Reviewer #2 (Public review):

Summary:

This study introduces SemReps-8K, a large multimodal fMRI dataset collected while subjects viewed natural images and matched captions, and performed mental imagery based on textual cues. The authors aim to train modality-agnostic decoders--models that can predict neural representations independently of the input modality - and use these models to identify brain regions containing modality-agnostic information. They find that such decoders perform comparably or better than modality-specific decoders and generalize to imagery trials.

Strengths:

(1) The dataset is a substantial and well-controlled contribution, with >8,000 image-caption trials per subject and careful matching of stimuli across modalities - an essential resource for testing theories of abstract and amodal representation.

(2) The authors systematically compare unimodal, multimodal, and cross-modal decoders using a wide range of deep learning models, demonstrating thoughtful experimental design and thorough benchmarking.

(3) Their decoding pipeline is rigorous, with informative performance metrics and whole-brain searchlight analyses, offering valuable insights into the cortical distribution of shared representations.

(4) Extension to mental imagery decoding is a strong addition, aligning with theoretical predictions about the overlap between perception and imagery.

Weaknesses:

While the decoding results are robust, several critical limitations prevent the current findings from conclusively demonstrating truly modality-agnostic representations:

(1) Shared decoding ≠ abstraction: Successful decoding across modalities does not necessarily imply abstraction or modality-agnostic coding. Participants may engage in modality-specific processes (e.g., visual imagery when reading, inner speech when viewing images) that produce overlapping neural patterns. The analyses do not clearly disambiguate shared representational structure from genuinely modality-independent representations. Furthermore, in Figure 5, the modality-agnostic encoder did not perform better than the modality-specific decoder trained on images (in decoding images), but outperformed the modality-specific decoder trained on captions (in decoding captions). This asymmetry contradicts the premise of a truly "modality-agnostic" encoder. Additionally, given the similar performance between modality-agnostic decoders based on multimodal versus unimodal features, it remains unclear why neural representations did not preferentially align with multimodal features if they were truly modality-independent.

(2) The current analysis cannot definitively conclude that the decoder itself is modality-agnostic, making "Qualitative Decoding Results" difficult to interpret in this context. This section currently provides illustrative examples, but lacks systematic quantitative analyses.

(3) The use of mental imagery as evidence for modality-agnostic decoding is problematic. Imagery involves subjective, variable experiences and likely draws on semantic and perceptual networks in flexible ways. Strong decoding in imagery trials could reflect semantic overlap or task strategies rather than evidence of abstraction.

The manuscript presents a methodologically sophisticated and timely investigation into shared neural representations across modalities. However, the current evidence does not clearly distinguish between shared semantics, overlapping unimodal processes, and true modality-independent representations. A more cautious interpretation is warranted. Nonetheless, the dataset and methodological framework represent a valuable resource for the field.

Reviewer #3 (Public review):

Summary:

The authors recorded brain responses while participants viewed images and captions. The images and captions were taken from the COCO dataset, so each image has a corresponding caption, and each caption has a corresponding image. This enabled the authors to extract features from either the presented stimulus or the corresponding stimulus in the other modality. The authors trained linear decoders to take brain responses and predict stimulus features. "Modality-specific" decoders were trained on brain responses to either images or captions, while "modality-agnostic" decoders were trained on brain responses to both stimulus modalities. The decoders were evaluated on brain responses while the participants viewed and imagined new stimuli, and prediction performance was quantified using pairwise accuracy. The authors reported the following results:

(1) Decoders trained on brain responses to both images and captions can predict new brain responses to either modality.

(2) Decoders trained on brain responses to both images and captions outperform decoders trained on brain responses to a single modality.

(3) Many cortical regions represent the same concepts in vision and language.

(4) Decoders trained on brain responses to both images and captions can decode brain responses to imagined scenes.

Strengths:

This is an interesting study that addresses important questions about modality-agnostic representations. Previous work has shown that decoders trained on brain responses to one modality can be used to decode brain responses to another modality. The authors build on these findings by collecting a new multimodal dataset and training decoders on brain responses to both modalities.

To my knowledge, SemReps-8K is the first dataset of brain responses to vision and language where each stimulus item has a corresponding stimulus item in the other modality. This means that brain responses to a stimulus item can be modeled using visual features of the image, linguistic features of the caption, or multimodal features derived from both the image and the caption. The authors also employed a multimodal one-back matching task, which forces the participants to activate modality-agnostic representations. Overall, SemReps-8K is a valuable resource that will help researchers answer more questions about modality-agnostic representations.

The analyses are also very comprehensive. The authors trained decoders on brain responses to images, captions, and both modalities, and they tested the decoders on brain responses to images, captions, and imagined scenes. They extracted stimulus features using a range of visual, linguistic, and multimodal models. The modeling framework appears rigorous, and the results offer new insights into the relationship between vision, language, and imagery. In particular, the authors found that decoders trained on brain responses to both images and captions were more effective at decoding brain responses to imagined scenes than decoders trained on brain responses to either modality in isolation. The authors also found that imagined scenes can be decoded from a broad network of cortical regions.

Weaknesses:

The characterization of "modality-agnostic" and "modality-specific" decoders seems a bit contradictory. There are three major choices when fitting a decoder: the modality of the training stimuli, the modality of the testing stimuli, and the model used to extract stimulus features. However, the authors characterize their decoders based on only the first choice-"modality-specific" decoders were trained on brain responses to either images or captions, while "modality-agnostic" decoders were trained on brain responses to both stimulus modalities. I think that this leads to some instances where the conclusions are inconsistent with the methods and results.

First, the authors suggest that "modality-specific decoders are not explicitly encouraged to pick up on modality-agnostic features during training" (line 137) while "modality-agnostic decoders may be more likely to leverage representations that are modality-agnostic" (line 140). However, whether a decoder is required to learn modality-agnostic representations depends on both the training responses and the stimulus features. Consider the case where the stimuli are represented using linguistic features of the captions. When you train a "modality-specific" decoder on image responses, the decoder is forced to rely on modality-agnostic information that is shared between the image responses and the caption features. On the other hand, when you train a "modality-agnostic" decoder on both image responses and caption responses, the decoder has access to the modality-specific information that is shared by the caption responses and the caption features, so it is not explicitly required to learn modality-agnostic features. As a result, while the authors show that "modality-agnostic" decoders outperform "modality-specific" decoders in most conditions, I am not convinced that this is because they are forced to learn more modality-agnostic features.

Second, the authors claim that "modality-specific decoders can be applied only in the modality that they were trained on, while "modality-agnostic decoders can be applied to decode stimuli from multiple modalities, even without knowing a priori the modality the stimulus was presented in" (line 47). While "modality-agnostic" decoders do outperform "modality-specific" decoders in the cross-modality conditions, it is important to note that "modality-specific" decoders still perform better than expected by chance (figure 5). It is also important to note that knowing about the input modality still improves decoding performance even for "modality-agnostic" decoders, since it determines the optimal feature space-it is better to decode brain responses to images using decoders trained on image features, and it is better to decode brain responses to captions using decoders trained on caption features.

Reviewer #1 (Public review):

In this manuscript, the authors describe a new method to more accurately estimate the fitness advantage of new SARS-CoV-2 variants when they emerge. This was a key public health question during the pandemic and drove a number of important policy choices during the latter half of the acute phase of the pandemic. They attempt to link fitness to expected wave size. The analyses are tested on data from 33 different US states for which the data were considered sufficient. The main novelty of the method is that it links the frequency of variants to the number of cases and thus estimates fitness in terms of the reproduction number.

The results with the new method appear to be more consistent estimates of fitness advantage over time, suggesting that the methods suggested are more accurate than the comparator methods.

Given that the paper presents a methodological advancement, the absence of a simulation study is a weakness. I am satisfied that the trends estimated via the different approaches suggest a useful advancement for a difficult problem. However, the work would have been considerably stronger if synthetic data had been used to illustrate without doubt how the revised method better captures underlying, pre-specified differences in fitness.

Reviewer #2 (Public review):

Summary:

This study develops a joint epidemiological and population genetic model to infer variant-specific effective reproduction numbers Rt and growth advantages of SARS-CoV-2 variants using US case counts and sequence data (Jan 2021-Mar 2022). For this, they use the commonly used renewal equation framework, observation models (negative binomial with zero inflation and Dirichlet-multinomial likelihoods, both to account for overdispersion). For the parameterization of Rt, again, they used a classic cubic spline basis expansion. Additionally, they use Bayesian Inference, specifically SVI. I was reassured to see the sensitivity analysis on the generation time to check effects on Rt.

This is an incredibly robust study design. Integrating case and sequence data enables estimation of both absolute and relative variant fitness, overcoming limitations of frequency-only or case-only models. This reminds me of https://www.medrxiv.org/content/10.1101/2023.01.02.23284123v4.full

I also really appreciated the flexible and interpretable parameterization of the renewal equations with splines. But I may be biased since I really like splines!

The approach is justified, however, it has some big limitations. Specifically, there are some notable weaknesses, that I detail below.

(1) The model does not account for demographic stochasticity or transmission overdispersion (superspreading), which are known to affect SARS-CoV-2 dynamics and can bias Rt, especially in low incidence or early introduction phases.

(2) While the authors explore the sensitivity of generation time, the reliance on fixed generation time parameters (with some adjustments for Delta/Omicron) may still bias results

(3) There is no explicit adjustment for population immunity, which limits the ability to disentangle intrinsic variant fitness (even though the model allows for inclusion of covariates - this to me is one of two major flaws in the study.

(4) The second major flaw in my opinion is that there is no hierarchical pooling across states - each state is modeled independently. A hierarchical Bayesian model could borrow strength across states, improving estimates for states with sparse data and enabling more robust inference of shared variant effects.

I would strongly recommend the following things in order of priority, where the first two points I consider critical.

(1) Implement a hierarchical model for variant growth advantages and Rt across states.

(2) Include time-varying covariates for vaccination rates, prior infection, and non-pharmaceutical interventions directly. This would help disentangle intrinsic variant transmissibility from changes in population susceptibility and behavior.

(3) Extend the renewal model to a stochastic or branching process framework that explicitly models overdispersed transmission.

(4) It would be good to allow for multiple seeding events per variant and per state. This can be informed by phylogeography in a minimum effort way and would improve the accuracy of Rt.

(5) By now, I don't think it will be a surprise that addressing sampling bias is standard, reweighting sequence data or comparing results with independent surveillance data to assess the impact of non-representative sequencing.

Reviewer #1 (Public review):

This is a well-designed and very interesting study examining the impact of imprecise feedback on outcomes on decision-making. I think this is an important addition to the literature and the results here, which provide a computational account of several decision-making biases, are insightful and interesting.

I do not believe I have substantive concerns related to the actual results presented; my concerns are more related to the framing of some of the work. My main concern is regarding the assertion that the results prove that non-normative and non-Bayesian learning is taking place. I agree with the authors that their results demonstrate that people will make decisions in ways that demonstrate deviations from what would be optimal for maximizing reward in their task under a strict application of Bayes rule. I also agree that they have built reinforcement learning models which do a good job of accounting for the observed behavior. However, the Bayesian models included are rather simple- per the author descriptions, applications of Bayes' rule with either fixed or learned credibility for the feedback agents. In contrast, several versions of the RL models are used, each modified to account for different possible biases. However more complex Bayes-based models exist, notably active inference but even the hierarchical gaussian filter. These formalisms are able to accommodate more complex behavior, such as affect and habits, which might make them more competitive with RL models. I think it is entirely fair to say that these results demonstrate deviations from an idealized and strict Bayesian context; however, the equivalence here of Bayesian and normative is I think misleading or at least requires better justification/explanation. This is because a great deal of work has been done to show that Bayes optimal models can generate behavior or other outcomes that are clearly not optimal to an observer within a given context (consider hallucinations for example) but which make sense in the context of how the model is constructed as well as the priors and desired states the model is given.

As such, I would recommend that the language be adjusted to carefully define what is meant by normative and Bayesian and to recognize that work that is clearly Bayesian could potentially still be competitive with RL models if implemented to model this task. An even better approach would be to directly use one of these more complex modelling approaches, such as active inference, as the comparator to the RL models, though I would understand if the authors would want this to be a subject for future work.

Abstract:

The abstract is lacking in some detail about the experiments done, but this may be a limitation of the required word count? If word count is not an issue, I would recommend adding details of the experiments done and the results. One comment is that there is an appeal to normative learning patterns, but this suggests that learning patterns have a fixed optimal nature, which may not be true in cases where the purpose of the learning (e.g. to confirm the feeling of safety of being in an in-group) may not be about learning accurately to maximize reward. This can be accommodated in a Bayesian framework by modelling priors and desired outcomes. As such the central premise that biased learning is inherently non-normative or non-Bayesian I think would require more justification. This is true in the introduction as well.

Introduction:

As noted above the conceptualization of Bayesian learning being equivalent to normative learning I think requires either further justification. Bayesian belief updating can be biased an non-optimal from an observer perspective, while being optimal within the agent doing the updating if the priors/desired outcomes are set up to advantage these "non-optimal" modes of decision making.

Results:

I wonder why the agent was presented before the choice - since the agent is only relevant to the feedback after the choice is made. I wonder if that might have induced any false association between the agent identity and the choice itself. This is by no means a critical point but would be interesting to get the authors' thoughts.

The finding that positive feedback increases learning is one that has been shown before and depends on valence, as the authors note. They expanded their reinforcement learning model to include valence; but they did not modify the Bayesian model in a similar manner. This lack of a valence or recency effect might also explain the failure of the Bayesian models in the preceding section where the contrast effect is discussed. It is not unreasonable to imagine that if humans do employ Bayesian reasoning that this reasoning system has had parameters tuned based on the real world, where recency of information does matter; affect has also been shown to be incorporable into Bayesian information processing (see the work by Hesp on affective charge and the large body of work by Ryan Smith). It may be that the Bayesian models chosen here require further complexity to capture the situation, just like some of the biases required updates to the RL models. This complexity, rather than being arbitrary, may be well justified by decision making in the real world.

The methods mention several symptom scales- it would be interesting to have the results of these and any interesting correlations noted. It is possible that some of individual variability here could be related to these symptoms, which could introduce precision parameter changes in a Bayesian context and things like reward sensitivity changes in an RL context.

Discussion:

(For discussion, not a specific comment on this paper): One wonders also about participant beliefs about the experiment or the intent of the experimenters. I have often had participants tell me they were trying to "figure out" a task or find patterns even when this was not part of the experiment. This is not specific to this paper, but it may be relevant in the future to try and model participant beliefs about the experiment especially in the context of disinformation, when they might be primed to try and "figure things out".

As a general comment, in the active inference literature, there has been discussion of state-dependent actions, or "habits", which are learned in order to help agents more rapidly make decisions, based on previous learning. It is also possible that what is being observed is that these habits are at play, and that they represent the cognitive biases. This is likely especially true given, as the authors note, the high cognitive load of the task. It is true that this would mean that full-force Bayesian inference is not being used in each trial, or in each experience an agent might have in the world, but this is likely adaptive on the longer timescale of things, considering resource requirements. I think in this case you could argue that we have a departure from "normative" learning, but that is not necessarily a departure from any possible Bayesian framework, since these biases could potentially be modified by the agent or eschewed in favor of more expensive full-on Bayesian learning when warranted. Indeed in their discussion on the strategy of amplifying credible news sources to drown out low-credibility sources, the authors hint to the possibility of longer term strategies that may produce optimal outcomes in some contexts, but which were not necessarily appropriate to this task. As such, the performance on this task- and the consideration of true departure from Bayesian processing- should be considered in this wider context. Another thing to consider is that Bayesian inference is occurring, but that priors present going in produce the biases, or these biases arise from another source, for example factoring in epistemic value over rewards when the actual reward is not large. This again would be covered under an active inference approach, depending on how the priors are tuned. Indeed, given the benefit of social cohesion in an evolutionary perspective, some of these "biases" may be the result of adaptation. For example, it might be better to amplify people's good qualities and minimize their bad qualities in order to make it easier to interact with them; this entails a cost (in this case, not adequately learning from feedback and potentially losing out sometimes), but may fulfill a greater imperative (improved cooperation on things that matter). Given the right priors/desired states, this could still be a Bayes-optimal inference at a social level and as such may be ingrained as a habit which requires effort to break at the individual level during a task such as this.

The authors note that this task does not relate to "emotional engagement" or "deep, identity-related, issues". While I agree that this is likely mostly true, it is also possible that just being told one is being lied to might elicit an emotional response that could bias responses, even if this is a weak response.

Comments on revisions:

In their updated version the authors have made some edits to address my concerns regarding the framing of the 'normative' bayesian model, clarifying that they utilized a simple bayesian model which is intended to adhere in an idealized manner to the intended task structure, though further simulations would have been ideal.

The authors, however, did not take my recommendation to explore the symptoms in the symptom scales they collected as being a potential source of variability. They note that these were for hypothesis generation and were exploratory, fair enough, but this study is not small and there should have been sufficient sample size for a very reasonable analysis looking at symptom scores.

However, overall the toned down claims and clarifications of intent are adequate responses to my previous review.

Reviewer #2 (Public review):

This important paper studies the problem of learning from feedback given by sources of varying credibility. The convincing combination of experiment and computational modeling helps to pin down properties of learning, while opening unresolved questions for future research.

Summary:

This paper studies the problem of learning from feedback given by sources of varying credibility. Two bandit-style experiments are conducted in which feedback is provided with uncertainty, but from known sources. Bayesian benchmarks are provided to assess normative facets of learning, and alternative credit assignment models are fit for comparison. Some aspects of normativity appear, in addition to possible deviations such as asymmetric updating from positive and negative outcomes.

Strengths:

The paper tackles an important topic, with a relatively clean cognitive perspective. The construction of the experiment enables the use of computational modeling. This helps to pinpoint quantitatively the properties of learning and formally evaluate their impact and importance. The analyses are generally sensible, and advanced parameter recovery analyses (including cross-fitting procedure) provide confidence in the model estimation and comparison. The authors have very thoroughly revised the paper in response to previous comments.

Weaknesses:

The authors acknowledge the potential for cognitive load and the interleaved task structure to play a meaningful role in the results, though leave this for future work. This is entirely reasonable, but remains a limitation in our ability to generalize the results. Broadly, some of the results obtain in cases where the extent of generalization is not always addressed and remains uncertain.

Reviewer #3 (Public review):

Summary

This paper investigates how disinformation affects reward learning processes in the context of a two-armed bandit task, where feedback is provided by agents with varying reliability (with lying probability explicitly instructed). They find that people learn more from credible sources, but also deviate systematically from optimal Bayesian learning: They learned from uninformative random feedback, learned more from positive feedback, and updated too quickly from fully credible feedback (especially following low-credibility feedback). Overall, this study highlights how misinformation could distort basic reward learning processes, without appeal to higher order social constructs like identity.

Strengths

• The experimental design is simple and well-controlled; in particular, it isolates basic learning processes by abstracting away from social context
• Modeling and statistics meet or exceed standards of rigor
• Limitations are acknowledged where appropriate, especially those regarding external validity
• The comparison model, Bayes with biased credibility estimates, is strong; deviations are much more compelling than e.g. a purely optimal model
• The conclusions are of substantial interest from both a theoretical and applied perspective

Weaknesses

The authors have addressed most of my concerns with the initial submission. However, in my view, evidence for the conclusion that less credible feedback yields a stronger positivity bias remains weak. This is due to two issues.

Absolute or relative positivity bias?

The conclusion of greater positivity bias for lower credible feedback (Fig 5) hinges on the specific way in which positivity bias is defined. Specifically, we only see the effect when normalizing the difference in sensitivity to positive vs. negative feedback by the sum. I appreciate that the authors present both and add the caveat whenever they mention the conclusion. However, without an argument that the relative definition is more appropriate, the fact of the matter is that the evidence is equivocal.

There is also a good reason to think that the absolute definition is more appropriate. As expected, participants learn more from credible feedback. Thus, normalizing by average learning (as in the relative definition) amounts to dividing the absolute difference by increasingly large numbers for more credible feedback. If there is a fixed absolute positivity bias (or something that looks like it), the relative bias will necessarily be lower for more credible feedback. In fact, the authors own results demonstrate this phenomenon (see below). A reduction in relative bias thus provides weak evidence for the claim.

It is interesting that the discovery study shows evidence of a drop in absolute bias. However, for me, this just raises questions. Why is there a difference? Was one a just a fluke? If so, which one?

Positivity bias or perseveration?

Positivity bias and perseveration will both predict a stronger relationship between positive (vs. negative) feedback and future choice. They can thus be confused for each other when inferred from choice data. This potentially calls into question all the results on positivity bias.

The authors clearly identify this concern in the text and go to considerable lengths to rule it out. However, the new results (in revision 1) show that a perseveration-only model can in fact account for the qualitative pattern in the human data (the CA parameters). This contradicts the current conclusion:

Critically, however, these analyses also confirmed that perseveration cannot account for our main finding of increased positivity bias, relative to the overall extent of CA, for low-credibility feedback.

Figure 24c shows that the credibility-CA model does in fact show stronger positivity bias for less credible feedback. The model distribution for credibility 1 is visibly lower than for credibilities 0.5 and 0.75.

The authors need to be clear that it is the magnitude of the effect that the perseveration-only model cannot account for. Furthermore, they should additionally clarify that this is true only for models fit to data; it is possible that the credibility-CA model could capture the full size of the effect with different parameters (which could fit best if the model was implemented slightly differently).

The authors could make the new analyses somewhat stronger by using parameters optimized to capture just the pattern in CA parameters (for example by MSE). This would show that the models are in principle incapable of capturing the effect. However, this would be a marginal improvement because the conclusion would still rest on a quantitative difference that depends on specific modeling assumptions.

New simulations clearly demonstrate the confound in relative bias

Figure 24 also speaks to the relative vs. absolute question. The model without positivity bias shows a slightly stronger absolute "positivity bias" for the most credible feedback, but a weaker relative bias. This is exactly in line with the logic laid out above. In standard bandit tasks, perseveration can be quite well-captured by a fixed absolute positivity bias, which is roughly what we see in the simulations (I'm not sure what to make of the slight increase; perhaps a useful lead for the authors). However, when we divide by average credit assignment, we now see a reduction. This clearly demonstrates that a reduction in relative bias can emerge without any true differences in positivity bias.

Given everything above, I think it is unlikely that the present data can provide even "solid" evidence for the claim that positivity bias is greater with less credible feedback. This confound could be quickly ruled out, however, by a study in which feedback is sometimes provided in the absence of a choice. This would empirically isolate positivity bias from choice-related effects, including perseveration.

Reviewer #1 (Public review):

Summary:

The authors use a gambling task with momentary mood ratings from Rutledge et al. and compare computational models of choice and mood to identify markers of decisional and affective impairments underlying risk-prone behavior in adolescents with suicidal thoughts and behaviors (STB). The results show that adolescents with STB show enhanced gambling behavior (choosing the gamble rather than the sure amount), and this is driven by a bias towards the largest possible win rather than insensitivity to possible losses. Moreover, this group shows a diminished effect of receiving a certain reward (in the non-gambling trials) on mood. The results were replicated in an undifferentiated online sample where participants were divided into groups with or without STB based on their self-report of suicidal ideation on one question in the Beck Depression Inventory self-report instrument. The authors suggest, therefore, that adolescents with decreased sensitivity to certain rewards may need to be monitored more closely for STB due to their increased propensity to take risky decisions aimed at (expected) gains (such as relief from an unbearable situation through suicide), regardless of the potential losses.

Strengths:

(1) The study uses a previously validated task design and replicates previously found results through well-explained model-free and model-based analyses.

(2) Sampling choice is optimal, with adolescents at high risk; an ideal cohort to target early preventative diagnoses and treatments for suicide.

(3) Replication of the results in an online cohort increases confidence in the findings.

(4) The models considered for comparison are thorough and well-motivated. The chosen models allow for teasing apart which decision and mood sensitivity parameters relate to risky decision-making across groups based on their hypotheses.

(5) Novel finding of mood (in)sensitivity to non-risky rewards and its relationship with risk behavior in STB.

Weaknesses:

(1) The sample size of 25 for the S- group was justified based on previous studies (lines 181-183); however, all three papers cited mention that their sample was low powered as a study limitation.

(2) Modeling in the mediation analysis focused on predicting risk behavior in this task from the model-derived bias for gains and suicidal symptom scores. However, the prediction of clinical interest is of suicidal behaviors from task parameters/behavior - as a psychiatrist or psychologist, I would want to use this task to potentially determine who is at higher risk of attempting suicide and therefore needs to be more closely watched rather than the other way around (predicting behavior in the task from their symptom profile). Unfortunately, the analyses presented do not show that this prediction can be made using the current task. I was left wondering: is there a correlation between beta_gain and STB? It is also important to test for the same relationships between task parameters and behavior in the healthy control group, or to clarify that the recommendations for potential clinical relevance of these findings apply exclusively to people with a diagnosis of depression or anxiety disorder. Indeed, in line 672, the authors claim their results provide "computational markers for general suicidal tendency among adolescents", but this was not shown here, as there were no models predicting STB within patient groups or across patients and healthy controls.

(3) The FDR correction for multiple comparisons mentioned briefly in lines 536-538 was not clear. Which analyses were included in the FDR correction? In particular, did the correlations between gambling rate and BSI-C/BSI-W survive such correction? Were there other correlations tested here (e.g., with the TAI score or ERQ-R and ERQ-S) that should be corrected for? Did the mediation model survive FDR correction? Was there a correction for other mediation models (e.g., with BSI-W as a predictor), or was this specific model hypothesized and pre-registered, and therefore no other models were considered? Did the differences in beta_gain across groups survive FDR when including comparisons of all other parameters across groups? Because the results were replicated in the online dataset, it is ok if they did not survive FDR in the patient dataset, but it is important to be clear about this in presenting the findings in the patient dataset.

(4) There is a lack of explicit mention when replication analyses differ from the analyses in the patient sample. For instance, the mediation model is different in the two samples: in the patient sample, it is only tested in S+ and S- groups, but not in healthy controls, and the model relates a dimensional measure of suicidal symptoms to gambling in the task, whereas in the online sample, the model includes all participants (including those who are presumably equivalent to healthy controls) and the predictor is a binary measure of S+ versus S- rather than the response to item 9 in the BDI. Indeed, some results did not replicate at all and this needs to be emphasized more as the lack of replication can be interpreted not only as "the link between mood sensitivity to CR and gambling behavior may be specifically observable in suicidal patients" (lines 582-585) - it may also be that this link is not truly there, and without a replication it needs to be interpreted with caution.

(5) In interpreting their results, the authors use terms such as "motivation" (line 594) or "risk attitude" (line 606) that are not clear. In particular, how was risk attitude operationalized in this task? Is a bias for risky rewards not indicative of risk attitude? I ask because the claim is that "we did not observe a difference in risk attitude per se between STB and controls". However, it seems that participants with STB chose the risky option more often, so why is there no difference in risk attitude between the groups?

Reviewer #2 (Public review):

Summary:

This article addresses a very pertinent question: what are the computational mechanisms underlying risky behaviour in patients who have attempted suicide? In particular, it is impressive how the authors find a broad behavioural effect whose mechanisms they can then explain and refine through computational modeling. This work is important because, currently, beyond previous suicide attempts, there has been a lack of predictive measures. This study is the first step towards that: understanding the cognition on a group level. This is before being able to include it in future predictive studies (based on the cross-sectional data, this study by itself cannot assess the predictive validity of the measure).

Strengths:

(1) Large sample size.

(2) Replication of their own findings.

(3) Well-controlled task with measures of behaviour and mood + precise and well-validated computational modeling.

Weaknesses:

I can't really see any major weakness, but I have a few questions:

(1) I can see from the parameter recovery that the parameters are very well identified. Is it surprising that this is the case, given how many parameters there are for 90 trials? Could the authors show cross-correlations? I.e., make a correlation matrix with all real parameters and all fitted parameters to show that not only the diagonal (i.e., same data is the scatter plots in S3) are high, but that the off-diagonals are low.

(2) Could the authors clarify the result in Figure 2B of a correlation between gambling rate and suicidal ideation score, is that a different result than they had before with the group main effect? I.e., is your analysis like this: gambling rate ~ suicide ideation + group assignment? (or a partial correlation)? I'm asking because BSI-C is also different between the groups. [same comment for later analyses, e.g. on approach parameter].

(3) The authors correlate the impact of certain rewards on mood with the % gambling variable. Could there not be a more direct analysis by including mood directly in the choice model?

(4) In the large online sample, you split all participants into S+ and S-. I would have imagined that instead, you would do analyses that control for other clinical traits. Or, for example, you have in the S- group only participants who also have high depression scores, but low suicide items.

Reviewer #3 (Public review):

This manuscript investigates computational mechanisms underlying increased risk-taking behavior in adolescent patients with suicidal thoughts and behaviors. Using a well-established gambling task that incorporates momentary mood ratings and previously established computational modeling approaches, the authors identify particular aspects of choice behavior (which they term approach bias) and mood responsivity (to certain rewards) that differ as a function of suicidality. The authors replicate their findings on both clinical and large-scale non-clinical samples.

The main problem, however, is that the results do not seem to support a specific conclusion with regard to suicidality. The S+ and S- groups differ substantially in the severity of symptoms, as can be seen by all symptom questionnaires and the baseline and mean mood, where S- is closer to HC than it is to S+. The main analyses control for illness duration and medication but not for symptom severity. The supplementary analysis in Figure S11 is insufficient as it mistakes the absence of evidence (i.e., p > 0.05) for evidence of absence. Therefore, the results do not adequately deconfound suicidality from general symptom severity.

The second main issue is that the relationship between an increased approach bias and decreased mood response to CR is conceptually unclear. In this respect, it would be natural to test whether mood responses influence subsequent gambling choices. This could be done either within the model by having mood moderate the approach bias or outside the model using model-agnostic analyses.

Additionally, there is a conceptual inconsistency between the choice and mood findings that partly results from the analytic strategy. The approach bias is implemented in choice as a categorical value-independent effect, whereas the mood responses always scale linearly with the magnitude of outcomes. One way to make the models more conceptually related would be to include a categorical value-independent mood response to choosing to gamble/not to gamble.

The manuscript requires editing to improve clarity and precision. The use of terms such as "mood" and "approach motivation" is often inaccurate or not sufficiently specific. There are also many grammatical errors throughout the text.

Claims of clinical relevance should be toned down, given that the findings are based on noisy parameter estimates whose clinical utility for the treatment of an individual patient is doubtful at best.

Reviewer #1 (Public review):

Summary:

In the present study, Chen et al. investigate the role of Endophilin A1 in regulating GABAergic synapse formation and function. To this end, the authors use constitutive or conditional knockout of Endophilin A1 (EEN1) to assess the consequences on GABAergic synapse composition and function, as well as the outcome for PTZ-induced seizure susceptibility. The authors show that EEN1 KO mice show a higher susceptibility to PTZ-induced seizures, accompanied by a reduction in the GABAergic synaptic scaffolding protein gephyrin as well as specific GABAAR subunits and eIPSCs. The authors then investigate the underlying mechanisms, demonstrating that Endophilin A1 binds directly to gephyrin and GABAAR subunits, and identifying the subdomains of Endophilin A1 that contribute to this effect. Overall, the authors state that their study places Endophilin A1 as a new regulator of GABAergic synapse function.

Strengths:

Overall, the topic of this manuscript is very timely, since there has been substantial recent interest in describing the mechanisms governing inhibitory synaptic transmission at GABAergic synapses. The study will therefore be of interest to a wide audience of neuroscientists studying synaptic transmission and its role in disease. The manuscript is well written and contains a substantial quantity of data. In the revised version of the manuscript, the authors have increased the number of samples analyzed and have significantly improved the statistical analysis, thereby substantially strengthening the conclusions of their study.

Reviewer #2 (Public review):

Summary:

The function of neural circuits relies heavily on the balance of excitatory and inhibitory inputs. Particularly, inhibitory inputs are understudied when compared to their excitatory counterparts due to the diversity of inhibitory neurons, their synaptic molecular heterogeneity, and their elusive signature. Thus, insights into these aspects of inhibitory inputs can inform us largely on the functions of neural circuits and the brain.

Endophilin A1, an endocytic protein heavily expressed in neurons, has been implicated in numerous pre- and postsynaptic functions, however largely at excitatory synapses. Thus, whether this crucial protein plays any role in inhibitory synapse, and whether this regulates functions at the synaptic, circuit, or brain level remains to be determined.

The three remaining concerns are:

(1) The use of one-way ANOVA is not well justified.

(2) The use of superplots to show culture to culture variability would make it more transparent.

(3) Change EEN1 in Figure 8B to EndoA1.

Comments on revised version:

The authors addressed the concerns adequately.

Reviewer #3 (Public review):

Chen et al. identify endophilin A1 as a novel component of the inhibitory postsynaptic scaffold. Their data show impaired evoked inhibitory synaptic transmission in CA1 neurons of mice lacking endophilin A1, and an increased susceptibility to seizures. Endophilin can interact with the postsynaptic scaffold protein gephyrin and promotes assembly of the inhibitory postsynaptic element. Endophilin A1 is known to play a role in presynaptic terminals and in dendritic spines, but a role for endophilin A1 at inhibitory postsynaptic densities has not yet been described, providing a valuable addition to the field.

To investigate the role of endophilin A1 at inhibitory postsynapses, the authors used a broad array of experimental approaches, including tests of seizure susceptibility, electrophysiology, biochemistry, neuronal culture and image analysis. The authors have addressed the remaining concerns in their revision. Taken together, their results expand the synaptic role of endophilin-A1 to include the inhibitory post synaptic element.

Reviewer #1 (Public review):

Summary:

This manuscript uses a diverse isolate collection of Streptococcus pneumoniae from hospital patients in the Netherlands to understand the population-level genetic basis of growth rate variation in this pathogen, which is a key determinant of S. pneumoniae within-host fitness. Previous efforts have studied this phenomenon in strain-specific comparisons, which can lack the statistical power and scope of population-level studies. The authors collected a rigorous set of in vitro growth data for each S. pneumoniae isolate and subsequently paired growth curve analysis with whole-genome analyses to identify how phylogenetics, serotype and specific genetic loci influence in vitro growth. While there were noticeable correlations between capsular serotype and phylogeny with growth metrics, they did not identify specific loci associated with altered in vitro growth, suggesting that these phenotypes are controlled by the collective effect of the entire genetic background of a strain. This is an important finding that lays the foundation for additional, more highly-powered studies that capture more S. pneumoniae genetic diversity to identify these genetic contributions.

Strengths:

The authors were able to completely control the experimental and genetic analyses to ensure all isolates underwent the same analysis pipeline to enhance the rigor of their findings.

The isolate collection captures an appreciable amount of S. pneumoniae diversity and, importantly, enables disentangling the contributions of the capsule and phylogenetic background to growth rates.

This study provides a population-level, rather than strain-specific, view of how genetic background influences growth rate in S. pneumoniae. This is an advance over previous studies that have only looked at smaller sets of strains.

The methods used are well-detailed and robust to allow replication and extension of these analyses. Moreover, the manuscript is very well written and includes a thoughtful and thorough discussion of the strengths and limitations of the current study.

Weaknesses:

As acknowledged by the authors, the genetic diversity and sample size of this newly collected isolate set is still limited relative to the known global diversity of S. pneumoniae, which evidently limits the power to detect loci with smaller/combinatorial contributions to growth rate (and ultimately infection).

The in vitro growth data is limited to a single type of rich growth medium, which may not fully reflect the nutritional and/or selective pressures present in the host.

The current study does not use genetic manipulation or in vitro/in vivo infection models to experimentally test whether alteration of growth rates as observed in this study is linked to virulence or successful infection. The availability of a naturally diverse collection with phylogenetic and serotype combinations already identified as interesting by the authors provides a strong rationale for wet-lab studies of these phenotypes.

Update on first revision:

The authors have responded to all of my initial comments as well as those of the other reviewers, and I have no further concerns to be addressed.

Reviewer #2 (Public review):

The study by Chaguza et al. presents a novel perspective on pneumococcal growth kinetics, suggesting that the overall genetic background of Streptococcus pneumoniae, rather than specific loci, plays a more dominant role in determining growth dynamics. Through a genome-wide association study (GWAS) approach, the authors propose a shift in how we understand growth regulation, differing from earlier findings that pinpointed individual genes, such as wchA or cpsE, as key regulators of growth kinetics. This study highlights the importance of considering the cumulative impact of the entire genetic background rather than focusing solely on individual genetic loci.

The study emphasizes the cumulative effects of genetic variants, each contributing small individual impacts, as the key drivers of pneumococcal growth. This polygenic model moves away from the traditional focus on single-gene influences. Through rigorous statistical analyses, the authors persuasively advocate for a more holistic approach to understanding bacterial growth regulation, highlighting the complex interplay of genetic factors across the entire genome. Their findings open new avenues for investigating the intricate mechanisms underlying bacterial growth and adaptation, providing fresh insights into bacterial pathogenesis.

Strengths:

This study exemplifies a holistic approach to unraveling key factors in bacterial pathogenesis. By analyzing a large dataset of whole-genome sequences and employing robust statistical methodologies, the authors provide strong evidence to support their main findings. Which is a leap forward from previous studies focused on a relatively smaller number of strains. Their integration of genome-wide association studies (GWAS) highlights the cumulative, polygenic influences on pneumococcal growth kinetics, challenging the traditional focus on individual loci. This comprehensive strategy not only advances our understanding of bacterial growth regulation but also establishes a foundation for future research into the genetic underpinnings of bacterial pathogenesis and adaptation. The amount of data generated and corresponding approaches to analyze the data are impressive as well as convincing. The figures are convincing and comprehensible too. The revised version of the manuscript, after the addition and including explanations, is more convincing and acceptable.

Weaknesses:

This study suggests evidence that the genetic background significantly influences bacterial growth kinetics. However, the absence of experimental validation remains a critical limitation. Although the authors acknowledge in their response to reviewers that bench-experiments were beyond the scope of this work and are planned, this gap of experimental validation weakens the current conclusions. Demonstrable validation will be essential to corroborate the associations identified through the GWAS approach. Future experimental efforts will be critical to substantiate these findings and to deepen our understanding of the genetic determinants governing bacterial growth dynamics.

Reviewer #3 (Public review):

This study provides insights into the growth kinetics of a diverse collection of Streptococcus pneumoniae, identifying capsule and lineage differences. It was not able to identify any specific loci from the GWAS that were associated with the growth features. It does provide a useful study linking phenotypic data with large scale genomic population data.

In the revised version, the authors have addressed the points raised by the reviewers. The authors have provided additional detail in the Introduction and Methods that both improves the general accessibility for the broad readership of eLife, and the ability of other researchers to reproduce the approaches used in this study. They have expanded the Results and Discussion text in some sections to provide greater clarity and accuracy in reporting their data.

The inclusion of a Data Availability statement was a useful addition and will help ensure the manuscript adheres to eLife's publishing policies.

Reviewer #1 (Public review):

Summary:

This work by Govorunova et al. identified three naturally blue-shifted channelrhodopsins (ChRs) from ancyromonads, namely AnsACR, FtACR, and NlCCR. The phylogenetic analysis places the ancyromonad ChRs in a distinct branch, highlighting their unique evolutionary origin and potential for novel applications in optogenetics. Further characterization revealed the spectral sensitivity, ionic selectivity, and kinetics of the newly discovered AnsACR, FtACR, and NlCCR. This study also offers valuable insights into the molecular mechanism underlying the function of these ChRs, including the roles of specific residues in the retinal-binding pocket. Finally, this study validated the functionality of these ChRs in both mouse brain slices (for AnsACR and FtACR) and in vivo in Caenorhabditis elegans (for AnsACR), demonstrating the versatility of these tools across different experimental systems.<br /> In summary, this work provides a potentially valuable addition to the optogenetic toolkit by identifying and characterizing novel blue-shifted ChRs with unique properties.

Strengths:

This study provides a thorough characterization of the biophysical properties of the ChRs' properties and demonstrated the versatility of these tools in different ex vivo and in vivo experimental systems. The authors also explored the potential of AnsACR for multiplexed optogenetics. Finally, the mutagenesis experiments revealed the roles of key residues in the photoactive site that can affect the spectral and kinetic properties of the channelrhodopsins.

Weaknesses:

The revised manuscript has addressed most of the previous major weaknesses.

Reviewer #2 (Public review):

Summary:

Govorunova et al present three new anion opsins that have potential applications silencing neurons. They identify new opsins by scanning numerous databases for sequence homology to known opsins, focusing on anion opsins. The three opsin identified, are uncommonly fast, potent, and are able to silence neuronal activity. The authors characterize numerous parameters of the opsins and compare these opsins to the existing and widely used GtACR opsins.

Strengths:

This paper follows the tradition of the Spudich lab, presenting and rigorously characterizing potentially valuable opsins. Furthermore, they explore several mutations of the identified opsin that may make these opsins even more useful for the broader community. The opsins AnsACR and FtACR are particularly notable having extraordinarily fast onset kinetics that could have utility in many domains. Furthermore, the authors show AnsACR is useable in multiphoton experiments having a peak photocurrent in a commonly used wavelength. Overall, the author's detailed measurements and characterization make for an important resource - both presenting new opsins that may be important for future experiment, and providing characterizations to expand our understanding of opsin biophysics in general.

