to support their claims.

Weaknesses:

(1) The motivation to switch from the system used in Figures 1 and 2 to the '2D fiber-retraction assay' is not clear. While the authors state that this system has 'reduced complexity', the differences between these assays appear to disrupt the 'cage-like' organization of fibrin around platelets shown in Figures 1 and 2 (compare images in Figure 2 with those in Figure 4). An in-depth comparison of two methods is needed to support the conclusions from the 2D system. Furthermore, the change in plasma volume (Figure 2 vs Figure 7) should also be tested - the authors state that this increases fibrin fiber formation, but this is not quantified or demonstrated in the figures. Notably, this appears to change the morphology of the fibrin fibers shown (comparing Figure 2 and Figure 7).

(2) It is unclear how the classification of platelets as 'fiber-winding' versus 'fiber compaction' differs in Figure 2. The criteria used for these classifications should be stated. Further, it seems premature to characterize fibers as wound without having established this earlier in the manuscript.

(3) Is the 'gearwheel' different from the 'cage' of fibrin fibers? They appear similar, but it is difficult to distinguish between them with only qualitative descriptions of these phenotypes.

(4) The quantification of platelet extensions in Figure 9 is confusing. While those in 9A are clear, those in 9B are not. For instance, what is the difference between #7 and #8 in the middle panel of 9B? It does not seem like #8 is labeling an extension.

(5) It is unclear what the modeling accomplishes, as there is no comparison between the results of these simulations and their experiments.

(6) The data presented in Figure 12 provides the most direct support for their mechanism, but falls short of directly testing their claims. These experiments should be repeated to include blebbistatin to test the contribution of myosin and include quantitative rather than qualitative comparisons of these experiments.

Reviewer #1 (Public review):

Summary:

The authors introduce the Training Village (TV), an open-source and modular system that allows group-housed rodents to live in enriched home cages while individually accessing a single shared operant box for automated cognitive training. The paper reported the animals' activity both in the operant box and in the home cages, which is novel.

Strengths:

A major strength of the work is that it moves beyond a proof-of-concept and demonstrates sustained box usage, long-term trial accumulation, and compatibility with different task designs.

(1) The platform provided a technical contribution in rodent cognitive neuroscience: obtaining large amounts of behavioral data from complex tasks while reducing experimenter intervention and preserving social housing.

(2) The authors demonstrate that the system can sustain prolonged task engagement (up to 12 months), maintain efficient use of a single operant box.

(3) The manuscript opens interesting opportunities for studying behavior outside standard session-based training. Because animals self-initiate training while remaining in a group-housed setting, the platform has the potential to illuminate relationships among motivation, spontaneous activity, and task engagement that are hard to access in conventional paradigms.

Weaknesses:

(1) One area that would benefit from further clarification is the manuscript's core advance relative to prior automated group-housed training systems, particularly Mouse Academy (Qiao et al., 2018). The authors listed some advantages in the Discussion section; however, those were some minor engineering improvements, and what is more interesting is the scientific question or results that can be asked or obtained from this study. The current study clearly presents a functional and carefully documented platform, but it would help the reader if the authors more explicitly distinguished the present system from earlier related approaches, both in terms of system design and in terms of experimental validation.

(2) At the system level, several of the claimed advantages could be supported more directly with quantitative data. For example, if the double-detection corridor and alarm system are important distinguishing features, it would be valuable to report measures such as detection accuracy, missed detections, co-entry failures, alarm frequency, and the degree of manual intervention required in practice. Similarly, the welfare-related arguments are plausible and important, but would be strengthened by more direct evidence, such as longitudinal body weight data, water intake, or comparison with group-housed no-task controls.

(3) At the experimental level, the manuscript would also benefit from a more detailed characterization of training performance. Although three behavioral paradigms are presented, the data currently shown provide a stronger demonstration of feasibility than of training optimization. For a study focused on automated cognitive training, it would be critical to include more information on learning speed, progression across stages, success and failure rates, and variability across animals. Along the same lines, the comparison with manual training is a useful addition, but a broader benchmark including learning curves, time to criterion, and between-animal variability would make the practical value of the system easier to assess.

(4) The authors claimed that they conducted 3 complex cognitive tasks (3AFC, 2AFC, 2AB) in their setup. However, those 3 tasks are quite basic for rodents and have been demonstrated in many studies, especially comparing tasks implemented in Yu et al., eLife 2025. Therefore, lowering this 'complex' statement is necessary.

(5) The authors claimed that they have successfully implemented the so-called hybrid mode, but it is only briefly described and not supported by citations or data. Since this may be one of the most broadly applicable use cases of the platform, a more detailed explanation of how the system can be integrated with recording workflows would strengthen the manuscript.