Reviewer #3 (Public review):

Summary:

The authors aimed to develop Channelrhodopsins (ChRs), light-gated ion channels, with high potency and blue action spectra for use in multicolor (multiplex) optogenetics applications. To achieve this, they performed a bioinformatics analysis to identify ChR homologues in several protist species, focusing on ChRs from ancyromonads, which exhibited the highest photocurrents and the most blue-shifted action spectra among the tested candidates. Within the ancyromonad clade, the authors identified two new anion-conducting ChRs and one cation-conducting ChR. These were characterized in detail using a combination of manual and automated patch-clamp electrophysiology, absorption spectroscopy, and flash photolysis. The authors also explored sequence features that may explain the blue-shifted action spectra and differences in ion selectivity among closely related ChRs.

Strengths:

A key strength of this study is the high-quality experimental data, which were obtained using well-established techniques such as manual patch-clamp and absorption spectroscopy, complemented by modern automated patch-clamp approaches. These data convincingly support most of the claims. The newly characterized ChRs expand the optogenetics toolkit and will be of significant interest to researchers working with microbial rhodopsins, those developing new optogenetic tools, as well as neuro- and cardioscientists employing optogenetic methods.

Weaknesses:

This study does not exhibit major methodological weaknesses.

Reviewer #1 (Public review):

The authors report on a thorough investigation of the interaction of megakaryocytes (MK) with their associated ECM during maturation. They report convincing evidence to support the existence of a dense cage-like pericellular structure containing laminin γ1 and α4 and collagen IV, which interacts with integrins β1 and β3 on MK and serve to fix the perisinusoidal localization of MK and prevent their premature intravasation. As with everything in nature, the authors support a Goldilocks range of MK-ECM interactions - inability to digest the ECM via inhibition of MMPs leads to insufficient MK maturation and development of smaller MK. This important work sheds light into the role of cell-matrix interactions in MK maturation, and suggests that higher-dimensional analyses are necessary to capture the full scope of cellular biology in the context of their microenvironment. The authors have responded appropriately to the majority of my previous comments.

Reviewer #2 (Public review):

Summary:

This study makes a significant contribution to understanding the microenvironment of megakaryocytes (MKs) in the bone marrow, identifying an extracellular matrix (ECM) cage structure that influences MK localization and maturation. The authors provide compelling evidence for the presence of this ECM cage and its role in MK homeostasis, employing an array of sophisticated imaging techniques and molecular analyses.

The authors have addressed most of the concerns raised in the previous review, providing clarifications and additional data that strengthen their conclusions

More broadly, this work adds to a growing recognition of the ECM as an active participant in haematopoietic cell regulation in the bone marrow microenvironment. This work could pave the way to future studies investigating how the megakaryocytes' ECM cage affects their function as part of the haematopoietic stem cell niche, and by extension, influences global haematopoiesis.

Reviewer #1 (Public review):

Summary:

This study shows a novel role for SCoR2 in regulating metabolic pathways in the heart to prevent injury following ischemia/reperfusion. It combines a new multi-omics method to determine SCoR2 mediated metabolic pathways in the heart. This paper would be of interest to cardiovascular researchers working on cardioprotective strategies following ischemic injury in the heart.

Strengths:

(1) Use of SCoR2KO mice subjected to I/R injury.

(2) Identification of multiple metabolic pathways in the heart by a novel multi-omics approach.

Comments on revisions:

Authors have addressed all concerns raised in the previous round of review. Substantial modifications have been made in response to those concerns. There are no further comments.

Reviewer #2 (Public review):

Summary:

This manuscript addresses the gap in knowledge related to the cardiac function of the S-denitrosylase SNO-CoA Reductase 2 (SCoR2; product of the Akr1a1 gene). Genetic variants in SCoR2 have been linked to cardiovascular disease, yet its exact role in heart remains unclear. This paper demonstrates that mice deficient in SCoR2 show significant protection in a myocardial infarction (MI) model. SCoR2 influenced ketolytic energy production, antioxidant levels, and polyol balance through the S-nitrosylation of crucial metabolic regulators.

Strengths:

Addresses a well-defined gap in knowledge related to the cardiac function of SNO-CoA Reductase 2. Besides the in-depth case for this specific player, the manuscripts sheds more light on the links between S-nytrosylation and metabolic reprogramming in heart.

Rigorous proof of requirement through the combination of gene knockout and in vivo myocardial ischemia/reperfusion

Identification of precise Cys residue for SNO-modification of BDH1 as SCoR2 target in cardiac ketolysis

Weaknesses:

The experiments with BDH1 stability were performed in mutant 293 cells. Was there a difference in BDH1 stability in myocardial tissue or primary cardiomyocytes from SCoR2-null vs -WT mice? Same question extends to PKM2.

In the absence of tracing experiments, the cross-sectional changes in ketolysis, glycolysis or polyol intermediates presented in Figures 4 and 5 are suggestive at best. This needs to be stressed while describing and interpreting these results.

The findings from human samples with ischemic and non-ischemic cardiomyopathy do not seem immediately or linearly in line with each other and with the model proposed from the KO mice. While the correlation holds up in the non-ischemic cardiomyopathy (increased SNO-BDH1, SNO-PKM2 with decreased SCoR2 expression), how do the Authors explain the decreased SNO-BDH1 with preserved SCoR2 expression in ischemic cardiomyopathy? This seems counterintuitive as activation of ketolysis is a quite established myocardial response to the ischemic stress. It may help the overall message clarity to focus the human data part on only NICM patients.

(partially linked to the point above) an important proof that is lacking at present is the proof of sufficiency for SCoR2 in S-Nytrosylation of targets and cardiac remodeling. Does SCoR2 overexpression in heart or isolated cardiomyocytes reduce S-nitrosylation of BDH1 and other targets, undermining heart function at baseline or under stress?

Comments on revisions:

Some of my points have been addressed. However, the points related to 1) BDH1 stability effect in cardiomyocytes; 2) human relevance of SNO-BDH1; 3) SCoR2 sufficiency remain unclear. That said, this manuscript will provide useful information to the field as such.

Reviewer #3 (Public review):

Summary:

This manuscript demonstrates that mice lacking the denitrosylase enzyme SCoR2/AKR1A1 demonstrate a robust cardioprotection resulting from reprogramming of multiple metabolic pathways, revealing<br /> widespread, coordinated metabolic regulation by SCoR2.

Strengths:

The extensive experimental evidence provided the use of the knockout model

Weaknesses:

No direct evidence for the underlying mechanism.

The mouse model used is not a tissue-specific knock-out.

Reviewer #1 (Public review):

Summary:

There is growing appreciation for the important of luminal (apical) ECM in tube development, but such matrices are much less well understood than basal ECMs. Here the authors provide insights into the aECM that shapes the Drosophila salivary gland (SG) tube and the importance of PAPSS-dependent sulfation in its organization and function.

The first part of the paper focuses on careful phenotypic characterization of papss mutants, using multiple markers and TEM. This revealed reduced markers of sulfation and defects in both apical and basal ECM organization, Golgi (but not ER) morphology, number and localization of other endosomal compartments, plus increased cell death. The authors focus on the fact that papss mutants have an irregular SG lumen diameter, with both narrowed regions and bulged regions. They address the pleiotropy, showing that preventing the cell death and resultant gaps in the tube did not rescue the SG luminal shape defects and discussing similarities and differences between the papss mutant phenotype and those caused by more general trafficking defects. The analysis uses a papss nonsense mutant from an EMS screen - I appreciate the rigorous approach the authors took to analyze transheterozygotes (as well as homozygotes) plus rescued animals in order to rule out effects of linked mutations. Importantly, the rescue experiments also demonstrated that sulfation enzymatic activity is important.

The 2nd part of the paper focuses on the SG aECM, showing that Dpy and Pio ZP protein fusions localize abnormally in papss mutants and that these ZP mutants (and Np protease mutants) have similar SG lumen shaping defects to the papss mutants. A key conclusion is that SG lumen defects correlate with loss of a Pio+Dpy-dependent filamentous structure in the lumen. These data suggest that ZP protein misregulation could explain this part of the papss phenotype.

Overall, the text is very well written and clear. Figures are clearly labeled. The methods involve rigorous genetic approaches, microscopy, and quantifications/statistics and are documented appropriately. The findings are convincing.

Significance:

This study will be of interest to researchers studying developmental morphogenesis in general and specifically tube biology or the aECM. It should be particularly of interest to those studying sulfation or ZP proteins (which are broadly present in aECMs across organisms, including humans).

This study adds to the literature demonstrating the importance of luminal matrix in shaping tubular organs and greatly advances understanding of the luminal matrix in the Drosophila salivary gland, an important model of tubular organ development and one that has key matrix differences (such as no chitin) compared to other highly studied Drosophila tubes like the trachea.

The detailed description of the defects resulting from papss loss suggests that there are multiple different sulfated targets, with a subset specifically relevant to aECM biology. A limitation is that specific sulfated substrates are not identified here (e.g. are these the ZP proteins themselves or other matrix glycoproteins or lipids?); therefore, it's not clear how direct or indirect the effects of papss are on ZP proteins. However, this is clearly a direction for future work and does not detract from the excellent beginning made here.

Reviewer #2 (Public review):

Summary

This study provides new insights into organ morphogenesis using the Drosophila salivary gland (SG) as a model. The authors identify a requirement for sulfation in regulating lumen expansion, which correlates with several effects at the cellular level, including regulation of intracellular trafficking and the organization of Golgi, the aECM and the apical membrane. In addition, the authors show that the ZP proteins Dumpy (Dpy) and Pio form an aECM regulating lumen expansion. Previous reports already pointed to a role for Papss in sulfation in SG and the presence of Dpy and Pio in the SG. Now this work extends these previous analyses and provides more detailed descriptions that may be relevant to the fields of morphogenesis and cell biology (with particular focus on ECM research and tubulogenesis). This study nicely presents valuable information regarding the requirements of sulfation and the aECM in SG development.

Strengths:

- The results supporting a role for sulfation in SG development are strong. In addition, the results supporting the involvement of Dpy and Pio in the aECM of the SG, their role in lumen expansion, and their interactions, are also strong.

- The authors have made an excellent job in revising and clarifying the many different issues raised by the reviewers, particularly with the addition of new experiments and quantifications. I consider that the manuscript has improved considerably.

- The authors generated a catalytically inactive Papss enzyme, which is not able to rescue the defects in Papss mutants, in contrast to wild type Papss. This result clearly indicates that the sulfation activity of Papss is required for SG development.

Reviewer #1 (Public review):

Summary:

The authors of this study propose a model in which NPY family regulators antagonize the activity of the pid mutation in the context of floral development and other auxin-related phenotypes. This is hypothesized to occur through regulation of or by PID and its action on the PIN1 auxin transporter.

Strengths:

The findings are intriguing.

Weaknesses and Major Comments:

(1) While the findings are indeed intriguing, the mechanism of action and interaction among these components remains poorly understood. The study would benefit from significantly more thorough and focused experimental analyses to truly advance our understanding of pid phenotypes and the interplay among PID, NPYs, and PIN1.

(2) The manuscript appears hastily assembled, with key methodological and conceptual details either missing or inconsistent. Although issues with figure formatting and clarity (e.g., lack of scale bars and inconsistent panel layout) may alone warrant revision, the content remains the central concern and must take precedence over presentation.

(3) Given that fertile progeny are obtained from pid-TD pin1/PIN1 and pid NPY OE lines, it would be important to analyze whether mutations and associated phenotypes are heritable. This is especially relevant since CRISPR lines can be mosaic. Comprehensive genotyping and inheritance studies are required.

(4) The Materials and Methods section lacks essential information on how the lines were generated, genotyped, propagated, and scored. There is also generally no mention of how reproducible the observations were. These genetic experiments need to be described in detail, including the number of lines analyzed and consistency across replicates.

(5) The nature of the pid alleles used in the study is not described. This is essential for interpretation.

(6) The authors measure PIN1 phosphorylation in response to NPY overexpression and conclude that the newly identified phosphorylation sites are inhibitory because they do not overlap with known activating sites. This conclusion is speculative without functional validation. Functional assays are available and must be included to substantiate this claim.

(7) Figure 5 implies that NPY1 acts downstream of PID, but there is no biochemical evidence supporting this hierarchy. Additional experiments are needed to demonstrate the epistatic or regulatory relationship.

(8) The authors should align their genetic observations with cell biological data on PIN1, PIN2, and PID localization and distribution.

Reviewer #2 (Public review):

Summary:

The study is well-conducted, revealing that NPY1, with previously less-characterized molecular functions, can suppress pid mutant phenotypes with a phosphorylation-based mechanism. Overexpression of NPY1 (NPY1-OE) results in PIN phosphorylation at unique sites and bypasses the requirement for PID for this event. Conversely, a C-terminal deleted form of NPY1 (NPY1-dC) fails to rescue pid despite promoting a certain phospho-profile in PIN proteins.

Strengths:

(1) The careful genetic analyses of pid suppression by NPY1-OE and the inability of NPY1dC to do the same.

(2) Phospho-proteomics approaches reveal that NPY1-OE induces phosphorylation of PINs at non-canonical sites, independent of PID.

Weaknesses:

(1) The native role of NPY1 is not tested by phospho-proteomics in loss-of-function npy1 mutants. Such analysis would be crucial to demonstrate that NPY1 is required for the observed phosphorylation events.

(2) The functional consequences of the newly identified phosphorylation sites in PINs remain speculative. Site-directed mutagenesis (phospho-defective and phospho-mimetic) would help clarify their physiological roles.

(3) The kinase responsible for NPY1-mediated phosphorylation remains unidentified. Since NPY1 is a non-kinase protein, a model involving recruitment of partner kinases (e.g., PIN-phosphorylating kinases other than PID) should be considered or discussed.

Reviewer #3 (Public review):

Summary:

This manuscript from Mudgett et al. explores the relative roles of PID and NPY1 in auxin-dependent floral initiation in Arabidopsis. Micro vectorial auxin flows directed by PIN1 are essential to flower initiation, and loss of PIN1 or two of its regulators, PID and NPY1 (in a yucca-deficient background) phenocopies the pinformed phenotype. This group has previously shown that PID-PIN1 interactions and function are dosage-dependent. The authors pick up this thread by demonstrating that a heterozygote containing a CRISPR deletion of one copy of PIN1 can restore quasi-wild type floral initiation to pid.

The authors then show that overexpression of NPY1 is sufficient to more or less restore wild-type floral initiation to the pid mutant. The authors claim that this result demonstrates that NPY1 functions downstream of PID, as this ectopic abundance of NPY1 resulted in phosphorylation of PIN1 at sites that differ from sites of action of PID. The authors pursue evidence that PID action via NPY1 is analogous to the mode of action by which phot1/2 act on NPH3 in seedling phototropism. Such a model is supported by the evidence presented herein that the C terminus of NPY1, which has abundant Ser/Thr content, is phosphorylated, and that the deletion of this domain prevents overexpression compensation of the pinformed phenotype.<br /> While the results presented support evidence in the literature that PID acts on NPY1 to regulate PIN1 function, it is also possible that NPY1 overexpression results in limited expansion of phosphorylation targets observed with other AGC kinases. And if the phot model is any indication, there may be other PID targets that modulate PIN1-dependent floral initiation.

However, overexpression of the NPY1 C-terminal deletion construct resulted in phosphorylation of both PIN1 and PIN2 and agravitropic root growth similar to what is observed in pin2 mutants. This suggests that direct PID phosphorylation of PINs and action via NPY1 can be distinguished by phosphorylation sites and by growth phenotypes.

Strengths:

A very important effort that places NPY1 downstream of PID in floral initiation.

Weaknesses:

As PID has been shown to act on sites that regulate PIN protein polarity as well as PIN protein function, it would be useful if the authors consider how their results would fit/not fit with a model where combinatorial function of NPY1 and PID regulate PIN1 in a manner similar to the way that PID appears to function combinatorially with D6PK on PIN3.

Reviewer #1 (Public review):

The authors use inducible Fz::mKate2-sfGFP to explore "cell-scale signaling" in PCP. They reach several conclusions. First, they conclude that cell-scale signaling does not depend on limiting pools of core components (other than Fz). Second, they conclude that cell-scale signaling does not depend on microtubule orientation, and third, they conclude that cell-scale signaling is strong relative to cell to cell coupling of polarity.

There are some interesting inferences that can be drawn from the manuscript, but there are also some significant challenges in interpreting the results and conclusions from the work as presented. I suggest that the authors 1) define "cell-scale signaling," as the precise meaning must be inferred, 2) reconsider some premises upon which some conclusions depend, 3) perform an essential assay validation, and 4) explain some other puzzling inconsistencies.

Major concerns:

The exact meaning of cell-scale signaling is not defined, but I infer that the authors use this term to describe how what happens on one side of a cell affects another side. The remainder of my critique depends on this understanding of the intended meaning.

The authors state that any tissue wide directional information comes from pre-existing polarity and its modification by cell flow, such that the de novo signaling paradigm "bypasses" these events and should therefore not be responsive to any further global cues. It is my understanding that this is not a universally accepted model, and indeed, the authors' data seem to suggest otherwise. For example, the image in Fig 5B shows that de novo induction restores polarity orientation to a predominantly proximal to distal orientation. If no global cue is active, how is this orientation explained? The 6 hr condition, that has only partial polarity magnitude, is quite disordered. Do the patterns at 8 and 10 hrs become more proximally-distally oriented? It is stated that they all show swirls, but please provide adult wing images, and the corresponding orientation outputs from QuantifyPolarity to help validate the notion that the global cues are indeed bypassed by this paradigm.

It is implicit that, in the de novo paradigm, polarization is initiated immediately or shortly after heat shock induction. However, the results should be differently interpreted if the level of available Fz protein does not rise rapidly and then stabilize before the 6 hr time point, and instead continues to rise throughout the experiment. Western blots of the Fz::mKate2-sfGFP at time points after induction should be performed to demonstrate steady state prior to measurements. Otherwise, polarity magnitude could simply reflect the total available pool of Fz at different times after induction. Interpreting stability is complex, and could depend on the same issue, as well as the amount of recycling that may occur. Prior work from this lab using FRAP suggested that turnover occurs, and could result from recycling as well as replenishment from newly synthesized protein.

From the Fig 3 results, the authors claim that limiting pools of core proteins do not explain cell-scale signaling, a result expected based on the lack of phenotypes in heterozygotes, but of course they do not test the possibility that Fz is limiting. They do note that some other contributing protein could be.

In Fig 3, it is unclear why the authors chose to test dsh1/+ rather than dsh[null]/+. In any case, the statistically significant effect of Dsh dose reduction is puzzling, and might indicate that the other interpretation is correct. Ideally, a range including larger and smaller reductions would be tested. As is, I don't think limiting Dsh is ruled out.

The data in Fig 5 are somewhat internally inconsistent, and inconsistent with the authors' interpretation. In both repolarization conditions, the authors claim that repolarization extends only to row 1, and row 1 is statistically different from non-repolarized row 1, but so too is row 3. Row 2 is not. This makes no sense, and suggests either that the statistical tests are inappropriate and/or the data is too sparse to be meaningful. For the related boundary intensity data in Fig 6, the authors need to describe exactly how boundaries were chosen or excluded from the analysis. Ideally, all boundaries would be classified as either meido-lateral (meaning anterior-posterior) or proximal-distal depending on angle.

If the authors believe their Fig 5 and 6 analyses, how do they explain that hairs are reoriented well beyond where the core proteins are not? This would be a dramatic finding, because as far as I know, when core proteins are polarized, prehair orientation always follows the core protein distribution. Surprisingly, the authors do not so much as comment about this. The authors should age their wings just a bit more to see whether the prehair pattern looks more like the adult hair pattern or like that predicted by their protein orientation results.

Reviewer #2 (Public Review):

This paper aims to dissect the relative importance of the various cues that establish PCP in the wing disc of Drosophila, which remains a prominent and relevant model for PCP. The authors suggest that one must consider cues at three scales (molecular, cell and tissue) and specifically design tests for the importance of cell-level cues, which they call non-local cell scale signalling. They develop clever experimental approaches that allow them to track complex stability and also to induce polarity at experimentally defined times. In a first set of experiments, they restore PCP after the global cues have disappeared (de novo polarisation) and conclude from the results that another (cell scale) cue must exist. In another set of experiments, they show that de novo repolarization is robust to the dosage of various components of core PCP, leading them to conclude that there must be an underlying cell scale polarity, which, apparently, has nothing to do with microtubule or cell shape polarity. They then describe nice evidence that de novo polarisation is relatively short range both in a polarised and unpolarised field. They conclude that there is a strong cell-intrinsic polarity that remains to be characterised.

Major concerns:

(1) The first set of repolarisation experiments is performed after the global cell rearrangements that have been shown to act as global signals. However, this approach does not exclude the possible contribution of an unknown diffusible global signal.

(2) The putative non-local cell scale signal must be more precisely defined (maybe also given a better name). It is not clear to me that one can separate cell-scale from molecular-scale signal. Local signals can redistribute within a cell (or membrane) so local signals are also cell-scale. Without a clear definition, it is difficult to interpret the results of the gene dosage experiments. The link between gene dosage and cell-scale signal is not rigorously stated. Related to this, the concluding statement of the introduction is too cryptic.

Critique:

The experiments described in this paper are of high quality with a sophisticated level of design and analysis. However, there needs to be some recalibration of the extent of the conclusions that can be drawn. Moreover, a limitation of this paper is that, despite the quality of their data, they cannot give a molecular hint about the nature of their proposed cell-scale signal.

Reviewer #3 (Public Review):

The manuscript by Carayon and Strutt addresses the role of cell-scale signaling during the establishment of planar cell polarity (PCP) in the Drosophila pupal wing. The authors induce locally the expression of a tagged core PCP protein, Frizzled, and observe and analyze the de novo establishment of planar cell polarity. Using this system, the authors show that PCP can be established within several hours, that PCP is robust towards variation in core PCP protein levels, that PCP proteins do not orient microtubules, and that PCP is robust towards 'extrinsic' re-polarization. The authors conclude that the polarization at the cell-scale is strongly intrinsic and only weakly affected by the polarity of neighboring cells.

Major comments:

The data are clearly presented and the manuscript is well written. The conclusions are well supported by the data. 

(1) The authors use a system to de novo establish PCP, which has the advantage of excluding global cues orienting PCP and thus to focus on the cell-intrinsic mechanisms. At the same time, the system has the limitation that it is unclear to what extent de novo PCP establishment reflects 'normal' cell scale PCP establishment, in particular because the Gal4/UAS expression system that is used to induce Fz expression will likely result in much higher Fz levels compared with the endogenous levels. The authors should briefly discuss this limitation.

(2) Fig. 3. The authors use heterozygous mutant backgrounds to test the robustness of de novo PCP establishment towards (partial) depletion in core PCP proteins. The authors conclude that de novo polarization is 'extremely robust to variation in protein level'. Since the authors (presumably) lowered protein levels by 50%, this conclusion appears to be somewhat overstated. The authors should tune down their conclusion.

Significance: 

The manuscript contributes to our understanding of how planar cell polarity is established. It extends previous work by the authors (Strutt and Strutt, 2002,2007) that already showed that induction of core PCP pathway activity by itself is sufficient to induce de novo PCP. This manuscript further explores the underlying mechanisms. The authors test whether de novo PCP establishment depends on an 'inhibitory signal', as previously postulated (Meinhardt, 2007), but do not find evidence. They also test whether core PCP proteins help to orient microtubules (which could enhance cell intrinsic polarization of core PCP proteins), but, again, do not find evidence, corroborating previous work (Harumoto et al, 2010). The most significant finding of this manuscript, perhaps, is the observation that local de novo PCP establishment does not propagate far through the tissue. A limitation of the study is that the mechanisms establishing intrinsic cell scale polarity remain unknown. The work will likely be of interest to specialists in the field of PCP.

Reviewer #1 (Public review):

Summary:

In this manuscript, Liu et al have tried to dissect the neural and molecular mechanisms that C. elegans use to avoid the digestion of harmful bacterial food. Liu et al show that C. elegans use ON-OFF state of AWC olfactory neurons to regulate the digestion of harmful gram-positive bacteria S. saprophyticus (SS). Authors show that when C. elegans are fed on SS food, AWC neurons switch to OFF fate, which prevents the digestion of S. saprophyticus, and this helps C. elegans avoid these harmful bacteria. Using genetic and transcriptional analysis as well as making use of previously published findings, Liu et al implicate p38 MAPK pathway (in particular, NSY-1, the C. elegans homolog of MAPKKK ASK1) and insulin signaling in this process.

Strengths:

The revised manuscript has improved significantly. The authors have addressed almost all the comments that I had in my initial review.

Weaknesses:

None.

Reviewer #2 (Public review):

Summary:

Using C. elegans as a model, the authors present an interesting story demonstrating a new regulatory connection between olfactory neurons and the digestive system. Mechanistically, they identified key factors (NSY-1, STR-130 et.al) in neurons, as well as critical 'signaling factors' (INS-23, DAF-2) that bridge different cells/tissues to execute the digestive shutdown induced by poor-quality food (Staphylococcus saprophyticus, SS).

Strengths:

The conclusions of this manuscript are mostly well supported by the experimental results shown.

Weaknesses:

The authors have done a nice job in addressing my comments.

Reviewer #3 (Public review):

Summary:

The study explores a molecular mechanism by which C. elegans detects low-quality food through neuron-digestive crosstalk, offering new insights into food quality control systems. Liu and colleagues demonstrated that NSY-1, expressed in AWC neurons, is a key regulator for sensing Staphylococcus saprophyticus (SS), inducing avoidance behavior and shutting down the digestive system via intestinal BCF-1. They further revealed that INS-23, an insulin peptide, interacts with the DAF-2 receptor in the gut to modulate SS digestion. The study uncovers a food quality control system connecting neural and intestinal responses, enabling C. elegans to adapt to environmental challenges.

Strengths:

The study employs a genetic screening approach to identify nsy-1 as a critical regulator in detecting food quality and initiating adaptive responses in C. elegans. The use of RNA-seq analysis is particularly noteworthy, as it reveals distinct regulatory pathways involved in food sensing (Figure 4) and digestion of Staphylococcus saprophyticus (Figure 5). The strategic application of both positive and negative data mining enhances the depth of analysis. Importantly, the discovery that C. elegans halts digestion in response to harmful food and employs avoidance behavior highlights a physiological adaptation mechanism.

Weaknesses:

Major weaknesses have been addressed.

Reviewer #1 (Public review):

The authors adequately addressed the concerns I raised in my initial review, which are noted below.

(1) I suggest that the authors choose a different term in their title, abstract and manuscript to describe the phenotypes associated with ufd-1 and npl-4 knockdown other than an "inflammation-like response." Inflammation is a pathological term with four cardinal signs: redness (rubor), swelling (tumor), warmth (calor) and pain (dolor). These are not symptoms known to occur in C. elegans. The authors could consider using "inappropriate," "aberrant" or "toxic" immune activation in the title and abstract.

(2) I think it is important to point out in the context of the authors novelty claim in the abstract and manuscript that the toxic effects of inappropriate immune activation in C. elegans has been widely catalogued. For example: doi.org/10.1371/journal.ppat.1011120 (2023); doi:10.1186/s12915-016-0320-z (2016).; doi:10.1126/science.1203411 (2011); doi:10.1534/g3.115.025650 (2016). In addition, doi:10.7554/eLife.74206 (2022) previously described a mutation that caused innate immune activation that reduced accumulation of P. aeruginosa in the intestine, but also caused animals to have a shortened lifespan.

Thus, I do not think this study reveals the existence of inflammatory-like responses in C. elegans, as stated by the authors. Indeed, I think it is important for the authors to remove this novelty claim from their paper and discuss their work in the context of these studies in a paragraph in the introduction.

(3) The authors rely on the use of RNAi of ufd-1 and npl-4 to study their effect on P. aeruginosa colonization and pathogen resistance throughout the manuscript. To address the possibility of off-target effects of the RNAi, the authors should consider both (i) showing with qRT-PCR that these genes are indeed targeted during RNAi, and (ii) confirming their phenotypes with an orthologous technique, preferably by studying ufd-1 and npl-4 loss-of-function mutants [both in the wild-type and sek-1(km4) backgrounds]. If mutation of these genes is lethal, the authors could use Auxin Inducible Degron (AID) technology to induce the degradation of these proteins in post-developmental animals.

(4) I am confused about the author's explanation regarding their observation that inhibition of the UFD-1/ NPL-4 complex extends the lifespan of sek-1(km25) animals, but not pmk-1(km25) animals, as SEK-1 is the MAPKK that functions immediately upstream of the p38 MAPK PMK-1 to promote pathogen resistance.

I am also confused why their RNA-seq experiment revealed a signature of intracellular pathogen response genes and not PMK-1 targets, which the authors propose is accounting for toxic immune activation. Activation of which immune response leads to toxicity?

(5) The authors did not test alternative explanations for why UFD-1/ NPL-4 complex inhibition compromises survival during pathogen infection, other than exuberant immune activation. For example, it is possible that inhibition of this proteosome complex shortens lifespan by compromising the general health/ normal physiology of nematodes. Immune responses could be activated as a secondary consequence of this stress, and not be a direct cause of early mortality. Does sek-1(km4) mutant suppress the lifespan shortened lifespan of ufd-1 and npl-4 knockdown? This experiment should also be done with loss-of-function mutants, as noted in point 3.

(6) The conclusion of Figure 6 hinges on an experiment that uses double RNAi to knockdown two genes at the same time (Fig. 6D and 6G), an approach that is inherently fraught in C. elegans biology owing to the likelihood that the efficiency of RNAi-mediated gene knockdown is compromised and may account for the observed phenotypes. The proper control for double RNAi is not empty vector + ufd-1(RNAi), but rather gfp(RNAi) + ufd-1(RNAi), as the introduction of a second hairpin RNA is what may compromise knockdown efficiency. In this context, it is important to confirm that knockdown of both genes occurs as expected (with qRT-PCR) and to confirm this phenotype using available elt-2 loss-of-function mutants.

(7) A supplementary table with the source data for at least three replications (mean lifespan, n, statistical comparison) for each pathogenesis assay should be included in this manuscript.

Comments on revisions:

The authors adequately addressed the concerns I raised.

Reviewer #2 (Public review):

Summary:

The authors aimed to uncover what role, if any, the UFD1/NPL4 complex might play in innate immune responses of the nematode C. elegans. The authors find that loss of the complex renders animals more sensitive to both pathogenic and non-pathogenic bacteria. However, there appears to be a complex interplay with known innate immune pathways since loss of UFD1/NPL4 actually results in increased survival of animals lacking the canonical innate immune pathways.

Strengths:

The authors perform robust genetic analysis to exclude and include possible mechanisms by which the UFD1/NPL4 pathway acts in the innate immune response.

Weaknesses:

The argument that the loss of the UFD1/NPL4 complex triggers a response that mimics that of an intracellular pathogen is not thoroughly investigated. Additionally, the finding of a role of the GATA transcription factor, ELT-2, in this response is suggestive, but experiments showing sufficiency in the context of loss of the UFD1/NPL4 complex need to be explored.

Comments on revisions:

The authors have performed several control experiments for their RNAi based experiments and also tested the requirement for xbp-1s in their paradigm. The findings and their interpretations are acceptable.

Reviewer #1 (Public review):

The authors have addressed all my concerns and have addressed them to my satisfaction.

Reviewer #3 (Public review):

Summary:

This study investigates the role of the host protein RBMX2 in regulating the response to Mycobacterium bovis infection and its connection to epithelial-mesenchymal transition (EMT), a key pathway in cancer progression. Using bovine and human cell models, the authors have wisely shown that RBMX2 expression is upregulated following M. bovis infection and promotes bacterial adhesion, invasion, and survival by disrupting epithelial tight junctions via the p65/MMP-9 signaling pathway. They also demonstrate that RBMX2 facilitates EMT and is overexpressed in human lung cancers, suggesting a potential link between chronic infection and tumor progression. The study highlights RBMX2 as a novel host factor that could serve as a therapeutic target for both TB pathogenesis and infection-related cancer risk.

Strengths:

The major strengths lie in its multi-omics integration (transcriptomics, proteomics, metabolomics) to map RBMX2's impact on host pathways, combined with rigorous functional assays (knockout/knockdown, adhesion/invasion, barrier tests) that establish causality through the p65/MMP-9 axis. Validation across bovine and human cell models and in clinical tissue samples enhances translational relevance. Finally, identifying RBMX2 as a novel regulator linking mycobacterial infection to EMT and cancer progression opens exciting therapeutic avenues.

Weaknesses:

There are a few minor weaknesses like grammatical errors, spelling mistakes. Also, the manuscript is too dense; improving the narratives in the Results and Discussion section could help readers follow the logic of the experimental design and conclusions.

Reviewer #1 (Public review):

In the manuscript, Aldridge and colleagues investigate the role of IL-27 in regulating hematopoiesis during T. gondii infection. Using loss-of-function approaches, reporter mice, and the generation of serial chimeric mice, they elegantly demonstrate that IL-27 induction plays a critical role in modulating bone marrow myelopoiesis and monocyte generation to the infection site. The study is well-designed, with clear experimental approaches that effectively address the mechanisms by which IL-27 regulates bone marrow myelopoiesis and prevents HSC exhaustion. I have two minor comments that could enhance the conceptual framework of this study:

(1) The authors indirectly show that IL-27R expression on HSPCs is necessary for regulating HSC proliferation and preventing exhaustion. However, given that they have access to IL-27RFlox mice, they could cross these with Fgd5Cre mice to specifically delete IL-27R on long-term HSCs. This would provide direct evidence for the role of IL-27 signaling in LTHSCs during infection.

(2) Since memory T and B cells often home to the bone marrow, it would be interesting to consider the potential cross-talk between these cells, HSPCs, and IL-27 signaling during secondary T. gondii infection. A brief discussion of this possibility would strengthen the study's broader implications.

Reviewer #2 (Public review):

Aldridge et al. demonstrate the important role of IL-27 in limiting emergency myelopoiesis in response to Toxoplasma gondii infection. Interestingly, IL-27 acts specifically at the level of early haematopoietic progenitors, inducing STAT signalling, which, in this case, dampens proliferation and preserves HSC fitness.

They used different mouse genetic models such as HSC lineage tracing, IL27 and IL27R-deficient mice to show that :

HSCs actively participate in emergency myelopoiesis during Toxoplasma gondii infection.

The absence of IL27 and IL27R increases monocyte progenitors and monocytes, mainly inflammatory monocytes CCR2hi.

At steady state, loss of IL27 impairs HSC fitness as competitive transplantation shows long-term engraftment deficiency of IL27 BM cells. This impairment is exacerbated after infection.

IL27 is produced by various BM and other tissue cells at steady state and its expression increases with infection, mainly by increasing the number of monocytes producing it.

This article highlights a new mechanism that acts directly at the level of early hematopoietic cells to limit over-inflammation during infection.

Reviewer #1 (Public review):

Summary:

The authors were attempting to describe if trained innate immunity would modulate antibody dependent-cellular phagocytosis (ADCP) and/or efferocytosis.

Strengths:

The use of primary murine macrophages, and not a cell line, is considered a strength.

The trained immunity mediated changes to phagocytosis affected both myeloma and breast cancer cells. The broad effect is consistent with trained immunity.

In this revised manuscript, the authors now include in vivo data to show in vivo relevance.

Weaknesses:

There are many types of cancers so it would be helpful to focus the title more for the types of cancers included in the present study, the most relevant of course would be the type of cancer used for the in vivo model.

Reviewer #3 (Public review):

Summary:

Chatzis et al showed that β-glucan trained macrophages have decreased phagocytic activity of apoptotic tumor cells and that is accompanied by lower levels of secreted IL-1β using mouse model.

Strengths:

This finding has potential impact on designing new cancer immunotherapeutic approaches by targeting macrophage efferocytosis.

The concerns have been addressed.

Reviewer #1 (Public review):

Summary:

This fundamental work employed multidisciplinary approaches and conducted rigorous experiments to study how a specific subset of neurons in the dorsal striatum (i.e., "patchy" striatal neurons) modulates locomotion speed depending on the valence of naturalistic contexts.

Strengths:

The scientific findings are novel and original and significantly advance our understanding of how the striatal circuit regulates spontaneous movement in various contexts.

Weaknesses:

This is extensive research involving various circuit manipulation approaches. Some of these circuit manipulations are not physiological. This is discussed.

Reviewer #2 (Public review):

Hawes et al. investigated the role of striatal neurons in the patch compartment of the dorsal striatum. Using Sepw1-Cre line, the authors combined a modified version of the light/dark transition box test that allows them to examine locomotor activity in different environmental valence with a variety of approaches, including cell-type-specific ablation, miniscope calcium imaging, fiber photometry, and opto-/chemogenetics. First, they found ablation of patchy striatal neurons resulted in an increase in movement vigor when mice stayed in a safe area or when they moved back from more anxiogenic to safe environments. The following miniscope imaging experiment revealed that a larger fraction of striatal patchy neurons was negatively correlated with movement speed, particularly in an anxiogenic area. Next, the authors investigated differential activity patterns of patchy neurons' axon terminals, focusing on those in GPe, GPi, and SNr, showing that the patchy axons in SNr reflect movement speed/vigor. Chemogenetic and optogenetic activation of these patchy striatal neurons suppressed the locomotor vigor, thus demonstrating their causal role in the modulation of locomotor vigor when exposed to valence differentials. Unlike the activation of striatal patches, such a suppressive effect on locomotion was absent when optogenetically activating matrix neurons by using the Calb1-Cre line, indicating distinctive roles in the control of locomotor vigor by striatal patch and matrix neurons. Together, they have concluded that nigrostriatal neurons within striatal patches negatively regulate movement vigor, dependent on behavioral contexts where motivational valence differs.

The strengths of this work include the use of multiple experimental approaches, including genetic/viral ablation of patch neurons, miniscope single-cell imaging, as well as projection-specific recording of axonal activity by fiber photometry, and causal manipulation of the neurons by chemogenetic and optogenetics. Although similar findings were reported previously, the authors' results will be of value owing to multiple levels of investigation. In my view, this study will add to the important literature by demonstrating how patch (striosomal) neurons in the striatum controls movement vigor.

Reviewer #3 (Public review):

Hawes et al. combined behavioral, optical imaging, and activity manipulation techniques to investigate the role of striatal patch SPNs in locomotion regulation. Using Sepw1-Cre transgenic mice, they found that patch SPNs encode locomotion deceleration in a light-dark box procedure through optical imaging techniques. Moreover, genetic ablation of patch SPNs increased locomotion speed, while chemogenetic activation of these neurons decreased it. The authors concluded that a subtype of patch striatonigral neurons modulates locomotion speed based on external environmental cues.

In the revision, the authors have largely addressed my concerns with additional explanation and discussion, although some of the key experiments to strengthen the authors' claim by identifying the function of specific cell populations remain to be conducted due to technical challenges. Nevertheless, the current results remain valuable and interesting to a wide audience in the field.

Reviewer #1 (Public review):

Summary:

The authors have investigated the role of GAT3 in the visual system. First, they have developed a CRISPR/Cas9-based approach to locally knock out this transporter in the visual cortex. They then demonstrated electrophysiologically that this manipulation increases inhibitory synaptic input into layer 2/3 pyramidal cells. They further examined the functional consequences by imaging neuronal activity in the visual cortex in vivo. They found that absence of GAT3 leads to reduced spontaneous neuronal activity and attenuated neuronal responses and reliability to visual stimuli, but without an effect on orientation selectivity. Further analysis of this data suggests that Gat3 removal leads to less coordinated activity between individual neurons and in population activity patterns, thereby impaired information encoding. Overall, this is an elegant and technically advanced study that demonstrates a new and important role of GAT3 in controlling processing of visual information.

Strengths:

Development of a new approach for a local knockout (GAT3)

Important and novel insights into visual system function and its dependence on GAT3

Plausible cellular mechanism

Weaknesses:

No major weaknesses.

Reviewer #2 (Public review):

Summary:

Park et al. has made a tool for spatiotemporally restricted knockout of the astrocytic GABA transporter GAT3 leveraging CRISPR/Cas9 and viral transduction in adult mice, and evaluated the effects of GAT3 on neural encoding of visual stimulation.

Strengths:

This concise manuscript leverages state-of-the-art gene CRISPR/Cas9 technology for knocking out astrocytic genes. This has to a little degree been preformed previously in astrocytes and represents an important development in the field. Moreover they utilize in vivo two-photon imaging of neural responses to visual stimuli as a readout of neural activity, in addition to validating their data with ex vivo electrophysiology. Lastly, they use advanced statistical modeling to analyze the impact on GAT3 knockout. Overall, the study comes across as rigorous and convincing.