(6) The manuscript highlights the opportunity to relate task behavior to home-cage activity and to study individualized behavioral patterns. To better support these aspects, it would be helpful to include more subject-level analyses, rather than relying predominantly on population averages, or alternatively to discuss in more concrete terms which features of the dataset may be especially informative for studying individuality. More generally, the manuscript would benefit from clarifying whether different parameter settings within this group-housed framework may be better suited for maximizing training efficiency versus preserving more naturalistic or socially modulated behavior, and what the implications of these choices may be for interpretation.

(7) In Table S1, 'Touch screen' is task-specific and is not necessarily a metric. 'Testing outside home cage' is also not necessarily an advantage (please clarify if it is). Many other systems implemented different levels of 'Alarm system', which is not reflected in the table.

(8) Table S3 shows important data that help the reader to evaluate the paper's work, thus is deserved to move to the main text.

Reviewer #2 (Public review):

Summary:

The Training Village (TV) is an innovative autonomous system for rodent training. By integrating an operant box with a group-housed home-cage environment, this platform enables animals to learn operant behaviors while preserving their social context and interactions, which is an aspect often overlooked in the field. The flexibility and modularity of the TV system allow training across multiple cognitive tasks in a continual learning framework. Furthermore, its remote accessibility and affordability make it a compelling tool for the broader neuroscience community.

Comments:

(1) Social Hierarchy and Access Competition

Previous studies on rodent social hierarchy (e.g., PMID: 21960531) have demonstrated clear dominance structures within group-housed animals. Based on this, one might expect dominant animal(s) to occupy more sessions and trials than subordinate animals by preferentially accessing the operant box. Therefore, it is somewhat surprising to observe a relatively uniform distribution of operant box occupancy across animals (Figure 2a, 2i). As a control, it would strengthen the manuscript to include an independent assessment of social hierarchy (e.g., tube test, barber assay, or similar behavioral metrics) to quantitatively characterize dominance relationships within the cohort. Correlating these rankings with chamber occupancy and trial frequency would significantly strengthen the validation of the system's equity.

(2) Behavioral Saving Effects in Continual Learning

The authors demonstrate that the TV platform allows for the sequential learning of multiple cognitive tasks (Figure S3e). This provides an excellent opportunity to examine a continual learning paradigm. A key hallmark of successful continual learning is the "behavior savings effect", where re-learning a previously acquired task occurs faster than initial learning. For example, if animals are trained sequentially on task A (e.g., 2AFC), then task B (e.g., 2AB), and subsequently re-trained on task A, do they exhibit accelerated re-learning? Including such an analysis would significantly strengthen the claim regarding continual learning capabilities.

(3) Robustness of Multi-Animal Attempt Detection

In the TV platform, only one animal can access the operant box at a time under group-housed conditions. This setup inherently introduces the possibility of "multi-animal attempts", as shown in Figure 2j-k and Figure S2c. While the authors address this using pixel-based classification, additional quantitative validation would improve confidence in this approach. For instance, presenting the distribution of pixel counts for single-animal versus multi-animal events would be informative. Moreover, given variability in body size across animals, a fixed pixel threshold may not be sufficient. It would be helpful to include analyses of classification performance (e.g., Type I and Type II error rates) across different animal pairings within the same cohort.

(4) Protocol Flexibility and Implementation

It would be helpful to clarify how behavioral task protocols are switched within the TV system. Specifically, are task changes applied globally to all animals sharing the operant box, or can they be assigned individually? Additionally, are task sequences pre-programmed prior to the experiment, or can they be modified dynamically during ongoing experiments?

(5) Presentation and Readability

To improve readability, the Discussion section could be streamlined, as it is currently somewhat lengthy and descriptive.

Reviewer #3 (Public review):

Summary:

The Training Village (TV) is an open-source automated platform for continuous training and testing of group-housed mice and rats in cognitive tasks. Animals live in enriched multi-compartment home cages and access a single operant box individually through a sorting corridor controlled by RFID identification and real-time video analysis. A Raspberry Pi 5 runs the entire system, manages an adaptive training algorithm, monitors animal welfare, and allows remote supervision via a graphical interface and Telegram alarm system. The system is validated across 12 groups totaling 121 animals, three cognitive paradigms of varying complexity, and experiments lasting up to 12 months.

Strengths:

(1) The open-source implementation is probably the paper's strongest point. The authors provide not just code but 3D-printable designs, a full bill of materials with costs (~5500€ total), assembly instructions, and a dedicated website. The estimated build time of 2-7 days is credible. In the current landscape of methods papers, this level of documentation is the minimum necessary to allow other laboratories to actually adopt and propagate the system - and the authors deliver it fully. The compatibility with two operant box designs, three cognitively distinct tasks, and two species - demonstrated empirically rather than merely claimed - makes the modularity argument credible and distinguishes the TV from systems designed around a single paradigm. Finally, the combination of automatic weighing at each exit, temperature and humidity tracking, and a granular Telegram alarm system (Table S2) represents a meaningful practical contribution. For a system operating 24/7 without daily human supervision, this level of welfare monitoring is a necessity, and it seems well implemented here.