Weaknesses:

Adding the following experiments would potentially have strengthened the conclusions and helped interpret the findings, although may be considered outside the scope of this manuscript, and be pursued in future work:

(1) Neural activity is quite profoundly influenced by GAT3 knockout. Corroborating these relatively large changes to neural activity with in vivo electrophysiology of some sort as an additional readout would have strengthened the conclusions.

(2) Given the quite large effects on neural coding in visual cortex assessed with jRGECO imaging it would have been interesting the mouse groups could have been subjected to behavioral testing assessing the visual system.

Reviewer #1 (Public review):

The manuscript by Yin and colleagues addresses a long-standing question in the field of cortical morphogenesis, regarding factors that determine differential cortical folding across species and individuals with cortical malformations. The authors present work based on a computational model of cortical folding evaluated alongside a physical model that makes use of gel swelling to investigate the role of a two-layer model for cortical morphogenesis. The study assesses these models against empirically derived cortical surfaces based on MRI data from ferret, macaque monkey, and human brains.

The manuscript is clearly written and presented, and the experimental work (physical gel modeling as well as numerical simulations) and analyses (subsequent morphometric evaluations) are conducted at the highest methodological standards. It constitutes an exemplary use of interdisciplinary approaches for addressing the question of cortical morphogenesis by bringing together well-tuned computational modeling with physical gel models. In addition, the comparative approaches used in this paper establish a foundation for broad-ranging future lines of work that investigate the impact of perturbations or abnormalities during cortical development.

The cross-species approach taken in this study is a major strength of the work. However, correspondence across the two methodologies did not appear to be equally consistent in predicting brain folding across all three species. The results presented in Figures 4 (and Figures S3 & S4) show broad correspondence in shape index and major sulci landmarks across all three species. Nevertheless, the results presented for the human brain lack the same degree of clear correspondence for the gel model results as observed in the macaque and ferret. While this study clearly establishes a strong foundation for comparative cortical anatomy across species and the impact of perturbations on individual morphogenesis, further work that fine-tunes physical modeling of complex morphologies, such as that of the human cortex, may help to further understand the factors that determine cortical functionalization and pathologies.

Reviewer #2 (Public review):

This manuscript explores the mechanisms underlying cerebral cortical folding using a combination of physical modelling, computational simulations, and geometric morphometrics. The authors extend their prior work on human brain development (Tallinen et al., 2014; 2016) to a comparative framework involving three mammalian species: ferrets (Carnivora), macaques (Old World monkeys), and humans (Hominoidea). By integrating swelling gel experiments with mathematical differential growth models, they simulate sulcification instability and recapitulate key features of brain folding across species. The authors make commendable use of publicly available datasets to construct 3D models of fetal and neonatal brain surfaces: fetal macaque (ref. [26]), newborn ferret (ref. [11]), and fetal human (ref. [22]).

Using a combination of physical models and numerical simulations, the authors compare the resulting folding morphologies to real brain surfaces using morphometric analysis. Their results show qualitative and quantitative concordance with observed cortical folding patterns, supporting the view that differential tangential growth of the cortex relative to the subcortical substrate is sufficient to account for much of the diversity in cortical folding. This is a very important point in our field, and can be used in the teaching of medical students.

Brain folding remains a topic of ongoing debate. While some regard it as a critical specialization linked to higher cognitive function, others consider it an epiphenomenon of expansion and constrained geometry. This divergence was evident in discussions during the Strüngmann Forum on cortical development (Silver et al., 2019). Though folding abnormalities are reliable indicators of disrupted neurodevelopmental processes (e.g., neurogenesis, migration), their relationship to functional architecture remains unclear. Recent evidence suggests that the absolute number of neurons varies significantly with position-sulcus versus gyrus-with potential implications for local processing capacity (e.g., https://doi.org/10.1002/cne.25626). The field is thus in need of comparative, mechanistic studies like the present one.

This paper offers an elegant and timely contribution by combining gel-based morphogenesis, numerical modelling, and morphometric analysis to examine cortical folding across species. The experimental design - constructing two-layer PDMS models from 3D MRI data and immersing them in organic solvents to induce differential swelling - is well-established in prior literature. The authors further complement this with a continuum mechanics model simulating folding as a result of differential growth, as well as a comparative analysis of surface morphologies derived from in vivo, in vitro, and in silico brains.

I offer a few suggestions here for clarification and further exploration:

Major Comments

(1) Choice of Developmental Stages and Initial Conditions

The authors should provide a clearer justification for the specific developmental stages chosen (e.g., G85 for macaque, GW23 for human). How sensitive are the resulting folding patterns to the initial surface geometry of the gel models? Given that folding is a nonlinear process, early geometric perturbations may propagate into divergent morphologies. Exploring this sensitivity-either through simulations or reference to prior work-would enhance the robustness of the findings.

(2) Parameter Space and Breakdown Points

The numerical model assumes homogeneous growth profiles and simplifies several aspects of cortical mechanics. Parameters such as cortical thickness, modulus ratios, and growth ratios are described in Table II. It would be informative to discuss the range of parameter values for which the model remains valid, and under what conditions the physical and computational models diverge. This would help delineate the boundaries of the current modelling framework and indicate directions for refinement.

(3) Neglected Regional Features: The Occipital Pole of the Macaque

One conspicuous omission is the lack of attention to the occipital pole of the macaque, which is known to remain smooth even at later gestational stages and has an unusually high neuronal density (2.5× higher than adjacent cortex). This feature is not reproduced in the gel or numerical models, nor is it discussed. Acknowledging this discrepancy-and speculating on possible developmental or mechanical explanations-would add depth to the comparative analysis. The authors may wish to include this as a limitation or a target for future work.

(4) Spatio-Temporal Growth Rates and Available Human Data

The authors note that accurate, species-specific spatio-temporal growth data are lacking, limiting the ability to model inhomogeneous cortical expansion. While this may be true for ferret and macaque, there are high-quality datasets available for human fetal development, now extended through ultrasound imaging (e.g., https://doi.org/10.1038/s41586-023-06630-3). Incorporating or at least referencing such data could improve the fidelity of the human model and expand the applicability of the approach to clinical or pathological scenarios.

(5) Future Applications: The Inverse Problem and Fossil Brains

The authors suggest that their morphometric framework could be extended to solve the inverse growth problem-reconstructing fetal geometries from adult brains. This speculative but intriguing direction has implications for evolutionary neuroscience, particularly the interpretation of fossil endocasts. Although beyond the scope of this paper, I encourage the authors to elaborate briefly on how such a framework might be practically implemented and validated.

Conclusion

This is a well-executed and creative study that integrates diverse methodologies to address a longstanding question in developmental neurobiology. While a few aspects-such as regional folding peculiarities, sensitivity to initial conditions, and available human data-could be further elaborated, they do not detract from the overall quality and novelty of the work. I enthusiastically support this paper and believe that it will be of broad interest to the neuroscience, biomechanics, and developmental biology communities.

Note: The paper mentions a companion paper [reference 11] that explores the cellular and anatomical changes in the ferret cortex. I did not have access to this manuscript, but judging from the title, this paper might further strengthen the conclusions.

Reviewer #1 (Public review):

Summary:

In this work, Wang et al. use a combination of genetic tools, novel experimental approaches and biomechanical models to quantify the contribution of passive leg forces in Drosophila. They also deduce that passive forces are not sufficient to support the body weight of the animal. Overall, the contribution of passive forces reported in this work is much less than what one would expect based on the size of the organism and previous literature from larger insects and mammals. This is an interesting finding, but some major caveats in their approach remain unanswered.

Strengths:

(1) The authors combine experimental measurements and modeling to quantify the contributions of passive forces at limb joints in Drosophila.

(2) The authors replicate a previous experimental strategy (Hooper et al 2009, J. Neuro) to suspend animals in air for measuring passive forces and, as in previous studies, find that passive forces are much stronger than gravitational forces acting on the limbs. While in these previous studies using large insects, a lot of invasive approaches for accurately quantifying passive forces are possible (e.g., physically cutting of nerves, directly measuring muscle forces in isolated preparations, etc), the small size of Drosophila makes this difficult. The authors overcome this using a novel approach where they attach additional weight to the leg (changes gravitational force) and inactivate motor neurons (remove active forces). With a few approximations and assumptions, the authors then deduce the contribution of passive forces at each joint for each leg.

(3) The authors find interesting differences in passive forces across different legs. This could have behavioral implications.

(4) Finally, the authors compare experimental results of how a free-standing Drosophila is lowered ("falls down") on silencing motor neurons, to a biomechanical "OpenSim" model for deducing the role of passive forces in supporting the body weight of the fly. Using this approach, they conclude that passive forces are not sufficient to support the body weight of the fly.

Weaknesses:

(1) Line 65 "(Figure 1A). Inactivation causes a change in the leg's rest position; however, in preliminary experiments, the body rotation did not have a large effect on the rest positions of the leg following inactivation. This result is consistent with the one already reported for stick insects and shows that passive forces within the leg are much larger than the gravitational force on a leg and dominate limb position [1]." This is the direct replication of the previous work by Hooper et al 2009 and therefore authors should ideally show the data for this condition (no weight attached).

(2) The authors use vglut-gal4, a very broad driver for inactivating motor neurons. The driver labels all glutamatergic neurons, including brain descending neurons and nerve cord interneurons, in addition to motor neurons. Additionally, the strength of inactivation might differ in different neurons (including motor neurons) depending on the expression levels of the opsins. As a result, in this condition, the authors might not be removing all active forces. This is a major caveat that authors do not address. They explore that they are not potentially silencing all inputs to muscles by using an additional octopaminergic driver, but this doesn't address the points mentioned above. At the very least, the authors should try using other motor neuron drivers, as well as other neuronal silencers. This driver is so broad that authors couldn't even use it for physiology experiments. Additionally, the authors could silence VGlut-labeled motor neurons and record muscle activity (potentially using GCaMP as has been done in several recent papers cited by the authors, Azevedo et al, 2020) as a much more direct readout.

(3) Figure 4 uses an extremely simplified OpenSim model that makes several assumptions that are known to be false. For example, the Thorax-Coxa joint is assumed to be a ball and socket joint, which it is not. Tibia-tarsus joint is completely ignored and likely makes a major contribution in supporting overall posture, given the importance of the leg "claw" for adhering to substrates. Moreover, there are a couple of recent open-source neuromechanical models that include all these details (NeuromechFly by Lobato-Rios et al, 2022, Nat. Methods, and the fly body model by Vaxenburg et al, 2025, Nature). Leveraging these models to rule in or rule out contributions at other joints that are ignored in the authors' OpenSim model would be very helpful to make their case.

(4) Figure 5 shows the experimental validation of Figure 4 simulations; however, it suffers from several caveats.

a) The authors track a single point on the head of the fly to estimate the height of the fly. This has several issues. Firstly, it is not clear how accurate the tracking would be. Secondly, it is not clear how the fly actually "falls" on VGlut silencing; do all flies fall in a similar manner in every trial? Almost certainly, there will be some "pitch" and "role" in the way the fly falls. These will affect the location of this single-tracked point that doesn't reflect the authors' expectations. Unless the authors track multiple points on the fly and show examples of tracked videos, it is hard to believe this dataset and, hence, any of the resulting interpretations.

b) As described in the previous point, the "reason" the fly falls on silencing all glutamatergic neurons could be due to silencing all sorts of premotor/interneurons in addition to the silencing of motor neurons.

c) (line 175) "The first finding is that there was a large variation in the initial height of the fly (Figure 5C), consistent with a recent study of flies walking on a treadmill[20]." The cited paper refers to how height varies during "walking". However, in the current study, the authors are only looking at "standing" (i.e. non-walking) flies. So it is not the correct reference. In my opinion, this could simply reflect poor estimation of the fly's height based on poor tracking or other factors like pitch and role.

d) "The rate at which the fly fell to the ground was much smaller in the experimental flies than it was in the simulated flies (Figure 5E). The median rate of falling was 1.3 mm/s compared to 37 mm/s for the simulated flies (Figure 5F). (Line 190) The most likely reason for the longer than expected time for the fly to fall is delays associated with motor neuron inactivation and muscle inactivation." I don't believe this reasoning. There are so many caveats (which I described in the above points) in the model and the experiment, that any of those could be responsible for this massive difference between experiment and modeling. Simply not getting rid of all active forces (inadequate silencing) could be one obvious reason. Other reasons could be that the model is using underestimates of passive forces, as alluded to in point 3.

(5) Final figure (Figure 6) focuses on understanding the time course of neuronal silencing. First of all, I'm not entirely sure how relevant this is for the story. It could be an interesting supplemental data. But it seems a bit tangential. Additionally, it also suffers from major caveats.

a) The authors now use a new genetic driver for which they don't have any behavioral data in any previous figures. So we do not know if any of this data holds true for the previous experiments. The authors perform whole-cell recordings from random unidentified motor neurons labeled by E49-Gal4>GtACR1 to deduce a time constant for behavioral results obtained in the VGlut-Gal4>GtACR1 experiments.

b) The DMD setup is useful for focal inactivation, however, the appropriate controls and data are not presented. Line 200 "A spot of light on the cell body produces as much of the hyperpolarization as stimulating the entire fly (mean of 11.3 mV vs 13.1 mV across 9 neurons). Conversely, excluding the cell body produces only a small effect on the MN (mean of 2.6 mV)." First of all, the control experiment for showing that DMD is indeed causing focal inactivation would be to gradually move the spot of light away from the labeled soma, i.e. to the neighboring "labelled" soma and show that there is indeed focal inactivation. Instead authors move it quite a long distance into unlabeled neuropil. Secondly, I still don't get why the authors are doing this experiment. Even if we believe the DMD is functioning perfectly, all this really tells us is that a random subset motor neurons (maybe 5 or 6 cells, legend is missing this info) labeled by E49-Gal4 is strongly hyperpolarized by its own GtACR1 channel opening, rather than being impacted because of hyperpolarizations in other E49-Gal4 labeled neurons. This has no relevance to the interpretation of any of the VGlut-Gal4 behavioral data. VGLut-Gal4 is much broader and also labels all glutamatergic neurons, most of which are inhibitory interneurons whose silencing could lead to disinhibition of downstream networks.

Reviewer #2 (Public review):

Summary:

The authors aim to quantify passive muscle forces in the legs of Drosophila, and test the hypothesis that these forces would be sufficient to support body weight in small insects. They take advantage of the genetic tools available in Drosophila, and use a combination of genetic silencing (optogenetic inactivation of motor neurons), kinematic measurements, and simulations using OpenSim. This integrative toolkit is used to examine the role of passive torques across multiple leg joints. They find that passive forces are weaker than expected - in particular, passive forces were found to be too weak to support the body weight of the fly. This challenges previous scaling assumptions derived from studies in larger insects and has potential implications for our understanding of motor control in small animals.

Strengths:

The primary strength of this work lies in its integration of multiple analyses. By pulling together simulations, kinematic measurements from high-resolution videos, and genetic manipulation, they are able to overcome limitations of past studies. In particular, optogenetic manipulation allowed for measurements to be made in whole animals, and the modeling component is valuable because it both validates experimental findings and elucidates the mechanism behind some of the observed dynamic consequences (e.g., the rapid fall after motor inactivation). The conclusions made in the study are well-supported by the data and could have an impact on a number of fields, including invertebrate neurobiology and bioinspired design.

Weaknesses:

While (as mentioned above) the study's conclusions are well-supported by the results and modeling, limitations arise because of the assumptions made. For instance, using a linear approximation may not hold at larger joint angles, and future studies would benefit from accounting for nonlinearities. Future studies could also delve into the source of passive forces, which is important for more deeply understanding the anatomical and physical basis of the results in this study. For instance, assessments of muscle or joint properties to correlate stiffness values with physical structure might be an area of future consideration

Reviewer #3 (Public review):

Summary:

The authors present a novel method to measure passive joint torques - torques due to internal forces other than active muscle contraction - in the fruit fly: genetically inactivating all motor neurons in intact limb acted upon by a gravitational load results in a change in limb configuration; evaluating the moment equilibrium condition about the limb joints then yields a direct estimate of the passive joint torques. Deactivating all motor neurons in an intact standing fly provided two further conclusions: First, because deactivation causes the fly to drop to the floor, the passive joint torques are deemed insufficient to maintain rotational equilibrium against the body weight; using a multi-body-dynamics simulation, the authors estimate that the passive torques would need to be about 40-80 times higher to maintain a typical posture without active muscle action. Second, a delay between the motor neuron inactivation and the onset of the "free fall" motivates the authors to invoke a simple exponential decay model, which is then used to derive a time constant for muscle deactivation, in robust agreement with direct electro-physiological recordings.

Strengths:

The experimental design that permits determination of passive joint torques is elegant, effective, novel, and altogether excellent; it permits measurements previously impossible. A careful error analysis is presented, and a spectrum of technically challenging methods, including multi-body dynamics and e-phys, is deployed to further interpret and contextualise the results.

Weaknesses:

(1) Passive torques are measured, but only some short speculative statements, largely based on previous work, are offered on their functional significance; some of these claims are not well supported by experimental evidence or theoretical arguments. Passive forces are judged as "large" compared to the weight force of the limb, but the arguably more relevant force is the force limb muscles can generate, which, even in equilibrium conditions, is already about two orders of magnitude larger. The conclusion that passive forces are dynamically irrelevant seems natural, but contrasts with the assertion that "passive forces [...] will have a strong influence on limb kinematics". As a result, the functional significance of passive joint torques in the fruit fly, if any, remains unclear, and this ambiguity represents a missed opportunity. We now know the magnitude of passive joint torques - do they matter and for what? Are they helpful, for example, to maintain robust neuronal control, or a mechanical constraint that negatively impacts performance, e.g., because they present a sink for muscle work?

(2) The work is framed with a scaling argument, but the assumptions that underpin the associated claims are not explicit and can thus not be evaluated. This is problematic because at least some arguments appear to contradict textbook scaling theory or everyday experience. For example, active forces are assumed to scale with limb volume, when every textbook would have them scale with area instead; and the asserted scaling of passive forces involves some hidden assumptions that demand more explicit discussion to alert the reader to associated limitations. Passive forces are said to be important only in small animals, but a quick self-experiment confirms that they are sufficient to stabilize human fingers or ankles against gravity, systems orders of magnitude larger than an insect limb, in seeming contradiction with the alleged dominance of scale. Throughout the manuscript, there are such and similar inaccuracies or ambiguities in the mechanical framing and interpretation, making it hard to fairly evaluate some claims, and rendering others likely incorrect.

Reviewer #1 (Public review):

The manuscript by Choi and colleagues investigates the impact of variation in cortical geometry and growth on cortical surface morphology. Specifically, the study uses physical gel models and computational models to evaluate the impact of varying specific features/parameters of the cortical surface. The study makes use of this approach to address the topic of malformations of cortical development and finds that cortical thickness and cortical expansion rate are the drivers of differences in morphogenesis.

The study is composed of two main sections. First, the authors validate numerical simulation and gel model approaches against real cortical postnatal development in the ferret. Next, the study turns to modelling malformations in cortical development using modified tangential growth rate and cortical thickness parameters in numerical simulations. The findings investigate three genetically linked cortical malformations observed in the human brain to demonstrate the impact of the two physical parameters on folding in the ferret brain.

This is a tightly presented study that demonstrates a key insight into cortical morphogenesis and the impact of deviations from normal development. The dual physical and computational modeling approach offers the potential for unique insights into mechanisms driving malformations. This study establishes a strong foundation for further work directly probing the development of cortical folding in the ferret brain. One weakness of the current study is that the interpretation of the results in the context of human cortical development is at present indirect, as the modelling results are solely derived from the ferret. However, these modelling approaches demonstrate proof of concept for investigating related alterations more directly in future work through similar approaches to models of the human cerebral cortex.

Reviewer #2 (Public review):

Summary:

Based on MRI data of the ferret (a gyrencephalic non-primate animal, in whom folding happens postnatally), the authors create in vitro physical gel models and in silico numerical simulations of typical cortical gyrification. They then use genetic manipulations of animal models to demonstrate that cortical thickness and expansion rate are primary drivers of atypical morphogenesis. These observations are then used to explain cortical malformations in humans.

Strengths:

The paper is very interesting and original, and combines physical gel experiments, numerical simulations, as well as observations in MCD. The figures are informative, and the results appear to have good overall face validity.

Weaknesses:

On the other hand, I perceived some lack of quantitative analyses in the different experiments, and currently, there seems to be rather a visual/qualitative interpretation of the different processes and their similarities/differences.

Ideally, the authors also quantify local/pointwise surface expansion in the physical and simulation experiments, to more directly compare these processes. Time courses of eg, cortical curvature changes, could also be plotted and compared for those experiments.

I had a similar impression about the comparisons between simulation results and human MRI data. Again, face validity appears high, but the comparison appeared mainly qualitative.

I felt that MCDs could have been better contextualized in the introduction.

Reviewer #1 (Public review):

Summary:

Foik et al. report that hypochlorous acid, a reactive chlorine species generated during host defense, activates the transcription of the froABCD in P. aeruginosa. This gene cluster had previously been associated with a potential role during the flow of fluids and appears to be regulated by the sigma factor FroR and its anti-sigma factor FroI. In the present study, the authors show that froABCD is expressed both in neutrophils and macrophages, which they claim is likely a result of HOCl but not H2O2 production. Fro expression is also induced in a murine model of corneal infection, which is characterized by immune cell invasion. Expression of the fro system can be quenched by several antioxidants, such as methionine, cysteine, and others. FroR-deficient cells that lack froABCD expression during HOCl stress appear more sensitive to the oxidant.

Strengths:

The authors provide a number of data supporting their claim that transcription of the froABCD system is induced by reactive chlorine species. This was shown by RNAseq, qRT-PCR, and through microscopy using a transcriptional reporter fusion. Likewise, elevated expression of froABCD was shown in vitro and in vivo, excluding potential in vitro artifacts. The manuscript, while mostly descriptive, is easy to follow, and the data were presented clearly.

Weaknesses:

(1) Lines 60-62: Some of the authors' conclusions are not supported by the data and thus appear unfounded. One example: "we determine that fro upregulation.....These data suggest a novel mechanism..." Their data do not show that MSR upregulation is a direct effect of FroABCD. Instead, it could be possible that the FroR sigma factor also controls the expression of msr genes, which would be independent of froABCD.

(2) The authors show increased fro transcription both in neutrophils and macrophages; however, the two types of immune cells differ quite dramatically with respect to myeloperoxidase activation and HOCl production. Neither has this been discussed nor considered here.

(3) With respect to the activation of fro expression upon challenge with conditioned media from stimulated neutrophils, does the conditioned media contain detectable amounts of HOCl? Do chloramines, which are byproducts of HOCl oxidation with amines, also stimulate expression?

(4) A better control to prove that this fro expression is indeed induced by HOCl in activated neutrophils would be to conduct the experiments in the presence of a myeloperoxidase inhibitor.

(5) The work was conducted with two different P. aeruginosa strains (i.e. AL143 and PAO1F). None of the figure legends provides details on which strain was used. For instance, in line 111, the authors refer to Figure S1B for data that I thought were done with PAO1F, while in 154, data were presented in the context of the infection model, which was conducted with the other strain.

(6) It would be good if immune cell recruitment at 2hrs and 20hrs PI could be quantified.

(7) The conclusions of Figure 4 are, in my opinion, weak (line 187-188; "It is possible that ....."). These antioxidants likely quench the low amounts of NaOCl directly. This would significantly reduce the NaOCl concentrations to a level that no longer activates expression of fro. There is no direct evidence provided that oxidized methionine induces fro expression. Do the authors postulate that this is free methionine, or could methionine and/or cysteine oxidation in FroR increase the binding affinity of the sigma factor to the promoter? Another possibility is that NaOCl deactivates the anti-sigma factor. None of these scenarios has been considered here.

(8) Line 184: The reaction constants of HOCl with Cys and Met are similar.

(9) Treatment with 16 uM NaOCl caused a growth arrest of ~15 hrs in the WT (Figure 5A), whereas no growth at all was recorded with 7.5 uM in Figure 3A.

(10) The concentration range of NaOCl causing fro expression is extremely narrow, while oxidative burst rapidly generates HOCl at much higher concentrations. This should be discussed in more detail.

Reviewer #2 (Public review):

Summary:

Foik et al. studied the regulation of the fro operon in response to HOCl, an oxidant derived from immune cells, especially neutrophils. They use a transcriptional fusion of YFP to the froA promoter in an mCherry-expressing P. aeruginosa strain to determine fro-induction under the microscope. They use this system to study fro expression in medium, in the presence of neutrophils and macrophages, neutrophil-conditioned medium, and several chemical stimuli, including NaCl, HOCl, hydrogen peroxide, nitric acid, hydrochloric acid, and sodium hydroxide. They also use a corneal infection model to demonstrate that froA is upregulated in P. aeruginosa 20 h post-infection and perform transcriptional analyses in WT and a froR mutant in response to HOCl.

Strengths:

Their data clearly shows that HOCl is a strong inducer of the fro Operon. The addition of HOCl-quenching chemicals together with HOCl abrogates the response. They also show that a froR mutant is more susceptible to HOCl than WT. Their transcriptomic data reveal genes under control of the FroR/FroI sigma factor/anti sigma factor system.

Weaknesses:

Although the presented evidence is mostly solid, some of their findings need to be evaluated more carefully; explaining the rationale behind some of the experiments might enhance the article, and some of the models proposed by the authors seem far-fetched, as outlined below:

(1) In line 76 the authors claim "Relative to P. aeruginosa that were incubated in host cell-free media, P. aeruginosa in close proximity to human neutrophils or that were engulfed in mouse macrophages appeared to increase fro expression (Fig. 1C)". Counting bacterial cells in Figure 1C shows that 1 in 17 bacteria (5.8%) induce the froA-promotor in media in the absence of immune cells, while 4 in 72 bacteria (only 5.5%) do the same in the presence of neutrophils. Contrary to the authors' claims, it appears that P. aeruginosa actually decreases fro-expression in close proximity to neutrophils. There is a slight increase in fro-expression in bacteria co-incubated with macrophages (3 in 21, or 14.3%). A more rigorous statistical analysis might substantiate the authors' claim, but, as is, the claim "neutrophils increase fro expression" is untenable.

(2) The authors should explain the rationale behind some of the chemicals used. Why did they use nitric acid? Especially at these high concentrations, a strong acid such as nitric acid might have a significant influence on the medium pH. I understand that the medium is phosphate-buffered, but 25 mM nitric acid in an unbuffered medium would shift the pH well below 2. Similar considerations apply to hydrochloric acid and sodium hydroxide.

(3) In line 187, the authors state that "It is possible that oxidized methionine increases fro expression" and they suggest a model to that effect in Figure 5D. It is unclear why the authors singled out methionine sulfoxide, since a number of other things get oxidized by HOCl. In line 184, the authors state, in the same vein, that "HOCl oxidizes methionine residues 100-fold more rapidly than other cellular components". The authors should state which other cellular compounds they are referring to. Certainly not cysteine and other thiols, which react equally fast and are highly abundant in the cell: P. aeruginosa contains 340 µM GSH, 140 µM CoA-SH (https://doi.org/10.1074/jbc.RA119.009934) plus free cysteine and cysteines in proteins (based on codon usage, 1.34% of amino acids in proteins are cysteine, while methionine is only slightly more present at 2.10%, although a number of starting methionines are removed from mature proteins).

(4) Overall (and this is probably not addressable with the authors' data), some very interesting questions remain unanswered: what is the molecular mechanism of fro-induction? How is the FroR/FroI system modulated by HOCl? Does the system sense free or protein-bound methionine-sulfoxide? Are certain methionine residues in these proteins directly oxidized by HOCl? Many "HOCl-sensing" proteins are also modified at cysteine residues or amino groups; could those play a role? And lastly: what is the connection between shear/fluid flow and HOCl, or are these totally separate mechanisms of fro-induction?

Reviewer #1 (Public review):

Summary:

This study investigated the heterogeneous responses to Mycobacterium tuberculosis (Mtb) in 19 wild-derived inbred mouse strains collected from various geographic locations. The goal of this study is to identify novel mechanisms that regulate host susceptibility to Mtb infection. Using the genetically resistant C57BL/6 mouse strain as the control, they successfully identified a few mouse strains that revealed higher bacterial burdens in the lung, implicating increased susceptibility in those mouse strains. Furthermore, using flow cytometry analysis, they discovered strong correlations between CFU and various immune cell types, including T cells and B cells. The higher neutrophil numbers correlated with significantly higher CFU in some of the newly identified susceptible mouse strains. Interestingly, MANB and MANC mice exhibited comparable numbers of neutrophils but showed drastically different bacterial burdens. The authors then focused on the neutrophil heterogeneity and utilized a single-cell RNA-seq approach, which led to identifying distinct neutrophil subsets in various mouse strains, including C57BL/6, MANA, MANB, and MANC. Pathway analysis on neutrophils in susceptible MANC strain revealed a highly activated and glycolytic phenotype, implicating a possible mechanism that may contribute to the susceptible phenotype. Lastly, the authors found that a small group of neutrophil-specific genes are expressed across many other cell types in the MANC strain.

Strengths:

This manuscript has many strengths.

(1) Utilizing and characterizing novel mouse strains that complement the current widely used mouse models in the field of TB. Many of those mouse strains will be novel tools for studying host responses to Mtb infection.

(2) The study revealed very unique biology of neutrophils during Mtb infection. It has been well-established that high numbers of neutrophils correlate with high bacterial burden in mice. However, this work uncovered that some mouse strains could be resistant to infection even with high numbers of neutrophils in the lung, indicating the diverse functions of neutrophils. This information is important.

Weaknesses:

The weaknesses of the manuscript are that the work is relatively descriptive. It is unclear whether the neutrophil subsets are indeed functionally different. While single-cell RNA seq did provide some clues at transcription levels, functional and mechanistic investigations are lacking. Similarly, it is unclear how highly activated and glycolytic neutrophils in MANC strain contribute to its susceptibility.

Reviewer #2 (Public review):

Summary:

These studies investigate the phenotypic variability and roles of neutrophils in tuberculosis (TB) susceptibility by using a diverse collection of wild-derived inbred mouse lines. The authors aimed to identify new phenotypes during Mycobacterium tuberculosis infection by developing, infecting, and phenotyping 19 genetically diverse wild-derived inbred mouse lines originating from different geographic regions in North America and South America. The investigators achieved their main goals, which were to show that increasing genetic diversity increases the phenotypic spectrum observed in response to aerosolized M. tuberculosis, and further to provide insights into immune and/or inflammatory correlates of pulmonary TB. Briefly, investigators infected wild-derived mice with aerosolized M. tuberculosis and assessed early infection control at 21 days post-infection. The time point was specifically selected to correspond to the period after infection when acquired immunity and antigen-specific responses manifest strongly, and also early susceptibility (morbidity and mortality) due to M. tuberculosis infection has been observed in other highly susceptible wild-derived mouse strains, some Collaborative Cross inbred strains, and approximately 30% of individuals in the Diversity Outbred mouse population. Here, the investigators normalized bacterial burden across mice based on inoculum dose and determined the percent of immune cells using flow cytometry, primarily focused on macrophages, neutrophils, CD4 T cells, CD8 T cells, and B cells in the lungs. They also used single-cell RNA sequencing to identify neutrophil subpopulations and immune phenotypes, elegantly supplemented with in vitro macrophage infections and antibody depletion assays to confirm immune cell contributions to susceptibility. The main results from this study confirm that mouse strains show considerable variability to M. tuberculosis susceptibility. Authors observed that enhanced infection control correlated with higher percentages of CD4 and CD8 T cells, and B cells, but not necessarily with the percentage of interferon-gamma (IFN-γ) producing cells. High levels of neutrophils and immature neutrophils (band cells) were associated with increased susceptibility, and the mouse strain with the most neutrophils, the MANC line, exhibited a transcriptional signature indicative of a highly activated state, and containing potentially tissue-destructive, mediators that could contribute to the strain's increased susceptibility and be leveraged to understand how neutrophils drive lung tissue damage, cavitation, and granuloma necrosis in pulmonary TB.

Strengths:

The strengths are addressing a critically important consideration in the tuberculosis field - mouse model(s) of the human disease, and taking advantage of the novel phenotypes observed to determine potential mechanisms. Notable strengths include,

(1) Innovative generation and use of mouse models: Developing wild-derived inbred mice from diverse geographic locations is innovative, and this approach expands the range of phenotypic responses observed during M. tuberculosis infection. Additionally, the authors have deposited strains at The Jackson Laboratory making these valuable resources available to the scientific community.

(2) Potential for translational research: The findings have implications for human pulmonary TB, particularly the discovery of neutrophil-associated susceptibility in primary infection and/or neutrophil-mediated disease progression that could both inform the development of therapeutic targets and also be used to test the effectiveness of such therapies.

(3) Comprehensive experimental design: The investigators use many complementary approaches including in vivo M. tuberculosis infection, in vitro macrophage studies, neutrophil depletion experiments, flow cytometry, and a number of data mining, machine learning, and imaging to produce robust and comprehensive analyses of the wild-derives d strains and neutrophil subpopulations in 3 weeks after M. tuberculosis infection.

Weaknesses:

The manuscript and studies have considerable strengths and very few weaknesses. One minor consideration is that phenotyping is limited to a single limited-time point; however, this time point was carefully selected and has a strong biological rationale provided by investigators. This potential weakness does not diminish the overall findings, exciting results, or conclusions.

Reviewer #1 (Public review):

Summary:

The work by Pinon et al describes the generation of a microvascular model to study Neisseria meningitidis interactions with blood vessels. The model uses a novel and relatively high throughput fabrication method that allows full control over the geometry of the vessels. The model is well characterized from the vascular standpoint and shows improvements when exposed to flow. The authors show that Neisseria binds to the 3D model in a similar geometry that in the animal xenograft model, induces an increase in permeability short after bacterial perfusion, and endothelial cytoskeleton rearrangements including a honeycomb actin structure. Finally, the authors show neutrophil recruitment to bacterial microcolonies and phagocytosis of Neisseria.

Strengths:

The article is overall well written, and it is a great advancement in the bioengineering and sepsis infection field. The authors achieved their aim at establishing a good model for Neisseria vascular pathogenesis and the results support the conclusions. I support the publication of the manuscript. I include below some clarifications that I consider would be good for readers.

One of the most novel things of the manuscript is the use of a relatively quick photoablation system. Could this technique be applied in other laboratories? While the revised manuscript includes more technical details as requested, the description remains difficult to follow for readers from a biology background. I recommend revising this section to improve clarity and accessibility for a broader scientific audience.

The authors suggest that in the animal model, early 3h infection with Neisseria do not show increase in vascular permeability, contrary to their findings in the 3D in vitro model. However, they show a non-significant increase in permeability of 70 KDa Dextran in the animal xenograft early infection. As a bioengineer this seems to point that if the experiment would have been done with a lower molecular weight tracer, significant increases in permeability could have been detected. I would suggest to do this experiment that could capture early events in vascular disruption.

One of the great advantages of the system is the possibility of visualizing infection-related events at high resolution. The authors show the formation of actin of a honeycomb structure beneath the bacterial microcolonies. This only occurred in 65% of the microcolonies. Is this result similar to in vitro 2D endothelial cultures in static and under flow? Also, the group has shown in the past positive staining of other cytoskeletal proteins, such as ezrin in the ERM complex. Does this also occur in the 3D system?

Significance:

The manuscript is comprehensive, complete and represents the first bioengineered model of sepsis. One of the major strengths is the carful characterization and benchmarking against the animal xenograft model. Beyond the technical achievement, the manuscript is also highly quantitative and includes advanced image analysis that could benefit many scientists. The authors show a quick photoablation method that would be useful for the bioengineering community and improved the state-of-the-art providing a new experimental model for sepsis.

My expertise is on infection bioengineered models.

Reviewer #2 (Public review):

Pinon and colleagues have developed a Vessel-on-Chip model showcasing geometrical and physical properties similar to the murine vessels used in the study of systemic infections. The vessel was created via highly controllable laser photoablation in a collagen matrix, subsequent seeding of human endothelial cells, and flow perfusion to induce mechanical cues. This model could be infected with Neisseria meningitidis as a model of systemic infection. In this model, microcolony formation and dynamics, and effects on the host were very similar to those described for the human skin xenograft mouse model (the current gold standard for systemic studies) and were consistent with observations made in patients. The model could also recapitulate the neutrophil response upon N. meningitidis systemic infection.

The claims and the conclusions are supported by the data, the methods are properly presented, and the data is analyzed adequately. The most important strength of this manuscript is the technology developed to build this model, which is impressive and very innovative. The Vessel-on-Chip can be tuned to acquire complex shapes and, according to the authors, the process has been optimized to produce models very quickly. This is a great advancement compared with the technologies used to produce other equivalent models. This model proves to be equivalent to the most advanced model used to date (skin xenograft mouse model). The human skin xenograft mouse model requires complex surgical techniques and has the practical and ethical limitations associated with the use of animals. However, the Vessel-on-chip model is free of ethical concerns, can be produced quickly, and allows to precisely tune the vessel's geometry and to perform higher resolution microscopy. Both models were comparable in terms of the hallmarks defining the disease, suggesting that the presented model can be an effective replacement of the animal use in this area. In addition, the Vessel-on-Chip allows to perform microscopy with higher resolution and ease, which can in turn allow more complex and precise image-based analysis.

A limitation of this model is that it lacks the multicellularity that characterizes other similar models, which could be useful to research disease more extensively. However, the authors discuss the possibilities of adding other cells to the model, for example, fibroblasts. It is also not clear whether the technology presented in the current paper can be adopted by other labs. The methodology is complex and requires specialized equipment and personnel, which might hinder its widespread utilization of this model by researchers in the field.

This manuscript will be of interest for a specialized audience focusing on the development of microphysiological models. The technology presented here can be of great interest to researchers whose main area of interest is the endothelium and the blood vessels, for example, researchers on the study of systemic infections, atherosclerosis, angiogenesis, etc. This manuscript can have great applications for a broad audience and it can present an opportunity to begin collaborations, aimed at answering diverse research questions with the same model.

Reviewer #3 (Public review):

Summary:

In this manuscript Pinon et al. describe the development of a 3D model of human vasculature within a microchip to study Neisseria meningitidis (Nm)- host interactions and validate it through its comparison to the current gold-standard model consisting of human skin engrafted onto a mouse. There is a pressing need for robust biomimetic models with which to study Nm-host interactions because Nm is a human-specific pathogen for which research has been primarily limited to simple 2D human cell culture assays. Their investigation relies primarily on data derived from microscopy and its quantitative analysis, which support the authors' goal of validating their Vessel-on-Chip (VOC) as a useful tool for studying vascular infections by Nm, and by extension, other pathogens associated with blood vessels.

Strengths:<br /> • Introduces a novel human in vitro system that promotes control of experimental variables and permits greater quantitative analysis than previous models<br /> • The VOC model is validated by direct comparison to the state-of-the-art human skin graft on mouse model<br /> • The authors make significant efforts to quantify, model, and statistically analyze their data<br /> • The laser ablation approach permits defining custom vascular architecture<br /> • The VOC model permits the addition and/or alteration of cell types and microbes added to the model<br /> • The VOC model permits the establishment of an endothelium developed by shear stress and active infusion of reagents into the system

Weaknesses:<br /> • The work presented here is mostly descriptive, with little new information that is learned about the biology of Nm or endothelial cells. However, the goal of this study was to establish the VOC model, and the validation presented here is necessary for follow-on studies on Nm pathogenesis and host response.<br /> • The VOC model contains one cell type, human umbilical cord vascular endothelial cells (HUVECs), while true vasculature contains a number of other cell types that associate with and affect the endothelium, such as smooth muscle cells, pericytes, and components of the immune system. These and other shortcomings of the VOC model as it currently stands warrant additional discussion.

Impact:<br /> The VOC model presented by Pinon et al. is an exciting advancement in the set of tools available to study human pathogens interacting with the vasculature. This manuscript focuses on validating the model, and as such sets the foundation for impactful research in the future. Of particular value is the photoablation technique that permits the custom design of vascular architecture without the use of artificial scaffolding structures described in previously published works.

Reviewer #1 (Public review):

Summary:

In this report, Yabaji et al describe studies designed to address the mechanism behind the TB susceptibility gene sst1. This locus is known to affect expression of IFN and synergizes with Myc to potentiate infectivity. Using a variety of molecular expression and imaging techniques, the authors demonstrate that mice harboring an sst1 transgene (compared to B6 controls) are highly susceptible to TB infection via a mechanism involving loss of antioxidant defense systems, the down regulation of key antioxidant genes and ferritin controlling intracellular iron levels. The combination of increased iron plus decreased antioxidant defense systems in turn increases lipid peroxidation and downstream sequelae. Inhibition of peroxidation diminishes infectivity increases ferritin levels. Furthermore, the authors demonstrate that Myc activation potentiates this process and that down regulation of NRF2 antioxidant defenses accompany potentiated infectivity. Increased peroxidation products (4-HNE) may activate the ASK1/JNK system leading to IFNb superinduction and diminished macrophage viability thereby diminishing ability to withstand TB infection. Extending these findings, additional mouse models plus some work in humans supports the peroxidation hypothesis. Overall, the work is significant for it introduces a molecular basis for TB infectivity and presents a potential novel therapeutic opportunity.

Strengths:

(1) Strengths of this study include a multi-omic analysis of infectivity combining gene expression analysis with biochemical and cell biological evaluation.

(2) Novel identification of an iron-catalyzed lipid peroxidation based mechanism for why the sst1 locus is linked to TB infection.

(3) Parallels to human biology are included via analysis of Myc upregulation in peripheral blood from patients.

(4) Appropriate statistical analysis

Weaknesses:

(1) Lipid peroxidation is a broad phenotype process and the authors honed in on 4-HNE dependent processes as a likely mechanism because they can measure 4-HNE conjugated proteins. However, lipid peroxidation is a complex phenomenon and the work presented herein is largely descriptive.

(2) The authors continually refer to increased 4HNE while they do not measure this 9 carbon lipid, they actually measure 4-HNE conjugated proteins immunochemically.

(3) The authors do not distinguish between increased protein-HNE adducts and increased membrane peroxidation (or both) as mechanistically linked to infectivity.

Reviewer #1 (Public review):

Summary:

The authors add to the body of evidence showing theta rhythmic modulations of neuronal activity and behavior.

Strengths:

Precise characterization of the effects of visual stimulation on theta-induced neuronal oscillations of spiking neurons in V1 and its relevance for behavior.

The manuscript is well-written and clearly presented,

Weaknesses:

The advances are limited over the established body of evidence. Both theta-induced visual oscillations and their relevance for behavior have been firmly established by prior work, including prior work from the authors. There is no major new technique, data, finding, or insight that extends our knowledge in a majorly significant way beyond existing knowledge, in my opinion. I would suggest that the authors re-evaluate the body of existing work to more strongly place their work in the context of existing work. A study that targets fundamental holes or open questions in the field would have been viewed as more impactful.

Reviewer #2 (Public review):

Summary:

Schmid & colleagues test an interesting hypothesis that V1 neurons might act as theta-tuned filters to incoming sensory information, and thereby influence downstream processing and detection performance.

Strengths:

The authors report that circular stimuli elicit theta oscillations in V1 single units and population activity. They also report that the phase of the theta oscillations influences performance in a change detection task.

Weaknesses:

The results are reported in terms of specific stimulus sizes. To truly reflect general-purpose spatial computations in the primary visual cortex, it will be important to establish a relationship between stimulus size and receptive field size.

I have several major concerns that I would like the authors to address:

(1) First paragraph of Results: The results are presented at very specific stimulus sizes: 0.3-degree, 1-degree, 4-degree, and so on. A key missing piece of information is the size of the receptive fields (RFs) that were recorded from. A related missing information is at what eccentricity these RFs were recorded from. Since there is nothing magical about a 1-degree stimulus, any general-purpose computation in the primary visual cortex has to establish a relationship between RF size and stimulus size.

(2) Second paragraph of Results: The authors state that "specific stimulus sizes consistently induced strong theta rhythmic activity: 1{degree sign} in MUA and 2{degree sign} in LFP". What is the interpretation of these specific sizes? Given that the LFP and MUAe reflect different aspects of neural activity, how does one interpret the discrepancy?

(3) Third paragraph of Results: Again related to (1), what is the relationship between the stimulus size that elicited the largest theta peaks and RF size at the population level? (1)-(3) taken together, there seems to be an opportunity to reveal something more fundamental about V1 processing that the authors might have missed here.

(4) Change detection task: It was not clear to me whether the timing of the luminance change, which varied from 500ms to 1500ms, was drawn from an exponential distribution or a uniform distribution. Only an exponential distribution has the property of a flat hazard function, which will be important to establish that the animal could not anticipate the timing of the upcoming change.

(5) Figure 3D: Have the authors tried to fit the data separately for each animal? There seems to be an inconsistency in the results between the 2 animals. The circular data points ('AL') seem positively correlated, similar to the overall trend, but the diamond data points ('DP') seem to have a negative slope.

Reviewer #3 (Public review):

Summary:

This paper investigates changes in brain oscillations in V1 in response to experimentally manipulating visual stimulus features (size, contrast at optimal size) and examines whether these effects are of perceptual relevance. The results reveal prominent stimulus-related theta oscillations in V1 that match in frequency the rhythms of behavioural performance (response speed in detecting targets in the visual display). Phase analyses relate these fluctuations of detection performance more formally to opposite theta phase angles in V1.

Strengths:

The non-human primate model provides unique findings on how brain oscillations relate to rhythms in perception (in two rhesus monkeys) that align well with findings from human studies (as occurring in the theta band). However, theta rhythms in humans are typically associated with fronto-parietal activity in the domain of spatial orienting, attentional sampling, while here the focus is on V1. Importantly, microsaccade-controls seem to speak against a spatial orienting/ attentional sampling mechanism to explain the observed effects (at least regarding overt attention).

Weaknesses:

This study provides interesting clues on perceptually relevant brain oscillations. Despite the microsaccade-control, I believe it remains an open question whether the V1 rhythmicity is of pure V1 origin, or driven by top-down input, as it is conceivable that specific stimuli capture attention differently (and hence induce specific covert attentional (re)orienting patterns). For perceptually relevant (yet beta) rhythmicity over occipital areas that are top-down generated, see e.g., Veniero et al., 2019.

Reviewer #2 (Public review):

This manuscript describes the role of the production of c-di-AMP on the chlamydial developmental cycle. The main findings remain the same. The authors show that overexpression of the dacA-ybbR operon results in increased production of c-di-AMP and early expression of transitionary and late genes. The authors also knocked down the expression of the dacA-ybbR operon and reported a modest reduction in the expression of both hctA and omcB. The authors conclude with a model suggesting the amount of c-di-AMP determines the fate of the RB, continued replication, or EB conversion.

Overall, this is a very intriguing study with important implications however the data is very preliminary and the model is very rudimentary. The data support the observation that dramatically increased c-di-AMP has an impact on transitionary gene expression and late gene expression suggesting dysregulation of the developmental cycle. This effect goes away with modest changes in c-di-AMP (detaTM-DacA vs detaTM-DacA (D164N)). However, the model predicts that low levels of c-di-AMP delays EB production is not not well supported by the data. If this prediction were true then the growth rate would increase with c-di-AMP reduction and the data does not show this. The levels of of c-di-AMP at the lower levels need to be better validated as it seems like only very high levels make a difference for dysregulated late gene expression. However, on the low end it's not clear what levels are needed to have an effect as only DacAopMut and DacAopKD show any effects on the cycle and the c-di-AMP levels are only different at 24 hours.

The data still do not support the overall model.

In Figure 1 the authors show at 24 hpi.

DacA overexpression increases cdiAMP to ~4000 pg/ml

DacAmut overexpression reduces cdiAMP dramatically to ~256 pg/ml)

DacATM overexpression increases cdiAMP to ~4000 pg/ml.

DacAmutTM overexpression does not seem to change cdiAMP ~1500 pg/ml .

dacAKD decreases cdiAMP to ~300 pg/ml .

dacAKDcom increased cdiAMP to ~8000 pg/ml.

DacA-ybbRop overexpression increased cdiAMP to ~500,000 pg/ml.

DacA-ybbRopmut ~300 pg/ml.

However in Figure 2 the data show that overexpression of DacA (cdiAMP ~4000 pg/ml) did not have a different phenotype than over expression of the mutant (cdiAMP ~256 pg/ml). HctA expression down, omcB expression down, euo not much change, replication down, and IFUs down. Additionally, Figure 3 shows no differences in anything measured although cdiAMP levels were again dramatically different. DacATM overexpression (~4000 pg/ml) and DacAmutTM (~1500). This makes it unclear what cdiAMP is doing to the developmental cycle.

In Figure 4 the authors knockdown dacA (dacA-KD) and complement the knockdown (dacA-KDcom) dacAKD decreases cdiAMP (~300) while DacA-KDcom increases cdiAMP much above wt (~8000).<br /> KD decreased hctA and omcB at 24hpi. Complementation resulted in a moderate increase in hctA at a single time point but not at 24 hpi and had no effect on euo or omcB expression. Importantly, complementation decreased the growth rate. Based on the proposed model, growth rate should increase as the chlamydia should all be RBs and replicating and not exiting the cell cycle to become EBs (not replicating). Interestingly reducing cdiAMP levels by over expressing DacAmut (~256 pg/ml) did not have an effect on the cycle but the reduction in cdiAMP by knockdown of dacA (~300 pg/ml) did have a moderate effect on the cycle.

For Figure 5 DacA-ybbRop was overexpressed and this increased cdiAMP dramatically ~500,000 pg/ml as compared to wt ~1500. This increased hctA only at an early timepoint and not at 24hpi and again had no effect on omcB or euo. Overexpression of the operon with the mutation DacA-ybbRopmut reduced cdiAMP to ~300 pg/ml and this showed a reduction in growth rate similar to dacAmut but a more dramatic decrease in IFUs.

Overall:

DacA overexpression increases cdiAMP to ~4000 pg/ml (decreased everything except euo)

DacAmut overexpression reduces cdiAMP dramatically (~256 pg/ml). (decreased everything except euo)

DacATM overexpression increases cdiAMP to ~4000 pg/ml (no changes noted)

DacAmutTM overexpression does not seem to change cdiAMP ~1500 pg/ml (no changes noted)

dacAKD decrease cdiAMP to ~300 pg/ml (decreased everything except euo)

dacAKDcom increased cdiAMP to ~8000 pg/ml (decreases growth rate, increase hctA a little but not omcB)

DacA-ybbRop overexpression increased cdiAMP to ~500,000 pg/ml (decreases growth rate, increase hctA a little but not omcB)

DacA-ybbRopmut ~300 pg/ml (decreased everything except euo)

Overall, the data show that increasing cdiAMP only has a phenotype if it is dramatically increased, no effect at 4000 pg/ml. Decreasing cdiAMP has a consistent effect, decreased growth rate, IFU, hctA expression and omcB expression. However, if their proposed model was correct and low levels of cdiAMP blocked EB conversion then more chlamydial cells would be RBs (dividing cells) and the growth rate should increase. Conversely, if cdiAMP levels were dramatically raised then all RBs would all convert and the growth rate would be very low. When cdiAMP was raised to ~4000 pg/ml there was no effect on the growth rate. However, an increase to ~8000 pg/ml resulted in a significant decrease but growth continued. Increasing cdAMP to ~500,000 pg/ml had less of an impact on the growth rate. Overall, the data does not cleanly support the proposed model.

Reviewer #1 (Public review):

Summary:

This is a contribution to the field of developmental bioelectricity. How do changes of resting potential at the cell membrane affect downstream processes? Zhou et al. reported in 2015 that phosphatidylserine and K-Ras cluster upon plasma membrane depolarization and that voltage-dependent ERK activation occurs when constitutively active K-RasG12V mutants are overexpressed. In this paper, the authors advance the knowledge of this phenomenon by showing that membrane depolarization up-regulates mitosis and that this process is dependent on voltage-dependent activation of ERK. ERK activity's voltage-dependence is derived from changes in the dynamics of phosphatidylserine in the plasma membrane and not by extracellular calcium dynamics. This paper reports an interesting and important finding. It is somewhat derivative of Zhou et al., 2015. (https://www.science.org/doi/full/10.1126/science.aaa5619). The main novelty seems to be that they find quantitatively different conclusions upon conducting similar experiments, albeit with a different cell line (U2OS) than those used by Zhou et al. Sasaki et al. do show that increased K+ levels increase proliferation, which Zhou et al. did not look at. The data presented in this paper are a useful contribution to a field often lacking such data.

Strengths:

Bioelectricity is an important field for areas of cell, developmental, and evolutionary biology, as well as for biomedicine. Confirmation of ERK as a transduction mechanism and a characterization of the molecular details involved in the control of cell proliferation are interesting and impactful.

Weaknesses:

The authors lean heavily on the assumption that the Nernst equation is an accurate predictor of membrane potential based on K+ level. This is a large oversimplification that undermines the author's conclusions, most glaringly in Figure 2C. The author's conclusions should be weakened to reflect that the activity of voltage gated ion channels and homeostatic compensation are unaccounted for.

There are grammatical tense errors are made throughout the paper (ex line 99 "This kinetics should be these kinetics")

Line 71: Zhou et al. use BHK, N2A, PSA-3 cells, this paper uses U2OS (osteosarcoma) cells. Could that explain the differences in bioelectric properties that they describe? In general, there should be more discussion of the choice of cell line. Why were U2OS cells chosen? What are the implications of the fact that these are cancer cells, and bone cancer cells in particular? Does this paper provide specific insights for bone cancers? And crucially, how applicable are findings from these cells to other contexts?

Line 115: The authors use EGF to calibrate 'maximal' ERK stimulation. Is this level near saturation? Either way is fine, but it would be useful to clarify.

Line 121: Starting line 121 the authors say "Of note, U2OS cells expressed wild-type K-Ras but not an active mutant of K-Ras, which means voltage dependent ERK activation occurs not only in tumor cells but also in normal cells". Given that U2OS cells are bone sarcoma cells, is it appropriate to refer to these as 'normal' cells in contrast to 'tumor' cells?

Line 101: These normalizations seem reasonable, the conclusions sufficiently supported and the requisite assumptions clearly presented. Because the dish-to-dish and cell-to-cell variation may reflect biologically relevant phenomena it would be ideal if non-normalized data could be added in supplemental data where feasible.

Figure 2C is listed as Figure 2D in the text

There is no Figure 2F (Referenced in line 148)

Reviewer #2 (Public review):

Sasaki et al. use a combination of live-cell biosensors and patch-clamp electrophysiology to investigate the effect of membrane potential on the ERK MAPK signaling pathway, and probe associated effects on proliferation. This is an effect that has long been proposed, but a convincing demonstration has remained elusive, because it is difficult to perturb membrane potential without disturbing other aspects of cell physiology in complex ways. The time-resolved measurements here are a nice contribution to this question, and the perforated patch clamp experiments with an ERK biosensor are fantastic - they come closer to addressing the above difficulty of perturbing voltage than any prior work. It would have been difficult to obtain these observations with any other combination of tools.

However, there are still some concerns as detailed in specific comments below:

Specific comments:

(1) All the observations of ERK activation, by both high extracellular K+ and voltage clamp, could be explained by cell volume increase (more discussion in subsequent comments). There is a substantial literature on ERK activation by hypotonic cell swelling (e.g. https://doi.org/10.1042/bj3090013, https://doi.org/10.1002/j.1460-2075.1996.tb00938.x, among others). Here are some possible observations that could demonstrate that ERK activation by volume change is distinct from the effects reported here:

i) Does hypotonic shock activate ERK in U2OS cells?

ii) Can hypotonic shock activate ERK even after PS depletion, whereas extracellular K+ cannot?

iii) Does high extracellular K+ change cell volume in U2OS cells, measured via an accurate method such as fluorescence exclusion microscopy?

iv) It would be helpful to check the osmolality of all the extracellular solutions, even though they were nominally targeted to be iso-osmotic.

(2) Some more details about the experimental design and the results are needed from Figure 1:

i) For how long are the cells serum-starved? From the Methods section, it seems like the G1 release in different K+ concentration is done without serum, is this correct? Is the prior thymidine treatment also performed in the absence of serum?

ii) There is a question of whether depolarization constitutes a physiologically relevant mechanism to regulate proliferation, and how depolarization interacts with other extracellular signals that might be present in an in vivo context. Does depolarization only promote proliferation after extended serum starvation (in what is presumably a stressed cell state)? What fraction of total cells are observed to be mitotic (without normalization), and how does this compare to the proliferation of these cells growing in serum-supplemented media? Can K+ concentration tune proliferation rate even in serum-supplemented media?

(3) In Figure 2, there are some possible concerns with the perfusion experiment:

i) Is the buffer static in the period before perfusion with high K+, or is it perfused? This is not clear from the Methods. If it is static, how does the ERK activity change when perfused with 5 mM K+? In other words, how much of the response is due to flow/media exchange versus change in K+ concentration?

ii) Why do there appear to be population-average decreases in ERK activity in the period before perfusion with high K+ (especially in contrast to Fig. 3)? The imaging period does not seem frequent enough for photobleaching to be significant.

(4) Figure 3 contains important results on couplings between membrane potential and MAPK signaling. However, there are a few concerns:

i) Does cell volume change upon voltage clamping? Previous authors have shown that depolarizing voltage clamp can cause cells to swell, at least in the whole-cell configuration:

https://www.cell.com/biophysj/fulltext/S0006-3495(18)30441-7 . Could it be possible that the clamping protocol induces changes in ERK signaling due to changes in cell volume, and not by an independent mechanism?

ii) Does the -80 mV clamp begin at time 0 minutes? If so, one might expect a transient decrease in sensor FRET ratio, depending on the original resting potential of the cells. Typical estimates for resting potential in HEK293 cells range from -40 mV to -15 mV, which would reach the range that induces an ERK response by depolarizing clamp in Fig. 3B. What are the resting potentials of the cells before they are clamped to -80 mV, and why do we not see this downward transient?

(5) The activation of ERK by perforated voltage clamp and by high extracellular K+ are each convincing, but it is unclear whether they need to act purely through the same mechanism - while additional extracellular K+ does depolarize the cell, it could also be affecting function of voltage-independent transporters and cell volume regulatory mechanisms on the timescales studied. To more strongly show this, the following should be done with the HEK cells where there is already voltage clamp data:

i) Measure resting potential using the perforated patch in zero-current configuration in the high K+ medium. Ideally this should be done in the time window after high K+ addition where ERK activation is observed (10-20 minutes) to minimize the possibility of drift due to changes in transporter and channel activity due to post-translational regulation.

ii) Measure YFP/CFP ratio of the HEK cells in the high K+ medium (in contrast to the U2OS cells from Fig. 2 where there is no patch data).

iii) The assertion that high K+ is equivalent to changes in Vmem for ERK signaling would be supported if the YFP/CFP change from K+ addition is comparable to that induced by voltage clamp to the same potential. This would be particularly convincing if the experiment could be done with each of the 15 mM, 30 mM, and 145 mM conditions.

(6) Line 170: "ERK activity was reduced with a fast time course (within 1 minute) after repolarization to -80 mV." I don't see this in the data: in Fig. 3C, it looks like ERK remains elevated for > 10 min after the electrical stimulus has returned to -80 mV

Comments on revisions:

The authors have done a good job addressing the comments on the previous submission.

Reviewer #3 (Public review):

Summary:

This paper demonstrates that membrane depolarization induces a small increase in cell entry into mitosis. Based on previous work from another lab, the authors propose that ERK activation might be involved. They show convincingly using a combination of assays that ERK is activated by membrane depolarization. They show this is Ca2+ independent and is a result of activation of the whole K-Ras/ERK cascade which results from changed dynamics of phosphatidylserine in the plasma membrane that activates K-Ras. Although the activation of the Ras/ERK pathway by membrane depolarization is not new, linking it to an increase in cell proliferation is novel.

Strengths

A major strength of the study is the use of different techniques - live imaging with ERK reporters, as well as Western blotting to demonstrate ERK activation as well as different methods for inducing membrane depolarization. They also use a number of different cell lines. Via Western blotting the authors are also able to show that the whole MAPK cascade is activated.

Weaknesses

A weakness of the study is the data in Figure 1 showing that membrane depolarization results in an increase of cells entering mitosis. There are very few cells entering mitosis in their sample in any condition. This should be done with many more cells to increase the confidence in the results. The study also lacks a mechanistic link between ERK activation by membrane depolarization and increased cell proliferation.

The authors did achieve their aims with the caveat that the cell proliferation results could be strengthened. The results, for the most par,t support the conclusions.

This work suggests that alterations in membrane potential may have more physiological functions than action potential in the neural system as it has an effect on intracellular signalling and potentially cell proliferation.

In the revised manuscript, the authors have now addressed the issues with Figure 1, and the data presented are much clearer. They did also attempt to pinpoint when in the cell cycle ERK is having its activity, but unfortunately, this was not conclusive.

Reviewer #1 (Public review):

Summary:

In this manuscript, Mack and colleagues investigate the role of posttranslational modifications, including lysine acetylation and ubiquitination, in methyltransferase activity of SETD2 and show that this enzyme functions as a tumor suppressor in a KRASG12C-driven lung adenocarcinoma. In contrast to H3K36me2-specific oncogenic methyltransferases, the deletion of SETD2, which is capable of H3K36 trimethylation, increases lethality in a KRASG12C-driven lung adenocarcinoma mouse tumor model. In vitro, the authors demonstrate that polyacetylation of histone H3, particularly of H3K27, H3K14 and H3K23, promotes the catalytic activity of SETD2, whereas ubiquitination of H2A and H2B has no effect.

Strengths:

Overall, this is a well-designed study that addresses an important biological question regarding the functioning of the essential chromatin component. The manuscript contains excellent quality data, and the conclusions are convincing and justified. This work will be of interest to many biochemists working in the field of chromatin biology and epigenetics.

Comments on revisions:

All previous comments are well addressed, and I enthusiastically support publication.

Reviewer #2 (Public review):

Summary:

Human histone H3K36 methyltransferase Setd2 has been previously shown to be a tumor suppressor in lung and pancreatic cancer. In this manuscript by Mack et al., the authors first use a mouse KRASG12D-driven lung cancer model to confirm in vivo that Setd2 depletion exacerbates tumorigenesis. They then investigate the enzymatic regulation of the Setd2 SET domain in vitro, demonstrating that H2A, H3, or H4 acetylation stimulates Setd2-SET activity, with specific enhancement by mono-acetylation at H3K14ac or H3K27ac. In contrast, histone ubiquitination has no effect. The authors propose that H3K27ac may regulate Setd2-SET activity by facilitating its binding to nucleosomes. This work provides insight into how cross-talk between histone modifications regulates Setd2 function.

Comments on revisions:

(1) Regarding New Figure 2F lane 1, please reference PMID: 33972509 Fig 4D bottom. Setd2-SET is a well-known robust K36 trimethylase. Why, under the authors' conditions, do WT nucleosomes show a significant amount of K36me1 and K36me2 accumulation, whereas K36me3 is not as pronounced? As a comparison, the authors should also report the evidence for the efficiency of each chemical modification that generates K36 methylation mimic.

(2) The bottom panel of Figure 2B does not match the top one; the number of repeats should be indicated in the figure legends.

(3) In Figure 4E, the differences between Setd2-bound WT and acetylated nucleosomes are minimal, as judged by both the decreasing trend of unbound nucleosomes and the increasing trend of bound fractions. This experiment needs to be quantified based on multiple repeats.

Reviewer #1 (Public review):

In this manuscript, Wolfson and co-authors demonstrate a combination of an injury-specific enhancer and engineered AAV that enhances transgene expression in injured myocardium. The authors characterize spatiotemporal dynamics of TREE-directed AAV expression in the injured heart using a non-invasive longitudinal monitoring system. They show that transgene expression is drastically increased 3 days post-injury, driven by 2ankrd1a. They reported a liver-detargeted capsid, AAV cc.84, with decreased viral entry into the liver while maintaining TREE transgene specificity. They further identified the IR41 serotype with enhanced transgene expression in injured myocardium from AAV library screening. This is an interesting study that optimizes the potential application of TREE delivery for cardiac repair.

Comments on revisions:

The authors are responsive and have addressed my concerns.

Reviewer #2 (Public review):

Summary:

In this manuscript by Wolfson et al., various adeno-associated viruses (AAVs) were delivered to mice to assess the cardiac-specificity, injury border-zone cardiomyocyte transduction rate, and temporal dynamics in the goal to find better AAVs for gene therapies targeting the heart. The authors delivered tissue regeneration enhancer elements (TREEs) controlling luciferase expression and used IVIS imaging to examine transduction in the heart and other organs. They found that luciferase expression increased in the first week after injury when using AAV9-TREE-Hsp68 promoter, waning to baseline levels by 7 weeks. However, AAV9 vectors transduced the liver, which was significantly reduced by using an AAV.cc84 liver de-targeting capsid. The authors then performed in vivo screening of AAV9 capsids and found AAV-IR41 to preferentially transduce injured myocardium when compared to AAV9. Finally, the authors combined TREEs with AAV-IR41 to show improved luciferase expression compared to AAV9-TREE at 7, 14 and 21 days after injury.

Overall, this manuscript provides insights into TREE expression dynamics when paired with various heart-targeting capsids, which can be useful for researchers studying ischemic injury of murine hearts. While the authors have shown the success of using AAV9-TREEs in porcine hearts, it is unknown whether the expression dynamics would be similar in pigs or humans, as mentioned in the limitations.

Strengths:

Important contribution to the AAV gene therapy literature.

Comments on revised version:

My concerns have been adequately addressed.

Reviewer #3 (Public review):

Summary:

The tissue regeneration enhancer elements (TREEs) identified in zebrafish have been shown to drive injury-activated temporal-spatial gene expression in mice and large animals. These findings increase the translational potential of findings in zebrafish to mammals. In this manuscript, the authors tested TREEs in combination with different adeno-associated viral (AAV) vectors using in vivo luciferase bioluminescent imaging that allows for longitudinal tracking. The TREE-driven luciferase delivered by a liver de-targeted AAV.cc84 decreased off-target transduction in liver. They further screened an AAV library to identify capsid variants that display enhanced transduction for infarcted myocardium post ischemia reperfusion and myocardial infarction. A new capsid variant, AAV.IR41, was found to show increased transduction post I/R and MI.

Strengths:

The authors injected AAV-cargo several days after ischemia/reperfusion (I/R) injury as a clinically relevant approach. Overall, this study is significant in that it identifies new AAV vectors that can be used to deliver promising genes as potential new gene therapies in the future. The manuscript is well-written and the data are also of high quality.

Weaknesses:

The authors have addressed my previous concerns.

Reviewer #2 (Public review):

This is a timely and insightful study aiming to explore the general physical principles for the sub-compartmentalization--or lack thereof--in the phase separation processes underlying the assembly of postsynaptic densities (PSDs), especially the markedly different organizations in three-dimensional (3D) droplets on one hand and the two-dimensional (2D) condensates associated with a cellular membrane on the other. Simulation of a highly simplified model (one bead per protein domain) is apparently carefully executed. Based on a thorough consideration of various control cases, the main conclusion regarding the trade-off between repulsive excluded volume interactions and attractive interactions among protein domains in determining the structures of 3D vs 2D model PSD condensates is quite convincing. The novel results in this manuscript should be published.

Comment on the revised manuscript:

The authors have adequately addressed all my previous concerns. The manuscript is now much improved, ready for publication as a version of record.

Reviewer #3 (Public review):

Summary:

In this work, Yamada, Brandani and Takada have developed a mesoscopic model of the interacting proteins in the postsynaptic density. They have performed simulations, based on this model and using the software ReaDDy, to study the phase separation in this system in 2D (on the membrane) and 3D (in the bulk). They have carefully investigated the reasons behind different morphologies observed in each case, and have looked at differences in valency, specific/non-specific interactions and interfacial tension.

Strengths:

The simulation model is developed very carefully, with strong reliance on binding valency and geometry, experimentally measured affinities, and physical considerations like the hydrodynamic radii. The presented analyses are also thorough, and great effort has been put into investigating different scenarios that might explain the observed effects.

Weaknesses:

The biggest weakness of the study, in my opinion, has been a lack of more in-depth and quantitative physical insights about phase separation theories. In the revised version, the authors have added text to point the interested reader to the respective theories, and have included a qualitative assessment of their findings in the light of said theories. This better positions their discussion. I still believe the role of entropic effects need more attention, which can be the subject of future studies.

The authors have revised their Introduction and added text to the Discussion, to enrich their view on the attractive and repulsive forces as well as mixing entropy. This version better covers the physics of phase separation.

I appreciate the added discussion about the different diffusive behavior in the membrane in contrast to the bulk (i.e. the Saffman-Delbrück model). This paves the way for future studies, including realistic kinetics of the studied system.

Joint Public Review:

This manuscript reconsiders the "general form" of Hamilton's rule, in which "benefit" and "cost" are defined as regression coefficients. It points out that there is no reason to insist on Hamilton's rule of the form -c+br>0, and that, in fact, arbitrarily many terms (i.e. higher-order regression coefficients) can be added to Hamilton's rule to reflect nonlinear interactions. Furthermore, it argues that insisting on a rule of the form -c+br>0 can result in conditions that are true but meaningless and that statistical considerations should be employed to determine which form of Hamilton's rule is meaningful for a given dataset or model.

Comments on latest version:

The authors have provided a robust, valuable and detailed response to the previous reviews.

Comments from Reviewer #1: I have nothing further to add.

Comments from Reviewer #2: I appreciate the clarifications the author has made to the manuscript regarding (i) "sample covariance" terminology, (ii) the generality of the "generalized Price equation", and (iii) the distinction between the covariance and regression forms of the Price equation. I also appreciate that the ms now engages more deeply with some of the previous literature on regression-based Hamilton's rules (e.g. Smith et al., 2010; Rousset 2015). I feel these revisions make this contribution more valuable, and also more technically sound, since the term "sample covariance" is no longer used incorrectly.

I also add that I agree with the substance of the authors' response to Reviewer #3. That is, the original submission was very clear that the regression-based Hamilton's rule is already completely general in the range of situations to which it applies, and that the added "generality" in the present ms refers to the variety of regression models that can be applied to these situations. In this way, the original ms already anticipates and addresses the criticism that Reviewer #3 raises.

Reviewer #3 did not provide comments on the revised version.

Reviewer #1 (Public review):

Filamentous fungi are established work horses in biotechnology with Aspergillus oryzae as a prominent example with a thousand-year of history. Still the cell biology and biochemical properties of the production strains is not well understood. The paper of the Takeshita group describes the change in nuclear numbers and correlate it to different production capacities. They used microfluidic devices to really correlate the production with nuclear numbers. In addition, they used microdissection to understand expression profile changes and found an increase of ribosomes. The analysis of two genes involved in cell volume control in S. pombe did not reveal conclusive answers to explain the phenomenon. It appears that it is a multi-trait phenotype. Finally, they identified SNPs in many industrial strains and tried to correlate them to the capability of increasing their nuclear numbers.

The methods used in the paper range from high quality cell biology, Raman spectroscopy to atomic force and electron microscopy and from laser microdissection to the use of microfluidic devices to study individual hyphae.

This is a very interesting, biotechnologically relevant paper with the application of excellent cell biology.

Comments on revised version:

The authors addressed all suggestions satisfactorily.

Reviewer #2 (Public review):

Summary:

In the study presented by Itani and colleagues it is shown that some strains of Aspergillus oryzae - especially those used industrially for the production of sake and soy sauce - develop hyphae with a significantly increased number of nuclei and cell volume over time. These thick hyphae are formed by branching from normal hyphae and grow faster and therefore dominate the colonies. The number of nuclei positively correlates with the thicker hyphae and also the amount of secreted enzymes. The addition of nutrients such as yeast extract or certain amino acids enhanced this effect. Genome and transcriptome analyses identified genes, including rseA, that are associated with the increased number of nuclei and enzyme production. The authors conclude from their data involvement of glycosyltransferases, calcium channels and the tor regulatory cascade in regulation of cell volume and number of nuclei. Thicker hyphae and an increased number of nuclei was also observed in high-production strains of other industrially used fungi such as Trichoderma reesei and Penicillium chrysogenum, leading to the hypothesis that the mentioned phenotypes are characteristic of production strains which is of significant interest for fungal biotechnology.

Strengths:

The study is very comprehensive and involves application of divers state-of-the-art cell biological, biochemical and genetical methods. Overall, the data are properly controlled and analyzed, figures and movies are of excellent quality.<br /> The results are particularly interesting with regard to the elucidation of molecular mechanisms that regulate the size of fungal hyphae and their number of nuclei. For this, the authors have discovered a very good model: (regular) strains with a low number of nuclei and strains with high number of nuclei. Also, the results can be expected to be of interest for the further optimization of industrially relevant filamentous fungi.

In the revision the authors addressed all my comments and as a result produced an even stronger study.

Reviewer #3 (Public review):

Summary:

The authors seek to determine the underlying traits that support the exceptional capacity of Aspergillus oryzae to secrete enzymes and heterologous proteins. To do so, they leverage the availability of multiple domesticated isolates of A. oryzae along with other Aspergillus species to perform comparative imaging and genomic analysis.

Strengths:

The strength of this study lies in the use of multifaceted approaches to identify significant differences in hyphal morphology that correlate with enzyme secretion, which is then followed by the use of genomics to identify candidate functions that underlie these differences.

Weaknesses:

Although the image analysis and data interpretation is convincing, the genetic data supporting the author's model is somewhat more speculative and will likely require additional investigation.

Overall, the authors have achieved their aims in that they are able to clearly document the presence of two distinct hyphal forms in A. oryzae and other Aspergillus species, and to correlate the presence of the thicker rapidly growing form with enhanced enzyme secretion. The image analysis is convincing. The discovery that addition of yeast extract and specific amino acids can stimulate formation of the novel hyphal form is also notable. Although the conclusions are generally supported by the results, this is perhaps less so for the genetic analysis as it remains unclear how direct the role of RseA and the calcium transporters might be in supporting the formation of the thicker hyphae.

The results presented here will impact the field. The complexity of hyphal morphology and how it affects secretion are not well understood despite the importance of these processes for the fungal lifestyle. In addition, the description of approaches that can be used to facilitate the study of these different hyphal forms (i.e., stimulation using yeast extract or specific animo acids) will benefit future efforts to understand the molecular basis of their formation.

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

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

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

In conclusion, the study conveys an important message, but, as it stands, the strength of evidence is incomplete. It would greatly benefit from a more detailed and complete analysis of the experimental data, a better fit between this analysis and the corresponding vertex model, and a more in-depth discussion of biological and biophysical aspects. These revisions should be rather easily done, and would then make the evidence much more solid.

Reviewer #2 (Public review):

Summary:

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

Strengths:

(1) Very detailed analysis of experiments to systematically characterize and quantify differences between mammary and bronchial epithelia.

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

Weaknesses:

(1) It is unclear what the mechanistic origin of the shape-tension coupling is, which is used in the vertex model, and how important that coupling is for the presented results. The authors claim that the shape-tension coupling is due to the anisotropic distribution of stress fibers when cells are under external stress. It is unclear why the stress fibers should affect an effective line tension on the cell boundaries and why the stress fibers should be sensitive to the magnitude of the internal isotropic cell pressure. In experiments, it makes sense that stress fibers form when cells are stretched. Similar stress fibers form when the cytoskeleton or polymer networks are stretched. It is unclear why the stress fibers should be sensitive to the magnitude of internal isotropic cell pressure. If all the surrounding cells have the same internal pressure, then the cell would not be significantly deformed due to that pressure, and stress fibers would not form. The authors should better justify the use of the shape-tension coupling in the model and also present simulation results without that coupling. I expect that most of the observed behavior is already captured by the differential tension, even if there is no shape-tension coupling.

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

(3) The authors should also analyze the cell line tension data in simulations and make a comparison with experiments.

Reviewer #1 (Public review):

Summary:

Sakelaris and Riecke used computational modeling to explore how neurogenesis and sequential integration of new neurons into a network support memory formation and maintenance. They focus on the integration of granule cells in the olfactory bulb, a brain area where adult neurogenesis is prominent. Experimental results published during recent years provide an excellent basis to address the question at hand by biologically constrained models. The study extends previous computational models and provides a coherent picture of how multiple processes may act in concert to enable rapid learning, high stability of memories, and high memory capacity. This computational model generates experimentally testable predictions and is likely to be valuable to understand roles of neurogenesis and related phenomena in memory. One of the key findings is that important features of the memory system depend on transient properties of adult-born granule cells such as enhanced excitability and apoptosis during specific phases the development of individual neurons. The model can explain many experimental observations, and suggests specific functions for different processes (e.g., importance of apoptosis for continual learning). While this model is obviously a massive simplification of the biological system, it conceptualizes diverse experimental observations into a coherent picture, it generates testable predictions for experiments, and it and will likely inspire further modeling and experimental studies.

Strengths:

- The model can explain diverse experimental observations

- The model directly represents the biological network

Weaknesses:

- As many other models of biological networks, this model contains major simplifications.

Reviewer #2 (Public review):

Summary:

The authors propose a mechanism to provide flexibility to learn new information while preserving stability in neural networks by combining structural plasticity and synaptic plasticity.

Strengths:

An intriguing idea, well embedded in experimental data.

Authors have done a great job addressing reviewers' concerns

Weaknesses:

None

Reviewer #3 (Public review):

The manuscript is focused on local bulbar mechanisms to solve the flexibility-stability dilemma in contrast to long range interactions documented in other systems (hippocampus-cortex). The network performance is assessed in a perceptual learning task: the network is presented with alternating, similar artificial stimuli (defined as enrichment) and the authors assess its ability to discriminate between these stimuli by comparing the mitral cell representations quantified by Fisher discriminant analysis. The authors use enhancement in discriminability between stimuli as function of the degree of specificity of connectivity in the network to quantify the formation of an odor-specific network structure which as such has memory - they quantify memory as the specificity of that connectivity.

The focus on neurogenesis, excitability and synaptic connectivity of abGCs is topical, and the authors systematically built their model, clearly stating their assumptions and setting up the questions and answers. In my opinion, the combination of latent dendritic representations, excitability and apoptosis in an age-dependent manner is interesting and as the authors point out leads to experimentally testable hypotheses.

In the revised manuscript, the authors have systematically addressed my previous concerns. In particular, they now refer to previous work on granule cells-mitral cell interactions more generally, they explain the pros and cons for usage of specificity in connectivity as a proxy for memory capacity, and the biological plausibility of the model.

Reviewer #1 (Public review):

Summary:

This work provides a comprehensive analysis of how adult zebrafish show fear responses to conspecific alarm substances (CAS) and retain their associative memory. It shows that freezing is a more reliable measure of fear response and memory compared to evasive swimming, and that the reactivity and the type of responses depend on the zebrafish strain. It further suggests neuronal substrates of different fear responses based on c-Fos mapping.

Strengths:

The behavioral part is the most comprehensive and detailed yet in the zebrafish field, providing strong support for the authors' claim. The flow from Figure 1 to Figure 4 is very smooth. They provide extremely detailed, yet complementary and necessary, analyses of how different categories of behavior emerge over time during the CAS exposure and memory retrieval. I'm convinced that neuro researchers who study fear/stress responses will always refer to this paper to plan and interpret their future experiments.

Weaknesses:

The neural analysis part is very comprehensive. Figure 5 and Figure 6 are independent but complement each other very well. They together support that the cerebellar system is the key brain component for a freezing response. Their extreme focus on high-level analyses, however, came at the expense of biological intuitions. I suggest adding some figure panels and result/discussion paragraphs to help with that aspect.

Reviewer #2 (Public review):

In this study, Fontana et al. develop a paradigm for associative conditioning by pairing exposure to an alarm substance with a novel tank. Exposure to conspecific alarm substance (CAS) in the novel tank triggers freezing and what they characterize as evasive swimming behaviour, which is subsequently seen in a re-exposure to the novel tank without the CAS present. Importantly, these states are identified via automated processes, including postural tracking and a random forest classification process, which could be very useful tools for subsequent studies.

In their experiments, they focus on the differences in behaviour among strains of zebrafish (both males and females), and among individual zebrafish. For males and females of different strains, they find some differences, though the clearest message seems to be that the most robust measure of the behaviour in response to both the CAS and in the memory trials is the freezing behaviour, while evasive behaviour is more variable. and not always seen. This may relate to their observation of significant "evasiveness" in vehicle control experiments (discussed further below).

Moving on to individual variation from within this multi-strain male/female dataset, they first examine transition matrices between states and find tthat his is not dramatically altered by stimulus exposure. They then use clustering to identify 4 different "classes" of zebrafish that differ in their expression (or not) of two types of behaviour: freezing and/or evasive behaviour. They show that over the three exposure epochs of the experiment, this classification is somewhat stable in an individual fish, though many fish change their behaviour - e.g., evading + freezing -> only freezing.

In the final set of experiments, the authors move beyond behavioural analyses and perform whole-brain cFos mapping of these individual zebrafish. They perform analyses aimed at identifying correlations between individual behavioural expression and the number of cFos-positive cells in different brain regions. Using partial least squares analysis, they find areas associated with two types of behavioural contrasts, which differ in their weighting of different behavioural expression during the Memory trials. Covariation and network structure analysis within different classes of larvae also find some differences in covariation among brain areas, providing hypotheses as to underlying network effects that may govern the expression of freezing and/or evasive behavior in the memory trial phases.

Overall, I find this to be an interesting study that employs state of the are methods of behavioural analyses and whole-brain cFos analyses, but I am left a little bit confused as to what the take home message is and what can be concluded from this complex study that mixes in analyses of strain, sex, and individuality within a quite complex assay with multiple behavioural parameters.

My suggestions are as follows:

(1) My first concern relates to the claim in the abstract that "We found that fear memory behavior fell into four distinct groups: non-reactive, evaders, evading freezers, and freezers".