(2) With 121 animals across 12 groups, three distinct cognitive paradigms, two species, and longitudinal data spanning up to 12 months, the validation effort is substantial. The authors acknowledge the limitations of their comparisons - notably that the TV vs. manual training comparison is not a controlled experiment. The rat dataset is limited in scope, but the authors at least demonstrate that the system can be adapted to a second species, which is a useful proof of concept. The demonstration that task engagement increases progressively over 12 months (Fig. 3g) is a novel observation at this temporal scale, with practical implications for the design of long-term experiments.

(3) The demonstration that operant box usage is distributed nearly uniformly across animals (Gini < 0.15 in all groups) is carefully demonstrated and addresses a question that any laboratory considering this type of system will legitimately ask, e.g., whether dominant individuals monopolize access at the expense of subordinates. This has been shown before in comparable systems, but remains a necessary validation for each new implementation. The control condition removing temporal constraints (Figure S4) adds useful mechanistic insight into the role of the refractory interval. However, the interpretation of this result deserves more nuance than the authors provide - see Weaknesses.

Weaknesses:

(1) The TV is more than an automation tool; its architecture makes the most sense if one intends to study how spontaneous home cage behavior relates to individual cognitive performance, and the introduction and discussion explicitly frame this as a key application. Yet the analysis delivers only group-level descriptive results, and the cognitive data are presented almost exclusively as group averages. The individual-level questions that the system is uniquely positioned to address (do stable home cage behavioral profiles emerge across animals, do animals learn at the same rate and using the same strategies, and do these dimensions correlate with each other ) are never asked. This is particularly relevant given that enriched social environments are precisely the conditions under which stable inter-individual differences tend to emerge spontaneously, even among genetically identical animals (Freund et al., 2013, Science), and that comparable systems have already linked such profiles to cognitive and neurochemical phenotypes (Torquet et al., 2018, Nature Communications). The TV clearly has the data to begin exploring this - doing so would substantially strengthen the paper's scientific contribution beyond its methodological value.

(2) Sustained daytime operant box usage in nocturnal animals deserves more discussion: Box occupancy during the light phase remains around 75% - only modestly below the ~85% seen at night (Fig. S5a-b). The authors conclude this reflects "sustained engagement with the task throughout the circadian cycle," but other explanations are not considered: residual thirst driving animals to seek sucrose water during the day, and the refractory interval mechanically redistributing sessions into the light phase? A more explicit discussion of the consequences of 24/7 unsupervised testing for data quality (daytime sessions may yield noisier behavioral data?) would be useful.

(3) The finding that all animals access the operant box in roughly equal proportions (Gini < 0.15) is practically important and carefully demonstrated. However, the authors' interpretation that animals self-organize in an egalitarian manner despite known social hierarchies deserves a note of caution. The system design itself constrains monopolization: the refractory interval imposes the same waiting time on all animals regardless of social rank, and session duration determines how often the box becomes available. The no-constraint control (Figure S4) partially addresses this but was run on already-trained animals, limiting its interpretive value. The key practical message, that all animals can access the task regularly under the proposed design, is well supported. Whether this reflects genuine social tolerance or is primarily a consequence of system constraints is a subtler question that the current data cannot fully resolve.

(4) The rat cohort consists of a single group of 6 female Long-Evans rats, yet species comparisons are drawn across multiple dimensions (daily sessions, task engagement, performance...). Observed differences could reflect group size, sex, strain, reward calibration, or simple individual variability rather than species differences. These results should be presented for what they are: a useful proof of concept showing the system works with a second species, not a basis for comparative conclusions.

Reviewer #1 (Public review):

Summary:

This paper examines whether humans use protracted temporal integration in a noise-free, deferred-response contrast discrimination task, using a covert evidence-duration manipulation combined with EEG (SSVEP, CPP, Mu/Beta). The key finding is that evidence for protracted sampling is behaviorally and neurally supported, but even joint CPP + behaviour fitting cannot fully discriminate a standard integration (DDM) model from a novel "extremum-flagging" non-integration model. The paper is transparent about this outcome.

Strengths:

This is a well-conducted and well-written study that makes a genuine contribution to the perceptual decision-making literature by introducing a clean experimental design for probing temporal integration without participants adapting their strategy and demonstrating for the first time that a non-integration model (extremum-flagging) can replicate CPP waveform dynamics that have long been considered hallmarks of evidence accumulation. The transparent treatment of equivocal modelling outcomes is commendable.

Weaknesses:

My main concerns relate to statistical power, the under-specification of the and the extremum-flagging mechanism. Addressing these would greatly strengthen the paper.