In my opinion, the "freezing" aspect is well supported as being both triggered by the CAS and for memory effect upon re-exposure to the tank, but I am less convinced about the "evasive" behaviour. In Figure 2, it appears that "evasiveness" is generally not increased in both the Exposure or Memory phases for many groups, and in Figure 5, it appears that "evasiveness" is expressed by nearly 50% of the fish in the pre-exposure condition before CAS addition and in all phases in the vehicle condition. Therefore, it appears that most of the expression of this behaviour is independent of any memory-based effect.

(2) My second concern relates to the claim in the abstract that "background strain and sex influenced how fish respond to CAS, with males more likely to increase evasive behaviors than females and the TU strain more likely to be non-reactive."

My understanding, based on the introduction and on the methods, is that it is likely important that the CAS be prepared from conspecifics of the same strain and sex, and for this reason, they prepared different CAS specific for each strain and each sex. Therefore, the "CAS" that is applied is necessarily different for each condition, and I am concerned about if the differences observed could relate more to variation in the quality, purity, concentration, etc. of the specific CAS samples for different groups, rather than their reactivity to the substance or their ability to form memories based on such experiences.

(3) My third concern relates to the interpretation of the cFos data.

As I mentioned above, I feel as though the behavioural analysis is perhaps more complex than is warranted via the inclusion of evasiveness, and I wonder if the conclusions from the experiments would be simpler if analyzed only from the perspective of freezing.

But considering the presented analyses: while I dont think there is anything wrong with the partial least squares approach and the network analyses, I am concerned that the simple messaging in the text does not reflect the complexity of this analysis combining different weightings of different behavioural characteristics in a behavioural contrast, or covariations among many regions and what such analyses mean at the level of brain function. For these reasons, I feel like statements along the lines of "Behavioral variation is driven by differences in the activity of brain regions outside the telencephalon, such as the cerebellum, preglomerular nuclei, preoptic area and hypothalamus" are not well supported.

Reviewer #3 (Public review):

Summary:

This manuscript by Fontana et al. sets out to fill a critical gap in our understanding of how individuality in fear responses corresponds to changes in brain activity. Previous work has shown in myriad species that fear behaviors are highly variable, and these variabilities correlate with sex and strain, with epigenetic modifications, and neural activity in specific regions of the brain, such as the amygdala. However, a whole-brain functional assessment of whether activity in different regions of the brain is associated with fear behavior has been difficult to assess, in part due to the large size and opacity of the brain. The Kenney group overcomes these limitations using the zebrafish, together with powerful behavioral and brain imaging approaches pioneered by their lab. To overcome the technical obstacles of delivering a reproducible unconditioned stimulus in water and quantifying nuanced behavioral responses, the authors developed a three-day conditioning paradigm in which fish were repeatedly exposed to CAS in one tank context and to control water in another. Leveraging automated cluster analysis across over 300 individuals from four inbred strains, they identified four distinct memory-recall phenotypes - non-reactive, evaders, evading freezers, and freezers - demonstrating both the robustness of their assay and the influence of genetic background and sex on fear learning. Finally, whole-brain imaging using the AZBA atlas (Kenney et al. eLife) and cfos mapping coupled with multivariate analysis revealed that although all fish reengaged telencephalic regions during recall, high-freezing phenotypes uniquely recruited cerebellar, preglomerular, and pretectal nuclei, whereas mixed evasion-freezing fish showed preferential activation of preoptic and hypothalamic areas - a finding that lays the groundwork for dissecting the distributed neural substrates of associative fear in zebrafish.

Strengths:

The strengths of the study lie in the use of zeberarish and the innovative behavioral, modeling, and brain imaging tools applied to address this question. The question of how brain-wide activity correlates with variations in fear behavior is fundamental, and arguably, this system is the only system that could be used to address this. The statistics are appropriate, and the study is well reasoned. Overall, I like this manuscript very much and think it adds invaluable information to the field of fear/anxiety.

Weaknesses:

I have a few questions and suggestions.

(1) The three-day contextual fear paradigm, as implemented - one CAS pairing on day 2 followed by a single recall test on day 3 - inevitably conflates acquisition and long-term memory, making it impossible to know whether strains like TU truly recall the association poorly or simply learn it more slowly. For example, given that TU fish extinguish fear faster than AB or TL strains in extended protocols, they may simply require additional or repeated CAS pairings to achieve the same asymptotic performance. To disentangle learning kinetics from recall strength, the assay could be revised to include multiple acquisition trials (e.g., conditioning on two or more consecutive days) with an immediate post-conditioning probe to assess acquisition independent of consolidation, and continuous measurement of freezing and evasive behaviors across each trial to fit learning curves for each strain. Such refinements - even if on a subset of the strains - would reveal whether "non-reactive" phenotypes reflect genuine recall deficits or merely delayed acquisition.

(2) My second major question is with respect to Figure 3 panel B. This is a complex figure, and I can understand the gist of what the authors are attempting to show, but it is difficult to understand as it is. Can this be represented in a way that is clearer and explained a bit more easily?

(3) The brain mapping is by far one of the most interesting aspects of this study, and the methods that the group used are interesting. The brain mapping, however, relies on generating "contrasting" groups (Figure 6A), and I was not clear as to how these two groups were formed. Could the authors elaborate a bit?

Reviewer #1 (Public review):

Summary:

In this study, the authors present a thorough mechanistic study of the J-domain protein Apj1 in Saccharomyces cerevisiae, establishing it as a key repressor of Hsf1 during the attenuation phase of the heat shock response (HSR). The authors integrate genetic, transcriptomic (ribosome profiling), biochemical (ChIP, Western), and imaging data to dissect how Apj1, Ydj1 and Sis1 modulate Hsf1 activity under stress and non-stress conditions. The work proposes a model where Apj1 specifically promotes displacement of Hsf1 from DNA-bound heat shock elements, linking nuclear PQC to transcriptional control.

Strengths:

Overall, the work is highly novel-this is the first detailed functional dissection of Apj1 in Hsf1 attenuation. It fills an important gap in our understanding of how Hsf1 activity is fine-tuned after stress induction, with implications for broader eukaryotic systems. I really appreciate the use of innovative techniques including ribosome profiling and time-resolved localization of proteins (and tagged loci) to probe Hsf1 mechanism. The overall proposed mechanism is compelling and clear-the discussion proposes a phased control model for Hsf1 by distinct JDPs, with Apj1 acting post-activation, while Sis1 and Ydj1 suppress basal activity.

The manuscript is well-written and will be exciting for the proteostasis field and beyond.

Comments on revised version:

The authors have addressed all my concerns,

Reviewer #2 (Public review):

Summary:

Overall, the work is exceptionally well done and controlled and the results properly and appropriately interpreted. While several of the approaches, while powerful, are somewhat indirect (i.e., following gene expression via ribosomal profiling) additional experiments utilizing traditional gene expression assays added in revision combine to ultimately provide a compelling answer to the main questions being asked.

The key finding from this work is the discovery that Apj1 regulates Hsf1 attenuation in a manner that includes Hsp70. That finding is strongly supported by the experimental data. While it would be ideal to also demonstrate Apj1-controlled differential binding of Ssa1/2 to Hsf1 at either the N- or C-terminal binding sites during attenuation, the Hsp70-Hsf1 interactions are difficult to reproducibly assess in cell extracts and are likely beyond the scope of this study. However, this work paves the way in the future for potential biochemical reconstitution assays that could elucidate both Hsp70-Hsf1 interactions as well as the distinct JDP-Hsf1 interactions reported here.

This discovery raises additional new questions about JDP specificity in HSR regulation and the role of JDPs in navigating protein aggregation and sensing of proteostatic challenge in the nucleus, thus advancing the field and opening new, exciting avenues for exploration.

Reviewer #3 (Public review):

Summary:

The heat shock response (HSR) is an inducible transcriptional program that has provided paradigmatic insight into how stress cues feed information into the control of gene expression. The recent elucidation that the chaperone Hsp70 controls the DNA binding activity of the central HSR transcription factor Hsf1 by direct binding has spurred the question how such a general chaperone obtains specificity. This study has addressed the next logical question, how J-domain proteins execute this task in budding yeast, the leading cell model for studying the HSR. While an involvement and in part overlapping function of general class A and B J-domain proteins, Ydj1 and Sis1 are indicated by the genetic analysis a highly specific role for the class A Apj1 in displacing Hsf1 from the promoters is found unveiling specificity in the system.

Strengths

The central strong point of the paper is the identification of class A J-domain protein Apj1 as a specific regulator of the attenuation of the HSR by removing Hsf1 from HSEs at the promoters. The genetic evidence and the ChIP data strongly support this claim. This identification of a specific role for a lowly expressed nuclear J-domain protein changes how the wiring of the HSR should be viewed. It also raises important questions regarding the model of chaperone titration, the concept that a chaperone with limiting availability is involved in a thug of war involving competing interactions with misfolded protein substrates and regulatory interactions with Hsf1. Perhaps Apj1 with its low levels and interactions with misfolded and aggregated proteins in the nucleus is the titrated Hsp70 (co)chaperone that determines the extent of the HSR? This would mean that Apj1 is at the nexus of the chaperone titration mechanism. Although Apj1 is not a highly conserved J domain protein among eukaryotes the strength of the study is that is provides a conceptual framework for what may be required for chaperone titration in other eukaryotes: One or more nuclear J-domain proteins with low nuclear levels that has an affinity for Hsf1 and that can become limiting due to interactions with misfolded Hsp70 proteins. The provides a pathway for how these may be identified using for example ChIP-seq.

Weakness

A built-in challenge when studying the mechanism of the HSR is the general role of Hsp70 chaperone system and its J domain proteins. Indeed, a weakness of the study is that it is unclear what of the phenotypic effects have to do with directly recruiting Hsp70 to Hsf1 dependent on a J domain protein and what instead is an indirect effect of protein misfolding caused by the mutation. This interpretation problem is clearly and appropriately dealt with in the manuscript text and in experiments but is of such fundamental nature that it cannot easily be fully ruled out.

Reviewer #1 (Public review):

Summary:

This manuscript from Jones and colleagues investigates a previously described phenomenon in which P. falciparum malaria parasites display increased trafficking of proteins displayed on the surface of infected RBCs, as well as increased cytoadherence in response to febrile temperatures. While this parasite response was previously described, it was not uniformly accepted, and conflicting reports can be found in the literature. This variability likely arises due to differences in the methods employed and the degree of temperature increase to which the parasites were exposed. Here, the authors are very careful to employ a temperature shift that likely reflects what is happening in infected humans and that they demonstrate is not detrimental to parasite viability or replication. In addition, they go on to investigate what steps in protein trafficking are affected by exposure to increased temperature and show that the effect is not specific to PfEMP1 but rather likely affects all transmembrane domain-containing proteins that are trafficked to the RBC. They also detect increased rates of phosphorylation of trafficked proteins, consistent with overall increased protein export.

Strengths:

The authors used a relatively mild increase in temperature (39 degrees), which they demonstrate is not detrimental to parasite viability or replication. This enabled them to avoid potential complications of a more severe heat shock that might have affected previously published studies. They employed a clever method of fractionation of RBCs infected with a var2csa-nanoluc fusion protein expressing parasite line to determine which step in the export pathway was likely accelerating in response to increased temperature. This enabled them to determine that export across the PVM is being affected. They also explored changes in phosphorylation of exported proteins and demonstrated that the effect is not limited to PfEMP1 but appears to affect numerous (or potentially all) exported transmembrane domain-containing proteins.

Weaknesses:

All the experiments investigating changes resulting from increased temperature were conducted after an increase in temperature from 16 to 24 hours, with sampling or assays conducted at the 24 hr mark. While this provided consistency throughout the study, this is a time point relatively early in the export of proteins to the RBC surface, as shown in Figure 1E. At 24 hrs, only approximately 50% of wildtype parasites are positive for PfEMP1, while at 32 hrs this approaches 80%. Since the authors only checked the effect of heat stress at 24 hrs, it is not possible to determine if the changes they observe reflect an overall increase in protein trafficking or instead a shift to earlier (or an accelerated) trafficking. In other words, if a second time point had been considered (for example, 32 hrs or later), would the parasites grown in the absence of heat stress catch up?

Reviewer #2 (Public review):

This manuscript describes experiments characterising how malaria parasites respond to physiologically relevant heat-shock conditions. The authors show, quite convincingly, that moderate heat-shock appears to increase cytoadherance, likely by increasing trafficking of surface proteins involved in this process.

While generally of a high quality and including a lot of data, I have a few small questions and comments, mainly regarding data interpretation.

(1) The authors use sorbitol lysis as a proxy for trafficking of PSAC components. This is a very roundabout way of doing things and does not, I think, really show what they claim. There could be a myriad of other reasons for this increased activity (indeed, the authors note potential PSAC activation under these conditions). One further reason could be a difference in the membrane stability following heat shock, which may affect sorbitol uptake, or the fragility of the erythrocytes to hypotonic shock. I really suggest that the authors stick to what they show (increased PSAC) without trying to use this as evidence for increased trafficking of a number of non-specified proteins that they cannot follow directly.

(2) Supplementary Figure 6C/D: The KAHRP signal does not look like it should. In fact, it doesn't look like anything specific. The HSP70-X signal is also blurry and overexposed. These pictures cannot be used to justify the authors' statements about a lack of colocalisation in any way.

(3) Figure 6: This experiment confuses me. The authors purport to fractionate proteins using differential lysis, but the proteins they detect are supposed to be transmembrane proteins and thus should always be found associated with the pellet, whether lysis is done using equinatoxin or saponin. Have they discovered a currently unknown trafficking pathway to tell us about? Whilst there is a lot of discussion about the trafficking pathways for TM proteins through the host cell, a number of studies have shown that these proteins are generally found in a membrane-bound state. The authors should elaborate, or choose an experiment that is capable of showing compartment-specific localisation of membrane-bound proteins (protease protection, for example).

(4) The red blood cell contains, in addition to HSP70-X, a number of human HSPs (HSP70 and HSP90 are significant in this current case). As the name suggests, these proteins non-specifically shield exposed hydrophobic domains revealed upon partial protein unfolding following thermal insult. I would thus have expected to find significantly more enrichment following heat shock, but this is not the case. Is it possible that the physiological heat shock conditions used in this current study are not high enough to cause a real heat shock?

Reviewer #3 (Public review):

Summary:

In this paper, it is established that high fever-like 39{degree sign}C temperatures cause parasite-infected red blood cells to become stickier. It is thought that high temperatures might help the spleen to destroy parasite-infected cells, and they become stickier in order to remain trapped in blood vessels, so they stop passing through the spleen.

Strengths:

The strength of this research is that it shows that fever-like temperatures can cause parasite-infected red blood cells to stick to surfaces designed to mimic the walls of small blood vessels. In a natural infection, this would cause parasite-infected red blood cells to stop circulating through the spleen, where the parasites would be destroyed by the immune system. It is thought that fevers could lead to infected red blood cells becoming stiffer and therefore more easily destroyed in the spleen. Parasites respond to fevers by making their red blood cells stickier, so they stop flowing around the body and into the spleen. The experiments here prove that fever temperatures increase the export of Velcro-like sticky proteins onto the surface of the infected red blood cells and are very thorough and convincing.

Weaknesses:

A minor weakness of the paper is that the effects of fever on the stiffness of infected red blood cells were not measured. This can be easily done in the laboratory by measuring how the passage of infected red blood cells through a bed of tiny metal balls is delayed under fever-like temperatures.

Reviewer #1 (Public review):

Summary:

In this article, Almeida and colleagues use a combination of NMR and ITC to study the interaction of the EBH domain of microtubule end-binding protein 1 (EB1) with SxIP peptides derived from the MACF plus-end tracking protein. EBH forms a dimer and in isolation has previously been shown to have a disordered C-terminal tail. Here, the authors use NMR to determine a solution structure of the EBH dimer bound to 11-mer SxIP peptides derived from MACF, and observe that the disordered C-terminal of EBH is recruited by residues C-terminal to the SxIP motif to fold into the final complex. By comparison of binding in different length peptides, and of EBH lacking the C-terminal tail, they show that these additional contacts increase binding affinity by an order of magnitude, greatly stabilising the interaction, in a binding mode they term 'dock-and-lock'.

The authors also use their new structural knowledge to design peptides with higher affinities, and show in a cell model that these can be weakly recruited to microtubule ends - although a dimeric construct is necessary for efficient recruitment. Ultimately, by demonstrating the feasibility of targeting these proteins, this work points towards the possibility of designing small-molecules to block the interactions.

Reviewer #2 (Public review):

Summary:

The C-terminal region of EB1 is responsible for protein-protein interactions, thereby recruiting the binding partners of EB1 to microtubules; the coiled-coil region (EBH) and the acidic tail are critical for their binding partners. The authors demonstrated by using NMR that the binding mode of EBH with the SxIP motif, which is a two-step process termed "dock-and-lock". The ITC analysis supports the results obtained from NMR. The initial version of the manuscript contained ambiguities on the ITC data; however, the results of the revised manuscript are convincing and support the two-step binding model.

Strength:

The authors propose a novel model of "dock-and-lock" by using multiple methods of NMR, ITC and cell biology.

Reviewer #1 (Public review):

This paper presents a computational model of the evolution of two different kinds of helping ("work," presumably denoting provisioning, and defense tasks) in a model inspired by cooperatively breeding vertebrates. The helpers in this model are a mix of previous offspring of the breeder and floaters that might have joined the group, and can either transition between the tasks as they age or not. The two types of help have differential costs: "work" reduces "dominance value," (DV), a measure of competitiveness for breeding spots, which otherwise goes up linearly with age, but defense reduces survival probability. Both eventually might preclude the helper from becoming a breeder and reproducing. How much the helpers help, and which tasks (and whether they transition or not), as well as their propensity to disperse, are all evolving quantities. The authors consider three main scenarios: one where relatedness emerges from the model, but there is no benefit to living in groups, one where there is no relatedness, but living in larger groups gives a survival benefit (group augmentation, GA), and one where both effects operate. The main claim is that evolving defensive help or division of labor requires the group augmentation; it doesn't evolve through kin selection alone in the authors' simulations.

This is an interesting model, and there is much to like about the complexity that is built in. Individual-based simulations like this can be a valuable tool to explore the complex interaction of life history and social traits. Yet, models like this also have to take care of both being very clear on their construction and exploring how some of the ancillary but potentially consequential assumptions affect the results, including robust exploration of the parameter space. I think the current manuscript falls short in these areas, and therefore, I am not yet convinced of the results.

In this round, the authors provided some clarity, but some questions still remain, and I remain unconvinced by a main assumption that was not addressed.

Based on the authors' response, if I understand the life history correctly, dispersers either immediately join another group (with 1-the probability of dispersing), or remain floaters until they successfully compete for a breeder spot or die? Is that correct? I honestly cannot decide because this seems implicit in the first response but the response to my second point raises the possibility of not working while floating but can work if they later join a group as a subordinate. If it is the case that floaters can have multiple opportunities to join groups as subordinates (not as breeders; I assume that this is the case for breeding competition), this should be stated, and more details about how.

So there is still some clarification to be done, and more to the point, the clarification that happened only happened in the response. The authors should add these details to the main text. Currently, the main text only says vaguely that joining a group after dispersing " is also controlled by the same genetic dispersal predisposition" without saying how.

In response to my query about the reasonableness of the assumption that floaters are in better condition (in the KS treatment) because they don't do any work, the authors have done some additional modeling but I fail to see how that addresses my point. The additional simulations do not touch the feature I was commenting on, and arguably make it stronger (since assuming a positive beta_r -which btw is listed as 0 in Table 1- would make floaters on average be even more stronger than subordinates). It also again confuses me with regard to the previous point, since it implies that now dispersal is also potentially a lifetime event. Is that true?

Meanwhile, the simplest and most convincing robustness check, which I had suggested last round, is not done: simply reduce the increase in the R of the floater by age relative to subordinates. I suspect this will actually change the results. It seems fairly transparent to me that an average floater in the KS scenario will have R about 15-20% higher than the subordinates (given no defense evolves, y_h=0.1 and H_work evolves to be around 5, and the average lifespan for both floaters and subordinates are in the range of 3.7-2.5 roughly, depending on m). That could be a substantial advantage in competition for breeding spots, depending on how that scramble competition actually works. I asked about this function in the last round (how non-linear is it?) but the authors seem to have neglected to answer.

More generally, I find that the assumption (and it is an assumption) floaters are better off than subordinates in a territory to be still questionable. There is no attempt to justify this with any data, and any data I can find points the other way (though typically they compare breeders and floaters, e.g.: https://bioone.org/journals/ardeola/volume-63/issue-1/arla.63.1.2016.rp3/The-Unknown-Life-of-Floaters--The-Hidden-Face-of/10.13157/arla.63.1.2016.rp3.full concludes "the current preliminary consensus is that floaters are 'making the best of a bad job'."). I think if the authors really want to assume that floaters have higher dominance than subordinates, they should justify it. This is driving at least one and possibly most of the key results, since it affects the reproductive value of subordinates (and therefore the costs of helping).

Regarding division of labor, I think I was not clear so will try again. The authors assume that the group reproduction is 1+H_total/(1+H_total), where H_total is the sum of all the defense and work help, but with the proviso that if one of the totals is higher than "H_max", the average of the two totals (plus k_m, but that's set to a low value, so we can ignore it), it is replaced by that. That means, for example, if total "work" help is 10 and "defense" help is 0, total help is given by 5 (well, 5.1 but will ignore k_m). That's what I meant by "marginal benefit of help is only reduced by a half" last round, since in this scenario, adding 1 to work help would make total help go to 5.5 vs. adding 1 to defense help which would make it go to 6. That is a pretty weak form of modeling "both types of tasks are necessary to successfully produce offspring" as the newly added passage says (which I agree with), since if you were getting no defense by a lot of food, adding more food should plausibly have no effect on your production whatsoever (not just half of adding a little defense). This probably explains why often the "division of labor" condition isn't that different than the no DoL condition.

Reviewer #2 (Public review):

Summary:

This paper formulates an individual-based model to understand the evolution of division of labor in vertebrates. The model considers a population subdivided in groups, each group has a single asexually-reproducing breeder, other group members (subordinates) can perform two types of tasks called "work" or "defense", individuals have different ages, individuals can disperse between groups, each individual has a dominance rank that increases with age, and upon death of the breeder a new breeder is chosen among group members depending on their dominance. "Workers" pay a reproduction cost by having their dominance decreased, and "defenders" pay a survival cost. Every group member receives a survival benefit with increasing group size. There are 6 genetic traits, each controlled by a single locus, that control propensities to help and disperse, and how task choice and dispersal relate to dominance. To study the effect of group augmentation without kin selection, the authors cross-foster individuals to eliminate relatedness. The paper allows for the evolution of the 6 genetic traits under some different parameter values to study the conditions under which division of labour evolves, defined as the occurrence of different subordinates performing "work" and "defense" tasks. The authors envision the model as one of vertebrate division of labor.

The main conclusion of the paper is that group augmentation is the primary factor causing the evolution of vertebrate division of labor, rather than kin selection. This conclusion is drawn because, for the parameter values considered, when the benefit of group augmentation is set to zero, no division of labor evolves and all subordinates perform "work" tasks but no "defense" tasks.

Strengths:

The model incorporates various biologically realistic details, including the possibility to evolve age polytheism where individuals switch from "work" to "defence" tasks as they age or vice versa, as well as the possibility of comparing the action of group augmentation alone with that of kin selection alone.

Weaknesses:

The model and its analysis is limited, which makes the results insufficient to reach the main conclusion that group augmentation and not kin selection is the primary cause of the evolution of vertebrate division of labor. There are several reasons.

First, the model strongly restricts the possibility that kin selection is relevant. The two tasks considered essentially differ only by whether they are costly for reproduction or survival. "Work" tasks are those costly for reproduction and "defense" tasks are those costly for survival. The two tasks provide the same benefits for reproduction (eqs. 4, 5) and survival (through group augmentation, eq. 3.1). So, whether one, the other, or both tasks evolve presumably only depends on which task is less costly, not really on which benefits it provides. As the two tasks give the same benefits, there is no possibility that the two tasks act synergistically, where performing one task increases a benefit (e.g., increasing someone's survival) that is going to be compounded by someone else performing the other task (e.g., increasing that someone's reproduction). So, there is very little scope for kin selection to cause the evolution of labour in this model. Note synergy between tasks is not something unusual in division of labour models, but is in fact a basic element in them, so excluding it from the start in the model and then making general claims about division of labour is unwarranted. I made this same point in my first review, although phrased differently, but it was left unaddressed.

Second, the parameter space is very little explored. This is generally an issue when trying to make general claims from an individual-based model where only a very narrow parameter region has been explored of a necessarily particular model. However, in this paper, the issue is more evident. As in this model the two tasks ultimately only differ by their costs, the parameter values specifying their costs should be varied to determine their effects. Instead, the model sets a very low survival cost for work (yh=0.1) and a very high survival cost for defense (xh=3), the latter of which can be compensated by the benefit of group augmentation (xn=3). Some very limited variation of xh and xn is explored, always for very high values, effectively making defense unevolvable except if there is group augmentation. Hence, as I stated in my previous review, a more extensive parameter exploration addressing this should be included, but this has not been done. Consequently, the main conclusion that "division of labor" needs group augmentation is essentially enforced by the limited parameter exploration, in addition to the first reason above.

Third, what is called "division of labor" here is an overinterpretation. When the two tasks evolve, what exists in the model is some individuals that do reproduction-costly tasks (so-called "work") and survival-costly tasks (so-called "defense"). However, there are really no two tasks that are being completed, in the sense that completing both tasks (e.g., work and defense) is not necessary to achieve a goal (e.g., reproduction). In this model there is only one task (reproduction, equation 4,5) to which both "tasks" contribute equally and so one task doesn't need to be completed if the other task compensates for it. So, this model does not actually consider division of labor.

Reviewer #1 (Public review):

Jiang et al. present a measure of phenological lag by quantifying the effects of abiotic constraints on the differences between observed and expected phenological changes, using a combination of previously published phenology change data for 980 species, and associated climate data for study sites. They found that, across all samples, observed phenological responses to climate warming were smaller than expected responses for both leafing and flowering spring events. They also show that data from experimental studies included in their analysis exhibited increased phenological lag compared to observational studies, possibly as a result of reduced sensitivity to climatic changes. Furthermore, the authors present evidence that spatial trends in phenological responses to warming may differ than what would be expected from phenological sensitivity, due to the seasonal timing of when warming occurs. Thus, climate change may not result in geographic convergences of phenological responses. This study presents an interesting way to separate the individual effects of climate change and other abiotic changes on the phenological responses across sites and species.

Strengths:

A straightforward mathematical definition of phenological lag allows for this method to potentially be applied in different geographic contexts. Where data exists, other researchers can partition the effects of various abiotic forcings on phenological responses that differ from those expected from warming sensitivity alone.

Identifying phenological lag, and associated contributing factors, provides a method by which more nuanced predictions of phenological responses to climate change can be made. Thus, this study could improve ecological forecasting models.

Weaknesses:

The analysis here could be more robust. A more thorough examination of phenological lag would provide stronger evidence that the framework presented has utility. The differences in phenologica lag by study approach, species origin, region, and growth form are interesting, and could be expanded. For example, the authors have the data to explore the relationships between phenological lag and the quantitative variables included in the final model (altitude, latitude, mean annual temperature) and other spatial or temporal variables. This would also provide stronger evidence for the author's claims about potential mechanisms that contribute to phenological lag.

The authors include very little data visualizations, and instead report results and model statistics in tables. This is difficult to interpret and may obscure underlying patterns in the data. Including visual representations of variable distributions and between-variable relationships, in addition to model statistics, provides stronger evidence than model statistics alone.

Reviewer #3 (Public review):

Summary:

The authors developed a new phenological lag metric and applied this analytical framework to a global dataset to synthesize shifts in spring phenology and assess how abiotic constraints influence spring phenology.

Strengths:

The dataset developed in this study is extensive, and the phenological lag metric is valuable.

Weaknesses:

The stability of the method used in this study needs improvement, particularly in the calculation of forcing requirements. In addition, the visualization of the results (such as Table 1) should be enhanced.

Reviewer #1 (Public review):

This work provides a new Python toolkit for combining generative modeling of neural dynamics and inversion methods to infer likely model parameters that explain empirical neuroimaging data. The authors provided tests to show the toolkit's broad applicability, accuracy, and robustness; hence, it will be very useful for people interested in using computational approaches to better understand the brain.

Strengths:

The work's primary strength is the tool's integrative nature, which seamlessly combines forward modelling with backward inference. This is important as available tools in the literature can only do one and not the other, which limits their accessibility to neuroscientists with limited computational expertise. Another strength of the paper is the demonstration of how the tool can be applied to a broad range of computational models popularly used in the field to interrogate diverse neuroimaging data, ensuring that the methodology is not optimal to only one model. Moreover, through extensive in-silico testing, the work provided evidence that the tool can accurately infer ground-truth parameters even in the presence of noise, which is important to ensure results from future hypothesis testing are meaningful.

Weaknesses

The paper still lacks appropriate quantitative benchmarking relative to non-Bayesian-based inference tools, especially with respect to performance accuracy and computational complexity and efficiency. Without this benchmarking, it is difficult to fully comprehend the power of the software or its ability to be extended to contexts beyond large-scale computational brain modelling.

Reviewer #2 (Public review):

Summary:

Whole-brain network modeling is a common type of dynamical systems-based method to create individualized models of brain activity incorporating subject-specific structural connectome inferred from diffusion imaging data. This type of model has often been used to infer biophysical parameters of the individual brain that cannot be directly measured using neuroimaging but may be relevant to specific cognitive functions or diseases. Here, Ziaeemehr et al introduce a new toolkit, named "Virtual Brain Inference" (VBI), offering a new computational approach for estimating these parameters using Bayesian inference powered by artificial neural networks. The basic idea is to use simulated data, given known parameters, to train artificial neural networks to solve the inverse problem, namely, to infer the posterior distribution over the parameter space given data-derived features. The authors have demonstrated the utility of the toolkit using simulated data from several commonly used whole-brain network models in case studies.

Strength:

- Model inversion is an important problem in whole-brain network modeling. The toolkit presents a significant methodological step up from common practices, with the potential to broadly impact how the community infers model parameters.<br /> - Notably, the method allows the estimation of the posterior distribution of parameters instead of a point estimation, which provides information about the uncertainty of the estimation, which is generally lacking in existing methods.<br /> - The case studies were able to demonstrate the detection of degeneracy in the parameters, which is important. Degeneracy is quite common in this type of models. If not handled mindfully, they may lead to spurious or stable parameter estimation. Thus, the toolkit can potentially be used to improve feature selection or to simply indicate the uncertainty.<br /> - In principle, the posterior distribution can be directly computed given new data without doing any additional simulation, which could improve the efficiency of parameter inference on the artificial neural network is well-trained.

Weaknesses:

- The z-scores used to measure prediction error are generally between 1-3, which seems quite large to me. It would give readers a better sense of the utility of the method if comparisons to simpler methods, such as k-nearest neighbor methods, are provided in terms of accuracy.<br /> - A lot of simulations are required to train the posterior estimator, which is computationally more expensive than existing approaches. Inferring from Figure S1, at the required order of magnitudes of the number of simulations, the simulation time could range from days to years, depending on the hardware. The payoff is that once the estimator is well-trained, the parameter inversion will be very fast given new data. However, it is not clear to me how often such use cases would be encountered. It would be very helpful if the authors could provide a few more concrete examples of using trained models for hypothesis testing, e.g., in various disease conditions.

Reviewer #1 (Public review):

Summary:

Ramirez Carbo et al. use the powerful M. xanthus spore morphogenesis model to address fundamental mechanisms in coordinated peptidoglycan remodeling and degradation. As peptidoglycan is an essential macromolecule and difficult to study in vivo, the authors use indirect but important methodology. The authors first identify two lytic transglycosylase (Ltg) enzymes necessary for spore morphogenesis using mutant phenotypic studies. They characterize these mutants for their role in coordinating spore morphogenesis induced either in fruiting bodies (starvation-dependent) or in liquid-rich media conditions (chemical-dependent). They conclude from these phenotypic and epistatic analyses that LtgA is necessary for morphogenesis during chemical-induced sporulation, and LtgB appears to be necessary to coordinate LtgA activity by interfering with LtgA function. Under starvation-induced sporulation, the absence of LtgB interferes with the building of fruiting bodies. LtgA does not appear to play a primary role in promoting aggregation into fruiting bodies, nor in degradation of peptidoglycan as assayed by loss of signal in anti-PG immunofluorescence. The authors demonstrate that the purified periplasmic domain of LtgA is highly active in degrading purified PG sacculi in vitro, while that of LtgB is highly reduced (relative to LtgA or lysozyme). The authors use photoactivated mCherry Lyt fusions and PALM to track the fusion protein mobility, which they state correlates with activity as immobilization results from PG binding. They demonstrate that in vegetative cells, a greater proportion of LtgA-PAmCh is more immobile (more active) than LtgB-PAmCh, but that directly after chemical-induction of sporulation, LtgB-PAmCh becomes more immobile (active). These analyses in the partner mutant backgrounds suggest that LtgA-PAmCh is more immobile (less active) in the absence of LtgB, but the reverse is not observed. Finally, the authors demonstrate that overexpression of LtgA in vegetative conditions leads to cell rounding, likely because of uncontrolled PG degradation, while overexpression of LtgB displays no phenotype.

Strengths:

This paper capitalizes on a novel spore morphogenesis mechanism to define proteins and mechanisms involved in peptidoglycan reorganization. The authors use the powerful PALM microscopy technique to assess Ltg activity in vivo by assaying for immobility as a proxy for PG binding. The authors elucidate a novel mechanism by which two Ltg's function together- with one (LtgB) seeming to regulate the activity of the other (the primary Ltg).

Despite some weaknesses, there is no question that this study provides important insight into mechanisms of peptidoglycan remodeling- a difficult but highly impactful area of study with implications for the development of novel therapeutics and the discovery of mechanisms of fundamental bacterial physiology.

Weaknesses:

In many places, the authors do not adequately justify interpretations of their assays, leading to some apparently unjustified conclusions. Many of these are minor and may just require citations to demonstrate that the interpretations are justified by previous studies (detailed in recommendations below), but two bigger concerns are as follows:

(1) It is not clear how the muropeptides listed in Figure 1 were assigned, and it is missing in the methods. In the sporulating conditions, the spectra look like combinations of multiple peaks, and the data, as stated, is not convincing to the non-specialist eye.

(2) The observation that the lytB mutant prevents appropriate aggregation into fruiting bodies does not allow the interpretation that the absence of LytB prevents PG morphogenesis in the starvation-induced sporulation pathway, per se. It is more likely that in the lytB mutant, the morphogenesis program is not even triggered. This is because signaling proteins and regulators (specifically, C-signal accumulation/activated FruA), which are dependent on increased cell-cell signaling in the fruiting body, do not accumulate appropriately in shallow aggregates. C-signal/FruA are necessary to trigger the sporulation program in FBs. BTW: A hypothesis to explain the indirect effect of ltgB absence on aggregation could be that UDP-precursors are not regulated appropriately (unregulated LtyA??), so polysaccharides necessary for motility are not properly produced.

Along these lines, fruiting body formation does not equal sporulation, and even "darkened" fruiting bodies can be misleading, as some mutants form polysaccharide-rich fruiting bodies (that appear dark under certain light conditions in the stereomicroscope) but do not sporulate efficiently. The wording in the text suggests that the authors assume that sporulation levels are normal because fruiting bodies are produced (see specific comments for details).

(3) The authors repeatedly state that production of spore coat polysaccharides likely affects the PG IP staining (see below), but this is not well justified. A citation is needed if this has already been directly shown, or the language needs to be softened.

(4) Better justification for the immobility of Lyt proteins in vivo as an assay for activity may be required. If this is well known in the field, it should be explicitly stated. The authors address this better in the discussion - but still state it is a correlation.

Reviewer #2 (Public review):

Summary:

The authors' initial goal was to demonstrate loss of PG during the slow sporulation process of Myxococcus xanthus, with examination of the PG degradation products in order to implicate possible enzymes involved. Upon finding a predominance of LGT products, they examined sporulation in strains lacking each of the 14 candidate LGTs encoded in the genome, leading to the identification of two sporulation-linked LGTs. An extensive characterization of the roles played by these LGTs. One LGT is responsible for the slow sporulation PG degradation, while another is required for the rapid sporulation process. Interestingly, the "slow" LGT seems to provide an important regulatory brake on the rapid enzyme. Single-molecule fluorescent tracking of these enzymes was used to develop a model for their interaction with PG that mimics their observed activity. The rate of PG synthesis activity was also shown to impact the rate of PG degradation, suggesting potential interplay between the synthetic and degradative enzymes.

Strengths:

The genetic analysis to identify sporulation-linked LGTs and their effects on growth, sporulation, and spore properties was well done and productive. The fluorescence microscopy to track LGT mobility, presumably tied to activity, produced a convincing argument about the mechanism of regulation of one LGT by another.

Weaknesses:

While the impact of LGTs on sporulation was clearly demonstrated, the PG analysis that resulted from the study of LGTs raised some important unanswered questions. The analyses suggest that the PG is degraded to quite small fragments, which would normally be lost during the purification of PG. How these small fragments were thus detected is unclear, and this suggests a more complex story concerning PG metabolism during sporulation. An anti-PG antibody is used to quantify PG in the spores, but it is not made clear what the specificity of this antibody is, and thus whether it would recognize the LGT-altered PG of the spore. The authors suggest a "new mechanism of sporulation" when they have actually simply identified an important factor (PG degradation by LGTs) within a complex "process of sporulation".

Reviewer #1 (Public review):

Summary:

In this manuscript, Chen et al. use cryo-electron tomography and an in vitro reconstitution system to demonstrate that the autoinhibited form of LRRK2 can assemble into filaments that wrap around microtubules. These filaments are generally shorter and less ordered than the previously characterized active-LRRK2 filaments. The structure reveals a novel interface involving the N-terminal repeats, which were disordered in the earlier active filament structure. Additionally, the autoinhibited filaments exhibit distinct helical parameters compared to the active form.

Strengths:

This study presents the highest-resolution structure of LRRK2 filaments obtained via subtomogram averaging, marking a significant technical advance over the authors' previous work published in Cell. The data are well presented, with high-quality visualizations, and the findings provide meaningful insights into the structural dynamics of LRRK2.

Weaknesses and Suggestions:

The revised manuscript by Chen et al. has fully addressed all of my previous suggestions regarding the rearrangement of the main figures.

Reviewer #2 (Public review):

The authors of this paper have done much pioneering work to decipher and understand LRRK2 structure and function and uncover the mechanism by which LRRK2 binds to microtubules and to study the roles that this may play in biology. Their previous data demonstrated that LRRK2 in the active conformation (pathogenic mutation or Type I inhibitor complex) bound to microtubule filaments in an ordered helical arrangement. This they showed induced a "roadblock" in the microtubule impacting vesicular trafficking. The authors have postulated that this is a potentially serious flaw with Type 1 inhibitors and that companies should consider generating Type 2 inhibitors in which the LRRK2 is trapped in the inactive conformation. Indeed the authors have published much data that LRRK2 complexed to Type 2 inhibitors does not seem to associate with microtubules and cause roadblocks in parallel experiments to those undertaken with type 1 inhibitors published above.

In the current study the authors have undertaken an in vitro reconstitution of microtubule bound filaments of LRRK2 in the inactive conformation, which surprisingly revealed that inactive LRRK2 can also interact with microtubules in its auto-inhibited state. The authors' data shows that while the same interphases are seen with both the active LRRK2 and inactive microtubule bound forms of LRRK2, they identified a new interphase that involves the WD40-ARM-ANK- domains that reportedly contributes to the ability of the inactive form of LRRK2 to bind to microtubule filaments. The structures of the inactive LRRK2 complexed to microtubules are of medium resolution and do not allow visualisation of side chains.

This study is extremely well written and the figures incredibly clear and well presented. The finding that LRRK2 in the inactive autoinhibited form can associate with microtubules is an important observation that merits further investigation. This new observation makes an important contribution to the literature and builds upon the pioneering research that this team of researchers has contributed to the LRRK2 fields.

Comments on revised version:

The authors have adequately addressed my questions and those of the other Reviewers in my opinion.

Reviewer #3 (Public review):

Summary:

The manuscript by Chen et al examines the structure of the inactive LRRK2 bound to microtubules using cryo-EM tomography. Mutations in this protein have been shown to be linked to Parkinson's Disease. It is already shown that the active-like conformation of LRRK2 binds to the MT lattice, but this investigation shows that full-length LRRk2 can oligomerize on MTs in its autoinhibited state with different helical parameters than were observed with active-like state. The structural studies suggest that the autoinhibited state is less stable on MTs.

Strengths:

The protein of interest is very important biomedically and a novel conformational binding to microtubules in proposed

The authors have addressed my original critique.