(1) The sample of 16 participants (15, after the exclusion of one participant) is described as "close to similar EEG studies" with no formal power analysis. Given that the paper's core claim rests on subtle quantitative differences between two model classes - differences that are, by the authors' own admission, not sufficient to declare a winner - even a modest increase in sample size might yield a more decisive outcome. At a minimum, the authors should report a sensitivity analysis or post-hoc power calculation to indicate what effect sizes the current N could reliably detect, particularly for the rmANOVA comparisons and the neural constraint fitting.

(2) The Extremum-flagging model is the paper's most novel contribution, yet its physiological basis is underspecified. The model posits that each decision-terminating bound-crossing triggers a stereotyped, half-sine-shaped centroparietal signal, but no neural circuit or computational mechanism is proposed for how the brain could detect the first bound-crossing event in a non-accumulating evidence stream or generate a temporally precise, fixed-amplitude signal in response. Possible connections to P3b theories of context updating and response facilitation are acknowledged, but these are vague functional descriptions rather than mechanistic accounts. I think the discussion should engage more directly with potential neural substrates that could generate this flagging signal, and whether these are consistent with the known generators of the CPP/P3b. Without this, the extremum-flagging model risks being viewed as a mathematical convenience rather than a biologically plausible alternative.

(3) The Integration model at the preferred neural weighting estimates a high-to-low contrast drift rate ratio of 8.7, whereas the empirical Mu/Beta lateralization slopes suggest a ratio of approximately 3.5. The authors attribute this discrepancy to the nonlinear contrast response function of early visual cortex and the salience of the high-contrast evidence onset, but these explanations are speculative. These outcomes are arguably the most quantitatively damaging result for the integration model, so they deserve more than a brief discussion. I would recommend that the authors (a) estimate what range of contrast response nonlinearities would be required to close this gap, (b) test whether an alternative drift rate parameterization (e.g., scaling drift rates directly by SSVEP amplitude rather than contrast) reduces the discrepancy, or (c) be more explicit about treating this as a point against the Integration account.

(4) The sensitivity analysis over neural constraint weightings (w = 0.1 to 1000) is thoughtful, but the paper ultimately acknowledges that the preferred weighting is w=10, chosen because it achieves "a good fit to CPP dynamics without substantively sacrificing behavioral fit" - a qualitative criterion. No principled statistical framework is used to select the optimal weighting or to compare models at a given weighting. A Bayesian model comparison could provide a more formal framework for combining behavioral and neural fit components, and would allow a clearer statement about the relative posterior probability of each model.

Reviewer #2 (Public review):

Summary:

The manuscript by Hajimohammadi, Mohr, O'Connell and Kelly is intended to demonstrate that participants integrate evidence over time to make a decision, even in a noise-free, static decision context. This is validated by the observation that (1) participant accuracy improves with increased exposure to the stimulus; and (2) there is a correlation between participant accuracy and a neural index of evidence accumulation, as measured by centro-parietal positivity (CPP).

Strengths:

(1) Joint modelling of accuracy and CPP dynamics is a significant achievement, as behaviour alone often cannot distinguish between competing theories of decision-making. In the case of protracted sampling in particular, the absence of reaction times (RT) due to the delayed nature of the response makes this method highly appealing.

(2) The experimental manipulations and the method used to extract the different neural indices are well chosen, enabling the mapping of putative cognitive processes such as evidence accumulation and motor preparation onto the recorded EEG with clarity.

(3) The in-depth discussion of the results clearly articulates those reported by the authors and in previous works.

Weaknesses:

(1) One main issue to support the interpretation of the authors toward the need for protracted sampling is the timing of the evidence. By design, participants believe that the signal is present for 1.6 seconds (reinforced by the fact that easy trials were displayed for 1.6 seconds). However, the difference in stimuli is turned off either 1.4, 1.2, 0.8 or 0 seconds before the cue to respond. While this makes sense in the context of the authors' question, it also raises the possibility that participants will focus on the last samples before answering. Even if participants apply equal weighting, this still favours them delaying evidence accumulation until they are sufficiently certain that the evidence should be present (e.g. participants might start accumulating after the stimulus has disappeared in the 0.2 condition). I do not see an easy way to test these alternative explanations outside of running a study in which the evidence is always offset before the go cue.

(2) Regarding the behavioural models, are these identifiable based on accuracy data alone? This should be addressed using a parameter recovery study, in which a set of parameters is used to generate data, and the same fitting routine used for the real data is used to estimate the parameters. This would enable us to determine what can be inferred from the model comparison presented. This is not a serious problem for the manuscript, as it specifically aims to go beyond behaviour. It is, however, worth noting that such a parameter recovery addition could be used to demonstrate the need for a joint modelling framework to answer the question of protracted sampling on delayed response times (RT).

Minor comments:

(1) I would advise authors to fix the D1 parameter and use it as a scaling parameter across all models. Currently, as I understand it, the models are scale-free, meaning the same fit is achieved by multiplying all parameters by two, for example. This makes the fit more complex (bounds on parameter values are required) and means that the models are less comparable in terms of their estimates. Perhaps I'm missing something, but I would have thought that fixing D1 (the common parameter across all models) would solve these issues.