Reviewer #1 (Public review):

This study examined the effect of blood pressure variability on brain microvascular function and cognitive performance. By implementing a model of blood pressure variability using intermittent infusion of AngII for 25 days, the authors examined different cardiovascular variables, cerebral blood flow and cognitive function during midlife (12-15-month-old mice). Key findings from this study demonstrate that blood pressure variability impairs baroreceptor reflex and impairs myogenic tone in brain arterioles, particularly at higher blood pressure. They also provide evidence that blood pressure variability blunts functional hyperemia and impairs cognitive function and activity. Simultaneous monitoring of cardiovascular parameters, in vivo imaging recordings, and the combination of physiological and behavioral studies reflect rigor in addressing the hypothesis. The experiments are well designed, and data generated are clear.

A number of issues raised earlier were addressed by the authors in the revised manuscript. The responses are convincing. These included circadian rhythm considerations, baroreflex findings, BP fluctuations driven by animal movement, and data presentation.

Overall, this is a solid study with huge physiological implications. I believe that it will be of great benefit to the field.

Reviewer #1 (Public review):

Summary:

Meijer et al. sought to investigate the role of cortical layer 6b (L6b) neurons in modulating sleep-wake states and cortical oscillations under baseline and sleep deprived conditions and in response to orexin A and B. Using chronic EEG recordings in mice with silencing of Drd1a+ neurons (via constitutive Cre-dependent knockout of SNAP25), the authors report that while overall baseline sleep-wake architecture and response to sleep deprivation minimal/unchanged, "L6b silencing" leads to a slowing of theta activity during wakefulness and REM sleep, and a reduction in EEG power during NREM sleep. Additionally, orexin B-induced increases in theta activity were attenuated in L6b silenced mice, which the authors state suggests a modulatory role for L6b in orexin-mediated arousal regulation. The manuscript is generally well written with clarity and transparency. However, a major concern is the lack of specificity in the genetic manipulation, which targets Drd1a+ neurons not exclusive to L6b, undermining the attribution of observed effects solely to L6b. Verification of neuronal silencing is also unclear, and statistical inconsistencies between the main text and figures/tables make it difficult to effectively evaluate the text and stated outcomes.

Strengths:

(1) The text is well written.

(2) The authors are transparent about methodological details.

(3) The stated sleep, circadian, and orexin infusion experiments appear to be well designed, executed, and analyzed (with the exceptions of some statistical analyses detailed below).

Weaknesses:

(1) All outcomes are attributed specifically to L6b neurons, but the genetic manipulation is not specific to L6b neurons. The authors acknowledge this as a limitation, but in my view, this global manipulation is more than a limitation - it affects the overall interpretations of the data. The Hoerder-Suabedissen et al., 2018 paper shows sparse, but also dense, expression of Drd1a+ neurons in brain regions outside of the L6b. Given this issue, the results are largely overstated throughout the paper.

(2) It is not clear to me that the "silencing" of Drd1a+ neurons was verified.

(3) There were various discrepancies (and potentially misattributions) between the stated significant differences in Supplementary Table T1 data and Figure 3a & S2 spectral plots. This issue makes it difficult to effectively evaluate the main text and stated outcomes.

Related, the authors stated that post hoc comparisons of EEG spectral frequency bins were not corrected for multiple testing. Instead, significance was only denoted if changes in at least two consecutive frequency bins were significant. However, there are multiple plots in which a single significance marker is placed over an isolated bin (i.e., 4c, 6, S5, S6). Unless each marker is equivalent to 2 consecutive frequency bins, these markers should be removed from the plots. Otherwise, please define the frequency and size of these markers in the main text.

(4) A rainbow color scale, as in Figure 3, we've now learned, can be misleading and difficult to interpret. The viridis color scale or a different diverging color scale are good alternatives.

(5) How much time elapsed between vehicle/orexin A & B infusions?

(6) For Figure 6, there are statistical discrepancies between the main text and the plots (pg. 10):

a) The text claims post hoc differences for relative ORXA frontal EEG, but there are no significance markers on the plot.<br /> b) The text states that there were no post hoc differences for the relative ORXA occipital EEG, but significance markers are on the plot.<br /> c) The main test for the relative ORXB frontal EEG was not significant, but there are post hoc significance markers on the plot.<br /> d) For relative ORXB occipital EEG, there are significant markers on the plot outside of the stated range in the text.

(7) Some important details are only available in figure captions, making it difficult to understand the main text. For example, when describing Figure 3c in the main text on page 7, it is not clear what type of transitions are being discussed without reading the figure caption. Likewise, a "decrease," "shift," and "change" are mentioned, but relative to what? Similar comment for the EEG theta activity description on pages 7 - 8. Please add relevant details to the main text.

(8) Statistical comparisons for data in Figure 3e, post hoc analyses for data in Figure S7a-b REM data, and post hoc analyses for Figure S7c (not b) occipital EEG should be included to support differences claims. Please denote these differences on the respective plots.

(9) In the subsection titled "Layer 6b mediates effects of orexin on vigilance states (pg. 8)," there does not seem to be any stated differences between control and L6b silenced mice. A more accurate subtitle is needed.

Reviewer #2 (Public review):

Summary:

In this manuscript, Meijer and colleagues investigated the effects of inactivation (conditional silencing) of cortical layer 6b neurons on sleep-wake states and EEG spectral power under the following three conditions: during natural sleep-wake states, after sleep deprivation, or after intracerebroventricular administration of orexin A and B. The authors report that silencing of L6b neurons did not have a significant effect on the total time spent in sleep-wake states, duration, or number of state epochs, or the response to sleep deprivation. However, silencing of L6b neurons did slow down theta-frequency (6-9 Hz) during wake and REM sleep, and reduced the total EEG power during NREM sleep. Infusion of orexin A in the mice in which cortical layer 6b neurons were inactivated produced an increase in wakefulness. A similar effect was observed after infusion of orexin A in the mice in which these neurons were not silenced, but the effect (i.e., increase in wakefulness) was of a smaller magnitude. Silencing of cortical layer 6b neurons attenuated the effect of orexin B in increasing theta activity, as was observed in the control mice. The authors conclude that the cortical neurons in layer 6b play an essential role in state-dependent dynamics of brain activity, vigilance state control, and sleep regulation.

Strengths:

(1) A focus on cortical layer 6b neurons, which are an understudied neuronal population, especially in the context of brain and behavioral state transitions.

(2) The authors used a well-established mouse model to study the effect of inactivation of cortical layer 6b neurons.

Weaknesses:

(1) Although the authors used a highly selective approach to silence layer 6b neurons, the observed changes in EEG oscillations cannot be solely attributed to layer 6b neurons because of the ICV route for orexin administration.

(2) The rationale for using only male rats is not provided.

Joint Public Review:

Summary:

There has been extensive electrophysiological research investigating the relationship between local field potential patterns and individual cell spike patterns in the hippocampus. In this study, the authors used innovative imaging techniques to examine spike synchrony of hippocampal cells during locomotion and immobility states. The authors report that hippocampal place cells exhibit prominent synchronous spikes that co-occur with theta oscillations during exploration of novel environments.

Strengths:

The single cell voltage imaging used in this study is a highly novel method that may allow recordings that were not previously possible using traditional methods.

Weaknesses:

Local field potential recordings were obtained from the contralateral hemisphere for technical reasons, which limits some of the study's claims.

Reviewer #1 (Public review):

Summary:

The work from this paper successfully mapped transcriptional landscape and identified EA-responsive cell types (endothelial, microglia). Data suggest EA modulates BBB via immune pathways and cell communication. However, claims of "BBB opening" are not directly proven (no permeability data).

Strengths:

First scRNA-seq atlas of EA effects on BBB, revealing 23 cell clusters and 8 cell types. High cell throughput (98,338 cells), doublet removal, and robust clustering (Seurat, SingleR). Comprehensive bioinformatics (GO/KEGG, CellPhoneDB for ligand-receptor interactions). Raw data were deposited in GEO (GSE272895) and can be accessed.

Weaknesses:

(1) No in vivo/in vitro assays confirm BBB permeability changes (e.g., Evans blue leakage, TEER).

(2) Only male rats were used, ignoring sex-specific BBB differences.

(3) Pericytes and neurons, critical for the BBB, were not captured, likely due to dissociation artifacts.

(4) Protein-level validation (Western blot, IHC) absent for key genes (e.g., LY6E, HSP90).

(5) Fixed stimulation protocol (2/100 Hz, 40 min); no dose-response or temporal analysis.

Reviewer #2 (Public review):

Summary:

This study uses single-cell RNA sequencing to explore how electroacupuncture (EA) stimulation alters the brain's cellular and molecular landscape after blood-brain barrier (BBB) opening. The authors aim to identify changes in gene expression and signaling pathways across brain cell types in response to EA stimulation using single-cell RNA sequencing. This direction holds promise for understanding the consequences of noninvasive methods of BBB opening for therapeutic drug delivery across the BBB.

Strengths:

(1) The study addresses an emerging and potentially important application of noninvasive stimulation methods to manipulate BBB permeability.

(2) The dataset provides broad transcriptional profiling across multiple brain cell types using single-cell resolution, which could serve as a valuable community resource.

(3) Analyses of receptor-ligand signaling and cell-cell communication are included and have the potential to offer mechanistic insight into BBB regulation.

Weaknesses:

(1) The work falls short in its current form. The experimental design lacks a clear justification, and readers are not provided with sufficient background information on the extent, timing, or regional specificity of BBB opening in this EA model. These details, established in prior work, are critical to understanding the rationale behind the current transcriptomic analyses.

(2) Further, the results are often presented with minimal context or interpretation. There is no model of intercellular or molecular coordination to explain the BBB-opening process, despite the stated goal of identifying such mechanisms. The statement that EA induces a "unique frontal cortex-specific transcriptome signature" is not supported, as no data from other brain regions are presented. Biological interpretation is at times unclear or inaccurate - for instance, attributing astrocyte migration effects to endothelial cell clusters or suggesting microglial tight junction changes without connecting them meaningfully to endothelial function.

(3) The study does include analyses of receptor-ligand signaling and cell-cell communication, which could be among its most biologically rich outputs. However, these are relegated to supplementary material and not shown in the leading figures. This choice limits the utility of the manuscript as a hypothesis-generating resource.

(4) Overall, while the dataset may be of interest to BBB researchers and those developing technologies for drug delivery across the BBB, the manuscript in its current form does not yet fulfill its interpretive goals. A more integrated and biologically grounded analysis would be beneficial.

Reviewer #1 (Public review):

Summary:

This work investigates the neural basis of continual motor learning, specifically how brains might accommodate new motor memories without interfering with previously learned behaviours. Mainly drawing inspiration from recent experimental studies in monkeys (Losey et al. and Sun, O'Shea et al.), the authors use recurrent neural networks (RNNs) to model sequential learning and examine the emergence and properties of two proposed neural signatures of motor memory: the "uniform shift" observed in preparatory activity and the "memory trace" observed in execution activity.

Strengths:

The work's main contribution is demonstrating that both uniform shifts and memory traces emerge in RNN models trained on a sequential BCI task, without requiring explicit additional mechanisms. The work explores the relationship between these signatures and behavioural savings, finding that the memory trace correlates with immediate retention savings in networks without context, while the uniform shift does not. The study also investigates how properties of the new task perturbation (within- vs. outside-manifold) and the presence of explicit context cues affect these signatures and their relationship to savings, generally finding that context signals and outside-manifold perturbations reduce savings by decreasing the inherent overlap in the neural strategies used to solve the task.

Weaknesses:

A primary weakness is the lack of clear definitions of the uniform shift and the memory trace, which are quite different metrics. Another primary weakness is that the task modelled is well-matched to the Losey et al. BCI paradigm, but not well-matched to the Sun, O'Shea et al.'s curl field paradigm, which is likely impacting some of the results, primarily the lack of a relationship between the uniform shift and motor memories. While there are improvements that could be made in this work, we think it is a demonstration that modeling learning in neural activity using neural network models continues to be a valuable tool, moving the field forward.

Reviewer #2 (Public review):

Summary:

Chang et al. develop an RNN model of a BCI sequential learning task to examine the emergence of motor memory in the network. They use this system to quantify signatures of memory in continual learning, comparing their model with experimental observations from monkeys in prior publications. They show that the RNN model has signatures of shifts associated with sequential learning without any non-standard learning rules. This convincing study contributes to the knowledge of how motor memories are formed and shaped so that they are flexible in acquiring multiple behaviors.

Strengths:

This paper describes a well-designed numerical experiment that comes to a clear interpretation of a set of neural BCI experiments. The learning signatures the authors describe are interesting and well laid out, and the paper is well written. I find it insightful that the neural signature of motor learning emerges in a trained network without special learning rules.

Weaknesses:

The paper could be stronger if it made a stronger interpretation of how memory traces and uniform shifts are related. These two observations are taken from the BCI sequential learning literature and introduced by two different prior experimental papers on two different tasks, so it seems like there is an opportunity here to use the RNN model to unite these concepts, or define another metric for signatures of learning from a more normative approach.

Reviewer #3 (Public review):

Summary:

The authors build and analyze recurrent neural network (RNN) models of brain-computer interface (BCI) multi-task learning, developing a valuable theoretical understanding of learning-related neural population phenomena ("memory traces" and "uniform shifts") that have been reported in recent experimental studies of BCI and motor learning. The authors find that both phenomena emerge in their RNN models, and both correlate in some manner to learning-related behavioral phenomena ("savings" and "forgetting"). The authors also reveal that RNN training details, in particular, incorporating a task-indicating contextual input, can impact these population-level signatures of learning in RNN activity and their relation to those behavioral phenomena.

Strengths:

The text is well written, and the figures are clearly composed to convey the core concepts and findings. The RNN studies are elegant in their ability to recapitulate the memory trace and uniform shift phenomena, and further allow evaluations of novel scenarios that were not tested in the original corpus of the modeled animal experiments. The authors assess the sensitivity of their results to multiple approaches to RNN training, including training connectivity within a model of motor cortex, training only an upstream model that provides inputs to the motor cortex model, and providing task-indicating contextual inputs.

Weaknesses:

(1) It is unclear to what extent these RNN models operate in regimes relevant to biological neural networks (e.g., motor cortex), even at the neural-population level of abstraction studied here. Can the authors speak to how sensitive their results are to details that might speak to these operating regimes (e.g., signal-to-noise ratios or dimensionality of the RNN activities)?

(2) The work could be further strengthened by analyses demonstrating a more direct link between the neural population phenomena (memory trace and uniform shift) and the behavioral phenomena (savings, forgetting, etc). While in animal experiments, it can be exceedingly difficult to demonstrate links beyond correlative effects, the promise of a model is the relative tractability of implementing manipulations that might establish something closer to a causal link between phenomena. Is it the case that the memory trace is a task-dependent, mean-preserving rotation of the across-target task-relevant activity space? And that the uniform shift is a translation (non-mean-preserving) of that space? If so, could the authors design regularization schemes that specifically target each of these effects, enabling a more direct test of the functional role the effects play in driving behavioral phenomena?

Minor Comments:

The current study is based on BCI learning of center-out tasks, analogous to the Losey et al. task that initially reported the memory trace phenomena. However, a rather different behavioral task - involving arm movements through curl force fields - was employed by the Sun, O'Shea, et al. study that originally reported the uniform shift phenomena. How should readers interpret the current study's findings related to the uniform shift? To what extent might the behavioral implications of the uniform shift depend on the demands of the task, e.g., the biomechanics, day-to-day experiencing of different curl-field perturbations, etc.?

Reviewer #1 (Public review):

Summary:

Bacterial species that frequently undergo horizontal gene transfer events tend to have genomes that approach linkage equilibrium, making it challenging to analyze population structure and establish the relationships between isolates. To overcome this problem, researchers have established several effective schemes for analyzing N. gonorrhoeae isolates, including MLST and NG-STAR. This report shows that Life Identification Number (LIN) Codes provide for a robust and improved discrimination between different N. gonorrhoeae isolates.

Strengths:

The description of the system is clear, the analysis is convincing, and the comparisons to other methods show the improvements offered by LIN Codes.

Weaknesses:

No major weaknesses were identified by this reviewer.

Reviewer #2 (Public review):

Summary:

This paper describes a new approach for analyzing genome sequences.

Strengths:

The work was performed with great rigor and provides much greater insights than earlier classification systems.

Weaknesses:

A minor weakness is that the clinical application of LIN coding could be articulated in a more in-depth way. The LIN coding system is very impressive and is certainly superior to other protocols. My recommendation, although not necessary for this paper, is that the authors expand their analysis to noncoding sequences, especially those upstream of open reading frames. In this respect, important cis-acting regulatory mutations that might help to further distinguish strains could be identified.

Reviewer #3 (Public review):

Summary:

In this well-written manuscript, Unitt and colleagues propose a new, hierarchical nomenclature system for the pathogen Neisseria gonorrhoeae. The proposed nomenclature addresses a longstanding problem in N. gonorrhoeae genomics, namely that the highly recombinant population complicates typing schemes based on only a few loci and that previous typing systems, even those based on the core genome, group strains at only one level of genomic divergence without a system for clustering sequence types together. In this work, the authors have revised the core genome MLST scheme for N. gonorrhoeae and devised life identification numbers (LIN) codes to describe the N. gonorrhoeae population structure.

Strengths:

The LIN codes proposed in this manuscript are congruent with previous typing methods for Neisseria gonorrhoeae, like cgMLST groups, Ng-STAR, and NG-MAST. Importantly, they improve upon many of these methods as the LIN codes are also congruent with the phylogeny and represent monophyletic lineages/sublineages.

The LIN code assignment has been implemented in PubMLST, allowing other researchers to assign LIN codes to new assemblies and put genomes of interest in context with global datasets.

Weaknesses:

The authors correctly highlight that cgMLST-based clusters can be fused due to "intermediate isolates" generated through processes like horizontal gene transfer. However, the LIN codes proposed here are also based on single linkage clustering of cgMLST at multiple levels. It is unclear if future recombination or sequencing of previously unsampled diversity within N. gonorrhoeae merges together higher-level clusters, and if so, how this will impact the stability of the nomenclature.

The authors have defined higher resolution thresholds for the LIN code scheme. However, they do not investigate how these levels correspond to previously identified transmission clusters from genomic epidemiology studies. It would be useful for future users of the scheme to know the relevant LIN code thresholds for these investigations.

Reviewer #1 (Public review):

The authors try to investigate how the population of microtubules (LSPMB) that originate from sporozoite subpellicular microtubules (SSPM) and are remodelled during liver-stage development of malaria parasites. These bundles shrink over time and help form structures needed for cell division. The authors have used expansion microscopy, live-cell imaging, genetically engineered mutants, and pharmacological perturbation to study parasite development with liver cells.

A major strength of the manuscript is the live cell imaging and expansion microscopy to study this challenging liver stage of parasite development. It gives important knowledge that PTMs of α-tubulin, such as polyglutamylation and tyrosination/detyrosination, are crucial for microtubule stability. Mutations in α-tubulin reduce the parasite's ability to move and proliferate in the liver cells. The drug oryzalin, which targets microtubules, also blocks parasite development, showing how important dynamic microtubules are at this stage.

The major problem in the manuscript was the way it flows, as the authors keep shifting from the liver stage to the sporogony stages and then back to the liver stages. It was very confusing at times to know what the real focus of the study is, whether sporozoite development or liver stage development. The flow of the manuscript could be improved. Some of the findings reported here substantiate the previous electron microscopy.

Overall, the study represents an important contribution towards understanding cytoskeletal remodelling during liver stage infection. The study suggests that tubulin modifications are key for the parasite's survival in the liver and could be targets for new malaria treatments. This is also the stage that has been used for vaccine development, so any knowledge of how parasites proliferate in the liver cells will be beneficial towards intervention approaches.

Reviewer #2 (Public review):

Summary:

The authors investigated microtubule distribution and their possible post-translational modifications (PTM) in Plasmodium berghei during development of the liver stage, using either hepatocytes or HeLa cells as models. They used conventional immunofluorescence assays and expansion microscopy with various antibodies recognising tubulin and, in the second part of the work, its candidate PTMs, as well as markers of Plasmodium, in addition to live imaging with a fluorescent marker for tubulin. In the third part of the study, they generated 3 mutants deprived of either the last four residues or the last 11 residues, or where a candidate polyglutamylation site was substituted by an alanine residue.

Strengths:

In the first part, microtubules are monitored by a combination of two approaches (IFA and live), revealing nicely the evolution of the sporozoite subpellicular microtubules (SSPM, the sporozoite is the developmental stage present in salivary glands of the mosquitoes and that infects hepatocytes) into a different structure termed liver-stage parasite microtubule bundle (LSPMB). The LSPMB shrinks during the course of parasite development and finally disappears while hemi-spindles emerge over time. Contact points between these two structures are observed frequently in live cells and occasionally in fixed cells, suggesting the intriguing possibility that tubulin might be recycled from the LSPMB to contribute to hemi-spindle formation.

In the second part, antibodies recognising (1) the final tyrosine found at the C-terminal tail and (2) a stretch of 3 glutamate residues in a side chain are used to monitor these candidate PTMs. Signals are positive at the SSPM, and while it remains positive for polyglutamylation, it becomes negative for the final tyrosine at the LSPM, while a positive signal emerges at hemi-spindles at later stages of development.

In the last part, the three mutants are fed to mosquitoes, where they show reduced development, the one lacking the alpha-tubulin tail even failing to reach the salivary glands. However, the two other mutants infect HeLa cells normally, whereas sporozoites with the C-terminal tail deletion recovered from the haemolymph did not develop in these cells.

The first part provides convincing evidence that microtubules are extensively remodelled during the infection of hepatocytes and HeLa cells, in agreement with the spectacular Plasmodium morphogenetic changes accompanying massive and rapid proliferation. The third part brings further confirmation that the C-terminal tail of alpha-tubulin is essential for multiple stages of parasite development, in agreement with previous work (50). Since it is the region where several post-translational modifications take place in other organisms (detyrosination, polyglutamylation, glycylation), it makes sense to propose that the essential function is related to these PTMs also in Plasmodium.

Weaknesses:

The significance of tubulin PTM relies on two antibodies whose reactivity to Plasmodium tubulins is unclear (see below). The interpretation of the literature on detyrosination and polyglutamylation is confusing in several places, meaning that the statements about the possible role of these PTMs need to be carefully revisited.

The authors use the term "tyrosination" but the alpha1-tubulin studied here possesses the final tyrosine when it is synthesised, so it is "tyrosinated" by default. It could potentially be removed by a tyrosine carboxypeptidase of the vasoinhibin family (VASH) as reported in other species. After removal, this tyrosine can be added again by a tubulin-tyrosine ligase (TTL) enzyme. It is therefore more appropriate to talk about detyrosination-retyrosination rather than tyrosination (this confusion is unfortunately common in the literature, see Janke & Magiera, 2020).

The difficulty here is that there is so far no evidence that detyrosination takes place in Plasmodium. Neither VASH nor TTL could be identified in the Plasmodium genome (ref 31, something we can confirm with our unsuccessful BLAST analyses), and mass spectrometry studies of purified tubulin, albeit from blood stages, did not find evidence for detyrosination (reference 43). Western blots using an antibody against detyrosinated tubulin did not produce a positive signal, neither on purified tubulin, nor on whole parasites (43). Of course, the situation could be different in liver stages, but the question of the detyrosinating enzyme is still there. The existence of a unique Plasmodium system for detyrosination cannot be formally ruled out, but given the high degree of conservation of these PTMs and their associated enzymes, it sounds difficult to imagine.

The fact that the anti-tyrosinated antibody still produced a signal in the cell line where the final tyrosine is deleted raises issues about its specificity. A cross-reactivity with beta-tubulin is proposed, but the Plasmodium beta-tubulin does not carry a final tyrosine, further raising concerns about antibody specificity.

The interpretation of these results should therefore be considered carefully. There also seems to be some confusion in the function of detyrosination cited from the literature. It is said in line 229 that "tyrosination has been associated with stable microtubules" (33, 34, 50, 55). References 33 and 34 actually show that tyrosinated microtubules turn over faster in neurons or in epithelial cells, respectively, while references 50 and 55 do not study de/retyrosination. The general consensus is that tyrosinated microtubules are more dynamic (see reference 24).

The situation is a bit different for polyglutamylation since several candidate poly- or mono-glutamylases have been identified in the Plasmodium genome, and at least mono-glutamylation of beta-tubulin has been formally proven, still in bloodstream stages (ref 43). The authors propose that the residue E445 is the polyglutamylation site. To our knowledge, this has not been demonstrated for Plasmodium. This residue is indeed the favourite one in several organisms such as humans and trypanosomes (Eddé et al., Science 1990; Schneider et al., JCS, 1997), and it is tempting to propose it would be the same here. However, TTLLs bind the tubulin tails from their C-terminal end like a glove on a finger (Garnham et al., Cell, 2015), and the presence of two extra residues in Plasmodium tubulins would mean that the reactive glutamate might be in position E447 rather than E445. This is worth discussing.<br /> On the positive side, it is encouraging to see that signals for both anti-tyrosinated tail and poly-glutamylated side chain are going down in the various mutants, but this would need validation with a comparison for alpha-tubulin signal.

Line 316: polyglutamylation "is commonly associated with dynamic microtubule behavior (78-80)". Actually, references 78 and 79 show the impact of this PTM on interaction with spastin, and reference 80 discusses polyglutamylation as a marker of stable microtubules in the context of cilia and flagella. The consensus is that polyglutamylated microtubules tend to be more stable (ref24).

Conclusion:

The first and the third parts of this manuscript - evolution of microtubules and importance of the C-terminal tails for Plasmodium development - are convincing and well supported by data. However, the presence and role of tubulin PTM should be carefully reconsidered.

Plasmodium tubulins are more closely related to plant tubulins and are sensitive to inhibitors that do not affect mammalian microtubules. They therefore represent promising drug targets as several well-characterised compounds used as herbicides are available. The work produced here further defines the evolution of the microtubule network in sporozoites and liver stages, which are the initial and essential first steps of the infection. Moreover, Plasmodium has multiple specificities that make it a fascinating organism to study both for cell biology and evolution. The data reported here are elegant and will attract the attention of the community working on parasites but also on the cytoskeleton at large. It will be interesting to have the feedback of other people working on tubulin PTMs to figure out the significance of this part of the work.

Reviewer #3 (Public review):

Summary:

The manuscript by Atchou et al. investigates the role of the microtubule cytoskeleton in sporozoites of Plasmodium berghei, including possible functions of microtubule post-translational modifications (tyrosination and polyglutamylation) in the development of sporozoites in the liver. They also assessed the development of sporozoites in the mosquito. Using cell culture models and in vivo infections with parasites that contain tubulin mutants deficient in certain PTMs, they show that may aspects of the life cycle progression are impaired. The main conclusion is that microtubule PTMs play a major role in the differentiation processes of the parasites.

However, there are a number of major and minor points of criticism that relate to the interpretation of some of the data.

Comments:

(1) The first paragraph of "Results" almost suggests that the presence of a subpellicular MT-array in sporozoites is a new discovery. This is not the case, see e.g. the recent publication by Ferreira et al. (Nature Communications, 2023).

(2) Why were HeLa cells and not hepatocytes (as in Figure 3) used for measuring infection rates of the mutants in Figure 5H and 5L? As I understand, HeLa cells are not natural host cells for invading sporozoites. HeLa cells are epithelial cells derived from a cervical tumour. I am not an expert in Plasmodium biology, but is a HeLa infection an accepted surrogate model for liver stage development?

(3) The tubulin staining in Figures 1A and 1B is confusing and doesn't seem to make sense. Whereas in 1A the antibody nicely stains host and parasite tubulin, in 1B, only parasite tubulin is visible. If the same antibody and the same host cells have been used, HeLa cytoplasmic microtubules should be visible in 1B. In fact, they should be the predominant antigen. The same applies to Figure 2, where host microtubules are also not visible.

(4) In Figures 2A and B, the host nuclei appear to have very different sizes in the DMSO controls and in the drug-treated cells. For example, in the 20 µM (-) image (bottom right), the nuclei are much larger than in the DMSO (-) control (top left). If this is the case, expansion microscopy hasn't worked reproducibly, and therefore, quantification of fluorescence is problematic. The scalebar is the same for all panels.

(5) I don't quite follow the argument that spindles and the LSPMB are dynamic structures (e.g., lines 145, 174). That is a trivial statement for the spindle, as it is always dynamic, but beyond that, it has only been shown that the structure is sensitive to oryzalin. That says little about any "natural" dynamic behaviour. Any microtubule structure can be destroyed by a particular physical or chemical treatment, but that doesn't mean all structures are dynamic. It also depends on the definition of "dynamic" in a particular context, for example, the time scale of dynamic behaviour (changes within seconds, minutes, or hours).

(6) I am not sure what part in the story EB1 plays. The data are only shown in the Supplements and don't seem to be of particular relevance. EB1 is a ubiquitous protein associated with microtubule plus ends. The statement (line 192) that it "may play a broader role..." is unsubstantiated and cannot be based merely on the observation that it is expressed in a particular life cycle stage.

(7) Line 196 onwards: The antibody IN105 is better known in the field as polyE. Maybe that should be added in Materials and Methods. Also, the antibody T9028 against tyrosinated tubulin is poorly validated in the literature and rarely used. Usually, researchers in this field use the monoclonal antibody YL1/2. I am not sure why this unusual antibody was chosen in this study. In fact, has its specificity against tyrosinated α-tubulin from Plasmodium berghei ever been shown? The original antigen was human and had the sequence EGEEY. The Plasmodium sequence is YEADY and hence very different. It is stated that the LSPMB is both polyglutamylated and tyrosinated. This is unusual because polyglutamylated microtubules are usually indicative of stable microtubules, whereas tyrosinated microtubules are found on freshly polymerised and dynamic microtubules. However, a co-localisation within the same cell has not been attempted. This is, however, possible since polyE is a rabbit antibody and T9028 is a mouse antibody. I suspect that differences or gradients along the LSPMB would have been noticed. Also, in lines 207/208, it is said that tyrosination disappears after hepatocyte invasion, which is shown in Figure 3. However, in Figure 3A, quite a lot of positive signals for tyrosination are visible in the 54 and 56 hpi panels.

(8) In line 229, it is stated that tyrosination "has previously been associated with stable microtubule in motility". This statement is not correct. In fact, none of the cited references that apparently support this statement show that this is the case. On the contrary, stable microtubules, such as flagellar axonemes, are almost completely detyrosinated. Therefore, tyrosination is a marker for dynamic microtubules, whereas detyrosinated microtubules are indicative of stable microtubules. This is an established fact, and it is odd that the authors claim the opposite.

(9) Line 236 onwards: Concerning the generation of tubulin mutants, I think it is necessary to demonstrate successful replacement of the wild-type allele by the mutant allele. I am sure the authors have done this by amplification and subsequent sequencing of the genomic locus using PCR primers outside the plasmid sequences. I suggest including this information, e.g., by displaying the chromatograph trace in a supplementary figure. Or are the sequences displayed in Figure S3B already derived from sequenced genomic DNA? This is not described in the Legend or in Materials and Methods. The left PCR products obtained for Figure S3 B would be a suitable template for sequencing.

(10) It is also important to be aware of the fact that glutamylation also occurs on β-tubulin. This signal will also be detected by polyE (IN105). Therefore, it is surprising that IN105 immunofluorescence is negative on the C-term Δ cells (Figure S3 D). Is there anything known about confirmed polyglutamylation sites on both α- and β-tubulins in Plasmodium, e.g., by MS? In Toxoplasma, both α- and β-tubulin have been shown to be polyglutamylated.

(11) Figure S3 is very confusing. In the legend, certain intron deletions are mentioned. How does this relate to posttranslational tubulin modifications? The corresponding section in Results (lines 288-292) is also not very helpful in understanding this.

(12) Figure 4E doesn't look like brightfield microscopy but like some sort of fluorescent imaging. In Figure 4C, were the control (NoΔ) cells with an integrated cassette, but no mutations, or non-transgenic cells?

(13) It is difficult to understand why the TyΔ and the CtΔ mutants still show quite a strong signal using the anti-tyrosination antibody. If the mutants have replaced all wild-type alleles, the signal should be completely absent, unless the antibody (see my comment above concerning T9028) cross-reacts with detyrosinated microtubules. Therefore, the quantitation in Figures 5F and 5G is actually indicative of something that shouldn't be like that. The quantitation of 5F is at odds with the microscopy image in 5D. If this image is representative, the anti-Ty staining in TyΔ is as strong as in the control NoΔ.

(14) The statement that the failure of CtΔ mutants to generate viable sporozoites is due to the lack of microtubule PTMs (lines 295-296) is speculative. The lack of the entire C-terminal tail could have a number of consequences, such as impaired microtubule assembly or failure to recruit and bind associated proteins. This is not necessarily linked to PTMs. Also, it has been shown in yeast that for microtubules to form properly and exquisite regulation (proteostasis) of the ratio between α- and β-tubulin is essential (Wethekam and Moore, 2023). I am not sure, but according to Materials and Methods (line 423), the gene cassettes for replacing the wild-type tubulin gene with the mutant versions contain a selectable marker gene for pyrimethamine selection. Are there qPCR data that show that expression levels of mutant α-tubulin are more or less the same as the wild-type levels?

(15) In the Discussion, my impression is that two recent studies, the superb Expansion Microscopy study by Bertiaux et al. (2021) and the cryo-EM study by Ferreira et al. (2023), are not sufficiently recognised (although they are cited elsewhere in the manuscript). The latter study includes a detailed description of the microtubule cytoskeleton in sporozoites. However, the present study clearly expands the knowledge about the structure of the cytoskeleton in liver stage parasites and is one of the few studies addressing the distribution and function of microtubule post-translational modifications in Plasmodium.

(16) I somewhat disagree with the statement of a co-occurrence of polyglutamylated and tyrosinated microtubules. I think the resolution is too low to reach that conclusion. As this is a bold claim, and would be contrary to what is known from other organisms, it would require a more rigorous validation. Given the apparent problems with the anti-Ty antibody (signal in the TyΔ mutant), one should be very cautious with this claim.

(17) In the Discussion (lines 311 and 377), it is again claimed that tyrosinated microtubules are "a well-known marker of stable microtubules". This statement is completely incorrect, and I am surprised by this serious mistake. A few lines later, the authors say that polyglutamylated is "commonly associated with dynamic microtubule behaviour". Again, this is completely incorrect and is the opposite of what is firmly established in the literature. Polyglutamylation and detyrosination are markers of stable microtubules.

(18) In line 339, the authors interpret the residual antibody staining after the introduction of the mutant tubulin as a compensatory mechanism. There is no evidence for this. More likely explanations are firstly the quality of the anti-Ty-antibody used (see comment above), and the fact that also β-tubulin carries C-terminal polyglutamylation sites, which haven't been investigated in this study. PTMs on β-tubulin are not compensatory, but normal PTMs, at least in all other organisms where microtubule PTMs have been investigated.

Specify the average time saved or the number of devices repaired per week to illustrate efficiency.

Quantify the impact of these relationships on sales growth or customer loyalty metrics.

Include specific savings amounts or percentage increases in customer retention due to these reviews.

Quantify the increase in customer satisfaction or sales resulting from these tailored solutions.

State how the UI/UX design improved user interaction or satisfaction rates.

Include specific metrics on user engagement or feedback received post-launch.

Mention the impact of this integration, such as reduced load times or improved user experience.

Quantify the data transfer speed or reliability improvements achieved through this implementation.

Add how this configuration improved performance or reduced resource usage.

Specify the outcome or impact of this development, e.g., improved efficiency or functionality.

Reviewer #1 (Public review):

Summary:

In the presented study, the authors aim to explore the role of nociceptors in the fine particulate matter (FPM) mediated Asthma phenotype, using rodent models of allergic airway inflammation. This manuscript builds on previous studies, and identify transciptomic reprogramming and an increased sensitivity of the jugular nodose complex (JNC) neurons, one of the major sensory ganglion for the airways, on exposure to FPM along with Ova during the challenge phase. The authors then use OX-314 a selectively permeable form of lidocaine, and TRPV1 knockouts to demonstrate that nociceptor blocking can reduce airway inflammation in their experimental setup.

The authors further identify the presence of Gfra3 on the JNC neurons, a receptor for the protein Artemin, and demonstrate their sensitivity to Artmein as a ligand. They further show that alveolar macrophages release Artemin on exposure to FPM.

Strengths:

The study builds on results available from multiple previous works, and presents important results which allow insights into the mixed phenotypes of Asthma seen clinically. In addition, by identifying the role of nociceptors, they identify potential therapeutic targets which bear high translational potential.

Weaknesses:

While the results presented in the study are highly relevant, there is a need for further mechanistic dissection to allow better inferences. Currently, certain results seem associative. Also, certain visualisations and experimental protocols presented in the manuscript need careful assessment and interpretation.

While Asthma is a chronic disease, the presented results are particularly important to explore Asthma exacerbations in response to acute exposure to air pollutants. This is relevant in today's age of increasing air pollution and increasing global travel.

Comments on revisions:

Thank you for addressing the suggestions. No further comments.

Reviewer #2 (Public review):

Summary:

The authors sought to investigate the role of nociceptor neurons in the pathogenesis of pollution-mediated neutrophilic asthma. The authors overall achieved the aim of demonstrating that nociceptor neurons are important to the pathogenesis of pollution-exacerbated asthma. Their results support their conclusions overall, although there are ways the study findings can be strengthened. This work further evaluates how nociceptor neurons contribute to asthma pathogenesis important for consideration while proposing treatment strategies for under treated asthma endotypes.

Strengths:

The authors utilize TRPV1 ablated mice to confirm the effects of intranasally administered QX-314 utilized to block sodium currents.

Use of intravital microscopy to track alveolar macrophage and neutrophil motility in their model

The authors demonstrate that via artemin, which is upregulated in alveolar macrophages in response to pollution, sensitizes JNC neurons thereby increasing their responsiveness to pollution. Ablation or inactivity of nociceptor neurons prevented the pollution induced increase in inflammation.

Weaknesses:

While neutrophilic, unclear of the endotype of asthma represented by the model

Comments on revisions:

The authors have addressed or commented on all concerns.

Reviewer #3 (Public review):

Asthma is a complex disease that includes endogenous epithelial, immune and neural components that respond to environmental stimuli. Small airborne particles with diameters in the range of 2.5 micrometers or less, so-called PM2.5, are thought to contribute to some forms of asthma. These forms of asthma may have neutrophils, eosinophils and macrophages in bronchoalveolar lavage. Here, Wang and colleagues build on a recent model that incorporated PM2.5 which was found to have a neutrophilic component. Wang altered the model to provide an extra kick via the incorporation of ovalbumin. The major strength of this work is that silencing TRPV1-expressing neurons either pharmacologically or genetically, modulated inflammation and the motility of neutrophils. By examining bronchoalveolar lavage fluid, they found not only that levels of a number of cytokines were increased, but also that artemin, a protein that supports neuronal development and function, was elevated, which did not occur in nociceptor- ablated mice. Their data strengthens links between pollutants, immune and neural interactions.

Comments on revisions:

The manuscript has been revised extensively, including the addition of new experiments, such as intravital microscopy. Did the comments from the reviewers, manifest by additional experiments and modifying how some of the data was presented, result in any changes in the hypotheses or the interpretation of such?

Reviewer #1 (Public review):

Summary:

This paper presents evidence that a relatively common genetic variant tied to several disease phenotypes affects the interaction between the mRNA of CCL2 and the RNA binding protein HuR. CCL2 is an immune cell chemoattractant protein.

Strengths:

The study is well conducted with relevant controls. The techniques are appropriate, and several approaches provided concordant results were generally supportive of the conclusions reached. The impact of this work, identifying a genetic variant that works by altering the binding of an RNA-regulatory protein, has important implications given that the HuR protein could be a drug target to improve its function and over-ride this genetic change. This could have important implications for a number of diseases where this genetic variant contributes to disease risk.

The authors have done a nice job of citing prior work. Details of the experimental protocols are well elaborated and the significance of the findings are well contextualized.

Weaknesses:

Authors have addressed prior weaknesses.

Reviewer #2 (Public review):

This study focuses on the differential binding of the RNA-binding protein HuR to CCL2 transcript (genetic variants rs13900 T or C). The study explores how this interaction influences the stability and translation of CCL2 mRNA. Employing a combination of bioinformatics, reporter assays, binding assays, and modulation of HuR expression, the study proposes that the rs13900T allele confers increased binding to HuR, leading to greater mRNA stability and higher translational efficiency. These findings indicate that rs13900T allele might contribute to heightened disease susceptibility due to enhanced CCL2 expression mediated by HuR. The study is interesting and most results are convincing, however the interpretation relative to RNA transcription and/or stability must be modified, and some data need better presentation or interpretation.

Major Points

Figure 2C:<br /> The authors describe an experiment to assess mRNA stability by labeling nascent RNA with EU for 3 hours, followed by washout of EU, and then incubation with or without actinomycin D for an additional 4 hours before measuring the remaining EU-labeled RNA. While the approach to label nascent RNA with EU is appropriate for tracking RNA decay, I have concerns regarding the use and interpretation of actinomycin D in this context.<br /> After EU washout, the pool of EU-labeled RNA is fixed and no new EU incorporation can occur. Therefore, the addition of actinomycin D at this stage should not affect the decay rate of the already labeled RNA, as transcription of EU-labeled RNA has effectively ceased. In this design, measuring the decrease in EU-labeled RNA over time reflects mRNA stability (even in absence of actinomycin D) rather than transcriptional activity.<br /> Therefore, the authors' statement that the non-actinomycin D treatment group represents transcriptional changes is not accurate here. Since EU labeling was stopped prior to the 4-hour incubation, any changes in EU-labeled RNA levels during this period reflect RNA decay, not new transcription.

In summary:<br /> To assess transcriptional changes, one would compare the amount of EU-labeled RNA synthesized during the initial labeling period (the first 3 hours), before washout.<br /> If the authors wish to use actinomycin D to block transcription, this should be done in a separate decay assay without EU labeling.<br /> In the current experimental setup, actinomycin D is unnecessary after EU washout and does not influence the decay of the labeled RNA.<br /> I recommend the authors reconsider the interpretation of their data accordingly. I recommend to remove the data points relative to the presence of actinomycin D, as the non-actinomycin D samples are already representative of post-transcriptional changes given that EU was washed out. If Authors want to assess transcriptional changes, they would have to assess the levels during the initial labeling period (before the washout). Transcriptional differences were not assessed, therefore I would modify the text accordingly.<br /> In this context, any changes observed in the actinomycin D-treated samples are likely attributable to general cellular stress induced by actinomycin D, which is known to be highly stressful for cells. This stress could indirectly influence the decay rates of already-labeled EU-RNA.

Figure 4C and 4D:<br /> The Author provided an updated gel with relative quantification - which effectively show the enhanced binding of CCL2 mRNA carrying the T variant to HuR - but they only provided it as data for reviewers (Figure R1). I highly recommend to use these data in the final manuscript instead of the data currently presented in Figure 4C and 4D. This would be important in order not to not create confusion in the reader or concerns regarding probe degradation or saturation.

Minor points<br /> For the IP, I recommend to explain in the final version why the input was not provided (lack of material) and to clarify that the specific binding of Actin was used as a loading control in absence of input. This would be highly beneficial for the readers.

Reviewer #1 (Public review):

Summary:

Chen et al. engineered and characterized a suite of next-generation GECIs for the Drosophila NMJ that allow for the visualization of calcium dynamics within the presynaptic compartment, at presynaptic active zones, and in the postsynaptic compartment. These GECIs include ratiometric presynaptic Scar8m (targeted to synaptic vesicles), ratiometric active zone localized Bar8f (targeted to the scaffold molecule BRP), and postsynaptic SynapGCaMP8m. The authors demonstrate that these new indicators are a large improvement on the widely used GCaMP6 and GCaMP7 series GECIs, with increased speed and sensitivity. They show that presynaptic Scar8m accurately captures presynaptic calcium dynamics with superior sensitivity to the GCaMP6 and GCaMP7 series and with similar kinetics to chemical dyes. The active-zone targeted Bar8f sensor was assessed for the ability to detect release-site-specific nanodomain changes, but the authors concluded that this sensor is still too slow to accurately do so. Lastly, the use of postsynaptic SynapGCaMP8m was shown to enable the detection of quantal events with similar resolution to electrophysiological recordings. Finally, the authors developed a Python-based analysis software, CaFire, that enables automated quantification of evoked and spontaneous calcium signals. These tools will greatly expand our ability to detect activity at individual synapses without the need for chemical dyes or electrophysiology.

Strengths:

(1) In this study, the authors rigorously compare their newly engineered GECIs to those previously used at the Drosophila NMJ, highlighting improvements in localization, speed, and sensitivity. These comparisons appropriately substantiate the authors' claim that their GECIs are superior to those currently in use.

(2) The authors demonstrate the ability of Scar8m to capture subtle changes in presynaptic calcium resulting from differences between MN-Ib and MN-Is terminals and from the induction of presynaptic homeostatic potentiation (PHP), rivaling the sensitivity of chemical dyes.

(3) The improved postsynaptic SynapGCaMP8m is shown to approach the resolution of electrophysiology in resolving quantal events.

(4) The authors created a publicly available pipeline that streamlines and standardizes analysis of calcium imaging data.

Weaknesses:

(1) Given the superior performance of GCaMP8m in the vesicle-tethered and postsynaptic applications, an analysis of its functionality at individual active zones ("Bar8m") would be a useful addition to this compendium, especially since the authors show that the faster kinetics of GCaMP8f are still not fast enough to resolve active zone-specific calcium dynamics.

(2) Description of the CaFire pipeline could be clearer (for example, what exactly is the role of Excel?), and the GitHub user guide could be more fleshed out (with the addition of example ImageJ scripts and analyzed images).

Reviewer #2 (Public review):

Summary

Calcium ions play a key role in synaptic transmission and plasticity. To improve calcium measurements at synaptic terminals, previous studies have targeted genetically encoded calcium indicators (GECIs) to pre- and postsynaptic locations. Here, Chen et al. improve these constructs by incorporating the latest GCaMP8 sensors and a stable red fluorescent protein to enable ratiometric measurements. In addition, they develop a new analysis platform, 'CaFire', to facilitate automated quantification. Using these tools, the authors demonstrate favorable properties of their sensors relative to earlier constructs. Impressively, by positioning postsynaptic GCaMP8m near glutamate receptors, they show that their sensors can report miniature synaptic events with speed and sensitivity approaching that of intracellular electrophysiological recordings. These new sensors and the analysis platform provide a valuable tool for resolving synaptic events using all-optical methods.

Strengths:

The authors present a rigorous characterization of their sensors using well-established assays. They employ immunostaining and super-resolution STED microscopy to confirm correct subcellular targeting. Additionally, they quantify response amplitude, rise and decay kinetics, and provide side-by-side comparisons with earlier-generation GECIs. Importantly, they show that the new sensors can reproduce known differences in evoked Ca²⁺ responses between distinct nerve terminals. Finally, they present what appears to be the first simultaneous calcium imaging and intracellular mEPSP recording to directly assess the sensitivity of different sensors in detecting individual miniature synaptic events.

Weaknesses:

Major points:

(1) While the authors rigorously compared the response amplitude, rise, and decay kinetics of several sensors, key parameters like brightness and photobleaching rates are not reported. I feel that including this information is important as synaptically tethered sensors, compared to freely diffusible cytosolic indicators, can be especially prone to photobleaching, particularly under the high-intensity illumination and high-magnification conditions required for synaptic imaging. Quantifying baseline brightness and photobleaching rates would add valuable information for researchers intending to adopt these tools, especially in the context of prolonged or high-speed imaging experiments.

(2) In several places, the authors compare the performance of their sensors with synthetic calcium dyes, but these comparisons are based on literature values rather than on side-by-side measurements in the same preparation. Given differences in imaging conditions across studies (e.g., illumination, camera sensitivity, and noise), parameters like indicator brightness, SNR, and photobleaching are difficult to compare meaningfully. Additionally, the limited frame rate used in the present study may preclude accurate assessment of rise times relative to fast chemical dyes. These issues weaken the claim made in the abstract that "...a ratiometric presynaptic GCaMP8m sensor accurately captures .. Ca²⁺ changes with superior sensitivity and similar kinetics compared to chemical dyes." The authors should clearly acknowledge these limitations and soften their conclusions. A direct comparison in the same system, if feasible, would greatly strengthen the manuscript.

(3) The authors state that their indicators can now achieve measurements previously attainable with chemical dyes and electrophysiology. I encourage the authors to also consider how their tools might enable new measurements beyond what these traditional techniques allow. For example, while electrophysiology can detect summed mEPSPs across synapses, imaging could go a step further by spatially resolving the synaptic origin of individual mEPSP events. One could, for instance, image MN-Ib and MN-Is simultaneously without silencing either input, and detect mEPSP events specific to each synapse. This would enable synapse-specific mapping of quantal events - something electrophysiology alone cannot provide. Demonstrating even a proof-of-principle along these lines could highlight the unique advantages of the new tools by showing that they not only match previous methods but also enable new types of measurements.

(4) For ratiometric measurements, it is important to estimate and subtract background signals in each channel. Without this correction, the computed ratio may be skewed, as background adds an offset to both channels and can distort the ratio. However, it is not clear from the Methods section whether, or how, background fluorescence was measured and subtracted.

(5) At line 212, the authors claim "... GCaMP8m showing 345.7% higher SNR over GCaMP6s....(Fig. 3D and E) ", yet the cited figure panels do not present any SNR quantification. Figures 3D and E only show response amplitudes and kinetics, which are distinct from SNR. The methods section also does not describe details for how SNR was defined or computed.

(6) Lines 285-287 "As expected, summed ΔF values scaled strongly and positively with AZ size (Fig. 5F), reflecting a greater number of Cav2 channels at larger AZs". I am not sure about this conclusion. A positive correlation between summed ΔF values and AZ size could simply reflect more GCaMP molecules in larger AZs, which would give rise to larger total fluorescence change even at a given level of calcium increase.

(7) Lines 313-314: "SynapGCaMP quantal signals appeared to qualitatively reflect the same events measured with electrophysiological recordings (Fig. 6D)." This statement is quite confusing. In Figure 6D, the corresponding calcium and ephys traces look completely different and appear to reflect distinct sets of events. It was only after reading Figure 7 that I realized the traces shown in Figure 6D might not have been recorded simultaneously. The authors should clarify this point.

(8) Lines 310-313: "SynapGCaMP8m .... striking an optimal balance between speed and sensitivity", and Lines 314-316: "We conclude that SynapGCaMP8m is an optimal indicator to measure quantal transmission events at the synapse." Statements like these are subjective. In the authors' own comparison, GCaMP8m is significantly slower than GCaMP8f (at least in terms of decay time), despite having a moderately higher response amplitude. It is therefore unclear why GCaMP8m is considered 'optimal'. The authors should clarify this point or explain their rationale for prioritizing response amplitude over speed in the context of their application.

Reviewer #3 (Public review):

Genetically encoded calcium indicators (GECIs) are essential tools in neurobiology and physiology. Technological constraints in targeting and kinetics of previous versions of GECIs have limited their application at the subcellular level. Chen et al. present a set of novel tools that overcome many of these limitations. Through systematic testing in the Drosophila NMJ, they demonstrate improved targeting of GCaMP variants to synaptic compartments and report enhanced brightness and temporal fidelity using members of the GCaMP8 series. These advancements are likely to facilitate more precise investigation of synaptic physiology.

This is a comprehensive and detailed manuscript that introduces and validates new GECI tools optimized for the study of neurotransmission and neuronal excitability. These tools are likely to be highly impactful across neuroscience subfields. The authors are commended for publicly sharing their imaging software.

This manuscript could be improved by further testing the GECIs across physiologically relevant ranges of activity, including at high frequency and over long imaging sessions. The authors provide a custom software package (CaFire) for Ca2+ imaging analysis; however, to improve clarity and utility for future users, we recommend providing references to existing Ca2+ imaging tools for context and elaborating on some conceptual and methodological aspects, with more guidance for broader usability. These enhancements would strengthen this already strong manuscript.

Reviewer #1 (Public review):

Summary:

This study probes the role of the NF-κB inhibitor IκBa in the regulation of pluripotency in mouse embyronic stem cells (mESCs). It follows from previous work that identified a chromatin-specific role for IκBa in the regulation of tissue stem cell differentiation. The work presented here shows that a fraction of IκBa specifically associates with chromatin in pluripotent stem cells. Using three Nfkbia-knockout lines, the authors show that IκBa ablation impairs the exit from pluripotency, with embryonic bodies (an in vitro model of mESC multi-lineage differentiation) still expressing high levels of pluripotency markers after sustained exposure to differentiation signals. The maintenance of aberrant pluripotency gene expression under differentiation conditions is accompanied by pluripotency-associated epigenetic profiles of DNA methylation and histone marks. Using elegant separation of function mutants identified in a separate study, the authors generate versions of IκBa that are either impaired in histone/chromatin binding or NF-κB binding. They show that the provision of the WT IκBa, or the NF-κB-binding mutant can rescue the changes in gene expression driven by loss of IκBa, but the chromatin-binding mutant can not. Thus the study identifies a chromatin-specific, NF-κB-independent role of IκBa as a regulator of exit from pluripotency.

Strengths:

The strengths of the manuscript lie in:<br /> (a) the use of several orthogonal assays to support the conclusions on the effects of exit from pluripotency;<br /> (b) the use of three independent clonal Nfkbia-KO mESC lines (lacking IκBa), which increase confidence in the conclusions; and<br /> (c) the use of separation of function mutants to determine the relative contributions of the chromatin-associated and NF-κB-associated IκBa, which would otherwise be very difficult to unpick.

Weaknesses:

No notable weaknesses remain in this revised version.

Reviewer #2 (Public review):

Summary:

This manuscript investigates the role of IκBα in regulating mouse embryonic stem cell (ESC) pluripotency and differentiation. The authors demonstrate that IκBα knockout impairs the exit from the naïve pluripotent state during embryoid body differentiation. Through mechanistic studies using various mutants, they show that IκBα regulates ESC differentiation through chromatin-related functions, independent of the canonical NF-κB pathway.

Strengths:

The authors nicely investigate the role of IκBα in pluripotency exit, using embryoid body formation and complementing the phenotypic analysis with a number of genome-wide approaches, including transcriptomic, histone marks deposition, and DNA methylation analyses. Moreover, they generate a first-of-its-kind mutant set that allows them to uncouple IκBα's function in chromatin regulation versus its NF-κB-related functions. This work contributes to our understanding of cellular plasticity and development, potentially interesting a broad audience including developmental biologists, chromatin biology researchers, and cell signaling experts.

Weaknesses:

Future experiments will likely help establish a more direct mechanistic link between IκBα activity and the chromatin remodeling events observed in pluripotent cells.

Reviewer #1 (Public review):

Summary:

The authors define the principles that, based on first principles, should be guiding the optimisation of transcription factors with intrinsically disordered regions (IDR). The authors introduce an original search process, coined "octopusing", that involves transcription factor IDR and their binding affinities to optimise search times and binding affinities. The first part concerns the optimal strategies to define binding affinities to the genome in the receiving region that is called the "antenna", highlighting the following: (i) reduce the target to IDR-binding distance on the genome, (ii) optimise the distance between the DNA binding domain and the binding sites on the IDR to be as close as possible to the distance between their binding sites on the genome; (iii) keep the same number of binding sites and their targets and modulate this number with binding strength, reducing them with increased strength; (iv) modulate the binding strength to be above a threshold that depends on the proportion of IDR binding sites in the antenna. The second part concerns the scaling of the search time in function of key parameters such as the volume of the nucleus, and the size of the antenna, derived as a combination of 3D search and 1D "octopusing". The third part focuses on validation, where the current results are compared to binding probability data from a single experiment, and new experiments are proposed to further validate the model as well as testing designed transcription factors.

Strengths:

The strength of this work is that it provides simple, interpretable and testable theoretical conclusions. This will allow the derived design principles to be understood, evaluated and improved in the future. The theoretical derivations are rigorous. The authors provide a comparison to experiments, and also propose new experiments to be performed in the future. This is a great value in the paper since it will set the stage and inspire new experimental techniques. Further, the field needs inspiration and motivation to develop these techniques, since they are required to benchmark the transcription factors designed with the methods presented in this paper, as well as to develop novel data based or in vivo methods that would greatly benefit the field. As such, this paper is a fundamental contribution to the field.

Weaknesses:

The model presents many first principles to drive the design of transcription factors, but arguably, other principles and mechanisms might also play a role by being beneficial to the search and binding process. These other principles are mentioned at the end of the discussion part of the paper. On the other hand, an important task left to do, is to critically consider these principles altogether, and analyse the available data to quantify which role is predominant among transcription factors IDRs functions. Further, since one function doesn't exclude another, a theoretical investigation of possible crosstalk, interaction, and cooperativity of those different hypothetical functions is still missing.

Reviewer #2 (Public review):

Summary:

This is an interesting theoretical exploration of how a flexible protein domain, which has multiple DNA-binding sites along it, affects the stability of the protein-DNA complex. It proposes a mechanism ("octopusing") for protein doing a random walk while bound to DNA which simultaneously enables exploration of the DNA strand and stability of the bound state.

Strengths:

Stability of the protein-DNA bound state and the ability of the protein to perform 1d diffusion along the DNA are two properties of a transcription factor that are usually seen as being in opposition of each other. The octopusing mechanism is an elegant resolution of the puzzle of how both could be accommodated. This mechanism has interesting biological implications for the functional role of intrinsically disordered domains in transcription factor (TF) proteins. They show theoretically how these domains, if flexible and able to make multiple weak contacts with the DNA, can enhance the ability of the TF to efficiently find their binding site on the DNA from which they exert control over the transcription of their target gene. The paper concludes with a comparison of model predictions with experimental data which gives further support to the proposed mechanism. Overall, this is an interesting and well-executed theoretical paper that proposes an interesting idea about the functional role for IDR domains in TFs.

Weaknesses:

It is not clear how ubiquitous among eukaryotic transcription factors are the DNA binding sites for multiple subdomains along the IDR, which are assumed by the model. These assumptions though, provide interesting points of departure for further experiments.

Reviewer #1 (Public review):

In their manuscript, Michelson et al use a combination of mesoscopic 1p and single-cell resolution 2p imaging to characterise cortical encoding of grooming behaviour. Despite their subcortical locus of control (and non-reliance on cortex), the authors report that grooming movements are accompanied by widespread activation of dorsal cortex. Different grooming movements elicit distinct spatiotemporal cortical activity patterns. They find that cortical engagement is greater at the beginning of grooming episodes than at their end. They also report greater cortical activation for atypical unilateral grooming movements seen under head-restraint in comparison to cortical activity during bilateral movements typical of unrestrained or spontaneous grooming.

While this is not the first study to report cortical representations of subcortically controlled behaviours, and the authors themselves cite many previous reports of cortical activation during locomotion and even grooming (Sjöbom et al 2020), the value of the present study lies in their use of imaging to reveal the widespread nature of cortical activation during execution of a complex, innate behaviour. I also appreciate the systematic approach used by the authors to break down grooming episodes into their constituent movements and reveal their transition structure.

I do have concerns, however, that some of the authors' claims are insufficiently supported by their results, and more analysis is required to convincingly rule out alternative interpretations.

(1) One possible explanation for the gradual decline in cortical activity is that unilateral movements associated with greater cortical activation dominate early in grooming episodes, whereas bilateral movements that elicit weaker cortical activity dominate later (Figure 3G and 2C). The authors could check whether cortical activity associated with the *same* grooming movement is constant or declines during such episodes. A related point: doesn't the regression analysis shown in Figure 3, Supplement 2, assume that a stationary relationship between movement and spatiotemporal patterns of cortical activity?

(2) From the decline in cortical responses during long grooming episodes, the authors suggest that "mesoscale cortical activity mostly reflects the initiation of subcortically-mediated behaviors, rather than the behavior itself". The authors have taken a lot of trouble to come up with a rich, detailed segmentation and clustering of the grooming behaviour into its constituent movements (Figure 1). Therefore, I am somewhat surprised that they make this claim solely from analysis of averaged cortical activity during nearly minute-long grooming episodes rather than a higher time resolution analysis of transitions between distinct grooming movements (like the prior study by Sjöbom et al and related work in striatal encoding of innate movement sequences by Markowitz et al).

(3) The authors find that unilateral, atypical grooming movements elicit cortical activity that is distinct from the more naturalistic bilateral movements. They interpret this as reflecting the temporal transition structure of the behaviour. However, an alternative explanation is that the differences (or similarities) in evoked activity simply reflect differences (or similarities) in the kinematics of these movements, with bilateral movements appearing more similar to each other than to unilateral movements. A related point: there is little description of the "non-grooming forelimb movements". Were these kinematically similar to the unilateral forelimb movements, which may explain why they cluster together in Figure 4H?

(4) Page 13, last paragraph: the authors suggest that similar encoding of non-grooming forelimb movements and unilateral grooming movements may reflect a shared reliance on the cortex. This is rather speculative. Several studies have demonstrated that voluntary unilateral movements employed for reaching or lever pressing are not generally reliant on the cortex (Whishaw et al, Beh Brain Res, 1991; Kawai et al, 2015). There isn't, in my opinion, a broad consensus for the authors' statement that "reaching for food is a cortex-dependent action". Rather than extrapolating from past studies, could the authors not experimentally assess whether unilateral grooming movements are more sensitive to cortical silencing than bilateral ones, possibly revealing a cortical locus of control?

Reviewer #2 (Public review):

Summary:

In this manuscript, Michelson, Gupta, and Murphy use calcium imaging to map the distribution of neural activity across the cerebral cortex of grooming, head-restrained mice. Animals groomed spontaneously and in response to wetting of the face. Individual movement elements, such as bilateral strokes across the face, resembled those observed in freely-moving animals. Sequencing of movement elements was structured, but did not consist of full "syntactic grooming chains." Widefield imaging across the cortex revealed distinct patterns of activity for distinct movement elements. Individual neurons responded strongly during movement and had largely similar properties across cortical areas.

Strengths:

In my opinion, this is a solid paper that will be of interest to the mouse sensorimotor neuroscience community. The experiments are technically sound, the text is well-written, and the figures are clear. The activity maps are presented in standardized Allen Atlas coordinates, and I expect they will be very useful for future studies of orofacial and limb movement.

Weaknesses:

While the manuscript provides a valuable description of cortical activity during head-restrained grooming, I think it could engage a bit more with contemporary theories and debates in cortical physiology and motor control. The Abstract nicely highlights an apparent paradox: the motor cortex sends strong projections to the spinal cord, and is strongly modulated during behaviors like grooming. Nevertheless, blocking corticospinal traffic by inactivating or lesioning the motor cortex leaves such behaviors intact. There are several potential resolutions to this paradox. First, cortical activity during grooming could be confined to an "output-null" subspace that is responsible for monitoring sensorimotor events and preparing voluntary movements, but does not drive muscle activity (c.f. work in the macaque: Kaufman et al., Nature Neuroscience 2014; Churchland & Shenoy, Nature Reviews Neuroscience 2024). Second, cortical activity during grooming could be transmitted to lower centers, but gated out through inhibition. Third, it is possible that cortical activity in intact animals does contribute to muscle activation during grooming, but following a lesion or inactivation, other descending pathways compensate for the cortical deficit. The authors might wish to discuss their findings in light of these considerations.

In the first paragraph of the Introduction, it could be made clearer which results are specific to mice. The Niell & Stryker finding, for example, holds in mice, but not marmosets (Liska et al., eLife 2024).

The "hotspots" in Figure 3G appear to be more anterior during bilateral elliptical than unilateral elliptical movements. How do the authors interpret this finding?

The distribution of single-neuron responses looks relatively similar across cortical areas, including forelimb, hindlimb, and trunk somatosensory cortex, and primary and secondary forelimb motor cortex. What do the authors make of this?

Reviewer #3 (Public review):

Summary:

The authors use a combination of a head-fixed grooming paradigm, single-photon mesoscale, and wide-field-of-view two-photon calcium imaging to characterize cortical activity patterns during evoked grooming. Previous work has shown that grooming behavior does not require cortex, but that there are neuronal representations of grooming in motor cortex. The authors extend these findings by showing cortex-wide activation patterns at the meso-scale that relate to distinct grooming elements. This activation is strongest at grooming onset, but declines over the course of extended grooming periods. They also find similar activity patterns during licking/drinking behavior. Two-photon imaging further revealed that individual neurons across the cortex are preferentially activated by grooming. While their activity also declines after grooming onset, they remain active throughout grooming periods. This work extends previous findings by revealing that grooming and other subcortically-generated behaviors may be represented not only in motor cortex, but across dorsal cortex, both on the mesoscale and single neuron levels. These findings may lead to further investigation into the role of cortical activity during subcortically generated behaviors.

Strengths:

(1) Detailed characterization of grooming behavior in a head-fixed paradigm.

(2) Combination of single photon mesoscale and two-photon wide field-of-view imaging to characterize grooming (and licking)-related activity across dorsal cortex on multiple levels

Weaknesses:

(1) The behavior observed in the head-fixed grooming paradigm only partially resembles spontaneous grooming, lacking typical elements of the syntactic chain, while additionally evoking non-typical behaviors, resembling unilateral reaches, making the interpretation of the observations and their relevance to natural behaviors difficult. Furthermore, the nature of the non-typical movements (which may be cortex-dependent while typical grooming is not) is not explored.

(2) Two important findings in relation to the neural representations of individual grooming behaviors remain unclear:

a) The authors state that individual grooming behaviors did not have distinct neuronal representations (except unilateral grooming; Figure 4G) - it remains unclear how this fits with the observation of distinct activation maps during the different grooming behaviors. Should this differential activation not also correspond to distinct activation patterns of 'grooming' neurons across the cortex? Or do they mean that the activity in the 'grooming' neurons is not consistent across grooming instances and therefore no distinct representation can be detected?

b) The authors state that the 'typical' grooming behaviors do not have consistent activation patterns across animals (Figure 3 and supplements). It remains, therefore, unclear what the averaged activation maps really represent. Furthermore, this observation leaves several open questions: Are the activation patterns consistent in individual animals? Do differences across animals emerge due to differences in their behavior? And most importantly, can the actual behavior be decoded from the activation patterns?

(3) Multiple statements/conclusions are not supported by quantification of the data, but only by qualitative assessments, e.g.: lines 433-435: "In general, the maximally activated networks involved in licking and unilateral grooming behaviors 'appeared' to be the most consistent across animals compared to the bilateral grooming movements (Figure 3G)."; 436-437: "Averaged cortical activation maps associated with licking and elliptical behaviors were 'qualitatively similar' between evoked and spontaneous sessions, where the water drop was not applied".; 480-482: "The unique explained variance maps for the licking behavior 'differed' in the drinking context compared to the grooming context (Figure 3-figure supplement 3F)." The lack of quantification leaves the significance of these observations unclear.

(4) It remains unclear what the ongoing activity in 'grooming' neurons represents, since there is no detailed analysis of the relationship between activity and the detailed kinematics of the grooming movements.

The authors show that neuronal representations of grooming and other subcortical behaviors can be found across dorsal cortex and that these representations are at least to some degree specific to distinct behavioral elements. While this study does not reveal functional insights into the role of cortical representations of subcortically-generated behaviors, it is a step towards more in-depth studies. In the future, it will be important to determine whether these representations are efference copies or sensory-driven, or whether they affect the behavior, and if so, under which circumstances.

Reviewer #2 (Public review):

General comments

We thank the reviewers and editor for their thoughtful feedback. We are glad that the minor comments appear resolved. In this revision, we added subject-specific analyses, further FC comparisons, and clarified our rationale for stimulation parameters. We acknowledge that two concerns remain: (1) the 1 mA-2 mA sequence may introduce confounds, and (2) electric field modeling was not included due to technical limitations. We now explicitly note these as limitations in the manuscript and provide justification and discussion accordingly.

Major comments

R.2.1. For the anesthetized monkeys, the anode location differs between subjects, with the electrode positioned to stimulate the left DLFPC in monkey R and the right DLPFC in monkey N. The authors mention that this discrepancy does not result in significant differences in the electric field due to the monkeys' small head size. However, this is incorrect, as placing the anode on the left hemisphere would result in a much lower EF in the right DLPFC than placing the anode on the right side. Running an electric field simulation would confirm this. Additionally, the small electrode size suggested by the Easy cap configuration for NHP appears sufficient to stimulate the targeted regions focally. If this interpretation is correct, the authors should provide additional evidence to support their claim, such as a computational simulation of the EF distribution.

R.2.1 Authors' answer: We thank the Reviewer for the comments. First, regarding the reviewer's statement that placing the anode on the left hemisphere would result in a much lower EF in the right DLPFC than placing the anode on the right side, we would like to clarify that we did not use a typical 4 x 1 concentric ring high-definition setup (which consists of a small centre electrode surrounded by four return electrodes), but a two-electrode montage, with one electrode over the left or right PFC and the other one over the contralateral occipital cortex. According to EF modelling papers, a 4 x 1 high-definition setup would produce an EF that is focused and limited to the cortical area circumscribed by the ring of the return electrodes (Datta et al. 2009; Alam et al. 2016). Therefore, targeting the left or right DLPFC with a 4 x 1 setup would produce an EF confined to the targeted hemisphere of the PFC. In contrast, we expect the brain current flow generated with our 2-electrode setup to be broader, despite the small size of the electrodes, because there is no constraint from return electrodes. Thus, with our setup, the current is expected to flow between the PFC and the occipital cortex (see also our responses to comments R3.3., R.E.C.#2.1. and R.E.C.#2.2.).

Second, we would like to point out that in awake experiments, in which we stimulated the right PFC of both monkeys, there was no gross evidence of left or right asymmetry in the computed functional connectivity patterns (Figure 3A, Figure 3 - figure supplement 2A; Figure 5A). These results, showing that our stimulation montages did not induce asymmetric dynamic FC changes in NHPs, support the idea that our setups did not generate EFs that were spatially focused enough to alter brain activity in one hemisphere substantially more than the other.

Third, it is also worth noting that current evidence suggests that human brains are significantly more lateralized than those of macaques. Macaque monkeys have been found to have some degree of lateralized networks, but these are of lower complexity, and the lateralization is less pronounced and functionally organized than in humans. (Whey et al., 2014; Mantini et al., 2013). This suggests that, even if the stimulation were focal enough to stimulate the left or the right part of the PFC only, the behavioural effects would likely be similar.

Follow-up comment: Thank you for the detailed response and for referencing both experimental data and prior literature. While I appreciate the discussion on the lack of functional asymmetry and reduced lateralization in macaques, my original concern was about the physical distribution of the electric field (EF) due to different anode placements. Functional connectivity outcomes do not necessarily reflect EF symmetry, and without EF modeling, it's difficult to determine whether the stimulation affected both hemispheres equally. I understand the challenges of NHP-specific modeling, but even a simplified simulation or acknowledgment of this limitation in the manuscript would help clarify the interpretability of your results.

R.2.2. For the anesthetized monkeys, the authors applied 1 mA tDCS first, followed by 2 mA tDCS. A 20-minute stimulation duration of 1 mA tDCS is strong enough to produce after-effects that could influence the brain state during the 2 mA tDCS. This raises some concerns. Previous studies have shown that 1 mA tDCS can generate EF of over 1 V/m in the brain, and the effects of stimulation are sensitive to brain state (e.g., eye closed vs. eye open). How do the authors ensure that there are no after-effects from the 1 mA tDCS? This issue makes it challenging to directly compare the effects of 1 mA and 2 mA stimulation.<br /> R.2.2 Authors' answer: We agree with the reviewer's comment that 1 mA tDCS may induce aftereffects, as has been observed in several human studies (e.g., (Jamil et al. 2017, 2020). Although the differences between the 1 mA post-stimulation and baseline conditions were not significant in our analyses, it's still possible that the stimulation produced some effects below the threshold of significance that may contribute, albeit weakly, to the changes observed during

Follow-up comment: Thank you for the clarification and for acknowledging the potential for 1 mA after-effects. While I appreciate the authors' transparency and the amendment to the manuscript, I still find it important that the limitation be clearly stated in the Discussion section. The fact that 2 mA stimulation always followed 1 mA introduces a potential confound, making it difficult to attribute observed changes uniquely to 2 mA. If a counterbalanced design was not feasible, I would recommend explicitly noting this as a limitation in the interpretation of dose-dependent effects.

R.2.3. The occurrence rate of a specific structural-functional coupling pattern among random brain regions shows significant effects of tDCS. However, these results seem counterintuitive. It is generally understood that non-invasive brain stimulation tends to modulate functional connectivity rather than structural or structural-functional connectivity. How does the occurrence rate of structural-functional coupling patterns provide a more suitable measure of the effectiveness of tDCS than functional connectivity alone? I would recommend that the authors present the results based on functional connectivity itself. If there is no change in functional connectivity, the relevance of changes in structural-functional coupling might not translate into a meaningful alteration in brain function, making it unclear how significant this finding is without corresponding functional evidence.

R.2.3. Authors' answer: First of all, we would like to make it clear that the occurrence rate of patterns as a function of their SFC is not intended to be used or seen as a 'better' measure of the efficacy of tDCS. Instead, it is one aspect of the effects of tDCS on whole-brain functional cortical dynamics, obtained from refined measures (phase-coherences), that specifically addresses the coupling between structure and function. This type of analysis is further motivated by its increasing use in the literature due to its suspected relationship to wakefulness (e.g., (Barttfeld et al. 2015, Demertzi et al. 2019; Castro et al. 2023)). Also, in our analysis, the structure is kept constant: the connectivity matrix used to correlate the functional brain states is always the same (CoCoMac82). Thus, the influence of tDCS on the structure-function side can only be explained by modulating the functional aspects, as suggested by intuition and previous results.

Then, we agree with the reviewer that studying the functional changes induced by tDCS alone could be valuable. However, usual metrics used in FC analysis are usually done statistically: FC-states are either computed through averaging spatial correlations over time, then analyzed through graph-theoretical properties for instance (or by just directly computing the element-wise differences), or either by considering the properties of the different visited FC-states by computing spatial correlations over a sliding time-window, and then similar analysis can be done as previously explained. But these are static metrics, if the states visited are essentially the same (which is expected from non-invasive neuromodulations that haven't already demonstrated strong and/or characteristic impact), but the dynamical process of visiting said states changes, one would see no difference in that regard. As such, in the case of resting-state fMRI, differences in FCs are hard to interpret given that between-sessions within-condition differences are usually found with some degree of variance for the respective conditions. Trying then to interpret between-condition differences is quite tricky in the case of subtle modulations of the system's activity. On the other hand, more subtle differences can be captured by considering more detailed analysis, such as using phase-based methods like we did, by incorporating some statistical learning component with regard to the dynamicity of the system (supervised learning for instance like we did followed by temporal & transition-based methodology), and by adding some dimensions along which one will be able to give some interpretation to the analysis. In our case we were interested in characterizing resting-state differences between stimulation conditions, which have nuanced and subtle interactions with the biological system. As such, classical measures of differences between FC states are likely to not be refined and precise enough. In fact, we propose additional files investigating those classically used measures such as differences in average FC matrices, or changes in functional graph properties (like modularity, efficiency and density) of the visited FC states. These figures show that, for the first case, comparing region-to-region specific FCs provides very few statistically significant results. With respect to the second part, we show that virtually no differences are observed in the properties of the functional states visited. These results suggest, as expected, that the actual brain states visited across the different stimulation conditions are topologically quite similar, and that only very few region-specific pairwise functional connectivities are particularly modulated by specific tDCS montages while, on the other hand, the actual dynamical process dictating how the brain activity passes from one state to another is in fact being influenced as shown by the dynamical analysis presented in the main figures in a more apparent and meaningful way (in that it is dependent on the montage, somewhat consistent with regard to the post-stimulations conditions, and can be made sense of by considering the theoretical effect of near-anodal versus near-cathodal neuromodulatory effects).

Actions in the text: We have added new supplementary files showing the effects of the stimulations on FC matrices and on classical functional graph properties in awake and anesthesia datasets (Supplementary Files 3 & 4). We have added new sentences about these new analyses on the effects of the stimulations on FC matrices and on classical functional graph properties in the Results section:<br /> Follow-up comment: Thank you for the detailed and comprehensive response. The clarification regarding the use of SFC dynamics and the additional analyses provided are convincing.

R2.4. The authors recorded data from only two monkeys, which may limit the investigation of the group effects of tDCS. As the number of scans for the second monkey in each consciousness condition is lower than that in the first monkey, there is a concern that the main effects might primarily reflect the data from a single monkey. I suggest that the authors should analyze the data for each monkey individually to determine if similar trends are observed in both subjects.

R.2.4. Authors' answer: We agree that the small number of subjects is a limitation of our study. However, we have already addressed these aspects by reporting statistical analyses that consider them, using linear models of such variables, and running them through ANOVA tests. In addition, we experimentally ensured that we recorded a relatively high number of sessions over a period of several years. Regardless, we agree that our study would benefit from further investigation into this matter. We have therefore prepared complementary figures showing the main analysis performed separately for the two monkeys as proposed, as well as further investigations into the inter-condition variability outmatching the inter-individual variability, itself being also outmatched by intra-individual changes.

Actions in the text: We have added a supplementary file showing the main analyses performed separately for the two monkeys (Supplementary File 2) and further investigations into the inter-condition variability (Supplementary Files 3 & 4). We have added new sentences about these analyses performed separately for the two monkeys in the Results section:

Follow-up comment: Thank you for addressing this concern and for providing the individual monkey analysis. The additional figures and statistical explanations are helpful and appreciated.

R2.5. Anodal tDCS was only applied to anesthetized monkeys, which limits the conclusion that the authors are aiming for. It raises questions about the conclusion regarding brain state dependency. To address this, it would be better to include the cathodal tDCS session for anesthetized monkeys. If cathodal tDCS changes the connectivity during anesthesia, it becomes difficult to argue that the effects of cathodal tDCS vary depending on the state of consciousness as discussed in this paper. On the other hand, if cathodal tDCS would not produce any changes, the conclusion would then focus on the relationship between the polarity of tDCS and consciousness. In that case, the authors could maintain their conclusion but might need to refine it to reflect this specific relationship more accurately.

R.2.5. Authors' answer: We agree with the reviewer that it would have been interesting to investigate the effects of cathodal tDCS in anesthetized monkeys. However, due to the challenging nature of the experimental procedures under anesthesia, we had to limit the investigations to only one stimulation modality. We chose to deliver anodal stimulation because, from a translational point of view, we aimed to provide new information on the effects of tDCS under anesthesia as a model for disorders of consciousness. It also made much more sense to increase the cortical excitability of the prefrontal cortex in an attempt to wake up the sedated monkeys rather than doing the opposite.

Actions in the text: We have added a new sentence in the Results section:

"Due to the challenging nature of the experimental procedures under anesthesia, we limited the investigations to only one stimulation modality. We chose to deliver anodal stimulation to provide new information on the effects of tDCS under anesthesia as a model for disorders of consciousness and to increase the cortical excitability of the PFC in an attempt to wake up the sedated monkeys."

Follow-up comment: Thank you for clarifying the rationale behind applying only anodal stimulation under anesthesia. While I appreciate the experimental constraints and the translational motivation, I would still encourage the authors to explicitly acknowledge in the Discussion that the absence of a cathodal condition under anesthesia limits the ability to dissociate polarity-specific effects from state-dependent effects. This clarification would help temper the conclusions and better reflect the scope of the current dataset.

Reviewer #3 (Public review):

Summary:

This study used transcranial direct current stimulation administered using small 'high definition' electrodes to modulate neural activity within the non-human primate prefrontal cortex during both wakefulness and anaesthesia. Functional magnetic resonance imaging (fMRI) was used to assess neuromodulatory effects of stimulation. The authors report on modification of brain dynamics during and following anodal and cathodal stimulation during wakefulness and following anodal stimulation at two intensities (1 mA, 2 mA) during anaesthesia. This study provides some support that prefrontal direct current stimulation can alter neural activity patterns across wakefulness and sedation in monkeys.

Strengths and Weaknesses:

A key strength of this work is the use of fMRI-based methods to track changes in brain activity with good spatial precision. Another strength is the exploration of stimulation effects across wakefulness and sedation, which has the potential to provide novel information on the impact of electrical stimulation across states of consciousness. The authors should be commended for undertaking this challenging and important work.

The lack of a sham stimulation condition is a limitation of the study, as it somewhat restricts the certainty with which the results can be attributed to the active stimulation as opposed to other external factors such as drowsiness or fatigue as a result of the experimental procedure? Nevertheless, I acknowledge the demanding nature of performing this work in non-human primates and that only runs with high fixation rates were included, which should have helped reduce any fatigue-related effects.

In the anaesthesia condition, the authors investigated the effects of two intensities of stimulation (1 mA and 2 mA). However, it is possible that the initial 1 mA stimulation block might have caused some level of plasticity-related changes in neural activity that could have potentially interfered with the following 2 mA block due to the lack of a sufficient wash-out period. This potentially limits the findings from the 2 mA block as they cannot be interpreted as completely separate to the initial 1 mA stimulation period, given that they were administered consecutively. However, I do acknowledge the author's point that differences between the 1 mA post-stimulation and baseline conditions were not significantly different, which provides some evidence against this possibility.

The different electrode placement for the two anaesthetised monkeys (i.e., Monkey R: F3/O2 montage, Monkey N: F4/O1 montage) is potentially problematic, as it might have resulted in stimulation over different brain regions. Electric field models of brain current flow for the monkeys would really be needed to understand with reasonable certainty, however, I recognise that these models are generally designed for human studies making their integration into non-human primate studies challenging.

Finally, the sample size is obviously small. However, I realise this is often a limitation in non-human primate research, which can be both expensive and labour intensive.

Assessment:

This manuscript presents some novel insights into the effects of transcranial direct current stimulation on functional brain dynamics in awake and anaesthetised monkeys using MRI-based connectivity indices. Overall, the study presents several interesting and potentially impactful findings regarding stimulation-induced changes in brain activity. There are some limitations, such as the small sample size, lack of a sham stimulation control, and lack of electric field models, which, if included, would have, in my view, further helped improve the rigour of the study. Nevertheless, the manuscript presents several important findings, which warrant further analysis in future work.

Reviewer #1 (Public review):

The manuscript by Sayeed et al. uses a comprehensive series of multi-omics approaches to demonstrate that late-stage human cytomegalovirus (HCMV) infection leads to a marked disruption of TEAD1 activity, a concomitant loss of TEAD1-DNA interactions, and extensive chromatin remodeling. The data are thoroughly presented and provide evidence for the role of TEAD1 in the cellular response to HCMV infection.

However, a key question remains unresolved: is the observed disruption of TEAD1 activity a direct consequence of HCMV infection, or could it be secondary to the broader innate antiviral response? In this respect, the study would benefit from more in-depth experiments that assess the effect of TEAD1 overexpression or knockdown/deletion on HCMV replication dynamics. The new data provided by the authors in Reviewer Response Figures 1 and 2 suggest that the presence of constitutively expressed TEAD1 does not substantially impact HCMV replication and gene expression as assessed at 72 and 96 hours post-infection. However, this does not discount the fact that HCMV infection induces significant TEAD1-related chromatin changes that may impact other cellular functions.

Reviewer #2 (Public review):

Summary:

This work uses genomic and biochemical approaches for HCMV infection in human fibroblasts and retinal epithelial cell lines, followed by comparisons and some validations using strategies such as immunoblots. Based on these analyses, they propose several mechanisms that could contribute to the HCMV-induced diseases, including closing of TEAD1-occupying domains and reduced TEAD1 transcript and protein levels, decreased YAP1 and phospho-YAP1 levels, and exclusion of TEAD1 exon 6. Some functional assays, using over-expression of TEAD1, are provided.

Strengths:

The genomics experiments were done in duplicates and data analyses show good technical reproducibility. Data analyses are performed to show changes at the transcript and chromatin level changes, followed by some Western blot validations.

Weaknesses:

For readers who are outside the field, some clarifications of the system and design would be helpful.

Reviewer #1 (Public review):

Summary:

There is growing appreciation for the important of luminal (apical) ECM in tube development, but such matrices are much less well understood than basal ECMs. Here the authors provide insights into the aECM that shapes the Drosophila salivary gland (SG) tube and the importance of PAPSS-dependent sulfation in its organization and function.

The first part of the paper focuses on careful phenotypic characterization of papss mutants, using multiple markers and TEM. This revealed reduced markers of sulfation and defects in both apical and basal ECM organization, Golgi (but not ER) morphology, number and localization of other endosomal compartments, plus increased cell death. The authors focus on the fact that papss mutants have an irregular SG lumen diameter, with both narrowed regions and bulged regions. They address the pleiotropy, showing that preventing the cell death and resultant gaps in the tube did not rescue the SG luminal shape defects and discussing similarities and differences between the papss mutant phenotype and those caused by more general trafficking defects. The analysis uses a papss nonsense mutant from an EMS screen - I appreciate the rigorous approach the authors took to analyze transheterozygotes (as well as homozygotes) plus rescued animals in order to rule out effects of linked mutations. Importantly, the rescue experiments also demonstrated that sulfation enzymatic activity is important.

The 2nd part of the paper focuses on the SG aECM, showing that Dpy and Pio ZP protein fusions localize abnormally in papss mutants and that these ZP mutants (and Np protease mutants) have similar SG lumen shaping defects to the papss mutants. A key conclusion is that SG lumen defects correlate with loss of a Pio+Dpy-dependent filamentous structure in the lumen. These data suggest that ZP protein misregulation could explain this part of the papss phenotype.

Overall, the text is very well written and clear. Figures are clearly labeled. The methods involve rigorous genetic approaches, microscopy, and quantifications/statistics and are documented appropriately. The findings are convincing.

Significance:

This study will be of interest to researchers studying developmental morphogenesis in general and specifically tube biology or the aECM. It should be particularly of interest to those studying sulfation or ZP proteins (which are broadly present in aECMs across organisms, including humans).

This study adds to the literature demonstrating the importance of luminal matrix in shaping tubular organs and greatly advances understanding of the luminal matrix in the Drosophila salivary gland, an important model of tubular organ development and one that has key matrix differences (such as no chitin) compared to other highly studied Drosophila tubes like the trachea.

The detailed description of the defects resulting from papss loss suggests that there are multiple different sulfated targets, with a subset specifically relevant to aECM biology. A limitation is that specific sulfated substrates are not identified here (e.g. are these the ZP proteins themselves or other matrix glycoproteins or lipids?); therefore, it's not clear how direct or indirect the effects of papss are on ZP proteins. However, this is clearly a direction for future work and does not detract from the excellent beginning made here.

Comments on revised version:

Overall, I am pleased with the authors' revisions in response to my original comments and those of the other reviewers

Reviewer #2 (Public review):

Summary

This study provides new insights into organ morphogenesis using the Drosophila salivary gland (SG) as a model. The authors identify a requirement for sulfation in regulating lumen expansion, which correlates with several effects at the cellular level, including regulation of intracellular trafficking and the organization of Golgi, the aECM and the apical membrane. In addition, the authors show that the ZP proteins Dumpy (Dpy) and Pio form an aECM regulating lumen expansion. Previous reports already pointed to a role for Papss in sulfation in SG and the presence of Dpy and Pio in the SG. Now this work extends these previous analyses and provides more detailed descriptions that may be relevant to the fields of morphogenesis and cell biology (with particular focus on ECM research and tubulogenesis). This study nicely presents valuable information regarding the requirements of sulfation and the aECM in SG development.

Strengths

-The results supporting a role for sulfation in SG development are strong. In addition, the results supporting the involvement of Dpy and Pio in the aECM of the SG, their role in lumen expansion, and their interactions, are also strong.

-The authors have made an excellent job in revising and clarifying the many different issues raised by the reviewers, particularly with the addition of new experiments and quantifications. I consider that the manuscript has improved considerably.

-The authors generated a catalytically inactive Papss enzyme, which is not able to rescue the defects in Papss mutants, in contrast to wild type Papss. This result clearly indicates that the sulfation activity of Papss is required for SG development.

Weaknesses

-The main concern is the lack of clear connection between sulfation and the phenotypes observed at the cellular level, and, importantly, the lack of connection between sulfation and the Pio-Dpy matrix. Indeed, the mechanism/s by which sulfation affects lumen expansion are not elucidated and no targets of this modification are identified or investigated. A direct (or instructive) role for sulfation in aECM organization is not clearly supported by the results, and the connection between sulfation and Pio/Dpy roles seems correlative rather than causative. As it is presented, the mechanisms by which sulfation regulates SG lumen expansion remains elusive in this study.

-In my opinion the authors overestimate their findings with several conclusions, as exemplified in the abstract:

"In the absence of Papss, Pio is gradually lost in the aECM, while the Dpy-positive aECM structure is condensed and dissociates from the apical membrane, leading to a thin lumen. Mutations in dpy or pio, or in Notopleural, which encodes a matriptase that cleaves Pio to form the luminal Pio pool, result in a SG lumen with alternating bulges and constrictions, with the loss of pio leading to the loss of Dpy in the lumen. Our findings underscore the essential role of sulfation in organizing the aECM during tubular organ formation and highlight the mechanical support provided by ZP domain proteins in maintaining luminal diameter."

The findings leading to conclude that sulfation organizes the aECM and that the absence of Papss leads to a thin lumen due to defects in Dpy/Pio are not strong. The authors certainly show that Papss is required for proper Pio and Dpy accumulation. They also show that Pio is required for Dpy accumulation, and that Pio and Dpy form an aECM required for lumen expansion. However, the absence of Pio and Dpy do not fully recapitulate Papss mutant defects (thin lumen). I wonder whether other hypothesis and models could account for the observed results. For instance, a role for Papss affecting secretion, in which case sulfation would have an indirect role in aECM organization. This study does not address the mechanical properties of Dpy in normal and mutant salivary glands.

-Minor issues relate to the genotype/phenotype analysis. It is surprising that the authors detect only mild effects on sulfation in Papss mutants using an anti-sulfoTyr antibody, as Papss is the only Papss synthathase. Generating germ line clones (which is a feasible experiment) would have helped to prove that this minor effect is due to the contribution of maternal product. The loss of function allele used in this study seems problematic, as it produces effects in heterozygous conditions difficult to interpret. Cleaning the chromosome or using an alternative loss of function condition (another allele, RNAi, etc...) would have helped to present a more reliable explanation.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors use anatomical tracing and slice physiology to investigate the integration of thalamic (ATN) and retrosplenial cortical (RSC) signals in the dorsal presubiculum (PrS). This work will be of interest to the field, as postsubiculum is thought to be a key region for integrating internal head direction representations with external landmarks. The main result is that ATN and RSC inputs drive the same L3 PrS neurons, which exhibit superlinear summation to near-coincident inputs. Moreover, this activity can induce bursting in L4 PrS neurons, which can pass the signals LMN (perhaps gated by cholinergic input).

Strengths:

The slice physiology experiments are carefully done. The analyses are clear and convincing, and the figures and results are well composed. Overall, these results will be a welcome addition to the field.

Weaknesses:

The conclusions about the circuit-level function of L3 PrS neurons sometimes outstrip the data, and their model of the integration of these inputs is unclear. I would recommend some revision of the introduction and discussion. I also had some minor comments about the experimental details and analysis.

Specific major comments:

(1) I found that the authors' claims sometimes outstrip their data, given that there were no in vivo recordings during behavior. For example, in the abstract that their results indicate "that layer 3 neurons can transmit a visually matched HD signal to medial entorhinal cortex", and in the conclusion they state "[...] cortical RSC projections that carry visual landmark information converge on layer 3 pyramidal cells of the dorsal presubiculum". However, they never measured the nature of the signals coming from ATN and RSC to L3 PrS (or signals sent to downstream regions). Their claim is somewhat reasonable with respect to ATN, where the majority of neurons encode HD, but neurons in RSC encode a vast array of spatial and non-spatial variables other than landmark information (e.g., head direction, egocentric boundaries, allocentric position, spatial context, task history to name a few), so making strong claims about the nature of the incoming signals is unwarranted.

(2) Related to the first point, the authors hint at, but never explain, how coincident firing of ATN and RSC inputs would help anchor HD signals to visual landmarks. Although the lesion data (Yoder et al. 2011 and 2015) support their claims, it would be helpful if the proposed circuit mechanism was stated explicitly (a schematic of their model would be helpful in understanding the logic). For example, how do neurons integrate the "right" sets of landmarks and HD signals to ensure a stable anchoring? Moreover, it would be helpful to discuss alternative models of HD-to-landmark anchoring, including several studies that have proposed that the integration may (also?) occur in RSC (Page & Jeffrey, 2018; Yan, Burgess, Bicanski, 2021; Sit & Goard, 2023). Currently, much of the Discussion simply summarizes the results of the study, this space could be better used in mapping the findings to the existing literature on the overarching question of how HD signals are anchored to landmarks.

Comments on revised version:

The authors addressed all of my major points and most of my minor points in the revised submission.

Reviewer #2 (Public review):

Richevaux et al investigate how anterior thalamic (AD) and retrosplenial (RSC) inputs are integrated by single presubicular (PrS) layer 3 neurons. They show that these two inputs converge onto single PrS layer 3 principal cells. By performing dual wavelength photostimulation of these two inputs in horizontal slices, the authors show that in most layer 3 cells, these inputs summate supra-linearly. They extend the experiments by focusing on putative layer 4 PrS neurons and show that they do not receive direct anterior thalamic nor retrosplenial inputs; rather, they are (indirectly) driven to burst firing in response to strong activation of the PrS network.

This is a valuable study, which investigates an important question - how visual landmark information (possibly mediated by retrosplenial inputs) converges and integrates with HD information (conveyed by the AD nucleus of the thalamus) within PrS circuitry. The data indicate that near-coincident activation of retrosplenial and thalamic inputs leads to non-linear integration in target layer 3 neurons, thereby offering a potential biological basis for landmark + HD binding.

Main limitations relate to the anatomical annotation of 'putative' PrS L4 neurons, and to the presentation of retrosplenial / thalamic input modularity. Specifically, more evidence should be provided to convincingly demonstrate that the 'putative L4 neurons' of the PrS are not distal subicular neurons (as the authors' anatomy and physiology experiments seem to indicate). The modularity of thalamic and retrosplenial inputs could be better clarified in relation to the known PrS modularity.

Reviewer #3 (Public review):

Summary:

The authors sought to determine, at the level of individual presubiculum pyramidal cells, how allocentric spatial information from retrosplenial cortex was integrated with egocentric information from the anterior thalamic nuclei. Employing a dual opsin optogenetic approach with patch clamp electrophysiology, Richevaux and colleagues found that around three quarters of layer 3 pyramidal cells in presubiculum receive monosynaptic input from both brain regions. While some interesting questions remain (e.g. the role of inhibitory interneurons in gating the information flow and through different layers of presubiculum, this paper provides valuable insights into the microcircuitry of this brain region and the role that it may play in spatial navigation.

Strengths:

One of the main strengths of this manuscript was that the dual opsin approach allowed the direct comparison of different inputs within an individual neuron, helping to control for what might otherwise have been an important source of variation. The experiments were well-executed and the data rigorously analysed. The conclusions were appropriate to the experimental questions and were well-supported by the results. These data will help to inform in vivo experiments aimed at understanding the contribution of different brain regions in spatial navigation and could be valuable for computational modelling.

Weaknesses:

Some attempts were made to gain mechanistic insights into how inhibitory neurotransmission may affect processing in presubiuclum (e.g. figure 5) but these experiments were a little underpowered and the analysis carried out could have been more comprehensively undertaken, as was done for other experiments in the manuscript.

Comments on revised version:

The authors have addressed all of my comments and I have nothing further to add. Well done for an interesting and valuable contribution!

Reviewer #1 (Public review):

In this study, the authors identified an insect salivary protein LssaCA participating viral initial infection in plant host. LssaCA directly bond to RSV nucleocapsid protein and then interacted with a rice OsTLP that possessed endo-β-1,3-glucanase activity to enhance OsTLP enzymatic activity and degrade callose caused by insects feeding. The manuscript suffers from fundamental logical issues, making its central narrative highly unconvincing.

(1) These results suggested that LssaCA promoted RSV infection through a mechanism occurring not in insects or during early stages of viral entry in plants, but in planta after viral inoculation. As we all know that callose deposition affects the feeding of piercing-sucking insects and viral entry, this is contradictory to the results in Fig. S4 and Fig 2. It is difficult to understand callose functioned in virus reproduction in 3 days post virus inoculation. And authors also avoided to explain this mechanism.

(2) Missing significant data. For example, the phenotypes of the transgenic plants, the RSV titers in the transgenic plants (OsTLP OE, ostlp). The staining of callose deposition were also hard to convince. The evidence about RSV NP-LssaCA-OsTLP tripartite interaction to enhance OsTLP enzymatic activity is not enough.

(3) Figure 4a, there was the LssaCA signal in the fourth lane of pull-down data. Did MBP also bind LsssCA? The characterization of pull-down methods was rough a little bit. The method of GST pull-down and MBP pull-down should be characterized more in more detail.

Reviewer #1 (Public review):

Summary:

The paper reports an analysis of whole-genome sequence data from 40 Faroese. The authors investigate aspects of demographic history and natural selection in this population. The key findings are that the Faroese (as expected) have a small population size and are broadly of Northwest European ancestry. Accordingly, selection signatures are largely shared with other Northwest European populations, although the authors identify signals that may be specific to the Faroes. Finally, they identify a few predicted deleterious coding variants that may be enriched in the Faroes.

Strengths:

The data are appropriately quality-controlled and appear to be of high quality. Some aspects of the Faroese population history are characterized, in particular, by the relatively (compared to other European populations) high proportion of long runs of homozygosity, which may be relevant for disease mapping of recessive variants. The selection analysis is presented reasonably, although as the authors point out, many aspects, for example differences in iHS, can reflect differences in demographic history or population-specific drift and thus can't reliably be interpreted in terms of differences in the strength of selection.

Weaknesses:

The main limitations of the paper are as follows:

(1) The data are not available. I appreciate that (even de-identified) genotype data cannot be shared; however, that does substantially reduce the value of the paper. Minimally, I think the authors should share summary statistics for the selection scans, in line with the standard of the field.

(2) The insight into the population history of the Faroes is limited, relative to what is already known (i.e., they were settled around 1200 years ago, by people with a mixture of Scandinavian and British ancestry, have a small effective population size, and any admixture since then comes from substantially similar populations). It's obvious, for example, that the Faroese population has a smaller bottleneck than, say, GBR.

More sophisticated analyses (for example, ARG-based methods, or IBD or rare variant sharing) would be able to reveal more detailed and fine-scale information about the history of the populations that is not already known. PCA, ADMIXTURE, and HaplotNet analysis are broad summaries, but the interesting questions here would be more specific to the Faroes, for example, what are the proportions of Scandinavian vs Celtic ancestry? What is the date and extent of sex bias (as suggested by the uniparental data) in this admixture? I think that it is a bit of a missed opportunity not to address these questions.

(3) I don't really understand the rationale for looking at HLA-B allele frequencies. The authors write that "ankylosing spondylitis (AS) may be at a higher prevalence in the Faroe Islands (unpublished data), however, this has not been confirmed by follow-up epidemiological studies". So there's no evidence (certainly no published evidence) that AS is more prevalent, and hence nothing to explain with the HLA allele frequencies?

Reviewer #2 (Public review):

In this paper, Hamid et al present 40 genomes from the Faroe Islands. They use these data (a pilot study for an anticipated larger-scale sequencing effort) to discuss the population genetic diversity and history of the sample, and the Faroes population. I think this is an overall solid paper; it is overall well-polished and well-written. It is somewhat descriptive (as might be expected for an explorative pilot study), but does make good use of the data.

The data processing and annotation follows a state-of-the-art protocol, and at least I could not find any evidence in the results that would pinpoint towards bioinformatic issues having substantially biased some of the results, and at least preliminary results lead to the identification of some candidate disease alleles, showing that small, isolated cohorts can be an efficient way to find populations with locally common, but globally rare disease alleles.

I also enjoyed the population structure analysis in the context of ancient samples, which gives some context to the genetic ancestry of Faroese, although it would have been nice if that could have been quantified, and it is unfortunate that the sampling scheme effectively precludes within-Faroes analyses.

I am unfortunately quite critical of the selection analysis, both on a statistical level and, more importantly, I do not believe it measures what the authors think it does.

Major comments:

(1) Admixture timing/genomic scaling/localization:<br /> As the authors lay out, the Faroes were likely colonized in the last 1,000-1,500 years, i.e., 40-60 generations ago. That means most genomic processes that have happened on the Faroese should have signatures that are on the order of ~1-2cM, whereas more local patterns likely indicate genetic history predating the colonization of the islands. Yet, the paper seems to be oblivious to this (to me) fascinating and somewhat unique premise. Maybe this thought is wrong, but I think the authors miss a chance here to explain why the reader should care beyond the fact that the small populations might have high-frequency risk alleles and the Faroes are intrinsically interesting, but more importantly, it also makes me think it leads to some misinterpretations in the selection analysis

(2) ROH:<br /> Would the sampling scheme impact ROH? How would it deal with individuals with known parental coancestry? As an example of what I mean by my previous comment, 1MB is short enough in that I would expect most/many 1MB ROH-tracts to come from pedigree loops predating the colonization of the Faroes. (i.e, I am actually quite surprised that there isn't much more long ROH, which makes me wonder if that would be impacted by the sampling scheme).

(3) Selection scan:

We are talking about a bottlenecked population that is recently admixed (Faroese), compared to a population (GBR) putatively more closely related to one of its sources. My guess would be that selection in such a scenario would be possibly very hard to detect, and even then, selection signals might not differentiate selection in Faroese vs. GBR, but rather selection/allele frequency differences between different source populations. I think it would be good to spell out why XP-EHH/iHS measures selection at the correct time scale, and how/if these statistics are expected to behave differently in an admixed population.

(4) Similarly, for the discussion of LCT, I am not convinced that the haplotypes depicted here are on the right scale to reflect processes happening on the Faroes. Given the admixture/population history, it at the very least should be discussed in the context of whether the 13910 allele frequency on the Faroes is at odds with what would be expected based on the admixture sources.

(5) I am lacking information to evaluate the procedure for turning the outliers into p-values. Both iHS and XP-EHH are ratio statistics, meaning they might be heavy-tailed if one is not careful, and the central limit theorem may not apply. It would be much easier (and probably sufficient for the points being made here) to reframe this analysis in terms of empirical outliers.

(6) Oldest individual predating gene flow: It seems impossible to make any statements based on a single individual. Why is it implausible that this person (or their parents), e.g., moved to the Faroes within their lifetime and died there?

Reviewer #1 (Public review):

Summary:

In the manuscript, Hallinan et al. describe off-target probe binding in the 10x Genomics Xenium platform, which results in invalid profiling of some genes in a spatial context. This was validated by comparing the Xenium results with Visium and scRNA-seq using human breast tissue, which are comprehensive and convincing. The authors also provide a dedicated tool to predict such off-target binding, Off-target Probe Tracker (OPT), which could be widely adopted in the field by researchers who are interested in validating the previously published results.

Strengths:

(1) This is the first study to suggest off-target binding of probes in the gene panels of the Xenium platform, which could be easily overlooked.

(2) The results were rigorously validated with two different methods.

(3) This paper will be a helpful resource for properly interpreting the results of previously published papers based on the Xenium platform (the signals could be mixed).

Weaknesses:

(1) The results were only tested with one tissue (human breast). However, this is not a major weakness, as one can easily extrapolate that this should be the case for any other tissue.

(2) Once the 10X Genomics corrects their gene panels according to this finding, the tool (OPT) will not be useful for most people. Still, it can be used by those who want to design de novo probes from scratch.

Reviewer #2 (Public review):

This paper describes an analysis of a commercially available panel for a spatial transcriptomic approach and introduces a computational tool to predict potential off-target binding sites for the type of probe used in the aforementioned panel. The performance of the prediction tool was validated by examining a dataset that profiled the same cancer tissue with multiple modalities. Finally, a detailed analysis of the potential pitfalls in a published study communicated by the company that commercialized the spatial transcriptomic platform in question is provided, along with best practice guidelines for future studies to follow.

Strengths:

The manuscript is clearly written and easy to follow.

The authors provide clean, organized, and well-documented code in the associated GitHub repository.

Weaknesses:

The manuscript section on the software tool feels underdeveloped.

Reviewer #3 (Public review):

Summary:

The authors present a new computational method (OPT) for predicting off-target probe binding in the commercial 10X Xenium spatial transcriptomics platform. They identified 28 genes in the 10x xenium human breast cancer gene panel (280 genes) that are not accurately detected at the single-molecule level. They validated the predicted off-target binding using reference data from single-cell RNA-seq and 3'-sequencing-based Visium RNA-seq. This work provides a practical resource and will serve as a valuable reference for future data interpretation.

Strengths:

(1) Provides a toolbox for the community to identify off-target probes.

(2) Validates the predictions using single-cell RNA-seq and sequencing-based Visium RNA-seq datasets.

Weaknesses:

(1) Does not apply the OPT method to the most widely used Xenium gene panels (e.g., pan-Human, pan-Mouse panels with ~5,000 genes each).

(2) Lacks clarity on how the confidence level of off-target predictions is calculated.

Reviewer #1 (Public review):

Summary:

This study aimed to investigate the effects of optically stimulating the A13 region in healthy mice and a unilateral 6-OHDA mouse model of Parkinson's disease (PD). The primary objectives were to assess changes in locomotion, motor behaviors, and the neural connectome. For this, the authors examined the dopaminergic loss induced by 6-OHDA lesioning. They found a significant loss of tyrosine hydroxylase (TH+) neurons in the substantia nigra pars compacta (SNc) while the dopaminergic cells in the A13 region were largely preserved. Then, they optically stimulated the A13 region using a viral vector to deliver the channelrhodopsine (CamKII promoter). In both sham and PD model mice, optogenetic stimulation of the A13 region induced pro-locomotor effects, including increased locomotion, more locomotion bouts, longer durations of locomotion, and higher movement speeds. Additionally, PD model mice exhibited increased ipsilesional turning during A13 region photoactivation. Lastly, the authors used whole-brain imaging to explore changes in the A13 region's connectome after 6-OHDA lesions. These alterations involved a complex rewiring of neural circuits, impacting both afferent and efferent projections. In summary, this study unveiled the pro-locomotor effects of A13 region photoactivation in both healthy and PD model mice. The study also indicates the preservation of A13 dopaminergic cells and the anatomical changes in neural circuitry following PD-like lesions that represent the anatomical substrate for a parallel motor pathway.

Strengths:

These findings hold significant relevance for the field of motor control, providing valuable insights into the organization of the motor system in mammals. Additionally, they offer potential avenues for addressing motor deficits in Parkinson's disease (PD). The study fills a crucial knowledge gap, underscoring its importance, and the results bolster its clinical relevance and overall strength.

The authors adeptly set the stage for their research by framing the central questions in the introduction, and they provide thoughtful interpretations of the data in the discussion section. The results section, while straightforward, effectively supports the study's primary conclusion-the pro-locomotor effects of A13 region stimulation, both in normal motor control and in the 6-OHDA model of brain damage.

Weaknesses:

(1) Anatomical investigation. I have a major concern regarding the anatomical investigation of plastic changes in the A13 connectome (Figures 4 and 5). While the methodology employed to assess the connectome is technically advanced and powerful, the results lack mechanistic insight at the cell or circuit level into the pro-locomotor effects of A13 region stimulation in both physiological and pathological conditions. This concern is exacerbated by a textual description of results that doesn't pinpoint precise brain areas or subareas but instead references large brain portions like the cortical plate, making it challenging to discern the implications for A13 stimulation. Lastly, the study is generally well-written with a smooth and straightforward style, but the connectome section presents challenges in readability and comprehension. The presentation of results, particularly the correlation matrices and correlation strength, doesn't facilitate biological understanding. It would be beneficial to explore specific pathways responsible for driving the locomotor effects of A13 stimulation, including examining the strength of connections to well-known locomotor-associated regions like the Pedunculopontine nucleus, Cuneiformis nucleus, LPGi, and others in the diencephalon, midbrain, pons, and medulla. Additionally, identifying the primary inputs to A13 associated with motor function would enhance the study's clarity and relevance.

The study raises intriguing questions about compensatory mechanisms in Parkinson's disease a new perspective with the preservation of dopaminergic cells in A13, despite the SNc degeneration, and the plastic changes to input/output matrices. To gain inspiration for a more straightforward reanalysis and discussion of the results, I recommend the authors refer to the paper titled "Specific populations of basal ganglia output neurons target distinct brain stem areas while collateralizing throughout the diencephalon from the David Kleinfeld laboratory." This could guide the authors in investigating motor pathways across different brain regions.

(2) Description of locomotor performance. Figure 3 provides valuable data on the locomotor effects of A13 region photoactivation in both control and 6-OHDA mice. However, a more detailed analysis of the changes in locomotion during stimulation would enhance our understanding of the pro-locomotor effects, especially in the context of 6-OHDA lesions. For example, it would be informative to explore whether the probability of locomotion changes during stimulation in the control and 6-OHDA groups. Investigating reaction time, speed, total distance, and even kinematic aspects during stimulation could reveal how A13 is influencing locomotion, particularly after 6-OHDA lesions. The laboratory of Whelan has a deep knowledge of locomotion and the neural circuits driving it so these features may be instructive to infer insights on the neural circuits driving movement. On the same line, examining features like the frequency or power of stimulation related to walking patterns may help elucidate whether A13 is engaging with the Mesencephalic Locomotor Region (MLR) to drive the pro-locomotor effects. These insights would provide a more comprehensive understanding of the mechanisms underlying A13-mediated locomotor changes in both healthy and pathological conditions.

(3) Figure 2 indeed presents valuable information regarding the effects of A13 region photoactivation. To enhance the comprehensiveness of this figure and gain a deeper understanding of the neurons driving the pro-locomotor effect of stimulation, it would be beneficial to include quantifications of various cell types:

• cFos-Positive Cells/TH-Positive Cells: it can help determine the impact of A13 stimulation on dopaminergic neurons and the associated pro-locomotor effect in healthy condition and especially in the context of Parkinson's disease (PD) modeling.

• cFos-Positive Cells /TH-Negative Cells: Investigating the number of TH-negative cells activated by stimulation is also important, as it may reveal non-dopaminergic neurons that play a role in locomotor responses. Identifying the location and characteristics of these TH-negative cells can provide insights into their functional significance.<br /> Incorporating these quantifications into Figure 2 would enhance the figure's informativeness and provide a more comprehensive view of the neuronal populations involved in the locomotor effects of A13 stimulation.

(4) Referred to Figure 3. In the main text (page 5) when describing the animal with 6-OHDA the wrong panels are indicated. It is indicated in Figure 2A-E but it should be replaced with 3A-E. Please do that.

Summary of the Study after revision

The revised manuscript reflects significant efforts to improve clarity, organization, and data interpretation. The refinements in anatomical descriptions, behavioral analyses, and contextual framing have strengthened the manuscript considerably. However, the study still lacks direct causal evidence linking anatomical remodeling to behavioral improvements, and the small sample size in the anatomical analyses remains a concern. The authors have addressed many points raised in the initial review, but further acknowledgement of the exploratory nature of these findings would enhance the scientific rigor of the work.

Key Improvements in the Revision

The revised manuscript demonstrates considerable progress in clarifying data presentation, refining behavioral analyses, and improving the contextualization of anatomical findings. The restructuring of the anatomical section now provides greater precision in describing motor-related pathways, integrating terminology from the Allen Brain Atlas. The addition of new figures (Figures 4 and 5) strengthens the accessibility of these findings by illustrating key connectivity patterns more effectively. Furthermore, the correlation matrices have been adjusted to improve interpretability, ensuring that the presented data contribute meaningfully to the overall narrative of the study.

The authors have also made significant improvements in their behavioral analyses, particularly in the organization and presentation of locomotor data. Figure 3 has been revised to distinctly separate results from 6-OHDA and sham animals, providing a clearer comparison of locomotor outcomes. Additional metrics, such as reaction time, locomotion bouts, and movement speed, further enhance the granularity of the analysis, making the results more informative.

The discussion surrounding anatomical connectivity has also been strengthened. The revised manuscript now places greater emphasis on motor-related pathways and refines its analysis of A13 efferents and afferents. A newly introduced figure provides a concise summary of these connections, improving the contextualization of the anatomical data within the study's broader scope. Moreover, the authors have addressed the translational relevance of their findings by acknowledging the differences between optogenetic stimulation and deep brain stimulation (DBS). Their discussion now better situates the findings within existing literature on PD-related motor circuits, providing a more balanced perspective on the potential implications of A13 stimulation.

Remaining Concerns

Despite these substantial improvements, a number of critical concerns remain. The anatomical findings, though insightful, remain largely correlative and do not establish a causal link between structural remodeling and locomotor recovery. While the authors argue that these data will serve as a reference for future investigations, their necessity for the core conclusions of the study is not entirely clear. Additionally, while the anatomical data offer an interesting perspective on A13 connectivity, their direct relevance to the study's primary goal-demonstrating the role of A13 in locomotor recovery-remains uncertain. The authors emphasize that these data will be valuable for future research, yet their integration into the study's main narrative feels somewhat supplementary. Based on this last thought of the authors it is even more relevant another key limitation lying in the small sample size used for connectivity analyses. With only two sham and three 6-OHDA animals included, the statistical confidence in the findings is inherently limited. The absence of direct statistical comparisons between ipsilesional and contralesional projections further weakens the conclusions drawn from these anatomical studies. The authors have acknowledged that obtaining the necessary samples, acquiring the data, and analyzing them is a prolonged and resource-intensive process. While this may be a valid practical limitation, it does not justify the lack of a robust statistical approach. A more rigorous statistical framework should be employed to reinforce the findings, or alternative techniques should be considered to provide additional validation. Given these constraints, it remains unclear why the authors have not opted for standard immunohistochemistry, which could provide a complementary and more statistically accessible approach to validate the anatomical findings. Employing such an approach would not only increase the robustness of the results but also strengthen the study's impact by providing an independent confirmation of the observed structural changes.

Reviewer #2 (Public review):

Summary:

The paper by Kim et al. investigates the potential of stimulating the dopaminergic A13 region to promote locomotor restoration in a Parkinson's mouse model. Using wild-type mice, 6-OHDA injection depletes dopaminergic neurons in the substantia nigra pars compacta, without impairing those of the A13 region and the ventral tegmentum area, as previously reported in humans. Moreover, photostimulation of presumably excitatory (CAMKIIa) neurons in the vicinity of the A13 region improves bradykinesia and akinetic symptoms after 6-OHDA injection. Whole-brain imaging with retrograde and anterograde tracers reveals that the A13 region undergoes substantial changes in the distribution of its afferents and projections after 6-OHDA injection, thus suggesting a remodeling of the A13 connectome. Whether this remodelling contributes to pro-locomotor effects of the photostimulation of the A13 region remains unknown as causality was not addressed.

Strengths:

Photostimulation of presumably excitatory (CAMKIIa) neurons in the vicinity of the A13 region promotes locomotion and locomotor recovery of wild-type mice 1 month after 6-OHDA injection in the medial forebrain bundle, thus identifying a new potential target for restoring motor functions in Parkinson's disease patients. The study also provides a description of the A13 region connectome pertaining to motor behaviors and how it changes after a dopaminergic lesion. Although there is no causal link between anatomical and behavioral data, it raises interesting questions for further studies.

Weaknesses:

Although CAMKIIa is a marker of presumably excitatory neurons and can be used as an alternative marker of dopaminergic neurons, some uncertainty remains regarding the phenotype of neurons underlying recovery of akinesia and improvement of bradykinesia.

Figure 4 is improved, but the results from the correlation analyses remain difficult to interpret, as they may reflect changes in various impaired brain regions independently of the A13 region. While the analysis offers a snapshot of correlated changes within the connectome, it does not identify which specific cell or axonal populations are actually increasing or decreasing. Although functional MRI connectome analyses are well-established, anatomical data seem less suitable for this purpose. How can one interpret correlated changes in anatomical inputs or outputs between two distinct regions?

Figure 5 is also improved, but there is room for further enhancement. As currently presented, it is difficult to distinguish the differences between the sham and 6-OHDA groups. The first column could compare afferents, while the second column could compare efferents. Given the small sample size, it would be more appropriate to present individual data rather than the mean and standard deviation.

Appraisal and impact

Although the behavioral experiments are convincing, the low number of animals in the anatomical studies is insufficient to make any relevant statistical conclusions due to extremely low statistical power.

Reviewer #3 (Public review):

Kim, Lognon et al. present an important finding on pro-locomotor effects of optogenetic activation of the A13 region, which they identify as a dopamine-containing area of the medial zona incerta that undergoes profound remodeling in terms of afferent and efferent connectivity after administration of 6-OHDA to the MFB. The authors claim to address a model of PD-related gait dysfunction, a contentious problem that can be difficult to treat by dopaminergic medication or DBS in conventional targets. They make use of an impressive array of technologies to gain insight into the role of A13 remodeling in the 6-OHDA model of PD. The evidence provided is solid and the paper is well written, but there are several general issues that reduce the value of the paper in its current form, and a number of specific, more minor ones. Also some suggestions, that may improve the paper compared to its recent form, come to mind.

The most fundamental issue that needs to be addressed is the relation of the structural to the behavioral findings. It would be very interesting to see whether the structural heterogeneity in afferent/effects projections induced by 6-OHDA is related to the degree of symptom severity and motor improvement during A13 stimulation.

The authors provide extensive interrogation of large-scale changes in the organization of the A13 region afferent and efferent distributions. It remains unclear how many animals were included to produce Fig 4 and 5. Fig S5 suggests that only 3 animals were used, is that correct? Please provide details about the heterogeneity between animals. Please provide a table detailing how many animals were used for which experiment. Were the same animals used for several experiments?

While the authors provide evidence that photoactivation of the A13 is sufficient in driving locomotion in the OFT, this pro-locomotor effect seems to be independent of 6-OHDA induced pathophysiology. Only in the pole test do they find that there seems to be a difference between Sham vs 6-OHDA concerning effects of photoactivation of the A13. Because of these behavioral findings, optogenic activation of A13 may represent a gain of function rather than disease-specific rescue. This needs to be highlighted more explicitly in the title, abstract and conclusion.

The authors claim that A13 may be a possible target for DBS to treat gait dysfunction. However, the experimental evidence provided (imparticular lack of disease-specific changes in the OFT) seem insufficient to draw such conclusions. It needs to be highlighted that optogenetic activation does not necessarily have the same effects as DBS (see the recent review from Neumann et al. in Brain: https://pubmed.ncbi.nlm.nih.gov/37450573/). This is important because ZI-DBS so far had very mixed clinical effects. The authors should provide plausible reasons for these discrepancies. Is cell-specificity, that only optogenetic interventions can achieve, necessary? Can new forms of cyclic burst DBS achieve similar specificity (Spix et al, Science 2021)? Please comment.

In a recent study, Jeon et al (Topographic connectivity and cellular profiling reveal detailed input pathways and functionally distinct cell types in the subthalamic nucleus, 2022, Cell Reports) provided evidence on the topographically graded organization of STN afferents and McElvain et al. (Specific populations of basal ganglia output neurons target distinct brain stem areas while collateralizing throughout the diencephalon, 2021, Neuron) have shown similar topographical resolution for SNr efferents. Can a similar topographical organization of efferents and afferents be derived for the A13/ ZI in total?

In conclusion, this is an interesting study that can be improved taking into consideration the points mentioned above.

Reviewer #1 (Public review):

Summary:

In this study, Bonnifet et al. profile the presence of L1 ORF1p in the mouse and human brain and report that ORF1p is expressed in the human and mouse brain specifically in neurons at steady state and that there is an age-dependent increase in expression. This is a timely report as two recent papers have extensively documented the presence of full-length L1 transcripts in the mouse and human brain (PMID: 38773348 & PMID: 37910626). Thus, the finding that L1 ORF1p is consistently expressed in the brain is important to document and will be of value to the field.

Strengths:

Several parts of this manuscript appear to be well done and include the necessary controls. In particular, the documentation of neuron-specific expression of ORF1p in the mouse brain is an interesting finding with nice documentation. This will be very useful information for the field.

Weaknesses:

The transcriptomic data using human postmortem tissue presented in Figures 4 and 5 are not convincing. Quantification of transposon expression on short read sequencing has important limitations. Longer reads and complementary approaches are needed to study the expression of evolutionarily young L1s (see PMID: 38773348 & PMID: 37910626 for examples of the current state of the art). As presented, the human RNA data is inconclusive due to the short read length and small sample size. The value of including an inconclusive analysis in the manuscript is difficult to understand. With this data set, the authors cannot investigate age-related changes in L1 expression in human neurons.

In line with these comments, the title should be changed to better reflect the findings in the manuscript. A title that does not mention "L1 increase with aging" would be better.

Comments on Revisions:

It is notable that the expression of ORF1p in the human brain shows two strong bands in the WB. As the authors acknowledge in their discussion, some labs report only one band. The authors have performed a number of controls to address this issue, acknowledge remaining uncertainty, and discuss the discrepancy in the field.

Reviewer #2 (Public review):

Summary:

Bonnifet et al. sought to characterize the expression pattern of L1 ORF1p expression across the entire mouse brain, in young and aged animals and to corroborate their characterization with Western blotting for L1 ORF1p and L1 RNA expression data from human samples. They also queried L1 ORF1p interacting partners in the mouse brain by IP-MS.

Strengths:

A major strength of the study is the use of two approaches: a deep-learning detection method to distinguish neuronal vs. non-neuronal cells and ORF1p+ cells vs. ORF1p- cells across large-scale images encompassing multiple brain regions mapped by comparison to the Allen Brain Atlas, and confocal imaging to give higher resolution on specific brain regions. These results are also corroborated by Western blotting on six mouse brain regions. Extension of their analysis to post-mortem human samples, to the extent possible, is another strength of the paper. The identification of novel ORF1p interactors in brain is also a strength in that it provides a novel dataset for future studies.

Weaknesses:

The main weakness of the IP-MS portion of the study is that none of the interactors were individually validated or subjected to follow-up analyses. The list of interactors was compared to previously published datasets, but not to ORF1p interactors in any other mouse tissue.

Comments on revisions:

The co-staining of Orf1p with Parvalbumin (PV) presented in Supplemental Figure S5 is a welcome addition exploring the cell type-specificity of Orf1p staining, and broadly corroborates the work of Bodea et al. while revealing that Orf1p also is expressed in non-PV+ cells, consistent with L1 activity across a range of neuronal subtypes. The authors also have strengthened their findings regarding the increased intensity of ORF1p staining in aged compared to young animals, and the newly presented results are indeed more convincing. The prospect of increased neuronal L1 activity with age is exciting, and the results in this paper have provided the groundwork for ongoing discoveries in this area. While it is disappointing that no Orf1p interactors were followed up, this is understandable and the data are nonetheless valuable and will likely prove useful to future studies.