(2) Why is the snapshot model so bad despite being a good model in Stine et al 2020? Can the authors speculate in the discussion?

(3) The meaning of the flag width is unclear. Figure 4 provides the reader with an intuitive understanding of the model that the authors have in mind. However, the tables in the appendices report values between 0.2 and 0.9. I understand that these values represent the width of the half-sine in seconds. This suggests that the actual estimated values for these flag events are much broader than those displayed in Figure 4. While this is probably fine for most models, it can be problematic for the extremum-flagging model, as it means that the rise to the peak takes between 0.1 and 0.45 seconds. While strictly speaking, this is still a 'flag' model, such a slow rise to the peak, given the usual expectation of evidence accumulation, would place this model closer to a smooth integration model than to a boundary-crossing flagging mechanism.

(4) In the modelling section, it is not clear overall (i.e. for G² and R²) how the participant dimension is taken into account. Are these individually fitted models, and if so, how are the secondary statistics generated from the individual estimates? Or were these fitted over all participants?

(5) On page 7, in the last sentence of the first paragraph of the section titled 'Decision-Related Neural Signals', the authors state that 'this stable contrast-difference encoding suggests that a constant (i.e. non-adapting) drift rate is a reasonable simplifying model assumption'. However, I am not sure how this is true given that SSVEP quantifies encoding, yet the drift rate can vary due to non-sensory aspects (e.g. attention).

(6) The mu/beta lateralisation does indeed favor the integration model more, but in terms of boundary estimation and starting-point analyses, both models are pretty far apart. Providing an interpretation of this observation, e.g. regarding alternative linking functions for mu/beta, would add to the manuscript.

Reviewer #3 (Public review):

Summary:

The authors aim to compare proposal models of perceptual decision making using a joint modeling approach, where they fit models to both behavioral outcomes as well as CPP. Most notably, they compare a standard evidence accumulation model with models that track the evidence without integrating it over time (extrema detection). The authors report that the joint CPP-behavioral data do not discriminate between two of their proposals.

Strengths:

This is an interesting finding that reinforces the idea that what we believe to see based on aggregation over trials may not be what happens on every single trial. The models are creative, and the simulations are convincing, relating the models to multiple neural markers of decision formation. These include the CPP but also mu/beta power spectra.

Weaknesses:

The paper makes some strong points, and the work seems generally well-executed. The weaknesses that I identified are twofold:

(1) Embedding in the literature/exposition of the main argument.

The focus in the introduction is on the noise-free nature of the stimulus and the prolonged presentation time. However, after reading the paper, I felt these were mostly experimental design choices that enable comparison of the different models using the CPP. Perhaps my misreading of the goals of the paper stems from two other observations:

a) The fact that the stimulus is noise-free does not entail that perception is noise-free. Thus, the argument that using a noise-free stimulus precludes the necessity of temporal integration seems not completely valid. Of course, one could argue that noise is limited in this case, but that makes a noise-free stimulus more of a design choice.

b) The focus on prolonged stimulus presentation, but at the same time the contrast with expanded judgement, did not make sense to me. Perhaps, as a non-native speaker, I am misreading the subtle difference between "protracted sampling" and "longer sampling", but again, the longer duration seems mostly a design choice.

More could be said about the optimality of the extrema detection methods. In particular, decades of work (centuries?) have shown that evidence integration is an optimal decision-making procedure: For example, the Sequential Probability Ratio Test is Bayes-optimal wrt mean RT (Wald, 1946); evidence accumulation together with collapsing threshold serves to maximize rewards in repeated choices (e.g., Bogacz et al., PsychRev, 2006; Boehm et al. APP, 2020). Given all this work, why would the brain have evolved to adopt a different mechanism? I realize that the paper is not about optimal decision making, but some discussion of this point seems warranted.

(2) Modeling choices.

The authors introduce a parameter, sampT, that represents uncertainty in the sampling onset time. It was not clear to me whether this parameter represented an offset of all trials, or a distribution (probably the latter). I wonder how exactly this parameter was integrated into the models, and in particular, if and how it interacts with the starting-point parameters. My intuition is that on a single-trial, IF early sampling occurs, you can model that with either a negative sampT and z at 0, or with sampT at 0 but a shift in z. This would suggest trade-offs between these parameters, making them hard to estimate independently. Since the paper does not depend on the identification of parameter estimates, this may not be a huge problem, but nevertheless it is good to explore the consequences.

The way the Bounded Integration model (BIntg) is formulated seems very close to the EZ-diffusion model (Wagenmakers et al., PBR, 2007). This model states that the proportion of correct responses Pc = 1/(1+exp(-B*D/s^2), with B and D the bound and drift rate parameters, respectively. However, filling in the numbers for the high contrast condition from Table 2, and assuming that s=2 (because the model description states that dt=2, with s undefined), I get a Pc of 80% for the 1.6H condition. This seems substantially less than what Figure 2 suggests.

On some occasions, it is unclear to me what modeling choices are being made:

a) It seems as if the models are fit on accuracy data alone (before introducing the neural data). This seems suboptimal given that the authors do report differences in RT.

b) Are the models fit on all data combined, or on the data of individual participants? Fitting individual participant data is preferred, as combined or aggregated data may be distorted by individual differences.

c) The authors seem to suggest that the diffusion coefficient s is estimated (in the section "Integration models"). Most likely, however, this is set to a fixed value. Obviously, it matters for the model comparison using AIC whether this parameter was freely estimated or not.

Not really a weakness, but I wondered about the effect of stimulus duration on RT. In particular, what hypothesis (or post hoc explanation) do the authors have for these RT effects? I could think of at least three hypotheses that are consistent with the behavioral data:

a) H1: The shorter the evidence duration, the more likely participants are to require a double-check before response execution, reflecting their uncertainty about their decision.<br /> b) H2: There is a collapsing threshold that initiates at stimulus offset, leading to quicker responses on trials where there is more evidence.<br /> c) H3: motor preparation is correlated with the evidence signal, which leads to faster responses on trials with more evidence.

Reviewer #1 (Public review):

Vasilevskaya and Keller test different models of cortical function through the lens of predictive processing, a powerful framework for the brain to learn and predict the statistics of the world via generative internal models. The authors use a clever combination of behavioral perturbations in closed-loop and open-loop visuomotor virtual reality assays, a paradigm the Keller lab pioneered and used effectively in the past decade, in conjunction with two-photon imaging of neuronal calcium responses and targeted optogenetic perturbations of activity. They specifically put to test proposed hierarchical vs. non-hierarchical circuit implementations of predictive processing by analyzing the logic of inter-lamina interactions (superficial vs. deep; L2/3 vs. L5/6).

The authors conclude that both versions of predictive processing architectures they analyze are likely invalid, and instead formulate an alternative novel model of cortical function based on a recently developed machine learning algorithm for self-supervised learning (joint embeddings of predictive architectures, JEPA) and its further refinements. JEPA borrows elements from predictive processing, engaging two encoder networks and training the output of one network to predict the output of the other. In their new model of cortical computations, prediction error neurons in L2/3 compare the deep layers (L5/6) activity, which is taken as a teaching signal, to a local, L2/3 prediction of this latent representation.

Specifically, the authors build on their previous work and reports from other groups that different sets of L2/3 neurons compute positive prediction errors (fire when sensory stimuli appear unexpectedly with respect to the movements of the animal; e.g., grating onsets in the absence of locomotion) and respectively negative prediction errors (fire when sensory stimuli are absent, while the brain expected them to be present; e.g. mice locomote but visual flow is suddenly halted - visuomotor mismatches). These L2/3 positive and negative prediction error neurons exchange messages with neurons in the deeper cortical layers that, the authors propose, build an internal representation (R) of the sensory stimuli given the animals' movements.

In the hierarchical model, internal representation neurons (R) are supposed to act as a teaching signal for both types of prediction error neurons; the output of the positive prediction error neurons is assumed to suppress activity of R such that the error between the teaching signal and the prediction is minimized; similarly, in the non-hierarchical version, R serves as a prediction for the prediction error neurons, and in turn it receives excitatory drive from the positive prediction error neurons and negative input from the negative prediction error neurons.

The authors find that the functional impact of L5 neurons on L2/3 neurons is not compatible with the non-hierarchical architecture they and other groups proposed, but rather in accordance with the hierarchical model. At the same time, the functional impact of L2/3 neurons (positive vs. negative prediction error neurons) on L5 neurons (internal representation) appears not compatible with the hierarchical model, but rather in accordance with the non-hierarchical implementation.

They further hypothesize that L2/3 prediction error neurons don't use sensory input, but rather the L5 activity as a teaching signal, and test it using perturbations (halts) of optogenetic stimulation of L5 neurons coupled with locomotion (Figure 7).

All in all, the question is topical, and the new model addresses a decades-long quest to develop a unifying model of cortical function. The findings reported here transform our understanding of cortical computations, opening new, exciting avenues for future investigation. The experimental design and execution are rigorous; the arguments are clearly laid out (in spite of ample potential for confusion given the numerous loops and sign flips). These include a discussion of why the non-hierarchical model proposed by the same group does not hold, as well as potential caveats in interpreting the results and novel testable proposed experiments emerging from the JEPA-like model.

I have several questions about the interpretations of some of the claims and suggestions for potential additional experiments and analyses.

(1) Some of the pieces of the puzzle remain to be identified and demonstrated: the existence of internal representation neurons in L2/3 and ascertaining that the L5/6 neurons analyzed function indeed as internal representation neurons. The authors find that stimulation of L2/3 positive prediction error neurons enhances activity of L5 neurons...If L5 neurons hold a latent representation that serves as a teaching signal for L2/3 neurons (as the authors posit), wouldn't one expect that the input they receive from the positive prediction neurons be suppressive, such that the error is further minimized?

(2) Do the authors envision any specific differences between the representations of the two encoder networks posited to exist in L2/3 and L5 in the JEPA-like implementation? Are they synchronous/offset in their temporal representations, or any other features?

(3) Where is the prediction coming from onto L2/3 neurons? Is it emerging locally in L2/3 from the putative internal representation neurons, or is it long-range - as work from the authors previously proposed? Or a mix of both?

(4) What is the role of the indiscriminate L4 input that appears to enhance activity of both positive and negative prediction error neurons in L2/3?

(5) Does Figure 7D change in a meaningful manner if the authors plot the correlation between optomotor mismatch response and visuomotor mismatch response specifically for the negative prediction error neurons in L2/3 (Adamts-2) rather than for all L2/3 cells sampled?

(6) Do the optomotor mismatch responses in L2/3 neurons depend on how long the closed-loop coupling of optogenetic stimulation of Tlx3 L5 neurons and locomotion speed has been in place for?

Reviewer #2 (Public review):

This manuscript reveals the functional connectivity of two different classes of cortical neurons that respond in opposite ways to mismatches between sensory and top-down inputs. These data are very valuable because different theories of information processing in the cortex make different predictions on the patterns of connectivity of these neurons. Therefore, these data strongly constrain possible theories of cortical processing.

General comments:

(1) The methods of statistical testing are insufficiently described. I did not understand the description in lines 1105-1119. The authors should provide sufficient details so the reader can reproduce their analyses. For example, it may be helpful to provide specific details of the testing procedure for one of the comparisons (e.g. the first comparison in Table S1).

(2) The authors should clarify how the problem of multiple comparisons was addressed for comparisons performed in multiple moments of time, where significance is indicated by a black bar (e.g. in Figure 2F).

(3) It would be helpful to add a figure in the Discussion summarising the functional connectivity suggested by all experiments.

(4) Throughout the manuscript, the authors use the term "teaching signals", but I am unclear what they mean by it: after reading the definition in lines 45-46, I thought that they corresponded to values (as they are compared to sensory signals). Later (428-430), the text suggests that they correspond to error neurons. But then lines 605-607 say it is not an error signal. The authors should define teaching signals very precisely or remove this term.

Reviewer #3 (Public review):

Vasilevskaya and Keller set out to experimentally distinguish between two variants of predictive processing: a hierarchical and a non-hierarchical variant. The hierarchical variant assumes a hierarchical organization in which internal representation neurons (believed to be a subset of layer 5 excitatory neurons) serve as a source of a teaching signal for local prediction error neurons as well as for the next higher level of the hierarchy, while simultaneously providing prediction signals to the preceding lower level. In contrast, the non-hierarchical variant posits that these layer 5 internal representation neurons provide local predictions to layer 2/3 prediction error neurons.

The interaction between internal representation neurons and prediction error neurons differs fundamentally between the two variants. In the hierarchical variant, internal representation neurons excite positive prediction error neurons and inhibit negative prediction error neurons, while at the same time being inhibited by positive prediction error neurons and excited by negative prediction error neurons. In the non-hierarchical variant, this pattern of connectivity is reversed.

This work is very exciting, timely, and carefully executed. The authors functionally, and later molecularly, identify layer 2/3 prediction error neurons in V1 and probe their interactions with genetically defined neuron types in cortical layers 5 and 6 using optogenetics. They demonstrate that the functional influence of putative prediction error neurons in layer 2/3 onto layer 5 is incompatible with the hierarchical variant, whereas the influence of layer 5 onto putative prediction error neurons in layer 2/3 is incompatible with the non-hierarchical variant. They then test an alternative hypothesis, in which layer 2/3 responses resemble prediction errors with respect to perturbations of artificial layer 5 activity patterns. To investigate this, they designed an experiment in which optogenetic activation of L5 IT neurons was closed-loop coupled to the mouse's locomotion speed in the absence of visual feedback, allowing them to probe the causal influence of L5 activity on layer 2/3 responses.

Finally, the authors hypothesize that their data are more consistent with a joint embedding predictive architecture (JEPA) and outline experimentally testable predictions arising from this framework.

While the work is overall convincing and significantly advances our understanding of the circuit-level implementation of predictive processing, there are a few weaknesses that should be addressed or discussed:

(1) The authors define putative positive prediction error neurons as the 15% of neurons most responsive to grating onset and putative negative prediction error neurons as the 15% most responsive to visuomotor mismatch. While this selection would be expected to overlap with negative and positive prediction error neurons, the criterion is not sufficiently stringent (independent of the exact percentage chosen). In particular, classification of a neuron as a prediction error neuron should ideally be accompanied by evidence that it does not exhibit a significant increase in activity when the prediction matches the sensory input or teaching signal.

(2) The authors "speculate that the prediction error responses in layer 2/3 may not be computed with respect to sensory input, but with respect to layer 5 activity as a teaching signal." However, it is unclear how this perspective differs from earlier statements in the manuscript. In the Introduction, the authors note that "these signals, typically referred to as sensory signals, we will refer to as teaching signals," and later describe the hierarchical variant as one "in which internal representation neurons act as a source of the teaching signal." Given this framing, it is difficult to identify what is conceptually novel in the updated view. Is the key distinction that layer 2/3 neurons are now proposed to generate predictions in an internal representation space rather than in sensory input space, as briefly suggested in the Discussion? Or are the authors introducing a distinction between an external (sensory) and an internal (cortical) teaching signal? If so, this distinction should be made explicit. Clarifying this point would considerably strengthen the manuscript.

(3) The authors propose that "L2/3 neurons predict L5 activity, hence making predictions in the internal representation space rather than the input space," and further suggest that, since both deep and superficial cortical layers receive thalamic input, the cortex may function like a JEPA. This idea appears closely related to the model introduced by Nejad et al. (2025), which effectively implements a JEPA-like architecture: L5 activity serves as a target against which L2/3 predictions are compared in a self-supervised manner, with both L5 and L2/3 (via L4) receiving thalamic input. It would be helpful for the authors to clarify how their framework differs from that model, and to specify the key conceptual or mechanistic distinctions between the present proposal and the approach described by Nejad et al..

Reviewer #1 (Public review):

Summary:

This manuscript investigates mutations and expression patterns of zinc finger proteins in Kenyan breast cancer patients. Whole-exome sequencing and RNA-seq were performed on 23 breast cancer samples alongside matched normal tissues.

Strengths:

Whole-exome sequencing and RNA-seq were performed on 23 breast cancer samples alongside matched normal tissues in Kenyan breast cancer patients. The authors identified mutations in ZNF217, ZNF703, and ZNF750.

Weaknesses:

(1) Research scope:

The results primarily focus on mutations in ZNF217, ZNF703, and ZNF750, with limited correlation analyses between mutations and gene expression. The rationale for focusing only on these genes is unclear. Given the availability of large breast cancer cohorts such as TCGA and METABRIC, the authors should compare their mutation profiles with these datasets. Beyond European and U.S. cohorts, sequencing data from multiple countries, including a recent Nigerian breast cancer study (doi: 10.1038/s41467-021-27079-w), should also be considered. Since whole-exome sequencing was performed, it is unclear why only four genes were highlighted, and why comparisons to previous literature were not included.

(2) Language and Style Issues

There are many typos and clear errors in the main text (e.g. (ref)).

Additionally, several statements read unnaturally. For example:

"Investigators uncovered 170 mutations ..." should instead be phrased as "We identified 170 mutations ...."

"The research team ..." should be rephrased as "Our team ...."

(3) Methods and Data Analysis Details

The methods section is vague, with general descriptions rather than specific details of data processing and analysis. The authors should provide:

(a) Parameters used for trimming, mapping, and variant calling (rather than referencing another paper such as Tang et al. 2023).

(b) Statistical methods for somatic mutation/SNP detection.

(c) Details of RNA purification and RNA-seq library preparation.

Without these details, the reproducibility of the study is limited.

(4) Data Reporting

This study has the potential to provide a valuable resource for the field. However, data-sharing plans are unclear. The authors should:

a) Deposit sequencing data in a public repository.

b) Provide supplementary tables listing all detected mutations and all differentially expressed genes (DEGs).

c) Clarify whether raw or adjusted p-values were used for DEG analysis.

d) Perform DEG analyses stratified by breast cancer subtypes, since differential expression was observed by HER2 status, and some zinc finger proteins are known to be enriched in luminal subtypes.

(5) Mutation Analysis

Visualizations of mutation distribution across protein domains would greatly strengthen interpretation. Comparing mutation distribution and frequency with published datasets would also contextualize the findings.

Comments on revisions:

The revised manuscript hasn't addressed any of these concerns. Careful proofreading is recommended, even if the authors do not intend to make further modifications to the manuscript.

Reviewer #2 (Public review):

Summary:

This work integrated the mutational landscape and expression profile of ZNF molecules in 23 Kenyan women with breast cancer.

Strengths:

The mutation landscape of ZNF217, ZNF703, and ZNF750 were comprehensively studied and correlate with tumor stage and HER2 status to highlight the clinical significance.

Weaknesses:

The current cohort size is relatively small to reach significant findings, and targeted exploration on ZNF family without emphasizing the reason or clinical significance hinders the overall significance of the entire work.

Reviewer #3 (Public review):

Summary: