Author Response

Reviewer #1 (Public Review):

The authors succeed at generating a large amount of data using a high-throughput platform to measure bacterial growth, analyzing its complexity and deriving some simple rules to model the system. The limited complexity of the system under consideration (with 3 nutrients quantitatively determining all dynamic parameters for this bacterium) suggests that very simple analysis tools would be enough to tackle this large amount of data. This study is a clear example of a clever combination of high-throughput data generation and machine learning.

Parametrization of growth curves (with lag times, growth rates, and growth saturation plateau as all-encompassing parameters) is simple, accurate and ultimately addressable. Indeed, using the large number of combinations of growth conditions (varied amino acids, metal ions, etc.) at different concentrations. It is very satisfying that a simple growth model and 3 parameters are enough to capture the entire dynamic complexity of these bacterial growth curves in vitro.

Thank you for the careful reading and the positive evaluation. Your thoughtful comments helped us to improve our manuscript.

The authors argue that the 3 dynamic parameters (lag time, growth rate, and carrying capacity) are essentially bimodal across all conditions (Fig. 2B). A closer inspection of the parameter K actually reflects 4 separatable peaks (see also Fig 7). Moreover, a simple PCA of the 3 dynamic parameters reveals only 4 separate clusters (while one could anticipate 2^3=8 clusters if the 3 parameters were truly bimodal and independent). The authors need to comment on the missing clusters e.g. what rules forbid some combinations of parameters (cf correlation between parameters as shown in Fig. 7).

Thank you for the insightful comment. Fig. 2C showed that a total of 966 medium combinations could be roughly divided into four clusters. It’s true that if the three growth parameters were independent, more than eight PCA clusters were theoretically estimated, because the three distributions of growth parameters were all multimodal. The disappearance of the PCA clusters strongly suggested that the growth parameters were somehow dependent, which was further demonstrated in Fig. 7. The following sentences were added.

(lines 92~95) “If the three parameters of τ, r and K, which all showed the multimodal distributions, were independent, more than eight clusters were anticipated. Only four separate clusters were identified, indicated that the growth parameters were somehow dependent.”

(lines 209~211) “The correlations demonstrated that τ, r and K were highly dependent, which well explained why the multimodal distributions of the growth parameters led to only four PCA clusters (Figure 2).”

Additionally, the relevance of the Machine Learning (ML) framework to analyze the data read like over-complicated for a "simple" classification task: the authors need to explain better what insight was derived from the ML analysis compared to simpler/unsupervised PCA and such.

Thank you for the advice. The benefit of using Machine Learning (ML) framework was additionally discussed by comparing with a simpler and more common analytical approach. Considering the interpretability (i.e., the quantitative contribution of individual chemicals to the three growth parameters), multiple regression was employed for the comparison. The results showed that the accuracy of multiple regression was worse than that of ML (Figure 3−figure supplement 1). Accordingly, the figures were revised and the corresponding description was added in the Discussion as follows (lines 289~297).

“First, the representative ML models and a commonly used statistic model of multiple regression were compared. Although multiple regression is known to have the highest interpretability, its accuracy of predictability was likely to be worse than that of the ML models (Figure 3−figure supplement 1). The results well supported the common sense that the ML approach was more suitable for studying the complex systems, which were the growing bacterial cells and the chemical media in the present survey. Additionally, among the tested ML models, the best accuracy was acquired with the ensemble model; nevertheless, as it required the longest time for model training (Figure 3−figure supplement 2) and was uninterpretable, the GBDT model was finally employed.”

Overall, this study reads strong in its experimental implementation and insight. Additional analysis and easier interpretation will help the reader better assess the relevance of the findings.

Thank you again for your supportive comments. We hope the revised manuscript meets your concern.

Reviewer #2 (Public Review):

This paper describes the analysis of a large data set collected from growth experiments on one strain of E. coli. The experimenters varied the growth media and used machine learning to try to deconstruct what was going on biologically. I have two major concerns with the methodology.

1) The results of growth experiments are often severely affected by whether or not the strain has had time to adapt to the growth conditions tested. There is no time allowed for the different cultures to become adapted to these different growth media.

2) All of these results are based on the concentration of chemical substances at t=0. As a culture grows it uses chemicals and releases other chemicals. That means the concentration of the different chemicals is changing as well as the ratio of different chemicals.

Because of this, I have serious doubts about the specific biological claims.

Thank you for reviewing our paper and the valuable comments, which helped us to improve the manuscript to a large extent. Taking all the concerns into account, we performed the additional experiments and analyses, and intensively revised the manuscript.

The concept of making ML methods less opaque and using them to tease apart specific biological processes is intriguing. This is also a very interesting and large data set that would be useful to others for developing algorithms. Readers who are interested in ML applications in biology would be interested in this paper.

We do agree and sincerely hope the findings, datasets and analytical approaches provided in the present study are valuable for the readers of varied research backgrounds.

Reviewer #3 (Public Review):

In this manuscript, the authors define 966 different media combinations on which they run over 12,000 growth curves for E. coli. After fitting the growth curves to estimate classical growth parameters (e.g. lag, growth rate and carrying capacity) the authors evaluate different machine learning methods in their ability to predict growth parameters from media composition. They use the results of the modeling to determine what media components are more important in affecting a certain parameter. The authors use the findings to try to explain why distinct "decision-making" components are found to associate with each of the growth parameters under an ecology and evolutionary biology light.

The experiment appears executed well. However, apart from making sure the 966 media combinations are well defined, this is running growth curves with E. coli. This has been established for many years. The machine learning modeling is not innovative. Better posed, the authors use off-the-shelf machine learning methods available from different python packages to perform regression.

Overall, the paper lacks motivation for why is this work done and what implications this work has. Based on the regression analysis the authors find that different growth medium components are more important (or associate specifically with) in predicting classical growth curve parameters including growth rate, carrying capacity and lag time. Knowing that the amount of glucose in the media determines the carrying capacity value has been known for several decades and does not need machine learning to tell us.

Given that the authors use the most studied and genetically manipulatable model system in biology, and they use growth curves as the experimental system I would have expected some creative validation experiment to confirm the biological interpretation that they give to the data. After reading and evaluating the paper I cannot say I have learned anything new.

Thank you for reviewing our paper and the helpful comments. Accordingly, the manuscript was intensively revised, associated with the additional results and newly provided figures. We hope the changes made in the paper meet your concern.

Author Response

Joint Public Review:

Strengths: The study represents a step forward in relating immune responses to infection outcomes that of urgent interest to public health, especially the timing of shedding and frequency of supershedding events. Nguyen et al.'s model provides a useful framework for understanding the links between immune effectors and infection outcomes, and it can be expanded to encompass further biological complexity. The study system is a good choice, given the ubiquity of both helminth and bacterial infections, and experimental infections of rabbits provide a useful point of comparison for past work in mice.

We appreciated these general comments.

Limitations: The present study does not explicitly account for differences in helminth infection dynamics across the two species represented in the data nor does it include feedbacks between the bacterial and helminth infections. Nguyen et a. therefore show the limits of what can be learned from focusing on the bacterial and immune dynamics alone, and this study should serve to motivate further work that can build on this modeling approach to produce a more comprehensive view of the interactions among species infecting the same host. Future studies examining the impact of helminth infection intensity would be tremendously useful for assessing the potential of anthelminthics to reduce the prevalence of bacterial respiratory diseases. Finally, subsequent studies may need to look beyond the factors examined here to understand why shedding varies so much through time for individual hosts.

We agree that focusing only on the bacterial infection is a limitation in this study. We followed a parsimonious approach and decided to concentrate on B. bronchiseptica shedding in the four types of infection. While we do have data on the dynamics of infection of the two helminth species, adding these data would have been an enormous amount of work and too much to present in a single paper. Yet, we have already investigated some of these bi-directional effects using the BT group (Thakar et al. 2012 Plos Comp. Biol.) and plan to keep working on these rich datasets in the future.

We also agree that it is important to understand the rapid variation in Bordetella shedding observed, which appears to be a common feature in many other host-pathogen systems. This requires a completely new set of experiments on infection and shedding at the local tissue level.

Specific comments

Definition of supershedding: A major stated goal of the MS is to investigate the effect of coinfection by helminths on supershedding. In order to compare animals with different coinfections, it is therefore necessary to have a common definition of supershedding. At present, the authors use a definition that depends on which arm of the experiment the animals belong to. This complicates the analysis and clouds its interpretation.

We value this comment and see the implication of using different datasets to quantify supershedding. To overcome this problem, we now propose a slightly different approach where we pull the four infections together and calculate a common 99th or 95th percentile threshold. This common threshold is then used to calculate the number of hosts with at least one supershedding event above this cut-off, for every type of infection. Therefore, while the threshold is the same the percentage of hosts with supershedding events varies among infection groups.

Inconsistent approach: Within each experimental treatment, the data display variability on at least three levels: (i) within animals, day-to-day shedding displays variability on a fast timescale; (ii) within animals, infection status varies more slowly over the course of infection; (iii) between animals, there is variation in both (i) and (ii). The authors' model seems well-designed to handle this variability, but the authors are strangely inconsistent in their use of it. To be specific, to account for level (i), the authors very sensibly adopt a zero-inflated model for the shedding data, whereby the rate of shedding (colony-forming units per second, CFU/s) is assumed to arise from a mixture of a quantitative process (which we might think of as intensity of potential shedding) and an all-or-nothing process (which might arise, for example, if some discrete behavior of the animal is necessary for shedding to occur at all). The inclusion of the all-or-nothing process necessitates an additional parameter, but it allows the non-zero shedding data to inform the model. To account for level (ii), the authors use a four-dimensional deterministic dynamical system. Three of the four variables are related to the measured components of the immune response. The fourth is related to the aforementioned potential shedding. Level (iii) is accounted for using a hierarchical Bayesian approach, whereby the individual animals have parameters drawn from a common prior distribution. This approach seems very well designed to address the authors' questions using the data at hand. However, they fail to exploit this, in at least three ways. First, even though the model appears designed specifically to allow for non-shedding animals, the authors exclude animals on an ad hoc basis. Second, rather than display the shedding data in the form recommended by the model, they display log(1+CFU/sec), which is arbitrary and problematic. Its arbitrariness stems from the fact that this quantity is sensitive to the units used for shedding rate. Third, despite the fact that the model appears specifically designed to account for variability at each of the three levels, they do not give enough information to allow the reader to judge whether the model does in fact do a good job of partitioning this variability.

Please see comments to each specific matter below.

Exclusion of animals: In view of the fact that the model the authors describe can account for variability on all three levels, it is strange that they exclude animals that shed too little or not at all. It would be preferable were the authors to base their conclusions on all the data they collected rather than on a subset chosen a posteriori. It is true that the non-shedders will have no information about the time-course of shedding; on the other hand, including them does not complicate the analysis, and it does allow for estimation of the all-or-nothing probability in a coherent fashion. In particular, the fact that coinfection appears to have an impact on whether animals shed at all is itself directly related to the authors' central questions. More generally, ad hoc exclusion of data raises concerns about the repeatability of the experiments that, in this case, appear entirely avoidable.

Rabbits that were infected but never shed were excluded from all our original analysis and continue to be excluded in our updated version. Our focus is on the dynamics of shedding and including animals that do not shed is not informative to our objective. Moreover, these animals do not provide meaningful information on rabbits that are infected but do not shed, since this is a very small number (n=7) to draw meaningful conclusions across four types of infection. Rabbits with three or less shedding events larger than zero (i.e. CFU/s>0) were originally excluded from the modeling and continue to be excluded. This decision was motivated by technical reasons of model convergence and our commitment to generate meaningful results; in other words, it is difficult to fit a model, and provide robust results, on a time series with only three points larger than zero, irrespective of the number of zero points in the time series.<br /> In summary our subset of animals was not chosen a posteriori but based on clear objectives (i.e. pattern of shedding between and within types of infections), a rigorous approach and reliable results. We have further clarified our approach in the Results and Material and Methods.

Incomplete description of the analysis: The description of the statistical analysis will not be complete until sufficient information is provided to allow the interested reader to decide for him- or herself whether the conclusions are warranted and for the motivated reader to reproduce the analysis. In particular, it is necessary to specify all priors fully. At present, these are not described at all, except in vague, and even incoherent, ways. Also, it is necessary to provide details of the MCMC performed. Specifically, the authors should describe the MCMC sampler and show their MCMC convergence diagnostics. Finally, it is good practice to display both the priors and the posteriors: it is impossible to assess the posteriors without an understanding of the priors.

We have carefully revised our approach and results and now provide a complete description of our analysis with additional/new details on Parameter calibration, Model fitting, Model validation and Model selection in Material and Methods, and Appendix (Appendix-3 and 4). Specifically, we have included all priors, along with all posteriors, for the four types of infection in Table 2. We have also explained how the MCMC simulations were performed and how model convergence diagnosis was assessed (section ‘Parameter calibration and Model fitting’). In Appendix-3 we also show the parameter MCMC trace plots for the four types of infection.

Second, rather than display the shedding data in the form recommended by the model, they display log(1+CFU/sec), which is arbitrary and problematic. Its arbitrariness stems from the fact that this quantity is sensitive to the units used for shedding rate.

A clear feature of our shedding data is that there is large variation in the level of shedding both within and between hosts. Because of this, data were presented as log(1+CFU/s) to reduce the skewness of the datasets, and thus the variance, and facilitate the visualization of the experimental and simulated results. The use of data in the form of CFU/s would have made the visualization much harder, especially at low shedding where a large fraction of the data come from.

The practice of displaying the data on a log-scale is appropriate when the underlying process is exponential or when the amount of relative variation is large, including when representing rates. This practice is widely used when modeling infectious diseases and describing biomedical results. A typical example is the overdispersion of macroparasite infections in host populations, or the large variation in the size of outbreaks by microparasite infections, these data are often described on a log-scale. An example closer to our case is the study on influenza-bacteria coinfection by Smith et al. 2013 Plos Pathogens. Given the nature of our data we found that plotting the level of shedding on a log-scale was the most effective way to represent our results.

Model adequacy: The authors' argument rests on the model's ability to adequately account for the data. The authors need to provide some evidence of this, in one form or another. Ultimately, the question is whether the data are a plausible realization of the model. The authors should show simulations from the model (including the measurement error and not merely the deterministic trajectories) and compare these simulations to the data. In particular, it seems worryingly possible that the fitted model is capable of capturing certain averages in the data while, at the same time, failing to describe the infection progression for any of the actual infected animals.

As previously reported, we have now provided full details on model fitting and model convergence in the section ’Parameter calibration and Model fitting’ and ‘Model validation’ in Material and Methods, and ‘Model validation’ and ‘Model convergence’ in Appendix (Appendix3 and 4).

Regarding the evidence that the data are a plausible realization of the model, we have moved the original figure S1 in the main text (now figure 5). This figure shows the good fit of the model to neutrophil, IgA and IgG, both using individual and group data from every infection. We have also revised the quality of the plot to highlight individual simulations. To avoid too much crowding the 95% CIs for every individual are not reported, however, in Appendix-1 we provide the posterior parameter estimations and their 95% CIs, for every individual and as a group average, for the three co-infections (simulations for B rabbits were performed at the group level only).

In the new figure 6 (original figure 5), we have now included the individual trajectories (without 95% CIs to avoid overcrowding), alongside the group trends, for the neutralization rates of neutrophils, IgA and IgG which are the important parameter regulating infection and where the CIs are large enough to show the individual data. The other rates have too narrow CIs to single out individual trajectories and, thus, we only reported the group trends.

In the revised figure 7 (original figure 6) we have revised the quality of the plots to highlight individual trajectories, in addition to the median trend, but have not included the individual 95% CIs, again to avoid overcrowding.

Finally, the main text associated to these figures has been updated accordingly.

Confusion of correlation and causation: At various points, the authors succumb to the temptation to interpret their model literally and to interpret the correlations they observe as evidence for a causal linkage between the three immune components they measure, bacterial shedding, and coinfection. They should be more careful and circumspect in the description of their results.

We have thoroughly revised the presentation and discussion of the results to avoid the overinterpretation of the findings.

Additional Issues:

Eqs 1-4. These equations are not mechanistic in any meaningful sense. Essentially, they posit the existence of exponential time-lags between the three immunity variables, and a simple linear killing relationship between each of the variables and pathogen load. To interpret the equations literally risks making unwarranted conclusions. For example, any physiological variable correlated with any of the three variables in the model might equally well be credited with the influence on shedding attributed to IgA, IgG, or neutrophils.

This work tests the hypothesis that neutrophils, IgA and IgG affect the dynamics of B. bronchispetica infection and, in turn, bacterial shedding. Of course, there are many other immunological mechanisms that could contribute to the pattern observed and that can be tested, as there are many other variables correlated with these dynamics that do not play any role in these patterns, as noted by the reviewer. We follow a parsimonious approach by focusing on three immune variables previously identified as important in regulating Bordetella infection. To avoid excessive complexity and allow model tractability, our informed decision was to simplify the relationship between immunity and infection, without losing the important role of the immune variables selected. Finally, by referring to previous work by others and us we do note that the immune mechanisms described can be much more complex.

l 456. Do the authors account for the variability in time spent with plates? Implicitly, the assumption is made that the amount of time a rabbit spends with a plate, i.e., the decision as to whether to engage in a behavior that will terminate the plate interaction, is independent of everything else. This raises the question: Does the time spent per plate correlate with anything?

We always recorded the amount of time spent with the plate, and every rabbit had a maximum interaction time of 10 minutes. Rabbits are very inquisitive and rarely we had animals that did not interact or had to remove the plate because they were chewing the media; usually animals used the entire 10 minutes. Analyses do account for the interaction time and are presented as Colony Forming Unit/second (CFU/s). As noted in the Material and Methods section ‘Observation model’: ‘The probability of having a shedding event is independent of time since inoculation, in that shedding can occur anytime during the experiment and anytime during the interaction with the petri dish”. This assumption is based on our observations of rabbit behavior during the trials.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors present a new technique for analysing low complexity regions (LCRs) in proteins- extended stretches of amino acids made up from a small number of distinct residue types. They validate their new approach against a single protein, compare this technique to existing methods, and go on to apply this to the proteomes of several model systems. In this work, they aim to show links between specific LCRs and biological function and subcellular location, and then study conservation in LCRs amongst higher species.

The new method presented is straightforward and clearly described, generating comparable results with existing techniques. The technique can be easily applied to new problems and the authors have made code available.

This paper is less successful in drawing links between their results and the importance biologically. The introduction does not clearly position this work in the context of previous literature, using relatively specialised technical terms without defining them, and leaving the reader unclear about how the results have advanced the field. In terms of their results, the authors further propose interesting links between LCRs and function. However, their analyses for these most exciting results rely heavily on UMAP visualisation and the use of tests with apparently small effect sizes. This is a weakness throughout the paper and reduces the support for strong conclusions.

We appreciate the reviewer’s comments on our manuscript. To address comments about the clarity of the introduction and the position of our findings with respect to the rest of the field, we have made several changes to the text. We have reworked the introduction to provide a clearer view of the current state of the LCR field, and our goals for this manuscript. We also have made several changes to the beginnings and ends of several sections in the Results to explicitly state how each section and its findings help advance the goal we describe in the introduction, and the field more generally. We hope that these changes help make the flow of the paper more clear to the reader, and provide a clear connection between our work and the field.

We address comments about the use of UMAPs and statistical tests in our responses to the specific comments below.

Additionally, whilst the experimental work is interesting and concerns LCRs, it does not clearly fit into the rest of the body of work focused as it is on a single protein and the importance of its LCRs. It arguably serves as a validation of the method, but if that is the author's intention it needs to be made more clearly as it appears orthogonal to the overall drive of the paper.

In response to this comment, we have made more explicit the rationale for choosing this protein at the beginning of this section, and clarify the role that these experiments play in the overall flow of the paper.

Our intention with the experiments in Figure 2 was to highlight the utility of our approach in understanding how LCR type and copy number influence protein function. Understanding how LCR type and copy number can influence protein function is clearly outlined as a goal of the paper in the Introduction.

In the text corresponding to Figure 2, we hypothesize how different LCR relationships may inform the function of the proteins that have them, and how each group in Figure 2A/B can be used to test these hypotheses. The global view provided by our method allows proteins to be selected on the basis of their LCR type and copy number for further study.

To demonstrate the utility of this view, we select a key nucleolar protein with multiple copies of the same LCR type (RPA43, a subunit of RNA Pol I), and learn important features driving its higher-order assembly in vivo and in vitro. We learned that in vivo, a least two copies of RPA43’s K-rich LCRs are required for nucleolar integration, and that these K-rich LCRs are also necessary for in vitro phase separation.

Despite this protein being a single example, we were able to gain important insights about how K-rich LCR copy number affects protein function, and that both in vitro higher order assembly and in vivo nucleolar integration can be explained by LCR copy number. We believe this opens the door to ask further questions about LCR type and copy number for other proteins using this line of reasoning.

Overall I think the ideas presented in the work are interesting, the method is sound, but the data does not clearly support the drawing of strong conclusions. The weakness in the conclusions and the poor description of the wider background lead me to question the impact of this work on the broader field.

For all the points where Reviewer #1 comments on the data and its conclusions, we provide explanations and additional analyses in our responses below showing that the data do indeed support our conclusions. In regards to our description of the wider background, we have reworked our introduction to more clearly link our work to the broader field, such that a more general audience can appreciate the impact of our work.

Technical weaknesses

In the testing of the dotplot based method, the manuscript presents a FDR rate based on a comparison between real proteome data and a null proteome. This is a sensible approach, but their choice of a uniform random distribution would be expected to mislead. This is because if the distribution is non-uniform, stretches of the most frequent amino will occur more frequently than in the uniform distribution.

Thank you for pointing this out. The choice of null proteome was a topic of much discussion between the authors as this work was being performed. While we maintain that the uniform background is the most appropriate, the question from this reviewer and the other reviewers made us realize that a thorough explanation was warranted. For a complete explanation for our choice of this uniform null model, please see the newly added appendix section, Appendix 1.

The authors would also like to point out that the original SEG algorithm (Wootton and Federhen, 1993) also made the intentional choice of using a uniform background model.

More generally I think the results presented suggest that the results dotplot generates are comparable to existing methods, not better and the text would be more accurate if this conclusion was clearer, in the absence of an additional set of data that could be used as a "ground truth".

We did not intend to make any strong claims about the relative performance of our approach vs. existing methods with regard to the sequence entropy of the called LCRs beyond them being comparable, as this was not the main focus of our paper. To clarify the text such that it reflects this, we have removed ‘or better’ from the text in this section.

The authors draw links between protein localisation/function and LCR content. This is done through the use of UMAP visualisation and wilcoxon rank sum tests on the amino acid frequency in different localisations. This is convincing in the case of ECM data, but the arguments are substantially less clear for other localisations/functions. The UMAP graphics show generally that the specific functions are sparsely spread. Moreover when considering the sample size (in the context of the whole proteome) the p-value threshold obscures what appear to be relatively small effect sizes.

We would first like to note that some of the amino acid frequency biases have been documented and experimentally validated by other groups, as we write and reference in the manuscript. Nonetheless, we have considered the reviewer's concerns, and upon rereading the section corresponding to Figure 3, we realize that our wording may have caused confusion in the interpretation there. In addition to clarifying this in the manuscript, we believe the following clarification may help in the interpretations drawn from that section.

Each point in this analysis (and on the UMAP) is an LCR from a protein, and as such multiple LCRs from the same protein will appear as multiple points. This is particularly relevant for considering the interpretation of the functional/higher order assembly annotations because it is not expected that for a given protein, all of the LCRs will be directly relevant to the function/annotation. Just because proteins of an assembly are enriched for a given type of LCR does not mean that they only have that kind of LCR. In addition to the enriched LCR, they may or may not have other LCRs that play other roles.

For example, a protein in the Nuclear Speckle may contain both an R/S-rich LCR and a Q-rich LCR. When looking at the Speckle, all of the LCRs of a protein are assigned this annotation, and so such a protein would contribute a point in the R/S region as well as elsewhere on the map. Because such "non-enriched" LCRs do not occur as frequently, and may not be relevant to Speckle function, they are sparsely spread.

We have now changed the wording in that section of the main text to reflect that the expectation is not all LCRs mapping to a certain region, but enrichment of certain LCR compositions.

Reviewer #3 (Public Review):

The authors present a systematic assessment of low complexity sequences (LCRs) apply the dotplot matrix method for sequence comparison to identify low-complexity regions based on per-residue similarity. By taking the resulting self-comparison matrices and leveraging tools from image processing, the authors define LCRs based on similarity or non-similarity to one another. Taking the composition of these LCRs, the authors then compare how distinct regions of LCR sequence space compare across different proteomes.

The paper is well-written and easy to follow, and the results are consistent with prior work. The figures and data are presented in an extremely accessible way and the conclusions seem logical and sound.

My big picture concern stems from one that is perhaps challenging to evaluate, but it is not really clear to me exactly what we learn here. The authors do a fine job of cataloging LCRs, offer a number of anecdotal inferences and observations are made - perhaps this is sufficient in terms of novelty and interest, but if anyone takes a proteome and identifies sequences based on some set of features that sit in the tails of the feature distribution, they can similarly construct intriguing but somewhat speculative hypotheses regarding the possible origins or meaning of those features.

The authors use the lysine-repeats as specific examples where they test a hypothesis, which is good, but the importance of lysine repeats in driving nucleolar localization is well established at this point - i.e. to me at least the bioinformatics analysis that precedes those results is unnecessary to have made the resulting prediction. Similarly, the authors find compositional biases in LCR proteins that are found in certain organelles, but those biases are also already established. These are not strictly criticisms, in that it's good that established patterns are found with this method, but I suppose my concern is that this is a lot of work that perhaps does not really push the needle particularly far.

As an important caveat to this somewhat muted reception, I recognize that having worked on problems in this area for 10+ years I may also be displaying my own biases, and perhaps things that are "already established" warrant repeating with a new approach and a new light. As such, this particular criticism may well be one that can and should be ignored.

We thank the reviewer for taking the time to read and give feedback for our manuscript. We respectfully disagree that our work does not push the needle particularly far.

In the section titled ‘LCR copy number impacts protein function’, our goal is not to highlight the importance of lysines in nucleolar localization, but to provide a specific example of how studying LCR copy number, made possible by our approach, can provide specific biological insights. We first show that K-rich LCRs can mediate in vitro assembly. Moreover, we show that the copy number of K-rich LCRs is important for both higher order assembly in vitro and nucleolar localization in cells, which suggests that by mediating interactions, K-rich LCRs may contribute to the assembly of the nucleolus, and that this is related to nucleolar localization. The ability of our approach to relate previously unrelated roles of K-rich LCRs not only demonstrates the value of a unified view of LCRs but also opens the door to study LCR relationships in any context.

Furthermore, our goal in identifying established biases in LCR composition for certain assemblies was to validate that the sequence space captures higher order assemblies which are known. In addition to known biases, we use our approach to uncover the roles of LCR biases that have not been explored (e.g. E-rich LCRs in nucleoli, see Figure 4 in revised manuscript), and discover new regions of LCR sequence space which have signatures of higher order assemblies (e.g. Teleost-specific T/H-rich LCRs). Collectively, our results show that a unified view of LCRs relates the disparate functions of LCRs.

In response to these comments, we have added additional explanations at the end of several sections to clarify the impact of our findings in the scope of the broader field. Furthermore, as we note in our main response, we have added experimental data with new findings to address this concern.

That overall concern notwithstanding, I had several other questions that sprung to mind.

Dotplot matrix approach

The authors do a fantastic job of explaining this, but I'm left wondering, if one used an algorithm like (say) SEG, defined LCRs, and then compared between LCRs based on composition, would we expect the results to be so different? i.e. the authors make a big deal about the dotplot matrix approach enabling comparison of LCR type, but, it's not clear to me that this is just because it combines a two-step operation into a one-step operation. It would be useful I think to perform a similar analysis as is done later on using SEG and ask if the same UMAP structure appears (and discuss if yes/no).

Thank you for your thoughtful question about the differences between SEG and the dotplot matrix approach. We have tried our best to convey the advantages of the dotplot approach over SEG in the paper, but we did not focus on this for the following reasons:

1) SEG and dotplot matrices are long-established approaches to assessing LCRs. We did not see it in the scope of our paper to compare between these when our main claim is that the approach as a whole (looking at LCR sequence, relationships, features, and functions) is what gives a broader understanding of LCRs across proteomes. The key benefits of dotplots, such as direct visual interpretation, distinguishing LCR types and copy number within a protein, are conveyed in Figure 1A-C and Figure 1 - figure supplements 1 and 4. In fact, these benefits of dotplots were acknowledged in the early SEG papers, where they recommended using dotplots to gain a prior understanding of protein sequences of interest, when it was not yet computationally feasible to analyze dotplots on the same scale as SEG (Wootton and Federhen, Methods in Enzymology, vol. 266, 1996, Pages 554-571). Thus, our focus is on the ability to utilize image processing tools to "convert" the intuition of dotplots into precise read-out of LCRs and their relationships on a multi-proteome scale. All that being said, we have considered differences between these methods as you can see from our technical considerations in part 2 below.

2) SEG takes an approach to find LCRs irrespective of the type of LCR, primarily because SEG was originally used to mask LCR-containing regions in proteins to facilitate studies of globular domains. Because of this, the recommended usage of SEG commonly fuses nearby LCRs and designates the entire region as "low complexity". For the original purpose of SEG, this is understandable because it takes a very conservative approach to ensure that the non-low complexity regions (i.e. putative folded domains) are well-annotated. However, for the purpose of distinguishing LCR composition, this is not ideal because it is not stringent in separating LCRs that are close together, but different in composition. Fusion can be seen in the comparison of specific LCR calls of the collagen CO1A1 (Figure 1 - figure supplement 3E), where even the intermediate stringency SEG settings fuse LCR calls that the dotplot approach keeps separate. Finally, we did also try downstream UMAP analysis with LCRs called from SEG, and found that although certain aspects of the dotplot-based LCR UMAP are reflected in the SEG-based LCR UMAP, there is overall worse resolution with default settings, which is likely due to fused LCRs of different compositions. Attempting to improve resolution using more stringent settings comes at the cost of the number of LCRs assessed. We have attached this analysis to our rebuttal for the reviewer, but maintain that this comparison is not really the focus of our manuscript. We do not make strong claims about the dotplot matrices being better at calling LCRs than SEG, or any other method.

UMAPs generated from LCRs called by SEG

LCRs from repeat expansions

I did not see any discussion on the role that repeat expansions can play in defining LCRs. This seems like an important area that should be considered, especially if we expect certain LCRs to appear more frequently due to a combination of slippy codons and minimal impact due to the biochemical properties of the resulting LCR. The authors pursue a (very reasonable) model in which LCRs are functional and important, but it seems the alternative (that LCRs are simply an unavoidable product of large proteomes and emerge through genetic events that are insufficiently deleterious to be selected against). Some discussion on this would be helpful. it also makes me wonder if the authors' null proteome model is the "right" model, although I would also say developing an accurate and reasonable null model that accounts for repeat expansions is beyond what I would consider the scope of this paper.

While the role of repeat expansions in generating LCRs has been studied and discussed extensively in the LCR field, we decided to focus on the question of which LCRs exist in the proteome, and what may be the function downstream of that. The rationale for this is that while one might not expect a functional LCR to arise from repeat expansion, this argument is less of a concern in the presence of evidence that these LCRs are functional. For example, for many of these LCRs (e.g. a K-rich LCR, R/S-rich LCR, etc as in Figure 3), we know that it is sufficient for the integration of that sequence into the higher order assembly. Moreover, in more recent cases, variation of the length of an LCR was shown to have functional consequences (Basu et al., Cell, 2020), suggesting that LCR emergence through repeat expansions does not imply lack of function. Therefore, while we think the origin of a LCR is an interesting question, whether or not that LCR was gained through repeat expansions does not fall into the scope of this paper.

In regards to repeat expansions as it pertains to our choice of null model, we reasoned that because the origin of an LCR is not necessarily coupled to its function, it would be more useful to retain LCR sequences even if they may be more likely to occur given a background proteome composition. This way, instead of being tossed based on an assumption, LCRs can be evaluated on their function through other approaches which do not assume that likelihood of occurrence inversely relates to function.

While we maintain that the uniform background is the most appropriate, the question from this reviewer and the other reviewers made us realize that a thorough explanation was warranted for this choice of null proteome. For a complete explanation for our choice of this uniform null model, please see the newly added appendix section, Appendix 1.

The authors would also like to point out that the original SEG algorithm (Wootton and Federhen, 1993) also made the intentional choice of using a uniform background model.

Minor points

Early on the authors discuss the roles of LCRs in higher-order assemblies. They then make reference to the lysine tracts as having a valence of 2 or 3. It is possibly useful to mention that valence reflects the number of simultaneous partners that a protein can interact with - while it is certainly possible that a single lysine tracts interacts with a single partner simultaneously (meaning the tract contributes a valence of 1) I don't think the authors can know that, so it may be wise to avoid specifying the specific valence.

Thank you for pointing this out. We agree with the reviewer's interpretation and have removed our initial interpretation from the text and simply state that a copy number of at least two is required for RPA43’s integration into the nucleolus.

The authors make reference to Q/H LCRs. Recent work from Gutiérrez et al. eLife (2022) has argued that histidine-richness in some glutamine-rich LCRs is above the number expected based on codon bias, and may reflect a mode of pH sensing. This may be worth discussing.

We appreciate the reviewer pointing out this publication. While this manuscript wasn’t published when we wrote our paper, upon reading it we agree it has some very relevant findings. We have added a reference to this manuscript in our discussion when discussing Q/H-rich LCRs.

Eric Ross has a number of very nice papers on this topic, but sadly I don't think any of them are cited here. On the question of LCR composition and condensate recruitment, I would recommend Boncella et al. PNAS (2020). On the question of proteome-wide LCR analysis, see Cascarina et al PLoS CompBio (2018) and Cascarina et al PLoS CompBio 2020.

We appreciate the reviewer for noting this related body of work. We have updated the citations to include work from Eric Ross where relevant.

Author Response

Reviewer #1 (Public Review):

The authors sought to create a machine learning framework for analyzing video recordings of animal behavior, which is both efficient and runs in an unsupervised fashion. The authors construct Selfee from recent computational neural network codes. As the paper is methodsfocused, the key metrics for success would be (1) whether Selfee performs similarly or more accurately than existing methods, and more importantly (2) whether Selfee uncovers new behavioral features or dynamics otherwise missed by those existing methods.

Weaknesses:

Although the basic schematics of Selfee are laid out, and the code itself is available, I feel that material in between these two levels of description is somewhat lacking. Details of what other previously published machine learning code makes up Selfee, and how those parts work would be helpful. Some of this is in the methods section, but an expanded version aimed at a more general readership would be helpful.

Thanks for the suggestions. We expanded the paragraphs describing training objectives and AR-HMM analysis. We also revised Figure 2C for clarity, and we have added a new figure, Figure 6, to describe how our pipeline works in detail. We also added a detailed instructions for Selfee usage on our GitHub page.

*The paper highlights efficiency as an important aspect of machine learning analysis techniques in the introduction, but there is little follow up with this aspect.

Our model only had a more efficient training process compared with other self-supervised learning methods. We also found our model could perform zero-shot domain transfer, so training may not even be necessary. However, we did not mean that our model was superior in terms of data efficiency or inference speed. We have revised some of the claims in the Discussion.

*In comparing Selfee to other approaches, the paper uses DeepLabCut, but perhaps running other recent methods for more comprehensive comparison would be helpful as well.

We compare Selfee feature extraction with features from FlyTracker or JAABA, two widely used software. We also visualized the tracking results of SLEAP and FlyTracker in complement to the DeepLabCut experiment.

*Using Selfee to investigate courtship behavior and other interactions was nicely demonstrated. Running it on simpler data (say, videos of individual animals walking around or exploring a confined space) might more broadly establish the method's usefulness.

We used Selfee with open field test (OFT) of mice after chronic immobilization stress (CIS) treatment. We demonstrated that our pipeline from data preprocessing to all the data mining algorisms with this experiment, and the results were added to the last section of Results.

Reviewer #2 (Public Review):

Jia et al. present a CNN based tool named "Selfee" for unsupervised quantification of animal behavior that could be used for objectively analyzing animal behavior recorded in relatively simple setups commonly used by various neurobiology/ethology laboratories. This work is very relevant but has some serious unresolved issues for establishing credibility of the method.

Overall Strengths: Jia et al have leveraged a recent development "Simple Siamese CNNs" to work for behavioral segmentation. This is a terrific effort and theoretically very attractive.

Overall Weakness: Unfortunately, the data supporting the method is not as promising. It is also riddled with incomplete information and lack of rationale behind the experiments.

Specific points of concern:

1) No formal comparison with pre-existing methods like JAABA which would work on similar videos as Selfee.

We added some comparisons with JAABA and FlyTracker extracted features, and also visualized FlyTracker and SLEAP tracking results aside from DeepLabCut. This result is now in the new Table 1. To avoid tracking inaccuracy during intensive interactions and potential inappropriately tuned parameters, we used a peer-reviewed dataset focused on wing extension behavior only. Our results showed a competitive performance of Selfee as other methods.

2) For all Drosophila behavior experiments, I'm concerned about the control and test genetic background. Several studies have reported that social behaviors like courtship and aggression are highly visual and sensitive to genetic background and presence of "white" gene. The authors use Canton S (CS) flies as control data. Whereas it is unclear if any or all of the test genotypes have been crossed into this background. It would be helpful if authors provide genotype information for test flies.

We have added a detailed sheet about their genotype in this version. The genetic information of all animals can also be found on the Bloomington fly center by the IDs provided. In brief, five fly lines used in this work are in the CS background: CCHa2-R-RAGal4, CCHa2-R-RBGal4, Dop2RKO, DopEcRGal4 and Tdc2RO54. We did not back cross other flies into the CS background for three reasons. First, most mutant lines are compared with their appropriate control lines. For example, in the original Figure 3B (the new Figure 4B), for CCHa2-R-RBGal4 > Kir2.1 flies contained wildtype white gene, so the comparison with CS flies would not cause any problem. For TrhGal4 flies, they were in white background, and so were other lines that had no phenotype. At the same time, in the original Figure 3G to J (the new Figure 4G to J), we used w1118 as controls for TrhGal4 flies, which were all in mutated white background. Second, in the original Figure 4F and G (the new Figure 5F and G), we admitted that the comparison between NorpA36, in mutated white background, and CS flies was not very convincing. Nevertheless, the delayed dynamic of NorpA mutants was reported before, and our experiment was just a demonstration of the DTW algorithm. Lastly, our method focused on the methodology of animal behavior analysis, and original videos were provided for research replications. Therefore, even if the behavioral difference was due to genetic backgrounds, it would not affect the conclusion that our method could detect the difference

3) Utility of "anomaly score" rests on Fig 3 data. Authors write they screened "neurotransmitter-related mutants or neuron silenced lines" (lines 251-252). Yet Figure 3B lacks some of the most commonly occurring neurotransmitter mutants/neuron labeling lines (e.g. Acetelcholine, GABA, Dopamaine, instead there are some neurotransmitter receptor lines, but then again prominent ones are missing). This reduces the credibility of this data.

First of all, this paper did not intend to conduct new screening assays, rather we used pre-existed data in the lab to demonstrate the application of Selfee. Previous work in our lab focused on the homeostatic control of fly behaviors, so most listed lines used here were originally used to test the roles of neuropeptides or neurons nutrient and metabolism regulation, such as CCHarelated lines, a CNMa mutant, and Taotie neuron silenced flies. There were some other important genes that were not involved in this dataset. Some most common transmitters are not included for two reasons. First, common neurotransmitters usually have a very global and broad effect on animal behaviors, and even if there is any new discovery, it could be difficult to interpret the phenomenon due to a large number of disturbed neurons. Second, most mutants of those common neurotransmitters are not viable, for example, paleGal4 as a mutant for dopamine; Gad1A30 for GABA, and ChATl3 for acetylcholine. However, we did perform experiments on serotonin-related genes (SerT and Trh), octopamine-related genes (Tdc and Oamb), and some other viable dopamine receptor mutants.

4) The utility of AR-HMM following "Selfee" analysis rests on the IR76b mutant experiment (Fig4). This is the most perplexing experiment! There are so many receptors implicated in courtship and IR76b is definitely not among the most well-known. None of the citations for IR76b in this manuscript have anything to do with detection of female pheromones. IR76b is implicated in salt and amino acid sensation. The authors still call this "an extensively studies (co)receptor that is known to detect female pheromones" (lines310-311). Unsurprisingly the AR-HMM analysis doesn't find any difference in modules related to courtship. Unless I'm mistaken the premise for this experiment is wrong and hence not much weight should be given to its results.

We have removed the Ir76b results from the Results. The demonstration of AR-HMM was now done with a mouse open field assay.

Reviewer #3 (Public Review):

This paper is describing a machine learning method applied to videos of animals. The method requires very little pre-processing (end-to-end) such as image segmentation or background subtraction. The input images have three channels, mapping temporal information (liveframes). The architecture is based on tween deep neural networks (Siamese network) and does not require human annotated labels (unsupervised learning). However, labels can still be used if they are produced, as in this case, by the algorithm itself - self-supervised learning. This flavor of machine learning is reflected in the name of the method: "Selfee." The authors are convincingly applying the Selfee to several challenging animal behavior tasks which results in biologically relevant discoveries.

A significant advantage of unsupervised and self-supervised learning is twofold: 1) it allows for discovering new behaviors, and 2) it doesn't require human-produced labels.

In this case of self-supervised learning the features (meta-representations) are learned from two views of the same original image (live-frame), where one of the views is augmented in several different ways, with a hope to let the deep neural network (ResNet-50 architecture in this case) learn to ignore such augmentations, i.e. learn the meta-representations invariant to natural changes in the data similar to the augmentations. This is accomplished by utilizing a Siamese Convolutional Neural Network (CNN) with the ResNet-50 version as a backbone. Siamese networks are composed of tween deep nets, where each member of the pair is trying to predict the output of another. In applications such as face recognition they normally work in the supervised learning setting, by utilizing "triplets" containing "negative samples." These are the labels.

However, in the self-supervised setting, which "Selfee" is implementing, the negative samples are not required. Instead the same image (a positive sample) is viewed twice, as described above. Here the authors use the SimSiam core architecture described by Chen, X. & He, K (reference 29 in the paper). They add Cross-Level Discrimination (CLD) to the SimSiam core. Together these two components provide two Loss functions (Loss 1 and Loss 2). Both are critical for the extraction of useful features. In fact, removing the CLD causes major deterioration of the classification performance (Figure 2-figure supplement 5).

The authors demonstrate the utility of the Selfee by using the learned features (metarepresentations) for classification (supervised learning; with human annotation), discovering short-lasting new behaviors in flies by anomaly detection, long time-scale dynamics by ARHMM, and Dynamic Time Warping (DTW).

For the classification the authors use k-NN (flies) and LightGBM (mice) classifiers and they infer the labels from the Selfee embedding (for each frame), and the temporal context, using the time-windows of 21 frames and 81 frames, for k-NN classification and LightGBM classification, respectively. Accounting for the temporal context is especially important in mice (LightGBM classification) so the authors add additional windowed features, including frequency information. This is a neat approach. They quantify the classification performance by confusion matrices and compute the F1 for each.

Overall, I find these classification results compelling, but one general concern is the criticality of the CLD component for achieving any meaningful classification. I would suggest that the authors discuss in more depth why this component is so critical for the extraction of features (used in supervised classification) and compare their SimSiam architecture to other methods where the CLD component is implemented. In other words, to what degree is the SimSiam implementation an overkill? Could a simpler (and thus faster) method be used - with the CLD component - instead to achieve similar end-to-end classification? The answer would help illuminate the importance of the SimSiam architecture in Selfee.

We added more about the contribution of the CLD loss in the last paragraph of Siamese convolutional neural networks capture discriminative representations of animal posture, the second section of Results. Further optimization of neural network architectures was discussed in the Discussion section. As for why CLD is that important, there are two main reasons. First of all, all behavior photos are so similar that it is not very easy to distinguish them from each other. In the field of so-called self-supervised learning without negative samples, researchers use either batch normalization or similar operations to implicitly utilize negative samples within a minibatch. However, when all samples are quite similar, it might not be enough. CLD uses explicit clusters to utilize negative samples within a minibatch, in the word of the authors “Our key insight is that grouping could result from not just attraction, but also common repulsion”, so that provides more powerful discrimination. The second reason is what the author argued in the CLD paper, CLD is very powerful in processing long-tailed datasets. As shown in the original Figure 2—figure supplement 5 (the new Figure 3—figure supplement 5), behavior data are highly unbalanced. As explained in the CLD paper. CLD fights against long-tailed distribution from two aspects. One is that it scales up the importance of negative samples within a mini-batch from 1/B to 1/K by k-means; another is that cluster operation could relieve the imbalance between the tail and head classes within a mini-batch. Here I quote: “While the distribution of instances in a random mini-batch is long-tailed, it would be more flattened across classes after clustering.” It was also visualized in Fig5 of the CLD paper.

To the best of our knowledge, SimSiam is the simplest method that would work with CLD. In the original CLD paper, they combined CLD method with other popular frameworks including BYOL and Mocov2. However, those popular frameworks are more complicated than SimSiam networks. We have attempted to combine CLD with BarlowTwins but failed. As the author of CLD suggested on Github: “Hi, good to know that you are trying to combine CLD with BarLowTwins! My concern is also on the high feature dimension, which may cause the low clustering quality. Maybe it is necessary to have a projection layer to project the highdimensional feature space to a low-dimensional one.” In terms of speed, there are two major parts. For inference, only one branch is used, so the major contribution of efficiency comes from CNN backbone. In theory, light backbones like MobileNet would work, but ResNet50 is already fast enough on a model GPU. As for training, the major computational cost aside from the CNN backbone is from Siamese branches. Two branches, two times of computation. Nevertheless, CLD relied on this kind of structure, so even if the learning framework is simpler than Simsiam, it is not likely to achieve a faster training speed. As for other structures, I think this new instance learning framework (https://arxiv.org/abs/2201.10728) is possible to achieve a similar result with fewer data and in a shorter time. However, this powerful method could be used with CLD. We might try it in the future.

One potential issue with unsupervised/self-supervised learning is that it "discovers" new classes based, not on behavioral features but rather on some other, irrelevant, properties of the video, e.g. proximity to the edges, a particular camera angle, or a distortion. In supervised learning the algorithm learns the features that are invariant to such properties, because humanmade labels are used and humans are great at finding these invariant features. The authors do mention a potential limitation, related to this issue, in the Discussion ("mode splitting"). One way of getting around this issue, other than providing negative samples, is to use a very homogeneous environment (so that only invariance to orientation, translation, etc, needs to be accomplished). This has worked nicely, for example, with posture embedding (Berman, G. J., et al; reference 19 in the manuscript). Looking at the t-SNE plots in Figure 2 one must wonder how many of the "clusters" present there are the result of such learning of irrelevant (for behavior) features, i.e. how good is the generalization of the meta-representations. The authors should explore the behaviors found in different parts of the t-SNE maps and evaluate the effect of the irrelevant features on their distributions. For example, they may ask: to what extent does the distance of an animal from the nearest wall affect the position in the t-SNE map? It would be nice to see how various simple pre-processing steps might affect the t-SNE maps, as well as the classification performance. Some form of segmentation, even very crude, or simply background subtraction, could go a very long way towards improving the features learned by Selfee.

In the new Figure 3—figure supplement 1, the visualization demonstrates that our features contained a lot of physical information, including wing angles, animal distance and positions in the chamber. “Mode-split” can be partially explained by those features. We actually performed background subtraction and image crop for mice behaviors, where we found them useful.

The anomaly detection is used to find unusual short-lasting events during male-male interaction behavior (Figure 3). The method is explained clearly. The results show how Selfee discovered a mutant line with a particularly high anomaly score. The authors managed to identify this behavior as "brief tussle behavior mixed with copulation attempts." The anomaly detection analyses were also applied to discover another unusual phenotype (close body contact) in another mutant line. Both results are significant when compared to the control groups.

The authors then apply AR-HMM and DTW to study the time dynamics of courtship behavior. Here too, they discover two phenotypes with unusual courtship dynamics, one in an olfactory mutant, and another in flies where the mutation affects visual transduction. Both results are compelling.

The authors explain their usage of DTW clearly, but they should expand the description of the AR-HMM so that the reader doesn't have to study the original sources.

We expanded the section that talks about AR-HMM mechanisms.

Author Response

Reviewer #1 (Public Review):

This work offers a simple explanation to a fundamental question in cell biology: what dictates the volume of a cell and of its nucleus, focusing on yeast cells. The central message is that all this can be explained by an osmotic equilibrium, using the classical Van't Hoff's Law. The novelty resides in an effort to provide actual numbers experimentally.

In this work, Lemière and colleagues combine physical modeling and quantitative measures to establish the basic principles that dictate the volume of a cell and of its nucleus. By doing so, they also explain an observation reported many times and in many different types of cells, of a proportionality between the volume of the cell and of its nucleus. The central message is that all this can be explained by an osmotic equilibrium, using the classical Van't Hoff's Law. This is because, in yeast cells, while the cell has a wall that can contribute to the equilibrium, the nucleus does not have a lamina and there is thus no elastic contribution in the force balance for the nucleus, as the authors show very nicely experimentally, using both cells and protoplasts and measuring the cell and nucleus volume for various external osmotic pressures (the Boyle Van't Hoff Law for a perfect gas, also sometimes called the Ponder relation) ¬- this was performed before for mammalian cells (Finan et al.), as cited and commented in the discussion by the authors, showing that mammalian cells have no significant elastic wall (linear relation) while the nucleus has one (non linear relation). This is well explained by the authors in the discussion. It is one of the clearer experimental results of the article. Together, the data and model presented in this article offer a simple explanation to a fundamental question in cell biology. In this matter, the principles are indeed seemingly simple, but what really counts are the actual numbers. While this article sheds some light on this aspect, it does not totally solve the question. The experiments are very well done and quantified, but some approximations made in the modeling are questionable and should at least be discussed in more length. Overall, this article is extremely valuable in the context of the recent effort of the cell biology and biophysics communities to understand the fundamental question of what dictates the size of cells and organelles. I have a few concerns detailed below. Importantly, there are many very interesting points of the article that I am not discussing below, simply because I completely agree with them.

1) The main concern is about the assumption made by the authors that the small osmolytes do not count to establish the volume of the nucleus. It was shown that small osmolytes such as ions are a vast majority of the osmolytes in a cell (more than ten times more abundant than proteins for example, which represent about 10 mM, for a total of 500 mM of osmolytes). This means that just a small imbalance in the amount of these between the nucleus and cytoplasm might have a much larger effect than the number of proteins, which is the osmolyte that authors choose to consider for the nuclear volume.

The point of the authors to disregard small osmolytes is that they can freely diffuse between the cytoplasm and the nucleus through the nuclear pores. They thus consider that the nuclear volume is established thanks to the barrier function of the nuclear envelope, which would retain larger osmolytes inside the nucleus and that the rest is balanced. This reasoning is not correct: for example, the volume of charged polymers depends on the concentration of ions in the polymer while there is no membrane at all to retain them. This is because of an important principle that the authors do not include in their reasoning, which is electro-neutrality.

Because most large molecules in the cell are charged (proteins and also DNA for the nucleus), the number of counterions is large, and is probably much larger than the number of proteins. So it is hard to argue that this could be ignored in the number of osmotically active molecules in the nucleus. This is known as the Donnan equilibrium and the question is thus whether this is actually the principle which dictates the nuclear volume.

The question then becomes whether the number of counterions differs between the cytoplasm and the nucleus, and more precisely whether the difference is larger than the difference considered by the authors in the number of proteins.

How is it possible to estimate this number? One of the numbers found in the literature is the electric potential across the nuclear envelope (Mazanti Physiological Reviews 2001). The number is between 1 and 10 mV, with more cations in the nucleus than in the cytoplasm. This number could correspond to much more cations than the number of proteins, although the precise number is not so simple to compute and the precision of the measure matters a lot, since there is an exponential relation between the concentrations and the potential.

This point above is simply made to explain that the authors cannot rule out the contribution of small osmolytes to the nuclear volume and should at least leave this possibility open in the discussion of their article.

As a conclusion, I totally agree with equation 3 which defines the N/C ratio, but I think that the Ns considered might not be the number of large macromolecules which cannot pass the nuclear envelope, but rather the small ones. Whether it is the case or not and what is actually the important species to consider depends on the actual numbers and these numbers are not established in this article. It is likely out of the scope of the article to establish them, but the point should at least be discussed and left open for future studies.

We appreciate these excellent points made by the reviewer and their numerous consultants. We amend the discussion of colloid osmotic pressure in the text to reflect these points.

2) The authors refer to the notion of colloidal pressure, discussed in the review by Mitchison et al. This term could be confusing and the authors should either explain it better or just not use it and call it perfect gas pressure or Van't Hoff pressure. Indeed, what is meant by colloidal pressure is simply the notion that all molecules could be considered as individual objects, independently of their size, and that it is then possible to apply the Van't Hoff Law just as it was a perfect gas, hence the notion of 'colloidal' pressure, which would be the osmotic pressure of all the individual molecules. The authors might want to discuss, or at least mention, that it is a bit surprising that all these crowded large macromolecules would behave like a perfect osmometer and that the Van't Hoff law applies to them. Alternatively, it could be simpler to consider that what actually counts for the volume is mostly small freely diffusing osmolytes, to which this law applies well, and which are much more numerous.

3) Very small point: on page 7 the authors refer to BVH's Law (Nobel, 1969). It is not clear what they mean. If they refer to the Nobel prize of Van't Hoff, it dates from 1901 (he died in 1911) and not 1969. I am not sure if there is something in one of the Nobel prizes delivered in 1969 which relates to this law. I checked but it does not seem to be the case, so it is probably a mistake in the date.

The citation is correct. It's a JTB paper by Park S. Nobel describing the BHV relation in biology.

4) On page 11, bottom, the result of the maintenance of the N/C ratio in protoplast is presented as an additional result, while it is a simple consequence of the previous results: both the cell and nuclear volume change linearly with the external osmotic pressure, so it is obvious that their ratio does not change when the external pressure is changed.

This result was not trivial. Although both cells and nuclei volume change linearly with the inverse of the external osmotic concentration in protoplasts, it was not obvious whether the two volumes change with the same proportion (ie same slope on the BVH graph).

Another result, not commented by the authors, is that this should be true only in protoplasts, since in whole cells, the cell wall is affecting the response of the cell volume, but not the nucleus, so the ratio should change.

In whole cells, the maintenance of the N/C ratio is in fact also maintained, consistent with the model. This result is now clarified in the manuscript (Figure 1C and D plus Figures 3D and S1C).

5) The results in Figure 5, with the inhibition of export from the nucleus, are presented as supporting the model. It is not really clear that they do. First the effect is very small, even if very clear. Again, the numbers matter here, so the interpretation of this result is not really direct and more calculation should be made to understand whether it can really be explained by a change of number of proteins. The result in panel F is even more problematic. The authors try to argue that the nucleus transiently gets denser, based on the diffusion of the GEMs and then adapts its density. It rather seems that it is overall quite constant in density, while it is the cell which has a decreasing density ¬- maybe, as suggested by the authors, because there are less ribosomes in the cytoplasm, so protein production is reduced. This could have an indirect effect on the number of amino acids (which would then be less consumed). A recent article by Neurohr et al (Trends in cell biology, 2020) suggests that such an effect can lead to cell dilution, in yeast, because the number of amino acids increases. In this particular case, this increase would affect the nuclear volume rather than the cell volume because of the presence of the cell wall and the rather small change.

We agree that there are different possible interpretations for these results. We have carefully reconsidered the interpretation and have rewritten the entire text for Figure 5

6) Page 16: it seems to me that the experiments presented in the chapter lines 360 to 376, on the ribosomal subunits, simply confirm that export is impaired, and they do not really contribute to confirm the hypothesis of the authors that it is the number of proteins in the nucleus which counts.

We agree. We highlight the ribosomal subunit proteins as they are very abundant nuclear shuttling proteins that provide a good example for the dynamics of nuclear protein accumulation.

The next paragraph with the estimation of the number of proteins in the nucleus and cytoplasm and how they change relatively upon export inhibition also appears to mostly demonstrate that export has been inhibited.

The authors propose to use the number they find, 8%, to compare it to the change in the N/C ratio, which is of the same order. Given how small these numbers are, and the precision of such measures, it is very hard to believe that these 8% are really precise at a level which could allow such a comparison. The authors should really estimate the precision of their measures if they want to claim that. It is more likely that what they observe is a small but significant change in both cases; a small change means it is small compared to the total, so it is a fraction of it, and it is measurable, which means it is more than just a few percent, which is usually not possible to measure. So it means that it is in the order of 10%. This is the typical value of any small but measurable change given a method for the measure which can detect changes around 10%. In conclusion, these numbers might not prove anything.

It could also be that the numbers match not just by chance, but that the osmolyte which matters is, for this type of experiment, changing in proportion to the amount of proteins (which would be possible for counter ions for example). But determining all that requires precise calculations and additional measures. It is thus more a matter of discussion and should be left more open by the authors.

We agree that these measurements are not so precise. We have carefully reworded this section and removed these specific comparisons.

Reviewer #2 (Public Review):

The goal of the paper is to test the idea that colloidal osmotic pressure controls nuclear growth as suggested by Tim Mitchison in a recent review.

In fleshing out the idea, Lemiere and colleagues develop a simple mathematical model that focuses on the forces generated by the movement of macromolecules across the nuclear-cytoplasmic boundary, ignoring any contribution of ions or small molecules which they assume equilibrate across the nuclear envelope. In testing this model, they focus their quantitative analysis on the response of cells that lack a wall (protoplasts) to osmotic shocks and to perturbations of nuclear export, protein synthesis and symmetric cell division. They also analyse the motion of small 40nm particles to test how diffusion is affected by these perturbations in both compartments.

Their analysis leads them to make some important observations that suggest that the system is even simpler than they might have hoped, since under the conditions tested nuclei (which lack lamins) behave as ideal osmometers. That is, the nuclei and cytoplasm grow and shrink in concert following sudden osmotic shocks. This suggests that the tension in the nuclear envelope, which gives nuclei their spherical shape, plays no role in constraining nuclear size.

While most of the paper's claims are well supported by their data under the assumptions of the model, there are a few claims that are less convincing.

For example, while their data are consistent with the idea that cells regulate their nuclear/cytoplasmic size ration using an adder type mechanism, in which a fix ratio of nuclear and cytoplasmic proteins are synthesised per unit time as cells grow, this has not been rigorously put to the test. In addition, while the diffusion analysis is very interesting, it does not fully support the authors' simple model linking diffusion, molecular crowding and colloidal osmotic pressure, something that could be more thoroughly discussed in the manuscript.

We added new data showing that slowing growth rate leads to a proportionate decrease in N/C ratio correction. This strengthens this portion of the paper.

We have added an improved discussion of the GEMs data and its limitations.

Reviewer #3 (Public Review):

This manuscript by Lemière and colleagues presents a view on how nuclear size is set by simple physical principles. The first part of the work describes a theoretical framework with the nucleus and the cell as two nested osmometers. Using fission yeast as a model, the authors then show that protoplasts and nuclei behave as ideal osmometers, i.e. show linear changes in volume upon change in external osmotic pressure. Consequently, the nuclear to cell volume ratio remains constant upon osmotic changes, but increases upon block of nuclear export, which leads to higher nuclear protein contents. Measurements of diffusion in the cytoplasm and nucleoplasm back these data. Finally, in the last part of the manuscript, the authors show that nuclear growth through a passive osmotic model can explain the previously described homeostasis of nuclear volume.

The manuscript is clearly written, and the data are clean and overall solid. I very much liked the simple view on the phenomenon of constant nuclear to cytosol ratio and the mix of modelling and experiments supporting the model that nuclear size is set passively by osmotic principles.

There are however a few points that are slightly at odds with the model and/or require further explanation to make the model compelling and discuss it in view of previous findings.

1) Isn't the finding that diffusion rates are faster in the nucleus (line 298, Fig S4C), indicating lower crowding in the nucleus, at odds with the finding that the non-osmotic volumes are similar in the two compartments? If the nucleus is less crowded, does this not suggest a lower pressure than the cytosol? I would also like to see this finding appear in Figure 4, which only reports on the normalized diffusion rates in both nuclei and cytosol.

We have added this figure to the main Figure 4, as requested. We agree that this raises some interesting questions. Our current interpretation is that composition of the nucleoplasm and cytoplasm are different and therefore affect GEMs diffusion and colloid osmotic pressure slightly differently.

2) Similarly, I don't understand the observed change in diffusion rates of GEMs upon LMB treatment (Fig 5F). If the nucleus behaves as an ideal osmometer, then any change in protein density between the nucleus and the cytosol, leading to change in osmotic pressure, will lead to a change in nuclear size that should re-equilibrate the osmotic pressures between the two compartments. The prediction would thus be that, if LMB treatment does not change overall protein concentration, at equilibrium there is no change in either osmotic pressure or density as measured by GEM diffusion rates. This is indeed illustrated by the constant normalized non-osmotic volume of the nucleus after LMB treatment. Is the change in diffusion rates perhaps only transient until a new steady state is reached? Or is there a change upon total protein content in the cell after LMB treatment?

3) In the experiments labelling proteins with FITC, are the reported values really those of protein concentrations or rather protein amounts? Isn't the enlargement of the nucleus upon LMB treatment compensating for this increase in amounts, returning the nucleus to a similar concentration as before treatment? A change in concentration is not in agreement with the reported constant non-osmotic volume of the nucleus.

These measurements of intensity are of concentrations. We add in the text this prediction that changes in concentration will be compensated for by swelling in nuclear volume and now interpret the data in light of this prediction. We add new data that total FITC staining for protein and RNA shows no change in concentration in compartments, consistent with this model.

4) The authors state that "a previous paper proposed a model for N/C ratio homeostasis based upon an active feedback mechanism (Cantwell and Nurse, 2019)" (lines 471-472). My understanding of this previous study is that nuclear size was proposed to be set by a limiting component, itself proportional to cell volume. No feedback was postulated. This previous model is in fact not too different from what the authors propose here, with the previously proposed limiting component now corresponding to the nuclear macromolecules that produce colloid osmotic pressure and thus set nuclear size. Though the present study goes significantly further in presenting the passive role of osmosis in setting nuclear size, it is a misrepresentation to portray this previous model as fundamentally different. Furthermore, it is not clear whether the new osmotic pressure-based model produces a better fit than the previous 'limiting component model'. Figure 7E here is very similar to Fig 4I in Cantwell and Nurse 2019, but it is difficult to judge the similarity of the fits.

The Cantwell and Nurse paper tested two models. The first was based upon nuclear growth being a fraction of cell growth. This model is qualitatively similar to ours. However, they discarded this initial model because it fitted poorly with their data. They then went to propose a second model, which contains a critical equation in which nuclear growth rate is a function of the N/C ratio, i.e. the system is sensing the N/C ratio and adjusting nuclear growth rate as a function of the N/C ratio. In other words, this is a feedback mechanism. The Cantwell paper does not describe this "feedback" term explicitly in the text, but it is clearly present in the equations. Therefore, our model which lacks any feedback term is fundamentally different from the Cantwell limiting component model.

We show that our model fits our data much better than the Cantwell model. We believe that the different views in these studies arise from differences in the experimental data. These differences may arise from two technical differences: 1) Their use of binning could be responsible for flattening the nuclear growth rate as a function of the nuclear volume at start. 2) Their estimates of cell and nuclear volumes using a 2D image and geometric assumptions may be less accurate than our automated 3D volume method.

5) If nuclear size is set purely by osmotic regulation, how do you explain that mutants in membrane regulation (such as nem1 and spo7, see Kume et al 2017; or lem2, see Kume et al 2019) previously shown to have an enlarged nucleus, display increased nuclear size?

This is an interesting question that we are currently pursuing. It is likely that these mutants affect multiple processes besides nuclear envelope expansion. For example, at least some of these mutants have altered chromatin organization could cause increase in colloid pressure. There may also be significant defects in chromosome segregation, which leads to production of different-sized nuclei with abnormal number of chromosomes. Some of the N/C ratio defects reported in these papers may arise from their 2D measurement methods, which are not accurate for misshapen nuclei. In our preliminary results, lem2 mutants do not have N/C ratio defects.

Author Response

Reviewer #1 (Public Review):

Kosillo et al. used dopamine neuron-specific cKO mice to examine the contributions of mTORC1 (Raptor cKO) and mTORC2 (Rictor cKO) to dopamine neuron dendrite and axon morphology, neuronal electrophysiological properties and dopamine release. Overall, Raptor cKO mice have stronger deficits as compared to Rictor cKO, while double cKO had additional deficits. These results suggest that mTORC1 is more critical to dopamine neuron function, and that there is some functional redundancy between mTORC1 and mTORC2.

The data presented is generally of high quality, and the conclusions drawn are consistent with the data presented. I have the following concerns:

1) Conclusion point 3: "mTORC2 inhibition leads to distinct cellular changes not observed following mTORC1 suppression, suggesting some independent actions of the two mTOR complexes in DA neurons." Currently, data supporting this conclusion is weak.

We appreciate the reviewer’s comment. Although we do see some distinct cellular changes, we agree that these are minor and we have removed this sentence from the main conclusions paragraph in the discussion.

Specifically, WT SNc DA neurons do not have typical morphology (very different from all other neurons, including WT neurons in Fig 1o), making the observed increase in proximal dendrite morphology hard to interpret.

We have replaced the example images in Fig. 2m with better representative examples of WT SNc DA neurons

Data presented in Figure 1o suggest no significant increase in total dendrite length. Are there changes in primary dendrite number?

We do find that deletion of Rptor from SNc and VTA neurons causes a reduction in total dendrite length (new Fig. 1u,v), which is observable in the example images (Fig. 1o,p) showing shorter dendrites in DA-Raptor KO cells. We have now quantified primary dendrite number in both DA-Raptor and DA-Rictor KO neurons and find that there are no significant differences compared to control neurons. These new data have been added to Figures 1 and 2

The electrophysiological results presented in Fig 5 are inconsistent with increased dendrite arborization. The authors need to either provide more evidence showing significant increase in dendrite morphology in Rictor cKO mice, or reinterpret their results.

While we do find that DA-Rictor KO neurons have increased dendritic complexity at 50-100µm from the soma by Sholl analysis, total dendrite length is not significantly changed (new Fig. 2mt). Since the cell body size of Rictor cKO DA neurons is significantly reduced, we believe that this is responsible for the reduced membrane capacitance and slightly increased resistance observed in these cells (Fig. 5a,f,g)

2) The manuscript is repetitive in some places, and the discussion largely reiterates the results. Could the authors please discuss why mTORC1 signaling contributes more to dopamine neuron function, as compared to mTORC2, based on existing knowledge of gene function and expression. Another point of interest is how the different parameters they measure are related, i.e. which parameters may be more causal than others in terms of changes in dopamine neuron function.

We thank the reviewer for this suggestion. We have significantly revised the discussion section and added further discussion of mTORC1 and mTORC2 functions as they relate to DA neuron properties.

Reviewer #3 (Public Review):

In this paper, Kosillo et al. investigated the structural and functional alterations of dopamine neurons in dopamine neuron-specific Raptor and Rictor KO mice. Physiological functions and cellular structures were broadly and markedly affected in Raptor cKO mice, while Rictor cKO mice exhibited marginal changes, indicating that each adaptor protein of mTOR in either mTORC1 or mTORC2 may play both similar or distinct roles in the maintenance of dopaminergic structures and functions. Non-specific activation or inhibition of mTOR pathways in the previous literatures have hampered the understanding of molecular mechanisms behind the functions of mTOR pathways in dopamine neurons and related brain diseases. By utilizing dopamine neuron-specific Raptor and Rictor cKO mice, this paper elucidated which of these mTOR complexes are responsible for the regulation of dopamine neuronal functions, revealing the importance of mTORC1/2 signaling for the structure and function of dopamine neurons. Providing comprehensive data including structural, physiological, and biochemical alterations by genetic deletion of Raptor/Rictor in dopamine neurons is another strong point of this paper. However, lack of mechanistic evidence directly (or indirectly) linking the deletion of Raptor (or Rictor) to the alterations in TH/DAT/p-DAT/neuronal structures is a weak point of this manuscript. Overall, the conclusion of this paper is unbiased, just reflecting the data presented.

We appreciate the reviewer’s positive comments on our manuscript. The goal of this study was to provide a thorough characterization of the effects of Raptor or Rictor loss on dopamine neuron properties. We acknowledge that while we have identified significant changes in dopamine neuron structure and function driven by mTORC1 deficiency, we have not yet probed the downstream mechanisms that may be responsible. We believe this is beyond the scope of the current manuscript but would be of interest for future studies.

Author Response

Reviewer #1 (Public Review):

Weaknesses:

The data presented in the first part of the study are convincing. However, it is unclear whether each step of cell elongation and alignment, cell migration, cell dedifferentiation and regenerative response, is required for fin regeneration following amputation. As indicated in the discussion, the authors cannot provide evidence for the requirement of migration or dedifferentiation for the overall success of fin regeneration. Such limitations should be more clearly stated.

We have modified the title and abstract to avoid overstating the requirement of the particular responses to successful regeneration. Furthermore, we have stated the limitations of our study more clearly in the discussion.

We have removed the word “requires” from the title, it now reads: Zebrafish fin regeneration involves generic and regeneration-specific osteoblast injury responses

In the discussion we state the limitations on page 21 as follows:

“Unfortunately, currently existing tools to block dedifferentiation are either mosaic (activation of NF- κB signalling using the Cre-lox system) or cannot be targeted to osteoblasts alone (treatment with retinoic acid). Due to these limitations in our assays, we can currently not test what consequences specific, unmitigated perturbation of osteoblast dedifferentiation has for overall fin / bone regeneration. Conversely, the interventions presented here that specifically perturb osteoblast migration are limited as they act only transiently, that is they can severely delay, but not fully block migration. Furthermore, while interference with actomyosin dynamics reduces regenerative growth, we cannot distinguish whether this is caused by the inhibition of osteoblast migration or due to other more direct effects on cell proliferation and tissue growth. Thus, an unequivocal test of the importance of osteoblast migration for bone regeneration requires different tools.”

In the second part of the study, the term trauma needs to be clarified or reconsidered. A trauma model would imply that healing is impaired. Evidence for a non-healing phenotype is lacking and is expected in support of a trauma model.

We apologize if our use of the term trauma has caused confusion. We have simply used it interchangeably with “injury”. We have now removed all references to “trauma” in the text.

The authors describe the process of fin regeneration that may share common features with bone regeneration in other species. In the absence of direct evidence of common mechanisms between fin regeneration and bone regeneration in other systems, the authors should remain focused on "fin regeneration" in their conclusions rather than referring to "bone regeneration" and "bone formation" in more general terms.

We have rephrased the conclusion to have it more centred on bone regeneration in the fin. The relevant parts of the discussion now read on page 25 as follows:

In conclusion, our findings support a model in which zebrafish fin bone regeneration involves both generic and regeneration-specific injury responses of osteoblasts. Morphology changes and directed migration towards the injury site as well as dedifferentiation represent generic responses that occur at all injuries even if they are not followed by regenerative bone formation. While migration and dedifferentiation can be uncoupled and are (at least partially) independently regulated, they appear to be triggered by signals that emanate from all bone injuries. In contrast, migration off the bone matrix into the bone defect, formation of a population of (pre-) osteoblasts and regenerative bone formation represent regeneration-specific responses that require additional signals that are only present at distal-facing injuries. The identification of molecular determinants of the generic vs regenerative responses will be an interesting avenue for future research.

Reviewer #2 (Public Review):

The study by Sehring et al. depends on an extensive and thoroughly acquired collection of data points in combination with a robust and rigorous statistical analysis. I see that the authors have spent a lot of effort into this and I am overwhelmed by the number of analyzed data points that again depend on careful measurements at the cellular level in a more or less intact tissue. However, since just a fraction of cells has been chosen to be incorporated into the statistical analysis, there is a certain risk of a biased selection. I think the reader of the paper would appreciate a somewhat clearer picture of how the authors get to their final numbers, starting from the original image data. This appears of particular importance when it comes to determining the elongation of cells and the angular deviations from the proximo-distal axis. In many cases (e.g. Fig.2 A, B, D and E), the reader has to take those numbers without seeing any primary image data. A practicable solution to that issue would be to complement the accompanying Excel sheets of raw data with corresponding image material. This should show an overview of a representative sample for the dedicated experiment, together with some appropriate magnifications of analyzed cells including the axes along which those measurements have been performed. Also, it would be important to state within the methods section of the paper whether the measurements have been done manually using Fiji or whether a certain automated Fiji plug-in has been used for this part of the analysis.

Osteoblasts line the bony hemirays on the inner and outer surface (see Figure 1A), and for quantifications of osteoblast morphology, we analysed the osteoblasts of the outer layer of one hemiray (the hemiray facing the objective in whole mount imaging). While we have no direct evidence for this, we think it is reasonable to assume that osteoblasts in the other “sister” hemiray behave the same, and we have anecdotal evidence that osteoblasts on the inner surface of the hemirays also migrate and dedifferentiate. Thus, we don’t think that restriction of the analysis to one hemiray and the outer surface introduces bias.

For measurement of morphology, we used a transgenic line expressing a fluorescent protein (FP) in osteoblasts in combination with Zns5 antibody labelling. Zns5 is a pan-osteoblastic marker which localizes to the cell membrane. Therefore, combination of a cytosolic FP labelling with the membrane labelling by Zns5 provides solid definition of single cell outlines. For general morphology studies and drug intervention studies, we used bglap:GFP transgenics. In the transgenic intervention studies (manipulation of NF-kB signalling), mCherry is expressed together with CreERT2 under the osterix promoter and used as cytosolic labelling of osteoblasts. Our analyses are always based on segments, e.g. we present data for segments 0, -1, 2. Within these segments all FP+ Zns5+ cells were included into the analysis, and cells along the whole proximodistal axis of a segment were measured. Measurements were performed manually, and the analysist was blinded. With these set-ups, not only a fraction but all FP+ Zns5+ osteoblasts present in those segments that we analysed were included into the analysis, and thus no selection was necessary that could have introduced bias. As suggested by Reviewer #2, we have added representative sample images to the accompanying Excel sheets of raw data for the dedicated experiments. Within these, the axes along which the measurements have been performed are indicated.

We have expanded the description of the analysis in the method section. It now reads on page 36 as follows:

“To quantify osteoblast cell shape and orientation, the transgenic line bglap:GFP in combination with Zns5 AB labelling was used. Osteoblasts of the outer layer of one hemiray (facing the objective in whole fin mounting) were imaged and analysed. As Zns5 localizes to the plasma membrane of all osteoblasts, the combination of both markers provides solid definition of single cell outlines. All GFP+ Zns5+ cells with such a defined outline within an analysed segment were included into the analysis, and cells along the whole proximodistal axis of a segment were measured. In the transgenic intervention studies, mCherry is expressed under the osx promoter and was used as cytosolic labelling of osteoblasts. Using Fiji (Schindelin et al., 2012), the longest axis of a FP+ Zns5+ cell was measured as maximum length, the short axis as maximum width, and the ratio calculated. Simultaneously, the angle of the maximum length towards the proximodistal ray axis was measured for angular deviation. All measurements were performed manually, with the analyst being blinded.”

Along the same line, it would strengthen the statement provided by the statistical diagram in Fig.3A if the authors could show images of cells from segment -1 and -2 for all three experimental conditions. In particular, since the depicted segment -1 osteoblasts look rather roundish than elongated (compare with Fig.1 C and D, images and width/length ratio).

As suggested by the reviewer, we have added representative sample images of cells in segment -1 to the figure, the images that were already there in the previous version of the figure were from segment -2 (new data in Figure 4A). As legible from the graphs, there is a certain range of morphology within each segment / assay with an obvious overlap between the segments. This can make it difficult to realize the difference between the segments by looking on the images alone, and we have therefore added arrowheads to highlight examples of roundish and elongated cells. Yet as mentioned above, all cells were included into the analysis.

In regards to the biology itself, Sehring and colleagues claim that the complement system is required for injury-induced directed osteoblast migration. To strengthen this point it would be beneficial if the authors could show that the central complement components C3 and C5 are indeed expressed at the amputation site where the dedifferentiated pre-osteoblasts migrate to. It would be interesting to learn about the localization of C3 and C5 expression in the conventional amputation as well as the double-injury condition. Apparently, the RNAscope-based in situ hybridization seems to work quite well in the Weidinger lab.

Complement precursor proteins are thought to be mainly expressed in the liver and distributed throughout the body via the circulation. Injury would then result in local production of the activated C3a and C5a peptides via a cascade of proteolytic processing. Unfortunately, we lack the tools to detect the C3 and C5 precursor proteins or the mature cleavage products of the complement factors, which mediate the biological function of the cascade (e.g. antibodies against the zebrafish proteins / peptides). We have also attempted RNAScope for c5a and c3a.1 in fins, but these turned out to not produce any specific stainings, thus the results of these experiments remained inconclusive and we have not included them in the manuscript.

However, we analysed expression of the RNA coding for the precursors of the complement factors c5 and the six zebrafish paralogs of c3 using qRT-PCR on liver, non-injured fins and fins at 6 hpa (samples derived from segment -1 plus segment 0). These new data can be found in Figure 5B. Compared to the expression levels in the liver, expression in non-injured fins could hardly be detected. Interestingly, c5 and c3a.5 levels were upregulated in injured fins, but compared to the expression in the liver still only slightly, e.g. c5 is about 17 Ct values (2 to the power of 17 = 130000 times) more highly expressed in the liver than in the injured fin. These results are consistent with the idea that the majority of complement factors that are activated after injury is derived from precursors that are expressed in the liver and are distributed via the circulation to the fin, as is considered standard for the complement system. Interestingly, however, local production might contribute as well.

Overall our new data support our conclusion that the complement system is an important regulator of osteoblast migration in vivo, since the receptors are present in osteoblasts (see also response to the next issue), while systemic and local expression can provide the precursors for injury-induced production of the activated factors that might act as guidance cues.

To judge whether this osteoblast's migratory response is cell-type specific and cell-autonomous it would be good to know if c5ar1 and c3ar are solely expressed in osteoblasts, or rather broadly within tissue lining the hemirays.

While we had already shown that c5aR1 is expressed in osteoblasts, we have now added additional RNAscope in situ analysis for c5aR1 showing that the receptor is also expressed in other cell types (new data in Figure 5 – figure supplement 1A). We have also attempted RNAScope for c3aR in fins, which however did not produce specific staining, thus remained inconclusive; we have not added these data to the manuscript. However, we established fluorescent activated cell sorting from bglap:GFP transgenic fins, which gives us an additional tool to analyse to which extent expression is specific to osteoblasts. By qRT-PCR analysis we found that c5aR1 and c3aR are expressed in both GFP+ osteoblasts and other cells that are GFP– (these will mainly represent epidermis and fibroblasts, to a lesser extent endothelial and other cell types). These new data can be found in Figure 5 – figure supplement 1B.

While our qRT-PCR data and the c5aR1 RNAScope results show that the complement receptors are not specifically expressed in osteoblasts, we do not consider this result to be in conflict with our model that the complement system regulates osteoblast migration. Other cell types migrate after fin amputation as well, which is best described for epidermal cells (Chen et al., Dev Cell 2016, 10.1016/j.devcel.2016.02.017), but likely also occurs for fibroblasts (Poleo et al., DevDyn 2001, doi: 10.1002/dvdy.1152), and it is conceivable that the complement system plays a role in regulating these events as well.

Reviewer #3 (Public Review):

Weaknesses:

1) The major conclusions on osteoblast dedifferentiation and migration are solely based on a bglap:GFP strain, which does not allow a pulse-chase approach in injury responses. Specificity of this strain to osteoblasts is also doubtful because as many as 20% of GFP+ cells are in proliferation. Specificity of bglap:GFP to mature osteoblasts is a major concern. Important caveats associated with this reporter strain are not carefully considered.

To address these comments, we have performed several additional experiments as described below. In addition, we would like to refer the reviewer to our previous papers, where we have analysed the process of osteoblast dedifferentiation (Knopf et al., Dev Cell 2011, doi: 10.1016/j.devcel.2011.04.014; Geurtzen et al., Development 2014, doi: 10.1242/dev.105817; Mishra et al. Dev Cell 2020, doi: 10.1016/j.devcel.2019.11.016). Using transgenic reporters and immunofluorescence we have shown in these previous papers that osteoblasts in the non-injured fin express Bglap but not the pre-osteoblast marker Runx2 (and are thus by our definition differentiated). We apologize if we failed to explain the logic of our approach in this manuscript, we have restructured the results to clarify these, as indicated below.

We have also performed the following additional experiments.

1) To confirm the specificity of the bglap:GFP line for mature osteoblasts, we have performed three experiments:

a) immunofluorescence against Runx2 on 7 dpa regenerates, at a stage where blastema proliferation at the distal tip of the regenerate produces new osteoblast progenitors, while in more proximal (older) regions osteoblasts have already started to differentiate and new bone matrix has formed. We found that Runx2 is expressed in distal regions in pre-osteoblasts, while bglap:GFP is only expressed in proximal regions in osteoblasts which do not express Runx2. Thus, formation of new bony segment during regenerative growth, bglap:GFP is activated in mature osteoblasts and the population does not include osteoblast precursor cells. These new data are found in Figure 2 – figure supplement 2B.

b) we have refined and expanded our methods and are now able to determine the expression patterns of markers of the osteoblast differentiation status with single cell resolution using RNAScope in situ hybridization. Using this, we can now show that at 1 day post amputation, in segment -2 of the fin stump, which represents a segment equivalent to the non-injured state, since no dedifferentiation occurs here, bglap:GFP+ cells do not express endogenous runx2a. These new data are found in Figure 1 – figure supplement 1A.

c) Using RNAScope, we can show that cyp26b1, a gene associated with dedifferentiated osteoblasts, is likewise not detected in bglap:GFP+ cells in segment -2 at 1 dpa (new data in Figure 1 – figure supplement 1B).

Together, these data confirm that the bglap:GFP line is specific for differentiated osteoblasts, and does not label osteoblast progenitors. See the response to issue 2 below for how we describe these new data in the revised version of the manuscript.

2) Regarding the proliferation of bglap:GFP osteoblasts: In the experiment the reviewer refers to (now Figure 5 – figure supplement 3A), we make use of the persistence of the GFP protein in the bglap:GFP line to detect dedifferentiated osteoblasts. Thus, at the time of analysis, when these GFP+ cells proliferate, they are not differentiated anymore. We can show this as follows:

Although bglap expression is downregulated during osteoblast dedifferentiation and thus also GFP levels eventually drop in the transgenic line, we can nevertheless use this line to trace osteoblasts, since GFP protein persists for up to three days in cells that shut down endogenous bglap and also bglap:GFP transgene transcription. While we have already shown this previously (Knopf et al., Dev Cell 2011, doi: 10.1016/j.devcel.2011.04.014; Geurtzen et al., Development 2014, doi: 10.1242/dev.105817; Mishra et al. Dev Cell 2020, doi: 10.1016/j.devcel.2019.11.016), we have now also used RNAScope to confirm this. We analysed the expression of GFP on protein and RNA level in the bglap:GFP line. In bglap:GFP fish, in a mature segment in non-injured fins the regions close to the joints are devoid of cells expressing GFP (Figure 1G). Yet after amputation, we observe GFP+ cells in this distal part of segment -1 (Figure 1G, D). RNAscope in situ shows that these GFP+ cells are negative for gfp RNA (new data in Figure 1D). Thus, the observed fluorescence is due to the persistence of the GFP protein and not due to a potential upregulation of the transgene (Figure 1E).

Importantly, we have now also added data describing the proliferative state of bglap:GFP+ osteoblasts. First, in the non-injured fin, bglap:GFP+ cells are non-proliferative (new data in Figure 5 – figure supplement 2B). After amputation, proliferation can be detected in GFP+ cells at 2 dpa (Figure 5 – figure supplement 2B), and proliferation is restricted to segment -1 and segment 0 (new data in Figure 5 – figure supplement 2C). As we show in Figure 1B, at 2 dpa, dedifferentiation as defined by bglap downregulation is not complete in segment -1, rather here a mixture of cells with different bglap levels are found. We have thus combined EdU labelling with RNAscope against bglap in segment -1 to analyse to which extent bglap and EdU anticorrelate. These data show that EdU is hardly ever incorporated into cells expressing high levels of bglap, while the majority of the proliferating osteoblasts are dedifferentiated, as they express only low levels of bglap (new data in Figure 5 – figure supplement 2D). Together, these data show that mature osteoblasts are non-proliferative, and upon amputation, when they are dedifferentiated, they become proliferative. Thus, the absence of proliferation in bglap:GFP+ cells in the non-injured fin adds to the evidence that this line is specific for mature osteoblasts, but due to the persistence of the GFP protein it can be used to analyse dedifferentiated osteoblasts.

These data are described on page 14 of the manuscript as follows:

“In the non-injured fin, bglap:GFP+ osteoblasts are non-proliferative, but upon amputation osteoblasts proliferate at 2 dpa (Figure 5 – figure supplement 2A, B). Proliferation is restricted to segment -1 and segment 0 (Figure 5 – figure supplement 2C), and RNAscope in situ analysis of bglap expression revealed that the majority of EdU+ osteoblasts have strongly downregulated bglap (Figure 5 – figure supplement 2D). Inhibition of C5aR1 with PMX205 had no effect on osteoblast proliferation in segment -1 at 2 dpa (Figure 5 – figure supplement 3A). Furthermore, upregulation of Runx2 was not changed by PMX205 treatment (Figure 5 – figure supplement 3B), and regenerative growth was not affected in fish treated with either W54011, PMX205 or SB290157 (Figure 5 – figure supplement Figure 3C). We conclude that the complement system specifically regulates injury-induced osteoblast migration, but not osteoblast dedifferentiation or proliferation in zebrafish.”

3) To support our conclusion that osteoblasts migrate, we performed time-lapse imaging using a transgenic line expressing the photoconvertible protein kaede in osteoblasts (entpd5:kaede). Local photoconversion of only the proximal half of a segment allowed us to trace these photoconverted osteoblasts. This revealed that converted cells appear in the distal part of the segment within 1 dpa, which can only be explained by relocation of the cells. These new data can be found in Figure 1F and they are described on page 7 of the revised manuscript as follows: To trace osteoblasts, we used the transgenic line entpd5:kaede (Geurtzen et al., 2014), in which Kaede fluorescence can be converted from green to red by UV light (Ando et al., 2002). We photoconverted osteoblasts in the proximal half of segment -1, while osteoblasts in the distal half remained green (Fig. 1F). At 1 dpa, red osteoblasts were found in the distal half (Fig. 1F), showing that photoconverted osteoblasts had relocated distally.

2) The authors poorly define dedifferentiation. They use reduced bglap:GFP or bglap mRNA expression as a sole criterion for dedifferentiation. The authors state that NF-kB and retinoic acid can inhibit osteoblast dedifferentiation. However, this simply reflects of the well-described fact that these signals promote osteoblast differentiation.

We define dedifferentiation as the reversion of a mature cell into an undifferentiated progenitor-like status. This involves the following characteristics: 1) the expression of markers of the differentiated state are downregulated; 2) early lineage markers are re-expressed; 3) the cells become proliferative; and 4) they have the ability to re-differentiate into mature cells. Based in this definition, the downregulation of an osteoblast-specific marker can be used as a read-out for osteoblast dedifferentiation. Bglap is an established marker for mature osteoblasts (Kaneto et al., 2016 doi.org/10.1186/s12881-016-0301-7¸ Yoshioka et al., 2021 doi: 10.1002/jbm4.10496; Kannan et al., 2020 doi: 10.1242/bio.053280; Sojan et al., 2022 doi.org/10.3389/fnut.2022.868805; Valenti et al., 2020 doi.org/10.3390/cells9081911). While we use downregulation of bglap expression as our main read-out for osteoblast dedifferentiation in our experimental interventions (actomyosin inhibition, retinoic acid treatment, complement inhibition), we have expanded our methods to characterize osteoblast dedifferentiation, and have re-arranged our manuscript to show these data in the beginning of the results.

Already in the previous version of the manuscript we have shown that endogenous bglap is strongly expressed in segment -2, (the segment that does not respond to fin amputation and thus represents the non-injured state), while it is downregulated in a graded manner in segment -1 and segment 0 (the segments where dedifferentiation happens). We have now moved this data to the re-designed Figure 1B. In addition to bglap, we can now show that entpd5, a gene required for bone mineralization, is strongly expressed in osteoblasts of segment -2, while it is massively downregulated in segment -1 and segment 0. These new data can be found in Figure 1C. Thus, entpd5 is another differentiation marker whose loss characterizes osteoblast dedifferentiation. Importantly, we can confirm by RNAScope that the pre-osteoblast marker runx2a is absent in mature segments but is upregulated in segment 0 and segment -1 at 1 dpa (new data in Figure 1 – figure supplement 1A). Similarly, cyp26b1, an enzyme shown to regulate dedifferentiation, is upregulated in segment 0 and segment -1, but not expressed in segment -2. (new data in Figure 1 – figure supplement 1B). Furthermore, we have repeated all experiments where we have previously quantified dedifferentiation upon experimental interventions using downregulation of bglap:GFP (actomyosin inhibition, retinoic acid treatment, complement inhibition). We now can fully confirm the previous conclusions using the more rigorous quantification of dedifferentiation using RNAScope analysis of endogenous bglap levels. We have replaced all bglap:GFP data with the new bglap RNAScope data. These new data are found in Figure 3F, Figure 3 – figure supplement 1A, Figure 4B and Figure 5F.

Overall, we support our conclusion that osteoblasts dedifferentiate by the loss of the two differentiation markers bglap and entpd5, the upregulation of the pre-osteoblast marker runx2a and the dedifferentiation-associated gene cyp26b1, and the fact that osteoblasts become proliferative. We hope that the reviewer considers this sufficient evidence.

In mammals, the available literature relatively convincingly concludes that NF-kB signaling negatively regulates osteoblast differentiation (Yao et al., 2014, doi: 10.1002/jbmr.2108; Swarnkar et al., 2014 doi.org/10.1371/journal.pone.0091421, Chang et al., 2009, doi.org/10.1038/nm.1954). Yet in zebrafish osteoblasts, we have previously shown that NF-kB signaling is active in mature osteoblasts and needs to be downregulated for dedifferentiation to occur (Mishra et al., 2020, 10.1016/j.devcel.2019.11.016). Importantly, in our previous work we showed that at least during fin regeneration, NF-kB signalling is not involved in osteoblast differentiation (Mishra et al., 2020, 10.1016/j.devcel.2019.11.016). Specifically, osteoblasts in which Nf-kappaB signaling is enhanced or inhibited differentiate completely normally during the later stages of fin regeneration in the fin regenerate. Hence, our findings with the Nf-kappaB intervention studies done in this manuscript, where we look at osteoblasts in the stump within 1 dpa, cannot be explained by them affecting osteoblast differentiation.

For retinoic acid signalling, multiple roles in bone development and repair have been described in mammals. For zebrafish osteoblasts, it was shown that during the outgrowth phase of bone regeneration, retinoic acid negatively regulates osteoblast differentiation in the blastema (Blum & Begemann, 2015, 10.1242/dev.120204). Yet importantly, it also negatively controls the dedifferentiation of osteoblasts in the stump right after amputation (Blum & Begemann, 2015, 10.1242/dev.120204). Thus, the effect we observe at the early timepoints we analyse in our intervention studies (retinoic acid treatment) are due to the effect on osteoblast dedifferentiation.

We have added a short definition of dedifferentiation to the results section (page 6). There it reads as follows:

“We have previously shown that osteoblasts dedifferentiate in response to fin amputation, that is they revert from a mature, non-proliferative state into an undifferentiated progenitor-like state, which includes loss of bglap expression and upregulation of the pre-osteoblast marker runx2 (Knopf et al., 2011; Geurtzen et al., 2014).”

In addition, we have restructured the results to describe our use of tools and the new data on page 6 of the revised manuscript as follows:

Using RNAScope in situ hybridization, we can now show that downregulation of bglap occurs in a graded manner and that entpd5 expression is similarly downregulated during dedifferentiation (Figure 1B, C). At 1 day post amputation (1 dpa), expression of entpd5 and bglap remains high in segment -2, but gradually decreases towards the amputation plane and is almost entirely absent from segment 0, with entpd5 downregulation being more pronounced (Figure 1B, C). While RNA expression of these genes is downregulated within hours after injury, GFP or Kaede fluorescent proteins (FPs) expressed in bglap or entpd5 reporter transgenic lines persist for up to three days, even though transgene transcription is shut down rapidly as well (Knopf et al., 2011). We can confirm these earlier findings using the more sensitive RNAScope in situs. In bglap:GFP transgenics at 2 dpa, gfp RNA and GFP protein colocalized to the same cells in segment -2, where osteoblasts do not dedifferentiate (Fig. 1D). In contrast, in the distal segment -1 GFP protein was present, but barely any gfp transcript could be detected (Fig. 1D). Thus, persistence of FPs in reporter lines can be used for short-term tracing of dedifferentiated osteoblasts (Fig. 1E). At 1 dpa, bglap:GFP+ cells upregulated expression of the pre-osteoblast marker runx2a and of cyp26b1, an enzyme involved in retinoic acid signalling (Blum and Begemann, 2015), which regulates dedifferentiation (Figure 1 – figure supplement 1A, B). Both markers were exclusively upregulated in segment -1 and segment 0 at 1 dpa, but were absent in segment -2. Together, these data show that osteoblasts in segment -1 and segment 0 lose expression of mature markers and gain expression of dedifferentiation markers.

3) The authors do not rigorously demonstrate that mature osteoblasts indeed migrate. What they showed in this study is simply cell shape changes.

We have the following evidence for osteoblast migration:

1) bglap:GFP+ cells relocate from the centre of segments towards the amputation plane (after fin amputations) or towards both injuries in the hemiray model. In this revised manuscript we show that transgene expression is not upregulated in these regions, but that GFP fluorescence there must be due to relocation of cells in which GFP protein persists (new data in Figure 1D, E; see also response to “Weaknesses, issue 1” above)

2) Using the entpd5:kaede transgenic line, which is expressed in mature osteoblasts throughout segments, we have photoconverted only the proximal half of a segment, which allowed us to trace these photoconverted osteoblasts. This revealed that converted cells appear in the distal part of the segment within 1 dpa, which can only be explained by relocation of the cells. These new data can be found in Figure 1F.

3) Already in the previous version of the manuscript, we have performed live imaging to track single cell behaviour. Using double transgenic fish expressing both GFP and kaede in osteoblasts, we deliberately only partly converted kaedeGreen to kaedeRed, which resulted in different hues for each osteoblast. This distinct colouring facilitates observing single cells. Video 1 shows the directed movement of cell bodies relative to their surroundings within 2 hours (see also Figure 2 – figure supplement 1A).

4) Osteoblasts display the typical cell shape changes associated with active migration (elongation along the axis of migration, extension of dynamic protrusions), data in Figure 2.

Together, we think these are convincing data supporting the conclusion that osteoblasts actively migrate.

4) The hemiray removal model is highly innovative, but this part of the study is not very well connected to the rest of the study.

We have rephrased the first sentence of the hemiray paragraph to make the connection more perceptible. It now reads as follows:

In response to fin amputation, all osteoblast injury responses occur directed towards the amputation plane, that is dedifferentiation is more pronounced distally, osteoblasts migrate distal wards and the proliferative pre-osteoblast population forms distally of the amputation plane. We wondered how osteoblasts respond to injuries that occur proximal to their location. To test this, we established a fin ray injury model featuring internal bone defects.

Author Response

Reviewer #1 (Public Review):

Kang et al. studied the role of cystathionine beta-synthase (CBS), an enzyme involved in homocysteine catabolism, in the senescent state stimulated by Akt. They report that Akt induces expression of CBS and other enzymes necessary to convert homocysteine into cysteine, and that blocking CBS enhances cell proliferation and reduces beta-galactosidase expression. Mechanistic studies reveal that Akt activates several markers of mitochondrial metabolism, including respiration, and that CBS silencing mitigates this change and reduces reactive oxygen species. Analysis of human gastric tumors reveals methylation of the CBS locus and reduced CBS expression relative to nonmalignant gastric mucosa. Finally, reexpressing CBS in gastric cancer cells reduces growth and Ki67 staining in xenografts. The authors conclude that CBS is a required component of the Akt-induced senescence pathway, and that reducing CBS expression is a mechanism by which some cancers suppress senescence and promote growth. Overall, the paper describes an interesting metabolic process of oncogene-induced senescence that appears selective for Akt. Few such mechanisms have been described, so a thorough exploration of CBS's role in senescence could be impactful. The authors succeed in showing that manipulating CBS expression in a limited number of models has substantial effects on senescence and growth. However, not all of the conclusions are supported by the data in the current version of the paper, the metabolic analysis of CBS's function in Akt-expressing cells is incompletely characterized, and some central aspects of the overall mechanism (particularly the relevance of CBS to mitochondrial respiration) are unexplained.

Specific comments:

1) CBS expression is induced upon Akt activation, but there needs to be better evidence that activity of the pathway has changed. The metabolomics results are not very convincing, as siCBS has no or minimal effects on some metabolite pools that should respond. An isotope tracing study would help here.

We thank the reviewer for the suggestions. We performed a [3-13C] L-serine tracing analysis by LC/MS in proliferating cells, AKT-induced senescent (AIS) cells, and AIS cells with CBS knockdown in cysteine-replete and depleted conditions. The results shown in Figure 3A-3E of the revised manuscript.

The tracer [3-13C] L-serine has been reported to incorporate into the cellular GSH pool via transsulfuration-derived cysteine (Zhu et al., 2019) (Figure A). We replaced all the serine in the culture medium with [3-13C] L-serine. After six hours of labelling, a substantial fraction of [3-13C] L-serine was detected intracellularly and in the cystathionine pool in proliferating (pBabe-siOTP), AIS (myrAKT1-siOTP) and AIS escaped (myrAKT1-siCBS) cells (Figure B and C). We did not detect [3-13C] L-serine incorporation into cysteine and GSH in the proliferating cells, possibly due to the short time period of metabolic labelling (Figure D and E). However, AIS cells displayed a small but significant fraction of 13C labelled cysteine and GSH along with a significant increase of total levels of serine, cysteine and GSH (Figure BE), supporting the upregulation of transsulfuration pathway activity in AIS. Consistent with the role of CBS in catalyzing de novo cystathionine synthesis, a significant decrease of cystathionine abundance was observed in CBS-depleted AIS escaped cells. Notably, the abundance of cysteine and GSH (Figure D and E) was not affected by CBS depletion. We hypothesized that CBS-depleted cells maintained the cysteine and GSH pools via increase of cysteine uptake from the culture medium. Indeed, deprivation of cysteine from the medium markedly diminished the intracellular cysteine and GSH abundance in AIS cells (Figure D and E). On the other hand, increase of cystathionine was observed under the cysteinedepleted conditions (Figure C), possibly attributed to a marked upregulation of CBS expression observed in AIS cells after cysteine deprivation (Figure 1B in the revised manuscript). This result thus suggests that cells enhance CBS-mediated transsulfuration pathway activity in response to cysteine deficiency.

Collectively, our results indicate that cells rely on exogenous cysteine for GSH synthesis and AKT overexpression increases cysteine import and the subsequent GSH abundance which is not affected by loss of CBS.

2) Furthermore, the AOAA experiments are hard to interpret. This drug is a promiscuous transaminase inhibitor, so its effects on cell confluency are not surprising, and it is unclear which particular aspect of metabolism is responsible for the effect. A genetic experiment silencing the relevant transaminase would be more informative.

We agree that the pharmacological action of AOAA is not limited to suppression of the CBS/ H2S axis. It binds irreversibly to the cofactor PLP, and therefore in addition to CBS, it also inhibits other PLP-dependent enzymes such as CTH, 3-MST, and GOT1. We therefore have modified our statement in the manuscript to be “this result suggested that H2S, the major metabolite downstream of the transsulfuration pathway, has a protective effect on AIS cells although the actions of AOAA on other PLP-dependent enzymes cannot be excluded.

We further analysed the data from the AIS-escape siRNA screen and presented these data in Figure 3-figure supplement 1A.

We found that except CBS, siRNA knockdown of other genes involved in the transsulfuration pathway did not significantly affect AIS cell numbers (robust Z score < 2). Therefore, it is likely that AIS escape in cysteine-replete conditions by loss of CBS is through a transsulfuration/transmethylation pathway-independent mechanism.

3)The GC/MS data in Fig. 3L are misleading, as the range on the color scale goes from FDR of 0.0504 to 0.0498. Also, the authors claim that CBS regulates the malate-aspartate shuttle, but no mechanism is proposed and this is not intuitive.

The altered activity of malate-aspartate shuttle is only based on the changes in glutamate and aspartate levels, as measured by GC-MS metabolomics analysis. We agree that these metabolite changes are not sufficient to support the specificity of malate-aspartate shuttle being involved in CBS-mediated metabolic alterations. Therefore, for clarity we have decided to remove this figure and the relevant text from the manuscript.

4) CBS's role in modulating mitochondrial function is complicated, but its ability to sustain OxPhos and ROS seem to underlie its effects on AIS. The key unanswered question is how CBS promotes OxPhos in these models.

To determine the mechanisms underlying the increased oxidative phosphorylation and ROS in CBS deficient cells, we investigated the mitochondrial localization of CBS. In addition to the immunofluorescent data showing localization of CBS in the mitochondria (Figure 4A), in the revised manuscript, we generated lentiviral expression vectors encoding wild type CBS and N-terminal and C-terminally truncated mutants. We showed that, consistent with a previous study (Teng et al., PNAS 2013), the C-terminal CBSD2 motif is required for CBS mitochondrial localization (Figure 4C-4F). We then reconstituted CBS-depleted AIS escaped cells with wild type CBS or a C-terminally truncated mutant (Δ468-551). Expression of wild type CBS prevented AIS escape while cells expressing the truncation mutant still escaped from AIS (Figure 4G and 4H), demonstrating that mitochondrial localization of CBS is required to maintain AIS. Consistent with these findings, the Seahorse analysis showed that reconstitution with wild type CBS rescued basal OCR and ATP production levels in CBSdepleted AIS cells. In contrast, AIS cells expressing C-terminally truncated CBS protein failed to restore basal OCR and ATP production. Collectively, our results support the concept that AKT overexpression promotes CBS translocation to mitochondria, increases oxidative phosphorylation and ROS production to sustain the senescence state.

Reviewer #3 (Public Review):

In the manuscript by Zhu, Haoran et al., titled "Cystathionine-β-synthase is essential for AKT-induced senescence and suppresses the development of gastric cancers with PI3K/AKT activation", the authors investigated the contributions of cystathionine-β-synthase (CBS) to AKT-induced senescence (AIS) and the potential mechanisms which drove these phenotypes. The authors showed that AKT hyperactivation (using myristoylated AKT) promoted H2S production and treatment with a compound (AOAA) that blocked H2S production, reduced proliferation, and promoted senescence in cells with hyperactivated AKT, compared to normally proliferating cells or cells that have expressed other oncogenes (i.e., HRAS). Next, they used genetic approaches (both knockdown of CBS and rescue experiments with reexpression of CBS in CBS-knockdown cells) to clearly demonstrate that CBS was required for AIS and loss of CBS promoted AIS-escape. The authors then extended these findings to patient tumors and in vivo systems. They found reduced CBS expression in gastric cancer samples compared to matched normal samples and that the reduced expression was due to hypermethylation of DNA encoding CBS. Finally, they found that CBS functions as a tumor suppressor in gastric cancer cells by showing that depletion of CBS promoted colony formation, and overexpression of CBS blocked tumor growth in vivo. This is a very strong study with relevance to numerous research fields. However, a major weakness of the study is the proposed mechanism by which CBS functions in AIS-escape, as the data are largely not supported by the mechanistic conclusions.

1) In Figure 1, the authors show that AIS cells are unaffected by cysteine depletion and conclude, "Furthermore, cysteine deprivation potently increased the expression levels of CBS and CTH in AIS cells (Figure 1B) and did not affect the survival of AIS cells, consistent with increased cysteine synthesis due to elevated CBS expression being critical for cell viability (Figure 1E)". Although the authors show in Fig. 3F that cysteine levels are elevated in AIS cells compared to control cells in cystine-replete media, they do not measure cysteine synthesis via the transsulfuration pathway in AIS and control cells in cystine-replete and cystine-depleted media.

Please see our response to the question #1 from the Reviewer 1.

2) The metabolic changes presented in Figure 3 are unclear. The authors state, "Depletion of CBS in AIS cells increases GSH metabolism in cysteine-replete condition", but it is not clear what "GSH metabolism" means, especially for the AIS-related phenotypes. Further, the authors appear to use "GSH metabolism" interchangeable with GSH synthesis; in the Discussion, they state, "In this study we uncovered another mechanism of AKT-mediated ROS detoxification by upregulation of transsulfuration pathway activity and enhancing glutathione and H2S synthesis (Fig.4H)." These conclusions are not supported by the findings presented in Figure 3 that show GSH levels are unchanged between control, AIS, and CBSdepleted AIS cells. While the authors show an increased abundance of the GSH precursor gamma-glutamylcysteine and the GSH catabolic product cysteinylglycine, how CBS would alter these metabolites are unclear. Additionally, they show that H2S levels are unaffected by CBS depletion, which further confounds the conclusions.

To determine the transsulfuration pathway activity in AIS cells and the effect of CBS loss, we performed a stable isotope tracing assay followed by LC-MS assay using [3-13C] L-serine. Please see our response to the question #1 from the Reviewer 1.

Author Response

Reviewer #1 (Public Review):

There are several key weaknesses. As the authors describe honestly and thoroughly, the high potential for misclassification of clusters is a real limitation. This is likely to be of higher relevance for the US data. Perhaps this is too subjective on my part, but the Canadian data seems likely to be more complete and less biased, particularly in terms of including singlet events with n=1 case. It also strains belief that the true cluster distribution would differ markedly between Canada and the US based on overlapping demographics, culture, class size, etc....For this reason, I would favor labeling the Canadian data as more representative of reality and interpreting the analysis accordingly. It seems fair to use the US data as a likely surrogate of what occurs when the model is applied to incomplete datasets with overrepresentation of large clusters. I would therefore consider excluding all data from the US in the main figures and writing the US data into a separate section at the end of the results associated with a supplementary figure. Overall, I think it is fair to assume that the Canadian dataset is more complete and more representative, not just of Canada but also of the US.

Thank you for these points. We agree, and we’ve followed your suggestion and moved the US data and analysis to the Appendix, and made more clear its limitations.

In the discussion, the authors fail to state the most obvious contributor to overdispersion which is aerosolization. Notably, influenza virus is associated with equivalently heterogeneous contact networks, similarly high variation in viral load and an overlapping major route of transmission. Yet, its degree of overdispersion is substantially less than SARS-CoV-2, SARS, or MERS, likely due to less aerosolization. Accordingly, influenza is much less commonly associated with large super-spreader events. Please see Goyal et al (Elife, 2021).

We now discuss aerosolization with the addition of the following sentence, and cite the important Goyal et al paper. “But a key factor in higher dispersion with SARS-CoV-2 in comparison to other pathogens such as influenza is aerosolization (Goyal et al), which allows the index case to infect others in the room even if they are not a close contact.”

Next, I am puzzled by one result which is the Canadian data in Figure 6. This panel suggests that clusters involving more than 12 cases never will happen. This is probably not correct. I think that the issue is that this analysis fails to account for the rarity, but high importance of larger super-spreader events. I am assuming that this figure is showing average values as it is directly extrapolated from parameter values. It would be more useful to show the range of expected times needed to see a cluster of different sizes. This would require stochastic simulation which could be performed by drawing randomly from a distribution with given values for Rc & k. The result would likely be a wide range in time to cluster for given set of Rc & k values. Without accounting for stochasticity, this figure is misleading and should probably be removed.

Following this suggestion, we have removed the time to detect analysis.

Author Response

Reviewer #2 (Public Review):

Summary: This substantial collaborative effort utilized virus-based retrograde tracing from cervical, thoracic and lumbar spinal cord injection sites, tissue clearing and cutting-edge imaging to develop a supraspinal connectome or map of neurons in the brain that project to the spinal cord. The need for such a connectome-atlas resource is nicely described, and the combination of the actual data with the means to probe that data is truly outstanding.

They then compared the connectome from intact mice to those of mice with mild, moderate and severe spinal cord injuries to reveal the neuronal populations that retain axons and synapses below the level of injury. Finally, they look for correlations between the remaining neuronal populations and functional recovery to reveal which are likely contributing to recovery and its variability after injury. Overall, they successfully achieve their primary goals with the following caveats: The injury model chosen is not the most widely employed in the field, and the anatomical assessment of the injuries is incomplete/not ideal.

Concerns/issues:

1) I would like to see additional discussion/rationale for the chosen injury model and how it compares to other more commonly employed animal models and clinical injuries. Please relate how what is being observed with the supraspinal connectome might be different for these other models and for clinical injuries.

We have added text to the Results and Discussion to explain our rationale for selecting the crush injury model, and to acknowledge differences between this model and more clinically relevant contusion models. (Results: line 360-364, Discussion 608-615). We agree wholeheartedly that a critical future direction will be to deploy brain-wide quantification in contusion models, and we are currently seeking funding to obtain the needed equipment.

2) The assessment of the thoracic injuries employed is not ideal because it provides no anatomical description of spared white matter (or numbers of spared axons) at the injury epicenter.

We address this more fully in the related point below. Briefly, we agree with a need to improve the assessment of the lesion but are hampered by tissue availability. We are unable to assess white matter sparing but can offer quantification of the width of residual astrocyte tissue bridges in four spinal sections from each animal (new Figure 5 – figure supplement 3). As discussed below, however, we recognize the limitations of the lesion assessment and agree with the larger point that the current quantification methods do not position us to make claims about the relative efficacy of spinal injury analyses versus whole-brain sparing analyses to stratify severity or predict outcomes. Our approach should be seen as a complement, not a substitute, for existing lesion-based analyses. We have edited language throughout the manuscript to make this position clearer.

3) Related to this, but an issue that requires separate attention is the highly variable appearance of the injury and tracer/virus injection sites, the variability in the spatial relationship with labeled neurons (lumbar) and how these differences could influence labeling, sprouting of axons of passage and interpretation of the data. In particular this is referring to the data shown in Figure 6 (and related data).

It is true that there is some variability in the relative position of the injury and injection, a surgical reality. The degree of variability was perhaps exaggerated in the original Figure 6 (Now Figure 5), in which one image came from one of two animals in the cohort with a notably larger gap between the injury and injection. Nevertheless, this comment raises the important question of how variability in injection-to-injury distance might affect supraspinal label. First, we would emphasize the data in Figure 1 – Figure Supplement 6, in which we showed that the number of retrogradely labeled supraspinal neurons is relatively stable as injection sites are deliberately varied across the lower thoracic and lumbar cord. Indeed, the question raised here is precisely the reason we performed this early test to determine how sensitive the results might be to shifts in segmental targeting. The results indicate that retrograde labeling is fairly insensitive to L1 versus L4 targeting. As an additional check for this specific experiment we also measured the distance between the rostral spread of viral label and the caudal edge of the lesion and plotted it against the total number of retrogradely labeled neurons in the brain. If a smaller injury/injection gap favored more labeling we might expect negative correlation, but none is apparent. We conclude that although the injury/injection distance did vary in the experiment, it likely did not exert a strong influence on retrograde labeling.

Reviewer #3 (Public Review):

In this manuscript, Wang et al describe a series of experiments aimed at optimizing the experimental and computational approach to the detection of projection-specific neurons across the entire mouse brain. This work builds on a large body of work that has developed nuclear-fused viral labelling, next-generation fluorophores, tissue clearing, image registration, and automated cell segmentation. They apply their techniques to understand projection-specific patterns of supraspinal neurons to the cervical and lumbar spinal cord, and to reveal brain and brainstem connections that are preferentially spared or lost after spinal cord injury.

Strengths:

Although this work does not put forward any fundamentally new methodologies, their careful optimization of the experimental and quantification process will be appreciated by other laboratories attempting to use these types of methods. Moreover, the observations of topological arrangement of various supraspinal centres are important and I believe will be interesting to others in the field.

The web app provided by the authors provides a nice interface for users to explore these data. I think this will be appreciated by people in the field interested in what happens to their brain or brainstem region of interest.

Weaknesses:

Overall the work is well done; however, some of the novelty claims should be better aligned with the experimental findings. Moreover, the statistical approaches put forward to understand the relationship between spinal cord injury severity and cell counts across the mouse brain needs to be more carefully considered.

The authors state that they provide an experimental platform for these types of analysis to be done. My apologies if I missed it but I could not find anywhere the information on viral construct availability or code availability to reproduce the results. Certainly both of these aspects would be required for people to replicate the pipeline. Moreover, the described methodology for imaging and processing is quite sparse. While I appreciate that this information is widely provided in papers that have developed these methods, I do not think it is appropriate to claim to have provided a platform for people to enable these types of analyses without a more in-depth description of the methods. Alternatively, the authors could instead focus on how they optimized current methodologies and avoid the overstatement that this work provides a tool for users. The exception to this is of course the viral constructs, the plasmids of which should be deposited.

We agree that we have not provided a tool per se, more of an example that could be followed. We have revised language in the abstract, introduction, and discussion to make it clear that we optimized existing methods and provide an example of how this can be done, but are not offering a “plug and play” solution to the problem of registration that would, for example, allow upload of external data. For example, in the abstract we replaced “We now provide an experimental platform” with “Here we assemble an experimental workflow.” (Line 28). The term “platform” no longer appears in the manuscript and has been replaced throughout by “example.” We how this matches the intention of the comment and are happy to revise further as needed. Note that the plasmids have been deposited to Addgene.

It was not completely to me clear why or when the authors switch back and forth between different resolutions throughout the manuscript. In the abstract it states that 60 regions were examined, but elsewhere the number is as many as 500. My understanding is that current versions of the Allen Brain Annotation include more than 2000 regions. I think it would make things clear for the readers if a single resolution was used throughout, or at least justified narratively throughout the text to avoid confusion.

Thank you for pointing this out. The Cellfinder application recognizes 645 discrete regions in the brain, and across all experiments we detected supraspinal nuclei in 69 of these. This number, however, includes some very fine distinctions, for example three separate subregions of vestibular nuclei, three subregions of the superior olivary complex, etc. True experts may desire this level of information, but with the goal of accessibility we find it useful to collapse closely related / adjacent regions to an umbrella term. Doing so generates a list of 25 grouped or summary regions. In the revised version we move the 69-region data completely to the supplemental data (there for the experts who wish to parse), and use the consistent 25-region system (plus cervical spinal cord in later sections) to present data in the main figures. We have added text to the Results section (lines 157-162) to clarify this grouping system.

The others provide an interesting analysis of the difference between cervical and lumbar projections. I think this might be one of the more interesting aspects of the paper - yet I found myself a bit confused by the analysis, and whether any of the differences observed were robust. Just prior to this experiment the authors provide a comparison of the mScarlet vs. the mGL, and demonstrate that mGL may label more cells. Yet, in the cervical vs. lumbar analysis it appears they are being treated 1 to 1. Moreover, I could not find any actual statistical analysis of this data? My impression would be that given the potential difference in labelling efficiency between the mScarlet and mGL this should be done using some kind of count analysis that takes into account the overall number of neurons labelled, such as a Chi-sq test or perhaps something more sophisticated. Then, with this kind of statistical analysis in place, do any of the discussed differences hold up? If not, I do not think this would detract from the interesting topological observations - but would call on the authors to be a bit more conservative about their statements and discussion regarding differences in the proportions of neurons projecting to certain supraspinal centers.

This is an important point. In response to this input and related comments from other reviewers we performed new experiments to assess co-localization. The new data address the point above by including quantification of the degree of colocalization that results from titer-matched co-injection of the two fluorophores, providing baseline data. The results of this can be found in Figure 3 – figure supplement 3 and form the basis for statistical comparisons to experimental animals shown in Figure 3.

Finally, I do have some concerns about the author's use of linear regression in their analysis of brain regions after varying severities of SCI. First of all, the BMS score is notoriously non-linear. Despite wide use of linear regressions in the field to attempt to associate various outcomes to these kinds of ordinal measures, this is not appropriate. Some have suggested a rank conversion of the BMS prior to linear analyses, but even this comes with its own problems. Ultimately, the authors have here 2-3 clear cohorts of behavioral scores and drawing a linear regression between these is unlikely to be robustly informative. Moreover, it is unclear whether the authors properly adjusted their p-values from running these regressions on 60 (600?) regions. Finally, the statement in the abstract and discussion that the authors "explain more variability" compared to typical lesion severity analysis is also unsupported. My suggestion would be the following:

Remove the linear regression analyses associated with BMS. I do not think these add value to the paper, and if anything provide a large window of false interpretation due to a violation of the assumptions of this test.

Consider adding a more appropriate statistical analysis of the brain regions, such as a non-parametric group analysis. Knowing which brain regions are severity dependent, and which ones are not, would already be an interesting finding. This finding would not be confounded by any attempt to link it to crude measures of behavior.

We agree that the linear regression approach was flawed and appreciate the opportunity to correct it. After consultation with two groups of statisticians we were forced to conclude that the data are simply underpowered for mixed model and ranking approaches. We therefore adopted a much simpler strategy. As you point out (and as noted by the statisticians), the behavioral data are bimodal; one group of animals regained plantar stepping ability, albeit with varying degrees of coordination (BMS 6-8), while the others showed at most rare plantar steps (BMS 0-3.5). We therefore asked whether the number of spared neurons in each brain region differed between the two groups and also examined the degree of “overlap” in the sparing values between the two groups. The data are now presented in Figure 6.

If the authors would like to state anything about 'explaining more variability' then the proper statistical analysis should be used, which in this case would be to compare the models using a LRT or equivalent. However, as I mentioned it does not seem to be appropriate to be doing this with linear models so the authors should consider a non-linear equivalent if they choose to proceed with this.

We thank the reviewer for the excellent suggestion. However as we explained above after consultation with two groups of statisticians we were forced to conclude that the data are underpowered and could not apply some of the methods suggested. Especially in light of our simplified analysis, we think it is better to remove any claims of the relative success of the sparing in different regions to explain more or less variability. Instead we can simply report that sparing in some regions, but not others, is significantly different between “low-performing” and “high-performing” groups.

Author Response

Reviewer #2 (Public Review):

The main strength of the paper is the parallel profiling of virus-specific CD4 T cells in different stages of acute and persistent infection, and the ease of publicly accessing the data and source code. These data extend previous studies, such as Khatun et al. JEM 2020 and Cicucci et al. Immunity 2019, by revealing single-cell transcriptome information on virus-specific CD4 T cells at different stages of infection.

The main drawback is the paper's advertised use as a 'comprehensive atlas of virus-specific CD4 T cells'. This study includes virus-specific T cells from a single organ (spleen) during infections with two clones of a single virus (LCMV). Therefore, its use as a reference atlas does not extend to other viruses or T cells from organs other than spleen during LCMV infection. If such samples were integrated with the splenic LCMV atlas, either new unique populations would be found and therefore not meaningfully annotated or they would be force-integrated with one of the splenic subsets, producing a potentially misleading and crude annotation. In this sense, the authors did not construct an atlas but rather a dataset on LCMV-specific splenic CD4 T cells which, like other datasets, can be compared with other single-cell sequencing datasets.

The methodology description does not include convincing evidence that the integration was successful in minimizing batch effects and retaining biological heterogeneity, virtually no data is presented in support of this point. Therefore, the scope of the work should be refined and the methodology significantly improved before this paper becomes acceptable for publication.

We thank the referee for recognizing the strengths of the study, as well as for advising where we had been insufficiently clear in describing the methodology – in particular with regards to data integration and generalizability of our bioinformatics tool. As detailed below, we provide new evidence supporting the quality of data integration, the robustness and replicability of the T cell states defined in our reference map, and its ability to make accurate predictions across multiple tissues (spleen, liver, lung, lymph nodes) and beyond the LCMV infection model. In addition, we conducted several additional analyses demonstrating the robustness of our predictions, and generated a new scRNA-seq dataset of tumor-specific CD4+ T cells, showing how our LCMV-derived reference map can help identify and characterize a novel cell state uniquely acquired by tumor-infiltrating CD4+ T cells.

Author Response

Reviewer #2 (Public Review):

This study uses cutting edge transcriptomics to decode the changes in transcript expression with neonatal development.

Strengths

The study is sufficiently detailed so that the reader can evaluate the data and conclusions. Most importantly, the scientist who is able to analyze data from RNA-sequencing such as this will be able to seek answers their own questions about gene ontology and pathways involved in pituitary cell development.

The study is validated by the use of the organoid cultures, which recapitulate the transcriptome expression of the developing pituitary stem cells. An important strength is the fact that they were able to develop growth media that is optimal for neonatal pituitaries, as the organoid media used by many has been developed for adult cultures. This will be an important addition for many laboratories wishing to study organoid cultures from neonatal pituitary populations.

The study of the damaged neonatal pituitary (damaged by the ablation of somatotropes) is interesting and shows that the damage focuses on somatotropes and does not ablate stem cells. The study is worth further analysis by those who are interested in the impact of loss of somatotropes on pituitary cell populations.

The populations subjected to scRNA-seq are available publicly and provide important tools for other researchers who want to decode stem cell activation.

Weaknesses

1) The study is best analyzed by individuals who are well versed in bioinformatics approaches or by individuals who have access to this expertise. This is not a major weakness, only a precautionary remark.

We thank the reviewer for this precautionary remark. For the reviewer’s informaton, during the last couple of years, our group acquired substantial bioinformatic skills to perform such scRNA-seq analyses, as witnessed by our recent publications (Hemeryck et al., 2022; Vennekens et al., 2021). Moreover, our group collaborates with (other) experts in the single-cell bioinformatic field (also listed as co-authors on previous and current papers) and the Leuven Institute for Single Cell Omics (LISCO; https://lisco.kuleuven.be), of which the PI is affiliated member. Moreover, we did our best to explain the bioinformatic findings (using established tools such as SCENIC and CellPhoneDB) as clear as possible to enable researchers, less experienced in single-cell bioinformatics, to understand the study.

2) This reviewer wonders about the use of the word "vividly" in the title and throughout the manuscript. Clearly these pituitary populations from the 7 day neonatal mice are maturing, however what about the study makes this maturation "vivid". The maturation is fairly ordinary and expected and not any more vivid than any other type of study of neonatal development. Vivid denotes a dynamic state and only one age was chosen for analysis of maturation.

We understand the reviewer’s concern and agree that ‘vivid’ may not be the most appropriate word (although it sounded so when translated to our native language). Therefore, we removed it (e.g. in title and Abstract), or replaced it throughout the manuscript with ‘active/dynamic’ (or other appropriate words) at the indicated places.

3) Readers need to recognize that this transcriptome reflects gene activity in the PND 7 mouse and there may be additional changes during the second week of development, especially when prolactin cells begin to differentiate. This is not a major weakness because these types of studies are very expensive (in the US) and one must choose one's model carefully. The rationale for the use of 7 day old neonate could be spelled out (why not 4 or 5 day mice). One might guess however that this has to do with the size of the pituitary which is very tiny in the developing mouse.

We thank the reviewer for this genuine reflection.

The PD7 age was chosen for several reasons. First, the particular age was analyzed in our previous study which showed signs of an activated stem cell state at this age (Gremeaux et al., 2012) (as referenced in the text). Second, and indeed, the neonatal mouse pituitary is very small in size, and to obtain a sufficient number of cells for downstream analyses, we chose the most useful (but still actively maturing) age of PD7. Third, for the damage and regeneration experiments, pups had to be i.p. injected with DT which had to start 3 days before the analysis timepoint at PD7, and PD4 was the limit age in which this could be (most) reliably performed.

It would certainly be interesting to explore still other ages during the early-postnatal maturation phase (e.g. the second week as suggested, however already focused on in (Russell et al., 2021)), but also in Europe/Belgium, scRNA-seq analyses are very expensive and therefore ages and models must be carefully selected.

4) It is impossible to remove the posterior pituitary and not also remove the intermediate lobe and the data show clearly that melanotropes were present in the PND 7 mouse as well as the adult.

Although we aimed at meticulously removing (under the stereomicroscope) the intermediate and posterior lobes, some residual intermediate lobe cells appear to remain attached to the anterior lobe as clear from the scRNA-seq analysis (adult). In the neonatal mouse, the pituitary tissue is still more ‘sticky’, making it technically still more challenging to dissect away the posterior and intermediate lobes. Hence, not only a cluster of melanotropes (as in adults) but also a (very small) cluster of posterior lobe (PL) cells remains present.

Author Response

Reviewer #1 (Public Review):

Using Tet-off system, Kir2.1 was expressed (or not) during the key time of callosal development from E15 to P15. Restoring activity either by adding Dox during a critical period from P6 to P15 or using DREADDs from P10-14 could rescue the callosal projection to the cortex, whereas later restoration of activity (with Dox) was not successful. Did this successful rescue lead to normal activity? Calcium imaging in animals with Kir2.1 had low levels of any kind of activity, both highly correlated and low correlation, but P6-13 dox treatment partially restored only low-correlation activity and not high correlation activity at P13. The effects of DREADDs on activity was not similarly measured though it was effective for at least partially restoring the callosal projection.

Overall this study builds on earlier findings regarding the importance of neuronal activity in the formation of a normal callosal projection, using in utero electroporation which is particularly well suited for this subject. It makes the case very compellingly that near-normal callosal connectivity can be produced if activity is permitted during a critical period window from P6 or P10 to P15, though the exact timing of this window is imprecise because the elimination of Kir expression was not systematically quantified. For transmembrane proteins like channels it can often take many days for protein expression to completely abate.

We thank the reviewer for their positive evaluation and the constructive comments. Based on the comment on Kir expression, we conducted new experiments using pTRE-Tight2Kir2.1EGFP, with which EGFP signals reflect localization of over-expressed Kir2.1, and examined when the expression of Kir2.1EGFP went down after Dox treatment at P6. At P6 (before Dox treatment), the signals of Kir2.1EGFP (stained with anti-GFP antibody) were observed in the periphery of the soma and along dendrites, implying that Kir2.1EGFP was transported to the cellular membrane. At P10 and P15 (4 days and 9 days after Dox treatment), Kir2.1EGFP signals were not observed in the periphery of the soma and along dendrites. We noted that low-level green signals were observed in the central part of the cell body. These may stem from low-level expression of Kir2.1EGFP in nuclei or cytosol even after Dox treatment. Alternatively, and more likely, these may reflect bleed-through of RFP signals into GFP channel. Overall, we confirmed that Kir2.1 proteins that were localized to the cellular membrane were largely down-regulated. We described these observations in detail in the figure legend of Figure 1-figure supplement 3, and added the result as Figure 1-figure supplement 3.

I found the quantification of the callosal projection to be rather minimal and the normalization approach not entirely transparent. For example does activity from P10-15 restore the full normal PATTERN of callosal connectivity or merely the density of input overall?

We thank the reviewer for this comment. Based on the comment, we added analyses of the pattern of callosal projections; the width of callosal axon innervation zone in layers 2/3 and 5, and densitometric line scans across all cortical layers. Our original quantification showed that the density of callosal axons reaching their target layer (i.e. cortical layer 2/3) is almost recovered in P6-P15 DOX condition (Fig1B-D), but new analyses suggest some aspects of callosal axon projections (the width of the innervation zone in layer 2/3 and 5 (Figure 1-figure supplement 4A,B), and lamina specific innervation pattern (Figure 1-figure supplement 4C)) might be only partially recovered. We have added these new results as Figure 1-figure supplement 4. In future study, we would like to assess the effect of the manipulations at finer resolution by 3D morphological reconstruction of axons of individual neurons.

Also in the discussion it would be nice to more clearly establish whether activity is thought to be maintaining a projection already formed by P10 or permitting the emergence of such a pattern.

Thank you for the suggestion. We have added thorough discussions about this point as follows. Page 7, lines 198-208:

“In the previous study, we showed that callosal axons could reach the innervation area almost normally under activity-reduction, and that the effects of activity-reduction became apparent afterwards (Mizuno et al., 2007). Callosal axons elaborate their branches extensively in P10P15 (Mizuno et al., 2010), and axon branching is regulated by neuronal activity (Matsumoto and Yamamoto, 2016). It is likely that activity is required for the processes of formation, rather than the maintenance of the connections already formed by P10, but the current study employed massive labeling of callosal axons which is not suited to clarify this. In addition, the restoration of activity in the Tet-off (Figure 1) or DREADD (Figure 2) experiment may not completely rescue the ramification pattern of individual axons. Single axon tracing experiments (Mizuno et al., 2010; Dhande et al., 2011) would be required to clarify this. Nonetheless, our findings suggest that callosal axons retain the ability, or are permitted, to grow and make region- and lamina-specific projections in the cortex during a limited period of postnatal cortical development under an activity-dependent mechanism.”

The calcium imaging is a valuable validation of the Kir expression approach, but it the study here appears to overinterpret what may simply be an intermediate level of activity restoration rather than a specific restoration of L events, as it seems that L events would be the most likely to occur under conditions of reduced overall activity. One possibility is that the absence of H events at P13 in the calcium is due to residual Kir expression creating a drag on high level network activation rather than any more complicated change in patterned spontaneous activity/connectivity. The conclusions from this study regarding the permissive role of activity during a critical window and the lack of a requirement for highly correlated activity are valuable, even if somewhat imprecise on both counts. The authors should probably refrain from use of the term patterned activity given that this was measured but not systematically compared to unpatterned spontaneous activity.

We thank the reviewer for this constructive comment. Based on this comment, we removed the term “patterned activity” throughout the manuscript and revised the title, abstract, introduction, results, and discussion extensively. For example, in the Discussion, we revised as follows.

“We have shown that the projections could be established even without fully restoring highly synchronous activity (Figure 4). L events, but not H events, were present in P13 cortex after Dox treatment at P6. L events may be sufficient for the formation of callosal projections. Alternatively, any form of activity with certain level(s) (i.e., “sufficiently” high activity with no specific pattern) could be permissive for the formation of callosal connections.”

Reviewer #2 (Public Review):

Tezuka et al. use in vivo manipulations of spontaneous activity to identify the activitydependent mechanisms of callosal projection development. Previous research of the authors' and other labs had shown that overexpressing the potassium channel Kir2.1, which reduces activity levels in the developing cortical network, blocks the formation of callosal connections almost entirely.

The current manuscript corroborates and extends these previous discoveries by:

1) Demonstrating that the effect of Kir overexpression can be rescued by pharmacogenetic network activation using DREADDs.<br /> 2) Revealing the requirement of network activity for the development of callosal projections during a particular developmental time window and by<br /> 3) Directly relating perturbed callosal development to the actual changes in activity patterns caused by the experimental manipulations.

Thus, this paper is important for our understanding of the role of neuronal activity in the development of long-range connections in the brain. In addition it provides strong evidence for a role of specific activity patterns in this process.

In general, the approach is very straightforward and the results clearly interpreted. Nevertheless, there are a few points to consider.

We thank the reviewer for these positive and supportive comments.

1) It is not clear in which cortical area(s) the in vivo 2-photon recordings were performed and in how far cortical areas that actually receive/send callosal projections were included or not in the analysis.

In response to this comment, we revised the text in the method section as follows.

“We aimed to record spontaneous neuronal activity in putative binocular zones in V1 (2.5 mm lateral of midline and 1 mm anterior of the posterior suture). Since the boundaries between V1 and higher visual areas, AL/LM are not as obvious as those in adult, our recordings likely contained juxtaposed lateral monocular V1 and AL/LM as well.”

Based on our colleaguesʼ unpublished observations, V1 and AL/LM can be distinguished solely by spontaneous activity patterns even before eye-opening. They also found frequencies of spontaneous activity are similar across mono/binocular regions of V1 and AL/LM (Murakami, Ohki, et al. unpublished). Thus, our results should hold even with the variability in recording sites.

2) It is not discussed what the duration of the CNO effect is. Do daily injections rescue activity patterns for 24 hours or a significant proportion of this period?

In response to this critical comment, we revised the text in the method section as follows.

“A previous study showed that an intraperitoneally injected CNO was effective (in terms of increasing activity) for about 9hrs (Alexander et al., 2009). The “partial rescue” effect we observed (Figure 2) may suggest that activity was not fully restored during 24hrs by our daily CNO injections.”

Reviewer #3 (Public Review):

The manuscript by Tezuka adds to an emerging story about the role of activity in the formation of callosal connections across the brain. Here, the authors show that they can use a TET system to switch off the activity of an exogenous potassium channel, in order to probe when activity might be necessary or sufficient for the formation of callosal connections. The authors find that artificial restoration of activity with DREADS is sufficient to rescue the formation of callosal connections, and that there is a critical period (somewhere between P5-P15) where activity must occur in order for the connections to form within the cortex. Finally, the authors show that when the potassium channel is removed during the critical period, the cortex exhibits activity, but few highly synchronous events. These results indicate that it is activity in general and not specifically highly synchronous activity that is necessary for the final innervation of the callosal cortex.

In general, the study is well done, and the writeup is polished, well summarized. The figures are solid. There are only a few criticisms/suggestions.

We thank the reviewer for the positive evaluation.

Major issue: Have the authors demonstrated a requirement for "patterned spontaneous activity"?

The authors claim variously in the abstract ("a distinct pattern of spontaneous activity") and in the results (pg 6, "our observations indicate that patterned spontaneous activity") and discussion (pg 6, "we demonstrated that patterned spontaneous activity") that it is "patterned" spontaneous activity that is key for the formation of callosal connections. However, when I was reading the paper, I came to the opposite conclusion: that any sufficiently high spontaneous activity is sufficient for the formation of these connections.

The authors showed that relieving the KIR expression from P5-15 allows the connections to form; however, in Figure 4, the authors show that the nature of the activity produced in the cortex (in terms of mixtures of H and L events) is very different. Nevertheless, the connections can form. Further, the authors showed that increasing activity when KIR is expressed using DREADS restores the connections. The pattern of activity produced by this DREADS + KIR expression is likely to be very different from the pattern of activity of a typically-developing animal. In total, I thought that the authors demonstrated, quite nicely, that it is just the presence of sufficient activity that is key to the innervation of the contralateral cortex. (It's not cell autonomous, as the authors showed before; there seems to be a "sufficient activity" requirement).

Therefore, I think the authors should remove references to the requirement of patterned activity and instead say something about sufficiently high activity (or some characterization that the authors choose). I think they've shown quite nicely that a specific pattern of the spontaneous activity is not important.

We thank the reviewer for this very important insight and interpretation. After considering all the currently presented data again, we have come to agree with the interpretation stated by the reviewer. We removed the term “patterned activity” throughout the manuscript and revised the title, abstract, introduction, results, and discussion extensively. Nevertheless, we would not completely discard the possibility that specific patterns of spontaneous activity, such as L-events, could potentially have some active contribution to the development of projection circuits, and would like to further address this in future study.

For example, in the Discussion, we revised the text as follows.

“We have shown that the projections could be established even without fully restoring highly synchronous activity (Figure 4). L events, but not H events, were present in P13 cortex after Dox treatment at P6. L events may be sufficient for the formation of callosal projections. Alternatively, any form of activity with certain level(s) (i.e., “sufficiently” high activity with no specific pattern) could be permissive for the formation of callosal connections.”

Author Response

Reviewer #1 (Public Review):

In computational modeling studies of behavioral data using reinforcement learning models, it has been implicitly assumed that parameter estimates generalize across tasks (generalizability) and that each parameter reflects a single cognitive function (interpretability). In this study, the authors examined the validity of these assumptions through a detailed analysis of experimental data across multiple tasks and age groups. The results showed that some parameters generalize across tasks, while others do not, and that interpretability is not sufficient for some parameters, suggesting that the interpretation of parameters needs to take into account the context of the task. Some researchers may have doubted the validity of these assumptions, but to my knowledge, no study has explicitly examined their validity. Therefore, I believe this research will make an important contribution to researchers who use computational modeling. In order to clarify the significance of this research, I would like the authors to consider the following points.

1) Effects of model misspecification

In general, model parameter estimates are influenced by model misspecification. Specifically, if components of the true process are not included in the model, the estimates of other parameters may be biased. The authors mentioned a little about model misspecification in the Discussion section, but they do not mention the possibility that the results of this study itself may be affected by it. I think this point should be discussed carefully.

The authors stated that they used state-of-the-art RL models, but this does not necessarily mean that the models are correctly specified. For example, it is known that if there is history dependence in the choice itself and it is not modeled properly, the learning rates depending on valence of outcomes (alpha+, alpha-) are subject to biases (Katahira, 2018, J Math Pscyhol). In the authors' study, the effect of one previous choice was included in the model as choice persistence, p. However, it has been pointed out that not including the effect of a choice made more than two trials ago in the model can also cause bias (Katahira, 2018). The authors showed taht the learning rate for positive RPE, alpha+ was inconsistent across tasks. But since choice persistence was included only in Task B, it is possible that the bias of alpha+ was different between tasks due to individual differences in choice persistence, and thus did not generalize.

However, I do not believe that it is necessary to perform a new analysis using the model described above. As for extending the model, I don't think it is possible to include all combinations of possible components. As is often said, every model is wrong, and only to varying degrees. What I would like to encourage the authors to do is to discuss such issues and then consider their position on the use of the present model. Even if the estimation results of this model are affected by misspecification, it is a fact that such a model is used in practice, and I think it is worthwhile to discuss the nature of the parameter estimates.

We thank the reviewer for this thoughtful question, and have added the following paragraph to the discussion section that is aims to address it:

“Another concern relates to potential model misspecification and its effects on model parameter estimates: If components of the true data-generating process are not included in a model (i.e., a model is misspecified), estimates of existing model parameters may be biased. For example, if choices have an outcome-independent history dependence that is not modeled properly, learning rate parameters have shown to be biased [63]. Indeed, we found that learning rate parameters were inconsistent across the tasks in our study, and two of our models (A and C) did not model history dependence in choice, while the third (model B) only included the effect of one previous choice (persistence parameter), but no multi-trial dependencies. It is hence possible that the differences in learning rate parameters between tasks were caused by differences in the bias induced by misspecification of history dependence, rather than a lack of generalization. Though pressing, however, this issue is difficult to resolve in practicality, because it is impossible to include all combinations of possible parameters in all computational models, i.e., to exhaustively search the space of possible models ("Every model is wrong, but to varying degrees"). Furthermore, even though our models were likely affected by some degree of misspecification, the research community is currently using models of this kind. Our study therefore sheds light on generalizability and interpretability in a realistic setting, which likely includes models with varying degrees of misspecification. Lastly, our models were fitted using robust computational tools and achieved good behavioral recovery (Fig. D.7), which also reduces the likelihood of model misspecification.“

2) Issue of reliability of parameter estimates

I think it is important to consider not only the bias in the parameter estimates, but also the issue of reliability, i.e., how stable the estimates will be when the same task is repeated with the same individual. For the task used in this study, has test-retest reliability been examined in previous studies? I think that parameters with low reliability will inevitably have low generalizability to other tasks. In this study, the use of three tasks seems to have addressed this issue without explicitly considering the reliability, but I would like the author to discuss this issue explicitly.

We thank the reviewer for this useful comment, and have added the following paragraph to the discussion section to address it:

“Furthermore, parameter generalizability is naturally bounded by parameter reliability, i.e., the stability of parameter estimates when participants perform the same task twice (test-retest reliability) or when estimating parameters from different subsets of the same dataset (split-half reliability). The reliability of RL models has recently become the focus of several parallel investigations [...], some employing very similar tasks to ours [...]. The investigations collectively suggest that excellent reliability can often be achieved with the right methods, most notably by using hierarchical model fitting. Reliability might still differ between tasks or models, potentially being lower for learning rates than other RL parameters [...], and differing between tasks (e.g., compare [...] to [...]). In this study, we used hierarchical fitting for tasks A and B and assessed a range of qualitative and quantitative measures of model fit for each task [...], boosting our confidence in high reliability of our parameter estimates, and the conclusion that the lack of between-task parameter correlations was not due to a lack of parameter reliability, but a lack of generalizability. This conclusion is further supported by the fact that larger between-task parameter correlations (r>0.5) than those observed in humans were attainable---using the same methods---in a simulated dataset with perfect generalization.“

3) About PCA

In this paper, principal component analysis (PCA) is used to extract common components from the parameter estimates and behavioral features across tasks. When performing PCA, were each parameter estimate and behavioral feature standardized so that the variance would be 1? There was no mention about this. It seems that otherwise the principal components would be loaded toward the features with larger variance. In addition, Moutoussis et al. (Neuron, 2021, 109 (12), 2025-2040) conducted a similar analysis of behavioral parameters of various decision-making tasks, but they used factor analysis instead of PCA. Although the authors briefly mentioned factor analysis, it would be better if they also mentioned the reason why they used PCA instead of factor analysis, which can consider unique variances.

To answer the reviewer's first question: We indeed standardized all features before performing the PCA. Apologies for missing to include this information - we have now added a corresponding sentence to the methods sections.

We also thank the reviewer for the mentioned reference, which is very relevant to our findings and can help explain the roles of different PCs. Like in our study, Moutoussis et al. found a first PC that captured variability in task performance, and subsequent PCs that captured task contrasts. We added the following paragraph to our manuscript:

“PC1 therefore captured a range of "good", task-engaged behaviors, likely related to the construct of "decision acuity" [...]. Like our PC1, decision acuity was the first component of a factor analysis (variant of PCA) conducted on 32 decision-making measures on 830 young people, and separated good and bad performance indices. Decision acuity reflects generic decision-making ability, and predicted mental health factors, was reflected in resting-state functional connectivity, but was distinct from IQ [...].”

To answer the reviewer's question about PCA versus FA, both approaches are relatively similar conceptually, and oftentimes share the majority of the analysis pipeline in practice. The main difference is that PCA breaks up the existing variance in a dataset in a new way (based on PCs rather than the original data features), whereas FA aims to identify an underlying model of latent factors that explain the observable features. This means that PCs are linear combinations of the original data features, whereas Factors are latent factors that give rise to the observable features of the dataset with some noise, i.e., including an additional error term.

However, in practice, both methods share the majority of computation in the way they are implemented in most standard statistical packages: FA is usually performed by conducting a PCA and then rotating the resulting solution, most commonly using the Varimax rotation, which maximizes the variance between features loadings on each factor in order to make the result more interpretable, and thereby foregoing the optimal solution that has been achieved by the PCA (which lack the error term). Maximum variance in feature loadings means that as many features as possible will have loadings close to 0 and 1 on each factor, reducing the number of features that need to be taken into account when interpreting this factor. Most relevant in our situation is that PCA is usually a special case of FA, with the only difference that the solution is not rotated for maximum interpretability. (Note that this rotation can be minor if feature loadings already show large variance in the PCA solution.)

To determine how much our results would change in practice if we used FA instead of PCA, we repeated the analysis using FA. Both are shown side-by-side below, and the results are quite similar:

We therefore conclude that our specific results are robust to the choice of method used, and that there is reason to believe that our PC1 is related to Moutoussis et al.’s F1 despite the differences in method.

Reviewer #2 (Public Review):

I am enthusiastic about the comprehensive approach, the thorough analysis, and the intriguing findings. This work makes a timely contribution to the field and warrants a wider discussion in the community about how computational methods are deployed and interpreted. The paper is also a great and rare example of how much can be learned from going beyond a meta-analytic approach to systematically collect data that assess commonly held assumptions in the field, in this case in a large data-driven study across multiple tasks. My only criticism is that at times, the paper misses opportunities to be more constructive in pinning down exactly why authors observe inconsistencies in parameter fits and interpretation. And the somewhat pessimistic outlook relies on some results that are, in my view at least, somewhat expected based on what we know about human RL. Below I summarize the major ways in which the paper's conclusions could be strengthened.

One key point the authors make concerns the generalizability of absolute vs. relative parameter values. It seems that at least in the parameter space defined by +LRs and exploration/noise (which are known to be mathematically coupled), subjects clustered similarly for tasks A and C. In other words, as the authors state, "both learning rate and inverse temperature generalized in terms of the relationships they captured between participants". This struck me as a more positive and important result than it was made out to be in the paper, for several reasons:

• As authors point out in the discussion, a large literature on variable LRs has shown that people adapt their learning rates trial-by-trial to the reward function of the environment; given this, and given that all models tested in this work have fixed learning rates, while the three tasks vary on the reward function, the comparison of absolute values seems a bit like a red-herring.

We thank the reviewers for this recommendation and have reworked the paper substantially to address the issue. We have modified the highlights, abstract, introduction, discussion, conclusion, and relevant parts of the results section to provide equal weight to the successes and failures of generalization.

Highlights:

● “RL decision noise/exploration parameters generalize in terms of between-participant variation, showing similar age trajectories across tasks.”

● “These findings are in accordance with previous claims about the developmental trajectory of decision noise/exploration parameters.”

Abstract:

● “We found that some parameters (exploration / decision noise) showed significant generalization: they followed similar developmental trajectories, and were reciprocally predictive between tasks.“

The introduction now introduces different potential outcomes of our study with more equal weight:

“Computational modeling enables researchers to condense rich behavioral datasets into simple, falsifiable models (e.g., RL) and fitted model parameters (e.g., learning rate, decision temperature) [...]. These models and parameters are often interpreted as a reflection of ("window into") cognitive and/or neural processes, with the ability to dissect these processes into specific, unique components, and to measure participants' inherent characteristics along these components.

For example, RL models have been praised for their ability to separate the decision making process into value updating and choice selection stages, allowing for the separate investigation of each dimension. Crucially, many current research practices are firmly based on these (often implicit) assumptions, which give rise to the expectation that parameters have a task- and model-independent interpretation and will seamlessly generalize between studies. However, there is growing---though indirect---evidence that these assumptions might not (or not always) be valid.

The following section lays out existing evidence in favor and in opposition of model generalizability and interpretability. Building on our previous opinion piece, which---based on a review of published studies---argued that there is less evidence for model generalizability and interpretability than expected based on current research practices [...], this study seeks to directly address the matter empirically.”

We now also provide more even evidence for both potential outcomes:

“Many current research practices are implicitly based on the interpretability and generalizability of computational model parameters (despite the fact that many researchers explicitly distance themselves from these assumptions). For our purposes, we define a model variable (e.g., fitted parameter, reward-prediction error) as generalizable if it is consistent across uses, such that a person would be characterized with the same values independent of the specific model or task used to estimate the variable. Generalizability is a consequence of the assumption that parameters are intrinsic to participants rather than task dependent (e.g., a high learning rate is a personal characteristic that might reflect an individual's unique brain structure). One example of our implicit assumptions about generalizability is the fact that we often directly compare model parameters between studies---e.g., comparing our findings related to learning-rate parameters to a previous study's findings related to learning-rate parameters. Note that such a comparison is only valid if parameters capture the same underlying constructs across studies, tasks, and model variations, i.e., if parameters generalize. The literature has implicitly equated parameters in this way in review articles [...], meta-analyses [...], and also most empirical papers, by relating parameter-specific findings across studies. We also implicitly evoke parameter generalizability when we study task-independent empirical parameter priors [...], or task-independent parameter relationships (e.g., interplay between different kinds of learning rates [...]), because we presuppose that parameter settings are inherent to participants, rather than task specific.

We define a model variable as interpretable if it isolates specific and unique cognitive elements, and/or is implemented in separable and unique neural substrates. Interpretability follows from the assumption that the decomposition of behavior into model parameters "carves cognition at its joints", and provides fundamental, meaningful, and factual components (e.g., separating value updating from decision making). We implicitly invoke interpretability when we tie model variables to neural substrates in a task-general way (e.g., reward prediction errors to dopamine function [...]), or when we use parameters as markers of psychiatric conditions (e.g., working-memory parameter and schizophrenia [...]). Interpretability is also required when we relate abstract parameters to aspects of real-world decision making [...], and generally, when we assume that model variables are particularly "theoretically meaningful" [...].

However, in midst the growing recognition of computational modeling, the focus has also shifted toward inconsistencies and apparent contradictions in the emerging literature, which are becoming apparent in cognitive [...], developmental [...], clinical [...], and neuroscience studies [...], and have recently become the focus of targeted investigations [...]. For example, some developmental studies have shown that learning rates increased with age [...], whereas others have shown that they decrease [...]. Yet others have reported U-shaped trajectories with either peaks [...] or troughs [...] during adolescence, or stability within this age range [...] (for a comprehensive review, see [...]; for specific examples, see [...]). This is just one striking example of inconsistencies in the cognitive modeling literature, and many more exist [...]. These inconsistencies could signify that computational modeling is fundamentally flawed or inappropriate to answer our research questions. Alternatively, inconsistencies could signify that the method is valid, but our current implementations are inappropriate [...]. However, we hypothesize that inconsistencies can also arise for a third reason: Even if both method and implementation are appropriate, inconsistencies like the ones above are expected---and not a sign of failure---if implicit assumptions of generalizability and interpretability are not always valid. For example, model parameters might be more context-dependent and less person-specific that we often appreciate [...]“

In the results section, we now highlight findings more that are compatible with generalization: “For α+, adding task as a predictor did not improve model fit, suggesting that α+ showed similar age trajectories across tasks (Table 2). Indeed, α+ showed a linear increase that tapered off with age in all tasks (linear increase: task A: β = 0.33, p < 0.001; task B: β = 0.052, p < 0.001; task C: β = 0.28, p < 0.001; quadratic modulation: task A: β = −0.007, p < 0.001; task B: β = −0.001, p < 0.001; task C: β = −0.006, p < 0.001). For noise/exploration and Forgetting parameters, adding task as a predictor also did not improve model fit (Table 2), suggesting similar age trajectories across tasks.”

“For both α+ and noise/exploration parameters, task A predicted tasks B and C, and tasks B and C predicted task A, but tasks B and C did not predict each other (Table 4; Fig. 2D), reminiscent of the correlation results that suggested successful generalization (section 2.1.2).”

“Noise/exploration and α+ showed similar age trajectories (Fig. 2C) in tasks that were sufficiently similar (Fig. 2D).” And with respect to our simulation analysis (for details, see next section):

“These results show that our method reliably detected parameter generalization in a dataset that exhibited generalization. ”

We also now provide more nuance in our discussion of the findings:

“Both generalizability [...] and interpretability (i.e., the inherent "meaningfulness" of parameters) [...] have been explicitly stated as advantages of computational modeling, and many implicit research practices (e.g., comparing parameter-specific findings between studies) showcase our conviction in them [...]. However, RL model generalizability and interpretability has so far eluded investigation, and growing inconsistencies in the literature potentially cast doubt on these assumptions. It is hence unclear whether, to what degree, and under which circumstances we should assume generalizability and interpretability. Our developmental, within-participant study revealed a nuanced picture: Generalizability and interpretability differed from each other, between parameters, and between tasks.”

“Exploration/noise parameters showed considerable generalizability in the form of correlated variance and age trajectories. Furthermore, the decline in exploration/noise we observed between ages 8-17 was consistent with previous studies [13, 66, 67], revealing consistency across tasks, models, and research groups that supports the generalizability of exploration / noise parameters. However, for 2/3 pairs of tasks, the degree of generalization was significantly below the level of generalization expected for perfect generalization. Interpretability of exploration / noise parameters was mixed: Despite evidence for specificity in some cases (overlap in parameter variance between tasks), it was missing in others (lack of overlap), and crucially, parameters lacked distinctiveness (substantial overlap in variance with other parameters).”

“Taken together, our study confirms the patterns of generalizable exploration/noise parameters and task-specific learning rate parameters that are emerging from the literature [13].”

• Regarding the relative inferred values, it's unclear how high we really expect correlations between the same parameter across tasks to be. E.g., if we take Task A and make a second, hypothetical, Task B by varying one feature at a time (say, stochasticity in reward function), how correlated are the fitted LRs going to be? Given the different sources of noise in the generative model of each task and in participant behavior, it is hard to know whether a correlation coefficient of 0.2 is "good enough" generalizability.

We thank the reviewer for this excellent suggestion, which we think helped answer a central question that our previous analyses had failed to address, and also provided answers to several other concerns raised by both reviewers in other section. We have conducted these additional analyses as suggested, simulating artificial behavioral data for each task, fitting these data using the models used in humans, repeating the analyses performed on humans on the new fitted parameters, and using bootstrapping to statistically compare humans to the hence obtained ceiling of generalization. We have added the following section to our paper, which describes the results in detail:

“Our analyses so far suggest that some parameters did not generalize between tasks, given differences in age trajectories (section 2.1.3) and a lack of mutual prediction (section 2.1.4). However, the lack of correspondence could also arise due to other factors, including behavioral noise, noise in parameter fitting, and parameter trade-offs within tasks. To rule these out, we next established the ceiling of generalizability attainable using our method.

We established the ceiling in the following way: We first created a dataset with perfect generalizability, simulating behavior from agents that use the same parameters across all tasks (suppl. Appendix E). We then fitted this dataset in the same way as the human dataset (e.g., using the same models), and performed the same analyses on the fitted parameters, including an assessment of age trajectories (suppl. Table E.8) and prediction between tasks (suppl. Tables E.9, E.10, and E.11). These results provide the practical ceiling of generalizability. We then compared the human results to this ceiling to ensure that the apparent lack of generalization was valid (significant difference between humans and ceiling), and not in accordance with generalization (lack of difference between humans and ceiling).

Whereas humans had shown divergent trajectories for parameter alpha- (Fig. 2B; Table 1), the simulated agents did not show task differences for alpha- or any other parameter (suppl. Fig E.8B; suppl. Table E.8, even when controlling for age (suppl. Tables E.9 and E.10), as expected from a dataset of generalizing agents. Furthermore, the same parameters were predictive between tasks in all cases (suppl. Table E.11). These results show that our method reliably detected parameter generalization in a dataset that exhibited generalization.

Lastly, we established whether the degree of generalization in humans was significantly different from agents. To this aim, we calculated the Spearman correlations between each pair of tasks for each parameter, for both humans (section 2.1.2; suppl. Fig. H.9) and agents, and compared both using bootstrapped confidence intervals (suppl. Appendix E). Human parameter correlations were significantly below the ceiling for all parameters except alpha+ (A vs B) and epsilon / 1/beta (A vs C; suppl. Fig. E.8C). This suggests that humans were within the range of maximally detectable generalization in two cases, but showed less-than-perfect generalization between other task combinations and for parameters Forgetting and alpha-.”

• The +LR/inverse temp relationship seems to generalize best between tasks A/C, but not B/C, a common theme in the paper. This does not seem surprising given that in A and C there is a key additional task feature over the bandit task in B -- which is the need to retain state-action associations. Whether captured via F (forgetting) or K (WM capacity), the cognitive processes involved in this learning might interact with LR/exploration in a different way than in a task where this may not be necessary.

We thank the reviewer for this comment, which raises an important issue. We are adding the specific pairwise correlations and scatter plots for the pairs of parameters the reviewer asked about below (“bf_alpha” = LR task A; “bf_forget” = F task A; “rl_forget” = F task C; “rl_log_alpha” = LR task C; “rl_K” = WM capacity task C):

Within tasks:

Between tasks:

To answer the question in more detail, we have expanded our section about limitations stemming from parameter tradeoffs in the following way:

“One limitation of our results is that regression analyses might be contaminated by parameter cross-correlations (sections 2.1.2, 2.1.3, 2.1.4), which would reflect modeling limitations (non-orthogonal parameters), and not necessarily shared cognitive processes. For example, parameters alpha and beta are mathematically related in the regular RL modeling framework, and we observed significant within-task correlations between these parameters for two of our three tasks (suppl. Fig. H.10, H.11). This indicates that caution is required when interpreting correlation results. However, correlations were also present between tasks (suppl. Fig. H.9, H.11), suggesting that within-model trade-offs were not the only explanation for shared variance, and that shared cognitive processes likely also played a role.

Another issue might arise if such parameter cross-correlations differ between models, due to the differences in model parameterizations across tasks. For example, memory-related parameters (e.g., F, K in models A and C) might interact with learning- and choice-related parameters (e.g., alpha+, alpha-, noise/exploration), but such an interaction is missing in models that do not contain memory-related parameters (e.g., task B). If this indeed the case, i.e., parameters trade off with each other in different ways across tasks, then a lack of correlation between tasks might not reflect a lack of generalization, but just the differences in model parameterizations. Suppl. Fig. \ref{figure:S2AlphaBetaCorrelations} indeed shows significant, medium-sized, positive and negative correlations between several pairs of Forgetting, memory-related, learning-related, and exploration parameters (though with relatively small effect sizes; Spearman correlation: 0.17 < |r| < 0.22).

The existence of these correlations (and differences in correlations between tasks) suggest that memory parameters likely traded off with each other, as well as with other parameters, which potentially affected generalizability across tasks. However, some of the observed correlations might be due to shared causes, such as a common reliance on age, and the regression analyses in the main paper control for these additional sources of variance, and might provide a cleaner picture of how much variance is actually shared between parameters.

Furthermore, correlations between parameters within models are frequent in the existing literature, and do not prevent researchers from interpreting parameters---in this sense, the existence of similar correlations in our study allows us to address the question of generalizability and interpretability in similar circumstances as in the existing literature.”

• More generally, isn't relative generalizability the best we would expect given systematic variation in task context? I agree with the authors' point that the language used in the literature sometimes implies an assumption of absolute generalizability (e.g. same LR across any task). But parameter fits, interactions, and group differences are usually interpreted in light of a single task+model paradigm, precisely b/c tasks vary widely across critical features that will dictate whether different algorithms are optimal or not and whether cognitive functions such as WM or attention may compensate for ways in which humans are not optimal. Maybe a more constructive approach would be to decompose tasks along theoretically meaningful features of the underlying Markov Decision Process (which gives a generative model), and be precise about (1) which features we expect will engage additional cognitive mechanisms, and (2) how these mechanisms are reflected in model parameters.

We thank the reviewer for this comment, and will address both points in turn:

(1) We agree with the reviewer's sentiment about relative generalizability: If we all interpreted our models exclusively with respect to our specific task design, and never expected our results to generalize to other tasks or models, there would not be a problem. However, the current literature shows a different pattern: Literature reviews, meta-analyses, and discussion sections of empirical papers regularly compare specific findings between studies. We compare specific parameter values (e.g., empirical parameter priors), parameter trajectories over age, relationships between different parameters (e.g., balance between LR+ and LR-), associations between parameters and clinical symptoms, and between model variables and neural measures on a regular basis. The goal of this paper was really to see if and to what degree this practice is warranted. And the reviewer rightfully alerted us to the fact that our data imply that these assumptions might be valid in some cases, just not in others.

(2) With regard to providing task descriptions that relate to the MDP framework, we have included the following sentence in the discussion section:

“Our results show that discrepancies are expected even with a consistent methodological pipeline, and using up-to-date modeling techniques, because they are an expected consequence of variations in experimental tasks and computational models (together called "context"). Future research needs to investigate these context factors in more detail. For example, which task characteristics determine which parameters will generalize and which will not, and to what extent? Does context impact whether parameters capture overlapping versus distinct variance? A large-scale study could answer these questions by systematically covering the space of possible tasks, and reporting the relationships between parameter generalizability and distance between tasks. To determine the distance between tasks, the MDP framework might be especially useful because it decomposes tasks along theoretically meaningful features of the underlying Markov Decision Process.“

Another point that merits more attention is that the paper pretty clearly commits to each model as being the best possible model for its respective task. This is a necessary premise, as otherwise, it wouldn't be possible to say with certainty that individual parameters are well estimated. I would find the paper more convincing if the authors include additional information and analysis showing that this is actually the case.

We agree with the sentiment that all models should fit their respective task equally well. However, there is no good quantitative measure of model fit that is comparable across tasks and models - for example, because of the difference in difficulty between the tasks, the number of choices explained would not be a valid measure to compare how well the models are doing across tasks. To address this issue, we have added the new supplemental section (Appendix C) mentioned above that includes information about the set of models compared, and explains why we have reason to believe that all models fit (equally) well. We also created the new supplemental Figure D.7 shown above, which directly compares human and simulated model behavior in each task, and shows a close correspondence for all tasks. Because the quality of all our models was a major concern for us in this research, we also refer the reviewer and other readers to the three original publications that describe all our modeling efforts in much more detail, and hopefully convince the reviewer that our model fitting was performed according to high standards.

I am particularly interested to see whether some of the discrepancies in parameter fits can be explained by the fact that the model for Task A did not account for explicit WM processes, even though (1) Task A is similar to Task C (Task A can be seen as a single condition of Task C with 4 states and 2 possible visible actions, and stochastic rather than deterministic feedback) and (2) prior work has suggested a role for explicit memory of single episodes even in stateless bandit tasks such as Task B.

We appreciate this very thoughtful question, which raises several important issues. (1) As the reviewer said, the models for task A and task C are relatively different even though the underlying tasks are relatively similar (minus the differences the reviewer already mentioned, in terms of visibility of actions, number of actions, and feedback stochasticity). (2) We also agree that the model for task C did not include episodic memory processes even though episodic memory likely played a role in this task, and agree that neither the forgetting parameters in tasks A and C, nor the noise/exploration parameters in tasks A, B, and C are likely specific enough to capture all the memory / exploration processes participants exhibited in these tasks.

However, this problem is difficult to solve: We cannot fit an episodic-memory model to task B because the task lacks an episodic-memory manipulation (such as, e.g., in Bornstein et al., 2017), and we cannot fit a WM model to task A because it lacks the critical set-size manipulation enabling identification of the WM component (modifying set size allows the model to identify individual participants’ WM capacities, so the issue cannot be avoided in tasks with only one set size). Similarly, we cannot model more specific forgetting or exploration processes in our tasks because they were not designed to dissociate these processes. If we tried fitting more complex models that include these processes to these tasks, they would most likely lose in model comparison because the increased complexity would not lead to additional explained behavioral variance, given that the tasks do not elicit the relevant behavioral patterns. Because the models therefore do not specify all the cognitive processes that participants likely employ, the situation described by the reviewer arises, namely that different parameters sometimes capture the same cognitive processes across tasks and models, while the same parameters sometimes capture different processes.

And while the reviewer focussed largely on memory-related processes, the issue of course extends much further: Besides WM, episodic memory, and more specific aspects of forgetting and exploration, our models also did not take into account a range of other processes that participants likely engaged in when performing the tasks, including attention (selectivity, lapses), reasoning / inference, mental models (creation and use), prediction / planning, hypothesis testing, etc., etc. In full agreement with the reviewer’s sentiment, we recently argued that this situation is ubiquitous to computational modeling, and should be considered very carefully by all modelers because it can have a large impact on model interpretation (Eckstein et al., 2021).

If we assume that many more cognitive processes are likely engaged in each task than are modeled, and consider that every computational model includes just a small number of free parameters, parameters then necessarily reflect a multitude of cognitive processes. The situation is additionally exacerbated by the fact that more complex models become increasingly difficult to fit from a methodological perspective, and that current laboratory tasks are designed in a highly controlled and consequently relatively simplistic way that does not lend itself to simultaneously test a variety of cognitive processes.

The best way to deal with this situation, we think, is to recognize that in different contexts (e.g., different tasks, different computational models, different subject populations), the same parameters can capture different behaviors, and different parameters can capture the same behaviors, for the reasons the reviewer lays out. Recognizing this helps to avoid misinterpreting modeling results, for example by focusing our interpretation of model parameters to our specific task and model, rather than aiming to generalize across multiple tasks. We think that recognizing this fact also helps us understand the factors that determine whether parameters will capture the same or different processes across contexts and whether they will generalize. This is why we estimated here whether different parameters generalize to different degrees, which other factors affect generalizability, etc. Knowing the practical consequences of using the kinds of models we currently use will therefore hopefully provide a first step in resolving the issues the reviewer laid out.

It is interesting that one of the parameters that generalizes least is LR-. The authors make a compelling case that this is related to a "lose-stay" behavior that benefits participants in Task B but not in Task C, which makes sense given the probabilistic vs deterministic reward function. I wondered if we can rule out the alternative explanation that in Task C, LR- could reflect a different interpretation of instructions vis. a vis. what rewards indicate - do authors have an instruction check measure in either task that can be correlated with this "lose-stay" behavior and with LR-? And what does the "lose-stay" distribution look like, for Task C at least? I basically wonder if some of these inconsistencies can be explained by participants having diverging interpretations of the deterministic nature of the reward feedback in Task C. The order of tasks might matter here as well -- was task order the same across participants? It could be that due to the within-subject design, some participants may have persisted in global strategies that are optimal in Task B, but sub-optimal in Task C.

The PCA analysis adds an interesting angle and a novel, useful lens through which we can understand divergence in what parameters capture across different tasks. One observation is that loadings for PC2 and PC3 are strikingly consistent for Task C, so it looks more like these PCs encode a pairwise contrast (PC2 is C with B and PC2 is C with A), primarily reflecting variability in performance - e.g. participants who did poorly on Task C but well on Task B (PC2) or Task A (PC3). Is it possible to disentangle this interpretation from the one in the paper? It also is striking that in addition to performance, the PCs recover the difference in terms of LR- on Task B, which again supports the possibility that LR- divergence might be due to how participants handle probabilistic vs. deterministic feedback.

We appreciate this positive evaluation of our PCA and are glad that it could provide a useful lens for understanding parameters. We also agree to the reviewer's observation that PC2 and PC3 reflect task contrasts (PC2: task B vs task C; PC3: task A vs task C), and phrase it in the following way in the paper:

“PC2 contrasted task B to task C (loadings were positive / negative / near-zero for corresponding features of tasks B / C / A; Fig. 3B). PC3 contrasted task A to both B and C (loadings were positive / negative for corresponding features on task A / tasks B and C; Fig. 3C).”

Hence, the only difference between our interpretation and the reviewer’s seems to be whether PC3 contrasts task C to task B as well as task A, or just to task A. Our interpretation is supported by the fact that loadings for tasks A and C are quite similar on PC3; however, both interpretations seem appropriate.

We also appreciate the reviewer's positive evaluation of the fact that the PCA reproduces the differences in LR-, and its relationship to probabilistic/deterministic feedback. The following section reiterates this idea:

“alpha- loaded positively in task C, but negatively in task B, suggesting that performance increased when participants integrated negative feedback faster in task C, but performance decreased when they did the same in task B. As mentioned before, contradictory patterns of alpha- were likely related to task demands: The fact that negative feedback was diagnostic in task C likely favored fast integration of negative feedback, while the fact that negative feedback was not diagnostic in task B likely favored slower integration (Fig. 1E). This interpretation is supported by behavioral findings: "Lose-stay" behavior (repeating choices that produce negative feedback) showed the same contrasting pattern as alpha- on PC1. It loaded positively in task B, showing Lose-stay behavior benefited performance, but it loaded negatively on task C, showing that it hurt performance (Fig. 3A). This supports the claim that lower alpha- was beneficial in task B, while higher alpha- was beneficial in task C, in accordance with participant behavior and developmental differences.“

Author Response

Reviewer #3 (Public Review ):

Rhodes et al. explored novel signalling peptides by searching genes encoding small proteins having signal peptide, which are transcriptionally induced upon biotic elicitor treatments in Arabidopsis thaliana. They found that small potentially secreted proteins, designate as CTNIPs based on the conserved sequence motif, are transcriptionally induced upon 7 different elicitors. In A. thaliana, 5 CTINPs are encoded in the genome, and CTNIP4 is strongly induced upon the elicitor treatments. Chemically synthesized signal peptide-deleted CTNIP proteins except for CTNIP5 show the activities to induce Ca2+ influx and MAP kinases phosphorylation in A. thaliana, which are the hallmarks of elicitor-induced immune signalling. The authors found that CTNIP4 can induce ROS burst in a BAK1-dependent manner in A. thaliana, suggesting that CTNIP4 receptor uses BAK1 as a co-receptor for CTNIP4-induced signalling. Moreover, they show that the C-terminal 23 amino acids of CTINP4 is sufficient to induce the responses, and the conserved 2 Cys residues in this C-terminal region is required for the activity. Based on these findings, the authors further explored a CTNIP receptor by identifying proteins that interact with BAK1 upon CTNIP4 treatment using an IP-MS approach. This approach identified HSL3, which is a leucine-rich repeat receptor-like kinase (LRR-RLK), as a receptor candidate. The authors elegantly demonstrate that HSL3 is a receptor of CTNIPs in A. thaliana by taking complementary biochemical and genetic approaches. They provide some evidences that CTNIP4-HSL3 pathway regulates root growth of A. thaliana. Lastly, the authors proposed that the HSL3-CTNIP signalling module is evolutionarily ancient, which appeared before the divergence of angiosperm species.

The conclusions of this paper regarding the CTNIP-HSL3 pair in A. thaliana are well supported by data. The identification of the CTNIP-HSL3 pair is very significant in the area of plant research.

Thank you for the positive comments.

Weaknesses of this paper would be

1) There is no evidence provided that CTNIPs are actually secreted from plant cells. And, mature forms of CTNIPs are not examined. And, thus, there is space for discussion whether CTNIPs function as secreted peptide hormones. However, generally speaking, addressing these are rather challenging.

Thank you for your comments, as mentioned previously, we agree that these are important considerations and limitations of the manuscript. We now discuss this further within the manuscript.

2) The CTNIPs in A. thaliana are initially screened and identified based on the inducibility by biotic elicitors. However, contributions of the CTNIP-HSL3 module to disease resistance are not examined.

In the current manuscript, we are reporting the initial identification of the HSL3-CTNIP signalling module and its phylogeny. Further work is now required to elucidate its physiological role(s). Under our conditions, we were unable to observe any phenotype upon spray-infection with P. syringae pv tomato DC3000 ΔAvrPto/ΔAvrPto, and have now included this data for information (Figure3-figure supplement 5). It remains to be established whether the HSL3-CTNIP signalling module contributes to resistance under different conditions or to different pathogens, or plays a role in the regulation of plant growth upon microbial perception. These are also now discussed in the text.

3) The authors have performed a phylogenetic analysis using full-length sequences of the receptor kinases. However, in order to discuss co-evolution of ligand-receptor pairs, it would be more appropriate to use ectodomains of the receptor kinases for the purpose. Actually, the phylogenetic tree in this paper is different form the trees in the published study (Furumizu et al. doi:10.1093/PLCELL/KOAB173), which used ectodomains for the analysis. Conclusions in this paper can be drawn differently. Based on Furumizu et al., HSL3-related LRR-RLKs in monocots are diversified and less related to HSL3 homologs in dicots. This raise a question whether HSL3 homologs in monocots are HSL3 orthologs to draw the conclusion that the HSL3-CTNIP module is conserved and diversified among angiosperms. It is favourable to test and show that CTNIP-HSL3 combinations from monocots also function as the functional module, for instance, using the Nicotiana benthamiana system. Related, testing one pair each for A. thaliana and M. truncatula is not sufficient to deliver the conclusion related to a co-evolution of ligand-receptor specificity because A. thaliana has 5 CTNIPs and Medicago truncatula has 7 HSL3 homologs and 5 CTNIPs, and thus different combinations may still function.

Thank you for your suggestions. We have included additional phylogenetic analyses based upon the full-length, ectodomain and the kinase domain.

We agree that further work is required to establish HSL3 homologs are functional orthologs and have now stated this explicitly within the text. Going forward it would be interesting to test this in the N. benthamiana and native systems.

Author Response

Reviewer #1 (Public Review):

This paper presents an approach to estimate Rt for 170 countries. While it is an impressive amount of work, I think the pipeline is similar to many currently available frameworks. The paper claims the following novelties over current framework, but more efforts are needed to be done to make it convincing.

1) Obtain stable estimate from multiple types of data:

It turns out the stable estimates just repeatedly use the same approaches to different time series (Figure 3A middle). From the wording I think there should be some methods to combine these time series to have a single estimate of Rt. Overall, the Rt and the time series of infection should be unique. It would be suboptimal, for example if there are big differences in the results from death time series and reported cases time series, which one should I trust?

We think it is a strength to compute different Rt values based on different data, as this allows researchers, policy makers and the public alike to compare the information from different observation types directly. Any discrepancy between two Re trajectories (e.g. between the Re based on cases, Rcc(t), and that based on hospitalisations Rh(t)) is an indication to investigate which external variables (e.g. testing strategy) have changed. We have found it a great advantage when communicating and sharing our results outside of academia that we could point to these separately obtained Re estimates: if the estimates all agreed, more confidence could be given to them.

If one would want to estimate a single estimate, this would require adopting a fundamentally different framework to estimate Re, which exceeds the scope of this work. One could use heuristics (weights representing the trustworthiness of a given source at a given time) to combine the various Re estimates into a single ensemble estimate. Alternatively, one could model the full underlying population dynamics (e.g. with a compartmental model including hospitalization and death) and adopt a fully Bayesian approach to fitting such a model. However, both options require heuristics or priors that will vary substantially through time and per country (as discussed in the Supplementary Discussion), and thus limit how widely the pipeline can be applied.

We have revised the manuscript to make it more clear (early on) that we estimate multiple Re values from separate types of data (see also the response to reviewer 3, item #5). In addition, we now discuss more explicitly what the advantages and disadvantages are of showing these estimates separately (lines 281-290).

2) Adequate representation of uncertainty:

This is the result in Figure 2, suggesting the CI from EpiEstim is too narrow. This would be expected given that EpiEstim assumed the input infection time series is observed and fixed. It would be expected that the proposed approach would provide wider CI and hence the proportion covered would be more. However, I think to validate the wider CI is the correct one, simulation studies are required. I think the most related one would be Figure 1B. The results suggested that the approach works when the Rt is not rapidly changing. However, I have concern on the methods for simulation (details below).

Indeed, the difference in coverage between our method and EpiEstim is due to observation noise. We agree the CI from EpiEstim should be correct assuming that the infection incidence time series can be observed perfectly. However, in reality quite a bit of variability is introduced between infection and case observation: not only due to the delay from infection to observation, but also due to e.g. reduced testing capacity on weekends or reporting errors. To accurately assess the coverage of our method (and whether the CIs are too narrow or too wide) we need to include realistic amounts of observation noise in the simulations. This is why we add autocorrelated noise to our simulated observations, where this noise mimics observed residuals in Switzerland and other countries (Figs. S3, S4, S15, S17).

We have now added explicit comparison to the EpiEstim confidence intervals to supplementary Fig. S4. In addition, we extended the corresponding method section to describe more extensively why and how we added observation noise to our simulations (lines 498-518; see also the detailed response to comment 4 below).

3) Real-time of the Rt

There is no simulation about the real-time property of the Rt. The most related one is still Figure 1B. However, looks at the right-tail of the figure (the real-time performance), the proportion covered the true value is decreasing and more efforts are needed to support the framework can be accurate in real-time. For example, how is the real-time performance when Rt is increasing, or Rt decrease sharply due to lock down?

As suggested, we included an additional simulation study to investigate the accuracy and stability of the last possible Re estimate. We present this analysis in a new results paragraph (subsection "Stability of Re estimates in an outbreak monitoring context"; line 121) and Figure S10. Using this analysis, we highlight the trade-off that exists between the timeliness of the Re estimates and their stability.

4) simulation methods to estimate Rt

Both 2) and 3) need simulation to support the results, and hence the simulation approach would be critical. The first part based on Poisson distribution to generate an infection time series, which is OK. However, the issue is the secondary part about how the authors obtained the time series for death/hospitalization/reported cases. To me, after generating the infection time series, based on the delay distribution from infection to death/hospitalization/reported, we could obtain those time series. I am not clear and sure if the authors approach is correct by using smoothing and fitting ARIMA to get those time series.

We believe there may have been some confusion about how our simulation set-up works, and we provided insufficient detail on the design decisions behind this set-up. We have added more explanation for both points to the paper (lines 503-518; additional supplementary Figs. S15-S17). In brief, our simulation process consists of three parts. We first conduct the two steps the reviewer also mentioned: (i) simulating the infection time series, and (ii) simulating the observed time series by using the delay distribution from infection to death/hospitalisation/case report.

However, we find that the observations simulated this way are too smooth compared to real data (see Figure S17). Possible reasons for this are that the delay distribution does not account for weekend and holiday effects, the random and occasional delay in recording confirmed cases, nor irregular components such as confirmed cases that are imported from abroad. We therefore added a noise term in our simulations, resulting in a third step: (iii) adding noise generated from an ARIMA model.

To obtain a realistic ARIMA model for this third step, we fitted a model based on the confirmed case data for SARS-CoV-2 in Switzerland. Specifically, we first obtained the additive residuals based on the log-transformed confirmed cases. We then fitted ARIMA models of various orders and assessed the resulting ACF and PACF plots of their residuals. Based on this, we chose an ARIMA(2,0,1)(0,1,1) model. We refer to Figure S16 to support this: The first row shows the ACF and PACF plots of the original residuals, showing strong autocorrelation. The second row shows the ACF and PACF plots of the residuals after fitting the ARIMA model. We see that there is little autocorrelation left, indicating that this model is reasonable.

In Figure S17, we present simulated observations based on all three steps, and one can see that they look more realistic than the simulated observations after step (ii).

We would also like to point out that the ARIMA model is only used to obtain simulated observations. Our main method to estimate Re and obtain the related confidence intervals does not require fitting an ARIMA model.

Minor comments:

1) What does near real-time mean? The estimates of Rt are delayed for a few days like other approaches?

Indeed, the estimates of Rt are delayed by the time it takes from infection to a case to be observed. We have replaced the term “near real-time” by “timely” throughout the manuscript, and added this explanation of the delay more explicitly to the text (line 86).

2) For the results in Table 1, I think if there are some results suggesting that other approaches (like EpiEstim) perform worse than the proposed approach, it would be better to illustrate the value of the proposed approach.

We have improved and extended the comparison of our method against others in two ways: (i) we added further comparison of the coverage of our method vs. that of EpiEstim to Fig. S4 (see also the response to major comment 2), and (ii) we added comparison against different commonly used pipelines (see minor comment 3 below). Instead of comparing to other approaches, the analysis in Table 1 was meant to illustrate the use of the Re estimates resulting from our method alone.

3) I think more discussions are needed for the similarity and differences for current approach. For example, Abbott et al (https://wellcomeopenresearch.org/articles/5-112) used a similar pipeline.

We added a section to the results (paragraph starting line 182; Fig. 3), dedicated to comparing our approach with relevant alternatives. We compared some of our empirical results with the estimates published on epiforecasts.io (based on EpiNow2 package from Abbott et al.), as well as official COVID-19 Re estimates for Austria (by AGES) and Germany (by RKI). We find that estimates published by the RKI and AGES health authorities are likely to be overconfident and to suffer from previously-identified biases (notably in Gostic et al., 2020, PLOS Computational Biology). We provide a detailed comparison of the features and approaches of these methods (EpiNow2, AGES, RKI), with the addition of the epidemia R-package (Supp File S2). This comparison highlights the unique features of the method developed: its ability to account for time-varying delay distributions and to combine symptom onset data with case data.

4) Figure S11 is about accounting for known imports. While if the local cases are dominant and hence imported cases would not have a big impact on estimates of Rt. The impact of imported cases on estimates of Rt could be complicated, as suggested in Tsang et al. (https://pubmed.ncbi.nlm.nih.gov/34086944/). In addition to assuming imported cases and 'exported' cases could be canceled, it is also assumed that the imported cases had similar transmissibility to the local cases, which may not be true if there is border control.

We thank the reviewer for this interesting comment and reference. We added a brief discussion in the result section of the manuscript to address this limitation (lines 174-177).

Reviewer #2 (Public Review):

This manuscript describes an algorithm of estimating real time effective reproductive number R_e (t). This algorithm combines several methods in a reasonable way: deconvolution of time series of reported case into time series of infection, a Poisson model for generation of infections, and block-bootstrap of residuals to assess uncertainty. Each component is not necessarily novel, but the performance of this algorithm has been validated using comprehensive simulation studies. The algorithm was applied to COVID-19 surveillance data in selected countries across continents, revealing a great deal of heterogeneity in the association of R_e (t) with nonpharmaceutical interventions. Overall, the conclusions seem reliable.

I have several moderate critiques and suggestions:

1) From a statistical point of view, it seems much more natural to integrate the infection generation process and the delay from infection to reporting, possibly with reporting errors, into the same model, with which you will avoid combining the bootstrap and the credible intervals in a somewhat awkward way. I understand you can take advantage of EpiEstim package, but the likelihood is very simple and easy to program up. Nevertheless, I'm not strongly against the current paradigm.

We agree that such an integrated approach is useful, and makes the uncertainty interval estimation more coherent. However, in such an integrated approach one can not use the analytical solution for the likelihood, and methods that choose this approach (like EpiNow2 and epidemia) tend to pay for it in computational complexity. It also makes it harder to include time-varying delay distributions into the model, one aspect that sets our pipeline apart from existing alternatives.

An additional advantage of our method is that estimates for the infection incidence are not influenced by priors on Re. In case of a bad model fit this allows us to separate more easily which part of the model may be misbehaving; and as such can help as a sanity check.

Lastly, our framework has the advantage of modularity: pieces of the pipeline can be (and were) continuously refined or replaced with better pieces. This continuous improvement process allowed a flexible response to the pressing circumstances (the COVID-19 pandemic), and allowed us to extend it to entirely new types of proxy data (e.g., wastewater viral loads - https://ehp.niehs.nih.gov/doi/10.1289/EHP10050 ).

2) Is there a strong reason to believe the residuals are autocorrelated? The block sampling with block size 10 seems arbitrary. The authors fitted an ARIMA model to the residuals for some countries, how good was the fitting? If the block size doesn't matter, then probably the stronger but simpler assumption of independent residuals may not compromise the estimation of R_e (t) much.

Yes, there is reason to believe the residuals are autocorrelated. New supplementary Figure S15 shows the ACF and PACF of the residuals based on the confirmed cases of Switzerland, China, New Zealand, France and the US, and one can see that for most countries, the obtained residuals are clearly autocorrelated. We added this point to the simulations method section in the paper (lines 503-518). Please also see our response to Reviewer 2, major point 4 above.

Choosing an optimal block size for the block bootstrap method is generally difficult. To capture weekly patterns, we need a block size of at least 7. We tried different sizes and found that 10 tended to work well in a variety of simulation settings (an example is given in Fig. S19).

3) I don't see the necessity of using segmented R_e (t) instead of a smooth curve in the simulation studies. The inferential performance, especially the coverage of the CI's, is much less satisfactory when a segment has a steep slope. The authors may consider constructing splines based on the segments or using basis functions directly.

We started using a segmented Re(t) trajectory to allow for simple parametric generation of different scenarios (e.g. in new Fig. S10), and to specifically study our ability to estimate sudden transitions in Re (discussed wrt. Table 1, Fig. S2). We agree this approach makes our method look worse than necessary, since it is generally difficult to estimate such abrupt changes in Re. However, we thought this would be the more stringent test of our method, as we will perform better on any more smooth trajectory.

4) The authors smoothed the log-transformed observed incidences to come up with the residuals. For Poisson data, a variance-stabilized transformation is taking the square root, not the logarithm. In addition, as you already have bootstrap estimates, why not using quantiles directly for CIs but instead using a normal approximation (asymptotic)? When incidence is low, the normal approximation may be much less satisfactory. Also, when using normal approximation for CI, it's much safer to calculate standard deviation and construct CI at the log-scale, i.e., log(θ ̂^*(t)), and then exponentiate back.

Our goal of transforming the original case observations is to stabilize the variance of the residuals. Indeed, the square root transformation is generally recommended if the data to be transformed is Poisson distributed. In our case, however, the original case observations are not quite Poisson. Specifically, the infection incidence at time t given the past incidence is modelled with a Poisson process (see Section 4.4), but the case observations are modelled with an additional convolution step of the infection incidence with a delay distribution, and there is additional variation due to e.g. weekday effects. It is thus not clear a priory which transformation works best for our data, and we therefore investigated various possible transformations (including the square root transformation). We found that no transformation was uniformly the best for data of different countries, but that the log-transformation tended to perform best overall. This is why we chose the log-transformation. Please see the new supplementary Figure S14, where we show the residuals after the square root transformation and the log transformations for various countries.

Regarding the bootstrap confidence intervals, we also investigated different options. Again it is not clear a priory which bootstrap confidence interval performs best for our data, so we compared common choices like quantile, reversed quantile and normal-based in a simulation study. Specifically, we assessed their coverage and found that the normal-based confidence intervals performed best overall (see Fig. S4).

For low incidence settings, none of the bootstrap methods perform very well (as bootstrap consistency does not apply). We now mention this consideration in the paper (line 442).

Finally, regarding the suggestion to compute exp(SD(log(X)): This quantity is generally different from SD(X), which we need for the confidence intervals. We also refer to the coverage in the various supplementary figures (e.g. S2, S4, S5) to support that our approach works well.

5) The stringency index is a convenient metric for intervention intensity. However, it doesn't reflect actual compliance as the authors admitted. Another likely more pertinent metric is human movement (could be multiple movement indices). Human movement indices may not be available in all countries, but they are available in some, e.g., the US, and first wave in China. In some states of the US, it was clear that human movement decreased substantially even before initiation of lockdown. Lack of human movement metrics most likely has contributed to the difficulty in the interpretation of Figure 4.

We have added mobility data (from Apple and Google location data) to our general dashboard, and to the analysis shown in Fig. 5. The mobility traces give more detailed insight in the behavior that may have led to decreases in Re. However, we find similar patterns wrt. decreases in Re as with the stringency index. A more extensive analysis that focuses on different phases of the pandemic may allow for more detailed insights, but we believe this is beyond the scope of our manuscript.

Author Response

Reviewer #1 (Public Review):

1) The Reviewer writes while the authors use an appropriate Cre line (Wnt1) to delete Elp1, they “need to consider reports that there also are Wnt1-negative neural crest cells residing in the mouse embryonic Vg, i.e., Wnt1-Cre is not expressed in every neural crest cell and therefore there will be neural crest derived cells in the Vg of their embryos in which Elp1 has not been deleted.”

We appreciate the Reviewer pointing this out. Although Wnt1-Cre targets ~96% of Sox10-positive migratory neural crest cells in the trunk (Hari et al., 2012), we acknowledge there is a reported population of neural crest cells in the trigeminal ganglion that is not targeted by Wnt1-Cre (~30% at E9.5-E10, Karpinski et al., 2016). These analyses by Karpinski et al. were undertaken on the embryonic trigeminal ganglion before the major period of neural crest-derived neurogenesis in the trigeminal ganglion (E11-13), which is the time period we are examining. Similar analyses are not easily conducted once neural crest-derived neurogenesis begins, because Sox10 is swiftly downregulated upon neuronal differentiation. Therefore, it remained unclear what proportion of neural crest-derived trigeminal ganglion neurons are Wnt1-Cre-negative at the stages we have examined.

These findings, along with suggestions by the other Reviewers, encouraged us to more rigorously address cellular origins of different trigeminal neuron populations from E10.5-15.5 using an additional mouse model. To this end, we crossed our Wnt1-Cre mouse with a ROSAmT/mG reporter mouse so that we could distinguish neural crest cells and their derivatives (Cre-positive, GFP-positive) from other cell types (Cre-negative, TdTomato (hereafter referred to as RFP)-positive, representing placode-derived cells and potentially other neural crest cell populations) in the trigeminal ganglion. Using this reporter, we found that Wnt1-Cre targets ~92% of Sox10-positive neural crest cells in the trigeminal ganglion at E10.5 (Figure 7). Additionally, we discovered that Six1, previously a marker attributed to the placodal lineage, labels all newly differentiating neurons in the trigeminal ganglion, irrespective of cellular origin (Figures 6 and 7). As development proceeds, it is likely that many of the RFP-positive (Cre-negative), Six1-negative neurons within the trigeminal ganglion were previously Six1-positive placodal neurons that have extinguished Six1, given what we observe with respect to Trk receptor expression. We have now carefully described our findings in the context of these previous studies and their limitations in the Results and Discussion sections.

2) The Reviewer writes “some figures should include high magnification of the cells” to better support the claims, including Figure 1-supplemental, Figure 1P, Figure 7-supplemental, and Figure 8.”

We thank the Reviewer for pointing this out and now provide higher magnification images in these figures as requested.

3) The Reviewer states while “Vg appears to form normally in Elp1 CKO embryos…the language implies that the authorized analyzed neural crest migration, which they did not.” In addition, the Reviewer points out that the authors’ statement that the cells are “appropriately distributed throughout the forming ganglion” is “rather vague with no description of the data that support the conclusion.”

We apologize for this overinterpretation of our data. We have modified the language in the manuscript to address these concerns and clarified that we did not directly analyze neural crest cell migration in this study. We have also removed language referring to cellular distribution within the trigeminal ganglion.

To more rigorously address early trigeminal ganglion formation in the Elp1 CKO, we have now quantified the size of the trigeminal ganglion and length of the ophthalmic and mandibular nerve branches at E10.5 in control and Elp1 CKO embryos and found no statistically significant changes. Additionally, we determined the ratios of undifferentiated neural crest cells and placodal neurons present in the trigeminal ganglion at E10.5 by counting cells in sections through the forming trigeminal ganglion in control or Elp1 CKO embryos after immunohistochemistry for Sox10 (undifferentiated neural crest cells) and Six1 (placodal neurons) or Islet-1 (placodal neurons). These data are now included in the manuscript and reveal no statistically significant difference in these ratios between control or Elp1 CKO embryos (Figure 2).

4) The Reviewer writes “it would be helpful to the reader if the composition of the “control” embryos was explained in the results/figure legends and not just in the methods” and a better description of the “number of litters examined, [whether] the images come from siblings, [and] the variance between litters.”

We apologize for this omission and now provide this information in the Materials and Methods, Results, and Figure Legends. All analyses comparing control and Elp1 CKO embryos included sibling groups from at least two litters. Control versus Elp1 CKO images presented in the manuscript are siblings that underwent simultaneous immunohistochemistry and were imaged/processed under the exact same conditions. All graphs representing statistical comparisons of control versus Elp1 CKO embryos now include individual data points against the mean and SEM to display the variance within each genotype.

5) The Reviewer states “there is virtually no quantitation of phenotypes” and recommends measuring, for example, the central root. Also, it is not clear if “the types and levels of abnormal axon trajectories shown in each figure found in every embryo analyzed.”

We thank the Reviewer for bringing this to our attention. We have now quantified several aspects of trigeminal ganglion and nerve development in Elp1 CKO embryos (or littermate controls). Besides the measurements and ratios described in #3 above, we have quantified, at multiple stages, the central root diameter; size of the innervation field of the infraorbital nerve entering the whisker pad; Trk and TUNEL fluorescence; the number of Six1-positive and Trk-expressing neurons (E10.5-12.5), Sox10-positive and Cre-positive cells (E10.5), Six1-positive and Cre-positive neurons (E10.5, E12.5), and Cre-negative and Trk-expressing neurons (E15.5); and the ratio of Six1 (or Sox10)-positive to DAPI-positive cells (E11.5). The Elp1 CKO phenotype is highly penetrant and we have now clarified the presence of axon trajectory deficits in the text, indicating that all embryos exhibit these phenotypes to some degree. We hope the Reviewer finds these additional measurements to improve the manuscript.

6) The Reviewer writes since “many of the findings for Vg are the same as what was found for trunk sensory ganglia, so impact is rather low. It could be increased significantly if other cranial ganglia were investigated for comparison…the facial nerve has one ganglion that is neural crest derived and one that is placode derived.”

The Reviewer brings up an excellent point. We have now examined aspects of geniculate ganglion development, which is the placode-derived component of the facial nerve and, thus, not targeted for Elp1 deletion. After whole-mount immunohistochemistry for Tubb3 and TUNEL staining on tissue sections, we find no change in Elp1 CKO geniculate ganglion size or length of the chorda tympani nerve (E10.5, Figure 2) and we observe normal axon trajectories in the chorda tympani nerve compared to control embryos (E11.5, Figure 3). Moreover, we do not observe increased TUNEL staining in placode-derived geniculate neurons at E12.5 (Figure 9-figure supplement 1). Interestingly, most geniculate neurons express TrkB during this stage of development (Yamout et al., 2005; Fei and Krimm, 2013; Rios-Pilier and Krimm, 2019). Thus, the sparing of both trigeminal and geniculate placode-derived TrkB neurons in Elp1 CKO nicely aligns.

7) The Reviewer indicates “the description in the text of whether Trk expression segregates with sensory modality and/or with neural crest versus placode origin is missing some references, for example, the apparent specific effect of the 22Q11 deletion on neural crest derived, TrkA+ Vg neurons. As stated above, it also would be useful to discern neural crest derived Vg neurons by a genetic lineage tracer such as Wnt1-GFP.”

We thank the Reviewer for pointing us to relevant references, which we have now added to the revised manuscript, including discussion of our data as they relate to the findings from 22Q11 Deletion mice. The Reviewer raises an important question about the origin of trigeminal ganglion neurons, which we have now addressed by crossing our Wnt1-Cre line with the ROSAmT/mG reporter (see Point #1) and performing additional analyses to delineate the dynamics of normal neurogenesis and nerve growth in the trigeminal ganglion. First, we examined Trk expression from E11-E12.5 (Figure 6-supplement 1) and observed, as shown previously (Huang, Zang, et al., 1999; Huang, Wilkinson, et al., 1999), that TrkB and TrkC neurons predominate in the trigeminal ganglion early (E10.5-11), but then ultimately TrkA neurons become the majority neuronal subpopulation later (E12.5). Next, we co-labeled sections through the forming trigeminal ganglion at E10.5, E11.5, and E12.5 to identify Six1- and Trk-expressing cell populations (Figure 6). In accordance with placodal neurons differentiating first (and expressing Six1), we found that over 75% of any Trk-expressing neuron was also Six1-positive at E10.5. Surprisingly, the majority of Six1-positive cells at E11.5 and E12.5 were TrkA-positive, suggesting Six1 labels newly differentiating neurons. We subsequently confirmed this, and the cellular origin of Trk-expressing neurons, by carrying out section immunohistochemistry on the forming trigeminal ganglion in the Wnt1-Cre; ROSAmT/mG reporter mouse (Figure 7). In keeping with our initial Six1 results, only 12% of Six1-positive cells were GFP-positive at E10.5, confirming previous reports that the majority of the Six1-positive cells are placode-derived at this stage (Karpinski et al., 2016). However, 92% of Six1-expressing cells at E12.5 were GFP-positive, indicative of a neural crest origin for these neurons. Finally, we determined Trk expression at E15.5 (Figure 8) with respect to RFP-expressing (mostly placode-derived) trigeminal neurons and noted that approximately three quarters of the TrkA neurons were RFP-negative (and therefore neural crest-derived). Collectively, these data point to a neural crest origin for most of the TrkA neurons in the trigeminal ganglion, while placode cells give rise to primarily TrkB and TrkC neurons.

Reviewer #2 (Public Review):

1) The Reviewer states “although the authors use TrkA/B/C staining to quantify some of their data, they should have taken advantage of these specific markers in addition to the position identity of neural crest and placode-derived neurons in the ganglia to strengthen their observations of specific knockout of Elp1 in neural crest derived neurons as well as targeting defects…[These] neurons are segregated in the proximal (neural crest) and distal (placode) regions of the ganglion. The authors could also use similar location of neurons in addition to differential expression of TrkA/TrkB to confirm the absence of Elp1 in neural crest-derived neurons as opposed to placode-derived neurons of the CKO mice and to also show that neuron apoptosis occurs in only the [proximal] region of the trigeminal ganglion. Furthermore, the authors could use this differential expression of TrkA and TrkB to show the specific loss of TrkA in the target sites of Elp1 CKO mice.”

We appreciate the point the Reviewer brings up regarding cell position within the trigeminal ganglion, particularly given our own research on chick trigeminal ganglion assembly. In the chick trigeminal ganglion, neurons are segregated by cellular origin such that placode-derived neurons reside in the distal ganglion (relative to the neural tube), while neural crest-derived neurons reside in the proximal ganglion. This pattern does not translate to the mouse trigeminal ganglion, which has been previously described as a mosaic of cellular subtypes with no preferential aggregation of any particular lineage (Karpinski et al., 2016; Motahari et al., 2021). Therefore, anatomical position is an unreliable tool for predicting placodal versus neural crest lineage in the mouse trigeminal ganglion. Our TrkA/B/C immunohistochemistry data, and the distribution of TrkA/TUNEL-double positive cells within Elp1 CKO trigeminal ganglion sections, also support this finding. Because of this, we cannot rely on position as another means to support our results. We have now addressed these differences between chick and mouse in the Discussion.

We have conducted additional section immunohistochemistry experiments in which we have co-stained for different Trks and Elp1 in control and Elp1 CKO embryos (Figure 5, Figure 5-supplement 1 and 2, E12.5). We discovered a statistically significant decrease in TrkA fluorescence intensity in Elp1 CKO versus control trigeminal ganglia, with no change observed for TrkB or TrkC. Additionally, there were fewer TrkA-expressing nerve endings in sections through the upper lip of Elp1 CKO embryos relative to control embryos, with no change observed in TrkC-expressing nerve endings. Remarkably in the Elp1 CKO, most TrkA neurons were devoid of Elp1 protein, while the majority of Elp1-positive neurons expressed TrkB or TrkC. Altogether, these data provide further evidence to support targeting of presumptive neural crest-derived TrkA neurons in the trigeminal ganglion upon Elp1 loss in neural crest cells.

2) The Reviewer writes the “authors state that two litters were examined per experiment, but do not provide the numbers of knockout and wildtype mice used for each experiment. In addition, quantification of the data such as the thickness of the central nerve root between control and Elp1 CKO mice would make the authors’ claim stronger.”

We apologize for the omission of these numbers and have added them to the manuscript. In addition, we have now quantified several aspects of trigeminal ganglion and nerve development (described in detail in Reviewer 1, Point #5 above), as per the recommendations of this Reviewer and Reviewer 1. We thank the Reviewer for this comment, as the new data have strengthened the manuscript. Additionally, the numbers of animals/litters per experiment have been clarified in figure legends, and graphs representing statistical comparisons between control and Elp1 CKO embryos now include individual data points against the mean/SEM to demonstrate the number of embryos examined and the variation within genotypes.

3) The Reviewer asks about “the expression pattern of NGF in the target tissue where the nerve bundles appear to be disformed in Elp1 CKO…[and whether] other neurotrophic factors [are present] in this region.”

The Reviewer brings up an excellent point. To address this, we have performed immunohistochemistry to examine NGF expression and distribution in Elp1 CKO and control littermates at E12.5 (Figure 9-supplement 2). Our data reveal NGF protein in trigeminal nerve target tissues of both control and Elp1 CKO embryos. Importantly, given the role of Elp1 in translation, these findings demonstrate that Elp1 is not altering NGF protein levels. These results are consistent with previously published data showing no difference in the amount of NGF transcripts (Naftelberg et al., 2016; Morini et al., 2021) or protein (George et al., 2013) levels between control and Elp1 CKO. With regards to other neurotrophic factors, BDNF and NT-3, which can serve as ligands for TrkB and TrkC, respectively, are also expressed in the ophthalmic and maxillary regions targeted by the trigeminal nerves (Ernfors et al., 1992; Arumäe et al., 1993; Buchman et al., 1993; O’Conner and Tessier-Lavigne, 1999).

4) Since the authors suggest that “most TrkA neurons do not express Elp1” and Elp1 is “knocked out in [neural crest]-derived neurons,” the Reviewer states “these results would be much stronger if they showed that Elp1 expression is maintained in the placode (TrkB) neurons under these conditions.”

We thank the Reviewer for this suggestion. We now provide data from the Elp1 CKO showing that TrkA neurons are typically devoid of Elp1 protein, while TrkB and TrkC neurons still express Elp1 (Figure 5-supplement 2; see also Point #1 in this section).

5) The Reviewer asks whether “specific targets are innervated by neural crest- or placode-derived neurons” and writes “it would be good to know what happens to placode-derived (TrkB) neurons that should be functioning normally” in Elp1 CKO.

The Reviewer raises an excellent question regarding target tissues innervated by neural crest- vs. placode-derived neurons emanating from branches of the trigeminal ganglion. We are actively pursuing this line of research in my lab but it is currently beyond the scope of this study given the mouse work and time required to rigorously interrogate this question. We have speculated about this in the Discussion as a future direction. As a foray into this, however, we have quantified Trk fluorescence at E12.5 and find no statistically significant difference in TrkB (or TrkC) fluorescence throughout the trigeminal ganglion between control and Elp1 CKO embryos (Figure 5), while TrkA fluorescence is reduced. Additionally, we show that TrkA nerve endings are reduced in sections through the whisker pad of E12.5 Elp1 CKO embryos, but TrkC nerve endings are maintained (Figure 5).

Author Response

Reviewer #1 (Public Review):

Xiong and colleagues use an elegant combination of theory development, simulations, and empirical population genomics to interrogate a largely unexplored phenomenon in speciation/ hybridization genomics: the consequences and implications of admixture between species with differing substitution rates. The work presented in this well-written manuscript is thorough, thought provoking, and represents an important advancement for the field. However, there are a few instances where I feel the strength of the conclusions drawn is not fully supported.

Thank you for the positive comments!

The authors begin by presenting evidence based on whole genome sequencing that the two focal species, P. syfanius and P. maackii, are highly diverged despite ongoing hybridization. Though the discussion of remarkable mitochondrial sequence similarity is underdeveloped. I do not understand how such a pattern is not most likely the result of introgression from one species to the other given the relatively high FST across much of the nuclear genome coupled with the generally higher mitochondrial mutation rate in animals.

That’s a very good point. We have included this likely explanation of mitochondrial genome similarity in Line 84-86.

Next, they posit that barrier loci are likely to exist. To support this assertion, the authors use a combination of parental population genetic diversity and divergence comparisons and ancestry pattern analysis in hybrid populations. They show that there is a strong correlation between divergence across pure species and within species diversity across the autosomes. Then using four hybrid individuals they show that low ancestry randomness, as quantified estimates of between group and within group entropy, is associated with genomic region of reduced within group diversity and elevated between group divergence. The use of entropy estimates as a stand-in for admixture proportions and ancestry block analysis when sample size is severely limited is particularly clever. Though I must admit, I do not fully understand the derivations of the two entropy measures, it seems to me that relatedness might have a strong effect on the interpretability of between individual entropy estimates (Sb). With very small population sizes this may be a real issue.

Yes, genetic relatedness will play a big role in between-individual entropy (Sb). A group of highly correlated individuals will produce highly predictable ancestry (knowing one individual’s local ancestry gives much information on the local ancestries of others), and Sb will be small because entropy is a measure of uncertainty. If inbreeding is very severe, Sb will no longer be a useful measure because it will be too small across the entire genome. In our hybrid samples, although some genomic regions imply the possibility of inbreeding (see local ancestry of Z chromosomes in Figure 3–Figure supplement 1), there is still considerable variation of Sb across the genome which allows us to test for its correlation with DXY and π.

A brief discussion of potential caveats in using the new method developed here seems warranted given its potential usefulness to the population genomics field more broadly. One plausible but less likely alternative interpretation of these patterns is briefly discussed.

We have now devoted the first subsection of Discussion to the caveats and various motivation for entropy metrics. The appendix also contains further explanation of our intuition (section “Appendix-The entropy of ancestry”).

The authors then move on to evidence for divergent substitution rates. Analysis of both D3 and D4 statistics using several different outgroups and a series of progressively stringent FST thresholds shows that site patterns between the two species are highly asymmetrical with P. maackii lineage harboring more substitutions than P. syfanius. The authors offer two possible explanations for this finding and then test both hypotheses. First, they use a comparative tree-based method to show that there is little phylogenetic evidence for lineage biased hybridization from outgroups into either of the focal lineages. Further, the range overlaps of the study species do not correspond with the inferred direction of allele sharing from the Dstat analysis. This is a good argument against contemporary gene flow between the outgroups and P. syfanius, but I am not convinced that ancient gene flow that could have occurred when, say, species distributions may have been different, can be ruled out using this analysis.

Yes, we also felt that our original wording was overly strong. Now we say that our argument is based on current geographic distributions, but that archaic gene flow cannot be totally ruled out. However, we also point out that archaic gene flow with outgroups should still leave some detectable fractions of paraphyletic local gene trees after phylogenetic reconstruction. (Line 192-194).

To test whether this asymmetry can be explained by a difference in substitution rate between the two species the authors show that observed D3 increases and D4 decreases with increasingly divergent outgroups as predicted by theory developed here. The authors take this as evidence supporting the divergent substitution rates. Though they claim only that existence such rate divergence is likely. The unfortunately limited samples sizes seem to preclude attaining more certainty than this. Interestingly, as a byproduct of using D4 as an extended measure of site pattern asymmetry the authors highlight one way in which the ABBA-BABA test can give false positives for introgression. This is an important contribution to the field.

We agree with the reviewer that, for our data type – a handful of unphased genomes, it will be difficult to obtain more direct evidence for substitution rate differences. In line 182-187, we show using maximum-likelihood gene tree reconstruction that P. maackii samples often inherit more derived mutations than P. syfanius. This could be viewed as a separate test utilizing more accurate substitution models in phylogenetic software, while our theoretical calculation provides a coarse but testable signature of D3 and D4.

To provide more direct evidence, we believe one ought to measure spontaneous mutation rates in both species under their native habitats, and obtain better knowledge of generation times and population sizes. The limitation of sampling and rearing these rare species are major barriers for incorporating this kind of evidence into this study.

Finally, the authors observe a monotonic relationship substitution rate ratio and relative genetic divergence across the genome which is in line with their theoretical predictions for differential substitution rates in the face of gene flow. From this they infer an 80% increase in substitution rate from P. syfanius to P. maackii. It is remarkable to be able to extract these substitution rates from genomic regions with the least gene flow. However the veracity of these estimates relies on the assumptions I have highlighted above and should be presented with appropriate caution.

We have included the limitations of our conclusions in the final subsection of the Discussion. Because high FST regions are relatively rare, estimates of observed rate ratio “r” have larger errors in those regions. This problem is partially resolved by using the entire monotonic relationship between r and FST to estimate the true rate ratio, so we rely not only on regions with the least gene flow but the full dataset.

However, we do agree with the reviewer that ours is still a coarse theoretical framework since we do not impose a realistic substitution model (e.g., we don’t allow reverse mutations). We have now emphasized this weakness in the Discussion (Line 348-350).

Reviewer #2 (Public Review):

In their manuscript ("Admixture of evolutionary rates across a hybrid zone"), Xiong et al. use whole genome resequencing data to assess rates of genome evolution between two species of butterflies and determine whether putative barrier loci between the species are also those that evolve at asymmetric rates between them. This work presents a novel hypothesis and rigorously tests these ideas using a combination of empirical and theoretical work. I think the authors could more formally link loci that are evolving at highly asymmetric rates with those that are most likely to be barrier loci by evaluating the relationship between ancestry entropy and ratios of substitution rates between species. Additionally, clarifying the relationship between barrier loci and asymmetric evolution would be beneficial (i.e. are loci that we typically envision to be barrier loci, such as loci involved in reproductive isolation, evolving at asymmetric rates or do asymmetrically evolving loci represent a new type of barrier loci?).

Many thanks for these comments! For the second point (clarifying the relationship between barrier loci and asymmetric evolution), we specifically mean that barrier loci (which specifically are of interest to those who study speciation) cause asymmetric rates of evolution to be preserved between hybridizing species. Asymmetric rates themselves are caused by other factors (spontaneous mutation rate differences, generation times, environmental effects) specific to each species, and barrier loci merely prevent the mixing of asymmetric rates. For the first point (evaluating the relationship between entropy and ratios of substitution rates).

Author Response

Reviewer #1 (Public Review):

The authors use available structural biology data to compute the energetic cost to build and maintain the activity of flagella in a broad range of unicellular swimming organisms, including bacteria, archaea and eukaryotes. From this energy balance, they try to decipher what advantages the different types of flagellum can provide in terms of motility, feeding and growth. This eventually brings new insights into why bacteria, archaea and eukaryotes have evolved with different types of flagella.

Strengths:

The main strength of this study relies on the collection of the data set from three types of unicellular swimming organisms - bacteria, archaea and eukaryotes - for about 200 species. Interestingly, selected species span a large phase space in terms of numbers of flagella/cilia, flagellum length, cell volume... This allows robust analysis and interpretation of the data.

The method for establishing the energy balance of the construction of complex protein structures seems to be robust. For example, the result obtained by this method to compute the energy cost of E. Coli flagellum is of the same order of magnitude as previously reported values estimated by other methods. This method could be used for other cellular functions for which it is otherwise difficult to estimate the energy cost either experimentally or theoretically.

Weaknesses:

The conclusion on the lack of an evolutionary advantage for small cells to swim to find food rather than waiting for food to diffuse is not particularly new. Indeed, Purcell in his famous 1977 paper "life at low Reynolds number" reached the same conclusion by using simple scaling arguments to estimate the trade-off between swimming to find more food and the swimming energy cost.

We are aware of the result by Purcell, but his estimate of swimming cost only included operating costs of the flagellum, not construction costs. Purcell also didn’t calculate the relative cost of swimming or compare this cost to gains in fitness. We include estimates of both the operating and the construction cost (relative to the whole cell budget), which constitutes a fitness penalty, and compared this to a fitness gain, i.e. an increased growth rate, from swimming in a homogenous environment (Fig. 2F). We made this comparison for many different species (using empirically derived swimming speeds and flagellar costs) and were able to obtain a volume at which swimming in a homogenous environment does yield a net fitness benefit (increased growth rate). Purcell only looked at E coli.

In the “Flagellar costs and benefits” section, we explicitly contrast our method with what had been done before (citing Wan et al., Phil. Trans. R. Soc. B 2021) and indicate the improvements that we made (i.e. adding construction cost and calculating a net fitness effect).

We have now added the Purcell 1977 paper as a reference.

Although the method does have strengths in principle, the weakness of the paper is that the main conclusions are not discussed enough or put in perspective with regards to the initial aims of the paper: better understand why three different types of flagellum exist. In particular, the fact that "there is no detectable difference in the cost-effectiveness of generating swimming speed between eukaryotic and prokaryotic flagella" is not really discussed. One of the major characteristics of eukaryotes is that they have evolved into more complex multicellular forms of life where multiciliated cells are ubiquitous and support more diverse physiological functions (transport, washing surface...) than swimming. So maybe an evolutionary advantage of eukaryotic flagella over prokaryotic flagella should be discussed in that context.

We do apply our findings to the problem of the different types of flagella in the section “Evolution of the eukaryotic flagellum”, where, among other things, we discuss the possible consequences of the bacterial and eukaryotic cell sizes and the disparate flagellar mechanisms (especially the different flagellar sizes) for the distribution of flagellar types across the tree of life. We did indeed not discuss differences in abilities between eukaryotic and bacterial flagella aside from the ability to generate speed. The eukaryotic flagellum may, by virtue of its distribution of motor proteins throughout its length, be able to generate beats that the bacterial flagellum is not capable of, potentially giving the eukaryote enhanced agility (ability to turn). We did not include these considerations because we are unaware of systematic data on agility that would allow us to compare the capacities of bacterial and eukaryotic flagella. Also, the investment in a single eukaryotic flagellum could pay for multiple prokaryotic flagella, which together may provide the same level of agility as a single eukaryotic flagellum.

We feel that the functions of eukaryotic flagella in multicellular species, although interesting in and of themselves, don’t bear on the issue of the evolution of the eukaryotic flagellum, as this flagellum was long established before the multicellular species arose. It is also not clear whether the eukaryotic flagellum would do a better job than the prokaryotic flagellum in various multicellular tasks.

We have added some of these considerations to the discussion.

Author Response

Reviewer #1 (Public Review):

Major points:

1) The "collateral" fitness effects of mutations on proteins, i.e. those which change overall fitness by means other than directly altering the specific function, are also important sources of abundance changes in DMS experiments [https://www.pnas.org/doi/10.1073/pnas.1918680117]. In this instance, given that expression of Mpro is toxic at high levels, it seems plausible that the fluorescence-based fitness measurements could be influenced by these effects. In these experiments, libraries are first grown for many generations, and in some instances are also expanded after selection before sequencing. The experimental design of the FACS experiments limits the impact of these collateral effects, but these may significantly shape the pre-selection library abundances. Given that the competitive growth experiment involves a T=0 sequencing sample, would it be possible to analyze this pre-selection variant distribution for potential bias?

To analyze enrichment/depletion of variants pre-selection, we compared each variant count in the plasmid library to that of the t=0 sample (immediately prior to induction of Mpro expression). Sequencing counts of the plasmid library correlate with counts in the t=0 sample indicating minimal selection before the induction of Mpro expression. Variants at low frequency showed a wider variance consistent with lower sampling. We added panels f and g to Figure 1- figure supplement 1 and the following text to the results section: “Variant counts analyzed by sequencing before and after the pre-selection amplification step were correlated, consistent with minimal to no selection prior to induction with β-estradiol (Figure 1 – figure supplement 1f and Figure 1 – figure supplement 1g).”

2) The comparisons with the clinically observed mutants are impressive. They note that "only nine having a score below that of the WT distribution". Are these seen with other mutations? As the authors note, their study is confined to single-site mutations and does not directly consider epistatic effects. Are there potential second-site mutations that could explain these 9 outliers?

Of the clinical isolated sequenced to date, fewer than 0.4% have more than one mutation in the Mpro gene. We therefore did not take epistatic effects into account when performing this analysis.

The following has been added to the text: “The vast majority of the clinical isolates that have been sequenced to date have either 0 or 1 Mpro mutations with fewer than 0.4% having 2 or greater mutations and thus we did not account for epistasis in our analysis.”

3) We have some additional questions about the data analysis. In all three experiments, variant proportions are mapped to [0,1], where average stop codon proportions are set as 0 and WT codons as 1. The use of this mapping should not influence the results, but it obscures the overall power. That is, the magnitudes of the changes in abundance underlying, e.g., an apparent loss of function mutation are unclear. The details of the unnormalized abundance changes should be included to improve reproducibility as well as interpretability. We also wonder whether the growth experiments should be fit to selection coefficients as well as normalized fitness scores.

The raw counts, unnormalized scores and normalized scores are reported for each screen in Figure 2 – source data 1. Additionally, the growth experiments have been fit to selection coefficients (slope of log2(variant counts/WT counts) and these are also reported in Figure 2 – source data 1. For the growth screen we chose to report the functional score as opposed to the selection coefficients in the paper so they would be directly comparable to the TF and FRET functional scores.

The following was added to the Materials and Methods: “The functional scores were normalized setting the score for the average WT Mpro barcode as 1 and the average stop codon as 0. Both the unnormalized and normalized scores are reported in Figure 2 – source data 1. For comparison, the counts for the growth-based screen were fit to selection coefficients (slope of log2(variant/WT counts)). We chose to report the functional scores as opposed to the selection coefficients in this paper so they would be directly comparable to the TF and FRET functional scores.”

4) Finally, we would request that the analysis scripts be made available. Given the current lack of standardization for DMS experiments and the difficulty with these types of analysis, this is both necessary for reproducibility and as a benefit for the community.

All custom analysis scripts have been deposited at https://github.com/JuliaFlynn. This information has been added to the Key Resource Table.

Autho Response

Reviewer #1 (Public Review):

Here the authors aimed to gain insight into the role of Septin-7 in skeletal muscle biology using a novel and powerful mouse model of inducible muscle specific septin-7 deletion. They combine this with CRISPR/Cas9 and shRNA mediated manipulation of Septin-7 in C2C12 cells in vitro to explore its role in muscle progenitor morphology and proliferation. There are a variety of interesting observations, with clear phenotypes induced by the Septin-7 manipulation, including effects on body weight, muscle force production, mitochondrial morphology, and cell proliferation. However each area is somewhat superficially examined, and certain conclusions require additional validation for robust support. Additionally, mechanistic insight into Septin 7's role is limited. Therefore, while the phenotypes are likely of intrigue to both the muscle and septin community, to significantly advance the field will require additional experimentation.

Specifically, it is currently difficult to distinguish between developmental and adult roles of Septin-7. The authors induce tamoxifen-mediated deletion at 1 month of age and examine muscle structure/function only at 4 months. By not studying early time points, it is difficult to determine whether particular phenotypes are directly due to Septin deletion or a secondary consequence of muscle atrophy and/or a decline in body weight. Further, by not inducing deletion at a later time point (i.e. after 2 months when muscle is generally matured), it is difficult to assess whether septin-7 plays a role in maintaining structure and function of mature muscle, or if its primary role is in muscle development.

We have conducted a number of trials for knocking-down of Septin-7 expression. These included Tamoxifen treatment of Cre- pregnant mothers, shorter treatments starting at early after birth, and treatments of adult animals. While the former led to still-born offsprings, the later resulted in only a minor – less than 20% - reduction of Septin-7 expression. These long trials led us to, on the one hand, concentrate on the protocol used throughout the manuscript (where a significant, up to 50%, reduction in the expression of the protein could be achieved) and to, on the other hand, focus also on myogenic cells in culture. This selection was also substantiated by the finding that Septin-7 expression is the highest in neonatal muscles and declines with age until adulthood (but remains essentially constant until an age of 18 months for the mice examined). As an identical Tamoxifen treatment of littermate Cre- mice did not result in any of the presented alterations (as demonstrated in the Supplementary material) we can conclude that they are the consequence of Septin-7 down-regulation. We, nonetheless, completely agree with the Reviewer that some observations are most likely indirect, i.e., are due to the loss of muscle mass. These include, e.g., the altered shape of the vertebra and the consequent “hunchback” phenotype. However, this observation further supports our claim that Septin-7 is essential for proper development of a normal musculature in these animals.

Further, the conclusion that septin-7 has an essential role in regeneration (seemingly based on expression increasing after injury) is unsupported and requires further experimentation where injury and regeneration is triggered in the absence of Septin-7 to establish a causative role.

We agree with the Reviewer that a clear causative role of Septin-7 in muscle regeneration would require a substantial amount of further experimentation on Septin-7 knock-down animals. We, however, believe that this – detailed description of the changes in transcription factors and key regulatory proteins together with changes in morphology in Septin-7 KD animals following muscle injury – is beyond the scope of the present manuscript and should be presented as a separate study. In this manuscript, however, we provide the essential background to substantiate this claim. We describe that fusion of myogenic cells is severely hindered if Septin-7 expression is suppressed while Septin-7 is upregulated following muscle injury to the extent which is significantly more than what would be expected if it would be simply due to the production of new muscle fibers.

Finally, there are intriguing observations in mitochondrial and myofiber organization and mitochondrial content; however further interrogation into additional relevant metrics of each, and at different time points of Septin-7 deletion, are needed to better understand these phenotypes and gain insight into Septin-7's role in their regulation.

Accepting the concern of the Reviewer we have conducted additional experiments to enable the proper characterization of the morphology. Additional relevant metrics – Aspect Ratios and Form Factors – have been calculated and are now incorporated into the revised MS and are presented in Figure 5.

Reviewer #2 (Public Review):

This is a comprehensive work describing for the first time the location and importance of the cytoskeletal protein Septin-7 in skeletal muscle. The authors, using a Septin-7 conditional knockdown mouse model, the C2C12 cell line, and enzymatically isolated adult muscle fibers, explore the normal location of this protein in muscle fibers, the morphological alterations in conditioned knockdown conditions, the developmental alterations, and the functional alterations in terms of force production. The global picture that emerges shows Septin-7 as a fundamental brick in both muscle construction, development, and regeneration; all this leads to reinforcing the basically structural nature of this protein role.

We thank the Reviewer for the appreciative words. We indeed believe that Septin-7 plays and important role in the proper organization and development of skeletal muscle. Even a partial knock-down of the protein at the early stages of life results in a severe loss in muscle mass accompanied by skeletal deformities. A complete knock-out of the protein results, at the myoblast level, in the inability of the cells to proliferate and form multinucleated cells confirming the essential role of this structural protein.

Reviewer #3 (Public Review):

This is an original study to explore the role of Septin-7, a cytoskeleton protein, in skeletal muscle physiology. The authors produced a unique mouse model with Septin-7 conditional knockdown specifically in skeletal muscle, which allowed them to examine the structure and function changes of skeletal muscle in response to the reduced protein expression level of Septin-7 in vivo and ex vivo at different development stages without the influence of other body parts with reduced Septin-7 expression. The study on the cellular model, C2C12 myoblast/myotubes with knockdown of Septin-7 expression, provided additional evidence of the importance of this cytoskeleton protein in regulating myoblast proliferation and differentiation. Majority of the data are supportive of the the major claim in this manuscript. However, additional key experiments and data analysis are needed to provide more mechanistic characterization of Septin-7 in muscle physiology.

We would like to express our thanks to the Reviewer for the critical comments on our manuscript and for the valuable suggestions that help substantiate our claim, that Septin-7 is an essential part of the cytoskeletal network in skeletal muscle and plays an important role in muscle differentiation as well as in myoblast proliferation and fusion.

A number of additional experiments were carried out to answer the comments/concerns of the Reviewer. Immunostaining of critical proteins (actin, myosin, and the L-type calcium channel) are now presented in Figure S4 for Cre+ animals. The T-tubules of enzymatically isolated fibers from these Septin-7 knock-down mice were also stained using Di-8-ANEPPS and the corresponding images are presented below. We describe how different Tamoxifen treatments at different time-points in the intra- and extra-uterine life of the animals resulted in the deletion of the SEPTIN 7 gene which ultimately led us to use the protocol (largest reduction with still viable mice) described in this manuscript. A more detailed description on how the fusion index, a clear marker a myotube differentiation, was conducted using desmin staining is now included and additional experiments (immunostaining and western blot) with MYH as suggested by the Reviewer are also presented. We carried out a thorough analysis of mitochondrial morphology (in line with the requirements of another Reviewer) and modified the corresponding figure in the revised MS accordingly.

Major Concerns:

1) The Septin-7 knockdown mouse model, the EM and IHC techniques are all established in the research group. It is a surprise to see that authors missed the opportunity to characterize the morphological changes in the T-tubule network, triad structure, the distribution of Ca release units (i.e., IHC of DHPR and RyR), and its co-localization with other key cytoskeletal proteins (i.e. actin) etc., in the muscle section or isolated muscle fibers.

We appreciate the reviewer's valuable critical comments. Even if we were not able to fully comply with all the requests, we corrected as many of the mentioned shortcomings as possible, by correcting the errors and to prove our claims with further experiments. Please find our responses to each critical remark below.

We conducted IHC staining on individual FDB fibers of C57Bl/6 mice presenting the distribution of skeletal muscle specific α-actinin, and RyR1 alongside with Septin-7 proteins (Figure 1E and F). As demonstrated in Figure 5E and F of the original MS (Figure 5 F and G in the revised version) normal triad structures were present both in Cre- and Cre+ muscle samples using EM analysis. However, the sarcomeres were distorted at places where large mitochondria appeared in Cre+ samples.

As suggested, T-tubule staining by Di-8-ANEPPS was carried out on isolated FDB fibers from Cre- and Cre+ animals, which revealed no considerable differences between the two groups.

Images present the T-tubule system of a single muscle fibers isolated from Cre- and Cre+ FDB muscle. Di-8-ANEPPS staining reveals no considerable difference between the two type of animals suggesting that the reduced Septin-7 expression does not alter the T-tubular system of skeletal muscle cells.

To further investigate the key components of muscle contraction and EC coupling, we carried out immunostaining in isolated single fibers from FDB muscle originating from Cre+ and Cre- mice. Immunocytochemistry revealed no significant alteration of actin, myosin 4, and L-type calcium channel labeling comparing the two mouse strains (see Figure S4 in the revised version).

2) The authors only studied one time point following the Tamoxifen treatment (4-month old with 3-month treatment). Based on Fig 2D, a significant body weight reduction was achieved after one month of the Tamoxifen treatment (at the age of 7 weeks), indicating a potential reduced muscle development at this age. Mice are considered fully matured at the age of 2 months. It will be more informative if the muscle samples and the in vivo and in vitro muscle activity are analyzed at this time point (7 or 8-week old), which should provide a direct answer if the knockdown of Septin-7 affects the muscle development. Additionally, a time dependent correlation of the level of Septin-7 knockdown with muscle function/morphology analysis should better define the role of Septin-7 in muscle development and function.

We agree with the Reviewer that Septin-7 has presumably more pronounced effect in the early stage of muscle development, since we detected higher expression level of the protein in muscle samples isolated from newborn and young as compared with adult animals. We conducted preliminarily in vivo and in vitro force experiments on 2-month-old mice after 1 month of Tamoxifen treatment. The grip force already decreased significantly in Cre+ mice but the decrease in twitch and tetanic force of EDL and Sol did not reach significance. These experiments were followed by the analysis of Septin-7 level in the muscle samples which showed less than 20% of reduction on average in the samples of Cre+ mice. This suggested that a more robust suppression of Septin-7 is needed to reach significant reduction in in vitro force thus we decided to extend the Tamoxifen treatment to 3 months.

3) Although the expression level of Septin-7 reduced during muscle development (Fig 1C), but its expression is still evident at the age of 4 months (Fig 1C and Fig S1F), indicating a potential role of Septin-7 in maintaining normal muscle function. It is important to examine whether the Tomaxifen treatment started after the muscle maturation at the age of 2-month old would affect the muscle structure and function. Particularly, these type of KD mice will be critical to answer if the KD will affect the regeneration rate following the muscle injury. The outcome will further test or support their claim of the essential roles of Septin-7 in muscle regeneration.

We agree with the Reviewer opinion that Septin-7 presumably plays an essential role not only during the early development of skeletal muscle but also in the matured tissue. In our preliminary studies Septin-7 protein expression was determined in skeletal muscle samples from mice at different developmental stage. As presented in Figure 1C we observed decrease in Septin-7 protein expression from newborn to adult stages. The expression profile of Septin-7 was also investigated in samples from 2, 4, 6, 9, and 18-month-old mice and a significant decrease was observed in samples isolated from mice of 4, 6, 9, and 18 months of age (58±8; 48±9; 66±16; 54±9% relative to the 2-month-old muscles, respectively), however there were no considerable changes between samples after 4 months of age.

In order to generate skeletal muscle specific, conditional Septin-7 knock-down animals, we applied Tamoxifen treatment at different developmental stages in our preliminary studies (see the table and figures below). When Cre- pregnant females were fed with Tamoxifen in the third trimester of pregnancy, it caused intrauterin lethality independent of the genotype. According to the animal ethics requirements we did not continue this experimental protocol. In the next stage of our initial experiments, 3 month-old mice were treated with both intraperitoneal injections for 5 consecutive days or Tamoxifen diet for 4 weeks. Here, only a moderate deletion of the exon4 was detected in SEPTIN 7 gene in Cre+ animals (data obtained from these mice are shown below).

These findings and the observation of ontogenesis dependent expression of Septin-7 indicated its significance at the early stage of development and suggested that we should try to modify the gene expression at earlier age. Six weeks of diet supplemented with Tamoxifen generated well detectable exon deletion in younger (1-month-old) mice. Regarding these observations we decided to start the Tamoxifen-supplemented diet in younger (4-week-old) animals immediately after separation from the mother and we continued the treatment for a longer period (3 months) to be sure that exon deletion will be prominent in all Cre+ animals.

Genetic modification of SEPTIN 7 gene following Tamoxifen treatment in mice mentioned above. RT-PCR

Figure presents the presence of floxed sites at SEPTIN 7 gene (white arrow) and the deletion of exon4 (red arrows) in the appropriate DNA samples isolated from mice treated with Tamoxifen from different age and using different methods and period of Tamoxifen application. Exon4 deletions were less than 20%, therefore these trials were not continued. Numbers above each lane correspond to the animal ID-s presented in the table above. Q – m. quadriceps, B- m. biceps femoris, P – m. pectoralis.

The knock-down of Septin-7 in the adult animals (where its expression is already low; see above) did not result in an appreciable further reduction. This led us to conclude that the role of Septin-7 is most pronounced in muscle development. In this framework, at the adult stage a possible function of Septin-7 in muscle regeneration following injury could be envisioned. This is demonstrated in Fiure 6 where we present that Septin-7 is upregulated following a mild injury. However, we believe, that a detailed examination of the role of Septin-7 in the regeneration is beyond the scope of the current manuscript and should be the basis of further studies.

4) Regarding the impact of Septin-7 on differentiation, it could be problematic if the images with the resolution shown in Figure S4A-C were used for fusion index calculation. If those are just zoomed in representative images and the authors used other lower resolution, global view images for quantification, those images are needed to be shown. The authors may also need to elaborate on why they stained Desmin instead of MYH for quantification of the fusion index of myotubes (page 27). Desmin also marks mesenchymal cells.

We apologize that the method used for fusion index calculation was not clear enough. Images in Figure S4A-C present the Septin-7 and actin cytoskeletal structure in proliferating myoblasts, before the induction of differentiation. Fusion index was determined in cultures where myotube differentiation was induced by reduced serum content (as described in Methods). We used desmin staining as the expression of this protein is present only in myotubes with 2 or more nuclei, where fusion of myoblasts has already started (see representative images below). Representative desmin-labeling images from control, scrambled and KD cultures are now included in Figure S5G at 5 days differentiated stage.

Figure presents two examples (bottom row is now added to Figure S5 as panel G) of the desmin-specific immunostaining used for the calculation of fusion index in the different C2C12 cultures. Specific signals of desmin are present following the fusion of single nuclei myoblast into myotubes (green), while non-differentiated myoblasts did not show immunolabeling for desmin. Nuclei are stained with DAPI (blue).

If Septin-7 is truly affecting differentiation, a decrease of MYH 2 expression can be readily detected by IHC or WB.

We are grateful for the Reviewer´s suggestion. We have conducted immunocytochemistry and WB experiments in proliferating myoblasts and myotubes at day 5 of differentiation. As the figure below demonstrates, myosin heavy chain-specific immunolabeling could be detected only in differentiated samples, while myoblasts did not show positive signal. However, there is a significantly lower number of MYH2-positive myotubes in Septin-7 KD cultures as compared with the control and scrambled samples. In addition, we detected decreased WB signal for MYH2 in Septin-7 KD protein samples compared with their control counterparts.

Figure presents the MYH2-specific immunostaining in the different C2C12 cultures. Specific signals of myosin heavy chain 2 (green) are present during myotube formation of differentiating cultures, however, less MYH2-positive myotubes are present in the Septin-7 KD cultures as a result of reduced capability of cells to fuse, here the DAPI-stained nuclei were only present. Proliferating myoblasts did not show specific immunolabeling for MYH2, as the confocal image and the appropriate part of the WB membranes show. We could also detect a decreased MYH2-specific labeling in Septin-7 KD samples as compared with the control ones using WB.

Additionally, Septin-7 may also affect the migration or fusion of myoblasts instead of differentiation. The observation of altered cell morphology and filopodia/lamellipodia formation (Figure 3C) in Septin7-KD cells before differentiation also implies a potential role of Septin-7 in migration. This possibility should be at least discussed.

We appreciate the Reviewer´s comment and suggestion. There are a few publication showing that alteration of septin (in some cases Septin-7) expression modifies the migration of different eukaryotic cell types, like in microvascular endothelial cells (PMID: 24451259), in human epithelial cells (PMID: 31905721), in neural crest cells (PMID: 2881782), and in human breast cancer or lung cancer cells (PMID: 27557506, 31558699, and 32516969). In the work of Li et al. (PMID:32382971) their findings revealed that miR-127-3p regulates myoblast proliferation by targeting Septin-7. In the present manuscript we described that Septin-7 modification alters myoblast fusion (Figure 3J), which is the accompanying phenomenon of differentiation. On the other hand, the effect of Septin-7 gene silencing on cell migration has been studied in detail and was presented to The Biophysical Society. The results are intended to be submitted as a separate manuscript.

5) The image shown in Figure 5F does not support the pooled data showed in Figure 5C. The size of mitochondria is remarkably lager in Cre+ muscle (Fig 5E and 5F). The morphology of mitochondria in Cre+ muscle are apparently normal (Fig 5F), while the mitochondrial DNA content are drastically reduced (Figure 5H), which is an important discovery and deserved to be further confirmed by WB and/or qPCR for critical mitochondrial proteins (i.e. MTCOX, COXV, etc.).

We thank the Reviewer for pointing out that the interpretation of images in Figure 5 was not clear enough. Based on this, and the on the clear request from the other Reviewer, a detailed evaluation of mitochondrial morphology was carried out and the panels of Figure 5 were redrawn and reorganized. The revised Figure 5 now presents the average Perimeter, the average Aspect Ratio, and the average Form Factor (panels C & H, for cross- & horizontal-sections, respectively), the relative distributions of the areas (panels D & I, for cross- & horizontal-sections, respectively), and the number of mitochondria normalized to fiber area (panel E, cross-sections). The mitochondrial DNA content is presented in panel J. As evidenced from these figures (and from the representative EM micro graphs), larger mitochondria, sometimes in large associations, are present in the muscles of Cre+ animals.

Furthermore, gene expression of four essential mitochondrial proteins cytochrome oxidase 1 (COX1), cytochrome oxidase 2 (COX2), succinate dehydrogenase (SDH), and ATP synthase) were determined in RNA samples from different skeletal muscles of Cre- and Cre+ animals using qPCR. As the figure below demonstrates there was a tendency of decreased expression of the aforementioned genes in Cre+ muscle samples, however, significant difference between the Cre- and Cre+ data could not be detected.

Figure represents the normalized mRNA expression of ATP synthase, SDH, COX1, and COX2 in Cre- (green) and Cre+ (red) samples isolated from m. quadriceps and m. pectoralis. Each gene expression was determined from 3 individual animals and a technical duplicate was used during the qPCR analysis. 36B4 gene encoding an acidic ribosomal phosphoprotein P0 was used as a normalizing gene.

6) Figure 2 H & I: It is unclear whether the muscle force was normalized to the individual muscle weight.

We are sorry about the incomplete representation and explanation of muscle force values. Figure 2F-I presents absolute force values without normalization to the cross sectional area. In order to answer the Reviewer´s comment the averages of normalized values are given in Table S3 in the modified manuscript.

7) The IHC results in Figure 6B are confusing. There are no centrally located nuclei in the Pax7 alone image of Figure 6B but abundant in the Pax7 + H&E image. The brown color of DAB and the purple color of hematoxylin are hard to be distinguished.

Images presenting the labeling of Pax7 (a transcription factor expressed in activated satellite cells) alone could not show centrally located nuclei, as the nuclei could only be visible when HE staining is applied. As the Reviewer mentioned brown color of DAB and the purple color of hematoxylin are sometimes difficult to distinguish, therefore, we first presented PAX7 expression visualized by DAB staining (localization was near the sarcolemma). In the next step we performed a double staining for PAX7 and HE to show both the cytoplasm and nuclei.

Author Response

Reviewer #1 (Public Review):

Redman and colleagues employed microprisms and two-photon optical imaging to track separately the structure of dorsal CA1 pyramidal neurons or the activity patterns of dorsal Dentate Gyrus, CA3, CA2 and CA1 pyramidal neurons, longitudinally in live mice. First, they carried out a characterization of the optical properties of their system. Second, they performed an example tracking of dendritic spines in the apical aspect of dorsal CA1 pyramidal neurons. Finally, they characterized differences in spatial coding along the tri-synaptic pathway, in the same animals. The main focus of the manuscript is technological and the authors show interesting data to support their technique, which I believe will be of relevance to neuroscientists interested in the hippocampal formation.

Strengths.

While using microprisms to achieve a "side" view of neurons in specific brain areas is not new per se [see Chia et al., J. Neurophysiol. (2009), Andermann et al., Neuron (2013), Low et al., PNAS (2014) etc.] the authors were able to visualize activity of a large neuronal circuit such as the hippocampal trisynaptic pathway - for the first time - in the same animal exploring an environment. This is not only a technical feat but it opens new scientific avenues to study how information is transformed at different stages within the hippocampus, as such I think this will be of broad interest for people in the field. In addition, the authors demonstrated imaging of dendritic spines in the apical aspect of pyramidal neurons but limited to dorsal CA1 due to the labelling density of the transgenic mouse line they decided to use. Despite the fact that imaging apical dendritic spines in dorsal CA1 has been shown earlier [see Schmid et al., Neuron (2016) and Ulivi et al., JoVE (2019)], the use of the micro periscope greatly increases the flexibility of these sort of experiments by enabling tracking of large portion (both apically and basally) of the dendritic arbors of dorsal CA1 pyramidal neurons.

Thank you for the positive comments. We have clarified that apical CA1 dendrites have been imaged in previous work as you point out, just not along the somatodendritic axis (lines 127-130). We have also clarified that we were able to image CA2 and CA3 spines as well (only DG exhibited the increased labeling density in Thy1-GFP-M mice; lines 130-132).

Weaknesses.

While the data are sufficient to demonstrate the technique, the conceptual advance of the paper is very narrow. The findings on spatial coding differences in different hippocampal subregions - namely a nonuniform distribution of spatial information in the different hippocampal subregions - do not add new knowledge but largely confirm the literature. The results on the dynamics of apical dendritic spines of pyramidal neurons in dorsal CA1 seem to confirm previous work, but the interpretation of these results differs fundamentally. In fact both papers cited by the authors (Attardo et al., and Pfeiffer et al.,) come to the conclusion that dendritic spines on basal dendrites of CA1 pyramidal neurons are highly unstable, at least by comparison to other neocortical areas. The authors seem to ignore this discrepancy. However, this discrepancy has importance also to the characterization of the technique the authors developed. In fact, the optical resolution of the system strongly affects the ability to resolve neighboring spines - especially at the high density of dorsal CA1 - and thus it has a direct effect on the measures of synaptic stability [Attardo et al., Nature, (2015)]. The authors duly report lateral and axial resolutions for their micro periscopes and both are lower than the ones of Attardo and Pfeiffer, thus the authors should consider the effects of this difference on the interpretation of their data.

We agree that the advance described in this manuscript is more methodological than conceptual. We do have other studies in progress that will be of greater conceptual interest. However, we believe the technique is of sufficient interest to the field that it is worth publishing the methodological approach and characterization as soon as possible.

We have also addressed the comparison with Attardo et al. and Pfeiffer et al. mentioned by the reviewer. We actually agree with the previous work that dendritic spines in CA1 show a high degree of instability compared to cortex, finding ~15% spine addition and ~13% spine subtraction between consecutive days (Fig. 3H, I), similar to single-day turnover rates observed in Attardo et al. and other papers. Despite the high turnover rate, the fraction of experimentally observed spines that persist across 8-10 days plateaus around 75-80%, indicating that there is a substantial fraction of apical spines that remain stable in the face of ongoing daily turnover. This was also observed in basal dendrites by Attardo et al. (with similar survival fractions) and Pfeiffer et al. (albeit with lower survival fractions), so we would not necessarily characterize this as a discrepancy. We have clarified these points in the manuscript (lines 157, 162-168, 331-332).

The reviewer pointed out that some previous studies used super-resolution microscopy to detect smaller structures and reduce optical merging. This would be an excellent extension of our work, as in principle super-resolution microscopy could be used with the implanted microperiscopes. Although the survival fractions we observed were similar to Attardo et al., they were higher than Pfeiffer et al., possibly due to the predicted effects of optical merging. We have updated the text to note that our results may inflate the degree of stability due to resolution limitations (lines 165-68, 335-340).

Reviewer #2 (Public Review):

Strengths

The Hippocampus is a key brain region for episodic and spatial memory. The major Hippocampal subregions: Dentate Gyrus (DG), CA3, and CA1 have predominantly been investigated independently due to technical limitations that only allow one subregion to be recorded from at a time. In this paper the authors developed a new method that allows DG, CA3, and CA1 to be imaged simultaneously in the same mouse during behavior with a 2-photon microscope. This method will allow investigation of the interactions between Hippocampal subregions during memory processes - a critical yet unexplored area of Hippocampal research. This method therefore provides a new tool that will help provide insight into the complex functions of the Hippocampus during behavior.

This method also provides high resolution optical access to deep dendritic structures that have been out of reach with existing methods. The authors demonstrate they can measure the structure of single spines on distal apical dendrites of CA1 cells. They track populations of spines and quantify spine changes, spines loss, and spine appearance. Spine turnover is thought to be a key process in how the Hippocampus encodes and consolidates memories, and this method provides a means to quantify spine dynamics over very long time periods (months) and can be used to study spine dynamics in CA3 and DG.

We appreciate the comments.

Weaknesses

This method requires the implantation of a relatively large glass microperiscope that cuts through part of the Septal end of the Hippocampus. This is a necessary step to image transversally and observe all the major subregions simultaneously. This is an unfortunate limitation as it damages the very circuits being investigated. The authors attempt to address this by measuring the functional properties of Hippocampal cells, such as their place field features, and claim they are similar to those measured with other methods that do not damage the Hippocampus. However, it is very likely the implant-induced damage is affecting the imaged cells in some way, so caution should be taken when using this method. The authors are very aware of this and briefly discuss the issue. In addition, the authors observe damaged adjacent to face of the glass microperiscope that extends to ~300 um from the face. This area should therefore be avoided when imaging the Hippocampus through the microperiscope.

We agree. This will be important for the interpretation of experiments using the microperisope approach. For many experiments, electrophysiology or traditional CA1 imaging approaches might be preferable to avoid damage to the hippocampal structure. We have tried to be straightforward about these caveats in our discussion. However, we believe the capability of imaging the transverse hippocampal circuit will allow a number of experiments that are currently intractable, and that the benefits will outweigh the caveats in these cases.

Reviewer #3 (Public Review):

Redman et al. describe a novel approach for long-term cellular and sub-cellular resolution functional and structural imaging of the transverse hippocampal circuit in mice. The authors discuss their procedure for implanting a glass microperiscope and show data that clearly support their ability to simultaneously record from neurons within the DG, CA3, and CA1 subregions of the hippocampus. They offer optical characterization demonstrating sufficient resolution to image at the cellular and subcellular level, which is further supported by experimental data characterizing changes in morphology of CA1 apical dendritic spines. Finally, neurons are recorded from as mice engage in navigation behavior, allowing authors to characterize spatial properties of hippocampal cells and relate findings to prior work in the field.

The ability to image from multiple hippocampal subregions simultaneously is a great technical achievement, sure to advance study of the hippocampal circuit. In particular, this approach will likely have tremendous application for addressing the question of how neural representations dynamically change across the hippocampal subfields during initial encoding of novel contexts or later during retrieval of familiar. While the feasibility and utility of this preparation is supported by the data, further characterization of recorded cells will aid the comparison of data collected using this imaging approach to data previously collected with other methodologies.

Thank you for the comments, we have addressed the specific concerns below.

1) Further measures could be taken to more thoroughly evaluate the impact of the implant on cell health. While authors evaluate glial markers, it is not obvious how long after implant these measurements were taken. Additionally, authors could characterize cell responses of neurons recorded proximal to and more distal to their implant to further evaluate implant effect on cell health.

Good points. We have added the date post implantation for the histology samples (Figure 1F caption). To address the second point, we added additional experiments characterizing functional response properties as a function of depth (Figure S7). We did not find systematic changes in place field width or place cell spatial information, as a function of imaging depth (lines 220-224; Figure S7A, B). We did however find a significant relationship between the decay constant for the fitted transients and depth, with cells close ( 130 um) to the surface of the microperiscope face exhibiting slower decay (Figure S7C). This appeared to be due to a small fraction of cells exhibiting longer decay times closer to the microperiscope face. As a result, we advise only imaging neurons >150 um from the microperiscope face (lines 224-226).

2) More in-depth analysis of place cells will aid the comparison of data collected using this novel approach to previously published data. For instance, trial-by-trial data and clearer descriptions of inclusion criteria will allow readers a more detailed understanding of observed place cells.

We have included example place cells with individual trial data (Figure 5C) and have added additional discussion and detail on our selection process for identifying place cells (lines 207-209, 663-666, 674676). In the revised manuscript, we further increased the stringency of our place cell criteria so that none of the cells with time shuffled responses pass the criteria. It should be noted that our place cells were not as reliable as those recorded in the presence of reward (Go et al, 2021). We chose to forgo reward to help ensure that the neurons were responding to spatial location and not to other task variables, but this likely reduced response reliability (see Krishnan et al, bioRxiv; Pettit et al, 2022). We have added discussion of this issue to the manuscript (lines 307-318).

Author Response

Reviewer #3 (Public Review):

The study by Petrov and colleagues examined whether rare cancer drivers can be examined in a network context. For this purpose, the authors develop a new computational tool that is based on two "channels" (MutSet and PathReg) to provide evidence on whether a gene might reflect a driver gene. Based on these channels, they evaluate ten large cancer cohorts and assess the overlap of their results with established cancer genes or datasets that are enriched for cancer genes. Based on this comparison, they find a strong enrichment for known cancer genes.

In my opinion, the study addresses an important point. Indeed, many discovery algorithms have been based on mutational recurrence. While these strategies robustly identify the most frequently mutated cancer genes, they yield diminishing returns for rare driver genes so that several magnitudes of large datasets would be required for identification of rare driver genes. Therefore, network-based identification of rare driver genes could be a useful criterion to identify rare driver genes, for instance, based on their interaction with canonical drivers. If could have an important impact on diagnostics and therapeutic decision making.

While this idea is intriguing, it is not entirely novel. For more than a decade, mutation data in TCGA have been viewed in networks and many previous studies have tried to identify driver genes based on networks. I think a critical point would be to compare the authors' methods against these previous approaches and to demonstrate that it overcomes the limitations that previous studies reported in this field.

Indeed, we included results from five network-based methods in the analysis (see the last para of “Estimation of discovery rates”). While the results significantly overlap, we cannot comprehensively evaluate performance in terms of e.g. false positive rates. Instead, it is the data context that distinguished NEAdriver: it uses only mutation lists per sample, can work on individual samples, and does not require information on transcription, methylation etc.

Author Response

Reviewer #1 (Public Review):

The goal of the work was to test for direct and indirect fitness costs associated with specific types of constructs that could be used for gene drive. The authors conclude that there are no direct fitness costs associated with the presence and expression of either Cas9 or the guide RNAs but that the Cas9 is causing off-target cuts that result in loss of fitness. They also conclude that a newer form of CAS doesn't cause these off-target cuts. While the goal of this study is important, there are many caveats associated with the work as reported, and these limit interpretation of the results, Many of the caveats are pointed out in the discussion.

1.a) I am specifically concerned by the fact that from what I read, a company made the transgenic lines and that there was only one transgenic line per treatment. Unless the fly line used for the insertion was completely homozygous for the chromosome where the insertion was made, the lines could have differed in fitness, due to somewhat deleterious reccessives captured in one G1 but not another. This cost could have persisted for a number of generations after the crosses were made, especially in the high frequency "releases". This may not have been a real problem, but without any replication it is difficult to know.

We apologize that this was unclear in our initial submission. We did in fact generate several transgenic lines of each construct and used independently obtained lines for each of our population cages, except for the Cas9_gRNAs construct, where four lines were used in seven population cages (replicates 1 to 4 were founded with the same line). All of these were also crossed to w1118 flies before we obtained homozygous lines, so the impact of deleterious alleles would have been minimized. We have edited the section “Generation of transgenic lines” in the Methods to clarify this.

We also examined the possibility of fitness effects being caused by such alleles in our maximum likelihood analysis (assuming they are unlinked from the construct — otherwise they should have appeared as direct fitness effects). This model was not a good match for the data, nor was the model with direct fitness effects. Based on these results, we consider it unlikely that such deleterious alleles had a major impact on the observed frequency trajectories in our cage populations.

1.b) My concern is reinforced by the fact that the no-Cas9, no-gRNA line goes up in frequency for the first 5 generations and then becomes stable in frequency. The loss of the fitness advantage is consistent with a fitness effect partially linked to the insertion site in that one cross but not others.

Both of these cages were made with independent lines. We agree with the reviewer that the increase in frequency of the no-Cas9_no-gRNAs construct at the beginning of the experiment seems surprising at first. However, if an initial fitness advantage was truly driving the dynamics of this construct, we would expect that the “initial off-target model” (where fitness costs originated before the experiment) should have yielded the highest model quality in our maximum likelihood analysis, since we also allowed advantageous cut off-target alleles (i.e., fitness estimates > 1) in this model. While the maximum likelihood fitness estimate in the “initial off-target model” indeed exceeded the reference value of 1, its 95% confidence interval still included a fitness value of 1, and a neutral model actually yielded the lowest AICc value (i.e., best model quality, Table 3). We think that one possible explanation for this apparent initial frequency increase is that population cages tend to undergo larger than average fluctuations in the first one or two generations due to the smaller initial population size and potential health differences between founding fly lines (which can persist for a generation or two). We briefly note this in the manuscript methods section.

1.c) It is important to note that the starting points are cages with separate vials of the control and experimental strain. Even a small difference in development time of the two strains in the first generation could lead to an excess of homozygotes in the next generation.

We agree. In our maximum likelihood framework, such differences in development time should show up as a viability difference (fraction of offspring that made it to adulthood in the time window of our experiment). We now note in our revised manuscript that fitness differences between genotypes could be due to longer development time rather than an increase in the juvenile death rate in Cas9_gRNAs carriers. In the “Phenotypic fitness assays” section of our revised manuscript, we additionally state that “longer development time of individuals carrying the Cas9_gRNAs construct would also have appeared as a viability cost in our cage study but not in these fitness assays.”

1.d) I am also concerned by the fact that the main conclusion is that the decline in frequency in the Cas9-gRNA line is due to off-target cuts, but there was no sequencing to back up that conclusion. In the discussion, this problem is mentioned but dismissed. I don't see how it can be dismissed when this is a major conclusion that remains based on very indirect evidence.

We thank the reviewer for raising this important concern, which touches on the issue of how our approach differs from previous approaches that sought to directly detect off-target cleavage through sequencing. Our approach, by contrast, seeks to provide a “direct” measurement of the fitness of an allele. While this allows us to avoid the challenging task of detecting off-target mutations in vivo through whole-genome, population-level sequencing (and then predicting their potential effects), it comes at the price that inferences about the molecular nature of these fitness effects will rely on indirect evidence. However, we want to point out that our conclusion of these fitness effects being primarily due to off-target cleavage is based on three independent lines of evidence: (i) The maximum likelihood analysis of the frequency trajectory of the Cas9_gRNAs construct, where statistical model comparison ranked the off-target effect model higher than the direct fitness costs model; (ii) The fact that we inferred fitness costs only for the Cas9_gRNAs construct but not the construct in which Cas9 was replaced with the high-fidelity Cas9HF1 endonuclease (which should have similar expression and thus, similar direct fitness costs); and (iii) The heterogeneity we observed in the frequency trajectories of the Cas9_gRNAs construct in our cages, which is consistent with a model where off-target sites accumulate over the course of the experiment yet more difficult to reconcile with a model of direct fitness costs.

Inspired by the reviewer’s recommendation, we wondered whether we may in fact be able to directly detect cuts at a few computationally predicted off-target sites. To this end, we performed Sanger sequencing at six sites that were computationally predicted for our Cas9_gRNAs construct by CRISPR Optimal Target Finder, which unfortunately revealed only wild-type sequences (this analysis is described in the new section “Evaluation of computationally predicted off-target sites”). However, we believe that this does not rule out off-target cutting as the primary driver of fitness costs for the Cas9_gRNAs construct due to the following arguments we state in the discussion section of our revised manuscript:

“For example, our sequencing approach would not have allowed us to detect larger insertion/deletion events, which are frequently observed at on-target sites (48, 49). More likely though, we suspect that cleavage events occurred at other sites than the six computationally predicted ones. Indeed, the predictions by CRISPR Optimal Target Finder are based on cleavage specificity in cell lines, where off-target cutting is known to occur more frequently than in animals (47). All but one of the predicted off-target sites carry combinations of single nucleotide mismatches in the PAM-proximal and the distal region, which could make in-vivo cleavage less likely at these sites. Generally, our results are consistent with other studies that found off-target cleavage to frequently occur at sites which would have been difficult to predict computationally (50).”

In a sense, our inability to detect any mutated alleles at this small set of computationally predicted off-target sites might actually highlight a key benefit of our approach: It can estimate the potential fitness costs of a construct without having to rely on accurate computational predictions of putative off-target sites or requiring the very costly approach of whole-genome, population-scale sequencing.

Additionally, we would like to point out that while we found off-target effects to explain the empirical data best, we would probably consider our estimation of the overall magnitude of the fitness costs of the Cas9_gRNAs construct as one of the main conclusions of our manuscript, together with the fact that these were avoided when using the high-fidelity Cas9HF1 endonuclease instead. Thus, even if some readers may remain skeptical about the role of off-target cleavage (and we made sure to qualify our claims on this in the Discussion section accordingly), our systematic analysis of the overall fitness effects is more robust and should be of broad interest.

1.e) When releasing homing gene drives, the initial frequency of the transgenic line is very low, and as in the Garrood et al paper cited, it is possible for the gene drive to outpace the non-target cutting. The modeling does not address what the impact of the presumed fitness costs in this experiment would be for a replacement/suppression drive released at low frequency.

We thank the reviewer for raising this point. It has led us to add a completely new analysis on the “Effect of off-target fitness costs on gene drive performance”, in which we now show simulation results to illustrate the effect of direct and off-target fitness effects on both modification and suppression homing drives. We have also added more discussion on how these different types of fitness costs may affect other frequency-dependent CRISPR based gene drives.

Reviewer #2 (Public Review):

This paper reports a set of Drosophila population cage experiments aimed at quantifying fitness effects associated with the expression of Cas9 gene drive constructs in the absence of homing. The study attempts to deconvolve fitness effects due to the presence of the active nuclease at a genomic location from those that arise from off-target effects elsewhere in the genome: an important issue when considering gene drive strategies in the wild. To distinguish effects due to cleavage at the target site from activity elsewhere in the genome, a construct where Cas9 was replaced with a high fidelity nuclease (Cas9HF1) was employed. The experimental design compares the active nuclease-gRNA constructs targeting a site on another chromosome with no gRNA and reporter only controls, all inserted in the same locus. The Cas9 construct was assayed in 7 replicates with Cas9HF1 and controls assessed as duplicates with cages running for between 8 and 19 generations.

2.a) There is a lack of clarity in terms of the cage set up design, the description in the supplementary methods could clarify if all the replicates came from a single founder and the difference in set-ups that necessitated ignoring some 1st generations.

Thank you for pointing this out. We have thoroughly revised and extended our Methods section on “Generation of transgenic lines” to clarify this point. We now explicitly mention that we generated several transgenic lines of each construct and used independently obtained lines for each of our population cages, except for the Cas9_gRNAs construct, where we used four lines in seven population cages (replicates 1 to 4 were founded with the same line).

For the cage start conditions, we now note that “To avoid potentially confounding maternal fitness effects on the construct frequency dynamics (which could arise based on minor differences in health or age between the initial batches of flies mixed together), we excluded the first generation of five cage populations…” In general, it is quite common for this to happen in insect population cage studies (please see some examples below) and is always a very short-term effect.

2.b) The main finding reported from this part of the work is that with the control populations the frequency of the construct remained fairly constant across the generations, but the active nuclease tended to decline. I am somewhat confused by some of the claims here. First, the authors report a "bottoming out" effect where construct frequency declines then levels off: I am not entirely convinced that Figure 2 shows this. For example, comparing replicates 4 and 5 (8 and 16 generations respectively), it looks to me that there is a steady decline at the same rate with no evidence for a plateau. Perhaps replicates 2 and 3 show "some" evidence of leveling. In addition, replicates 4, 5, 6 and 7 have similar construct starting frequencies (particularly 5 and 7, which are only a few % different) yet the former show a steady decline whereas the latter maintain the construct at a steady level. This does not appear to be consistent with the author's explanation of higher off-target effects in populations carrying high frequencies of the construct. It would be helpful if the authors could more clearly explain the trajectories presented in Figure 2.

We agree with the reviewer that our initial description of the raw construct frequency dynamics solely based on visual clues was making too strong claims (e.g., “different frequency dynamics between single replicates”) without providing more quantitative statistical support. This was originally intended as some basic introduction, with our maximum likelihood analysis then providing a more rigorous assessment in the next section. To improve clarity, we have completely restructured this in our revised manuscript. We removed the comparison of Cas9_gRNAs replicates solely based on visual clues, highlighted the general heterogeneity in trajectories among replicates (without making any specific claims), and instead of the vaguely defined “bottoming out” interpretation, we now only mention the average construct frequency change for the Cas9_gRNAs construct. In addition, we now present our more rigorous maximum likelihood analysis of the construct frequency trajectories and statistical model comparison earlier on in the Results section, so that all of our conclusions are now based on this statistical analysis, rather than an initial visual inspection of the curves. Please see also our comments to point 3.a) below, as reviewer 3 made very similar comments and suggestions.

2.c) Utilising the allele frequencies obtained from the cages, 2 locus ML models were applied with the construct insertion site and an idealised off target site. They argue, correctly in my view, that fitness effects can be attributed to off target activity and not cleavage at the 3L target since the Cas9HF1 construct shows no substantive effect. In the models they assume that the presence of Cas9 in the germline (or maternally contributed) will invariably lead to cleavage at the idealised site. The model indicates that the construct insertion per se has no direct fitness costs but that off-target effects may have fitness consequences of approximately 30%, and seek to support this conclusion with simulations. I found this section difficult to follow but I feel that the conclusions are supported.

We agree with the reviewer that the “Maximum likelihood analysis” section was too dense and therefore challenging to follow, especially for non-expert readers who may not be very familiar with such methods. We have revised and extended this section. In particular, we now also provide a brief summary of the modeling approach at the beginning of the section and have added subsection titles aiming to better guide the reader through the various steps of the analysis. Furthermore, we added a table with an overview of all tested models and highlighted the best-fitting models in tables 2 and 3. We hope that this has improved the clarity of our revised manuscript.

2.d) Direct phenotypic assays with the active Cas9 nuclease were performed, looking at viability, mating preference and fecundity. Relegating these data to the supplements is not useful. While significant effects are attributed to the Cas9-gRNA construct, the authors cannot rule out a DsRed effect and it is a shame they did not assay at least one of the control constructs. In addition, in their modelling they assume that Cas9 activity will always cleave but see no evidence for this in the heterozygote viability assay. Whether this is due to the difference in rearing conditions that the authors claim is debatable.

We thank the reviewer for this valuable feedback. As suggested, we have moved the phenotypic assays (Methods & Results) of the Cas9_gRNAs construct to the main part of the revised manuscript. We decided to conduct phenotypic assays only for the Cas9_gRNAs construct, because it was the only one that displayed some fitness costs in our maximum likelihood analysis (in particular, the DsRed construct did not display any fitness costs in the cages). However, given more time and capacity, we agree that additional phenotypic assays would have been desirable (e.g., a larger sample size per construct and additional constructs). Regarding our choice of model for the maximum likelihood analysis, we used a highly simplified off-target approach, which was necessary given the available information.

2.e) Finally, since the initial cage experiments suggest that the Cas9HF1 enzyme reduces off-target effects they assay this enzyme in a model homing drive, indicating that this enzyme performs as well as the regular Cas9. Again, relegation of these data to supplementary datasets is unhelpful and it would improve the manuscript if these results could be simply summarised in a figure.

We added an additional figure at the end of the “Cas9HF1 homing drive” section in the Results showing the gene drive inheritance rate and resistance allele formation rate in early embryos for the Cas9HF1 and Cas9 homing drive respectively. The gene drive inheritance rate is the percentage of offspring with DsRed fluorescence when crossing individual gene drive heterozygotes with “wildtype” homozygotes (i.e., not carrying any gene drive allele) and is used to calculate the gene drive conversion rate (i.e., the rate at which wildtype alleles are converted to drive alleles) mentioned in the main text. We hope that this has improved the clarity of our revised manuscript.

2.f) Taken together, I think this is a useful study but is presented in a way that is at times impenetrable to the non expert. More clarity in presenting the cage and modelling data, as well as promotion of figures from supplementary material to the main manuscript would considerably aid the non expert and provide greater confidence in the interpretations. If these issue could be clarified I feel the work provides a useful addition to the gene drive field and will help those thinking about developing such strategies, particularly relevant are the findings related to the Cas9HF1 enzyme.

We thank the reviewer for the valuable feedback. We have significantly revised the Results as well as the Discussion, provided additional information on the modeling approach, and shifted supplementary material to the main text of the manuscript. We hope this has improved the overall clarity of the manuscript.

Reviewer #3 (Public Review):

The manuscript by Langmuller, Champer and colleagues reports a set of experiments and models investigating the fitness effects of transgenes in Drosophila melanogaster carrying CRISPR components to determine how useful such transgenes may be for population control. This study benefits from well-designed transgene constructs that allow the investigators to distinguish the effects of on-target and off-target Cas9 endonuclease activity, and a sophisticated maximum likelihood modeling framework that allows estimation of the fitness effects of the transgene constructs. The manuscript's major shortcoming is the absence of statistical analysis of the allele frequency data and some potentially unrealistic assumptions that went into the model.

3.a) My first recommendation is that a statistical analysis of the allele frequency data should be included in the manuscript, rather than inferring patterns solely from visual inspection of the data. Specifically, the manuscript claims that (lines 176-180): "We found Cas9_gRNAs to be the only construct that systematically decreased in frequency across all replicate cages (Figure 2). Interestingly, the allele frequency change was not consistent with fixed direct fitness costs. Instead, the construct frequency "bottomed out" in most replicates, and this occurred more quickly when the starting frequency was higher (Figure 2)." These conclusions regarding allele frequency changes should be supported by statistical analyses. What is the uncertainty surrounding the allele frequency estimates? Some indication of this uncertainty (such as error bars) could be added to Figure 2. Which of the trajectories in Figure 2 show a statistically significant change in allele frequency over the course of the experiment? Is the increase in the frequency of the no-Cas9_no-gRNA replicates significant? What support is there for the claim that the allele frequency changes "bottomed out"? Does a non-linear model fit these data significantly better than a linear trend? What is the evidence that allele frequency decreases slowed earlier "when the starting frequency was higher"? What is the evidence that "replicates 3 and 4 ... had very different frequency dynamics"? While they started at different frequencies, the slope of those two trajectories could be statistically indistinguishable. What is the authors' interpretation of the Cas9_gRNAs replicates 6 & 7 whose trajectories did not decrease?

We thank the reviewer for this detailed recommendation. We agree that our description of construct frequency dynamics solely from visual clues was indeed making too strong claims (e.g., regarding “different frequency dynamics”) without providing enough statistical support for these specific statements. We had originally thought that some readers would prefer we first provide such a qualitative description of the allele frequency trajectories, prior to going into the mathematically more rigorous (but therefore also more complicated) maximum likelihood inference of fitness costs and statistical model comparison of different selection scenarios (“full inference model” vs. “construct model” vs. “off-target model”, etc.)

In response to the reviewer’s comments, we decided to completely restructure this first part of the Results section. Specifically, we have removed our comparison of Cas9_gRNAs replicates solely based on visual clues, and also any mention of the admittedly vaguely defined “bottoming out” behavior. Instead, we now only mention the average frequency change for the Cas9_gRNAs construct across all replicates, while highlighting the heterogeneity among replicates. The maximum likelihood analysis is now introduced right after this and has also been revised extensively to improve clarity. We believe that this analysis provides a very powerful framework for the systematic inference of fitness costs and for assessing which of the different selection scenarios best explains our empirical data. This is because it combines the data from all replicates while fully accounting for the heterogeneity among them. For example, it could well be that construct frequency trajectories in individual replicates may not be statistically distinguishable from neutral evolution, yet in aggregate, an inferred fitness cost of the construct becomes highly significant. Note that the maximum likelihood framework also provides confidence intervals for its estimates, based on the entirety of the data. So the question of whether a departure from a neutral model is significant comes down to whether the 95% confidence interval surrounding the fitness estimate of the given construct still includes a value of 1 (which it does for the “direct fitness” estimate of the full model, but not for the “off-target fitness” estimate, see Table 2).

Regarding the comment about error bars for the allele frequency trajectories in Figure 2, we want to point out that our construct frequency estimates are actually based on the genotype counts of all adult flies present in the given cage experiment at the specific time point. We therefore did not include uncertainty estimates in Figure 2, nor did we include sampling noise in the maximum likelihood analysis. We have now clarified this in the caption of Figure 2 and in the Methods section (“Maximum Likelihood framework for fitness cost estimation”). We also acknowledge that we still cannot rule out sampling noise completely (for example through escaped flies, phenotyping errors, or loss of frozen flies due to destruction or other issues). However, we expect that the relative contribution of these errors should be negligible compared to drift.

The reviewer raises an interesting question: Why did the Cas9_gRNAs construct frequency not decrease in the two replicates with the highest construct starting frequency (replicate 6 and 7)? A possible explanation could be that — given a limited set of off-target sites — cut off-target alleles that impose a fitness cost will accumulate and start to independently segregate from the construct alleles very quickly in populations where the construct has a high starting frequency (and thus a higher overall rate of cleavage events). We now state this possible explanation in the section on “Construct frequency dynamics suggest moderate off-target fitness costs” of our revised manuscript.

3.b) My second recommendation involves the assumptions that went into the maximum likelihood modeling. In particular, it strikes me as unrealistic to assume that 1) the genome contains only a single off-target site that is entirely responsible for the decrease in fitness due to Cas9 activity; and 2) that the rate of off-target mutation is as high as it is assumed to be ("In individuals that carry a construct, all uncut off-target alleles are assumed to be cut in the germline, which are then passed on to offspring that could suffer negative fitness consequences."). Regarding point 1), isn't a more realistic scenario that there are multiple off-target sites, each with a potentially different fitness consequence resulting from Cas9-induced mutations? If so, doesn't the likelihood that all off-target sites have been cut depend on the number of such sites, as multiple off-target sites should reduce the mutation rate at any single site. This possibility also suggests that there may be multiple loci with potentially deleterious Cas9-induced alleles segregating within the experimental populations. Regarding point 2), even assuming only a few potential off-target sites per genome, it seems like the rate of off-target cutting would have to be unrealistically high to approach mutating all off-target sites in the population. The conversion efficiency of the constructs used here is reported as ~80% and 60% in females and males, respectively; it seems likely that the rate of Cas9 mutation at off-target sites is lower than this efficiency for the target site. These assumptions should be justified or relaxed before claiming that mutational saturation of off-target sites is responsible for a decreasing fitness loss over the course of the experiments (after confirming that there is statistical support for the claim that the allele frequency trajectories bottom out).

The reviewer raises a very important point: modeling only one off-target site that represents the net fitness effect of Cas9 cleavage outside the target region as well as a cut rate of 100 % (i.e., the off-target site is always cut in the presence of Cas9) is highly idealized.

(1) We agree with the reviewer that in reality, the experimental populations might have a polygenic off-target landscape, where the fitness of cleavage alleles could differ vastly within as well as between loci. However, given the limited number of data points (e.g., n=87 generation transitions for experimental populations with the Cas9_gRNAs construct), it would be extremely difficult if not impossible to disentangle the numerous parameters that would be necessary to describe such a more complex off-target scenario with our modeling approach. We have now highlighted our model choices, potential caveats, and resulting limitations in both the Discussion section and also the section “Construct frequency dynamics suggest moderate off-target fitness costs” in the Results.

(2) Similar to the single off-target locus, our cut rate of 100 % is an idealized assumption that was chosen with the aim to reduce model complexity. As outlined above, it would be extremely hard to disentangle the cut rate from other parameters (such as the number of target sites if fitness effects are multiplicative across loci). Additionally, we would like to point out that the reported conversion efficiencies (~80 % in males, ~60% in females) are not the conversion efficiencies of the constructs in the experimental populations shown in Figure 2, but of separate homing drives with a single gRNA. All constructs in the experimental populations are designed in a way that no homing can occur, and they have four gRNAs if any. We apologize for the confusion. Our revised manuscript contains now a paragraph in the “Cas9HF1 homing drive” section in the Results that highlights the differences between the constructs in the cage populations and the homing drives assessed in this study. Furthermore, we have added an additional figure that displays the individual results of the homing drive (Figure 5) — we hope this improves clarity.

3.c) My third suggestion involves the correspondence between the results of the likelihood modeling and the phenotypic assays. The best fit model inferred a viability loss of 26% and no detectable effects on female choice (or male attractiveness) or fecundity. In contrast, the phenotypic assays inferred no detectable effect on viability, but a 50% reduction in male attractiveness and 25% reduction in female fecundity. I think that the authors' conclusion that "[t]hese assays broadly confirmed our previous findings" needs some context or explanation as to how these numerically discrepant findings are broadly confirming, beyond the speculation that the discrepancy in viability may be due to rearing in vials vs. population cages.

We thank the reviewer for pointing this out. We removed the claim that the phenotypic assays “broadly confirmed our previous findings” and highlight now the differences in estimated fitness costs for male and females in the phenotypic assays as well as the discrepancy to our maximum likelihood estimates. Furthermore, we provide now additional explanations for what might be causing this phenomenon (i.e., single crosses vs. large populations, vial vs. cage, interactions between individual genotypes and the environment, delayed development of construct homozygotes being interpreted as reduced viability in the maximum likelihood analysis). We also point towards the discrepancies in the Discussion of our revised manuscript and recap potential explanations.

3.d) My fourth suggestion involves the comparison between the Cas9_gRNAs and Cas9HF1_gRNAs transgenes. The inference that off-target cuts are the major source of fitness loss for the Cas9_gRNAs construct relies heavily on the observation that there was no decrease in allele frequency for the two Cas9HF1_gRNAs replicates. It therefore seems critical to be confident in this observation, and to rule out alternative explanations as much as possible. For example, did the authors confirm that the Cas9HF1_gRNAs construct has on-target Cas9 activity levels as high as the Cas9_gRNAs construct? Although I am not certain about this (see comments in the next paragraph on this point), I think the transgene constructs used to estimate drive conversion rates are different from the constructs used for the population cage experiments; if this is correct, I think it would be helpful to provide the on-target mutation rates for the actual constructs used in the population cages.

The reviewer is correct: The constructs in the population cages are different to the homing gene drives for which we estimated the gene drive conversion rates. However, we were able to confirm at least one mutated gRNA target site in every PCR-based genotyped offspring of individuals carrying either the Cas9_gRNAs or the Cas9HF1_gRNAs construct (this is now specified in the manuscript). Thus, we did not expect a systematic difference in on-target mutation rates for Cas9_gRNAs, and Cas9HF1_gRNAs constructs respectively. We acknowledge in the Discussion that construct performance might substantially vary with genomic sites and even organisms.

3.e) Relatedly, I was confused about the portion of the manuscript that reports the drive conversion efficiency. The manuscript states, "As a proof-of-principle that Cas9HF1 is indeed a feasible alternative, we designed a homing drive that is identical to a previous drive (45), except that it uses Cas9HF1 instead of standard Cas9. This drive targets an artificial EGFP target locus with a single gRNA (see Methods)." Given that the rate of drive conversion was estimated by the loss of GFP, these homing drive constructs must be different from the constructs used in the population cage experiments, as those constructs targeted a site on chromosome 3L which does not contain GFP. I could not find a description of these homing constructs in the Methods - while a reader might be able to puzzle this out by reading reference #45, I think it would be helpful to explicitly describe these details in this manuscript.

We apologize for the confusion. We have highlighted the similarities (e.g., nanos promoter, DsRed) as well as the differences (e.g., number of gRNAs) between the homing drives and the constructs in the cage populations at the beginning of the section “Cas9HF1 homing drive” in the Results. We hope this makes it more clear.

Author Response

Reviewer #3 (Public Review):

The primary strength of this study is in establishing the N999S heterozygous mouse as a useful model system for debilitating paroxysmal non-kinesigenic dyskinesia (PKND), with or without epilepsy. This outcome was hard-won following a comprehensive analysis of biophysical, neurophysiological, and behavioral tests. Ultimately the convincing evidence was demonstrated through a clever application of a stress-related behavioral test (quite in alignment with triggers in patients) to elicit the hypo-motility associated with PKND. Like patients who exhibit variable penetrance, even highly inbred mice exhibit much variability, and uncovering a robust phenotype took a nuanced approach and perseverance.

To reach this point, several experiments provided mechanistic insights into the mutant channel behavior. First, whole-cell patch clamp experiments revealed shifts in the G-V consistent with gain-of-function behavior previously characterized using the N999S and D434G mutants expressed heterologously. Novel observations of H444Q revealed a loss-of-function (LOF) behavior with the G-V shifted to positive potentials but to a lesser degree. These electrophysiological phenotypes establish the rank of predicted severity as N999S>D434G>H444Q.

This prediction was tested in brain slices of heterozygous animals where the mutant channels would be normally spliced and associate with WT subunits and other components such as beta subunits. The investigators evaluated BK currents by patch clamp from hippocampal neurons where BK channels are known to play key functional roles. Both N999S and D434G showed the predicted increase in current magnitude, though interestingly the differences between them apparent in heterologous expression were lost in the native setting. Curiously, no differences in BK current magnitude were observed in neurons of heterozygotes carrying the putatively LOF mutation H444Q.

In terms of seizure susceptibility, D434G mutants different from WT and less severe than N999S mutants with respect to time to evoked seizure, although differences in "EEG power" were not statistically significant between D434G and WT. These observations support the conclusion that D434G represents an intermediate disease phenotype.

The behavioral studies were the most effective in revealing differences among the variants and in defining GOF N999S heterozygotes as a compelling animal model for PKND and providing evidence that the LOF mutation conferred the opposite effect of hyperkinetic mobility. The findings provide the new insight that KCNMA is the target of heritable, monogenic disease, a conclusion that was previously not forthcoming because known human mutations have arisen de novo. The dyskinetic phenotypes in response to stress induction are wholly consistent with patient symptoms.

With respect to rigor and reproducibility, it is commendable that the investigators were blinded to genotype during data collection and analysis. Moreover, the study provides an important confirmation of previous findings from another lab regarding the cellular phenotype of the N999S mutant. WT controls were compared to transgenic littermates within individual transgenic lines. In some cases, the sample sizes were rather low (see below), but otherwise the study seems rigorous.

The strengths of the manuscript far outweighed the weaknesses. The experiments interpreted to suggest a gene dosage effect with D434G were not compelling to this reviewer and might be better documented in the supplement with the conclusion that further work is required.

Due to pandemic-related animal and lab issues, we were unable to generate and surgically implant full Kcnma1D434G/D434G homozygous cohorts for the EEG/seizure portion of the study. We focused instead on using the limited mice of this genotype for the novel PNKD3 assays (n=7), leaving the seizure dataset at n=3.

To address the concern, the Kcnma1D434G/D434G data was removed from Figure 4 to avoid overinterpretation of a gene dosage effect. However, we did retain the individual measurements within the Results text (lines 383 and 385), on the basis of facilitating direct comparisons between our study and other D434G studies. For example, even with only three measurements, the trend toward the shortest seizure latencies in Kcnma1D434G/D434G mice is similar to the result obtained with an independently generated D434G mouse model (Dong et al, 2022). Yet seizure power and the presence of spontaneous seizures do not show a similar trend, suggesting our results differ from theirs in these important aspects. This is now stated more clearly in the revised conclusion for that paragraph, ‘While not conclusive and requiring substantiation in a larger cohort, the Kcnma1D434G/D434G seizure data raise the possibility of a gene dosage effect with D434G that qualitatively differs from an independently-generated D434G mouse model (Dong et al., 2022),’ (lines 388-390).

In contrast to the seizure part of the study, the increased severity of Kcnma1D434G/D434G PNKD-immobility is fully supported by the data with sufficient statistical power (Figure 5D). However, the idea that the increased severity with homozygous D434G in PNKD-immobility was consistent with gene dosage observations for seizure was removed for consistency (lines 549-550).

As a side note, we also added additional clinical descriptors (akinesia) and colloquial descriptions for PNKD3 (‘drop attack’) to disambiguate how a PNKD3 episode appears different from other types of motor dysfunction. This was to facilitate comparison with the two other KCNMA1-D434G models (mouse and fly; Dong et al, 2022; Kratschmer et al., 2021), which report aspects of dyskinesia in the setting of baseline locomotor dysfunction. To our knowledge, these models have not been evaluated for the striking ‘drop attack’ immobility presenting in patients (lines 84-85).

The consequences of the altered BK current levels were assessed on the voltage dependence of firing frequency in the hippocampal neurons, but it was not very clear how increased BK current would enhance neuronal excitability. Also, how might it lead to the PKND phenotype? A paragraph even speculating on these mechanistic links in the Discussion would be welcome.

The mechanism for how BK currents increase action potential firing are not fully identified in this study (see also response to reviewer #2). In the Results, a new paragraph was added at the end of action potential section to summarize the AHP changes in more detail and speculate an indirect mechanism of action for the increase in BK current, predicted from a similar ‘GOF’ BK current type, where β4 regulation of BK channels is lost (lines 294-304). Additional details have also been added to the Discussion regarding the factors contributing to lower seizure threshold (lines 675-680).

Additional re-organization of Discussion text addresses the basis for PNKD. A direct statement that it is not clear yet which neurons/circuits are the most critical for PNKD-like symptomology was added, and which of these express BK channels (lines 680-700). We follow with a succinct summary of phenotypically-relevant PNKD models. While there is a lot to unpack with respect to similarities and differences between different paroxysmal dyskinesia models in the literature, they ultimately shed little light the question of KCNMA1 PNKD3-related dysfunction. With the addition of the d-amp rescue control, we focus mainly on the amphetamine response predicting a CNS locus (lines 692-693). The d-amp response may even suggest dopaminergic pathways (some of which express BK channels) as a plausible to investigate in future studies, but due to the complex interplay of d-amp dosage and the novel motor assay, we don’t think speculating on a specific circuit is supported with enough actual data to add in the Discussion.

Author Response

Reviewer #1 (Public Review):

The 2019, Johnson et al., Science study (referred to as "2019 study" or "prior study" in the rest of the comments) measured mutational robustness in F1 segregants derived from a yeast cross between a laboratory and a wine strain, which differ at >35,000 loci. To realize this, the authors developed a pipeline 1) to create the same set of transposon insertion mutations in each yeast strain via transformation; and 2) to measure the fitness effects of these specific insertion mutations.

In this manuscript, the authors applied the same pipeline to laboratory evolved yeast strains that differ in only tens or hundreds of loci and thus are much less divergent than those used in the prior study. Both studies aim to characterize how the fitness of the sets of insertion mutations (mostly deleterious) vary depending on the existing mutations (mostly beneficial) in those yeast strains. However, the current manuscript, especially when compared to the prior study, suffers from several major weaknesses.

First, only 91 genes out of >6,000 genes in the yeast genome are perturbed in the manuscript. The small set of disruption mutations is unlikely to faithfully capture the pattern of epistasis in the selected clones. By comparison, >1,000 insertion mutations were evaluated in the 2019 study. Because the majority of the >1,000 tested mutations were neutral, the authors focused on 91 insertions that had significant fitness effects. The same 91 insertion mutations are used in the current study. However, as evident in both studies, epistasis plays an important role in how insertion mutations interact with different genetic backgrounds. Considering the vastly different genetic backgrounds between clones used in the prior and current studies, the insertion mutations of interest in the current study is unlikely to be the same as those in the prior study. The large-scale genetic insertion used in the prior study is suggested to be conducted in the current study.

This concern is summarized in Essential Revision 1 above; see our comments there for our detailed response. Briefly, we have added an additional Figure Supplement (Fig. 1 – Supplement 8; see above) demonstrating that the 91 insertion mutants have a similar range of effects in this study as in the previous one (which may be expected since the genetic backgrounds here are as closely related to those in the 2019 study as the backgrounds in the 2019 study are to each other).

Second, the statistical power in the current manuscript is insufficient to support the conclusions. Fitness errors were not considered when several main conclusions were drawn (fitness errors on the y-axis of Figure 1B are not available; fitness errors on the x-axis of Figure 2 are not available). The current conclusions are invalid without knowing the magnitude of fitness error. Fitness of each clone should be measured in at least two replicates in order to infer errors of fitness measurements. Additionally, the authors isolated two clones from the same timepoint of each population and treated them as biological replicates based on the fitness correlation between the two clones. However, this practice can be problematic because the extent of fitness correlation varies across populations and it is less likely to capture the patterns of epistasis when clones are isolated from more heterogeneous populations. Similarly, the authors could avoid this bias by measuring the fitness of each clone in multiple replicates and treat the two clones from the same timepoint/population separately.

We agree that details about statistical methods, most of which are taken from Johnson et al. (2019), were not clear in our text. As we also describe in our response to the Essential Revisions above, we have rewritten a large part of the methods text to provide more details about statistical methods and have calculated and reported errors more broadly:

Errors on fitness effects: We have expanded our methods text describing how the fitness effect of a mutation is determined for a single clone / condition. This text now emphasizes the internal replication provided by redundant barcodes, which allows us to calculate a standard error for the effect of a mutation in a single clone / condition. These errors are shown in Figure 1 – Figure Supplements 1-3. We have also added details on how errors are calculated for a mutation for a population-timepoint, and these errors are now included in Figure 2.

Errors on the DFE mean: We discuss this below.

Considering clones separately: As we also describe in the essential revisions above, Johnson et al. (2021) shows that the mutational dynamics in these evolving populations are dominated by successive selective sweeps, so we expect clones isolated from the same population-timepoint to rarely differ by many mutations. However, we agree that there are likely some cases in which the two clones have important genetic differences. To address this concern, we have reanalyzed our data as you suggest, considering each clone separately. The results of this analysis are included for every main text figure in the form of figure supplements (Figure 1 - figure supplement 7, Figure 2 - figure supplement 5, Figure 3 - Figure supplement 5, and Figure 4 - figure supplement 1), which show that our qualitative conclusions are unchanged.

Reviewer #2 (Public Review):

Johnson and Desai have developed a yeast experimental-evolution system where they can insert barcoded disruptive mutations into the genome and measure their individual effect on fitness. In 2019 they published a study in Science where they did this in a set of yeast variants derived by crossing two highly diverged yeast. They found a pattern that they termed "increasing cost epistasis": insertion mutations tended to have more deleterious effects on higher fitness backgrounds. The term "increasing cost epistasis" was coined to play off the converse pattern commonly observed in experimental evolution of "diminishing returns epistasis" wherein beneficial mutations tend to have smaller effects on more fit backgrounds. Another way to think about fitness effects is in terms of robustness: when mutations tend to have little effect on phenotype, the system is said to be robust. Thus, when increasing costs epistasis is observed, it suggests that higher fitness backgrounds are less robust.

In this paper, Johnson and Desai use this same barcoded-insertions system in yeast, but here the backgrounds receiving insertions are adapting populations. More specifically, they took 6 replicate populations that evolved for 8-10k generations and inserted a panel of 91 mutations at 6 timepoints along the evolutions. They then did this entire experiment in two different environments: one in rich media at permissive temperature (YPD 30) and one in a defined media at high temperature (SC 37). Importantly, the mutations accumulating in a population over time here are driven by selection-and thus the patterns of epistasis observed here are probably more relevant to "real" evolution than the backgrounds from the 2019 paper. The overarching question, then, is whether similar patterns of epistasis is found in these long-term adaptations and across conditions as was previously observed.

The first major finding in this work is that at YPD 30 (where the yeast are presumably "happy"), the mean fitness effect does decline in most (but not all) populations as they adapt. Since the population is becoming more fit over time (relative to a constant reference type), this is consistent with the previously observed pattern of increasing cost epistasis. The strength of the effect is, however, weaker than in that previous work. The authors speculate that this may reflect the fact that far few mutations are involved here than in the previous study-giving far fewer opportunities for (mostly negative) epistatic effects. I find this explanation likely correct, although speculative.

The second major, and far more surprising, result is that in the other condition (SC 37), the insertion mutations mutations do not show a consistent trend: mean fitness effect of the insertion mutations does not change as adaptation proceeds. This is despite the fact that fitness increases in these population over time just as it did in the YPD populations. Toward the end of the paper, the authors speculate as to why this is the case. They argue that in the YPD 30 environment, selection is mainly on pure growth rate. They suggest that the growth rate depends on different components such as DNA synthesis, production of translation machinery, and cell wall synthesis. Critically, these components are non-redundant and can't "fill in" for each other. So, for example, rapid DNA synthesis is of little value if cell-wall synthesis is slow. As adaptation fixes mutations that increase the function of one of these growth components, they shift the "control coefficient" to other components. This, they argue, may be the major explanation behind increasing cost epistasis. I find the logic of their argument compelling and potentially providing great insight into developing a richer view of epistasis. Future experiments will be needed to test how well the hypothesis holds up. They then flip the argument around and suggest that in the SC 37 environment, the targets of selection are fundamentally different from those in growth-centric YPD 30 conditions. Instead, they argue, there is likely more redundancy in the components that mutations are affecting. I again find their arguments compelling.

After establishing these observed patterns for mean effects, they examine individual mutations and look at the relationship of fitness effects as a function of background fitness. The upshot of this analysis is that there are more negative correlations than positive ones (especially in the YPD 30 conditions), but also that there is a lot of variation: there are many mutations that show no correlation and a small number with a positive correlation. This casts substantial doubt on the simplistic view that for the vast majority of mutations, fitness itself causes mutations to have greater costs.

We thank the reviewer for these positive comments and the nice summary of our work.

As a minor point of criticism, a lot of statistical test are being done here and there is no attempt to address the issue of multiple testing. I would like the authors to address this. I say minor because I don't think the overarching patterns are being affected by a few false positive tests.

Related points were also raised by the other reviewer. To address this, we have added multiple-hypothesis-corrected p-values for these least-squares Wald Tests (using the Benjamini-Hochberg method) to our dataset (Supplementary File 1). As you suggest, for this particular analysis in which we compare the overall number of mutations following each pattern, we are willing to accept the possibility of false positives, so we still use the original p-values to categorize the mutations in Figure 2. We address this point in the main text and provide the numbers of mutations falling in each category after we perform this correction:

“Because we are primarily focused on comparing the frequency of each pattern across environments, we report these values before multiple-hypothesis-testing correction here and in Figure 2; after a Benjamini Hochberg multiple-hypothesis correction these values fall to 24/77 (~31%), 15/74 (~20%), 9/77 (~12%), and 11/74 (~15%), respectively.”

From here the authors turn to using a formal modeling to understand epistasis better. For each mutation, they fit the fitness data to three models: fitness-mediated model = fitness effects are explained by background fitness, idiosyncratic model = fitness effects can change at any point in an evolution when a new mutation fixes, and full model = fitness effects depend on both fitness and idiosyncratic effects.

My major criticism of the work lies here: the authors don't explain how the models work carefully and thoroughly, leaving the reader to question downstream conclusions. Typically, when models are nested (as the fitness-mediated and idiosyncratic models appear to be nested within the full model), the full model will, by definition, fit the data better than the nested models. But that is not the case here: for many mutations the idiosyncratic model explains more of the variance than the full model (e.g. Figure 3A). (Note, the fitness-mediated model never fits better than the full model). Further, when dealing with nested models in general, one should ask whether the more complex model fits the data enough better to justify accepting it over simpler model(s). There are clearly details and constraints in the models used here (and likely in the fitting process) that matter, but these are not discussed in any detail. Another frustrating part of the model fitting is that each model is fit to each mutation individually, but there is no attempt to justify this approach over one where each model is expected to explain all mutations. I'm not saying I think the authors have chosen a poor strategy in what they have done, but they have made a set of decisions about how to model the problem that carries consequences for interpretation, and they don't justify or discuss those decisions. I think this needs to be added to the paper. I think this should include both a high level, philosophy-of-our-approach section and, probably elsewhere, the details.

The reason this matters is because the authors move on to use the fitted models and the estimated coefficients from the models in discussing and interpreting the structure of epistasis. For example, they say "We find that the fitness model often explains a large amount of variance, in agreement with our earlier analysis, but the idiosyncratic model and the full model usually offer more explanatory power." Looking at Figure 3A, this certainly appears to be the case, yet that type of statement is squarely in the domain of model comparison/selection-but as explained above, this issue is not addressed. Relatedly, the authors go on to argue that "Positive and negative coefficients in the idiosyncratic model represent positive and negative epistasis between mutations that fix during evolution and our insertion mutations." I'm left wondering whether the details of the model fitting process matter. I am left asking how the idiosyncratic model would perform on data that arose, for example, under the fitness-mediated model? Or how it would perform on data originating under the full model? Is it true that when data arises under a different model (say the full model) but is fit under the idiosyncratic model, negative coefficients always represent negative epistasis and positive coefficients will always represent positive epistasis and that model misspecification does not introduce any bias? Another thing I am left wondering about concerns the number of observed coefficients in the idiosyncratic model: if one mutation shows similar effects across backgrounds, it might generate one coefficient during model fitting, while another mutation that has different effects on different backgrounds could give rise to several coefficients-is there some type of weighting that addresses the fact that individual mutations can generate different numbers of coefficients? One can imagine bias arising here if this isn't treated carefully.

One of the main conclusion that the authors reach is that the pattern of increasing cost epistasis (observed previously and here in the YPD 30 environment) may not arise from the effect of background fitness itself, but instead arise because epistatic effects tend to be negative-and the more interactions there are (with mutations accumulating over time), the more they tend to have a negative cumulative effect. I find it very likely that the authors have this major conclusion correct. By contrast, they find that at SC 37, the distribution of fitness effects is less negatively skewed-with a considerable number of coefficients estimated to be > 0. They close with a really interesting discussion exploring how these patterns likely arise from underlying biology of the cell, metabolic flux, redundancy, and selection for loss-of-function vs gain-of-function. I find a lot of this interesting and insightful. But because some of their conclusions rest squarely on the modeling, I encourage the authors to be more thorough and convincing in how they execute this aspect of the work.

Thanks for these detailed comments about the modeling approach and analysis, which raise points that were also described in the Essential Revisions and by Reviewer 1. We agree that these details were not presented sufficiently clearly in the original manuscript. In the revised manuscript, we have added a much more in-depth section on the details of the modeling procedures in the Materials and Methods, including formulas for each model and a discussion of how noise could affect our modeling results (see responses to essential revisions and reviewer 1 above for more information). This includes an analysis of shuffled and simulated datasets, which will give readers a better sense of how to interpret these modeling results. We have also included a new paragraph in the results that compares the models for each mutation and for the entire dataset using the Bayesian Information Criteria (BIC):

“We can also ask which model best explains the data using the BIC, which penalizes models based on the number of parameters. The small squares below the bars in Figure 3A indicate which model has the lowest BIC for each mutation. In YPD 30°C, the full model has the lowest BIC for 40/77 (~52%) mutations and the idiosyncratic model has the lowest BIC for 37/77 (~48%). In SC 37°C, the full model has the lowest BIC for 49/73 (~67%) mutations and the idiosyncratic model has the lowest BIC for 24/73 (~33%). When we assess how well each model fits the entire dataset in each environment, the full model has a lower BIC than the idiosyncratic model in both environments.”

We also appreciate the suggestion to look at how coefficients are spread among mutations. We have made a new supplemental figure (Figure 3 - Figure supplement 3) that clearly shows the coefficients broken down by mutation for each condition. This figure shows that coefficients are often clustered for one mutation. That is, multiple populations often have similar coefficients / patterns of epistasis for a particular mutation. We don’t view this as a source of bias in our data, but as an indication that the mutations fixing in these populations sometimes exhibit similar patterns of epistasis with these insertion mutations. We now reference this supplemental figure in the main text (“see Figure 3 – figure supplement 3 for a breakdown of coefficients by individual mutations”) as a better representation of the coefficients that result from our modeling.

Author Response

Reviewer #2 (Public Review):

This manuscript from Shi, Ballesta, and Padoa-Schioppa examines the relationship between neural activity in the monkey orbitofrontal cortex (OFC) and various choice patterns that arise in sequential (versus simultaneous) choice. This approach addresses a central question in the study of decision-making: how can one identify value-dependent versus value-independent effects on choice behavior when value is defined from that behavior itself? Here, the authors document three behavioral differences in sequential choice: choosers are nosier, show an order bias, and show a preference bias. Leveraging a conceptual computational framework for OFC activity that the authors have developed over many years, the authors link reduced accuracy to changes in neural valuation in the OFC, order effects to post-valuation decision activity in the OFC, and preference effects to extra-OFC processes. For decision neuroscientists, these findings show specific differences between sequential and simultaneous choice, and suggest the integration of multiple stages (valuation, decision, and post-decision) in the selection process. More broadly, this work shows how an examination of neural activity can shed light on aspects of the decision process that cannot be distinguished by an examination of behavior alone.

Strengths:

Overall, this paper presents a novel and thoughtful task design that allows comparison of neural and behavioral value and choice effects. In concert with an established circuit-based framework for parsing different types of OFC response patterns, the authors test and validate a number of hypotheses on the link between neural activity and choice.

(1) Comparing sequential and simultaneous choice tasks in an interleaved manner is a clever approach to separate valuation and comparison processes in time. While not entirely novel (e.g. see work from the Hayden group), the combination of this approach with the OFC response pattern (offer value, chosen value, chosen juice) framework allows a distinction between valuation and comparison-related effects.

(2) This paper is the latest in a significant series of related papers on orbitofrontal activity from this group, and cleverly utilizes their expertise in characterizing, analyzing, and conceptualizing different patterns of OFC activity. In addition to the long-established offer value/chosen value/chosen juice categorization, recent papers from this group have established the causal contribution of OFC offer value activity to economic choice and established similar OFC neural contributions to sequential and simultaneous choice tasks.

(3) Apart from a causal test (e.g. cell type specific stimulation) of the contribution of different neural responses to different choice effects, the next strongest evidence is a demonstration of a consistent relationship across sessions. The authors show such a relationship between offer value coding strength and choice accuracy, between chosen value sequence effects and behavioral order bias, and between chosen juice inhibition and order bias. At the least, these relatively strong effects show a strong correlation between different OFC responses and behavior.

Thank you for emphasizing these points.

Weaknesses:

While the experimental approach and rigor of the analyses are strengths, there are issues of interpretation and generality of analytical approaches that should be clarified.

(1) The abstract, introduction, and discussion touch on canonical behavioral economic choice effects as a prelude to the behavioral effects documented here, but it's not clear they are so closely related. [A] Many of the effects in the cited literature (framing effects in risky choice, preference reversals, etc.) are robust across different task paradigms, whereas the effects shown here arise specifically from a comparison of choice across different task paradigms (sequential vs. simultaneous). Furthermore, [B] it's not clear that the term "bias" adequately captures the array of effects in the behavioral economic literature (for that matter, [C] one of the main effects in this paper is reduced choice accuracy rather than a bias). [D] The paper would benefit from a clearer conceptual linkage between documented behavioral biases (particularly in humans) and the effects shown here.

[B] We beg to differ. In our reading of the literature, the term “bias” is very general and it is invoked practically every time choices present some effect that seems idiosyncratic or “irrational”. The list of documented biases is very long – a good reference is the Wikipedia page on cognitive biases (for more scholarly references, see (Gilovich et al., 2002; Kahneman et al., 1982)).

[A] As for whether biases documented in behavioral economics are robust across task paradigms, that’s really matter of perspectives. For example, we all understand the phenomenon of loss aversion (a.k.a. “status quo bias”) to be very robust and almost intuitive. But before the prospect theory paper of Kahneman and Tversky (1979), that was not at all the case. In the 15 years following that paper, much of what Kahneman and Tversky did was to show how loss aversion affected choices in different domains (Kahneman and Tversky, 2000). Other biases are much less reliable. For example, there is an extensive literature on decoy effects – i.e., violations of the axiom of “independence of irrelevant alternatives”. However, it turns out that the strength and even the direction of decoy effects depend on seemingly minor details (Spektor et al., 2021). In other words, decoy effects are not as robust as one might think. As for the biases dicussed here, our hunch is that the order bias is quite ubiquitous. Indeed, it was already documented using different tasks in different species (Krajbich et al., 2010; Rustichini et al., 2021). The preference bias might also be the manifestation of a rather general phenomenon. Afterall, there is a common intuition that when a decision is difficult we sometimes fail to finalize it, and eventually choose some default option. In conclusion, we think of the two biases discussed here as conceptually very comparable to biases described in behavioral economics.

[C] We agree that the drop in accuracy is (strictly speaking) not a choice bias, and we carefully chose the title and wrote the whole manuscript to keep that point clear. However, let us note that the drop in accuracy observed under sequential offers could easily be construed as a choice bias – specifically, a bias favoring in any situation the lesser option (lower value). As we conclude the present study, this phenomenon continues to fascinate us. Indeed, while it is clear that the behavioral effect arises at the valuation stage, we still don’t understand why the activity range of offer value cells is reduced under sequential offers. Naively, one might have guessed the opposite – i.e., that when only one offer is on display, the lack of competition translates to stronger offer value signals. We plan to give this issue more thought in the future. One possibility is that the system modulates the activity range of offer value cells depending on the task and/or the behavioral context. If so, differences in choice accuracy measured under sequential versus simultaneous offers would be a manifestation of a more general phenomenon. Of course, this matter remains open for future research.

[D] The link between the biases discussed here and other biases described in the literature is conceptual. The main point we want to make is this: Over the past 20 years, we have gained some understanding of the neural circuit and mechanisms underlying simple economic choices. While our understanding remains incomplete and object of ongoing research, notions acquired for simple choices can be used to make sense of a broader class of choices. Thus, in principle at least, it is possible to shed light on a variety of traits and biases by observing the activity of particular cell groups. The last paragraph of the ms conveys this point.

(2) The analyses rely on a particular quantification of choice behavior (probit regression), which interprets choice effects (e.g. relative valuation of the two juices, sigmoid steepness) via specific parameter combinations and relies on specific assumptions about the construction of choice (e.g. cumulative normal distribution, constant sigmoid slope across order effects). This method of quantifying choice behavior is well-documented in previous studies, allowing a comparison to past work. However, given the importance of this approach to both quantifying choice effects and comparing choice to OFC responses, the paper would benefit from directly addressing two issues: (1) how well does probit regression actually capture stochastic choice behavior (in both Task 1 and Task 2), and (2) do the findings rely on specific choice modeling assumptions? The second issue is most important for the order bias effects, which assume a constant sigmoid across conditions - do the authors reach similar conclusions if this assumption is relaxed?

Thanks for raising this question. We address it more thoroughly below (under “Recommendations for the authors”, point (2)). In a nutshell, when we designed the behavioral analysis, we chose the probit function and the log value ratio model (as opposed to the value difference model) based on general considerations and for consistency with our previous studies. We now conducted a series of control analyses using logit instead of probit and value difference instead of log value ratio. We also repeated all the analyses of neuronal activity using measures for relative value, choice accuracy and order bias derived from these behavioral models. The upshot is that all of our results hold true independently of the regression model used to analyze choices. Thus we kept the results as in the original ms, and we included a new section in the Methods to describe our control analyses (p.16-17).

(3) There are some issues with the strength and interpretation of the preference bias that need to be addressed. Re: strength and significance of the preference bias, the text seems to overemphasize the dependence of the effect on relative value (rotation of the rho-2 vs rho-1 ellipse) at the cost of the simple task difference (shift in the ellipse above the identity line). Conceptually, a preference bias (an shift in relative value towards the favored item) requires only the task difference, not the dependence on relative value. It would be clearer for example if the main text (pg. 6) presented the statistics (t-test, Wilcoxon) supporting the difference in relative values (rhos) between Tasks 1 and 2. Furthermore, the rotation does not seem as robust: the text states that the result is significant in both animals (p<0.04) but the ANCOVA results (Fig 3C and 3F) suggests that the effect is only significant in Monkey J. Is the preference effect significant only in one animal, and if so, is the effect significant across the combined data?

Let us refer to Fig.3C. There is no question that the separation between the red and blue lines is statistically significant (order bias). In addition, the two lines appear (a) displaced upwards and (b) rotated counterclockwise compared to the identity line. In our understanding, the question raised by R2 is whether the two effects – displacement (a) and rotation (b) – are both present and both necessary to define the preference bias. We actually gave this issue extensive thought early on, and we concluded that displacement and rotation are not easily dissociable, at least in our data set. The reason is simple: to dissociate them, we would have to make some assumption about the center of rotation. For example, if we assume that the center of rotation is [0, 0], then there clearly is a rotation but the displacement is close to zero. Conversely, if the center of rotation is [1, 1] (which, in some ways, is a more logical assumption), the rotation is still there but the displacement is >0. When we considered these elements, we realized that any choice of a center of rotation would be somewhat arbitrary. Further complicating things, once a center of rotation is chosen, rotation and displacement are non-commutative operations. Importantly, this issue only affects the displacement, meaning that the rotation angle (and its statistical significance) does not depend on choosing any particular center of rotation. In this light, we chose to define the preference bias in a way that is more tight to the rotation than to the displacement, while noting that the net effect of the phenomenon was to bias choices in favor of the preferred juice (hence, the phrase “preference bias”). The only problem with this definition is that it doesn’t do full justice to the phenomenon in monkey G (Fig.3F), where the displacement is more clearly evident than the rotation (indeed, the latter only trends towards statistical significance (p=0.07)). Still, we don’t see a better way to design our analyses. Thus we kept the ms unchanged in this respect.

(4) On a related note, the authors present and view the effects as detrimental for the animals, but I think they have to more explicitly state how they are defining outcomes. For example, the abstract states "By neuronal measures, each phenomenon reduced the value obtained on average in each trial and was thus costly to the monkey". Does this mean that outcomes are less valuable, with value defined by (offer value cell) firing rates? A clarification is particularly important for the preference bias, where animals show a stronger bias for the preferred option compared to simultaneous choice. At the behavioral level, this effect seems to only be a poorer outcome if one assumes that simultaneous choice demonstrates true values - can it not be assumed that sequential choice demonstrates true preference, and the preference bias reduces performance in simultaneous choice? The authors may have an explanation in mind based on OFC value coding, and it would be helpful to be explicit here.

Thank you for raising this question. The revised ms includes a new section (Discussion; ‘The cost of choice biases’; p.13) that discusses this important issue. In a nutshell, if in two conditions subjective values are the same but choices are different, in one or both conditions the subject fails to choose the higher value. In that sense, the choice bias is detrimental. Our analyses of neuronal activity indicated that subjective offer values were (a) the same in the two tasks and (b) independent of the presentation offer in Task 2. Hence, both the preference bias and the order bias were detrimental to the animal.

(5) Finally, at a broad level, the authors rigorously define and test hypotheses about how the different behavioral effects relate to OFC activity within the context of their neurocomputational framework (offer value, chosen value, chosen juice cells arranged in a competitive inhibition network; Fig. 1). However, it should be acknowledged that the primary conclusions - about how the different behavioral effects arise during valuation, comparison, or post-comparison - relies on the assumption that the different OFC response patterns reflect these specific circuit functions, and that OFC is causally related to choice. It would be more balanced if the authors could acknowledge this point in the discussion, and discuss any relevant potential alternative explanations for their findings.

This issue is addressed above (Essential revision, point 1). In essence, R2 is correct: all our analyses were designed, and all our results are interpreted, under a series of assumptions. Most of these are backed by empirical evidence (e.g., showing that the encoding of decision variables in OFC is categorical in nature). However, one assumption remains a working hypothesis. Specifically, we assume that the cell groups identified in OFC constitute the building blocks of a decision circuit. If so, the activity of different cell groups may be associated with different computational stages. We edited the Discussion to clarify this point (p.11-12). As for possible alternative explanations, we agree that it is a very reasonable question to ask, but we honestly are at a loss addressing it. Indeed, one would never conduct the analyses presented in this ms if not in the framework of Fig.1. Consequently, it is hard to come up with any interpretation for the results without embracing that computational framework. If R2 can propose some alternative interpretation for the results presented in the ms, we would be more than happy to think about it, and possibly revise our thinking.

Author Response

Reviewer #3 (Public Review):

In this manuscript the authors study the consequences in neurons of knocking out the cohesin subunit Rad21. The authors have previously performed a version of chromatin conformation capture called 5C in which they are able to generate very high-resolution chromatin interaction maps across focused regions of the genome. In that study they focused on several activity-inducible genes and showed that there were both pre-existing and activity-inducible interactions of putative enhancers with the promoters of activity-inducible genes. Here to determine if Rad21 is important for those interactions and their functional consequences on gene regulation, they do two different knockouts in postmitotic neurons (cell type cKO and rapid TEV-mediated cleavage). Loss of Rad21 led to impaired expression of many neuronal genes at baseline as well reduced branching and spine density, by comparing against previous HiC maps, the authors show that the most affected genes are those with the largest loops. Then they move on to activity-regulated genes, where they compare the effects of Rad21 deletion on their 5C maps as well as gene expression. These data show that activity-induced genes expression and inducible looping between promoters and putative enhancers proceed largely normally in the absence of Rad21, though large CTCF loops are disrupted.

Understanding the mechanisms of chromatin organization in the nucleus is important and this group has one of the best methods for studying high resolution chromatin interactions. Knocking out Rad21 is a reasonable strategy to disrupt looping and the 5C data support that the authors did successfully change some aspects of loops in postmitotic neurons that are important for neuronal development. However, the most notable finding in the data is that for the most part, activity-induced gene expression and activity-induced changes in promoter looping to putative enhancers were unaffected in Rad21 knockout neurons. This is rather different from the results of a previously published Rad21 knockout, though the authors don't discuss this.

Overall this is a well-executed study that presents descriptive data about the functions of cohesin-mediated chromatin architecture in neurons and offers data that suggests that Rad21 is mostly not required for activity-dependent transcription.

We thank the referee for these thoughtful and constructive comments. However, we note that the interpretation that 'for the most part, activity-induced gene expression and activity-induced changes in promoter looping to putative enhancers were unaffected' appears to overlook that many inducible genes were deregulated at baseline in cohesin-deficient neurons, and a significant proportion of LRGs remained deregulated after activation with KCl or BDNF. We also note that, in contrast to neurons, a sizeable proportion of secondary response genes in macrophages are dependent on interferon expression, which is reduced in the absence of cohesin. Accordingly, exogenous interferon rescues the expression of numerous secondary response genes in cohesin-deficient macrophages (Cuartero et al., 2018). We have addressed these points in detail in the revised manuscript.

Author Response

Reviewer #1 (Public Review):

Overall, this study is well designed with convincing experimental data. The following critiques should be considered:

1) It is important to examine whether the phenotype of METTL18 KO is mediated through change with RPL3 methylation. The functional link between METTL18 and RPL3 methylation on regulating translation elongation need to be examined in details.

We truly thank the reviewer for the suggestion. Accordingly, we set up experiments combined with hybrid in vitro translation (Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) and the Renilla–firefly luciferase fusion reporter system (Kisly et al. NAR 2021) (see Figure 5A).

To test the impact of RPL3 methylation on translation directly, we purified ribosomes from METTL18 KO cells or naïve HEK293T cells supplemented with ribosome-depleted rabbit reticulocyte lysate (RRL) and then conducted an in vitro translation assay (i.e., hybrid translation, Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) (see figure above and Figure 5A). Indeed, we observed that removal of the ribosomes from RRL decreased protein synthesis in vitro and that the addition of ribosomes from HEK293T cells efficiently recovered the activity (see Figure 5 — figure supplement 1A).

To test the effect on Tyr codon elongation, we harnessed the fusion of Renilla and firefly luciferases; this system allows us to detect the delay/promotion of downstream firefly luciferase synthesis compared to upstream Renilla luciferase and thus to focus on elongation affected by the sequence inserted between the two luciferases (Kisly et al. NAR 2021) (see figure above and Figure 5A). For better detection of the effects on Tyr codons, we used the repeat of the codon (×39, the number was due to cloning constraints in our hands). We note that the insertion of Tyr codon repeats reduced the elongation rate (or processivity), as we observed a reduced slope of downstream Fluc synthesis (see Figure 5 — figure supplement 1B).

Using this setup, we observed that, compared to ribosomes from naïve cells, RPL3 methylation-deficient ribosomes led to faster elongation at Tyr repeats (see Figure 5B). These data, which are directly reflected by the ribosomes possessing unmethylated RPL3, provided solid evidence of a link between RPL3 methylation and translation elongation at Tyr codons.

2) The obvious discrepancy between the recent NAR an this study lies in the ribosomal profiling results (such as Fig.S5). The cell line specific regulation between HAP1 (previously used in NAR) vs 293T cell used here ( in this study) needs to be explored. For example, would METLL18 KO in HAP1 cells cause polysome profiling difference in this study? Some of negative findings in this study (such as Fig.S3B, Fig.S5A) would need some kind of positive control to make sure that the assay condition would be working.

According to the reviewer’s suggestion, we conducted polysome profiling of the HAP1 cells with METTL18 knockout. For this assay, we used the same cell line (HAP1 METTL18 KO, 2-nt del.) as in the earlier NAR paper. As shown in Figure 9 — figure supplement 2A and 2B, we observed reduced polysomes in this cell line, as observed in the NAR paper.

We did not find the abundance of 40S and 60S by assessing the rRNAs and the complex mass in the sucrose gradient (see Figure 9 — figure supplement 2C-E) by METTL18 KO in HAP1 cells. This observation was again consistent with earlier reports.

Overall, our experiments in sucrose density gradient (polysome and 40S/60S ratio) were congruent with NAR paper. A difference from our finding in HEK293T cells was the limited effect on polysome formation by METTL18 deletion (Figure 4 — figure supplement 1A and 1B). To further provide a careful control for this observation, we induced a 60S biogenesis delay, as requested by the Reviewer. Here, we treated cells with siRNA targeting RPL17, which is needed for proper 60S assembly (Wang et al. RNA 2015). The quantification of SDG showed a reduction of 60S (see figure below and Figure 3 — figure supplement 1D-F) and polysomes (see Figure 4 — figure supplement 1C and 1D), highlighting the weaker effects of METTL18 depletion on 60S and polysome formation in HEK293T cells. We note that all the sucrose density gradient experiments were repeated 3 times, quantified, and statistically tested.

To further assess the difference between our data and those in the earlier NAR paper, we also performed ribosome profiling on 3 independent KO lines in HAP1 cells, including the one used in the NAR paper (METTL18 KO, 2-nt del.). Indeed, all METTL18 KO HAP1 cells showed a reduction in footprints on Tyr codons, as observed in HEK293 cells (see Figure 4H), and thus, there was a consistent effect of RPL3 methylation on elongation irrespective of the cell type. On the other hand, we could not find such a trend (see figure below) by reanalysis of the published data (Małecki et al. NAR 2021).

Thus far, we could not find the origin of the difference in ribosome profiling compared to the earlier paper. Culture conditions or other conditions may affect the data. Given that, we amended the discussion to cover the potential of context/situation-dependent effects on RPL3 methylation.

3) For loss-of-function studies of METLL18, it will be beneficial to have a second sgRNA to KO METLL18 to solidify the conclusion.

We thank the reviewer for the constructive suggestion. Instead of screening additional METTL18 KO in HEK293T cells, we conducted additional ribosome profiling experiments in HAP1 cells with 3 independent KO lines. In addition to ensuring reproducibility, these experiments should assess whether our results are specific to the HEK293T cells that we mainly used. As mentioned above, even in the different cell lines, we observed faster elongation of the Tyr codon by METTL18 deficiency.

4) In addition to loss-of-function studies for METLL18, gain-of-function studies for METLL18 would be helpful for making this study more convincing.

Again, we thank the reviewer for the constructive suggestion. To address this issue, we conducted RiboTag-IP and subsequent ribosome profiling. Here, we expressed Cterminal FLAG-tagged RPL3 of its WT and His245Ala mutant, in which METTL18 could not add methylation (Figure 2A), in HEK293T cells, treated the lysate with RNase, immunoprecipitated FLAG-tagged ribosomes, and then prepared a ribosome profiling library (see figure below, left). This experiment assessed the translation driven by the tagged ribosomes. Indeed, we observed that, compared to the difference in Tyr codon elongation in METTL18 KO vs. naïve cells, His245Ala provided weaker impacts (see figure below, right). Given that METTL18 KO provides unmodified His, the enhanced Tyr elongation may be mediated by the bare His but not by Ala in that position. Since this point may be beyond the scope of this study, we omitted it from the manuscript. However, we are happy to add the data to the supplementary figures if requested.

Reviewer #3 (Public Review):

In this article, Matsuura-Suzuki et al provided strong evidence that the mammalian protein METTL18 methylates a histidine residue in the ribosomal protein RPL3 using a combination of Click chemistry, quantitative mass spectrometry, and in vitro methylation assays. They showed that METTL18 was associated with early sucrose gradient fractions prior to the 40S peak on a polysome profile and interpreted that as evidence that RPL3 is modified early in the 60S subunit biogenesis pathway. They performed cryo-EM of ribosomes from a METTL18-knockout strain, and show that the methyl group on the histidine present in published cryo-EM data was missing in their new cryo-EM structure. The missing methyl group gave minor changes in the residue conformation, in keeping with the minor effects observed on translation. They performed ribosome profiling to determine what is being translated efficiently in cells with and without METTL18, and found decreased enrichment of Tyrosine codons in the A site of ribosomes from cells lacking METTL18. They further showed that longer ribosome footprints corresponding to sequences within ribosomes that have already bound to A-site tRNA contained less Tyrosine codons in the A site when lacking METTL18. This suggests methylation normally slows down elongation after tRNA loading but prior to EF-2 dissociation. They hypothesize that this decreased rate affects protein folding and follow up with fluorescence microscopy to show that EGFP aggregated more readily in cells lacking METTL18, suggesting that translation elongation slow down mediated by METTL18 leads to enhanced folding. Finally, they performed SILAC on aggregated proteins to confirm that more tyrosine was incorporated into protein aggregates from cells lacking METTL18.

The article is interesting and uses a large number of different techniques to present evidence that histidine methylation of RPL3 leads to decreased elongation rates at Tyrosine codons, allowing time for effective protein folding.

We thank the reviewer for the positive comments.

I agree with the interpretation of the results, although I do have minor concerns:

1) The magnitude of each effect observed by ribosome profiling is very small, which is not unusual for ribosome modifications or methylation. Methylation seems to occur on all ribosomes in the cell since the modification is present in several cryo-EM structures. The authors suggest that the modification occurs during biogenesis prior to folding and being inaccessible to METTL18, so it is unlikely to be removed. For that reason, I do not think it is warranted to claim that this is an example of a ribosome code, or translation tuning. Those terms would indicate regulated modifications that come on and off of proteins, but the authors have not presented evidence that the activity is regulated (and don't really need to for this paper to be impactful).

We thank the reviewer for making this point, and we agree that the nuance of the wording may not fit our results. We amended the corresponding sentences to avoid using the terms “ribosome code” and “translation tuning” throughout the manuscript.

2) In Figure 4-supplement 1, it appears there are slightly more 80S less 60S in the METTL18 knockout with no change in 40S. It might be normal variability in this cell type, but quantitation of the peaks from 2 or more experiments is needed to make the claim that ribosome biogenesis is unaffected by METTL18 deletion. Likewise, the authors need to quantitate the area under the curve for 40S and 60S levels from several replicates and show an average -/+ error for figure 3, supplement 1 because that result is essential to claim that ribosome biogenesis is unaffected.

Accordingly, we repeated all the sucrose density gradient experiments 3 times, quantified the data, and statistically tested the results. Even in the quantification, we could not find a significant change in either the 40S or 60S levels by METTL18 deletion in HEK293T cells (see Figure 3 — figure supplement 1B and 1C).

Moreover, for the positive control of 60S biogenesis delay, we treated cells with siRNA targeting RPL17, which is needed for proper 60S assembly (Wang et al. RNA 2015). The quantification of SDG showed a reduction in 60S (see figure below and Figure 3 — figure supplement 1D-F) and polysomes (see Figure 4 — figure supplement 1C and 1D), highlighting the weaker effects of METTL18 depletion on 60S and polysome formation.

3) The effect of methylation could be any step after accommodation of tRNA in the A site and before dissociation of EF-2, including peptidyl transfer. More evidence is needed for claiming strongly that methylation slows translocation specifically. This could be followed up in vitro in a new study.

We truly thank the reviewer for the suggestion. Accordingly, we set up experiments combined with hybrid in vitro translation (Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) and the Renilla–firefly luciferase fusion reporter system (Kisly et al. NAR 2021) (see Figure 5A).

To test the impact of RPL3 methylation on translation directly, we purified ribosomes from METTL18 KO cells or naïve HEK293T cells supplemented with ribosome-depleted rabbit reticulocyte lysate (RRL) and then conducted an in vitro translation assay (i.e., hybrid translation, Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) (see figure above and Figure 5A). Indeed, we observed that removal of the ribosomes from RRL decreased protein synthesis in vitro and that the addition of ribosomes from HEK293T cells efficiently recovered the activity (see Figure 5 — figure supplement 1A).

To test the effect on Tyr codon elongation, we harnessed the fusion of Renilla and firefly luciferases; this system allows us to detect the delay/promotion of downstream firefly luciferase synthesis compared to upstream Renilla luciferase and thus to focus on elongation affected by the sequence inserted between the two luciferases (Kisly et al. NAR 2021) (see figure above and Figure 5A). For better detection of the effects on Tyr codons, we used the repeat of the codon (×39, the number was due to cloning constraints in our hands). We note that the insertion of Tyr codon repeats reduced the elongation rate (or processivity), as we observed a reduced slope of downstream Fluc synthesis (see Figure 5 — figure supplement 1B).

Using this setup, we observed that, compared to ribosomes from naïve cells, RPL3 methylation-deficient ribosomes led to faster elongation at Tyr repeats (see Figure 5B). These data, which are directly reflected by the ribosomes possessing unmethylated RPL3, provided solid evidence of a link between RPL3 methylation and translation elongation at Tyr codons.

Author Response

Reviewer #3 (Public Review):

The import of soluble precursor proteins into the mitochondrial matrix is a complex process that involves two membranes, multiple protein interactions with the translocating substrate, and distinct forms of energetic input. The traditional approaches for in vitro measurement of protein translocation across membranes typically involve radiography or immunodetection-based assays. These end-point approaches, however, often lack optimal resolution to analyze the sequential processes of protein transport. Therefore, the development of techniques to dissect the kinetic steps of this process will be of great interest to the field of protein trafficking.

This study by Ford et al. employs a novel bioluminescence-based technique to analyze the import of presequence-containing precursors (PCPs) into the mitochondrial matrix in real time. As a follow-up study to previous work from the Collinson group (Pereira et al. 2019), this approach makes use of the split NanoLuc luciferase enzyme strategy, whereby mitochondria are isolated from yeast expressing matrix localized 'LgBiT' (encoded by the mt-S11 gene) and used for import experiments with purified PCPs containing 'SmBiT' (the 11-residue pep86 sequence). The light intensity that results from the high-affinity interaction of pep86 with mt-S11 is convincingly shown in this study to be a reliable reporter of protein import into the matrix space. Therefore, from a technical stance, this appears to be a very promising approach for making high-resolution measurements of the different kinetic steps of protein translocation.

The authors leverage this technology to seek insights into several features of mitochondrial protein import, with some observations challenging key longstanding paradigms in the field. Using series of PCP constructs differing in length and placement of the pep86 peptide, the authors perform luminescence-based import tests with varying protein concentration, energetic input, and presequence charge distribution. Fits to the time course data suggest two main kinetic steps that govern matrix-directed import: transit of the PCP across the TOM complex into the IMS and association of the PCP with the TIM23 motor complex. The results support some very interesting insights into TIM23-mediated protein import, including: that precursor accumulation is strongly dependent on length; that the kinetically limiting step of IM transport is engagement with the TIM23 complex, not transmembrane transport itself; and that presequence charge distribution differently affects import rate and matrix accumulation. The results of this study appear repeatable among samples and the mathematical fits to time courses are well explained. However, there remain some questions about the nature of the experimental approach and the interpretation of the kinetics data in terms of the underlying biological processes. These questions are as follows:

Major points

Overall system characterization and mathematical analysis

1) The Western-based characterization of the amount of matrix-localized 11S (shown in Figure 1 - figure supplement 1) shows that the concentration of 11S varies significantly (> twofold concentration difference, quantified as a ratio to Tom40) among yeast/mitochondria preps. Is there a particular reason for this large variability? Perhaps more significantly, the import efficiency (judged by luminescence amplitude) shows high batch variability as well (> twofold efficiency difference). While this series of experiments makes the case that the luminescence readout of import is not limited by matrix-localized 11S, it does raise a potential concern of batch-to-batch variation in import competence. Could this have any implications for the reproducibility of results by this assay, particularly regarding the kinetic parameters reported?

It is very difficult to know what causes this variability as it can be seen even between triplicate preparations carried out on the same day. It could be due to slight differences in the flasks used to grow cells (such as the size of the baffles). However, we have determined that the variability in 11S concentration does not correlate with import competence (Figure 1 – figure supplement 1C), and that the kinetics of import are not affected (Figure 1 – figure supplement 2C).

2) My understanding from the Pereira 2019 JMB paper is that the yeast expressing the matrix-targeted 11S were engineered so that the 11S construct contained a 35 residue presequence from ATP1. In Figure 1 - figure supplement 1, panel A, it looks like the mitochondria-derived 11S constructs are significantly larger than the purified 11S constructs used to calibrate concentration. If the added residues on the mitochondrial 11S constitute a presequence, then they should be cleaved up on import to yield the mature sized protein. Why are the mitochondrial 11S constructs so much larger than the purified ones? Explicit labeling of MW markers would be useful here.

We noted that it seemed likely that the presequence was not getting cleaved off. There may also be some kind of SDS-PAGE mobility issues for 11S (common for beta-barrels), such that the purified version has a different mobility to the matrix localised version. Therefore, the possibility remains that the MTS is cleaved off, but the mature product migrates anomalously on gels. For this reason we carried out experiments to show that 11S is matrix localised, which turned out to be the case (Figure 1 – figure supplement 1D). So irrespective non-MTS cleavage, or unexpected gel mobility of correctly processed 11S, the reporter is where it should be – in the matrix. These points are elaborated in the text.

Labels have been added to molecular weight markers, as requested.

3) From Figure 1D, given that the amplitude linearly increases with added Acp1pep86 up to ~45 nM, this suggests that matrix-localized 11S is in stoichiometric excess of imported peptide within this range of added substrate. Given a matrix [11S] of 2.8 uM, a stoichiometrically equivalent amount of Acp1-pep86 would be equivalent to an import of <0.5% of added substrate, and it is suggested that import efficiency is actually much lower than that. How can this very low import efficiency be explained?

Import is single turnover under our assay conditions and is therefore limited by the number of import sites rather than matrix [11S]. Under standard conditions, we intentionally add substrate in vast excess and only anticipate that a very small proportion will be imported.

4) Apropos of point #3 above: Given the low efficiency of import observed for the purified PCP substrates in this study, one wonders if this due to the formation of off-pathway (translocation incompetent) precursors established during the import reaction, before substrates have a chance to engage OM receptors (e.g., due to aggregation, etc.) In this case, the interpretation of single-turnover conditions may instead be caused by a vast majority of PCP losing translocation competence, rather than the requirement for energetic resetting that is suggested. Might this be a possibility?

We anticipate that some PCP will aggregate and add substrate in excess to allow for that. Our interpretation of the reaction as single turnover was drawn from a comparison of PCP-pep86-DHFR import amplitude in the presence versus absence of MTX, rather than amplitudes from absolute amounts of PCP. We cannot think of a reason why MTX would affect protein solubility.

5) Import time courses in many cases show a progressive drop in luminescence at later time points after a maximum value has been reached. This reduction in signal cannot be accounted for by the two rate constants in the equation used in two-step kinetic model. How were such luminescence deviations accounted for when fitting data to obtain these kinetics parameters? What might be the reason for this downward drift in signal once maximum amplitude has been reached?

We almost always see this gradual drop in luminescence in both the mitochondrial and bacterial systems. The data points acquired after the amplitude are excluded for the fitting. The assay is based on an enzymatic reaction and we think that the downward drift is due to a combination of substrate depletion and accumulation of reaction products.

Import kinetics: dependence on total protein size

6) In Figure 3 - figure supplement 1, some of the kinetic parameters from the PCP concentration-dependent responses are quite noisy. For instance, responses for the shortest constructs (L and DL) show a lot of variability in the k1 and k2 parameters. Is this (partly) due to difficulty in resolving these two parameters during the nonlinear least-squares fitting protocol for these particular constructs?

It is difficult to resolve k1 and k2 perfectly, so the numbers are only estimates.

7) The data in Figure 3, panels E and F (derived from Figure 3 - figure supplement 1) in some cases show non-linear dependence of kinetic parameters on the 'N to pep86 distance' for the length (panel E) and position (panel F) variants. For instance, from the length series, the k1 mean goes from 132 to 385 to 237 nM for the DL, DDL, and DDDL constructs, respectively. The variances suggest that these differences are real. Is there a reason that kinetic parameters would have such non-monotonic dependence on length?

We don’t know the reason for this variance, but it could be investigated in future studies.

Import kinetics: dependence on energetic input

8) The data of Figure 4A show the results of partial dissipation of the membrane potential by 10 nM valinomycin. Most studies designed to cause a gradual dissipation of membrane potential do so by protonophore (e.g., CCCP) titration. Given that matrix-directed import is completely blocked by low micromolar amounts of this potent ionophore, it would be useful to have an independent readout (e.g., TMRM measurements) of the residual membrane potential that exists upon treatment with the lower concentrations of valinomycin used here.

We have now included data that shows the partial effect of 10 nM valinomycin on membrane potential (TMRM measurements) and protein import (Figure 4 – figure supplement 1A-B).

9) The step associated with k1, designated as transport across the TOM complex, is suggested to go to completion before starting the step associated with k2, engagement of the TIM23 complex. The k1 step shows a strong dependence on membrane potential (Fig. 4A, middle), particularly for the length series. Why would this be, given that no part of translocation across the OM should be associated with a valinomycin-sensitive electric potential?

This effect is relatively small and mainly affects shorter PCPs. Our interpretation is that passage of the PCP through TOM is reversible, and committing PCP to import across the IMM (which requires ∆ψ) prevents this reversibility. However, it is also possible that transport through TOM and TIM23 are partially coupled. Both these possibilities are discussed in the discussion.

Working model

10) One of the most surprising outcomes of this study is that passive transport of substrates across the TOM complex and energy-coupled transport via the TIM23 complex are kinetically separable and independent events. As the authors note in the Discussion, the current paradigm of the field is that matrix-targeted substrates concurrently traverse the OM and IM via the TIM-TIM23 supercomplex, and this model is supported by quite a bit of experimental evidence. Even in this study, the fact that the PCP-pep86-DHFR construct exposes the pep86 sequence to the matrix in the presence of MTX (Figure 2) is evidence of a two membrane-spanning intermediate. Key mechanistic questions arise regarding the model proposed in this study. For example, if PCPs traverse the TOM complex as a stand-alone step, what is the driving force (e.g., a simple pathway of protein interactions with increasing affinity)? And would soluble, matrix-directed substrates be expected to accumulate in the very restricted space of the IMS? If so, how would TIM23directed membrane proteins keep from aggregating in the aqueous IMS? These questions would be worth addressing in the discussion of the model.

We have included a discussion of the experimental evidence for TOM-TIM23 supercomplexes. The acid chain hypothesis has been proposed as the driving force for PCP transport though TOM ‒ an interaction between positive charges of the presequence and negatively charged residues within the TOM40 channel. Proteins that are targeted to the IMS are imported through TOM without the participation of TIM23 and we think that matrix-targeted proteins can do the same. This could explain why TOM is in excess over TIM23. We also think that some matrix-targeted PCPs can accumulate in the IMS, although this may not be true of membrane proteins.

Import kinetics: dependence on MTS charge distribution

11) The fact that import rates are increased with a more electropositive presequence makes sense in terms of the electrophoretic pull exerted on the PCP (matrix, negative). However, the greater accumulation of precursors containing more electronegative presequences remains puzzling. In the manuscript, this is explained based on the concept that accumulation of positive charges will cause partial collapse the membrane potential. However, I am still uncertain about this explanation for a few reasons. First, for each PCP, the presequence will constitute just a small fraction of the total length of the precursor, and therefore contribute a small fraction of the total charge density of imported protein. Would such a small change in total PCP charge be expected to have the dramatic effect observed among samples?

The majority of the total PCP charge is from the mature region, and whilst the positive charges in the presequence undoubtedly deplete ∆ψ, the differences in extent of ∆ψ depletion that we see between PCPs that vary in charge, is due to the difference in charge of the mature regions (as their presequences are identical).

Second, given the small amount of protein imported under these conditions, would the total charge of imported PCPs be expected to affect transmembrane ion distribution so significantly? For instance, as I recall, it takes up to micromolar amounts of mitochondria-targeted lipophilic cations (e.g., TPP+) to cause a major change in the TMRM-detected membrane potential.

The effect was indeed unexpected. Despite the seemingly small number of PCPs that are imported, the total number of charged residues will be much greater.

Finally, I would expect isolated mitochondria to be capable of respiratory control. It is well known, for example, that isolated mitochondria can respond to temporary draw-down of the membrane potential (e.g., by ADP/Pi addition) by going into state 3 respiration and restoring membrane gradients. Why would that not be the case here (Figure 5D)?

The isolated mitochondria that we used for the import assays demonstrate increased O2 consumption in response to ADP addition, as expected (Figure 5 – figure supplement 1A-B). In addition to this new figure, we have now included TMRM data (Figure 6 – figure supplement 2B) that shows a depletion of ∆ψ in response to ADP addition, that is temporary and dependent on the amount of ADP added. We are therefore confident that our isolated mitochondria are capable of respiratory control as expected. We think that the lack of restoration of ∆ψ, following import-induced dissipation, is a consequence of the import process in vitro. Perhaps the import process compromises the channel resulting in concomitant ion/ charge dissipation during the active process. Moreover, this is likely to be exacerbated in vitro upon acute exposure to PCP, causing a sudden saturation of the import sites – thereby compromising the ∆ψ and the mitochondria’s ability to rapidly recover (this possibility has been noted in the MS).

General

12) Although the spectral approach in this study is developed as an alternative to the more traditional import assays, it would be useful to have some control import tests (done with Westerns or autoradiography) as complements to the luminescence-based imports. For example, control tests to accompany Figure 1 that show import efficiency or tests that accompany Figure 3 to show import of the different length and position series constructs. Perhaps this could be done with immunodetection of Acp1 or the pep86 epitope, showing protease-protected, processed import substrates that appear in a membrane potential/ATP-dependent manner. Even if the results from the more traditional techniques ran contrary to the results using the NanoLuc system, this would still allow the authors to compare which effects are consistent and which are dissimilar between different approaches.

We have now included a Western blot import assay for the PCP-pep86-DHFR substrate and show that import is ∆ψ-dependent (Figure 2 ‒ figure supplement 1).

13) The authors might also consider conducting imports with mitoplasts as a way to test the kinetic model that includes the TIM23-mediated step alone.

We conducted import assays with mitoplasts and have now included this as a main Figure 5.

14) It is difficult to follow the logic in the Discussion regarding the number of TIM23 sites limiting the number of 11S imported into mitochondria in live cells (page 15, lines 23-27). Are the authors suggesting that in vivo, one TIM23 complex serves to transport a single protein? This needs to be clarified.

This has been removed, and this section of the discussion has been clarified.

Author Response

Reviewer #1 (Public Review):

The paper is very well written, the question is interesting, and the analyses are innovative. However, I do have concerns about the overall approach. My main concern is about looking at asymmetries in the low dimensional representation of connectivity. A secondary concern has to do with looking at the parcellated connectome. I explain these concerns in succession below.

We thank the Reviewer for the appreciation of our work and the insightful comments, which we have addressed below. The page numbers are corresponding to the clean version of the manuscript.

The first concern is to me quite a fundamental issue: looking at connectivity in a low dimensional space, that of the laplacian eigenvectors. There are two issues with this. The first one, which is less important than the second, is that the authors have a reference embedding to which they align other embeddings using a procrustes method with no scaling. While the 3D embedding is still optimally representing the connectivity (because distances don't change under rotations), we can no longer look at one axis at a time, which is what the authors do when they look at G1. In this case, G1 is representative of the connectivity of the reference matrix (LL), but not the others.

But even if the authors only projected their matrices onto a single G1 dimension with no procrustes (and only sign flipping if necessary), there is still a major issue. One implicit assumption of this whole approach is that if there is a change in connectivity somewhere in the original matrix, the same "nodes" of the matrix will change in the embedding. This is not the case. Any change in the original matrix, even if it is a single edge, will affect the positions of all the nodes in the embedding. That is because the embedding optimises a global loss function, not a local one.

To make this point clear, consider the following toy example. Say we have 4 brain regions A,B,C,D. Let us say that we have the following connectivity:

In the Left Hemisphere: A-B-C-D

In the Right Hemisphere: A-B=C-D

So the connection between B and C is twice as strong in the right hemi, and everything else remains the same.

The low dimensional embedding of both will look like this:

Left: ... A ... B ....... C ... D ...

Right A... ... ... B ... C ... ... ... D

Note how B,C are closer to each other in the RIGHT, but also that A,D have moved away from each other because the eigenvector has to have norm 1.

So if we were to calculate an asymmetry index, we would say that:

A is higher on the LEFT

B is higher on the RIGHT

C is higher on the LEFT

D is higher on the RIGHT

So we have found asymmetry in all of our regions. But in fact the only thing that has changed is the connection between B and C.

This illustrates the danger of using a global optimisation procedure (like low-dim embedding) to analyse and interpret local changes. One has to be very careful.

We thank the Reviewer for the detailed description of the first concern. We agree that low-dimensional embeddings describe global embedding of local features, rather than local phenomena. Moreover, we indeed assume that the connectivity embedding of a given node gives us information about its position along ‘gradients’ relative to other nodes and their respective embedding. Thus, indeed, when a single node (node X) has a different connectivity profile in the right hemisphere relative to the left, this will also have some impact on the embeddings of all nodes showing a relevant (i.e., top 10%) connection to node X.

To evaluate whether asymmetry could be observed in average connectivity within functional networks, an alternative approach to measure asymmetry was taken by computing average connectivity within different functional networks. Following we compared the within-network connectivity between left and right. We have now added this conceptual analysis to our results robustness analysis section. In short, we observed that transmodal networks (DMN, FPN, and language network) showed higher connectivity in the left hemisphere but other networks showed higher connectivity in the right hemisphere. Thus, this indicates that observations made with respect to asymmetry of functional gradients are similar to those observed for within-network functional asymmetry between the left and right hemispheres. We have now detailed the outcome of this analysis in our Result section and Supplementary Materials.

Results, p.14.: “As low-dimensional embedding is a global approach to summarize functional connectivity we reiterated our analysis by evaluating asymmetry of within network functional connectivity in the current sample. Observations made with respect to asymmetry of functional gradients are similar to those observed for within-network functional asymmetry between the left and right hemispheres.”

“To further explore functional connectivity asymmetry between left and right hemispheres, we calculated the LL within network FC and RR within network FC (Figure 2-figure supplement 5). It showed that connections in the left hemisphere and right hemisphere were relatively equal in the global scale. However, for the local differences, networks showed significant subtle leftward or rightward asymmetry (vis1: t = -5.203, P < 0.001; vis2: t = -22.593, P < 0.001; SMN: t = -8.262, P < 0.001; CON: t = -32.715, P < 0.001; DAN: t = -11.272, P < 0.001; Lan.: t = 33.827, P < 0.001; FPN: t = 24.439, P < 0.001; Aud.: t = 0.191, P = 0.849; DMN: t = 11.303, P < 0.001; PMN: t = -35.719, P < 0.001; VMN: t = -11.056, P < 0.001; OAN: t = 0.311, P = 0.756).”

Irrespectively, we have further highlighted that such a global interpretation for asymmetry of areas is still meaningful, given that a node is always placed in a global context. We have now further explained that our metrics give insights in local embedding of global phenomena in the introduction, p. 3.

Introduction, p. 3: “These low-dimensional gradient embeddings describe global embedding of local features, rather than local phenomena. Thus, interpretation for asymmetry of areas is under a global context.”

My second concern is about interpreting the brain asymmetry as differences in connectivity, as opposed to differences in other things like regional size. The authors use a parcellated approach, where presumably the parcels are left-right symmetric. If one area is actually larger in one hemisphere than in the other, the will manifest itself in the connectivity values. To mitigate this, it may be necessary to align the two hemispheres to each other (maybe using spherical registration) using connectivity prior to applying the parcellation.

Thanks for this nice idea. We have now computed the differences of the mean rsfMRI connectome along the first gradient at the vertex level using 100 random subjects, as we have the data mapped to a symmetric template (fs_LR_32k), indicating that each vertex has a symmetric counterpart in the right hemisphere. Our results show left-right asymmetry as language/default mode-visual-frontoparietal vertices, which is consistent with the main results of the parcel-based approach. We have also added this response to the Supplementary materials.

Though overall findings are consistent, spherical registration may also have new issues. Total anatomical spatial symmetry may not provide functional comparability at the vertex level between left and right hemisphere. For example, during language tasks in the current sample, the activated frontal region in the left hemisphere is larger than the activated contralateral region in the right hemisphere. In the current study, we aimed to evaluate asymmetry between functionally and structurally homologous regions, as described by the Glasser atlas. In case of the resting state fMRI data, we used the region-wise symmetric multimodal parcellation (Glasser et al., 2016). This parcellation ensures the functional contralateral regions in both hemispheres. A previous study (Williams et al., 2021) investigated the structural and functional asymmetry in newborn infants. They used spherical registration (make fs_LR symmetric) for structural asymmetry but not for functional asymmetry. As such spheric registration may hide functional information, we think spherical registration may be more suitable for structural studies.

To address the concern regarding the alignment of hemispheres, we used joint alignment for LL and RR to compare the results between this and the Procrustes alignment technique (Pearson r=0.930, P_spin<0.001), below is the figure of asymmetry along the principal gradient (upper: joint alignment, below: Procrustes alignment) indicating convergence between both approaches. We have reported this information in the Supplementary Materials.

Lastly, we do agree that parcel size might be an important issue influencing the asymmetry pattern. To test for such an effect, we performed the correlation between the rank of parcel size (left-right)/(left+right) and rank of asymmetry index. It suggests only a small insignificant correlation along G1 (Spearman r_intra=0.130, P_spin=0.105; Spearman r_inter=0.130, P_spin=0.084). Of note, there is a systematic difference in parcel size as a function of sensory-association hierarchy, indicating that the link between parcel-size and asymmetry may vary as a function of sensory vs associative regions.

Reviewer #2 (Public Review):

Using recently-developed functional gradient techniques, this study explored human brain hemispheric asymmetry. The functional gradient is a hot technique in recent years and has been applied to study brain asymmetries in two papers of 2021. Compared to previous studies, the current study further evaluated the degree of genetic control (heritability) and evolutionary conservation for such gradient asymmetries by using human twin data and monkey's fMRI data. These investigations are of value and do provide interesting data. However, it suffers from a lack of specific hypotheses/questions/motivations underlying all kinds of analyses, and the rich observational or correlational results seem not to offer significant improvement of theoretical understanding about brain asymmetries or functional gradient. In addition, given the limited number of twins in HCP project (for a heritability estimation), the limited number of monkeys (20 monkeys), and the relatively poor quality of monkeys' resting functional MRI data, the results and conclusion should be taken cautiously. Below are major concerns and suggestions.

We thank the Reviewer for the evaluation of our work and the helpful suggestions.

The gradient from resting-state functional connectome has been frequently used but mainly at the group level. The current study essentially applied the gradient comparison (i.e., gradient score) at the individual level. Biological interpretation for individual gradient score at the parcel level as well as its comparability between individuals and between hemispheres should be resolved. This is the fundamental rationale underlying the whole analyses.

We thank the Reviewer for this remark, and are happy to provide further rationale for using and comparing individual gradients scores to evaluate individual variation in asymmetry and associated heritability. Though gradients from resting-state functional connectivity have been frequently used at the group level, various studies have also studied individual differences. For example, using linear mixed models to compare gradient scores between left and right across subjects (Liang et al., 2021), applying the individual gradient scores to compare disease and controls (Dong et al., 2020, 2021; Hong et al., 2019; Park et al., 2021), and link individual hippocampal gradients to memory recollection (Przeździk et al., 2019). Together, these studies show individual variations of local gradients, indicating changes in node centrality and hubness (Hong et al., 2019), and connectivity profile distance (Y. Wang et al., 2021). Of note, low-dimensional embeddings describe global embedding of local features, rather than local phenomena. Thus, interpretation for asymmetry of areas is under a global context. The biological interpretation for individual gradients would be to what degree the system segregated and integrated has changed patterns of ongoing neural activity (Mckeown et al., 2020). It reflects that individuals have different functional boundaries between anatomical regions. Whereas, individual neurons are embedded under the global-local boundaries through a cortical wiring space consisting of intricate long- and short-range white matter fibers (Paquola et al., 2020).

Introduction, p. 4: “We applied the individual gradient scores to study the asymmetry, consistent with prior studies (Gonzalez Alam et al., 2021; Liang et al., 2021). Individual variation along the gradients reflects a global change across subjects in the functional connectome integration and segregation, and it is under genetic control (Valk et al., 2021). Moreover, to what degree the system segregated and integrated relates to patterns of ongoing neural activity (Mckeown et al., 2020), and different individuals have different functional boundaries between anatomical regions.”

Results, p. 5: “Next, individual gradients were computed for each subject and the four different FC modes and aligned to the template gradients with Procrustes rotation. It rotates a matrix to maximum similarity with a target matrix minimizing sum of squared differences. As noted, Procrustes matching was applied without a scaling factor so that the reference template only matters for matching the order and direction of the gradients. Therefore, it allows comparison between individuals and hemispheres. The individual mean gradients showed high correlation with the group gradients LL (all Pearson r > 0.97, P spin < 0.001).”

Only the first three gradients are used but why? What about the fourth gradient? Specific theoretical interpretation is needed. At the individual level, is it ensured that the first gradients of all individuals correspond to each other? In this study, it is unclear whether we should or should not care about the G2 and G3. The results of G2 and G3 showed up randomly to some degree.

In the current study we focused on the principal gradient in the main analysis, given its association with sensory-transmodal hierarchy, microstructure, and evolutionary alterations (Margulies et al., 2016; Paquola et al., 2019; Xu et al., 2020).

Conversely, gradient 2 reflects the dissociation between visual and sensory-motor networks and gradient 3 is linked to task-positive, control, versus ‘default’ and sensory-motor regions. We analyzed asymmetry and its heritability of the first three gradients (explaining respectively 23.3%, 18.1%, and 15.0% of the variance of the rsFC matrix). However, we extracted the first ten gradients to maximize the degree of fit (Margulies et al., 2016; Mckeown et al., 2020). We have now also shown G4-10 mean asymmetry results as a supplementary figure. To ensure correspondence of gradients across individuals, we aligned the individual gradients to the group level template with Procrustes rotation. Procrustes rotation rotates a matrix to maximum similarity with a target matrix minimizing sum of squared differences. The approach is typically used in comparison of ordination results and is particularly useful in comparing alternative solutions in multidimensional scaling. Figure S1 shows the mean gradients across subjects of each FC mode, which is close to the Figure 1D template gradient space.

Results, p. 5: “The current study analyzed asymmetry and its heritability of the first three gradients explaining most variance (Figure 1d). As they all have reasonably well described functional associations (G1: unimodal-transmodal gradient with 24.1%, G2: somatosensory-visual gradient with 18.4%, G3: multi-demand gradient with 15.1%). However, given we extracted ten gradients to maximize the degree of fit 26,52. We stated mean asymmetry of G4-10 in Figure 1-figure supplement 1.”

The intra-hemispheric gradient is institutive. However, it is hard to understand what the inter-hemispheric gradient means. From the data perspective, yes you can do such gradient comparison between the LR and RL connectome but what does this mean? Why should we care about such asymmetry? From the introduction to the discussion, the authors simply showed the data of inter-hemispheric gradients without useful explanation. This issue should be solved.

We are happy to further clarify. The LR and RL connectivity reflects cross-hemispheric functional signal interaction via corpus callosum, whose structural asymmetry is usually studied (Karolis et al., 2019). Such intra-hemispheric connections, compared to the inter-hemispheric connections, have been suggested to reflect the inhibition of corpus callosum, and underlie hemispheric specialization. Different information relies on hemispheric specialization (e.g., visual, motor, and crude information) and/or inter-hemispheric information transfer (e.g., language, reasoning, and attention) (Gazzaniga, 2000). To clarify and motivate the analysis of both intra- and inter-hemispheric asymmetry in functional gradients, we have now added further detail in the introduction, p. 5.

Here is text: Introduction, p. 4. “The full FC matrix contains both intra-hemispheric and inter-hemispheric connections. Intra-hemispheric connections, compared to the inter-hemispheric connections, have been suggested to reflect the inhibition of corpus callosum and may underlie hemispheric specializations involving language, reasoning, and attention. Conversely, inter-hemispheric connectivity may reflect information transfer between hemispheres, for example a wide range of modal and motor information, and crude information concerning spatial locations 48. Previous studies have reported intra-hemispheric FC to study gradient asymmetry 6,38. By having the callosum related to association white matter fibers, one hemisphere could develop for new functions while the other hemisphere could continue to perform the previous functions for both hemispheres 48. Therefore, in addition to the intra-hemispheric FC gradients, we depicted the inter-hemispheric FC, which is abnormal in patients with schizophrenia 23,49 and autism 24.”

as well as Discussion, p. 16 “Conversely, the transmodal frontoparietal network was located at the apex of rightward preference, possibly suggesting a right-ward lateralization of cortical regions associated with attention and control and ‘default’ internal cognition 62,63. The observed dissociation between language and control networks is also in line with previous work suggesting an inverse pattern of language and attention between hemispheres 3,64. Such patterns may be linked to inhibition of corpus callosum 65, promoting hemispheric specialization. It has been suggested that such inter-hemispheric connections set the stage for intra-hemispheric patterns related to association fibers 48. Future research may relate functional asymmetry directly to asymmetry in underlying structure to uncover how different white-matter tracts contribute to asymmetry of functional organization.”

and Discussion, p.18 “Though overall intra- and inter-hemispheric connectivity showed a strong spatial overlap in humans, we also observed marked differences between both metrics across our analysis. For example, although we found both intra- and inter-hemispheric differences in gradient organization to be heritable, only for intra-hemispheric asymmetry we found a correspondence between degree of asymmetry and degree of heritability. Similarly comparing asymmetry observed in human data to functional gradient asymmetry in macaques, we only observed spatial patterning of asymmetry was conserved for intra-hemispheric connections. Whereas intra-hemispheric asymmetry relates to association fibers, commissural fibers underlie inter-hemispheric connections 77 It has been suggested that there is a trade-off within and across mammals of inter- and intra-hemispheric connectivity patterns to conserve the balance between grey and white-matter 76. Consequently, differences in asymmetry of both ipsi- and contralateral functional connections may be reflective of adjustments in this balance within and across species. Secondly, previous research studying intra- and inter-hemispheric connectivity and associated asymmetry has indicated a developmental trajectory from inter- to intra-hemispheric organization of brain functional connectivity, varying from unimodal to transmodal areas 78,79. It is thus possible that a reduced correspondence of asymmetry and heritability in humans, as well as lack of spatial similarities between humans and macaques for inter-hemispheric connectivity may be due to the age of both samples (young adults in humans, adolescents in macaques). Further research may study inter- and intra-hemispheric asymmetry in functional organization as a function of development in both species to further disentangle heritability and cross-species conservation and adaptation.”

When aligning intra-hemispheric gradient, choosing averaged LL mode as the reference may introduce systematic bias towards left hemisphere. Such an issue also applies to LR-RL gradient alignment as well as cross-species gradient alignment. This methodological issue should be solved.

We thank the Reviewer for raising this point. Indeed, we also used RR as reference, the results were virtually identical. We have stated this in the Results, p. 13. Regarding the cross-species alignment, we averaged the left and right hemispheres to reduce the systematic bias. It showed that the correlation and comparison results remained robust. Now we have updated the method and corresponding results (p.10). Here is the text:

Results (p.15): “We also set the RR FC gradients as reference, the first three of which explained 22.8%, 18.8%, and 15.9% of total variance. We aligned each individual to this reference. It suggested all results were virtually identical (Pearson r > 0.9, P spin < 0.001).”

Results (p.10): “To reduce a possible systematic hemispheric bias during the cross-species alignment, we averaged the left and right hemisphere. We found that the macaque and macaque-aligned human AI maps of G1 were correlated positively for intra-hemispheric patterns (Pearson r = 0.345, P spin = 0.030). For inter-hemispheric patterns, we didn’t observe a significant association (Pearson r = -0.029, P spin = 0.858)”

The sample size of monkey (i.e., 20) is far less than human subjects (> 1000). Such limitation raises severe concern on the validity of the currently observed gradient asymmetry pattern in the monkey group, as well as the similarity results with human gradient asymmetry pattern. Despite the marginal significance of G1 inter-hemisphere gradient between humans and monkeys, I feel overall there is no convincingly meaningful similarity between these two species. However, the authors' discussion and conclusion are largely based on strong inter-species similarity in such asymmetry. The conclusion of evolutionary conservation for gradient asymmetry, therefore, is not well supported by the results.

We agree with your comments. Although it is a small sample compared to humans, in NHP studies, it is a relatively decent sample size (most of the studies have N<10). Of note, recent work suggested that the individual variation pattern can be captured using 4 subjects in both human and macaques (Ren et al., 2021).

To overcome potential overinterpretation of our findings, we have now changed the title to a more descriptive format: “Heritability and cross-species comparisons of asymmetry of human cortical functional organization”

And further detailed findings already in the Abstract; “These asymmetries were heritable in humans and, for intra-hemispheric asymmetry of functional connectivity, showed similar spatial distributions in humans and macaques, suggesting phylogenetic conservation.”

We have pointed out the small sample size in the limitation. Please find the text below: Discussion, p. 18: “Due to the small sample size of macaques, it is important to be careful when interpreting our observations regarding asymmetry in macaques, and its relation to asymmetry patterning observed in humans. Therefore, further study is needed to evaluate the asymmetry patterns in macaques using large datasets 53,79”

And nuanced the conclusion, p.19: “This asymmetry was heritable and, in the case of organization of intra-hemispheric connectivity, showed spatial correspondence between humans and macaques. At the same time, functional asymmetry was more pronounced in language networks in humans relative to macaques, suggesting adaptation.”

Author Response

Reviewer #2 (Public Review):

Weaknesses:

1) It is surprising that certain enzymes with established depalmitoylation activity were excluded from BrainPalmSeq data-base (e.g. ABHD4, ABHD11, ABHD12, ABHD6)

We have now included additional depalmitoylating enzymes in our database and manuscript.

2) Albeit not essential it will be of great interest to include in the established database enzymes necessary for synthesis of ACYL-CoA (e.g. ACSL enzymes). One improvement may include the ability of future researchers to add such curated analysis to the platform within future research studies.

We agree with the reviewer there are many expansions of our gene set that would be interesting to include. Given the size of the current manuscript however, for brevity we have decided at present to curate data for the core set of genes that directly regulate dynamic palmitoylation. We have also added a ‘Contact Us’ feature to the website, so that repeatedly requested genes or datasets can be added in future.

3) The experimental validation presented in figure 6 relies on over-expression of substrates and ZDHHC enzymes. This setup is known to often provide unspecific S-acylation events which result from excess enzyme or substrate availability. Hence, such validation would be greatly strengthened by loss of function experiments.

We have now done loss-of-function experiments and included results in major discussion point 1 above. If the editors/reviewers think it is appropriate to add to the manuscript, we will comply. However, as our negative data does not negate the fact that ZDHHC9 is able to palmitoylate the myelin proteins tested, but merely suggests it may not be necessary for protein palmitoylation in vivo, we do not think it strengthens the manuscript.

4) The authors relevantly use in-situ hybridization images from the Allen Brain atlas to validate their predictions. Although it is understandable that an extensive experimental validation of the predictions here established would be out of the scope of the current study, this work could be improved by validating the RNA expression at the protein level of certain abundant ZDHHC enzymes in available neuro-associated cell types.

We have now validated RNA expression at the protein level for a few palmitoylating and depalmitoylating enzymes.

5) It would be interesting if the authors would further compare the predicted association clusters (e.g. figure 1), substrates (figures 1 and 2), and S-acylation pairs (figure 4) here determine, with previous determined ZDHHC enzyme associations described in different cell types and biological systems. Alternatively, further relevant validation could include testing whether further established ZDHHC-ZDHHC cascades (e.g. ZDHHC3-7) can be also detected with specific cells or regions of the CNS.

On our website, all expression data can be downloaded below the heatmaps for each study, and the cell type expression relationships between any 2 genes can be plotted by the user to reveal cell types (if any) within which genes are co-expressed. In response to this comment and that of Reviewer 3 below, we have now performed such analysis on ZDHHC5/ZDHHC20 and ZDHHC6/ZDHHC16, which are to our knowledge the best established ZDHHC cascades. We have included these plots in new Figure 1 – figure supplement 2, along with discussion on line 172. Similar analysis has been performed on the known ZDHHC-accessory protein pairs (see below).

6) Figure 3B: it is not clear why the cluster of zdhhcs with high layer specific expression displayed at the top of the graph does not follow the low-to-high expression scale of the table.

The expression data in this figure is grouped by hierarchical clustering, rather than in order of low-to-high expression, in order to be consistent with Figure 2B. While we believe this is the better way to display the data, we are willing to modify if the editors/reviewers have a strong preference.

7) Figure 4D: the more relevant potential cooperative pairs (ZDHHCs-APTs) could be highlighted in more contrasted colours.

We thank the reviewer for this suggestion but at this stage would prefer to keep the color scheme as it is so that readers are better able to formulate their own hypotheses when observing these figures.

Reviewer #3 (Public Review):

Weaknesses:

1) There is a vast amount of data available and the description and discussion of this could be endless, but there are a few points that could be brought out in more detail. For example, the correlation (or lack of correlation) of expression of the proposed zDHHC-PAT accessory proteins with their cognate zDHHCs. The dominance of a relatively small number of zDHHC enzymes (20, 2, 17, 3, 21, 8) in the CNS also merits some discussion. Is the combination of a high-capacity, low-specificity enzyme (zDHHC3) with others that are regarded as more 'specific'? I believe none of these are ER-resident - they represent Golgi and PM?

The reviewer brings up many interesting questions. Indeed, we were hopeful that this type of mining of RNAseq data would bring to light many questions that can be followed up on in future publications.

We have addressed the correlation in expression of accessory proteins with their cognate ZDHHCs with new data.

We are unsure how to address the dominance of a relatively small number of ZDHHC enzymes (20, 2, 17, 3, 21, 8) in the CNS, beyond highlighting this expression pattern. We believe that interpretation of the expression of this in any way (e.g. co-expression of high-capacity, low-specificity enzymes (ZDHHC3) with more 'specific' ZDHHCs) would merely be speculative. However, we are open to adding further discussion with some guidance from the reviewer.

Author Response

Reviewer #1 (Public Review):

In this work, Hoye et al. analyzed a conditional mouse model for DDX3X syndrome, an important cause of neurodevelopmental disorders in humans, and provide critical insights into the pathomechanisms of this disorder. They show that homozygous loss of DDX3X in females in neural progenitors leads to microcephaly and massive apoptosis due to impaired neural progenitor cells. Furthermore, they show that conditional DDX3X KO mice are sexually dimorphic. In males, it seems that the paralog DDX3Y on the Y chromosome is also required for neurogenesis and may be partially able to compensate DDX3X function leading to comparable phenotypes of cKO males comparable to cHET females. The authors therefore mostly focus their analysis on cHET females and cKO males. The number of progenitors is increased in cHET females and cKO males. Additionally, they show that DDX3X dosage is important for proper neuron numbers. They could link the abrogated number of neuronal cell types to a globally prolonged cell cycle and identify altered cell cycle exit of radial glial cells (RGCs) as a possible explanation for fewer neurons. Finally, the authors shed light on the molecular mechanisms by which DDX3X impairs neurogenesis using ribosomal profiling (RIBO-Seq). Large-scale studies of translational profiling are rare and this dataset provides a novel and valuable resource of translational profiles in early mouse brain development to the community. In addition, their RIBO-Seq data on DDX3X deficient cells reveal an essential requirement of DDX3X for the translation of cortical progenitor-specific mRNAs. Several targets are critical for cortical development, as investigated in more detail for Setd3 in this manuscript. Overall, this study is of great importance and provides novel insights into the pathogenesis of DDX3X syndrome and the crucial role of DDX3X during cortical development.

The manuscript is well written and the data, in general, support the conclusions drawn, but some aspects need to be clarified or modified:

We thank the reviewer for carefully reading our manuscript and for their helpful suggestions.

1) I have one concern regarding the mouse model, which the authors need to better explain. It is unclear to me why the expression levels in the male cKO are reduced to levels comparable to the cHET females at D11.5 (Figure 1D, E), and not comparable to cKO females as one might expect. This to me raises the question if this is indeed a good model for male cKO of DDX3X. Do the authors have an explanation for this? Could it be that the probes/primers used here are indeed specific for DDX3X or also detecting DDX3Y, or is there is another explanation?

We apologize for the lack of clarity regarding this point. We quantified that WT females had ~25% higher levels of Ddx3x mRNA expression than WT males (Figure 1G). Thus, we originally plotted males and females separately to illustrate the reduction of Ddx3x in conditional mice relative to their sex-matched controls (original Figures 1D, E). Because females have higher levels than males at baseline, the relative reduction in Ddx3x levels in cHet females and cKO males is similar, particularly at E11. In this revision, we now plot all of the sexes together which makes it easier to compare levels across all genotypes (new Figures 1E and 1F). Our probes are specific for Ddx3x, as evidenced in Figure 2C (in which we knockdown Ddx3y but observe no change in Ddx3x).

Importantly, males also express Ddx3y, which acts redundantly with Ddx3x. While there are no available DDX3Y specific antibodies, Ddx3y is upregulated at the RNA level in cKO males (Figure 2A). Thus we posit that the overall levels of DDX3 protein in males and females is relatively similar.

2) While the increase in progenitor cells in cHET females and cKO males is convincing, the reduction in neurons is only supported by weak evidence and trends. Significance levels used to draw these conclusions are somewhat inconsistent (Figure 3 - figure supplement 2). For instance, in Figure 3 - figure supplement 2E results with a p-value of 0.2 are communicated as a trend, whereas in Figure 3 - figure supplement 2F a p-value of 0.15 is marked as no difference. Overall, the findings of reduced number of neurons during development are not well supported by the data in this manuscript, which should be improved or toned down.

We apologize for this lack of consistency and thank the reviewer for pointing it out. We have modified the text throughout the manuscript to ensure we are consistent in what we call significant. We agree that the reduction in neurons is modest, especially at E14.5 (Figure 3-figure supplement 1D). However, three additional pieces of data support the conclusion that excitatory neurons are reduced. First, the lamination at P0 clearly show significant reductions in several cortical excitatory neurons (layers V, VI, Figure 3D-G). Second, our cell cycle exit data (% EdU+Sox2-Tbr2-) supports the observation of fewer neurons (Figure 4E). Third, the live imaging reflects reduced production of neurons (Figure 5E). We thus observed significant differences at multiple timepoints (E14.5 and P0) and with multiple markers (Tbr2-Sox2-, Ctip2, Tbr1). However, we agree with the reviewer that the reduction in neurons is modest and have modified the results (p. 9 and 11) and discussion (p. 18) to reflect this modest reduction.

3) Do the authors have an explanation for why the increased cell cycle duration and reduced neuron numbers may not lead to microcephaly?

We cannot rule out subtle brain size defects with our current analysis at P0. However, in human DDX3X syndrome, the microcephaly is mild or absent in patients with nonsense mutations (microcephaly is primarily associated with missense mutations). Thus, our findings are consistent with disease pathology. We have added this point to the discussion (p. 19).

4) For their ribosomal profiling experiments, the authors focused on cKO females and males, while in the rest of the paper they argue that cKO males are actually comparable to cHET females. And then for polysome fractionation, they go back to cHET females. Those inconsistencies are not well justified in the manuscript. I am worried that those data are then not really comparable, and differences in RNA abundance that they attribute to different developmental time points in RIBO seq vs. polysome fractionation (E11.5 vs. E14.5) may actually be due to different DDX3X levels.

We thank the reviewers for this suggestion. While we did use cKO females and males for the ribosome profiling experiment, this was done for several reasons. 1) Ribo-seq is more technically challenging than a standard RNAseq experiment, so we aimed to maximize the effect of Ddx3x knockout by using the cKO females. Because of the profound apoptosis that begins at E12.5 in cKO females, we opted to do these experiments at E11.5 to avoid potential complications due to cell death and composition changes. 2) The bulk of our paper focuses on the cortical development phenotypes of the cHet females and cKO males (to best model DDX3X syndrome), with significant phenotypes at E14.5. Thus, we initially performed the polysome fractionation of these genotypes at E14.5 to determine whether any of the DDX3X-dependent translation changes might be contributing to phenotypes at this stage. We did not include cKO females in this assay because at E14.5, most of the cells in the cortex are apoptotic.

In response to reviewer concerns, in this revised manuscript we include new polysome fractionation analyses at E11.5 using cKO females and cKO males-this provides validation of Ribo-seq of the same genotypes. These data show significant enrichment in monosome fractions for 2 targets (Rcor2 and Topbp1) and trends for a 3rd (Setd3, p=0.10). This also validates the same transcripts which are altered in polysomes at E14.5 in cHet females and cKO males. We include these new data in Figures 6H, J and Figure 6- figure supplement 2A,B.

We agree that differences in RNA abundance could be due to different developmental timepoints and DDX3X levels. We have included this important possibility in the discussion and removed this point from the results.

Author Response:

We fully agree that there are more detailed theoretical descriptions of both bone mineral density and the pharmacokinetics of the considered drugs and we are aware of the details of these submodels. We deliberately chose a simplified description to keep the model computationally manageable and reduce the number of free parameters to a minimum. In our opinion, the precision with which the model can capture clinical data in even complex scenarios demonstrates that such a simplified approach is warranted. That is why we regard these model features as simplifications rather than weaknesses. We would also be happy to explain the rationale behind these simplifications in more detail in the revised manuscript.

Author Response

Reviewer #2 (Public Review):

Specific comments/concerns:

1) The section relating SCS-flight reactions to alpha responses and fear potentiated startle (FPS) is interesting and potentially important. However, parts of this narrative are unclear. First, FPS has a strong associative component but the flight reaction studied here apparently does not. Second, pairing a tone with shock increases startle reactions preceded by a tone. Here, pairing noise with shock suppresses alpha reactions. Is there evidence that pairing startle-eliciting noises with shock reduces typical startle reactions? Is the issue here that SCS-flight studies are designed poorly to demonstrate the phenomenon (pairing the whole SCS compound with shock vs pairing just the tone with shock then testing noise reactions after a tone)? Lastly, an important experiment by Totty et al (Fig 5) is not discussed. They show that SCS presentations fail to elicit flight reactions in a threatening context (previously paired with unsignaled shocks) unless they were paired with shock in an earlier phase (different context). This seems inconsistent with the FPS interpretation of SCS-flight, since the threatening context should have increased alpha reactions to the novel noise. Along with other control experiments, it also suggests that associative processes related to SCS-shock pairings make a strong contribution to flight. Perhaps there is something unique about compound stimuli paired with shock that cannot be addressed with the simple noise-shock control experiments reported here? This should be discussed in the manuscript.

We thank the reviewer for these insightful suggestions and concerns. First, we have attempted to clarify in the text that for FPS and the cue-elicited activity observed in the experiments presented here, associative fear is necessary for the behavior to be observed; but this does not mean the behavior itself is associative. For example, in FPS, what is measured is a change in the unconditional startle response when the animal is tested in an environment they fear through prior associative learning or after a discrete cue which, through fear conditioning, has acquired fearful properties. If you pair a tone with shock, later presentations of the tone will enhance startle response to a noise (the basic fear-potentiated startle effect). Again, associative fear [to the tone] is necessary, but the potentiated startle is a potentiated unconditional response to a separate noise cue.

Regarding the question of whether pairing a startle-eliciting noise with shock can reduce startle reactions, we do not believe there is prior evidence of this, making this study the first to suggest such a relationship. It is important to realize however, that without fear to the context, the noise stimulus used here supported only very low levels of startle/activity bursts if at all. Yes, we agree that SCS-flight studies are poorly designed to demonstrate the phenomenon of noise-elicited flight, as we show that not only is the compound unnecessary to produce such flight but that SCS studies which do not include standard learning controls for at least pseudoconditioning are unable to determine to what extent any flight is associative vs non-associative.

Finally, we agree that we could have spent more time addressing specific differences and contradictions between our findings and those of Totty et al. We have added one paragraph to the discussion to explicitly address Totty et al. Figure 5 as well as analysis in the results and general text in the discussion to talk about why our observations differ.

2) Sex differences have been reported for darting behavior in a Pavlovian paradigm using a single tone CS, but have not been observed in studies using a tone-noise SCS. The combined analyses here (lines 424-429) also finds no sex differences for mice conditioned with a single noise CS. However, the original reports identified only a subset of females that showed prominent darting and stronger shock reactions. Is there any evidence for this Darter vs. Non-darter classification in your dataset? Either way it would be helpful to add graphs illustrating the sex difference analysis that include data points for individuals, at least in supplemental.

We have followed this suggestion and included a Figure 11 which details the sex difference analysis described in the discussion section, including at least a visual analysis of potential sub-populations of darter vs non-darter classification. Based on the criteria set forth in Gruene et al., in our current study with mice, all animals would be classified as darters, and there were no major sex differences—certainly none which suggest greater darting in female mice.

3) Lines 432-439: This concluding paragraph is a missed opportunity for a more nuanced discussion of "active vs. passive" defense and perhaps different categories of "flight". The papers cited do not suggest that rats freeze because no other response is available (thought the Blanchards may have said this elsewhere). All the studies investigate CRs in situations where both freezing and locomotor movements are possible. Although it is true that freezing is not the absence of a response, it is the absence of movement. The distinction between movement/ambulation and immobility in threatening situations is important for describing brain circuits of defense and necessary to explain transitions to flight, escape, active avoidance, and even "choosing locations to freeze" by moving down threat gradients. Similar passive vs active terminology goes back at least to Konorski (1967), though "stationary" may be more appropriate than "passive" (Sigmundi, 1987). Related:

-Line 66: "but not activity bursts", Line 77: "Gruene et al suggest that freezing and darting were competing CRs to the same level of threat". Please clarify the Predatory Imminence Theory views on this. If conditioned rats move to the safest spot to freeze (de Oca et al, 2007), is this not an activity burst? Does the velocity of the movement matter? How do these movements relate to the startle-like responses seen at CS onset vs. the more sustained activity reported here for paired groups? de Oca 2007 describes conditioned flight to a familiar enclosure and freezing as compatible post-encounter responses to the same threat, but flight and freezing cannot occur at the same time and must be competitive.

The reviewer brings up important points and important misconceptions that we have [hopefully] addressed in the text. We have added a significant portion to the discussion to detail how we address these concerns. In this section, we attempt to make it much clearer as to our [and the literature’s] position on freezing vs flight vs immobility and active vs passive. Additionally, based both on prior literature and on an analysis of darting topography in our experiments here we suggest that initial ballistic bursts of flight to CS onset are topographically and functionally distinct from subsequent, directed bursts of locomotion which occur later in the CS and may be potentiated by CS-shock pairings. This second burst of locomotion is indeed smaller in our data and we propose that it can be thought of as a behavior that is functionally a part of the freezing suite of behaviors.

4) The notion that noise is a (weak) US requires further discussion. Specifically, how do you define a US? And are these properties necessary for the argument that apparent conditioned flight/darting reactions are non-associative startle-like reactions? Freezing goes up when rats experience noise alone trials, but this does not appear to be a result of context conditioning (no BL freezing on day 2 of training). Further, there appears to be no summation once the context is paired with shock (freezing during habituated noise; Exp 4). Noise-elicited freezing appears to sensitize in phase 1 but at the same time darting responses habituate. This pattern is unlike what one might expect for even a very weak shock. One reason this seems important: the paper begins by explaining the challenge posed by the SCS-flight paradigm and the conditioned darting paradigm. However, the studies presented here focus on noise-elicited behavior and imply that similar phenomena occur in the conditioned darting paradigm. The conditioned darting studies all use a pure tone that may not be characterized as a US. Tone-elicited behavior isn't discussed much in the manuscript, but tone-elicited darts in Experiment 2 (pseudoconditioning control) appear lower than those elicited after tone-shock pairings in Experiment 1. So it remains unclear if conditioned darting results from non-associative processes, especially if the tone does not act as a weak US.

We thank this reviewer for pointing out an area that we could be clearer. We have added a section to the discussion to address our views on how stimulus type and properties may impact the behavior observed in these experiments. Generally, our arguments do not require that the CS in question have properties of a US. Additionally, we have added a direct comparison of the Replication and Stimulus Change groups from Experiment 1. While there appear to be slight differences in tone-elicited behavior between these two groups, statistical analyses reveal that while there are general increases in activity bursts in the Stimulus Change Group, these differences were not specific to any particular CS type.

5) Baseline data for Darts is missing throughout and should be added to all trial-by-trial graphs. This is important since all phases occurred in same chambers and baseline fear levels could drive darting before stimuli are presented.

We have added baseline darting data to all graphs and found little baseline darting that did not differ between groups and tended to be 0 after Day 1 of each experiment.

6) Line 133: "noise was never paired with shock". This is an important point -- but the white noise stimulus contains the tone frequency, and this was paired with shock in the previous phase.

The reviewer brings up an interesting point. While this may be a concern for this experiment, subsequent experiments (2, 3, and 4) all included groups which only received shock with no stimulus-shock pairings.

Author Response

Reviewer #3 (Public review):

1) The central component of the model is the fast activation of AHA by BRI1, a rapid, non-transcriptional response. More experimental support is needed to establish that, in the root, AHAs are activated rapidly and not by the transcriptional pathway. Minami et al., 2019 showed that AHA activation in the hypocotyls requires tens of minutes and is likely mediated by the accumulation of SAUR proteins. In other words, the activation is not a rapid BRI1mediated phosphorylation. The model, however, uses the findings from Minami et al 2019 as the support for the immediate activation of AHAs by phosphorylation (at the line 143).

The kinetics of AHA activation possibly through the accumulation of SAUR proteins is now discussed in detail in the Discussion section. In fact, this process is much slower compared to the mechanism presented here. As shown by the phosphoproteomics data of Lin et al. (2015), the rapid phosphorylation of AHAs within 5 min after BR application occurs at Ser315 and Thr 328 in the large cytoplasmic domain of the pumps and not at Thr947.

2) Further, one of the crucial outputs that is used to compare experimental a modelled data - the apoplastic pH - seems very noisy in the provided figures. This is particularly apparent in the time-course response of apoplastic pH to 10nM BL application. Figure 4B should show that there is a rapid acidification that is maintained, however the figure shows rather a noisy behavior (in particular when we consider that the errors represent SEM) and, moreover, the figure 4B does not fit the results from 4A. Similar noisy results are shown in the figure 6A and B and the model does not seem to fit the experimental data in the meristematic cells. In the case of these figures, the conclusions in the text do not seem to fit with the data presented in the figures.

We have now incorporated the statistics of the data (also) into Figures 4 and 6. Considering the statistical outcome, we see a good fit. The HPTS method is not technically straightforward in itself, to which some variability can be attributed. In addition, even the cells of the same tissue in different root samples show a variable response. Since the response in the meristematic zone is generally lower, the variability is particularly noticeable there and sometimes at the border of significance.

3) Further, the cngc10 mutant pH responses are not very convincing: the cells of the meristematic zone of the control line do not respond to BL (Appendix Fig3) while in figure 7C the meristematic zone of control does respond to BL. However, I think other physiological phenotypes of the mutant lines should be tested that would determine whether CNGC10 is involved in the response of roots to brassinosteroids. What is the expression of CNGC10 - is it expressed in the same cells as BRI1 and AHA2? What are the densities of CNGC10 molecules along the root developmental gradient? Such questions should be clarified to substantiate the conclusion that this channel is a major player in the regulation of membrane potential.

As far as the response of the MZ in Fig. 8 is concerned, we would like to refer to the answer to the statistics above and restrict the analysis of the CNGC10 function to the fast acidification process presented here. According to the data of the eFP browser, the accumulation of CNGC10 transcripts occurs quite evenly across all cells and tissues of the root and in the cells in which the other components of the mechanism described here are also expressed. A single cell annotation of CNGC10 transcript is not possible, as its expression is already induced by the protoplasting of the root cells.

4) Why the predictions of the model regarding the BIR3 involvement were not tested experimentally? This could again show that the model predicts the cellular behavior correctly. It would be particularly interesting to test the model predictions along the longitudinal root axis, where the ratio of signaling components is changing.

As suggested by the other reviewers, we have transferred the BIR3 modelling results to the Suppl. Data, but discuss them briefly in the Discussion. In fact, the modelling data are underpinned by experimental results published by Imkampe et al. (2017).

Author Response

Reviewer #1 (Public Review):

Bice et al. present new work using an optogenetics-based stimulation to test how this affects stroke recovery in mice. Namely, can they determine if contralateral stimulation of S1 would enhance or hinder recovery after a stroke? The study provides interesting evidence that this stimulation may be harmful, and not helpful. They found that contralesional optogenetic-based excitation suppressed perilesional S1FP remapping, and this caused abnormal patterns of evoked activity in the unaffected limb. They applied a network analysis framework and found that stimulation prevented the restoration of resting-state functional connectivity within the S1FP network, and resulted in limb-use asymmetry in the mice. I think it's an important finding. My suggestions for improvement revolve around quantitative analysis of the behavior, but the experiments are otherwise convincing and important.

Thank you for the positive feedback regarding our work.

Other comments - Data and paper presentation:

1) Figure 1A is misleading; it appears as if optogenetic stimulation is constant (which indeed would be detrimental to the tissue). Also, the atlas map overlaps color-wise with conditions; at a glance it looks like the posterior cortex might be stimulated; consider making greyscale?

We have updated Figure 1A to address these concerns.

Reviewer #2 (Public Review):

These studies test the effect of stimulation of the contralateral somatosensory cortex on recovery, evoked responses, functional interconnectivity and gene expression in a somatosensory cortex stroke. Using transgenic mice with ChR2 in excitatory neurons, these neurons are stimulated in somatosensory cortex from days 1 after stroke to 4 weeks. This stimulation is fairly brief: 3min/day. Mice then received behavioral analysis, electrical forepaw stimulation and optical intrinsic signal mapping, and resting state MRI. The core finding is that this ChR2 stimulation of excitatory neurons in contralateral somatosensory cortex impairs recovery, evoked activity and interconnectivity of contralateral (to the stimulation, ipsilateral to the stroke) cortex in this localized stroke model. This is a surprising result, and resonates with some clinical findings, and a robust clinical discussion, on the role of the contralateral cortex in recovery. This manuscript addresses several important topics. The issue of brain stimulation and alterations in brain activity that the studies explore are also part of human brain stimulation protocols, and pre-clinical studies. The finding that contralateral stimulation inhibits recovery and functional circuit remapping is an important one. The rsMRI analysis is sophisticated.

Thank you for the supportive comments regarding our manuscript

Concerns:

1) The gene expression data is to be expected. Stimulation of the brain in almost any context alters the expression of genes.

We agree with the reviewer that stimulation of the brain is expected to broadly alter gene expression. However, in this set of studies, we examined a subset of genes that are of particular interest in neuroplasticity, and compared expression in ipsi-lesional vs. contra-lesional cortex in the presence or absence of contralesional stimulation during the post stroke recovery period. Genes like Arc, for example, have been shown by our group to be necessary for perilesional plasticity and recovery (Kraft, et al., Science Translational Medicine, 2018). The finding that validated plasticity genes are suppressed by contralesional stimulation is consistent with the central finding that contralesional stimulation suppresses the recovery of normal patterns of brain organization and activity. Importantly, there were also genes associated with spontaneous recovery that were unaltered or increased by contra-lesional brain stimulation. While these data do not provide causal associations, they may prove to be useful for developing hypotheses regarding molecular mechanisms involved in spontaneous brain repair for future studies.

In light of the reviewer’s comment, we have altered text throughout to not focus on specific directionality of transcripts. Instead, we indicate that relevant transcript changes are those that are altered in association with spontaneous recovery, and which are altered in the opposite direction with contralesional brain stimulation.

Minor points.

1) Was the behavior and the functional imaging done while the brain was being stimulated?

We have updated the methods (page 17) to clarify that the only experiments during which the photostimulus occurred during neuroimaging are reported in new Figure 6, and to clarify that photostimulation did not occur during the behavioral tests of asymmetry.

2) It would be useful to understand what is being stimulated. The stimulation method is not described. Is an entire cortical width of tissue stimulated, and this is what is feeding back onto the contralateral cortex? Or is this stimulation mostly affecting excitatory (CaMKII+) cells in upper or lower layers? This will be important to be able to compare to the Chen et al study that gave rise to the stimulation approach here. This gets to the issue of the circuitry that is important in recovery, or in inhibiting recovery. One might answer this question by doing the stimulation and staining tissue for immediate early gene activation, to see the circuits with evoked activity. Also, the techniques used in this study could be applied with OIS or rsMRI during stimulation, to determine the circuits that are activated.

We have clarified the stimulation protocol in response to Essential point 2.2. Due to light scattering and appreciable attenuation of 473nm in brain tissue, only ~1% of photons penetrate to a depth of 600 microns. Experimentally, this provides superficial-layer specificity to Layer 2/3 Camk2a cells (https://doi.org/10.1016/j.neuron.2011.06.004)

To answer the question of what circuits are affecting recovery, we performed 2 sets of additional experiments – Experiment 1: OISI during photostimulation before and after photothrombosis, and Experiment 2: tissue staining for IEG expression (cFOS). We describe each below:

Experiment 1 New results are included from 16 Camk2a-ChR2 mice (Results, page 10-11; Methods, page 18) and reported as new Figure 6. Similar to the previously reported experiments, all mice were subject to photothrombosis of left S1FP, half of which received interventional optogenetic photostimulation beginning 1 day after photothrombosis (+Stim) while the other half recovered spontaneously (-Stim). To visualize in real time whether contralesional photostimulation differentially affected global cortical activity in these 2 groups, concurrent awake OISI during acute contralesional photostimulation was performed in +Stim and –Stim groups before, 1, and 4 weeks after photothrombosis. At baseline, all mice exhibited focal increases in right S1FP activity during photostimulation that spread to contralateral (left) S1FP and other motor regions approximately 8-10 seconds after stimulus onset. While activity increases within the targeted circuit, subtle inhibition of cortical activity can also be observed in surrounding non-targeted cortices. Thus, activity both increases and decreases in different cortical regions during and after optogenetic stimulation of the right S1FP circuit. Of note, regions that are inhibited by S1FP stimulation show more pronounced decreases in activity in +Stim mice at 1 and 4 weeks compared to baseline and were significantly larger in +Stim mice compared to –Stim mice. We conclude that focal stimulation of contralesional cortex results in significant, widespread inhibitory influences that extend well beyond the targeted circuit.

Experiment 2 For experiment 2, we hypothesized that IEG expression would increase in photostimulated regions, cortical regions functionally connected to targeted areas, and potentially deeper brain regions. For the IEG experiments, healthy ChR2 naïve animals (C57 mice) or CamK2a-ChR2 mice were acclimated to the head-restraint apparatus described in the manuscript used for photostimulation treatment. Once trained, awake mice were subject to the same photostimulus protocol as described in the manuscript applied to forepaw somatosensory cortex in the right hemisphere. After stimulation, mice were sacrificed, perfused, and brains were harvested for tissue slicing and immunostaining for cFOS. Tissue slices containing right and left primary forepaw somatosensory cortex and primary and secondary motor cortices (+0.5mm A/P) or visual cortex (-2.8mm A/P) were examined for cFOS staining and compared across groups.

Below is a summary table of our findings, and representative tissue slices. While c-FOS IHC was successful, results are not consistent with expectations from the mouse strains used. Only 1 ChR2+ mouse exhibited staining patterns consistent with local S1FP photostimulation, while expression in ChR2- mice was more variable, and in some instances exhibits higher expression in targeted circuits compared to ChR2+ mice. It is possible that awake behaving mice already exhibit high activity in sensorimotor cortex at rest, which might obscure changes specific to optogenetic photostimulation. Regardless, because the tissue staining experiments were inconclusive in healthy animals, we did not proceed with further experiments in the stroke groups, and do not report these findings in the manuscript.

3) Also, it is possible that contralateral stimulation is impairing recovery, not through an effect on the contralateral cortex (the site of the stroke), but on descending projections, or theoretically even through evoking activity or subclinical movement of the contralateral limb (ipsilateral to the stroke). By more carefully mapping the distribution of the activity of the stimulated brain region, and what exactly is being stimulated, these issues can be explored.

The reviewer raises an excellent point. We have added to the “Limitations and Future work” section of the Discussion on pages 15-16

Author Response

Reviewer #2 (Public Review):

The manuscript by Qiao et al studies the important problem of how to achieve accurate oscillation robustly in biological networks where noise level may be high. The authors adopted a comprehensive approach and studied how different network configurations affect osciillation. This is based on enumeration of all major architectures of 2- and 3-nodes networks.

This work makes important contributions to the field, as it offers the first comprehensive survey of networks motifs capable of oscillation, with further characterization of their robustness. The authors identified core motifs of repressilator with a positive autoregulation, and activatorinhibitor oscillator. In addition, the authors have identified different mechanisms of attenuation of different sources of noises. Overall, this is an important study reporting many new results.

1) The current stochastic model is based on the deterministic model shown in Fig 1D. However, there are a lot of assumptions in this ODE model. These include the assumption that the substrate is in instantaneous chemical equilibrium with the protein-ligand/DNA complex, and the reaction involving one receptor and n identical simultaneously binding ligands, with the Hill coefficient phenomenologically characterizing cooperativity. However, it is not clear what the specifics are when applied to the networks studied, i.e., what reactions are assumed instantaneous equilibrium, or why the important phenomenon of slow TF and promoter binding can be ignored and why that is reasonable? Also, what are the receptors and what are the binding reactions of multiple ligands that gives to the Hill coefficient?

Thank you for the good suggestion. To clarify the model assumptions, we updated the Methods section Deterministic model.

As the reviewer pointed out, these assumptions may not hold in some biological systems, e.g., the case that the binding/unbinding of TF to the promotor is slow. In the revision, we added discussions on the limitations of our methods on Page 23.

2) The described kinetic models based on ODE approximations may not be applicable to study strong intrinsic stochasticity arising at low copy number of molecules, where the MichelisMenton/Hill-type of ODE models are not valid. A more straightforward model would be based on mass action but more detailed reactions, without additional assumptions, from which one can write down the corresponding master equation.

In that light, it will be helpful to write out the set of equations for the stochastic networks, which is equivalent to the set of chemical master equations, from which Gillespie simulation samples.

Thank you for the suggestion. In the manuscript, we simulated the system by using Gillespie algorithm with Hill-type reaction rates (see Section “Simulations using the Gillespie algorithm lead to similar conclusions” and Figure S2). The simulation results are similar to those using Langevin equations (Figure 3 for results using Langevin equations). We updated the section "Stochastic model in the presence of intrinsic noise" to describe how we use Gillespie algorithm.

However, using Hill-type reaction rates in stochastic simulations may not be always accurate and could fail to capture the role of detailed reactions in stochasticity. Thus, we anticipate the need for a more detailed model where every reaction of Hill-type form is decomposed into the elementary reactions. The related discussions were added in the revision (see also the response to the 3rd question).

3) There may be another issue with the stochastic model for the intrinsic noise, as the reaction system do not model some of the important stochasticity occurring in the system. To study transcriptional regulation under different molecules, the binding of transcription factor to the DNA/promoter is an important source of stochasticity, as copy numbers of that specific regulating protein TF may vary, at the same time it also regulates the production rate of another protein. This process cannot be adequately modeled only by copy number change of the regulated protein. That is, the binding and unbinding of the transcription factor to the promoter plays important roles in stochasticity when modeling the intrinsic noise of the biochemical reactions. It would be desirable to account for the process explicitly. If the authors decide not to model such stochasticities, potential caveats should be pointed out.

In addition, protein-gene interactions often involve dimerization, that is, gene product forms a dimer, which then interact with the other gene. This dimerization may also qualitatively affect stochastic behavior of a GRN. The authors may wish to discuss all these issues.

Thank you for the good suggestion. In the revision, we added the following paragraph in the Discussion: “Another limitation of our work is that we didn’t decompose the reactions in the deterministic model into detailed elementary reaction steps when using Gillespie algorithm. The advantage of simulating non-elementary reactions with Hill-type rate functions is the low computation cost, and in some biological networks, it leads to consistent results with the model composed of all elementary reactions (Gonze et al., 2002; Kim et al., 2014; Sanft et al., 2011). However, this approach may not be always accurate, depending on the timescale separation of reactions (Kim et al., 2014; Sanft et al., 2011); for example, the Hill-type reaction rate is based on the quasi-steady-state approximation, which does not hold when binding/unbinding of TF to the promotor is slow or comparable to the timescales of protein production or decay (Choi Paul et al., 2008). Furthermore, this method neglects detailed reactions in gene regulatory networks, and thus fails to study roles of these reactions in stochasticity. These detailed reactions include the binding and unbinding of the transcription factor to the promoter, dimerization of transcription factors, transcription and translation (Cao et al., 2018; Shahrezaei and Swain Peter, 2008; Terebus et al., 2019).”

4) A potential drawback of the study is that the oscillation behavior hinges upon the behavior of the ODE deterministic model. It is well known even for simple networks such as transcription regulation without feedback, or when protein binding is involved there can be significant divergency between ODE model and stochastic model, where the latter exhibit multistabilities and the former none (e.g., doi.org/10.1063/1.3625958, doi.org/10.1103/PhysRevE.91.042111, doi.org/10.1063/1.5124823). There is now an increasing body of literature documenting this. This issue and potential ramifications should be discussed.

As an example, there is a new mechanism of stochastic oscillation found in toggle switch under weak promoter binding condition. This is not obvious from the corresponding ODE model and requires computation of the global map of discrete flux (doi.org/10.1063/1.5124823). It will be missed if protein-DNA binding is not modeled explicitly. It will be interesting if the authors can discuss the relationship of this type of oscillation with those based on repressilator/autoregulation and activator-inhibitor. Do they belong to perhaps different class of stochastic oscillations and if so, what are the differences?

Thank you for the good suggestion. In the revision, we added one paragraph on Page 22 to discuss this potential drawback: “Our work only focused on the effects of biological noise on oscillation accuracy, neglecting other dynamic changes caused by noise. These dynamics may include the loss of multistability and the occurrence of oscillation. Specifically, the way to model the noise may cause the loss of multistability (Duncan et al., 2015; Vellela and Qian, 2009); the presence of noise can produce oscillation even when the corresponding deterministic model cannot oscillate, which has been validated in the toggle-switch system and excitable system (Lindner et al., 2004; Terebus et al., 2019; Zaks et al., 2005). The possible reason might be the noise-induced transition between different states. Since our work only studied network topologies whose deterministic model can generate oscillation, we did not count the topologies that cannot oscillate in the deterministic model but begin to oscillate in the stochastic model. Due to the popularity of such topologies, how these topologies buffer noise will be of interest and may lead to the discoveries of new principles.”

5) The authors decided to use Chemical Langevin Equation to model the stochastic process due to computational cost. However, recent development shows that computing cost may no longer be an issue, as the finite buffer ACME algorithm can generate full probability surfaces without running costly trajectories (doi: 10.1073/pnas.1001455107, doi: 10.1137/15M1034180). In fact, this has been done for 3-node networks (feedforward loops), where extensive parameter sweeps enables construction of 10^4 probability landscape, from which phase diagrams of multimodality can be constructed (doi.org/10.3389/fgene.2021.645640). I understand that the authors choose to use the Langevin model, but the probability surface governed by the chemical master equation can now be computed rather rapidly, without resorting time-consuming Gillespie simulations. Therefore, the rationale of high computing cost may not be justifiable. This advancement should be pointed out.

Thank you for the good suggestion. In the revision, we added the following text to introduce the advancement of algorithms in the Discussion: “We anticipate the need for a more detailed model where every reaction of Hill-type form is decomposed into the elementary reactions. The recent development about stochastic algorithms with fast computation makes it feasible to simulate such detailed model for all two- and three-node network topologies, for example, algorithms focusing on solving the chemical master equations (Cao et al., 2010; Cao et al., 2016; Munsky and Khammash, 2006; Terebus et al., 2021) and variants of Gillespie algorithms that directly simulate the temporal dynamics (Gillespie and Petzold, 2003). Besides, the construction of probability surfaces through these algorithms may shed light on new principles for accurate oscillation.”

6) For the reason that there are many differences between master equation model, Langevin model, and ODE model, the statement on p.8 “the system responds to the noise is usually linked to the deterministic features” should be modified/qualified.

Sorry for the confusion. To clarify this, in the revision, we expanded this sentence to the following texts on Page 9: “Note that how the system responds to the noise is often linked to the deterministic features (Monti et al., 2018; Paulsson, 2004; Wang et al., 2010). For example, Monti et al. found that the circuit’s ability to sense time under input noise becomes worse when this circuit’s deterministic behavior cannot generate the limit cycle; Wang et al. adopted a similar form of noise and demonstrated the importance of signed activation time, a quantity calculated based on deterministic behavior, on the noise attenuation; by using an Ωexpansion to approximate the birth-and-death Markov process, Paulsson obtained the variance of the protein in gene networks and found it is related to network’s elasticity which is calculated from the deterministic model.”

Author Response

Reviewer #1 (Public Review):

The authors showed that longer reverberation time prolongs inhibitory receptive fields in cortex and suggest that this helps producing sound representations that are more stable to reverberation effects. The claims is qualitatively well supported by two controls based on probe responses to the same type of white noise in two different reverberation contexts and based on receptive fields measured at different time points after the switch between two reverberation conditions. The latter gives stronger results and thus constitutes a more convincing control that the longer decay of inhibition is not an artifact of stimulus statistics. The limits of the study include the use of anesthesia and the fact that cortex shows a very broad range of dereverberation effects, actually much broader than predicted by a simple model. This result confirms that reverberation produces cortical adaptation as suggested before, and suggests as a mechanistic hypothesis that rapid plasticity of inhibition underlies this adaptation. However the paper does not address whether this adaptation occurs in cortex or in subcortical structures. The fact that an effect is observed under anesthesia suggests a subcortical origin.

We agree that it is important to consider subcortical processing levels too, as we have done previously when investigating neuronal adaptation to mean sound level and contrast. However, these and other forms of adaptation are known to be organized hierarchically and are most prominent in the auditory cortex. In particular, in ferrets, the species we use in our study, contrast adaptation is a weaker and less consistent property of neurons in the inferior colliculus than of neurons in the primary auditory cortex (Rabinowitz et al., 2013, PLOS Biol. 11:e1001710). Similar results have been obtained for stimulus-specific adaptation and prediction error signaling in other species (Parras et al. 2017, Nature Comms. 8:2148; Harpaz et al., 2021, Prog. Neurobiol. 202:102049). It therefore makes considerable sense to focus here on the primary auditory cortical areas in ferrets, where adaptation to reverberation has been demonstrated before (Mesgarani et al., 2014, PNAS 111:6792-7), in order to explore the possible basis for this effect. We agree that future work should investigate whether adaptive shifts in the inhibitory components of the receptive fields with room size are a property of the cortex only or also found in subcortical auditory areas, such as the thalamus or midbrain.

We chose to record from anesthetized ferrets in order to provide the stability required for presenting the long stimulus sequences that were essential for characterizing the effects of reverberation on the responses of cortical neurons. This strategy was adopted only because we have previously shown that contrast adaptation is indistinguishable in the primary auditory cortex of awake and anesthetized ferrets (Rabinowitz et al., 2011, Neuron 70:1178-91). Furthermore, adaptation to background noise has been shown to enhance the representation of speech in the human auditory cortex independently of the attentional focus of the listeners (Khalighinejad et al., 2019, Nature Comms. 10:2509). All the same, while there is much evidence to indicate that adaptation does not differ, at least qualitatively, with brain state, it would be interesting in future research to determine how task engagement affects the inhibitory plasticity that we observed in this study.

Reviewer #2 (Public Review):

Ivanov et al. examined how auditory representations may become invariant to reverberation. They illustrate the spectrotemporal smearing caused by reverberation and explain how dereverberation may be achieved through neural tuning properties that adapt to reverberation times. In particular, inhibitory responses are expected to be more delayed for longer reverberation times. Consistently, inhibition should occur earlier for higher frequencies where reverberation times are naturally shorter. In the manuscript, these two dependent relationships were derived not directly from acoustic signals but from estimated relationships between reverberant and anechoic signal representations after introducing some basic nonlinearity of the auditory periphery. They found consistent patterns in the tuning properties of auditory cortical neurons recorded from anesthetized ferrets. The authors conclude that auditory cortical neurons adapt to reverberation by adjusting the delay of neural inhibition in a frequency-specific manner and consistent with the goal of dereverberation.

Strengths:

This main conclusion is supported by the data. The dynamic nature of the observed changes in neural tuning properties are demonstrated mainly for naturalistic sounds presented in persistent virtual auditory spaces. The use of naturalistic sounds supports the generalization of their findings to real live scenarios. In addition, three control investigations were conducted to backup their conclusions: they investigated the build-up of the adaptation effect in a paradigm switching the reverberation time after every 8 seconds; they analyzed to which degree the observed changes in tuning properties may result from differences in the stimulus sets and unknown nonlinearities; and, most convincingly, they demonstrated after-effects on anechoic probes.

Thank you.

Weaknesses:

1) The strength of neural adaptation appears overestimated in the main body of the text. The effect sizes obtained in control conditions with physically identical stimuli (anechoic probes, Fig. 3-Supp. 3B; build-up after switching, Fig. 3-Supp. 4B-C) are considerably smaller than the ones obtained for the main analyses with physically different stimuli. In fact, the effect sizes for the control conditions are similar to those attributed to the physical differences alone (Fig. 3-Supp. 2B).

The best estimates of the magnitude of the neural adaptation in our paper come from the STRF analysis, and the potential effects of stimulus differences is estimated using our simulated neurons method. While the noise burst and room switching experiments are very valuable controls for verifying the presence of the adaptation, they may underestimate the adaptation’s magnitude because the responses to the anechoic noise burst probes may become partially unadapted during their progress, lessening the adapted effects for these sounds. Likewise, the room switching control may not capture the full magnitude of the adaptive effect because the time spans of two time windows used to assess the adaptation (i.e. L1 and L2 or S1 and S2) have limited resolution and may not be optimally matched to the timescourse of the adaptation. However, the noise burst and room switching analyses are critical controls in our study, even if the measured effects may be more subtle. Crucially, these analyses demonstrate that the reverberation adaptation can be observed even for physically identical stimuli. This confirms, in addition to our simulated neuron methods, that the effects described in our manuscript cannot be entirely due to fitting artifacts resulting from comparing neural responses to different acoustic stimuli, but rather result, at least in part, from an underlying adaptive process.

2) All but one analysis depends on so-called cochleagrams that very roughly approximate the spectrotemporal transfer characteristics of the auditory periphery. Basically, logarithmic power values of a time-frequency transformation with a linear frequency scale are grouped into logarithmically spaced frequency bins. This choice of auditory signal representation appears suboptimal in various contexts:

On the one hand, for the predictions generated from the proposed "normative model" (linear convolution kernels linking anechoic with reverberant cochleagrams), the non-linearity introduced by the cochleagrams are not necessary. The same predictions can be derived from purely acoustical analyses of the binaural room impulse responses (BRIRs). Perfect dereverberation of a binaural acoustic signal is achieved by deconvolution with the BRIR (first impulse of the BRIR may be removed before deconvolution in order to maintain the direct path). On the other hand, the estimation of neural tuning properties (denoted as spectro-temporal receptive fields, STRFs) assumes a linear relationship between the cochleagram and the firing rates of cortical neurons. However, there are well-described nonlinearities and adaptation mechanisms taking place even up to the level of the auditory nerve. Not accounting for those effects likely impedes the STRF fits and makes all subsequent analyses less reliable. I trust the small but consistent effect observed for the anechoic probes (Fig. 3-Supp. 3B) the most because it does not rely on STRF fits. Finally, the simplistic nature of the cochleagram is not able to partial out the contribution of peripheral adaptation from the adaptation observed at cortical sites.

The reviewer brings up two important issues to consider here. The first is our use of cochleagrams to model peripheral input to the auditory cortex. The second is our use of STRFs to model the receptive fields of auditory cortical neurons.

In a recent study (Rahman et al., 2020, PNAS 117:28442-51), we tested a wide range of cochlear models to examine which model provides the best preprocessing stage for predicting neural responses to natural sounds in the ferret primary auditory cortex. We found that the cochlear models used to produce cochleagrams in the current manuscript performed best, outperforming even more complicated and biologically-inspired cochlear models (e.g. Bruce et al., 2018, Hearing Research 360:40-54). This therefore determined our choice of cochlear model. However, to address the reviewer’s concern, we replicated our reverberation adaptation findings using Bruce et al.’s (2018) more complex cochlear model, and we include the results of this analysis in our revised version of the manuscript.

STRFs are widely used to model the receptive fields of neurons in the auditory system, and particularly in the primary auditory cortex. Nevertheless, the reviewer is correct to point out that these linear models of neural receptive fields are limited, and many cortical neurons show nonlinear aspects in their frequency and temporal tuning. In the present study, the use of STRFs in the normative deverberation model allowed us to produce predictions for neural tuning across reverberant conditions that could be directly tested in the STRFs of real cortical neurons. It is less clear to us how an acoustical analysis of BRIRs would translate into predicted neural firing patterns. While the simple STRF model used here provided new insights into a mechanism for reverberation adaptation in the auditory cortex, it would be interesting and valuable for future studies to test non-linear receptive field properties in this context. Future studies should also examine contributions to reverberation adaptation at other levels of the auditory system, including subcortical stations.

Author Response

Reviewer #3 (Public review):

Weaknesses:

1) The authors reconstruct a single phylogenetic tree for both the HK and RR components, concatenating the sequences together and then performing a single analysis. This could be problematic. First, if horizontal gene transfer occurred for one, but not the other, partner, the gene trees for the HK and RR components could be discordant. In this scenario, the reconstructed sequences would be incorrect because they were done on an a prior concordant tree. Second, there was insufficient detail in the methods to know how the matched pairs of HK/RR sequences were generated. If the authors inadvertently mixed up paralogs (e.g. generating incorrect HK1-RR2 or HK2-RR1 concatenations) this could lead to a poor phylogenetic inference. A simple way to check for both problems would be to generate phylogenetic trees for HK and RR separately and check for tree concordance. If the separate trees are concordant, the concatenated sequences are justified. If the separate trees are discordant, the authors would have to determine whether independent reconstructions would alter their reconstructed sequences.

Discussed in Essential Revisions, above. In addition, a better description was added to the methods section to specify that only adjacent HK and RR sequences were matched, and any ambiguous clusters of two component systems were removed from the analysis to avoid this type of artifact.

2) The authors use a simple in vitro phosphorylation assay as their assay for the ability of HK to phosphorylate RR. There were, however, two aspects of the assay that were not clear in the text.

2A) First, the authors built their quantification around tracking the depletion of phosphorylated HK. There were a number of variants that showed much slower HK dephosphorylation than others, with barely detectable RR phosphorylation. A sceptical reviewer might wonder if this is slow activity represents specific dephosphorylation or instead spontaneous dephosphorylation to inorganic phosphate. (If the latter, the reconstructed protein is not really functional at all). An appropriate negative control would be tracking the rate of dephosphorylation of HK with no RR added.

This is a reasonable concern, and a new figure has been added (Figure 1 – Figure Supplement 2) to show that each HK is stably phosphorylated over the 30 minutes timecourse when no RR is added. A sentence has also been added to the results to reference this control (last paragraph of “EnvZ/OmpR has undergone duplication and diversification in alpha-proteobacteria”).

2B) Second, the authors used this assay to compare relative catalytic efficiencies (kcat/KM) of their variants. It was unclear how they extracted this information from the data as presented, which consist of a single velocity curve determined at a fixed concentration of HK and RR. In most contexts, obtaining kcat/KM requires measuring V0 vs. S0. More information on what precisely is being reported is necessary. (I should note that their qualitative results, looking at the gels, won't be affected by this; just statements like a 28-fold preference of ancHK2 for ancRR2 vs. ancRR1).

We have added a better explanation of how these relative catalytic efficiencies were calculated both to the results section (penultimate paragraph of “Ancestral protein reconstruction reveals early acquisition of paralog specificity”) and to the methods section.

3) There are a number of places where existing work in the field could be cited more appropriately. The authors argue in a couple of places that ASR has not been used to reconstruct historical protein-protein interactions; however, this is not true. Examples include: Holinksi Proteins 2016 https://doi.org/10.1002/prot.25225; Wheeler et al 2018 Biochemistry https://doi.org/10.1021/acs.biochem.7b01086; Lauren et al. MBE 2020. https://doi.org/10.1093/molbev/msaa198; and Wheeler et al MBE 2021. https://doi.org/10.1093/molbev/msab019. Further, on p. 17, the authors cite Field and Matz MBE 2010 as an example of a study looking at the evolution of protein/small-molecule interactions. This is not true: that study looked at the evolution of GFP-like protein color.

Thank you for this suggestion, and for noting the error. A sentence in the discussion has been changed to clarify that this isn't the first study of ancestral sequence reconstruction for proteinprotein interactions. The incorrect reference has been removed from the discussion and references have been added for the other noted protein-protein ASR papers in the introduction.

4) The authors suggest in a few places that the deepest ancestor (ancHK/ancRR) was not optimized for phosphate transfer because this activity improves for later ancestors. An alternative interpretation is that these deepest ancestors are relatively poorly reconstructed, and thus that overall activity is lower. Indeed the alternate reconstruction of ancHK-alt/ancRR-alt barely showed detectable activity. As such, I think the poor reconstruction hypothesis is much more likely than a suboptimal ancestral function that was subsequently optimized.

This is a fair criticism and we have added a sentence to acknowledge it explicitly in the discussion.

Author Response

Reviewer #1 (Public Review):

The authors have developed cochlear implant prototypes with microcoils that allow magnetic stimulation of spiral ganglion neurons instead of conventional electrical stimulation. The neuronal response at the cortical level was evaluated in a mouse model. Magnetic stimulation was compared to acoustic stimulation and conventional electrical stimulation. The results obtained by the authors demonstrated a better spatial selectivity with a better dynamic.

The article is well written with an introduction and a problematic allowing to understand the goal of the work by readers not expert of the domain. The scientific approach is logical and progressive allowing to explain the work in a very educational way. The figures are clear and illustrate the quality of the work.

Here are my comments:

Concerning the methodology and in particular the electrical stimulation, it would be necessary that the authors specify that the stimulation was monopolar. this choice of stimulation involves a more important diffusion of the current. This makes the comparison with magnetic stimulation more flattering.

In the discussion, several points should be addressed to better explain to the reader the interest and the limits of the chosen technology. I think that you should start by reminding the reader that there are other modes of electrical stimulation than monopolar stimulation. bipolar or tripolar stimulation can reduce the diffusion of the current to improve selectivity. this stimulation strategy is already used by some manufacturers in the clinic.

We agree with the comment and have added language to the Discussion section to remind the reader that the electric stimulation was delivered in a monopolar configuration and that bipolar, tripolar and focused multipolar stimulation strategies would all provide narrower spreads of activation. Comparisons to micro-coil stimulation will be conducted in a future project.

[Line 336] “In this study, electric stimulation was delivered in a monopolar configuration. Other configurations, e.g., bipolar, tripolar, and focused multipolar result in improved spatial selectivity in both animal models (Snyder et al., 2008, Bierer et al., 2010, George et al., 2015) and human trials (van den Honert and Kelsall, 2007) although at the expense of increased thresholds (Bierer and Faulkner, 2010, Zhu et al., 2012, George et al., 2015). Due to the small size of the mouse cochlea, it was not feasible to test configurations that required the insertion of two or more electrodes into the cochlea. In addition, the advantage of multipolar stimulation is less obvious in species with smaller cochleae, e.g., even in the gerbil cochlea difference in spatial spread between monopolar and bipolar stimulation was not significant (Dieter et al., 2019). Nevertheless, it will be still interesting to compare spreads from micro-coils to the diverse configurations of electric stimulation in future studies.”

In the animal model used, it is likely that even in spite of recent hearing loss, the trophicity of the spiral ganglion is preserved. This does not reflect the pathological conditions of the implanted patients. Thus, it is not at all certain that the better selectivity is the better dynamics observed with magnetic stimulation can be observed in case of damaged spiral ganglion.

This is a good point – it is a limitation of our work and we have modified the text to remind the reader of this possibility. Because one of the main goals of our study was to compare the spread of activation across different stimulation modalities, all SGNs needed to be viable so as to not introduce any bias e.g., tonotopic sections without SGN innervation might obscure the measurement of spectral spread. In future studies, it will be essential to test magnetic stimulation in a model of neonatally deafened animals to further evaluate the translational potential of magnetic stimulation to human subjects.

[Line 388] “In the present study, it is likely that most SGNs were intact since our deafening procedure mainly targeted hair cells. Maintaining uniform survival of SGNs was essential to ensure accurate comparison of the spread of activation across modalities, however, this situation does not uniformly reflect the pathological conditions of all implanted patients. Patients typically receive CIs months or years after the onset of deafness and often have considerable SGN loss (Khan et al., 2005; Nadol and Eddington, 2006). Thus, in future studies, it will be necessary to test coil effectiveness in neonatally deafened animals so as to more closely mimic pathological conditions of implanted patients.”

If the passage of current in the microcoils generates a magnetic field, it is possible that an inverse effect, or even a heating effect, could be observed if this type of implant is subjected to an external magnetic field, as in an MRI. Have the authors considered this potential disadvantage in view of a clinical transfer of this technology?

This is an important concern. Bonmassar and Serano (2020) conducted a study addressing this question in micro-coils for deep brain stem stimulation and compared micro-coils to a typical wire implant in a 1.5T MRI. Their results showed warming of the implant in both groups, however, the degree was far less in the microcoils (<1° C), than in the wire (~10° C). Conventional electrode-based cochlear implants have been also evaluated in 1.5T MRI, where a slight degree of warming was observed, however, less than seen in lead wires (Bonmassar and Serano 2020, Zeng et al., 2018). Nevertheless, we agree that it is important to point out this potential limitation and have added the following paragraph.

[Line 381] “Another potential concern would be the compatibility of implanted micro-coils with strong exogenous magnetic fields. A previous study has tested the effect of 1.5T exogenous magnetic field on micro-coils and electric wire-based implants designed for deep brain stem stimulation (Bonmassar and Serano, 2020). Their results showed warming of the implants in both groups, however, the degree was far less in the micro-coils (<1° C) than in the electric wires (~10° C). Nevertheless, testing the effect of exogenous magnetic fields on coil-based CIs will be crucial for the translation of this technique to humans.”

Reviewer #2 (Public Review):

Lee, Seist et al. investigated whether magnetic stimulation of the cochlear would lead to less spread of activity - a major limitation of classical cochlear implants used nowadays - than electrical stimulation. To do so, they measured neuronal responses in the inferior colliculus of mice to acoustic, electric, and magnetic stimulation of the cochlea. The acoustic stimulation consisted of 5 ms long pure frequency tones covering the range from 8 to 48 kHz, whereas the magnetic and electrical stimulations were pulses of 25 um duration presented at a rate of 25 pulses/s delivered at 2 locations along the cochlear (one basal, one apical). The neuronal responses were measured along a 16-channel recording array inserted along the tonotopic axis of the inferior colliculus. The results demonstrate that magnetic stimulation elicited responses that were more spatially constrained and had a larger dynamic range than electrical stimulation. As one of the main limitations of the cochlear implants used nowadays is the large spatial spread of stimulation, these data bring a lot of hope for improving this neuroprosthetic technology and put magnetic stimulation as one of the most promising approaches to improve cochlear implant technologies.

The conclusions of the paper are mostly well supported by data, but some aspects of the experimental procedure, the neuronal response acquisition, and the data analysis need to be clarified and extended.

1) From the current description, it is not clear whether the recording electrode stays at the same location for the acoustic, magnetic, and electrical stimulation, or whether it is removed and reinserted. If it is removed and reinserted, it might be that slightly different regions of the IC are recorded from, or that the brain gets slightly damaged on every new insertion. A more detailed quantification of the brain state or neuronal responses would then be a welcome addition. This could be done in several ways. For example, the spontaneous activity or general excitability of IC neurons could be compared across the three different stimulation paradigms in the few experiments they were performed in the same mice (l. 407). Another possibility would be to compare electrical stimulation responses when performed before vs. after the magnetic stimulation (l. 403). More generally, any possible paired-statistical analysis (i.e., when the same recording sites were used to compare the different stimulating methods) would be welcome. Related to my previous comment, it is written that “experiments were terminated when responses to magnetic stimulation were no longer robust” (l. 406). Why would responses lose robustness? If this is due to damage of the recorded neurons or to cochlea damage, it will most probably also affect the results overall and hence the conclusions of the manuscript.

The positioning of the recording electrode remained at the same location; we have added the following statement to clarify our methods:

[Line 421] “After the original insertion into the inferior colliculus, the position of the multielectrode recording array was not repositioned while switching from one stimulus modality to the next (acoustic, electric, magnetic). Due to the fragility of the recording electrode array, we took extra care to avoid disturbing the skull, as dislodgement of the array would have altered tonotopicity and thus weakened the ability to accurately compare spectral spread between trials.”

To minimize the potential for pain or discomfort to the animal, experiments were terminated when vital signs, such as heart rate and respiration rate, declined; this typically occurred at about 5 – 7 hours after onset of the experiment. Such declines were typically preceded by a decline in inferior colliculus responses. We have modified the language in the manuscript to make this clearer.

[Line 474] “Experiments were terminated whenever the animal’s vital parameters, as measured by heart and respiratory rate, declined. The decline was typically observed at around 5 – 7 hours and preceded by a decline in inferior colliculus responses.”

2) In a number of figures, only example data are presented (Figures 2, 3, 6). To give the reader the possibility to judge the variability of the results across different experiments (and hence the robustness of the results), it would be important to show also average values, or - in cases this is not relevant - at least 3 example mice.

We agree with this concern and have added more data for ABR and IC responses in the supplement figure section (Figure 3 – figure supplement 1; Figure 4 – figure supplements 1 and 2). We also present data points for individual samples in each plot. All source data used to make figures have been uploaded to the repository following the guideline of the eLife journal. We believe this will help interested readers assess our results quantitatively.

The advantages and limitations of magnetic stimulations are well described in the introduction and discussion sections and leave the reader with the information that is needed to evaluate the potential strengths and weaknesses of the technique. These sections also nicely emphasize that future experiments have to be performed to further characterize this stimulation strategy.

Reviewer #3 (Public Review):

This article describes a new way to activate auditory nerve fibers (ANFs) by magnetic stimuli (generated by micro-coils) instead of electrical currents (generated by conventional electrodes). The activation of ANFs triggered by the micro-coils seems clear but several physiological quantifications are inappropriate and the major claims are based on a very small number of experiments. I sincerely encourage the authors to continue their experiments and use more straightforward ways to quantify their results (closer to the raw data) to progress toward clarifying their effects.

In the case of severe and profound deafness, cochlear implant is the solution to recover partial hearing and speech understanding. Cochlear implant is probably the most successful neuroprothesis but it still has limitations, especially as it is difficult to focus the currents inside the cochlea, the electrodes being in contact with a conductive liquid named perilymphe.

In this study, the authors aim at describing a new way to activate the auditory nerve fibers (ANFs) by the use of small coils (micro-coils) which are supposed to confine ANF activation more narrowly than can be achieved with conventional electrodes used in cochlear implants. The authors recorded neuronal activity from the inferior colliculus (a subcortical auditory structure) and claim that the spread of activation is narrower with magnetic stimulation compared to electric stimulation. They also point out that the dynamic range is wider with the magnetic stimulation than with electric stimulation. Finally, they show that the evoked responses in the inferior colliculus also occurred in mice chronically deafened indicating that the micro-coils directly activate the ANFs. Activation of the ANFs triggered by the micro-coils seems clear, however, to what extent this activation differs between electric and magnetic stimulation; and differs with acoustic stimulation is unclear. Several basic quantifications are missing and the quantifications performed here are not appropriate. In addition, all the claims are based on very small samples.

For most of the study, our conclusions are based on a sample size (N = 6-12) that is in line with similar types of studies. Our statistical calculations provided enough power for significant results. We agree with the reviewer that it would be desirable to have performed more than N=2 experiments with chronically deafened animals. However, constraints arising from the COVID-19 pandemic as well as the relocation of Dr. Stankovic’s laboratory, made it impossible to perform these additional experiments. We acknowledge that only limited conclusions can be drawn from the experiment with 2 animals (i.e., the result from chronically deafened animals; Figure 7), but nevertheless, feel the result is worth presenting.

Quantification of the frequency response area FRA using the d’ index is very puzzling. If the authors want to quantify the breadth of the tuning curves they can use the Q10dB, the Q40dB or the Octave distance which are classically used in auditory neuroscience. Comparing the different levels of stimulus intensity to determine the breadth of tuning to sounds and to electric/magnetic stimuli does not make any sense.

In general, we tried to use conventional methods so that readers can readily understand and interpret our results. We acknowledge that measuring the spread of activation at certain dB levels above threshold is commonly used to evaluate responses to acoustic stimulation. However, we felt that the use of the classic Q10dB or Q40dB measures to compare the spread of activation across different modalities was less suitable since each modality has a different dynamic range. For example, the dynamic range of electric stimulation was only ~ 3 dB, while that of acoustic stimulation was more than 20 dB. Therefore, we adopted an approach based on fixed significance of response strengths, i.e., measuring at an identical discrimination index. In this way, the estimation of the spread of excitation becomes independent of the stimulus’s nature and makes neural activation by different modalities more comparable. This approach is similar to that used in many previous studies in which new stimulation paradigms were evaluated (Middlebrooks et al., 2007; Bierer et al., 2010; Moreno et al., 2011; Richter et al., 2011; George et al., 2015; Xu et al., 2019; Dieter et al., 2019; Keppeler et al., 2020) and thus allows the performance of micro-coils to be more easily compared. Nevertheless, we agree that providing more detailed explanations would be helpful to many readers and have added additional language in the Method section of the revised manuscript.

The italicized text indicates passages from the revised manuscript: [Line 528] “The value of d’ represents the distance between the means in units of a standard deviation – the larger the d’ value, the more separated the distributions are.”

[Line 532] “To estimate the spread of activation from acoustic stimulation, previous studies measured the width of IC activation at a sound pressure level of 10 - 40 dB above threshold. However, given that dynamic ranges are significantly different across modalities (e.g., the dynamic ranges of acoustic and electric stimulations are 25.96 ± 9.17 dB SPL and 3.24 ± 0.99 dB mA, respectively.), comparing spatial spreads at a fixed dB level above threshold was not feasible. Alternatively, some studies measured spatial spreads at different dB levels above threshold for different modalities., e.g., 20 dB and 6 dB above threshold for acoustic and electric stimulation, respectively (Snyder et al., 2004). More recent studies that have evaluated novel stimulation modalities and compared them to acoustic and/or electric responses compared spatial spreads at a given response strength, typically at cumulative d’ values of 2-4 (Middlebrooks and Snyder, 2007, Bierer et al., 2010, Moreno et al., 2011, Richter et al., 2011, George et al., 2015, Xu et al., 2019, Dieter et al., 2019, Keppeler et al., 2020). Thus, to remain consistent with these previous studies, we also compared spectral spreads from acoustic, magnetic, and electric stimulation at cumulative discrimination indexes of 2 and 4.”

We have also plotted the cumulative d’ index with respect to dB levels above threshold for each modality (Figure 2 – figure supplement 2) and added relevant descriptions in the Materials and Methods section. We believe these will facilitate understanding of our results by readers, especially those who are accustomed to the analysis based on fixed dB levels.

[Line 550] “On average, the cumulative d′ levels of 2 and 4 correspond to 7.23 ± 5.34 and 18.53 ± 9.94 dB SPL above threshold for acoustic stimulation, 0.47 ± 0.30 and 1.41 ± 0.53 dB 1 mA above threshold for electric stimulation, and 2.57 ± 1.33 and 7.98 ± 5.41 dB 1 V above threshold for magnetic stimulation (Figure 2 – figure supplement 2).”

Quantification of the spectral spread of activation used in figure 4A-B is not correct. Based on the 11 animals tested with ipsilateral tones (and not contralateral tones), the authors estimated that each electrode corresponds to a particular frequency, then the between-electrode distance is converted in an octave distance. First, what is the purpose of converting distances into octave? In fact, there is no possibility to calibrate the acoustic stimuli and the electric/magnetic stimuli the same way: we cannot know if a particular sound intensity (e.g. 80dB) corresponds a particular voltage (for magnetic stimulation) or intensity (for electric stimulation). By using ipsilateral sounds instead of contralateral sounds, the authors largely underestimated the acoustic inputs reaching the recording sites (because the main ascending pathways cross the midline between the cochlear nucleus and the superior olivary complex). Therefore, the comparisons between acoustic and electric/magnetic activation cannot be properly assessed, which is the crucial part of this paper.

As the reviewer mentioned, we converted the distance of activated electrodes to octave distance based on the characteristic frequency of each electrode derived from Figure 2D. This translation provides an estimate of the activated frequency band across the tonotopic organization of the cochlea by stimulation and previous studies evaluating novel methods of artificial stimulation presented the spread of activation by artificial stimulation in a similar way (Dieter et al., 2019; Keppeler et al., 2020). Therefore, we felt the use of this approach would provide the most direct comparison to previous work. Nevertheless, we agree that quantifying the activation spread by electrode distance would be more intuitive to some readers and have added the corresponding plots in Figure 5.

We thank the reviewers for highlighting the anatomy of the auditory pathway and, specifically, its crossing over the midline. The wording in the original manuscript was confusing as all modes of stimulation (acoustic, electric, magnetic) were delivered to the left cochlea and responses measured from the right inferior colliculus (IC); the side to which stimulation was delivered was referred to as ipsilateral and the opposite side was referred to as contralateral. We revised the wording as shown below and believe it will greatly reduce the potential for confusion.

[Line 100] “We stimulated the left cochlea with acoustic, electric, and magnetic stimuli and measured responses from a 16-channel recording array implanted along the tonotopic axis of the right (contralateral) inferior colliculus (IC) in anesthetized mice (Figure 1C; MATERIALS AND METHODS).”

Author Response

Reviewer #1 (Public Review):

1) The connectivity patterns along the anterior-posterior hippocampal axis broadly follow an anterior-posterior cortical bias, such that posterior regions, e.g. the visual cortex, are preferentially connected to the hippocampal tail, and anterior regions, e.g. the temporal pole, are preferentially connected to the hippocampal head. The authors focus on the twenty regions with the highest connectivity profiles, which appears to capture the majority of all connections. However, some of the present structural connectivity patterns differ in interesting ways from previously described cortical networks reported in resting-state fMRI studies. Most notably, the medial PFC and orbitofrontal regions combined account for less than 1% of all connections in the present investigation (Table S1 & S2). This is an interesting contrast to functional investigations which tend to find that these regions cluster with the aHPC (e.g., Adnan et al. 2016 Brain Struct Func; Barnett et al. 2021 PLoS Biol; Robinson et al. 2016 NeuroImage). In contrast, the present DWI results suggesting preferential pHPC-medial parietal connectivity dovetail with those observed in fMRI studies. It seems important to discuss why these differences may arise: whether this is a differentiation between structural and functional networks, or whether this is due to a difference in methods.

We thank Reviewer 1 for making this important point and agree that these observations are deserving of further expansion. We have now included additional text where we place the surprising observation of sparse connectivity between PFC regions and the hippocampus more firmly in the context of recent evidence and argue that these observations suggest a potential differentiation between structural and functional networks.

We have included the following text in the discussion (pp. 16-17, lines 439-457);

“While many of our observed anatomical connections dovetail nicely with known functional associations, patterns of anatomical connectivity strength did not always mirror well characterised functional associations between the hippocampus and cortical areas. For example, a surprising observation from our study was that only weak patterns of anatomical connectivity were observed between the hippocampus and the ventromedial prefrontal cortex (vmPFC) and other frontal cortical areas. This lies in contrast to well documented functional associations between these regions (46-48). Our observation, however, supports a growing body of evidence that direct anatomical connectivity between the hippocampus and areas of the PFC may be surprisingly sparse in the human brain. For example, Rosen and Halgren (49) recently reported that long range connections between the hippocampus and functionally related frontal cortical areas may constitute fewer than 10 axons/mm2 and more broadly observed that axon density between spatially distant but functionally associated brain areas may be much lower than previously thought. Our observation of sparse anatomical connectivity between the hippocampus and PFC mirrors this recent work and suggests a potential differentiation between structural and functional networks as they relate to the hippocampus. It remains possible, however, that methodological factors may contribute to these differences. We return to this point later in the discussion. A future dedicated study aimed at assessing whether the well characterised functional associations between the hippocampus and vmPFC are driven by sparse direct connections or primarily by intermediary structures is necessary to address this issue in an appropriate level of detail.”

2) While the analytic pipeline is described in sufficient detail in the Methods, it is somewhat unclear to a non-DWI expert what the major methodological advance is over prior approaches. The authors refer to a tailored processing pipeline and 'an advance in the ability to map the anatomical connectivity (p. 5), but it's not immediately clear what these entail. It would be useful to highlight the key methodological differences or advances in the Introduction to help with the interpretation of the similarities and differences with previous connectivity findings.

We have now included a brief description in the Introduction highlighting the key methodological advances used in the current study.

We have included the following text in the Introduction (pp. 4-5, lines 130-144);

“In typical fibre-tracking studies, we cannot reliably ascertain where streamlines would naturally terminate, as they have been found to also display unrealistic terminations, such as in the middle of white matter or in cerebrospinal fluid (39). While methods have been proposed to ensure more meaningful terminations (40), for example, with terminations forced at the grey matter-white matter interface (gmwmi), this approach is still not appropriate for characterising terminations within complex structures like the hippocampus. A key methodological advance of our approach was to remove portions of the gmwmi inferior to the hippocampus (where white matter fibres are known to enter/leave the hippocampus). This allowed streamlines to permeate the hippocampus in a biologically plausible manner. Importantly, we combined this with a tailored processing pipeline that allowed us to follow the course of streamlines within the hippocampus and identify their ‘natural’ termination points. These simple but effective methodological advances allowed us to map the spatial distribution of streamline ‘endpoints’ within the hippocampus. We further combined this approach with state-of-the-art tractography methods that incorporate anatomical information (40) and assign weights to each streamline (41) to achieve quantitative connectivity results that more faithfully reflect the biological accuracy of the connection’s strength (39).”

3) Related to the point above, it was a bit unclear to me how the present connections map onto canonical white matter tracts. In Fig., 4A, the tracts are shown for a single participant, but it would be helpful to map or quantify know how many of the connections for a given hippocampal subregion are associated with a given tract to provide a link to prior work or clarify the approach. A fairly large body of prior research on hippocampal white matter connectivity has focused on the fornix, but it's a little difficult to align these prior findings with the connectivity density results in the current paper.

We thank Reviewer 1 for this comment and agree this would be an interesting avenue to pursue. However, the reliable segmentation of white matter fibre bundles is currently an area of contention in the DWI community. This pervasive and problematic issue was highlighted in a recently published large multi-site study that revealed a high degree of variability in how white matter bundles are defined, even from the same set of whole-brain streamlines (Schilling et al., 2021, Neuroimage. Nov; 243:118502. https://pubmed.ncbi.nlm.nih.gov/34433094/). This means that, even if we were to choose a particular method to segment white matter bundles, our results would not be readily translatable to those reported in previous DWI studies. This significantly limits meaningful comparison and/or interpretation. Indeed, such an approach may paradoxically take away from the detailed characterisations we have achieved in the current study. As highlighted in that study, it is now paramount that consensus is reached in this field to define criteria to reliably and reproducibly define white matter fibre bundles. Once that is achieved, we plan to conduct a follow-up study to characterise this in more detail, with bundles that will be able to be reliably reproduced by others.

4) Finally, on a more speculative note: based on the endpoint density maps, there seems to be a lot of overlap between the EDMs associated with different cortical regions (which makes sense given the subregion results). Does this effectively mean that the same endpoints may be equally connected with multiple different cortical regions? Part of the answer can be found in Fig. 3D showing the combined EDM for three different regions, but how spatially unique is each endpoint? This is likely not a feasible question to address analytically but it might be helpful to provide some more context for what these maps represent and how they might relate to differences across individuals.

The primary aim of the current analysis was to characterise broad patterns of endpoint density captured by our averaged group level analysis. However, Reviewer 1 is astute in assuming that, although there is overlap in the group averaged endpoint density maps (EDMs) associated with different cortical areas, at the single participant level, there are both overlaps and spatial uniqueness in the location of individual endpoints. For example, while group level analysis revealed that area V1 and area V2 showed preferential connectivity with overlapping regions of the posterior medial hippocampus, when visualising individual endpoints associated with each of these areas at the single participant level, we can see that some endpoints overlap while others display spatially unique patterns (see image below). Although a more in-depth analysis of individual variability in these patterns was beyond the scope of this investigation (as noted on Page14; Lines 379-381), we agree with Reviewer 1 that this is an important point to note in the manuscript. We have, therefore, included additional text touching on this and have included a new Supplementary Figure (Page 42; also see below) to emphasise that, at the single participant level, different cortical areas display both overlapping and spatially unique endpoints within specific regions of the hippocampus (using areas V1 and V2 as an example).

We have included the following text in the Results section (pp. 14, lines 370-379);

“Finally, while we observed clear overlaps in the group averaged EDMs associated with specific cortical areas, a closer inspection of individual endpoints at the single participant level revealed that endpoints associated with different cortical areas displayed both overlapping and spatially unique characteristics within these areas of overlap. For example, at the group level, areas V1 and V2 showed preferential connectivity with overlapping regions of the posterior medial hippocampus (see Supplementary Figure S5) while, at the single participant level, individual endpoints associated with each of these areas display both overlapping and spatially unique patterns (see Supplementary Figure S6). This suggests that, while specific cortical areas display overlapping patterns of connectivity within specific regions of the hippocampus, subtle differences in how these cortical regions connect within these areas of overlap likely exist.”

Reviewer #2 (Public Review):

Dalton and colleagues present an interesting and timely manuscript on diffusion weighted imaging analysis of human hippocampal connectivity. The focus is on connectivity differences along the hippocampal long axis, which in principle would provide important insights into the neuroanatomical underpinnings of functional long axis differences in the human brain. In keeping with current models of long-axis organisation, connectivity profiles show both discrete areas of higher connectivity in long axis portions, as well as an anterior-to-posterior gradient of increasing connectivity. Endpoint density mapping provided a finer grained analysis, by allowing visualisation of the spatial distribution of hippocampal endpoint density associated with each cortical area. This is particularly interesting in terms of the medial-lateral distribution with hippocampal head, body and tail. Specific areas map to precise hippocampal loci, and some hippocampal loci receive inputs from multiple cortical areas.

This work is well-motivated, well-written and interesting. The authors have capitalised on existing data from the Human Connectome Project. I particularly like the way the authors try to link their findings to human histological data, and to previous NHP tracing results.

Many thanks.

1) There are some important surprises in the results, particularly the relatively strong connectivity between hippocampus and early visual areas (including V1) and low connectivity with areas highly relevant from functional perspectives, such as the medial prefrontal cortex (rank order by strength of connectivity 7th and 78th of all cortical structures, respectively). This raises a concern that the fibre tracking method may be joining hippocampal connections with other tracts. In particular, given the anatomical proximity of the lateral geniculate nucleus to the body and tail of the hippocampus, the reported V1 connectivity potentially reflects a fusion of tracked fibres with the optic radiation. In visualizing the putative posterior hippocampus-to-V1 projection (Figure 4B, turquoise), the tract does indeed resemble the optic radiation topography. Although care was taken to minimise the hippocampus mask 'spilling' into adjacent white matter, this was done with focus on the hippocampal inferior margin, whereas the different components of the optic radiation lie lateral and superior to the hippocampus.

We agree with Reviewer 2 that our observations relating to area V1 could be the result of limitations inherent to current tracking methodology. Indeed, probabilistic tracking can result in tracks mistakenly ‘jumping’ between fibre bundles. Unfortunately, primarily due to limitations in image resolution, we do not believe that we can categorically rule this possibility out in the current dataset beyond the measures we have already taken in our analysis pipeline. We have now included additional text in the Discussion acknowledging and emphasising this possible limitation of our study.

We have included the following text in the Discussion section (Page 25; Lines 694-699);

“Also, we cannot rule out that some connections observed in the current study may result from limitations inherent to current probabilistic fibre-tracking methods whereby tracks can mistakenly ‘jump’ between fibre bundles (e.g. for connections between the posterior medial hippocampus and area V1 due to the proximity to the optic radiation), especially in “bottleneck” areas. Again, future work using higher resolution data may allow more targeted investigations necessary to confirm or refute the patterns we observed here.”

Beyond the possibility of tracks jumping between fibre bundles, we feel it is important to emphasise that an integral part of our analysis was the detailed attention we took to minimise mask ‘spillage’ of the entire hippocampus mask. It is not the case that we primarily focussed on inferior portions of the hippocampus as stated by Reviewer 2. Equal focus was paid to medial, lateral and superior portions of the mask which lie adjacent to visual thalamic nuclei, the optic radiation posteriorly and a number of other structures. We can see that our description relating to this lacked the necessary detail to convey this important point clearly and we apologise for the confusion. We have, therefore, included additional text in the Methods section clarifying this further.

We have included the following text in the Methods section (Page 26; Lines 751-755);

“We took particular care to ensure that all boundaries of the hippocampus mask (including inferior, superior, medial and lateral aspects) did not encroach into adjacent white or grey matter structures (e.g., amygdala, thalamic nuclei). This minimised the potential fusion of white matter tracts associated with other areas with our hippocampus mask.”

These points notwithstanding, our results support recently observed structural and functional associations between the posterior hippocampus and early visual processing areas. We agree that these findings are potentially of great conceptual importance for how we think about the hippocampus and its connectivity with primary sensory cortices in the human brain and we have now included a brief comment relating to this in the Discussion.

We have included the following text in the Discussion (Page 23-24; Lines 638-644);

“However, this observation supports recent reports of similar patterns of anatomical connectivity as measured by DWI in the human brain (38) and functional associations between these areas (43, 60). Collectively, these findings are potentially of great conceptual importance for how we think about the hippocampus and its connectivity with early sensory cortices in the human brain and open new avenues to probe the degree to which these regions may interact to support visuospatial cognitive functions such as episodic memory, mental imagery and imagination.”

2) A second concern pertains to the location of endpoint densities within the hippocampus from the cortical mantle. These are almost entirely in CA1/subiculum/presubiculum. It is, however, puzzling why, in Supp Figure 2, the hippocampal endpoints for entorhinal projections is really quite similar to what is observed for other cortical projections (e.g., those from area TF). One would expect more endpoint density in the superior portions of the hippocampal cross section in head and body, in keeping with DG/CA3 termination. I note that streamlines were permitted to move within the hippocampus, but the highest density of endpoints is still around the margins.

We agree with Reviewer 2 that, in relation to the entorhinal cortex, we would expect to see more endpoint density in areas aligning with the dentate gyrus (DG) and CA3 regions of the hippocampus. We noted in the discussion that “Despite the high-quality HCP data used in this study, limitations in spatial resolution likely restrict our ability to track particularly convoluted white-matter pathways within the hippocampus and our results should be interpreted with this in mind”. We believe that this limitation applies to pathways between the entorhinal cortex and DG/CA3. We have now included additional text specifically noting that this limitation likely affects our ability to track streamlines as they relate to DG/CA3. A targeted investigation of this effect using higher resolution diffusion MRI data may help address this issue, and this will be the subject of future work.

We have included the following text in the Discussion (Page 25; Lines 690-693);

“Indeed, this may explain the surprising lack of endpoint density observed in the DG/CA4-CA3 regions of the hippocampus where we would expect to see high endpoint density associated with, for example, the entorhinal cortex which is known to project to these regions. Future dedicated studies using higher resolution data are needed to assess these pathways in greater detail.”

3) On a related point, the use of "medial" and "lateral" hippocampus can be confusing. In the head, CA2/3 is medial to CA1, but so are subicular subareas, just that the latter are inferior.”

We agree that applying the terms ‘medial’ and ‘lateral’ to our three-dimensional representations can lead to some ambiguities and confusion. We have included a new description defining our use of these terms in the Results section.

We have included the following text in the Results section (Page 10; Lines 268-273).

“In relation to nomenclature, our use of the term ‘medial’ hippocampus refers to inferior portions of the hippocampus aligning with the distal subiculum, presubiculum and parasubiculum. Our use of the term ‘lateral’ hippocampus refers to inferior portions of the hippocampus aligning with the proximal subiculum and CA1. In instances that we refer to portions of the hippocampus that align with the DG or CA3/2 we state these regions explicitly by name”.

Author Response*

Reviewer #3 (Public Review):

AAA protein are involved in a variety of cellular activity. They all share the same structural fold and still they are all incredibly specialised. This study works towards the direction of understanding the unique specialisation of the AAA protein ATAD1. While the general mechanism of substrate threading by AAA proteins is by now fairly well-elucidated, it remains to describe and understand the finer structural protein details that make each specific AAA perform unfolding (threading) of certain substrate rather than others. Additionally, regulation and stabilisation of each AAA is also finely regulated by specific subdomain.

This work is definitively strong in addressing these two points for ATAD1.

The structural data are solid and the analysis of the pore loops residues and the role of a11 overall convincing.

1) The cell fluorescence microscopy assay is a very good tool for checking in the cell the hypothesis risen by analysing of the structure. However, the assay is currently only based on the localisation of the Gos28 substrate, which leaves open the possibility that ATAD1 a11 mutants will have a different phenotype on different substrates.

We agree with the reviewer that it would be interesting to test ATAD1’s activity on other known substrates. To do that, we picked Pex26, an established tail-anchored protein substrate of ATAD1. We stably expressed EGFP-Pex26 in ATAD1-/- cells and tested the effect of ATAD1 expression on Pex26 mislocalization. As shown in the figure below, we found that although the general trend observed for Gos28 also holds true for Pex26, the measured PCC values clearly have a bimodal distribution, with some cells showing the complete mislocalization (PCC = 1.0) of Pex26. One exciting possibility to explain this result is that Pex26 is important in peroxisome biogenesis. Once enough Pex26 is mislocalized to the mitochondria, peroxisomal biogenesis becomes impaired, thus causing less Pex26 to be correctly inserted. A partial impairment in Pex26 peroxisomal insertion in turn creates a vicious cycle that leads to the complete mislocalization of Pex26. It will be an interesting to follow up on the cause of this bimodal distribution, which, however, is beyond the scope of this paper.

*Quantification of live-cell imaging showing using the localization of EGFP-Pex26 as a readout. Mean Pearson correlation coefficient (PCC) values and the SEM between EGFP-Pex26 and the mitochondria when expressing the ATAD1 variants indicated. Individual cell PCC values are represented as a single dot. *

Author Response

Reviewer #2 (Public Review):

Chylinski et al. investigate sleep EEG properties in a cohort of older individuals, to test how sleep microarchitecture is linked to amyloid burden and memory changes over time, which is important for understanding the evolution of neurodegenerative disease. They report that the temporal coupling of spindles to a specific slow wave type, which they term 'slow switchers', is correlated with A-beta and predictive of subsequent memory decline years later. Strengths of the study are the extensive sleep phenotyping, relatively large cohort, and the acquisition of a follow-up cognitive timepoint two years later. The effect sizes are small, which may be expected due to the nature of this scientific question. The analyses are interesting, but some additional analyses and reporting would be beneficial in the methods and results, particularly the analyses focused on differentiating SW types.

We thank the reviewer for their comments and suggestions which we address in the following lines.

Main issues:

1) The EEG signal processing and analysis methods need additional details. A coincidence of slow wave peaks and spindles is defined as 'co-occurrence' - within what time window do the two events have to co-occur to be considered coincident?

SW and spindles were detected automatically through published approaches. If the initiation of a spindle was located within the detected period of a SW, both events were considered as co-occurring. The phase of the coupling was set as the moment of the ignition of the spindle with respect to the down and up states of the SWs. We modified the methods to provide more details on these aspects (PAGES 17-18): “After detection of SW and spindles, analysis of their coincidence was performed. A coincidence was defined as to occurrence of the ignition of a spindle within the time frame of a SW: SW ignition at zero µV = phase 0°, SW maximum hyperpolarisation = π/2, zero crossing = π, SW maximum depolarisation = 3π/2, SW termination at zero µV = 2π. This criterion was used on slow and fast switchers.”

2) In Fig. 1, the analysis does not control for the fact that slow switcher SWs will have a longer time period before the peak than spindles. Fig. 1b's result that more spindles occur in the same phase period could be partially explained by the fact that this phase simply takes a longer period of time for slow switcher SWs (i.e. greater chance of having a spindle if it takes 5x as much time to get from phase -1 to 0, as suggested in Fig. 1c). A control analysis is needed to account for this.

The duration of the entire SW cycle (zero >> down state >> zero >> up state >> zero) is shorter for SW of overall faster frequency while the duration of the down-to-up-state transition will be shorter in fast switchers. Yet, whether a precise phase of coupling occurs does not depend on the overall frequency or transition frequency of the SW. It could potentially affect the shape of the distribution of phase which could form a plateau. The fact that we find a narrow peak of coupling phase for slow switchers pleads against this bias. The fact that distribution of coupling phase is much broader suggests that spindles do not really co-occur at a particular phase of the SW (yet distribution is not uniform, please see next comment). The former figure 1c consisted in a circular heatmap of the phase distribution of spindles onto SW and did not relate to duration between phases for each slow wave type. We removed this circular display as it was redundant with former figure 1b. Please note that figures 1 and 2 were merged in a single figure 1. We further invite the reviewer to read our response to Essential comment 1) on a related matter dealing with SW type duration.

3) The green shading in Fig. 1c seems to suggest some phase-coupling for fast switchers too, so it would be appropriate to add a statistic for the statement "no such preferred coupling was detected for fast switcher SWs".

As already mentioned, we removed fig. 1c from the revised version of the manuscript. We thank the reviewer for this insightful comment. Our initial submission included statistics to demonstrate that coupling phase was different between SW types. Based on visual inspection of the distribution we concluded that only slow switcher SWs showed a preferential coupling phase, but we did not actually test this assumption. We now test it and find that both distributions are not uniform, meaning that, although spindle coupling onto fast switcher SWs is much more widespread, is not random. It is important to note that this result does not interfere with our main finding that is that only spindle coupling onto slow switcher SWs is associated with Ab and memory.

We corrected the results section according to this new result (PAGE 8):”We assessed whether spindles showed a preferential phase of anchoring with both slow and fast switcher SWs. Qualitative appreciation of the distributions suggests that there is no preferential phase of anchoring of spindles onto the fast switcher SWs while spindle initiation onto slow switcher SWs would show a clear preferred phase (Figure 1e). Watson U² tests indicate, however, that the phase of anchoring onto slow and fast SWs are both non-uniformly distributed (see methods; slow switcher SWs: U² = 904.29, p <0.001; fast switcher SWs: U² = 136.76, p <0.001), i.e. they both show some phase preference. Importantly, further statistical analysis with Watson’s U² test showed that the distribution of spindles anchoring phase was significantly different between slow and fast switcher SWs (U² = 71.143, p <0.001).”

We also modified the discussion accordingly (PAGE 12): “Three present results confirm that the two types of SW –slow and fast switchers – behave differentially. First, sleep spindles show a difference in their preferential coupling with the transition period from down-to-up state of the slow and fast switcher SWs. While spindles occurring concomitantly to slow switchers SWs show a clear preference to the late part of the depolarisation phase, spindles co-occurring with fast switcher SWs show more widespread phase of coupling (that is still not random/uniformly distributed).”

We further modified the method section accordingly (PAGE 20): ”We further assessed whether the distribution of spindle onset on the phase of SWs per type was different from a uniform distribution. For each SW type, we generated series of uniformly distributed random values composed of the same number of values spanning the same ranges. Watson’s non-parametric two-sample U² test compared this random series to the actual values.”

4) The precise implementation of the main statistical tests is a bit unclear in the Methods. When stated "slow wave spindle coupling" is an independent variable, what precisely is in the variable? Is it the phase of the coupling? Is it the proportion of SWs with a spindle for one individual?

We used the cosine of the individual averaged phase of coupling of the initial part of the spindle within the SW cycle. Cosine were preferred to accommodate the circular nature of a phase detection where the end of SW cycle can also be the beginning of the next SW cycle (using phase of coupling in degrees rather than cosine value did not alter the statistical outputs of our analyses.

We modified the methods to provide more details on these aspects (PAGES 17-18): “After detection of SW and spindles, analysis of their coincidence was performed. A coincidence was defined as to occurrence of the ignition of a spindle within the time frame of a SW: SW ignition at zero µV = phase 0°, SW maximum hyperpolarisation = π /2, zero crossing = π, SW maximum depolarisation = 3π/2, SW termination at zero µV = 2 π. This criterion was used on slow and fast switchers.” And PAGE 20: “The phase of spindle-SW coupling was set as the phase of the onset of the spindle on the SW converted to its cosine value, to deal with the circularity of the phase variable and perform linear statistics (analysis using the phase in degrees yielded the same outcome).”

5) Given the small effect size reported for slow switcher SWs, it seems a potential reason for not finding the same result in fast switcher SWs is that there are ~4 times fewer fast switcher SWs. Even if fast switcher SWs had the same size as the underlying effect, is this sample size sufficient to detect it? Is it possible that the difference in the slow wave types reflects the different number of events in each group? Since the analysis does not directly test for a difference between fast and slow (but rather detects a significant effect with slow SWs, and fails to detect it with a smaller number of fast SWs, which does not specifically test for a difference between the two), it seems there is still additional evidence needed if aiming to draw conclusions about these fast and slow SWs being different.

Please refer to the second main issue above regarding the potential influence of the number of SW types.

Reviewer #3 (Public Review):

Strengths: - EEG analyses are novel, extensive, and carefully done. - Inclusion of baseline amyloid PET is a strength. - There is great interest in the transition from normal cognition to cognitive impairment in the earliest stages of disease, and therefore this study population is quite relevant.

We thank the reviewer for acknowledging the interest of our work and for raising important issues.

Weaknesses:

1) The abstract isn't clear regarding the number of participants supporting the principal conclusions. The conclusion RE amyloid was based on the stated n=100, while the one concerning cognitive decline was based only on a subset of n=66.

We have modified the abstract to make it clear that only 66 individuals took part to the longitudinal assessment.

2) In the statistical methods, the authors' stated primary analyses were 1) coupling of spindles to slow switching slow waves and 2) coupling of spindles to fast switching slow waves, neither of which has anything specific to do with cognition or dementia. They adjusted these two analyses for 2 comparisons with a threshold of p=0.025. The remainder of the analyses are considered by the authors to be exploratory and therefore not to require adjustment for multiple comparisons. However, in the abstract, the stated goal of the study is to investigate "whether 22 the coupling of spindles and slow waves are associated with early amyloid-beta (Aβ) brain burden, a hallmark of AD neuropathology, and cognitive change over 2 years". This doesn't align with the stated primary analyses in the statistical methods. Moreover, it suggests at a minimum 2 primary outcomes (amyloid burden and cognitive change), and 2 predictors (spindle-slow-switch phase, and spindle-fast-switch phase) for 4 primary analyses that need to be corrected for, resulting in a p-value threshold of 0.05/4 = 0.0125. Neither of the study's primary conclusions (1. that earlier occurrence of spindles on slow-depolarization slow waves is associated with higher prefrontal Ab burden p=0.014 and 2. that earlier occurrence of spindles on slow-depolarization slow waves is associated with greater longitudinal memory decline p=0.032) meets this cutoff. This is even if we disregard the many other comparisons that were made (in the study, there are at least 3 outcomes of interest - baseline cognition, baseline amyloid, and change in cognition) and many EEG predictors examined. Indeed, if we consider all the analyses performed in this study (3 outcomes as above [amyloid, baseline cognition, change in cognition] x 7-8 different EEG measures = 24 comparisons) the 2 significant results at p<0.05 are not all that much more than would be expected by chance.

We thank the reviewer for raising this important issue. Please refer to Essential comment 3) for full details regarding this point.

3) It is not 100% clear how the authors selected specifically phase angles between spindles and slow waves (rather than, for instance, percent coincidence, or dispersion of phase angle as a measure of the "tightness" of coupling) as their primary predictors. If these were looked at they would require even more extensive adjustment for multiple comparisons.

Other metrics could indeed be envisaged but they would raise multiple comparison issues. Our rationale is that it is the timing of spindle and SW co-occurrence (or coupling) that matters for optimal information exchange during sleep. As reported at the beginning of the result section a substantial part of spindle and SW co-occur meaning we are not focusing on a marginal aspect of sleep microstructure. In addition, previous studies (Bouchard et al. 2021) reported that the phase of spindle to SW coupling changes in ageing when it is established that ageing is associated with important sleep changes. This further supports that we are focussing on a relevant aspect of sleep microstructure. Note that we do not observe an effect of age on spindle-SW coupling phase, most likely because of the limited age-range of our sample (50-69y)

We modified the methods to provide more details on these aspects (PAGES 17-18): “After detection of SW and spindles, analysis of their coincidence was performed. A coincidence was defined as to occurrence of the ignition of a spindle within the time frame of a SW: SW ignition at zero µV = phase 0°, SW maximum hyperpolarisation = π /2, zero crossing = π, SW maximum depolarisation = 3π/2, SW termination at zero µV = 2π. This criterion was used on slow and fast switchers.” And PAGE 20: “The phase of spindle-SW coupling was set as the phase of the onset of the spindle on the SW converted to its cosine value, to deal with the circularity of the phase variable and perform linear statistics (analysis using the phase in degrees yielded the same outcome).”

4) The authors conclude that their findings suggest that "altered coupling of sleep microstructure elements, key to its mnesic function, contributes to poorer brain and cognitive trajectories in ageing." In their discussion, they do acknowledge that this sort of causal inference is not possible based on the non-interventional nature of this study. Indeed, it is certainly plausible that differences in the phase relationship between spindles and slow waves, rather than being contributors to cognitive decline, may instead be markers of early AD-related brain changes, not picked up on by amyloid PET (e.g. amyloid oligomers, or non-amyloid processes) that are the proximate cause of 2-year cognitive decline.

We modified the text to temper our statement and state that spindle-SW coupling and cognition could be sensitive to a similar causal factor (PAGE 15): “Finally, given that our protocol does not include manipulation of the coupling of the spindles onto the SWs, it precludes any inference on the causality of one aspect onto the other. It may be that cognition and the coupling of spindle and SWs are sensitive to the same age-related or AD-related phenomenon (e.g. presence of amyloid oligomers, or non-amyloid processes, that would go mostly undetected using common PET scan Aβ radioligand).

Together, our findings reveal that the timely occurrence of spindles onto a specific type of SWs showing a relative preservation in ageing may play an important role in ageing trajectory, both at the cognitive level and with regards to structural brain integrity. These findings may help to unravel early links between sleep, AD-related pathophysiology and cognitive trajectories in ageing and warrants future clinical trials attempting at manipulating sleep microstructure or Aβ protein accumulation.”

Author Response

Reviewer #2 (Public Review):

Tumors such as glioblastoma contain several types of cells: cancerous and reactive non-cancerous cells, and among cancerous cells, cancer cells with tumorigenic properties so-called "stem" and pseudo-differentiated cancer cells.

Strengths: a multidisciplinary international cooperation gathering complementary expertises. An impressive quantity of experiments and presented data (28 supplementary figures with multiple panels!). First description of Fibromodulin as a secreted factor acting in a paracrine manner to activate an Integrin-dependent Notch signaling in endothelial cells. A detailed analysis of the molecular signaling triggered by integrin activation. Most of the results support this claim.

Weaknesses: Several formulations in the introduction are controversial. Several results should be more clearly explained and the precise methods used are difficult to find since they are dispersed between the text, the "methods section" and often lacking in the legend of the figure.

These points are addressed appropriately; in particular, the figure legends are extensively modified. Changes are also added in the methods section.

More precisely the following points should be addressed:

1- The formulation "non-cancer stem cells" is confusing since these are cancer cells but without the functional characteristics of cancer stem cells and within the tumor exist non-cancer cells co-opted to the tumor, such cells being called "microenvironment" even if they are bona fide part of the tumor.

We understand the possibility that the use of "non-cancer-stem cells (non-CSCs)" may create confusion as it may sound like referring to stromal cells of cancer that are actually non-cancer cells of the tumor. This was rightly pointed out by reviewer # 2. After obtaining advice from Dr. Caigang Liu, Reviewing Editor, we decided to use "glioma stem-like cells" (GSCs) and "differentiated glioma cells" (DGCs) in place of CSCs and non-CSCs respectively.

2- Lines 91 to 95 are particularly controversial and even erroneous since CD133- GSC have been reported by several authors and nestin is not a selective marker of CSC. This is most-likely due to referencing reviews of a single group that promoted this dichotomy that do not correspond to most of the reported results. Furthermore it is well known that GSC proliferation or DGC reprogrammation to GSC are favored by hypoxia, illustrated in vivo by the failure of anti-VEGF treatment to increase life expectancy.

3- As soon as 2012-2013 (thus before the referenced Suva et al 2014 paper), the group of Thierry Virolle demonstrated that stem cell-like properties of GSC fuel glioblastoma development by providing the different cell types that comprise the tumor. Reference to their work is surprisingly missing. Of note, after describing that the miR-302-367 cluster is strongly induced during stemness suppression, they showed that stable miR-302-367 cluster expression is sufficient to suppress the stemness signature, self-renewal, and cell infiltration within a host brain tissue, through inhibition of the CXCR4 pathway involving the SHH-GLI-NANOG network. Micro-RNA profiling studies to search for regulators of stem cell plasticity, allowed them to identified miR-18a as a potential candidate and its expression correlated with the stemness state. MiR-18a expression promotes clonal proliferation in vitro and tumorigenicity in vivo.

Turchi L, Debruyne DN, Almairac F, Virolle V, Fareh M, Neirijnck Y, BurelVandenbos F, Paquis P, Junier MP, Van Obberghen-Schilling E, Chneiweiss H, Virolle T. Tumorigenic potential of miR-18A* in glioma initiating cells requires NOTCH-1 signaling. Stem Cells. 2013 Jul;31(7):1252-65. doi: 10.1002/stem.1373. PMID: 23533157

Fareh M, Turchi L, Virolle V, Debruyne D, Almairac F, de-la-Forest Divonne S, Paquis P, Preynat-Seauve O, Krause KH, Chneiweiss H, Virolle T. The miR 302367 cluster drastically affects self-renewal and infiltration properties of gliomainitiating cells through CXCR4 repression and consequent disruption of the SHHGLI-NANOG network. Cell Death Differ. 2012 Feb;19(2):232-44. doi: 10.1038/cdd.2011.89.

We agree with reviewer # 2 (points 2 and 3) that there exists heterogeneity among GSCs of glioma and that multiple markers can characterize the GSCs. Hence, the statement regarding biomarker of GSC is addressed appropriately, taking the recommendations. Accordingly, references that reported the stemness properties of CD133- glioma cells (Beier et al., 2007; Chen et al., 2010; Joo et al., 2008; Ogden et al., 2008; Wang et al., 2008), involvement of miR302-367 cluster and miR18A* in the regulation of stemness (Fareh et al., 2012, Turchi et al., 2013), and the existence of stem cell-associated heterogeneity in GBM (Dirkse et al., 2019) are referred in the revised manuscript.

4- A main question arises from the use of multiple cellular models, some highly valuables such as MGG4, MGG6 and MGG8, that correspond to patient-derived cell line maintained in culture conditions known to preserve the phenotype and genotype encountered in real patient tumors, and other cell lines (LN229, U251, U87) known to be highly unrepresentative since grown for a long time in serum conditions. However, after the first set of experiments, only MGG8 is used in the rest of the paper, with no validation on MGG4 and MGG6 and one should wonder why.

We agree with the reviewer that more human patient-derived GSC lines could have been used in animal models. However, we would present our views on the usage of GSC lines as below:

1) We have used three patient-derived GSC lines (MGG4, MGG6, and MGG8) for the initial discovery and in vitro validation of the DGC-specific expression of FMOD.

2) We have used one human patient-derived GSC line (MGG8) and two murine GSC lines (AGR53 and DBT-Luc) in an intracranial orthotopic mouse model experiment to prove the importance of FMOD induced angiogenesis in tumor growth. While the MGG8 line silenced for FMOD using short hairpin RNA (shRNA) was used to prove the importance of FMOD in tumor angiogenesis and growth, AGR53 and DBT-Luc lines carrying doxycycline-inducible shRNAs proved the importance of FMOD secreted by de novo generated DGCs from a GSC initiated tumor in angiogenesis and growth.

3) The only mouse model experiment carried out using the U251 cell line is now moved to the supplementary section as these cell lines are highly unrepresentative since they are grown for a long time in serum conditions, as recommended by reviewer # 2

4) The other places where the established glioma cell lines, LN229, U251, and U87 used are in main figure 4 and the associated supplementary figures. In these experiments, we used these cells only as a source of secreted FMOD to study the angiogenesis-inducing property. However, we would like to point out that conditioned media from MGG4, MGG6, and MGG8 also showed the angiogenesis-inducing property of FMOD.

5- Results presented in Fig2C and 2D are really strange and do not support the claim that "results indicate that FMOD secreted by DGCs is essential for the growth of tumors initiated by GSCs. FMOD induces angiogenesis of host-derived and tumor-derived endothelial cells" First, one should wonder about the subcutaneous model used since such xenograft do not raise a glioblastoma-like tumor but a mesenchymal-like highly undifferentiated tumor. Second, considering the development of the graft at day 5 and the growth curve of GSC alone, one should wonder why inhibiting expression of FMOD in DGC triggers a necrosis of the initial tumor and not a slower growth parallel to the one of GSC alone.

We agree with the reviewer in principle. However, we would like to explain the possible reason for the acute reduction in tumor growth after FMOD silencing in DGCs as below. The FMOD provided by the coinjected DGCs may induce extensive angiogenesis and may result in faster tumor growth. In such conditions, silencing FMOD through doxycycline injection may lead to phenomena like necrosis, thus resulting in a drastic reduction in the tumor size.

The subcutaneous model was used only for the co-implantation experiment. The intracranial orthotopic mouse model is used in all our animal experiments.

6- Line 445: "Cellular hierarchy is well established in GBM." This is an old view mimicking normal differentiation. Since GSC can pseudo-differentiate into DGC and DGC can be reprogrammed into GSC, no hierarchy exists, only cells with different properties and functions in tumor growth. GSC is not the origin of glioblastoma but the ultimate state of aggressiveness.

Keeping the views of the reviewer, we have now removed the sentence "Cellular hierarchy is well established in GBM" which appeared in the beginning of the Discussion. We have indeed discussed the cellular plasticity and the formation of GSCs from DGCs during chemotherapy and hypoxia in 4th paragraph in the revised manuscript.

7- Lines 452-53 "GSCs are known to promote the establishment of a highly vascularized microenvironment by being in close physical contact with endothelial cells (Calabrese et al., 2007)." This in only partially true since many soluble factors have been described to support the dialog between endothelial cells and GSC: secreted proteins such as VEGF, HDGF, GDF15, and multiple types of microRNA.

We have now added the references that describe the soluble factors from GSCs that induce angiogenesis in the first paragraph of the Discussion of the revised manuscript.

Author Response

Reviewer #1 (Public Review):

Thank you for your comments. We incorporated concepts, details, and analysis to make the narrative clearer. We tested some additional computational simulations, completely silencing the inhibitory neurons, to investigate inhibition influence in the detection of communication paths. However, by silencing inhibition the firing rate of excitatory neurons increased about 70 times, which impaired the analysis given the limitations of the techniques used. Including the decrease of accuracy in the inference of connections from the spike trains with 70 times more spikes. To obtain similar results as for the empirical data the procedure to exclude spurious connections must be adjusted to be even more rigorous, but this change would make the comparison with connections inferred from actual data unfeasible. Such an increase in firing rate was not observed in our results even for stages of maturation before the excitatory-to-inhibitory GABA switch (7-8 DIV, Soriano et al., PNAS 2008) most likely due to neuron homeostatic mechanisms. We understand and agree with the need for additional models, but the inclusion of such an analysis would require a considerable modification of the pipeline and the format and interpretation of the text. Therefore, we included this issue in the discussion and make explicit the limitations of the current analyses.

Reviewer #2 (Public Review):

Thank you for your review and suggestions.

(1) Once the work used a fully recorded data set, a highly recommended approach for reducing the use of animals, by using creative ways to extract different information from the same data, the study of key mechanisms behind the formation of the networks is limited. However, we used the results to leverage new insights into possible mechanisms and promote ideas to new experimental approaches. The novel contribution of this study relies on the fine-scale analysis of the formation of the information flow in neuronal assemblies. Which could be compared with neuronal firing rate and neuron’s physical location. We formulated one hypothesis related to the activation of silent synapses as a mechanism related to the phenomenon. But other alternative explanations may also be possible. However, we believe our results can help other scientists guide their research to look at synapses activation, GABAR switch, formation of effective networks in low [CA2+]E, and intrinsic neuronal mechanisms related to firing rate control.

(2) Although in vitro experiments have their limitations, we can assume the neuronal assembly hypothesis in Hebb's postulate (Hebb, 1949, doi: 10.1126/science.1238411), that says the coactivation of neurons is what gives rise to functional neural circuits. It means that even dissociated from the brain, if neurons have retained their intrinsic properties, they will connect among them, building networks.<br /> However, we agree that some aims of this work were not very well described. We did not intend to infer neuronal structures from dynamics as sometimes it seems in the first version of the manuscript. In our analysis, by ‘connections’ we meant strong paths for information flow rather than actual structural connections. Synaptic pruning is a structural mechanism that could be for example related to synapses that were not activated. However, despite may exist correlations (Park & Friston, 2013, doi: 10.1126/science.1238411), we cannot directly relate it with the increase in edge density of effective connections. The self-organization of neuronal assemblies is a complex process that involves many mechanisms, and in this work, we are looking at the formation of paths of information flow.

We add this explanation in the Results sections.

Author Response

Reviewer #1 (Public Review):

We thank the reviewer for a very constructive evaluation of our work and for a fair summary of its main strengths. We have addressed her/his main concerns as follows:

1) The experiments involve an invasive neurosurgical procedure used to perform hippocampal imaging, which removes the ipsilateral overlying somatosensory cortex, and it is not possible to evaluate from the data provided that this surgery does not disrupt network function, especially given the focus on movement-related activity patterns.

We thank the reviewer for bringing up this important issue. Indeed, our experimental access to early hippocampal activity with 2-photon calcium imaging relies on a quite invasive procedure. However, the many control experiments we have performed indicate that early hippocampal dynamics were not significantly altered by the surgery. First, our extracellular electrophysiological recordings from a sample of 6 mice (ranging from P6 to P11, Figure 1- figure supplement 1C) show that the frequency of early sharp waves (eSW) was slightly but not significantly reduced in the ipsilateral hemisphere compared to the contralateral one. Of note, a similar “non-significant” decrease had been previously reported by another group (Graf et al 2021 Fig S6C). As suggested by the reviewer, we can speculate that this slight decrease may result from a reduction of the sensory feedback re-afference originating from the right limbs. Indeed, we observed that movements of the right limbs (contralateral to the window implant) elicited a slightly smaller response than those from the left limbs. This observation has been added to Figure 1 - Supplement 1E and described in the results (lines 128-134) and discussion (lines 314-320).

We have performed additional control experiments using EMG nuchal electrodes in two pups aged P5 and P6. We observed that, an hour following the surgery (corresponding to the recovery time in our experimental procedure), the composition of the sleep-wake cycle (with 70 to 80 % of active sleep) was comparable to previous reports (Jouvet-Mounier, 1969, Fig 4). This quantification was added to Figure 1- figure supplement 1B (lines 82-86).

2) State-dependent parameters are not adequately described, controlled, and examined quantitatively to ensure that data from similar behavioral states is being used for analysis across ages. Network activity from wakefulness, REM/active sleep and NREM/quiet sleep should not be presumed to be indistinguishable.

We would like to point out that our analysis across ages focused on the population response following animal movements, and not across all behavioral states. That said, it is true that two types of movements can be distinguished, namely the twitches and the complex ones. To take this behavioral heterogeneity into account, we have now separately quantified the hippocampal activation following twitches (movement during active sleep) and complex movement (during wakefulness). We show in Figure 2 - figure supplement 1B that the hippocampal response to twitches and complex movements is similar across ages. Thus, even if the amount of time spent in each behavioral state is modified over the developmental period that we have studied, we are pretty confident that it does not impact the transition we have described in the relationship between animal movements and hippocampal activity. Additionally, we were able to combine in one P5 mouse pup 2p-imaging with nuchal EMG recordings and separately computed the PMTH for movements observed during REM or wakefulness (Figure 2 - figure supplement 1C). We show that CA1 hippocampal neurons were activated time-locked to movement in both behavioral states, with only the amplitude of the population response differing between wakefulness than during REM. This point is now included in the result section (lines 148-152) and discussed (lines 324-327).

3) Currently employed statistics are not rigorous, unified, or sensitive, and do not support all of the authors' claims. Data shown suggest potentially significant changes that have not been identified due to suboptimal statistical approach and/or underpowering.

We obviously agree with this reviewer that rigorous statistics should be employed and can certify that the data analyzed in the submitted manuscript was carefully examined following that principle. We feel that his/her strong criticism regarding that point was not fully justified. In particular, we do not understand why statistical tests should be “unified” across different figures of the paper. Rather, statistical tests should be adapted to the sample size and distribution. Of course, the same tests were used for similar datasets. This revised manuscript now contains further description and justification of all the tests included in every figure panels.

4) The authors use an artificial neural network approach to infer cell classification (pyramidal cell vs. interneuron). From the data provided, it is not possible to adequately evaluate whether these 'inferred' interneurons represent the same population as conventionally labeled interneurons.

We thank the reviewer for this important remark and apologize for the lack of detailed description of our method to ‘infer’ interneurons. This method was previously published (Denis et al., 2020), and designed to identify interneurons from their calcium fluorescence signals in the absence of a reporter. Most importantly, this cell type classifier was trained and tested on a dataset in which interneurons were labeled using a reporter mouse line (GAD 76-Cre). This dataset is included in this article. This means that all the ‘labelled’ interneurons included here were also used for the training and the test dataset. As for the activity classifier, the training and test data sets covered all the developmental ages used in the study. Thus, the previously published statistics (accuracy/sensitivity) of this classifier should well account for the present analysis. This method is now described in better detail in the results (line 183) and methods parts (lines 616-619). We now also illustrate in the figures how this classifier can infer interneurons with 91% precision (split up of prediction vs ground truth in test data are reported from Denis et al) and that these ‘infered’ interneurons are activated with movement just as genetically ‘labeled’ interneurons (Figure 3 - figure supplement 1B-E).

5) Functional GABAergic activity is not assessed across development (only at P9-10), limiting mechanistic conclusions that can be drawn.

We thank the reviewer for this comment that reveals some lack of clarity in the previous description of our experiments. Indeed, functional GABAergic activity was also assessed before P9, however, given that there are no GABAergic axons in the CA1 pyramidal layer at early stages (for both CCK cf. Morozov and Freund 2003, and prospective PV cells cf. Figure 4A,B), there is no signal to be measured either. We have now added a new figure (Figure 4 - figure supplement 1) to clarify this point. In agreement with our Syt2 longitudinal quantification, we show, using tdTomato expression in the Gad67cre driver mouse line, that GABAergic perisomatic innervation is only visible after p9. This matches as well our attempted imaging experiments using axon enriched GCaMP in mice before P9.

6) The present analyses are almost exclusively focused on movement-related epochs, substantially limiting conclusions that can be drawn as to what neural dynamics are actually occurring during epochs that the authors propose comprise internal representations.

We agree with this reviewer that our study is focusing on movement-related episodes and that we are not assessing hippocampal representations, especially since the pups are recorded in conditions that minimize external environmental influences. Still, we observe that there is a switch in the distribution of spontaneous activity in CA1 after P9, with most activity occurring outside from the synchronous calcium events and detached from movement. The exact nature of this activity remains to be studied, however, it is most likely not evoked by extrinsic phasic inputs and rather represents local dynamics. We have now removed reference to ‘internal representations” or “internal models” in the two previous instances of use i(abstract and discussion) and replaced them, when possible by “self-referenced” representations alluding to self-generated-movement-triggered activity.

Reviewer #2 (Public Review):

The study by Dard et al aims to uncover the post-natal emergence of mature network dynamics in the hippocampus, with a particular focus on how pyramidal cells and interneurons change their response to spontaneous limb movement. Several previous studies have investigated this topic using electrophysiology, but this study is the first to utilize 2-photon calcium imaging, enabling the recording of hundreds of individual neurons, and discrimination between pyramidal cell and interneuron activity. The aims of the study are of broad interest to all neuroscientists studying development (including neurodevelopmental disorders) and the basic science of network dynamics.

The main conclusions of the study are that (1) in early life, most pyramidal cell activity occurs in bursts synchronized to spontaneous movement, (2) by P12, pyramidal cell activity is largely desynchronized from spontaneous movement, and indeed movement triggers an inhibition in the pyramidal network (approximately 2-4sec following movement), (3) unlike pyramidal cells, interneuron activity remains positively modulated by movement, throughout the period P1-P12, (4) the changes in pyramidal cell activity are achieved by means of increases in perisomatic inhibition, between P8 and P10.

It should be noted that conclusion (1) and to some extent conclusion (2) have already been reported, by previous studies using electrophysiology (as clearly acknowledged by the authors).

A principal strength of this manuscript is the extremely high quality of the data that the authors are able to use in support of (1) and (2), with very large numbers of neurons being analyzed to clearly delineate the relationship between neural activity and movement. The finding that pyramidal cells become inhibited following movement is novel, I believe. Furthermore, this study offers the first description of the development of interneuron activity, in this experimental context.

The main weakness of the manuscript is that the authors cannot provide direct functional evidence for the conclusion (4). As shown by the analysis in support of conclusion (3), interneuron activity with respect to movement does not actually change during the developmental period being studied, making it prima facie unlikely that this is the cause of changes in pyramidal network responses to movement. To overcome this, the study describes the activity of GABA-ergic axon terminals in the pyramidal cell layer at P9-10, but it appears that due to technical problems this was not possible in younger animals. It, therefore, remains unknown if the functional inhibitory inputs to pyramidal cells are changing over the ages studied.

We thank this reviewer for acknowledging the broad interest of the study, its novelty, and the high quality of our dataset. The main concern raised by this reviewer (lack of axonal activity experiments in younger pups) was in fact a misunderstanding of the experiments performed and we apologize for this lack of clarity. Reviewer #2 is correct in that the relationship between interneuron activity and movement does not change over the developmental period studied. However, we have only included GABAergic axonal imaging after P9, not due to a technical problem but rather because there are no GABAergic axons in the pyramidal layer before (we see GABAergic neurites only outside the layer). We have now dedicated a new supplementary figure (Figure 4 - figure supplement 1) to explain why we could not image GABAergic axons in the pyramidal cell layer at earlier developmental stages.

The study does describe increases in the protein synaptotagmin-2, in the pyramidal cell layer, between P3 and P11, but in my opinion, this molecular evidence for increases in perisomatic inhibition does not match the (very high) standards of neuronal function/activity reported elsewhere in the manuscript.

In the absence of parvalbumin expression in early development, synaptotagmin-2 has been described as the best marker of prospective PV boutons in the cortex (Someijer et al. 2012). This molecular marker has been used in other studies (Modol et al. Neuron 2020, Sigal et al. PNAS 2019). We respectfully disagree with this reviewer, and think that quantification from immunohistochemistry experiments is as high of a standard as functional imaging as it is the only way to describe the anatomical structure of active neuronal processes.

Reviewer #3 (Public Review):

Dard and colleagues use both in vivo calcium imaging and computational modelling to explore the relationship between the early movement of CA1 hippocampal activity in neonatal mice.

The manuscript represents a significant technical advance in that the authors have pioneered the use of multiphoton imaging to record activity in the hippocampus of awake neonates. Overall the presentation of the data is convincing although I would recommend a number of tweaks to the figures and the inclusion of some raw data to better direct and inform non-expert readers. I also believe that the assessment of long-range inputs using pseudo-rabies virus should be present in the main body of the manuscript as opposed to supplemental material. The computational modeling supports their idea but does not exclude other possibilities. Further, it is not clear to what extent the strengthening of local excitatory input onto the interneurons - the dominant route of recurrent input in the hippocampus, is important; something that the authors acknowledge in the discussion.

Overall, I believe the paper adds to our knowledge of the timeline of development and further identified the postnatal day (P)9-P10 window as important in emergent cortical processing. The fact that this is linked to an increase in GABAergic innervation has implications for our understanding of both normal and dysfunctional brain development.

We thank the reviewer for his constructive comments and helpful suggestions. As suggested, this revised version now includes some raw-data and better descriptions to guide non-expert readers. Regarding the inclusion of rabies-tracing experiments in the main part of the MS, we would like to state here that there are still a number of limitations with the use of this method during development (incubation time, spatial precision of the injection site, etc. ) that limit the interpretation and quantification of the results. As a result, we have decided to remain only qualitative, focusing on identifying the brain regions that could send projections onto CA1 pyramidal cells and interneurons. We believe that this type of description is more suited for a supplementary figure than a principal figure, but will be happy to change this, if the reviewer and editors think otherwise.

Author Response

Reviewer #2 (Public Review):

The basic idea of assessing whether adaptive responses in speech learning mirror those observed in upper limb movements is appealing. However, there are a number of concerns regarding the present paper. First, the perturbations which are used are unpredictable and hence unlearnable. From work on upper limb movement, it is known that when subjects are presented with unlearnable perturbations, their response is adaptive but different than that observed in response to learnable perturbations. With unpredictable perturbations subjects cocontract to resist limb displacement whereas a directional response is observed when the perturbation is predictable. Although compensation is present here in response to unpredictable perturbations, whether it matches that which occurs in learning is uncertain. It is hard to know whether responses to unpredictable speech perturbations can serve as a model to understand the adaptation that occurs during learning. This would seem important in the present context where the goal is to understand the structure of sequential dependencies in learning.

We agree that differences exist between adaptive responses to consistent vs. inconsistent perturbations, particularly in studies with mechanical perturbations of the limb. Random perturbations very similar to those used here have been used extensively in the reaching literature studying one-shot learning, especially when the error is purely sensory (i.e. when visual feedback is perturbed), taking co-contractions due to limb displacement out of the equation. The current study has a similar advantage in avoiding the possibility of stiffening/co-contraction as an adaptive strategy, and does show that even inconsistent sensory errors can elicit measurable directional responses. We agree that the magnitude of this one-shot adaptation may underestimate the adaptation seen in when perturbations are consistent across trials; a brief discussion of these points has been added (lines 159-165).

A further concern is the magnitude of the on-line compensation response and the adaptation response observed in the following movement. While there are statistical differences in the magnitudes of responses to upward and downward shifts in auditory feedback, neither response alone appears to be different than zero, nor are these specific tests reported. It is hard to draw any conclusion from non-zero responses.

We now report differences from 0: the adaptation response was significantly different from 0 in the pre-defined time window for post-up trials. The response was numerically but not significantly larger than 0 in this time window for post-down trials; however, a cluster-based permutation analysis of all time points across the syllable yielded significant differences from 0 in both post-up and post-down conditions (see new horizontal bars on Fig. 2A). This is described in the results in lines 120-122 and in the methods in lines 263-266 and 295-297.

The claim that on-line compensation responses and the frequency shifts associated with the subsequent utterance are based on separate mechanisms rests on the absence of a relationship between these variables. However, it is difficult to know what to conclude when a relationship is absent. One might suspect that part of the reason for the null relationship is that all perturbations in the present study were all more or less equal in magnitude. Accordingly, variations in both the compensatory response and the response on the subsequent trial may effectively be noise. A more convincing demonstration might involve the use of perturbations of different magnitudes. One would be more inclined to find the absence of a relationship between the variables of interest more informative if there was no relationship under these conditions.

We now present further evidence for a trial-level relationship between compensation and adaptation using a test on the distribution of correlation coefficients across individuals, replacing our Monte Carlo simulation (see response to Reviewer 1 above). We have amended our explanation and discussion in lines 133-139 & 166-177. We recast these conflicting results (no main effect of compensation on adaptation, but a significant tendency for correlation within individuals) as mixed results that do not rule out a direct feedforward relationship; however, there is a stronger burden on models that have a reliance on this trial-level relationship to show that it is reliably predictive of adaptive behavior. We agree that datasets with parametrically varying perturbation size (within the same participants) would allow for a more controlled elicitation of variability in compensation responses and may shed more light on the individual relationship.

Author Response

Reviewer #1 (Public Review):

This manuscript is filling an important gap in the literature which is the association between the excitation/inhibition unbalance found in animal models and findings in human neurophysiology. Thus, the idea of using computational models as a linkage between those two levels of analysis help to reconcile many of the previous results. In addition, it provides a reinforcement of the strong relationship between neurophysiological findings with MEG and protein imaging by PET. Therefore, I have found this work of great interest for the literature on the neurophysiology of dementia. I have some comments that are mainly trying to have a better understanding of the findings and aim to get potential associations with previous stages of the disease.

1) If the patients involved in the study are already with a diagnosis of dementia (MMSE <24; CDR 0.72), why they are still presenting hyperexcitability? Typically, amyloid hyperexcitability starts years before in earlier stages of the disease. The continuous hyper calcium neuronal intake should induce toxic effects leading to neuronal death and accelerating degeneration. Furthermore, in the AD stage, Tau is typically dominating inducing neuronal silence. If this process is true, why at the stage of dementia patients still show hyperexcitable activity instead of showing a more global reduced neuronal activity?

Indeed, Aβ accumulation starts decades before the clinical symptoms and contributes to hyperexcitability in the early stages of the disease. Furthermore, it is well accepted tau induces neuronal silencing. However, the opposing effects of Aβ contributing to hyperexcitability and tau contributing to neuronal silencing are more complicated and don’t seem to simply cancel out each other in AD progression. There are several reasons. First, the spatial patterns of Aβ and Tau distributions are distinct and lead to complex effects on neuronal hyperexcitability (see response to point 2 below). Second, tau appears to have an important enabling role for network hyperexcitability in AD mice.8-10 While the amount of wild-type tau corelates with the degree of network hyperexcitability, genetic reductions in tau expression block epileptiform manifestations and stabilize networks.11-13 Specifically, tau ablation modulates the baseline excitatory neuronal activity and excitability of inhibitory neuronal activity, counteracting the network hyperexcitability.11 Collectively, hyperexcitability is expected to be observed throughout the course of AD progression and not just during the early stages of the disease. (Discussion: page 18, lines 18-27; page 19, lines 1-4; Figure 5 and Discussion section 4.2)

2) About the role of Aβ in the modulation of alpha and beta. As indicated in the manuscript alpha and beta bands tend to be enhanced in power due to the presence of Aβ. However, the final effect is a reduction of power in comparison with the control group leading to the idea that the Tau effect is stronger in these particular frequency bands. Because tau and Aβ distribution across the cortex is differential I wonder whether in regions with fewer tau deposits alpha and beta power increased. This could be a good validation/test for the model proposed in this study.

We completely agree with the reviewer that the associations between frequency specific oscillatory signatures and the protein accumulations are region-specific. Furthermore, as correctly predicted by the reviewer the alpha and beta oscillatory changes in the frontal cortices, where there is a relatively higher amyloid accumulation than tau, show an increased pattern. We have included an additional supplementary figure illustrating these changes and also briefly discuss these additional findings in the revised manuscript. (Appendix figure.1)

3) In some previous studies, increased excitatory activity, due to loss of inhibition, leads to effects in the gamma band. This was shown in both animal models (Palop and Mucke, 2016) and in humans (Rammp et al, 2020; Cuesta et al, 2022). Is there any reason for not finding effects in this frequency band?

We completely agree with the reviewer that gamma band activity is crucially important in studying abnormal excitatory-to-inhibitory activity in AD. However, accurate reconstruction of regional power spectrum from resting-state MEG data in the gamma band, which has extremely low signal-to-noise ratio is more challenging. Application of neural mass model to compare against empirical spectra based on such low values may lead to spurious associations and potentially inaccurate conclusions. Therefore, in this study, where our main goal was to examine the abnormal excitatory-to-inhibitory activity in AD patients using the neural mass model and empirical power spectrum, we excluded gamma band from our analysis. Notwithstanding the low signal-to-noise ratio, methodologies that incorporate cross frequency phase-amplitude coupling and transfer entropy measures may be better suited to examine the changes in gamma rhythms. This indeed is our current work-in-progress and we expect to present these findings in future manuscripts.

4) The readers, and I, could need an explanation of the association between slow waves and hyperexcitability. In data from human patients with brain damage and atrophy, a typical finding is delta to theta activity. Therefore, white and grey matter damage explains better the appearance of these rhythms. Again, in epilepsy, a seizure could lead to high-frequency oscillations and it is after a seizure when slow waves show up (when inhibition bit excitation). I perfectly understand that in the data presented in this work amyloid modulates this rhythm, but explanations such as amyloid induce neurodegeneration and consequently, slow waves, could not be ruled out. The explanations already indicated in the discussion section are perfectly fine and could inspire future work, but more traditional ones could be indicated as well. Honestly, I was expecting having Tau more associated with slow waves, as tau has been linked to brain atrophy. Is true that Tau is affecting the reduction of more rapid frequencies such as alpha and beta, but its association with neurodegeneration should not lead to the increase of slow waves?

We thank the reviewer for raising this important point. Considering the complexity of cellular, molecular, and ionic components involved in generating oscillatory rhythms, it is likely that more than one underlying mechanism may contribute to abnormal oscillations. The extensive literature on brain damage ranging from acute perinatal hypoxic injuries to chronic traumatic brain damage report various electrophysiological phenotypes including increased delta power, reduced alpha power, abnormal non rapid eye movement sleep rhythms as well as epileptiform manifestations.14,15 However, the causal relationships between electrophysiological phenotypes and neuronal loss remain unknown.

Diverse investigations in AD have demonstrated that neuronal loss is not an immediate functional consequence of Aβ accumulation.16,17 In contrast, as the reviewer correctly pointed out, neuronal loss is tightly coupled to tau accumulation in vulnerable networks.18 Neither do we have compelling evidence to support the hypothesis that Aβ directly causes loss of neurons first which in turn is followed by network hyperexcitability, nor to support that neuronal loss in AD causes directly contributes to increased slow wave activity. On the contrary, there is much evidence from electrophysiological and fMRI studies to support the hypothesis that functional changes occur much earlier in the time course of Aβ accumulation.19,20 Our current findings are consistent with such prior observations. Moreover, many patients in the current study had only mild cognitive deficits with minimal atrophy. Together, these findings suggest that spectral power increases associated with Aβ, as well as decreases associated with tau, represent early functional abnormalities, independent of atrophy.

We completely agree with the important observation pointed out by the reviewer that focal and generalized slowing of brain rhythms are characteristic patterns of electrophysiological abnormalities in epilepsy, especially during the interictal period. In fact, recent studies from our group as well as from others studying epileptiform activity in patients with AD identified focal and generalized slow waves as a strong indicator of subclinical epileptic activity in patients with AD21,22. The current findings of slowed oscillatory spectra in AD patients who harbor network hyperexcitability is therefore in complete agreement with the fundamental knowledge base in epilepsy literature. The exact mechanisms how increased delta-theta and reduced alpha may contribute to network hyperexcitability remains to be elucidated. Our working framework for potential interactions of molecular and network mechanisms leading to altered excitatory and inhibitory network activity in AD are now included in our revised discussion. (Page 20, Discussion section 4.2; Figure 5)

5) Previous work has found a strong association between amyloid and alpha rhythm in the frontal regions. Here authors found this association with delta to theta in the same brain regions. However, delta is associated with local hyperexcitability and, in Nakamura et al (2018,) they associate alpha with the same phenomena. How this could be justified?

In fact, the findings in this study is completely consistent with what was reported in Nakamura et. al. 20185 : (1) A main finding in the current study is that compared to controls, individuals in AD neuropathological spectrum (Aβ+ MCI/mild-AD) have increased delta-theta power correlated with higher Aβ. Nakamura et. al. 2018 results show consistent findings in their Aβ+MCI patients compared to controls (Aβ+ and Aβ-). For example, as depicted in Figure-1A of Nakamura et. al. 2018, in all 10 brain regions examined, delta-theta range power is higher and alpha power is lower in Aβ+ MCI compared to controls (either Aβ+ or Aβ-). (2) In our analysis we found a positive correlation between Aβ and alpha and beta band spectral power, although the absolute power value is reduced in patients compared to controls. This is also a consistent finding in Nakamura et. al. 2018 paper, as illustrated in their Figure 1A where Aβ+ MCI patients consistently showed reduced values of alpha power compared to controls either Aβ+ or Aβ- and a positive main effect of Aβ on alpha power. (3) Our spectral analysis highlights the signature spectral change as high delta-theta and low alpha and beta in AD patients, while the neural mass model application considering the full spectrum demonstrates the abnormal excitatory-to-inhibitory activity in patients with AD. Nakamura et. al.2018, on the other hand, reports the same signature spectral change in their Aβ+MCI patients, and speculate about the potential mechanism of abnormal excitatory-to-inhibitory activity albeit without the application of neural mass model.

Having pointed out the strong, consistent message about the signature changes between these two studies we would also like to draw attention to some particular details. First, 40% of the patients considered as MCI in Nakamura et. al 2018 are Aβ-, and as such are not in the AD neuropathological spectrum. It is likely that these patients either belong to frontotemporal lobar degeneration type dementia or other rear non-AD neurodegenerative conditions. This is a strong confound which influenced the conclusion of regional associations of Aβ and spectral changes and any other conclusions derived from that study (e.g., Figure 1B, in Nakamura 2018 et. al). Second, Nakamura et. al. 2018 did not use tau imaging in their study and were not in a position to make associations between reduced spectral power and tau accumulation or speculate about its effects on abnormal excitatory-to-inhibitory activity. We discuss the Nakamura 2018 et. al. findings explicitly in our revised discussion. (Discussion: page 21, 17-26)

6) I fully agree that findings in oscillatory activity, and its associations with pathological proteins, are stage-specific rather than disease-specific. However, why alpha and delta increases can be associated with the same neuronal mechanism (hyperexcitability) at different stages of the disease?

The reviewer is absolutely correct here. The key to the answer here lies in the fact that AD is progressive in nature and the relative effects of Aβ and tau are indeed different at different stages of disease. Therefore, despite the mechanistic effects of these proteins having an invariant pathological effect their manifestations may vary along the temporal timeline of AD (early Aβ, followed by tau). What our results suggest (and consistent with basic science data) is that Aβ strongly affects inhibitory neurons while tau affects excitatory neurons. An important observation here therefore is that not only Aβ associated inhibitory neuronal changes but also tau associated excitatory changes are contributors to hyperexcitability. (Discussion: section 4.2 & 4.3)

Reviewer #2 (Public Review):

Ranasinghe and co-authors explored the relationship between amyloid-beta and tau deposition and neural oscillatory behaviour in Alzheimer's disease (AD) by using a computational neural mass model that can generate neurophysiological power spectra comparable to EEG- or MEG-like, macroscopic brain activity assessments. The model parameters that represent neuronal excitation and inhibition were tuned to optimally resemble the empirical MEG data from AD patients in different relevant frequency bands, and subsequently, the different parameter changes in all 68 cortical neural masses, representing local neuronal excitation or inhibition, were compared with the local amyloid and tau deposition rates. This comparison was used to demonstrate the different, frequency-specific effects of these two proteins, to form an integrated, multimodal/-scale explanation of the molecular/neurophysiological AD disease mechanism.

The role of neurophysiology in AD pathophysiology is underestimated in the AD research community, as for many it appears to be a more 'downstream' aspect than protein deposition, inflammation or genetic predisposition. However, given the tight relation between cognition and brain activity, the clear involvement of neurophysiology at micro and macro levels, and reports that neuronal activity can influence structural pathology in AD, its central role is evident. It is very laudable that this author group aims to focus on the combination of neurophysiology and computational modelling to further explore how AD pathology actually leads to cognitive impairment. As multi-scale, simultaneous, longitudinal recordings in humans are too burdensome, computational modeling represents a very flexible and powerful new instrument to bridge different levels of detail and predict developments over time. However, the pitfall of using models is the endless options for designing the model, as they will ultimately affect the results and interpretation. However, by constraining the model with biologically plausible effects and parameters, and by validating it with empirical data, it can not only serve to unravel mechanistic principles of disease but also predict successful interventions. Currently, it is not known what model simplifications can be accepted, and which elements need more detail, and this probably also depends on the specific research question and hypotheses. The novel, well-described approach makes the present study a valuable addition to a research field that is under development.

The conclusions of this paper are mostly well supported by data, but some methodological aspects, as described below, limit the power of the study, or rather provide a valuable perspective on the proposed neurophysiological mechanisms, but not the only valid one.

Strengths:

• The group is a high-profile team, known for many influential publications.

• The use of state-of-the-art techniques like tau-PET and source-space MEG combined with computational modeling may currently be the most powerful approach available for this purpose.

• AD patient diagnosis is pathology-supported and conforms to NIAAA.

• The modeling and empirical data are processed and analyzed rigorously; statistical analysis is sound.

• The methods and result sections are well-written and presented in a logical order.

We thank the reviewer for highlighting many strengths in our work.

Weaknesses:

1) The chosen AD patient cohort is relevant and well-defined, but broad: it includes both persons at the predementia and dementia levels of AD. Since brain changes during the AD disease course are gradual and variable, this heterogeneous group may have limited the observed changes and interpretation. Changes in brain activity are frequently reported to be non-linear, involving transient increases in activity in the early, predementia phase. Also, the effect of amyloid-beta may depend on deposition load (see for example Gaubert ea, Brain 2019). The group heterogeneity in the present study may have obscured distinct activity patterns in different phases of the disease.

We agree with the reviewer that group heterogeneity in the present study and the dynamicity of AD disease could contribute to variability in our observations. Indeed, an ideal study design to capture such dynamic phenomena is a true longitudinal study where we follow each subject from high-risk AD stage through pre-clinical and then clinical stages of the disease, which requires extensive resources for patient follow-up on all aspects including clinical and imaging facilities. Although not complete substitutes to such longitudinal design, cross-sectional models, such as ours, do provide valuable information to understand the mechanistic relationships along the biological progression of AD. While our cohort includes patients with mild cognitive impairment (MCI) whose Clinical Dementia Rating (CDR)=0.5 and those with mild dementia (CDR=1) and moderate (CDR=2), our cohort predominantly represents MCI (15 out of 20 patients are CDR=0.5; 75%). Among the 5 patients who were identified as CDR1 and 2, only two had low values in mini mental score exam (MMSE) ranging below 19 points. Recent studies using in-vivo tau-PET imaging have clearly demonstrated that patients with AD and at CDR 0.5 have almost saturated amyloid accumulation and tau accumulation up to mid-Braak stages. As such, our cohort although heterogenous, is clearly representative of early-stage AD or pre-clinical AD. Together, our findings suggest that oscillatory changes in the earliest stages in the biological progression of AD is robust and provide clear indices of underlying pathological manifestations. Nevertheless, we acknowledge that these results need to be replicated in larger cohorts within homogenous CDR categories and in longitudinal studies. We address this in our revised ‘limitations’ section. (Page 23, lines 15-17)

2) As the authors state, PET is sensitive to aggregates of proteins. However, soluble oligomers in early phases are toxic as well but cannot be assessed with the current approach. This may have led to a misinterpretation of local toxic effects which is hard to quantify, limiting the power of the current approach. As the authors state, the neural gain parameter might be more sensitive to early, soluble protein toxicity, but how can this be supported?

We agree with the reviewer that soluble oligomers that may be important biomarkers of AD. However, they cannot be measured clearly with the current assays. Although the PET signal is incomplete as it is only capturing the deposited proteins, it has also been shown in basic science models that soluble amyloid oligomers are concentrated around plaques.23 Therefore, it is reasonable to conclude that while the full strength of the association may not be evaluated in our analyses, that regional effects are well captured. It is possible that neural gain parameters which were abnormal in patients with AD, are influenced more by soluble oligomers than by deposited proteins where the latter did not show significant associations with the gain parameters. However, testing this hypothesis is beyond the scope of the current study. We acknowledge this issue in the revised ‘limitations’ section and aim to address these important molecular associations raised by the reviewer in our future investigations using cerebral organoids with AD pathology. (Page 23, lines 7-10)

3) Pathological deposition in subcortical regions and its effect on large-scale oscillatory behaviour is not considered in this study, while early subcortical (e.g. entorhinal) changes are a key feature of the disease. As the authors used source space MEG, involving subcortical structures is technically feasible (e.g. AAL atlas), and may have given a more accurate view.

We thank the reviewer for this important point and allowing us to clarify. Our regions indeed included entorhinal cortex. The terminology used as ‘cortical’ included both neocortex and the allocortex, the latter which include the entorhinal cortex. The subcortical regions we have excluded in this study only included the basal ganglia. We have now clarified these details in our methods section. (Page 6, lines 6-8)

4) The authors use a recently developed spectral graph neural mass model, which has several theoretical advantages over more complex, biophysically realistic models. However, there are also disadvantages. Since the model does not generate oscillatory output that can be assessed visually, it is unclear whether the parameter changes required to match the empirical MEG spectra are still within a range that would produce realistic oscillatory behaviour, that also visually resembles AD patient data. Also, since model parameters are less directly linked to neuronal properties as in for example a Jansen-Rit model, the meaning of parameter changes is more difficult to grasp. For example, it seems logical that increased time constants in the model lead to spectral slowing, but how would time-constant abnormalities translate to (inter)neuron dysfunction? Also, since no simulations are required, the contribution of coupled neural masses that influence each other's behaviour during a neurodegenerative process is not captured.

We thank the reviewer for raising important questions about our spectral graph model. In the current study, we focus on capturing the steady state frequency response of local neural oscillators. The model is certainly capable of producing oscillatory output (characterized by strong peaks in the spectra). Although our model was constructed in the frequency domain, its oscillatory output can be examined in the time-domain using inverse Laplace transforms. We have demonstrated this in one of our most recent studies.24 In that study, we found that the transient impulse response of this model is either a decaying oscillation, limit cycle, or an unstable oscillation. We respectfully disagree that our model parameters are any less interpretable than comparable non-linear models like the Jansen-Rit models. They are both neural field models with differences only in implementation details and inference procedures. For instance, while our model does not require simulations because it allows for a closed-form solution, it does indeed capture coupled neural subpopulation interactions.25

5) In the discussion section, the associations between a-beta and tau and neuronal hyper/hypoactivity are adequately compared to recent basic science literature, but since the authors state that the observed effects indicate an overall, net balance between underlying excitatory and inhibitory dysfunction, it is not clear how the model could help to further determine the exact link between -for example- a-beta-induced glutamate toxicity and neuronal behaviour. This less specific link makes it easier but also more ambiguous to explain the directions of the observed effects.

We completely agree with the reviewer that increased amyloid in basic science models have been shown to correlate with abnormal inhibitory neuronal activity as well as with excitatory neuronal activity. Consistent with these observations, we found that increased amyloid accumulation of associated with increased inhibitory time-constants. However, we did not find any association between higher amyloid and excitatory neuronal parameter deficits. NMM estimations are derived for the level of local neuronal subpopulations. It is important to reiterate that the current findings indicate an overall inhibitory functional deficit at the level of local networks which in turn may be contributed by abnormal inhibitory as well as excitatory deficits at cellular level. We have included these points to our discussion and also refer the reviewer to figure 5 in the revised manuscript which summarizes our findings and posits a framework to examine these interactions. (Page 18, lines 13-17; Figure 5 and section 4.2 in Discussion)

Author Response

Reviewer #1 (Public Review):

Mitra et al. extensively utilized the publicly available pan-cancer multi-omics datasets including CCLE, TCGA, RNAseq, and ChIPseq datasets from GEO, and conducted impressive computational analysis work to discover the potential regulatory functions of lncRNA at the pan-cancer level. The idea of using co-essential modules generated by Wainberg et al. 2021 is very interesting and was important to leverage the genome-wide set of functional modules to identify the new lncRNA functions. The overall statistical analyses are rigorous, and the evidence in this paper is logical and solid, especially given the additional RNAseq/ChIPseq data analysis. The validation experiments using cell lines were also appropriate. Overall, this is an excellent paper that combines both dry and wet lab experiments to systematically discover unknown functions of lncRNAs in cancer.

We thank the reviewer for recognizing our study as statistically rigorous, logical, and impressive and that has used multiple approaches and validation to systematically identify critical proliferation/growth regulatory functions of previously uncharacterized lncRNAs in cancer.

Reviewer #2 (Public Review):

Mitra and colleagues performed statistical analyses to evaluate associations between lncRNAs and mRNAs, using transcriptome data generated in tumor tissue samples in multiple cancer types from both CCLE and TCGA projects. They further integrated the association results into previously wellcharacterized co-essential pathways/modules (Wainberg et al., 2021), together with additional pathway/Hallmark genesets annotations, aiming to explore function potential for lncRNAs. Based on these analyses, they characterized 30 high-confidence pan-cancer proliferation/growth-regulating lncRNAs. Importantly, they provided in vitro functional evidence to verify potential tumor-suppressive roles of two prioritized lncRNAs (PSLR-1 and PSLR-2) in proliferation and growth in two lung adenocarcinoma cell models. Overall, this is a well-motivated and conducted study, especially given the large number of lncRNAs that currently have poor-characterized functions. The findings in this manuscript could advance the overall understanding of the roles of lncRNAs in cancer formation and progression.

We thank the Reviewer for recognizing the quality of our study and its importance in increasing the understanding of lncRNAs in cancer development and progression.

Author Response

Reviewer #2 (Public Review):

Weaknesses:

Although this is certainly a technically difficult goal, the paper does not show a direct interaction between WhyD (or its GlpQ sub-domain) with WTAs. While the effect of WhyD over WTA levels showed here is undeniable, and the proposed interaction is the simplest explanation, it's not possible to assert whether this is the case without a crosslink co-purification using an inactive mutant of WhyD.

We show in Figure 3 that the purified GlpQ domain of WhyD hydrolyzes WTAs from purified cell wall sacculi. It’s hard to imagine how the enzyme could accomplish this without making direct contact with WTAs. We therefore think this result along with the finding that the ∆whyD mutant has high levels of WTAs provides strong support for our conclusion that WhyD acts on WTAs.

Another aspect the paper could improve is the explanation of the labeled cell-wall analogs, very well established in the cell-wall field but likely obscure to other biologists. Especially on figures that nothing at all is said about the data (Figures 4 and 5). The microscopy data, despite evidently being well-performed, begs for better quantitation and visualization. For example, it's not clear whether there were replicates, the sample size (informing that at least 300 cells were used is not enough information to inform on sample size effects). Sub-panels where no signal is apparently detected (e.g. Figure 7 and supplements) should be clarified and the background should be displayed.

We thank the reviewer for requesting more information for the general reader. We have included more information about the probes in the Materials and Methods section.

Author Response

Reviewer #1 (Public Review):

1) In terms of the prior hypothesis here I think the authors justify a prior with respect to striatum and I think the most principled analysis of their hypothesis would be based on volumes of interest in striatum. Figure 1 does show difference in MTsat in striatum between neurotypicals and DLDs but the changes are all in the caudate I think- I cannot see anything in putamen. The authors actually describe changes in only one part of anterior caudate. The authors do describe a number of previous conflicting studies that examine caudate structural changes but that is not their hypothesis. The discussion goes into developmental changes affecting striatum at different times that might be relevant and would require a longitudinal study for a definitive study - as the authors acknowledge.

The reviewer is correct that at this statistical threshold we only observe MTsat differences in the caudate nucleus. Changes in the putamen did not survive this threshold. Lowering the threshold for MTsat (our maps are openly available on Neurovault), or an ROI analysis (see (https://osf.io/2ba57/)) does not reveal significant statistical differences in the putamen. As we noted in the paper, there are differences in the putamen in R1 (these are also observed in the ROI analysis).

2) There is a lot of overlap between the caudate signal in the two groups - although the correlation of individual differences is reasonable. The caudate signal would not allow group classification.

Yes, it is clear that these differences would not be sufficient to allow for group classification of DLD. We have discussed this overlap in the discussion.

3) Outside of the caudate they do show changes in left IFG and auditory cortex that are hypothesised. But there is a lot else going on - I was struck by occipital changes in figure 1 which are only mentioned once in the manuscript.

We now discuss these differences in the discussion. Note that we did not have any a priori hypotheses about these regions; to our knowledge, they have not been previously described and are not predicted by any theoretical accounts of DLD.

4) Should I be concerned by i) apparent signal changes in right anterior lateral ventricle from group comparison in figure 1 ii) signal change correlation in right anterior lateral ventricle in figure 4 (slice 22) and iii) signal change outside the pial surface of the occipital lobe in figure 1?

No – these may be accounted for by smoothing during analyses. Note, these changes at tissue boundaries are fairly commonly seen in statistical maps following smoothing but are not evident when data are projected onto a 3D surface.

Reviewer #2 (Public Review):

This work demonstrates the value that multiparameter mapping imaging protocols can have in uncovering microstructural neural differences in populations with atypical development. Previous studies looking at differences in brain structure have typically used voxel based morphometry (VBM) approaches where differences in volumes can be hard to interpret due to complex tissue compositions. The imaging protocol outlined in this paper can specifically index different tissue properties e.g. myelin, giving a much more sensitive and interpretable measure of structural brain differences. This paper applies this methodology to a population of adolescents with developmental language disorder (DLD). Previous evidence of structural brain differences in DLD is very inconsistent and, indeed, using traditional VBM the authors do not find a difference between children with DLD and those with typical language development. However, they provide convincing evidence that despite no macrostructural differences, children with DLD show clear differences in levels of myelin in the dorsal striatum and in brain regions in the wider speech and language network. This can help to reconcile previous inconsistent findings and provide a useful springboard for both theoretical and empirical work uncovering the nature of the brain bases of language disorders.

We are grateful for these comments, and to the reviewer for pointing out some key strengths of this work.

Strengths:

The imaging protocol is robust and is explained very clearly by the authors. It has been used before in other populations so is an established method but has not been applied to populations of children with DLD before, yielding novel and very interesting results. The authors demonstrate that this is a methodology which could have great value in other populations that display atypical development, increasing the impact of these findings.

The sample size is large for research in this area which increases confidence in the results and the conclusions.

Rather than relying solely on group differences in brain microstructure to draw conclusions about neural bases of language development, the authors correlated brain microstructural measures with performance on standardised language tests, allowing stronger inferences to be drawn about the relationships between structure and function. This is often an important omission from developmental neuroimaging work. It gave increased confidence in the finding that alterations in striatal myelin are linked to language difficulties.

Weaknesses:

The authors rightly use the CATALISE definition of developmental language disorder, which differs from much of the previous literature by not requiring that children with language difficulties have nonverbal ability that is in the normal range. As can be common when using this definition of DLD, the group with DLD have significantly weaker nonverbal ability than the typically developing group. The authors show that brain microstructural differences correlate with language ability but they don't rule out a correlation with nonverbal or wider cognitive skills. Given the widespread differences in myelination across areas of the brain, including those that weren't predicted e.g. medial temporal lobe, it is plausible that perhaps some of the brain microstructural differences are not linked directly to language impairment but a broader constellation of difficulties. Some of the arguments in the paper would be strengthened if this interpretation could be ruled out.

To rule out the effect of nonverbal IQ or wider cognitive differences, we have conducted stepwise regression analyses on the quantitative data extracted from the statistical cluster covering the caudate nuclei, assessing the influence of factors such as language proficiency, verbal memory and IQ. We find that language status accounts for the most variance, rather than nonverbal IQ or verbal memory (details are included in the paper).

We also discuss this point in the discussion, pointing to the presence of co-occurring differences in DLD and how these might account for some of the broader group differences we observe.

The authors acknowledge in the limitations section that their data cannot speak to whether brain differences are a cause or consequence of language impairment. However, there are some implied assumptions throughout the discussion of the results that brain differences in myelination have functional consequences for language learning. A correlation between structure and function does not indicate this level of causality, particularly in an adolescent population - function could just as easily have had structural consequences or environmental differences could have influenced both structure and function. In my view, the speculations about functional consequences of myelin differences are not fully supported by the data collected.

The reviewer is correct in saying that the myelin deficit could be either a cause or a consequence of DLD or even that both are caused by a third factor. We specifically address this in the discussion section, and note a longitudinal analysis would be the best way to address this question. Indeed, R3 notes about our paper, “…it does a very good job of avoiding the common trope of assuming neural differences play a causal role in DLD (when in fact, reduced atypical development could cause neural differences)”.

The data suggest that there is much greater variability in left caudate nucleus MTsat values for the DLD group than the other two groups. The impact this may have on the results is not discussed in the interpretation and it is unclear whether this greater variability occurs throughout all of the key MPM measures for the DLD group.

Thank you for raising this important issue. In figure 1, we only plot the MTsat values from the caudate nucleus for visualisation, and as you note, there we is a considerable degree of variability within the DLD group. However, and crucially, this difference would not influence statistical interpretation of our results. The whole-brain analysis used involves permutation testing, and is robust to a difference in group variability. However, the issue of variability within DLD is important and we now highlight this in our discussion, noting that not every child with DLD will have reduced striatal myelin. Indeed, this variability is even more evident in figure 4. An important challenge for future studies is to understand the link between striatal myelination and the spectrum of language variability.

Reviewer #3 (Public Review):

Developmental Language Disorder (DLD) is observed in children who struggle to learn and use oral language despite no obvious cause. It is extremely wide-spread affecting 7-10% of children, and extremely consequential as it persists throughout life and has downstream effects on reading, academic outcomes, and career success. A large number of prior studies have attempted to identify the structural neural differences that are associated with DLD. These have generally shown mixed results, but support a number of candidate regions including left hemisphere language areas (particularly the inferior frontal gyrus), and striatal regions that are possibly linked to learning. However, these studies have suffered from small sample sizes and conflicting results. Part of this may be their reliance on traditional voxel-based-morphometric techniques which estimate cortical thickness and gray matter density. The authors argue that these measures are biologically imprecise; gray matter can be thinner for example, due to synaptic pruning or increased mylenation.

The authors of this study offer a powerful new tool for understanding these differences. Multi-Parameter Mapping (MPM) is based on standard MRI techniques but offers several measures with much greater biological precision that can be tied specifically to myelination, a key marker of efficient neural transmission. The test a very large number of children (>150) with and without DLD using MPM and show strong evidence for fundamental biological differences in these children.

This study features a number of key strengths. First, at the level of neuro-imaging, the MPM technique is new in this population and offers fundamental insight that cannot be obtained by other measures. Indeed, the authors wisely use a traditional gray matter approach (voxel based morphometry) and find few if any differences between children with DLD and typical development. This offers a powerful proof of the sensitivity of this approach. Moreover, the authors analyze their data comprehensively, looking at two measures of myelin (MTsat and R1) and their convergence.

However, at the most important level, I think structural approaches (like MPM, diffusion weighted imaging and so forth) offer tremendous promise for dealing with this as they avoid the ambiguity associated with interpreting functional MRI. Are children showing reduced BOLD because they are less good at language processing? Or do the differences in brain function cause poorer language processing? Structural approaches - and MPM in particular - offer tremendous promise as they unambiguously assess the fundamental neuro-biology.

Beyond the neuro-imaging this study is also strong in their sample and the measurements of language. The sample size is very large and an order of magnitude larger than existing studies. It is well characterized, and the authors use a large set of well-motivated measures that capture the relevant dimensionality of language. Moreover, the authors treat language both as a clinical category and a continuous measure which is consistent with current thinking on the nature of DLD as potentially the low end of a continuous scale rather than a discrete disorder.

Finally, the discussion of this paper for the most part does a good job of fitting these neurobiological findings into our broader understanding of DLD. It does an excellent job of mapping the observed brain differences onto functional differences in the child. Importantly, in doing this it does a very good job of avoiding the common trope of assuming neural differences play a causal role in DLD (when in fact, reduced atypical development could cause neural differences).

We are very grateful for the reviewer for taking the time to read our work so closely and pointing out these strengths in the work.

Despite these strengths, I have a number of substantive concerns that if addressed will improve the overall impact of this paper.

First, as the authors are aware, there is a long running and active debate in DLD as to whether DLD is the tail end of continuous distribution of children or a unique disorder (Leonard, 1987, 1991; Tomblin, 2011; Tomblin & Zhang, 1999). The results here offer great promise for informing that debate. And in that vein the authors quite appropriately analyze their data in two ways: once using DLD as a categorical variable and once using continuous measures of language. However, they don't really attempt to wrestle with the differences between the model.

We have now included a section on the implications of our results for DLD in the discussion.

Second, I was a little surprised to see the authors highlight left IFG in the discussion to the degree they did. While there was clear evidence for reduced myelin there in the MTsat analysis, this did not hold up in R1 analysis, and even in the MTsat, IFG was clearly not the primary locus. Rather the areas of differences seemed to be centered at Pre- and Post-Central gyrus and extending ventrally (to IFG) and posteriorly from there. Given debate on the role of IFG in language specific processing in general (Diachek, Blank, Siegelman, Affourtit, & Fedorenko, 2020; Fedorenko, Duncan, & Kanwisher, 2013), it was not immediately clear to me why that area was important to highlight. For example, some of the posterior temporal areas (and motor areas) that were found were equally important for perceptual, lexical and phonological processing that are important for other theories of DLD.

We do see group differences in left IFG in the R1 analysis (see Figure 2) and they were more extensive than those seen in the MTsat analysis with which they overlapped. The reviewer is correct that the differences were limited to the opercular part of the IFG in both analyses whereas they extended more dorsally in the R1 analysis. They also extended ventrally to the anterior insular cortex. We respectfully disagree with the reviewer about the importance of highlighting these differences, given the importance of this region for language processing, and our previous hypotheses about this region. Even so, we agree that the posterior temporal and motor areas are of equal importance and have highlighted these in the discussion.

The authors rightly point to their differences in the striatum as supporting theories of DLD centered around differences learning. However, as they discuss, there are also large differences throughout the brain in both perceptual, motor and language areas. These would seem to support theories of DLD centered around processing and representation. In particular, the differences in myelination likely are linked to differences in the efficiency of neural coding. This would seem to favor two theoretical views that might be worth mentioning - speed of processing (Miller, Kail, Leonard, & Tomblin, 2001), and approaches based on lexical processing (McMurray, Klein-Packard, & Tomblin, 2019; McMurray, Samelson, Lee, & Tomblin, 2010; Nation, 2014). I was surprised these were not mentioned, given the clear link to the timecourse of processing. Does then suggest that these theories might complement each other? It would be useful to see some more discussion of the implications of these findings for broader theories.

We have now incorporated mention of these theories in the discussion and discuss implications. We agree with the reviewer that it would be interesting to see whether the different theories could be reconciled.

Author Response

Reviewer #1 (Public Review):

In this manuscript the authors investigate the spatiotemporal dynamics of oscillations in the human insula. The authors measure human intracranial EEG data in ten patients who had stereo EEG electrodes placed in the insula. They identify two dominant low frequency oscillations: a theta and a beta rhythm. The frequency and power gradients of these oscillations along the anterior-posterior and superior-inferior axes of the insula are then delineated. They find a beta power gradient that decreases anterior to posterior in both left and right insula. They also find that theta frequency increases and power decreases from anterior to posterior in the left insula. They show examples of traveling waves in some participants and using a cross-correlation analysis, they find that time-shifts between the amplitude and traveling wave strength indicate a functional role for these oscillations in the insula. The manuscript concludes that traveling waves have an important role in intra and inter insular communication.

These data contribute in an interesting way to the ongoing understanding of oscillations in human brain regions by taking a detailed approach of identifying oscillations in one specific region, the insula. Such careful delineation contributes to our overall understanding of neural oscillations in different brain regions.

The delineation of traveling waves in the human brain is a particularly challenging problem, where many lower-level analysis issues can affect the outcome statistics. The authors did a careful assessment of many of these analysis concerns, but several questions remain that may have a major impact on the outcomes and conclusions.

We thank the reviewer for the encouraging comments. Below, please find point-by-point responses to the concerns.

1) The authors should use additional metrics to ensure that results are not driven by individual subjects. For example, the theta frequency gradient shown in the left insula in figure 2A seems to be strongly driven by two sEEG probes with a lower frequency in the anterior insula. These seem to potentially correspond to subject 3 shown in figure 4C.

We have revised the paper to more clearly explain that our main statistical analyses were all performed using a mixed-effects model that specifically ensured our findings were not driven by individual subjects. All group-level statistical tests for the spatial frequency and power gradients accounted for the identity of the subject that contributed each electrode, represented as a categorical variable in the linear mixed effects model, thus ensuring that subject-level results were not separately modeled. As a result of this procedure, therefore, all reported t-statistics reflect the overall strength (effect size) and spatial direction of spectral gradients across subjects, because the method separately accounted for the differences between them. Similarly, we also found that the number of electrodes contributed by each subject was also similar, with relatively low variance across subjects (mean = 23.9 contacts, standard error = +/- 2.43 contacts). Nevertheless, we do understand the concern and have now added a supplementary figure (Figure S11) in the revised version of our manuscript showing that single-subject gradients directionally align with the group level results. The text in manuscript has now been modified to reflect these changes (pages 6-7).

2) To establish the fundamental spatiotemporal dynamics of oscillations in the human insula, the authors should include the full range of lower frequencies for their analysis. It is unclear why the 9-15 Hz range is excluded. Moreover, the peak frequency estimates in figure 1C seem to be found most often in the middle of the theta 6-9Hz and the beta 15-30Hz range. The possibility that including a certain frequency range introduces bias in the algorithm towards finding a peak in the middle of the range should be excluded.

We fairly tested for oscillations and traveling waves at all frequencies and found no 9-15 Hz signals in the insula. The revised paper more clearly describes this interesting absence (see page 9).

3) An assessment for the confidence of the power and frequency gradients should be presented. The authors carefully fit a 1/f function to the power spectrum to delineate the peak frequencies in the theta and beta range, but confidence intervals for the frequency and power estimates within each electrode should additionally be calculated to ensure that temporal outliers within an electrode do not drive the results. Moreover, while the peaks in figure 1 seem quite broad in the frequency range, varying in steps of about 0.25Hz, the frequencies of the oscillation clusters seem quite detailed, reported with 0.001Hz accuracy. These differ by several orders of magnitude. Information about the confidence for the frequency and power within individual electrodes compared to the variance across electrodes will provide better intuition about the relative variability of the estimates over time and space.

We thank the reviewer for this concern. We added the following statement to the subsection ‘Analysis of frequency and power gradients’ in the Methods section to clarify the frequency resolution, “The resting-state recordings were five minutes duration and were analyzed from 1-50 Hz in 0.1 Hz intervals (491 frequencies).” The cluster frequency values reported in the Figures S1-S9 represent the average of the peak frequencies across all the electrodes and not the individual peak frequency values. While it is numerically correct, we agree that it is confusing to report these values with 3 significant figures, and we now report only one significant digit in the revised paper. The variability in peak frequencies across individual electrodes is shown via the red shading in Figure 1B, which indicates the standard error, and also in the histograms in Figure 1C. Peak frequencies of theta and beta oscillations appear to have relatively normal distributions across the insula. The caption of Figure 1 has been modified accordingly in the revised version of our manuscript to reflect these changes.

4) The overall signal level can vary across electrodes, especially when they have different distances from the white matter. It should be assessed that the reported power gradients are not simply driven by the relative position of the electrodes.

We appreciate the reviewer for pointing out the possibility that our results were impacted by white matter. We have analyzed this issue in detail and there is no meaningful impact of white matter to our results.

Author Responses

Reviewer #1 (Public Review):

This study uses a nice longitudinal dataset and performs relatively thorough methodological comparisons. I also appreciate the systematic literature review presented in the introduction. The discussion of confound control is interesting and it is great that a leave-one-site-out test was included. However, the prediction accuracy drops in these important leave-one-site-out analyses, which should be assessed and discussed further.

Furthermore, I think there is a missed opportunity to test longitudinal prediction using only pre-onset individuals to gain clearer causal insights. Please find specific comments below, approximately in order of importance.

We thank the reviewers for their positive remarks and for providing important suggestions to improve the analysis. Please see our detailed comments below.

1) The leave-one-site-out results fail to achieve significant prediction accuracy for any of the phenotypes. This reveals a lack of cross-site generalizability of all results in this work. The authors discuss that this variance could be caused by distributed sample sizes across sites resulting in uneven folds or site-specific variance. It should be possible to test these hypotheses by looking at the relative performance across CV folds. The site-specific variance hypothesis may be likely because for the other results confounds are addressed using oversampling (i.e., sampling with replacement) which creates a large sample with lower variance than a random sample of the same size. This is an important null finding that may have important implications, so I do not think that it is cause for rejection. However, it is a key element of this paper and I think it should be assessed further and discussed more widely in the abstract and conclusion.

We thank the reviewer for raising this point and providing specific suggestions. As mentioned by the reviewer, the leave-one-site-out results showed high-variance across sites, that is, across cross validation (CV) folds. Therefore, as suggested by the reviewer, we further investigated the source of this variance by observing how the model accuracies correlates with each site and its sample sizes, ratio of AAM-to-controls, and the sex distribution in each site. We ranked the sites from low to high accuracy and observed different performance metrics such as sensitivity and specificity:

As shown, the models performed close-to-chance for sites ‘Dublin’, ‘Paris’ and ‘Berlin’ (<60% mean balanced accuracy) in the leave-one-site-out experiment, across all time-points and metrics. Notably, the order of the performance at each site does not correspond to the sample sizes (please refer to the ‘counts’ column in the above figure). It also does not correspond to the ratio of AAM-to-controls, or to the sex distribution.

To further investigate this, we performed another additional leave-one-site-out experiment with all 8 sites. Here, we repeated the ML (Machine Learning) exploration by using the entire data, including the data from the Nottingham site that was kept aside as the holdout. Since there are 8 sites now, we used a 8-fold cross validation and observed how the model accuracy varied across each site:

The results were comparable to the original leave-one-site-out experiment. Along with ‘Dublin’ and Berlin’, the models additionally performed poorly on the ‘Nottingham’ site. Results on ‘London’ and ‘Paris’ also fell below 60% mean balanced accuracy.

Finally, we compared the above two results to the main experiment from the paper where the test samples were randomly sampled across all sites. The performance on test subjects from each site was compared:

As seen, the models struggled with subjects from ‘Dublin’ followed by ‘Nottingham’ ‘London’ and ‘Berlin’ respectively, and performed well on subjects from ‘Dresden’, ‘Mannheim’, ‘Hamburg’ and ‘Paris’.

Across all the three results discussed above, the models consistently struggle to generalize to subjects particularly from ‘Dublin’ and ‘Nottingham’. As already pointed out by the reviewer, the variance in the main experiment in the manuscript is lower because of the random sampling of the test set across all sites. Since these results have important implications, we have included them in the manuscript and also provided these figures in the Appendix.

2) The authors state that "83.3% of subjects reported having no or just one binge drinking experience until age 14". To gain clearer insights into the causality, I recommend repeating the MRIage14 → AAMage22 prediction using only these 83% of subjects.

We thank the reviewer for this valuable comment. As suggested by the reviewer, we now repeated the MRIage14 → AAMage22 analysis by including (a) only the subjects who had no binge drinking experiences (n=477) by age 14 and (b) subjects who had one or less binge drinking experiences (n=565). The results are shown below. The balanced accuracy on the holdout set were 72.9 +/- 2% and 71.1 +/- 2.3% respectively, which is comparable to the main result of 73.1 +/- 2%.

These results provide further evidence that certain form of cerebral predisposition might be preceding the observed alcohol misuse behavior in the IMAGEN dataset. We discuss these results now in the Results section and the 2nd paragraph of Discussion.

3) The feature importance results for brain regions are quite inconsistent across time points. As such, the study doesn't really address one of the main challenges with previous work discussed in the introduction: "brain regions reported were not consistent between these studies either and do not tell a coherent story". This would be worth looking into further, for example by looking at other indices of feature importance such as permutation-based measures and/or investigating the stability of feature importance across bootstrapped CV folds.

The feature importance results shown in Figure 9 is intended to be illustrative and show where the most informative structural features are mainly clustered around in the brain, for each time point. We would like to acknowledge that this figure could be a bit confusing. Hence, we have now provided an exhaustive table in the Appendix, consisting of all important features and their respective SHAP scores obtained across the seven repeated runs. In addition, we address the inconsistencies across time points in the 3rd paragraph in the Discussion chapter and contrast our findings with previous studies. These claims can now be verified from the table of features provided in the Appendix.

Addressing the reviewer's suggestions, we would like to point out that SHAP is itself a type of permutation-based measure of feature importance. Since it derives from the theoretically-sound shapley values, is model agnostic, and has been already applied for biomedical applications, we believe that running another permutation-based analysis would not be beneficial. We have also investigated the stability of our feature importance scores by repeating the SHAP estimation with different random permutations. This process is explained in the Methods section Model Interpretation.

Additionally now, the SHAP scores across the seven repetitions are also provided in the Appendix table 6 for verification.

Author Response

Reviewer #1 (Public Review):

However, their rationale is weakened by the fact that the authors do not examine the number of mechanoreceptive hair cells (as a minimum) and their sensitivity to mechanical stimulation (ideally).

We have performed additional experiments to address these concerns. We found that hair cell quantities per neuromast are similar between surface and cavefish (Figure 1 F). We have also performed additional electrophysiological recordings to evaluate the mechanical sensitivity of the system. We also took the initiative to stimulate across several stimulus frequencies, which revealed that cavefish are more responsive at higher stimulus frequencies than surface fish (Figure 2 F).

I also did not quite like their use of "regression of the efferent system". In my opinion, this implies that the ancestral animals have a weak efferent system, which developed further in Astyanax (generally) and then regressed upon cave colonisation. I would have used another word that more precisely defines a weakening of activity.

We thank the reviewer for pointing this out and have replaced the term with the phrase “partial loss of function”.

I found it curious that the authors did not discuss the evident reduction of swim bout length in cavefish, compared to surface fish (F2Aii). Also, this difference seems not to correlate with motoneuron spike bout frequency. Perhaps the authors can add a sentence or two to discuss these issues, or simply explain to me if I got it wrong.

We thank the reviewer for bringing this to our attention. Exemplar traces (now Figure 3 Ai & Bi) were selected due to their similarity to each other in order to highlight the inhibition during swimming in surface fish and a loss of effect in cavefish. It was not meant to represent the population mean. The reviewer is correct, and we now report results from a new statistical analysis that confirms that cavefish do exhibit significantly shorter swim bout durations (264 ± 4 ms) compared to surface fish (357 ± 5ms).

Author Response

Reviewer #1 (Public Review):

The manuscript by Sim and colleagues explores HLA C1 and C2 defining polymorphism and its impact on TCR recognition as opposed to the more documented impacts on KIR recognition. The manuscript is well written but requires some relatively minor changes prior to publication. The overall findings that subtle changes in peptide repertoire and peptide binding dictate TCR recognition is perhaps not surprising. The context of the study looking at KRAS G12D derived peptides provide additional interest to this manuscript. The work has been performed to a high level and includes reports of novel ternary complexes of HLA-C with a G12D heteroclitic peptide analogue along with associated biophysical characterization of the TCR interaction with these pHLA complexes.

We thank the reviewer for the kind comments. We also agree that even subtle changes in peptide sequence can be expected to change recognition of HLA-I by TCR. What we did find somewhat surprising is that the HLA-C C1/C2 dimorphism alone, in HLA-C molecules that are otherwise identical, puts constraints on peptide sequences that can be accommodated in the peptide binding site. It is the difference in those amino acids that, unsurprisingly, affect recognition by TCR, independently of TCR contact with amino acids 77 and 80 in HLA-C.

Reviewer #2 (Public Review):

This manuscript by Sim et al. describes the impact of different HLA-C1 and -C2 allotypes on T cell receptor (TCR) recognition. The study demonstrates that dimorphic position 77 in the HLAC heavy chain affected amino acid preferences at the C-terminus of the bound peptide, resulting in a weaker TCR affinity for HLA-C2 allotypes. The manuscript is clearly written, the data is sound and the figures are of high quality. The study is interesting and original; however the overall biological relevance remains unclear. It is uncertain how generalizable the findings will be to TCR recognition of HLA-C1 vs -C2 alleles in general, or whether the findings are perhaps more limited to this particular system. Moreover, the link/relevance to KIR recognition (if any) was not explained.

We thank the reviewer for these comments. We agree that it is unclear how generalizable our finding that C2 allotypes are worse TCR ligands than C1 allotypes. Further study of HLA-C restricted TCRs would be required to establish whether the effect we observed is truly generalizable. Such studies could examine how substitutions at position 77 and 80 influence responses of HLA-C restricted TCRs. Although, our study indicates that the effect is generalizable as both TCRs use different V genes and recognise different epitopes, and in both cases the C2 allotype is a worse ligand. Further, some of our other findings appear generalizable, such as the impact of the C1/C2 dimorphism on HLA-C immunopeptidomes and HLA-C structure. Presently, the translational relevance of our findings appear limited to the context of patients with KRASG12D-induced cancers in individuals carrying C08:02 or C05:01. In the context of KIR, earlier work has shown that positions 7 and 8 of 9mer peptides bound to HLA-C can have a large impact on KIR binding. An ongoing study by us is exploring the relevance of peptide-specific recognition of HLA-C by different KIR family members.

Author Response

Reviewer #2 (Public Review):

Schumacher and Carlson present volumetric data on the brain and main brain areas in several linages of fish that have independently evolved electroreceptors and electrogenesis. The main question is if the evolution of this novel sensory system has led to similar changes in the brain. Previously, the same authors (Sukhum et al 2018) have shown an increase in the relative size of the cerebellum and hindbrain in mormyrid fishes, one group of electrogenic fish. Here they have collected data on South American weakly electric fishes (Gymnotiformes) and weakly electric catfishes (Synodontis spp.) as well as some outgroups. (22 additionally species). I think the question is very interesting, and the inclusion of electrogenic catfishes is particularly interesting as they are a largely understudied group. I do have some concerns about how the data has been analysed and presented.

1) A first conclusion is that gymnotiform and siluriform brains are not as enlarged as mormyrid brains, and that this suggests that an increase in brain size is not directly tied to an electrosensory system evolution. I think the story here is more complicated than that. From the data presented, it seems that mormyrids have a different body size-brain volume slope than other groups, but is unclear if this was tested in the PGLS model for brain vs body size, although mormirids show different slopes than other groups in the scaling of the cerebellum to brian volume. This difference in slope for body brain allometry has been confirmed by a manuscript published after the submission of this manuscript (Tsuboi 2021 BBE) with a large data set (~ 850 species, 21 of Osteoglossiformes). This steep slope close to one means that mormyrids with large body size have very large relative brain sizes but smaller mormyrids don't (this can be seen in figure 2). I think this needs to be addressed more carefully. First testing in the PGLS for body size vs brain size if mormyrids have a different slope and then in the discussion. Why mormyrids but not other electrogenic fish have evolved such a unique brain scaling?

We thank the reviewer for this suggestion. We combined our data with the data from Tsuboi 2021 and assessed how the brain-body allometry has changed across 870 actinopterygians. We identified 3 shifts in lineages with at least 3 descendants and 7 shifts total that were supported by both the OUrjMCMC and PGLS analyses. One of these identified shifts was along the branch leading to osteoglossiforms, with a secondary decrease in one lineage within mormyoids. A second identified shift was along the branch leading to Synodontis multipunctatus. However, we find no shifts along the branches leading to other electrosensory lineages. This suggests that although mormyroids do have a different brain-body allometry compared with other electrogenic fishes, this shift predates the origin of mormyrids as it is found in all osteoglossiforms and thus is unlikely to be related to the evolution of electrosensory systems. These changes are reflected in lines 778-826, 110-153, 513-528, 530-538, 569-575 and figure 3 and associated source data files. See also our detailed response to essential revision 1.

2) I think the number of outgroups species used are too few and spread among several different linages of teleosts. I think this unfortunately tampers some of the conclusions. Particularly seems to leave unanswered the question if other electrogenic fish have brain larger than non electrosensory or electrogenic fish. A large data set of brain and body size data for teleost has been published (Tsuboi et al 2018; 2021). Adding this data should allow to test for changes in body-brain size relationships in the each electrogenic clades. The addition of the additional data should allow to accurately test for difference in relative brain size between and within electrogenic clades and make it possible to test when exactly in the phylogeny of teleost have grade shits in the body-brain allometry have happened.

We thank the reviewer for this suggestion. We explicitly addressed this question by fixing shifts along the branches that evolved our three electrosensory phenotypes: evolution of electrogenesis, tuberous electroreceptors, and ampullary electroreceptors. After comparing these models to the unfixed shift model, a model where only osteoglossiforms have a shifted allometry (following the finding of Tsuboi 2021), a model where only intercept can shift, and a model with one shared allometry across all actinopterygians, we found that the unfixed shift model has a better fit than any of the electrosensory phenotype associated models. This further supports the conclusion that a shifted allometry/ large brain size is not necessary to evolve an electrosensory system. These additions are reflected in lines 778-826, 110-153, 513-528, 530-538, 569-575 and figure 3 and associated source data files. See also our detailed response to essential revision 1.

3) Next, the authors use a principal component analysis and phylogenetic linear models to test how much of brain variation is explained by concerted evolution vs mosaic and where the mosaic change have happened. Here, despite the few non electrogenic/ electrocereptive species, the differences are more clear. I do think that in the case of the linear models, the use brain volume as the independent variable is unnecessary. By regressing the total brain volume, the authors are regressing each structure partially against the same value, and not surprisingly, this generates tight linear correlations. Further, this makes grade shifts (i.e. changes in relative size) less apparent. I think only brain volume -the structure should be used and shown in all figures. This has been the standard in the field when testing for grade shifts.

We thank the reviewer for this comment. There is much debate in the field regarding whether to use brain volume or brain volume – region of interest as the independent variable, and both are commonly used. Originally, we had looked at both and found qualitatively similar results, but only presented the ‘region x brain volume’ results in the main text for brevity. We have revised this to include the results of statistical analyses for ‘region x brain volume – region’ and the accompanying figures in the main text for both the electrosensory phenotype comparisons and the within electrosensory phenotype comparisons (broadly distributed throughout the results and figure 5—figure supplement 1, figure 5—source data 4-6, figure 7—figure supplement 1, figure 7—source data 2). All of the major findings of relative mosaic shifts between tuberous receptor taxa and non-electric taxa, between electrogenic + ampullary only and non-electric taxa for cerebellum and torus, and no mosaic shifts with electrosensory phenotype in telencephalon hold regardless of the method, and we only find minor differences between the analyses for comparisons that had p values near 0.05. These discrepancies do not change any major conclusions. However, we have kept the reporting of ‘region x total brain volume’ analyses in the main text figures to be consistent with other large comparative studies in the field and our group’s previous work (Yopak et al 2010, Sukhum et al 2018).

4) Related to the previous point, the authors report significant decreases electrogenic clades in the size of the olfactory bulb, rest of the brain and optic tectum. I think this is and artifact that results from including the cerebellum and other enlarged areas (TS and hindbrain) in the dependent variable. Similarly, the authors state that they found no increase in the size of the telencephalon in electrogenic clades and that non-electric osteoglossiforms have a mosaic increase in telencephalon relative to non-electric otophysans. Again, I think this suffers from the same problem. Figure 4-figure supplement 2 actually provides some insight in this respect. When plotted against the rest of the brain, no apparent differences are found in the size of the optic tectum. In the case of the olfactory bulb only two of the out-group species seem to have larger OB than all other species. Regarding the telencephalon, when plotted against RoB, all osteoglossiform seem to have similar telencephalon size. These conclusions need to be carefully evaluated.

We thank the reviewer for identifying this miscommunication. We have moved previous figure 4—figure supplement 2 to the main text (now figure 6) and have added the statistical analyses and discussion of this point to both the results and discussion. We have also clarified the distinction between relative and absolute shifts in region sizes throughout but see in particular lines 261-295, 307-317, 330-331, 473-499. See also our detailed response to essential revision 3.

Reviewer #3 (Public Review):

The authors use micro-CT scanning and sophisticated statistical techniques to compare the sizes of various major brain regions across a sample of 32 fish species, including lineages that have independently evolved passive electroreception and, in a smaller subset, the ability to generate and sense weakly electric fields. They found that most of the variation in brain region sizes is linked to variation in total brain size, indicating concerted evolution. However, the analysis also reveals that the electrogenic lineages/species have selectively enlarged the cerebellum, the midbrain torus semicircularis, and the hindbrain. These findings are interesting and usefully extend the last author's prior work on a subset of these species.

A significant strength of the work is that it includes a relatively large number of species, makes a good attempt to understand how these species are related to one another (though the authors admit that the phylogeny is tentative), and that the analytical methods are quantitative and relatively sophisticated. It is also true that other researchers have long argued about the relative frequency and importance of concerted versus mosaic evolution. The present study is a valiant attempt to address this issue.

However, some key results must be viewed cautiously. Most important is that the dramatic increase in the cerebellum (and torus semicircularis and hindbrain), relative to the rest of the brain, must necessarily lead to some other brain regions appearing to have decreased in size. Therefore, their absolute size may well have stayed the same or even increased in evolution; it's just that the enlarged brain regions decrease the proportions of at least some other regions. The authors mentioned this caveat in their previous paper on mormyroids (Sukhum et al., 2018), but not in the present manuscript. As a result of the problem, it is difficult to interpret the documented variation in olfactory bulb, optic tectum, or telencephalon size; is that variation "real" or just artifacts of major changes in the size of other brain regions (mainly cerebellum, torus, and hindbrain). The best way to address this problem would have been to repeat the analysis using a "reference" brain region that is thought not to vary dramatically in size across the species of interest (e.g., "rest of brain"). However, I acknowledge that this approach also has limitations. Still, the problem should be addressed somehow.

We thank the reviewer for identifying this miscommunication. We have moved previous figure 4—figure supplement 2 to the main text (now figure 6) and have added the statistical analyses and discussion of this point to both the results and discussion. We have also clarified the distinction between relative and absolute shifts in region sizes throughout but see in particular lines 261-295, 307-317, 330-331, 473-499. See also our detailed response to essential revision 3.

One strength of the manuscript is that it provides information about y-intercepts and slopes. Many other studies simply note increases or decreases in average volume (before or after correcting for absolute brain size). I like knowing which changes in relative brain region size are grade shifts (changes in intercept) versus changes in slope. However, the authors don't really do anything with those results. What do they mean? Are there different kinds of evo-devo mechanisms that underlie the two types of changes (slope versus intercept)?

We thank the reviewer for this suggestion. We have added some discussion on potential mechanisms for evolutionary changes in intercept and slope (lines 543-559). Unfortunately, this topic is not well studied in fishes, which have extensive adult neurogenesis.

On a related note, do the major brain regions vary in allometric slope within a given lineage? The realization that such differences do exist (at least in mammals and cartilaginous fishes) contributed much to the excitement around the concept of concerted evolution, since it means that evolutionary changes in absolute brain size can lead to major shifts in brain region proportions, but the authors seemingly ignore this point.

We thank the reviewer for this suggestion. We do find variability in slope for different regions of each lineage. We reported these values (figure 5—source data 1, figure 7—source data 1) and add discussion of this point (lines 539-542).

Finally, I must confess that some of the study's findings didn't surprise me. It is well known among fish neurobiologists that mormyrids have a dramatically enlarged cerebellum and that all electrogenic gymnotoids and mormyroids have a very large torus semicircularis and dorsal/alar hindbrain. One didn't need the fancy analytical techniques to confirm this. To be fair, however, it had not been clear whether the cerebellum is enlarged in gymnotoid electric fish and their non-electrogenic relatives (the authors report that it is). Nor was it known that the weakly electric catfishes have a larger cerebellum (not so much for the torus) than their non-electric relatives. This is new information that raises interesting questions about how the electric catfishes are using their electrosensory system (I would have liked to see some discussion of this).

We thank the reviewer for this comment. We too agree that electric catfishes warrant further study into which species are electrogenic, whether their discharges are sporadic versus continuous, and how they are using their electrosensory systems. We have added further discussion on electric catfishes (lines 411-416, 425-437).

On balance, I appreciate that the authors have provided a large and useful data set , which they used to address an interesting set of questions about how brain evolution "works." I'm just disappointed that, for me, there are relatively few significant, novel insights. For example, the notion that "selection can impact structural brain composition to favor specific regions involved in novel behaviors" (last sentence of the abstract) is one that I've accepted for a long time. Maybe the conclusion can be made more interesting by focusing more explicitly on changes in the size of major brain regions versus smaller cell groups (where mosaic evolution is widely accepted).

We thank the reviewer for this suggestion. We agree that mosaic evolution is more readily detected in smaller subregions/ nuclei/ circuits and is found less so at the scale of major brain regions. We have adjusted the text throughout to further highlight this distinction, but see in particular lines 42-48, 500-528.

Reviewer #4 (Public Review):

The authors present a detailed and thorough comparative analysis of brain composition across 3 different lineages of weakly electric fish, and several non-electric fishes. The goal of this comparison was to determine whether the evolution of electrosensory systems is associated with common changes in brain composition across the three lineages. Several aspects of this research are highly novel, such as the use of m-CT imaging and phylogeny-informed multivariate statistics. Overall, the authors show that cerebellar enlargement is key to the evolution of electrosensory systems of all three groups and the enlargement of the hindbrain and torus semicircularis varies depending on the types of electroreceptors and electrical signals produced. This is one of very few examples in evolutionary neuroscience of convergent evolution of brain anatomy and behaviour and sets the stage for future research on other sensory specialists and clades.

Strengths

The comprehensive analysis provided by Schumacher and Carlson has several strengths. First, the use of m-CT scans to derive neuroanatomical measurements in fish is relatively novel and the detailed descriptions of brain region borders were greatly appreciated. Few papers that focus on comparative neuroanatomy put this degree of effort into describing how regions were differentiated and defined, but the level of detail provided here will allow other researchers to acquire data in an identical method and is therefore an important resource.

Second, the statistical analysis is phylogeny-informed and uses an array of approaches. Too many neurobiology papers either avoid phylogeny-informed statistics or execute them poorly. This paper is neither of those and should serve as a template for future studies in the field.

Third, the inclusion of some recording data for Synodontis is an important contribution. I am not an expert on weakly electric fish, but I do know that the catfish are understudied compared with gymnotiforms and mormyroids. Hopefully, this will result in some well-deserved attention to the diversity of catfishes.

Fourth, I found the manuscript as a whole well written and presented. In particular, the authors provided a novel way of incorporating additional statistical information into Figures 3 and 4.

Last, the supplemental video was great addition to the data presented.

Weaknesses

First, the Introduction was a bit brief for readers unfamiliar with weakly electric fishes. It would be helpful to provide a bit more information to a general audience. Including a figure depicting the phylogenetic relationships among some (not all) bony fish clade to illustrate the independent evolution of electrosensory systems across the three clades would be particularly helpful in this regard.

We thank the reviewer for this comment. We have included more background on the evolution of electrosensory systems in actinopterygians and included a figure showing this (lines 76-83, figure 1).

Second, I think it is important to determine if the principal component analysis changes if the volumetric data is scaled. One issue that can affect multivariate analyses is including variables that differ greatly in scale. For example, if one brain region varies between 0.5-1.2 mm3, but another varies from 10-50 mm3 across species, that difference in scale can sometimes affect the PCA. I suggest checking that the analyses are broadly the same if the volumetric data is scaled (e.g., converting to z-scores).

We thank the reviewer for this suggestion. We z-score normalized the regions and repeated the pPCA and found nearly identical results (lines 175-177, figure 4—figure supplement 1).

Third is there any information regarding malapteurid catfish? Are they similar enough to Synodontis or could they exhibit yet another brain type from that discussed in this study? The reason I ask is that the authors raise the issue of Torpedo, but do not discuss other strongly electric fish like Malapteurus (which is a siluriform related to Synodontis).

We thank the reviewer for this comment. We too agree that they would be worthwhile species to add. Unfortunately, there is no data available on malapteurid catfish, and we were unable to sample any. We have added discussion of this point to lines 411-416.

Last, some of the graphs in the supplemental material are too small with datapoints too crowded to effectively read them. Larger graphs would enable a more effective evaluation of how the various clades differ from one another.

We thank the reviewer for this comment. We enlarged the region x region plots and plotted species means instead to make it easier to visualize these data (Figure 6, figure 7—figure supplement 2-4).

Author Response

Reviewer #1 (Public Review):

This study focuses on elucidating the function of CD59, a small GPI-anchored glycoprotein, in Schwann cell development. Patients with CD59 deficiency suffer from neurological dysfunctions, but the link between CD59 deficiency and the development of neurological dysfunctions remains unclear. To clarify this link, the authors used zebrafish as an animal model. They generated cd59 mutant zebrafish and studied their Schwann cell development. The authors started this study by showing CD59 expression data from different sources in the Schwann cell and oligodendrocyte lineages in zebrafish and mice. They continued by demonstrating that CD59 is expressed only by a subset of developing Schwann cells, which is very interesting conceptually for the identification of different Schwann cell populations and their specific functions and also for the potential development of future techniques targeting specific Schwann cell populations. However, since the authors focused in the following parts of the article on Schwann cell development, it is unclear why they have included data on oligodendrocytes at the start of the manuscript.

Thank you for this question. We included the data on oligodendrocytes because we wanted to be thorough and transparent. Additionally, because some of our own expression data show oligodendrocyte expression, we felt it was prudent to confirm this expression in published RNAseq datasets. Finally, we created and/or used tools to label cd59-positive cells, and we often used expression in both oligodendrocytes and Schwann cells as a readout of complete expression of these tools.

In this study, the authors show that cd59 ablation in zebrafish leads to increased Schwann cell proliferation between 48 and 55 hpf (hours post fertilization), which is quite convincing. However, they claim that this transient increase in proliferation leads to impaired myelination and node of Ranvier formation. Unfortunately, these findings remain correlative and it appears unclear why an increased number of Schwann cells that stop proliferating at the same time-point as wild type Schwann cells would impair myelination and node of Ranvier formation. This phenotype is attributed by the authors to increased proliferation of Schwann cells between 48 and 55 hpf, which seems rather unlikely or not supported by the data currently presented. The hypomyelination phenotype is rather mild, while the impairment of node of Ranvier formation seems quite strong - however, the data currently presented is not very convincing and needs improvement.

Thank you for your observations. With regards to how an increase in SC proliferation could impact myelination and node of Ranvier formation, although the rate of proliferation transiently increases, these excess SCs persist on the nerve. So, even though the mutants can stop developmental proliferation at the same stage, the mutants ultimately have more SCs on the nerve after proliferation has ceased. This raises the interesting question of how could more SCs lead to less myelin? To address this question, we added to the discussion to speculate on possible hypotheses as to why this is the case (please see line 510).

With regards to comparing the strength of the myelin phenotype and the node of Ranvier phenotype, there is no reason to suspect that there is a linear relationship between myelin volume and node of Ranvier assembly. We do know that myelination and SCs are necessary for node of Ranvier assembly. So, it is very possible that any perturbation in myelination could drastically affect node of Ranvier assembly. That said, this relationship is very interesting, and we hope that the cd59 mutant model can be utilized to further investigate these questions in future studies.

In regards to the node of Ranvier data itself, we have provided co-labeling of NF186 and NaV channels on mbpa:tagrfp-caax-positive nerves (see Figure 5 – figure supplement 1D). Using Imaris, we demonstrate that each NF186 cluster colocalizes with a NaV channel cluster. Furthermore, this colocalization only occurs within the myelinated nerve. Collectively, this data demonstrates that our quantification of nodes of Ranvier is reliable.

The data showing an increase of complement activation in cd59 mutants is also not very convincing and should be improved.

Thank you for sharing your concern. To address this issue, we have used Imaris to show MACs that are bound to SC membranes (see Figure 6B) for a clearer view of the data. Comparing wildtype and mutant larvae, there is a visible and significant increase in MAC binding to SC membranes when cd59 is perturbed. Additionally, we have included controls for these antibody labeling experiments to show specificity of these tools.

In addition, the link between increased complement activation and increased proliferation remains to be proven in the context of this study, and the choice of dexamethasone as an inhibitor of complement activation does not appear to be the best choice since it is not specific to the complement.

Thank you for sharing your concern. We agree that dexamethasone impacts other aspects of immune activation other than complement. With this in mind, we did test another drug called compstatin, which inhibits complement protein 3 (C3). Inhibition of C3 impairs all three complement pathways and would abrogate downstream assembly of MACs. Our preliminary data was very promising, demonstrating the same relationship that we see with our dexamethasone treatment (see below). However, we were unable to reproducibly get the same results in subsequent experiments after we purchased a new stock of this drug. To solve this problem, we tried compstatin from a different company as well as increasing the concentration, but none of our troubleshooting efforts yielded the same results that we had originally observed. Obviously, this is incredibly disappointing to us. So, although these results initially repeated, we did not feel it was ethical to publish this data. (In the figure below, wildtype and mutant embryos were treated with 1% DMSO or 50 µM compstatin in 1% DMSO from 24 hpf to 55 hpf. The number of SCs was quantified with a Sox10 antibody and confocal imaging at 55 hpf).

Given these technical limitations, we ultimately decided to include the dexamethasone experiments because they were reproducible. Considering the broader effects of dexamethasone on the immune system, we have softened our claims to include inflammation as well as complement activation. That said, we hope future studies will be able to use this model to gather more information on the specific pathways that are regulating Cd59-dependent SC proliferation.

Page 49, lines 437-439: Here the authors claim that their data "demonstrates that developmental inflammation aids in normal SC proliferation and that this process is amplified when cd59 is mutated." The data presented in Figure 6C-D and commented by the authors on page 49, lines 435-437, show however that "Dex treatment in cd59uva48 mutant embryos restored SC numbers to wildtype levels, whereas wildtype SCs were not significantly affected by Dex application". Dex (dexamethasone) was used here to inhibit inflammation and associated complement activation. Therefore, these data do not show that developmental inflammation aids in normal SC proliferation, but rather that it has no influence.

Thank you for your comment. When compared alone, there are significantly fewer SCs in dexamethasone-treated wildtype larvae compared to DMSO-treated wildtype larvae. We have updated the figure and text to better highlight this relationship (please see Figure 7A, C and line 457). We also quantified EdU incorporation into SCs treated with dexamethasone. Here we also observed a decrease in EdU-positive SCs in wildtype larvae treated with dexamethasone, supporting our observation that developmental inflammation is contributing to normal SC proliferation (please see Figure 7B, D).

Dexamethasone treatment: The authors claim that dexamethasone treatment, by decreasing inflammation and associated complement activation, leads to a decrease of SC proliferation in the cd59 mutant. To support this, there is only Figure 7-Figure Supplement 1 showing a decreased SC number in the mutant treated by dexamethasone as compared to vehicle-treated mutant. To strengthen this point, the authors also need to specifically quantify proliferation by EdU incorporation, as they did in Figure 4, and also cell death.

Thank you for your comment. We have added quantification of EdU incorporation after dex treatment (please see Figure 7B, D). Dr. Feltri, the Reviewing Editor, told us that measuring apoptosis after treatment was not necessary for the revision.

In addition, the mechanistic hypothesis of increased proliferation in cd59 mutant is that cd59 interferes with the activation of the complement and complement-induced pore formation in the plasma membrane. However, dexamethasone is not a specific inhibitor of the complement. Therefore, its potential effect on SC proliferation could be due to other effects than complement inactivation. It is unclear why the authors did not use an inhibitor of the complement that is more specific than dexamethasone.

Thank you for your comment. Please see our previous response to this comment.

Page 54, lines 456-457: The following statement "Collectively, these data demonstrate that inflammation-induced SC proliferation contributes to perturbed myelin and node of Ranvier development." is not accurate since these data remain correlative. Indeed, there is in this study nothing showing that increased SC proliferation between 48 and 55 hpf leads to perturbed myelin and node of Ranvier development. In addition, the term "inflammation" is not precise enough here. What the authors attempt to show is an increase of complement activation due to the absence of cd59 expression in SCs. The authors did not try to induce inflammation in wild type animals to see whether this induces proliferation and perturbed myelin and node of Ranvier development. They also did not try to directly knock down C8/C9 in cd59 mutants to see whether they would rescue the phenotype of the cd59 mutant, at least to some extent. In addition, their statement mentioned above needs to be more precise by stating that their findings apply to cd59 mutants and not to wild type animals.

Thank you for your comment. Please see our previous responses to these comments.

Reviewer #3 (Public Review):

Wiltbank and colleagues explore the function of CD59 in developmental Schwann cell myelination. Using previously published transcriptomics data sets they arrive at CD59 as a differentially expressed gene in myelinating glia. In addition, patients with pathogenic variants have neuropathy. The authors construct a transgenic zebrafish reporter line for cd59. Surprisingly, it labels a very, very small percentage of Schwann cells (less than 10% throughout development). The authors then construct several loss-of-function mutants for cd59. They report these mutants have increased numbers of Schwann cells, but nerves are smaller and EM shows they have reduced the number of myelin wraps. Consistent with impaired myelination they also observe fewer nodes of Ranvier. The authors suggest loss of cd59 results in increased MAC deposition on myelinating Schwann cells. Remarkably, using an inhibitor of inflammation (dexamethasone), the authors show that they can normalize/rescue the main phenotypes: 1) normalize the number of SCs, 2, dramatically improve myelination to normal nerve volumes, and 3) rescue node of Ranvier formation. This last experiment that rescues the phenotype is really terrific. The experiments are mostly very well done and the story is both interesting and conceptually novel. Nevertheless, there are a few points that I think the authors could address:

1) It is very surprising that the cd59 reporter line only showed expression in a small subset (10% or less) of Schwann cells. How do the authors explain the widespread effects? Similarly, the authors make a point of stating that motor Schwann cells did not express cd59. Did myelinated motor axons show the same phenotype - reduced myelination, impaired node formation? How can the expression of cd59 in only 10% of cells cause widespread effects throughout the nerve? How can it limit overproliferation if 9/10 cells don't even express it?

Thank you for the question. It is really interesting that a small subset of cells can have such a big impact on nerve development. One of our current hypotheses is that overproliferation of SCs has led to activation of contact-inhibition pathways, which in turn are negatively regulating myelination. We expand further on this hypothesis in our discussion (please see line 536). We also suggest questions addressing glial cell heterogeneity to explore in the future (please see line 603).

In regards to the motor nerves, we quantified the number of Sox10-positive cells (SCs and MEP glia) on motor nerves at 72 hpf and showed that there was no overproliferation of these cell types (please see Figure 4I, J). We have not observed any issues with motor nerve myelination, which is what we would expect if motor SC proliferation was unaffected. That said, these differences between motor and pLLN SCs are really interesting because it opens up discussion for glial cell heterogeneity between nerve types (e.g. sensory versus motor nerves). We see similar evidence of this in satellite glia that populate the cochlear spiral ganglion versus those that surround the dorsal root ganglia (see Tasdemir-Yilmaz et al. 2021 or Wiltbank and Kucenas 2021), so it makes sense that there could be some SC diversity between nerve types as well. We expand further on these ideas in our discussion (please see line 603).

2) It is surprising to me that there is a significant increase in SC proliferation, but no change in the length of myelin sheaths. Does this mean there are more SCs that remain unmyelinated and undifferentiated?

Thank you for your comment. We were also surprised. With our current tools, we are unable to determine the fate of these extra SCs but hope that future studies will be able to clarify this question. We have added discussion around this topic to the text (please see line 554).

3) The results showing deposition of the MAC (via C5b-9+C5b-8 immunostaining) are not convincing. The overall background level of immunostaining is dramatically increased. This result is central to the overall story in the paper. What controls were performed to confirm this doesn't simply reflect an overall higher background artifact during immunostaining?

Thank you for your comment. We have added our antibody controls to the supplemental figures (please see Figure 6 – figure supplement 1A) demonstrating that we can increase MAC deposition by inducing complement activation (either through heat-related damage or DNase-elicited DNA damage). We also do not observe signal when the primary antibody is not present. Based on our controls, we do not think the extra MAC labeling is background. Rather, we believe that MAC deposition has increased globally in the cd59 mutant embryos. This is not surprising given that complement activation leads to a positive feedback loop of more complement and immune activation, which is likely occurring in the cd59 mutants.

To help clarify the MAC data, we have also added Imaris renderings of the MACs that are bound to the SC membranes, demonstrating that there are more MACs embedded in the cd59 mutant SC membranes compared to wildtype SCs (see Figure 6B).

4) Can the authors speculate on a mechanism for how promoting more MAC results in increased proliferation?

Thank you for your question. We have added discussion around this topic to the text (please see line 585).

Author Response

Reviewer #1 (Public Review):

The authors succeeded in providing a well-done investigation on the psychological impacts of the COVID-19 pandemic. The major strength of this manuscript is the sound methodology and the huge sample size recruited for the investigations of study aims. Another strength of this manuscript is incorporating the role of social media in this issue. No major weakness is apparent in this investigation.

Thank you for your careful review of our work. Your feedback helps us a lot to improve our manuscript. We have worked through your comments point by point and adjusted our manuscript accordingly.

Reviewer #2 (Public Review):

Daimer et. al investigated cross-sectional associations using an online survey for assessing the association of 2 predictor factors (i.e., life concerns of COVID-19 and social relationships) with 3 mental health outcomes namely schizotypal trait, depression, and anxiety related symptoms. The authors also assessed for mediating factors such as sleep duration, alcohol consumption, drug use, social media exposure, etc. and finally explored any mediating effects of anxiety and depressive symptoms in the association between the predictor factors with schizotypal trait. The main take-away message of the analysis is the direct positive associations observed for COVID-19-related concerns, social adversity with the mental health outcomes and also to some extent via the mediating effects of excessive media use.

The conclusions of this paper are mostly well supported by statistical analysis; however, some biases need to emphasized as limitations.

Thank you for your careful review of our manuscript and your comments and suggestions for improvement. We have edited and added them in the paper. See below for a detailed response to your suggestions.

1) Authors do not address the plausible reasons for their finding on the association of more exercise with higher levels of anxiety.

Thank you for pointing that out. This association is interesting, as it contradicts general findings, of the positive impact of exercise and mental health. Here, however, we may need to consider that gyms, swimming pools, sports classes were closed or cancelled during the pandemic, forcing individuals to compensate with other types of exercise, which might lead to frustration or anxiety. We have expanded the section on this in the discussions.

P34/35: “We did not find a negative association between COVID related life concerns and physical activity; however, we found a positive association between physical activity and mental health scores; indicating that more physical activity is associated with higher anxiety in the September/ October 2020 survey and May 2021 survey. This is surprising and contradicts a large body of literature showing the positive effect of exercise on levels of anxiety, depression and stress (for review see (Mikkelsen et al., 2017)). However, people who play sports frequently may have suffered more from the pandemic containment measures, which included severe restrictions on the execution of sports. Here, especially team sports are affected, which combines positive social interaction with sports. In order to compensate, affected individuals may over-compensate with individual sports which lacked the social component. The associations found in our surveys occurred when general restrictions were lower, therefore, more exercise potentially means an increased risk of exposure to potentially infected individuals, for example, in gyms. A study by Mehrsafar et al. showed that among professional athletes, isolation from their athletic team, reduced activity and training, lack of formal coaching, and lack of social support from fans and media triggered emotional distress (Mehrsafar et al., 2020). A third possibility could be that individuals started exercising more frequency and regularly during the pandemic as a result of loneliness, boredom or the knowledge of positive effects of sports on anxiety and depression; however, sport alone cannot completely protect against mental health problems (Pensgaard et al., 2021).”

2) Though the authors have stated the uncertainty of the observed associations but do not fully discuss its reasons, e.g., the sampling bias (i.e., recruitment via social media will lead to disproportionately selecting participants with excessive media consumption leading to biased associations) or volunteer bias (i.e., if some age-group/one particular gender/particular educational category are more likely to participate than others) which are inherent to this type of study designs.

Thank you for pointing this out. We have added a paragraph in limitation section in the discussion, see our response to point 4 in essential revisions above.

P37: “Second, the sample might be biased due to the recruitment strategy. Recruitment was performed through print and social media; however, the questionnaire was only available online, so people without internet access or less ability in using the internet were either excluded from participation or had to rely on people guiding them through the survey. This especially applies to older individuals, who have less access to the internet than young people (Prescott, 2021; Quittschalle et al., 2020). However, we were able to recruit individuals from ages 18-93, with 16.73% aged above 60, which shows a good general representation of age. Since excessive media consumption was investigated in this study, the recruitment strategy, especially via the Internet, may have led to a bias, reaching a disproportionately large number of people who use media excessively. However, in the first investigation (Knolle et al., 2021) using the same recruitment strategy we found that media consumption increased during the COVID-19 pandemic compared to prior to the pandemic. Also, a sampling bias may have occurred over-representing individuals attracted to the topic of mental health (Andrade, 2020), which could one the one hand heighten the strength of the observed associations compared with a representative general population sample and on the other explain the overrepresentation of individuals with higher educational backgrounds. Biases like these are difficult to overcome especially in psychological research. These limitations may affect the generalizability and representativeness of the study.”

Author Response

Reviewer #1 (Public Review):

Apicomplexan parasites, including the malaria parasite Plasmodium, possess a characteristic inner membrane complex (IMC), which plays an essential role in maintaining the parasite shape and regulating motility. In this interesting study, Qian and colleagues determine the IMC proteome of erythrocytic stages in the rodent malaria parasite Plasmodium yoelii, and identify the palmitoyl-acyl-transferase DHHC2 as a key enzyme that regulates the localization of IMC proteins through palmitoylation. The authors used a proximity biotinylation strategy based on TurboID to identify by mass spectrometry 300 proteins associated with the IMC. Using genetic tagging they could confirm IMC localization of 19 out of 22 selected candidate proteins. This analysis revealed that many of the IMC proteins are predicted to undergo palmitoylation, a modification that is known to play a role in protein localization to the IMC. The authors identified 3 candidate IMC palmitoyl-acyl-transferase, including DHHC2, which was most highly expressed and predicted to interact with many of the identified IMC proteins. Using conditional protein depletion based on the auxin degron system, the authors demonstrate that DHHC2 is essential for blood stage growth, schizont segmentation and merozoite invasion, and show that DHHC2 palmitoylates GAP45 and CDPK1, two essential IMC proteins. Altogether this study provides a comprehensive view of the IMC proteome and the role of palmitoylation in Plasmodium erythrocytic stages.

The study identifies a large number of putative IMC proteins, with only partial overlap with other studies performed in P. falciparum. This suggests a potentially high rate of false positives, although 11 out of 14 new proteins were confirmed to be localized in the IMC. The authors should explain how they selected the 14 candidate proteins. This is important to ensure the absence of bias. Do these proteins correspond to the 22 proteins with assigned GO term IMC (line 219)? It is likely that many of the identified proteins correspond to trafficking-related proteins, as discussed in the text, or plasma membrane proteins (such as PMP1) or cytosolic proteins (since the ligase is exposed on the cytosolic face of the IMC).

In the initial manuscript of this study, we chosen 22 hits for their protein subcellular localization test. There are 8 protein hits previously validated localizing at IMC in other Plasmodium species and 14 hit candidates whose localization at IMC have not been validated in the Plasmodium. These 22 hits were chosen basically in a random manner, but they showed various (high, middle, and low) levels in the enrichment ratio detected by the TurboID-mediated proximity labeling (Figure 2A).

Reviewer #3 (Public Review):

In this manuscript, the authors use TurboID proximity labeling to identify novel components of the Plasmodium inner membrane complex. They then verify many of the identified candidate proteins, demonstrating the utility of the approach. They build on this by identifying the major palmitoylacyltransferase involved in tethering IMC proteins to the membranes of the organelles and directly test the importance of palmitoylation in the trafficking and function of several key IMC proteins. The experiments are supported by extensive controls throughout the paper. Overall, this is a robust paper that provides an important addition to the field. Specific comments are below.

1) line 149 and S2A. The authors use the term "signal peptide" for the N-terminal 20 amino acids of ISP1 that target TurboID to the IMC

a. "signal peptide" is likely to be confused with a secretory signal peptide for entrance into the lumen of the ER/golgi. There is no predicted signal peptide on ISP1 (Signal P Prediction), instead ISP1 is likely both myristoylated and palmitoylated as previously shown in T. gondii. This tethers the protein to the cytoplasmic face of the IMC (and potentially to vesicles targeting to the IMC).

b. Line 565-573 This becomes more confusing in the discussion when the authors claim that the "signal peptide" directs the fusion through the ER/Golgi secretory pathway. Together, this would be better stated as an "IMC targeting peptide" to avoid confusion with this well-established nomenclature (and modify the discussion accordingly)

Thanks for reviewer’s good suggestion. We changed the “IMC signal peptide” to the “IMC targeting peptide” through the text.

2) Regarding predicted acylation of TurboID identified IMC protein candidates

a) It would be useful to state how many of the proteins are predicted to be palmitoylated and add this to table S1.

We have added a new column containing related information in Table S1.

b) Since myristoylation also plays a role in IMC trafficking, it would also be useful to state how many of the proteins are predicted to be myristoylated (also add to S1).

We have added a new column containing related information in Table S1

Author Response

Reviewer #2 (Public Review):

This manuscript describes a method for generating floxed conditional alleles in the zebrafish. The method employs the authors' previously reported GeneWeld CRISPR/Cas9 short homology-directed targeted integration strategy to introduce a "UFlip" cassette that allows target genes to be "turned off" or "turned on" in a tissue-specific manner with appropriate cre driver lines. The authors provide data to show the efficacy of their new method by targeting hdac1, rbbp4, and rb1. Although a variety of other methods have recently been reported for gene inactivation in the zebrafish (many of which were cited and discussed by the authors of this manuscript), the authors method could provide some notable and significant advances including speed and ease of generation of conditional alleles and flexibility to generate "on" and "off" alleles at the same genomic locations. However, the authors would need to do more to provide additional and more quantitative data validating some of the important features and advantages of their method. A few of the most significant issues that should be addressed include:

Better assessment of the efficiency of cre/dre "flipping" of integrated constructs.

It's important that the authors provide data showing not just that inversion of their integrated constructs can happen, but quantitatively measuring how efficiently this occurs. The authors should provide qPCR or other measurements to assess % inversion of their constructs via injected and transgene-driven cre. The authors should also provide data quantitating the % efficiency of dre/rox inversion used to turn "off" alleles into "on" alleles and vice-versa (see Supp Fig. 5).

We performed genomic qPCR to assess efficiency of Cre-mediated inversion. Cre injection led to robust inversion efficiency of 82-93%. As expected, the efficiency of inversion with transgenic ascl1b-2A-Cre and neurod1-2A-Cre was lower, ranging from 20-30%, due to the expression of these Cre drivers in a subset of cells in the embryo.

The utility of the rox sites is illustrated in Figure 3. We injected Dre mRNA injection into rbbp4off/+ embryos and screened adults for germline transmission of an inverted rbbp4off to rbbp4on allele (Figure 3). This was highly efficient, >50% of adults that were injected with Dre mRNA as embryos transmitted the inverted allele to progeny, with a frequency of 7-43% inheriting the rbbp4on allele. Starting with a UFlip-2A-mRFP “off” allele, which we recovered at frequencies of 12.5% (rbbp4off is61) and 14% (rb1off is63) (Table 2), it is easy to recover the conditional “on” allele by Dre-mediated inversion.

Although the authors provide junction qRT-PCR suggesting efficient transcript blocking by "off" insertion alleles (eg Fig 2B,J) it would also be useful to further validate and explore the effects of "off" UFlip transgene insertions on expression of targeted genes by similar qRT-PCR on upstream and downstream exons in control vs. het or homozygous transgene insertion animals to assess whether truncated transcripts are degrading, and whether expression of downstream exons is indeed absent.

We used both RT-qPCR and phenotypic assessment to determine the impact of the cassette integration on gene expression and gene activity. As suggested, we included RT-qPCR results for the wildtype exon-exon splicing that would be disrupted by the cassette integration in the intron. We also examined splicing between exons downstream of the integration. These results demonstrate that in the gene “off” orientation endogenous gene expression is 99% knocked down. Integration in the passive “on” orientation did reduce expression in homozygotes (rbbp4on/on Figure 4 J reduced by 40.7%; rb1on/on Figure 7 J 1 reduced by 17.1%). However, the reduction in expression did not lead to mutant phenotype in heterozygotes ,or in combination with loss of function alleles (Figure 4 K-N; Figure 7, K-P), indicating gene activity was not disrupted. This may be gene dependent.

Better validation that "null phenotypes" can be generated.

Although the qRT-PCR data the authors provide suggests efficient transcript blocking by "off" insertion alleles, the authors need to strengthen some of their data showing that null phenotypes are being generated by these alleles. In many cases the authors provide only anecdotal images, describe relatively generic phenotypes, or provide quantitative measurements of mutant phenotypes (eg pH3 positive cells) that lack key positive controls such as comparable quantitative measurements on previously generated bona fide "null mutant" alleles of the same genes. All of this is important to demonstrate that this method can generate robust phenotypes that are both qualitatively and quantitatively comparable to null mutants.

For each conditional allele that was isolated we performed RT-qPCR on embryos from each genotypic class of a conditional allele incross, to determine the impact of the targeted allele on gene expression (Figures 4, 5).

Quantification of mutant phenotypes and statistical analyses to determine significance have been performed for 1. The characterization of the conditional alleles 2. The assessment of conditional rescue or inactivation. Data plots with p values are included in all figures and figure legends.

Demonstrate tissue-specific "flipping on." One of the major points of novelty and most exciting features of the authors methods over other recently reported approaches is the potential to carry out tissue-specific gene activation (by cre-flipping on "UFlip-Off" alleles). This would be an exceptionally useful and powerful new tool for fish researchers (and others). Surprisingly, this particularly exciting feature is curiously unexplored in this manuscript, although the authors do generate a number of UFlip-On alleles. The impact and significance of this manuscript would be substantially increased by a well-validated and quantitated demonstration of tissue-specific activation of a "UFlip Off" allele, perhaps demonstrating rescue and lack of rescue of tissue-specific specific mutant phenotypes by activation using different cre drivers.

Thank you for this suggestion. We performed the following experiments:

• Tissue-specific conditional rescue: Using the conditional rbbp4off and rb1off alleles we demonstrate the ability to turn a gene “on” and rescue a loss of function phenotype. Conditional rescue of rbbp4off to “on” with ascl1b-2A-Cre lead to a reduction in apoptosis in the midbrain, although not significant (Figure 5). Conditional rescue with neurod1-2A-Cre did not lead to any apparent rescue, suggesting rbbp4 isn’t required in this cell population for survival.

Conditional rescue of rb1off to on with neurod1-2A-Cre was clear and robust (Figure 8 O), suppressing the mutant phenotype with significant reduction in the number of mutant cells throughout the midbrain and retina. The same rescue was observed with the ascl1b-2A-Cre, but in the interest of space we did not include this data in Figure 8.

• Tissue-specific conditional inactivation: Using the conditional rbbp4on and rb1on alleles, we demonstrate using cell type specific proneural Cre drivers that each gene is required in the progenitor population during brain development. Conditional inactivation of rbbp4on to “off” with ascl1b-2A-Cre leads to apoptosis in the developing midbrain optic tectum (Figure 6, Figure 6-figure supplement 1 and 2). Conditional inactivation of rb1on to “off” with neurod1-2A-Cre leads to inappropriate cell cycle entry in the midbrain tectum and retina. (Figure 9, Figure 9-figure supplement 1).

Together with the conditional inactivation experiments using ascl1-2A-Cre and neurod1-2A-Cre that validate the cell type-specific requirement for these genes, the data demonstrating cell type-specific rescue is compelling.

Future work using tamoxifen responsive CreERT2 drivers would help refine these analyses of cell type-specific requirements for gene function. We believe our current study provides a solid foundation demonstrating both conditional inactivation and rescue are possible.

• Ubiquitous conditional inactivation and rescue: By Cre injection, we demonstrate robust conditional inactivation (“on” to “off”) and induction of mutant phenotypes for both genes (Figures 6 and 9). We also demonstrate robust conditional activation (“off” to “on”) and rescue of mutant phenotypes for both genes (Figures 5 and 8).

• In all cases we provide rigorous quantification and statistical analysis of phenotypic changes and measure the frequency of Cre-mediated recombination.

Author Response

Reviewer #1 (Public Review):

This is a fascinating study that apparently began with an original observation (a Hif-1a splice variant heretofore unexamined in insect flight muscles) that sparked the sort of "can't miss" question that all scientists crave, where any outcome is interesting. In this case, what are two Hif-1a variants doing in a highly aerobic tissue in migratory locusts, a species that is both physiologically fascinating and a major agricultural pest? The authors undertook a well-designed and thorough experimental study that used a broad swath of methods to examine bioinformatic data, tissue- and age-specific gene and protein expression, downstream regulation of metabolic genes and metabolites, upstream regulation by PHD, redox regulation, and effects on speed and duration of locusts during prolonged flight. Numerous molecular manipulations were performed to make the study rigorous and results easy to interpret. Ultimately, by using this highly integrative approach, the study provides a compelling picture that the Hif-1a2 splice variant plays a previously undescribed function by regulating Dj-1, which is both an antioxidant and a regulator of other anti-oxidant genes, thereby limiting oxidative damage during prolonged aerobic activity and long migratory flights.

The study and its presentation have many strengths. These include the clear formation of a series of testable hypotheses and critical experiments, progressing from each set of experimental results to the next hypotheses and experiments, and an interesting and nuanced discussion of the results that is well framed in prior findings in other species (including birds and humans) that are similar or different in their physiology and behavior. Ultimately it is an interesting and thought-provoking paper, and a valuable contribution to knowledge in areas that encompass oxygen-related regulatory biology, insect physiology, and animal flight.

We greatly appreciate the reviewer’s invaluable and helpful comments.

1. Something that is present in a supplementary figure but not discussed in the text is a taxonomic consideration of the presence of Hif-1a splice variants in other insects. Are these unique to locusts or Orthoptera, or are they general to all insects? There are, for example, four Hif-1a splice variants in Drosophila, so the authors should discuss what is known and unknown in this realm.

The reviewer raises a good point. We performed taxonomic analysis of Hif-1α splice variants across taxa based on transcriptome data and documentary reports (Figure 1-figure supplement 2). Hif-1α in the locust species generates two transcripts, i.e., the full-length Hif-1α1 and the short Hif-1α2 that lacks the domain C-TAD. We analyzed the transcriptome data of Deracantha onos (Orthoptera), Grylloblatta bifratrilecta (Grylloblattodea) and Periplaneta americana (Blattodea). Only in D. onos did we find Hif-1α transcript variants with structure similar to those in the locust. Previous reports also showed that the C-TAD domain as well as its inhibitor FIH are absent in Hif-1α at the genomic level in some complete metamorphosis insects, including wasps (Hymenoptera), fruit flies (Diptera), moths and butterflies (Lepidoptera). Thus, the C-TAD-lacked Hif-1α transcripts seem to commonly exist in different insect taxa. However, different from the Orthoptera species, the C-TAD-lacked transcripts of Hif-1α in other taxa are not generated from alternative splicing.

We have added the Hif-1α splice variants of D. onos to Figure 1-figure supplement 2, and submitted these transcripts to NCBI with gene accession number ON137898 and ON137899. A statement of this issue have been added in Results as follows:

“Evolutionary analysis revealed that such Hif-1α splice form also exists in other Orthoptera (Accession no. ON137898 and ON137899 for Deracantha onos), some birds (e.g., XP_025006307.1 for Gallus gallus and XP_013038471.1 for Anser cygnoides domesticus), and human (NP_851397.1). Additionally, the TADs of Hif-α have varied distributions amongst insects. In incomplete metamorphosis insects and beetles the Hif-α protein possesses two TADs (N-TAD and C-TAD), but in flies and moths the C-TAD and its inhibitor FIH are completely missing at the genomic level. Therefore, C-TAD-lacking Hif-1α transcripts, with distinct origins, seem to commonly exist in different insect taxa (Figure 1-figure supplement 2).” (Line 108-116)

Meanwhile, we have given discussion as follows:

“Alternative splicing may be a source of functional innovation for Hif-α in locusts. In this study, we found that Hif-1α in locust species generates two transcripts, i.e., the full-length Hif-1α1 and the short Hif-1α2 that lacks the C-TAD domain. The C-TAD of Hif-α is under strong selective pressure in invertebrates; it first appears in non-bilaterians (Nematostella vectensis) and has a varied distribution amongst invertebrates (Graham and Presnell, 2017). This domain and its inhibitor FIH are completely absent at the genomic level in some newly emerged insect species, including wasps (Hymenoptera), true flies (Diptera), moths and butterflies (Lepidoptera), all of which are outstanding flyers (Graham and Presnell, 2017). Genetic variations in the Hif pathway can affect the tracheal volume and flight performance of lowland butterfly populations under well oxygenate environment (Marden et al., 2013). This evidence combined with our findings, implies that the emergence of C-TAD-lacking Hif-1α transcripts is likely to be a substrate for flight adaptation in some insect species.” (Line 366-377)

1. The most prominent unanswered question from a mechanistic standpoint is "what causes the Hif-1a2 variant to have unique upstream and downstream regulation?". Age and tissue specific expression of Hif-1a2 implies that the locust Hif-1a gene may have promoters that differently affect alternative splicing during development, and in an oxygen sensitive fashion in mature flight muscle. The paper states that lack of regulation of genes that inhibit mitochondria suggests that Hif-1a2 transcription factor activity is altered by absence of the C-TAD. Figure 6F is a compact summary of the functional differences, but a more complex supplementary figure showing a hypothesis that summarizes both the upstream and downstream regulatory details would help readers form a mechanistic understanding. The text could do this by elaborating a bit more on the ideas in lines 288-290.

We’re glad to follow the reviewer’s suggestion and added a supplementary figure to present a mechanistic hypothesis (Figure 6-figure supplement 2). We added discussion on this issue:

“The regulatory mechanism underlying the spatiotemporal expression of Hif-1α2 remains elusive. Alternative splicing is one of the main sources of spatiotemporally specific mRNA expression and proteomic diversity in eukaryotes. The diverse expression of alternatively spliced mRNA isoforms is usually attributed to alternative promoters or regulatory splicing factors (Fu and Ares, 2014; Russcher et al., 2007). Alternative promoters can produce a wide variety of transcripts at transcription initiation sites or even affect the splicing patterns of downstream exons (Zavolan et al., 2003). The regulatory splicing factors with cell-type–specific expression can bind specifically to enhancers or silencers of a premature mRNA to promote or repress splicing (Fu and Ares, 2014). Therefore, alternative usage of promoters or regulatory splicing factors could contribute to the age and tissue-specific expression of the locust Hif-1α transcripts (Figure 6-figure supplement 2). However, detailed mechanism requires further elucidation.”(Line 404-414)

The downstream regulatory mechanism was discussed in Line 285-294.

1. In the conclusion, the authors should perhaps be more explicit about the hypothesis that Hif-1a2, which is expressed in normoxia and more so at low oxygen tension, provides continuously variable expression of anti-oxidant genes so that protection is in place before the damage occurs. This is different from the way Hif-1a1 is typically activated only at very low oxygen tension, which in a highly active tissue may provide protective effects too late to prevent oxidative damage. Thinking in this way may stimulate experiments across time courses and/or graded oxygen tension that provide additional insight and further refine thinking about canonical versus non-canonical function of Hif gene variants. Such a discussion may be a springboard for pondering why all species don't do this. Or is it possible that they do, and this study is only the first glimpse?

We appreciate the reviewer for providing the thoughtful insight for discussion. Following the reviewer’s suggestion, we have given a discussion on this topic in Discussion as follows:

“The two Hif-1α splices may coordinate their roles in long-lasting flight tasks. In locusts, the canonical role of Hif pathway is modulated by Hif-1α1, which regulates metabolic reprogramming and possibly controls tracheal growth under low oxygen tension. However, the abundant tracheal system of the locust flight muscle may keep the intracellular oxygen tension above the low level that triggers Hif-1α1 stability. Meanwhile, the relatively easy task of flying with weight support on a flight mill in the present study may render the role of Hif-1α1 in flight muscle undetectable. Nevertheless, when it comes to highly active tissue, Hif-1α1 may provide protective effects too late to prevent oxidative damage. Instead, Hif-1α2, which is expressed in normoxia and has a graded activity with decreasing oxygen, provides continuously variable expression of antioxidant genes so that protection is in place before the damage occurs. This is different from the way Hif-1α1 is typically activated only at very low oxygen tension. As shown in Figure 1-figure supplement 2, the similar transcript form of locust Hif-1α2 also exists in some other insect species and birds. Therefore, the Hif-1α2-mediated protective mechanism is possibly applicable to other flying animals, with the locust in this study as the first glimpse.”(Line 390-403)

1. On a related note, the discussion may benefit by considering other findings regarding oxidative damage caused by flight in insects that differ in their flight physiology, behavior and life history. (https://academic.oup.com/biomedgerontology/article/61/2/136/542463; https://www.science.org/doi/abs/10.1126/science.aah4634; https://journals.biologists.com/jeb/article/221/6/jeb171009/246/Enzyme-polymorphism-oxygen-and-injury-a-lipidomic. Have these species independently evolved different mechanisms, or might this new discovery be part of a suite of mechanisms for oxygen-related physiological and protective mechanisms in insect flight muscles?

Thanks for providing these informative documents. We have added a discussion on this issue:

“Additionally, oxidative damage caused by flight in insects differs in their flight physiology, behavior and life history. A sustained flight throughout life can cause a higher mortality rate to Drosophila (Magwere et al., 2006). Flight activity of honey bees directly leads to increased oxidative damage, which in turn detrimentally affects their flight performance and foraging ability (Margotta et al., 2018). Insects have evolved a series of adaptive strategies to cope with intermittent and migratory flight-induced oxidative stress. Glanville Fritillary butterflies carrying Sdhd M allele are associated with the activated Hif signalling, reduced metabolic rate, and larger tracheal volume in larvae, and these associations contribute to less oxidative injury in flight muscle and better flight performance during intermittent flight in adults (Marden et al., 2021; Pekny et al., 2018). Nectar feeding hawkmoths use their antioxidant stores during migratory flight and through PPP to produce an antioxidant potential to recover from oxidative damage during rest (Levin et al., 2017). While, the utilization of PPP was reported to be positively correlated with the activation of Hif pathway (Sadiku and Walmsley, 2019; Tokuda et al., 2019). Therefore, at the molecular level, the Hif pathway likely plays a central role in regulating redox homeostasis during insect flight.”(Line 321-335)

Author Response

Reviewer #1 (Public Review):

The genome-editing strategies presented here represent a fantastic technology pipeline, comprehensively tested and precious to the cell biology field. While I am positive about the value of this contribution, I have three major requests that require some experimental work to make the study truly convincing and comprehensible.

1. The DExCon system allows re-expression of N-terminal tagged proteins from the endogenous locus and, in theory, should allow re-expression of all protein-coding splicing isoforms. This provides an advantage over generation of a KO cell line and subsequent tet-inducible rescue from a viral vector containing cDNA. This is undeniably an important technical advantage because it can potentially recapitulate the spectrum of functions of the locus. However, the authors do not provide direct evidence that the DExCon system does allow for re-expression of multiple splicing isoforms. One suggestion would be to identify the Rab11 splice variants expressed in A2780 cells and demonstrate that the relative abundance of these splice variants is not altered upon fluorescent-tagging and CMV-promotor-driven overexpression of Rab11 from the endogenous locus. This seems to me to be a crucial result to demonstrate the effectiveness of the method.

We thank for this great suggestion and have included new data to answer this as described in Figure 2 figure supplement 1 and the text on page 5 of the new manuscript.

1. The authors use a CMV-promotor to rescue of Rab11/25 gene expression. They convincingly show that it is possible to tune expression levels by FACS sorting. However, for most experiments, the authors use expression levels of Rab11a/b/Rab25 that are much higher than endogenous levels. Since high expression levels of Rab11a/b can affect its localization (transient expression Fig 2G), they should show that the Rab11a/b/Rab25 expression levels used do not alter localization and function. This could be tested simply by a transferrin recycling assay. To ensure that DExCon-Rab11/25 expression levels do not affect localization, the authors could use cells containing a knock-in of mCH-Rab11a on one allele and DExCon-mNG-Rab11a on the other allele and compare their localization.

We thank the reviewer for these important and interesting suggestions, which have been answered in a new Figure 7 and new Figure 5 figure supplement 2.

1. In Fig 6F, the effect of Rab11 on migration is tested using DExogron-mCH-R11b in a wound healing assay. Loss of R11b expression by DExogron-mCH-R11b reduced migration and this effect could be rescued by dox-induced expression of DExogron-mCH-R11b. However, IAA treatment failed to prevent this rescue as would have been expected. The authors hypothesize that this results from incomplete protein degradation under +dox +IAA conditions. In Fig 6K the authors solve this problem by removing dox when treating with IAA. The authors should repeat the experiment 6F under -dox +IAA conditions.

This is an important point and we have addressed this in a new Figure 6 figure supplement 2F and in the text on page 17.

Reviewer #2 (Public Review):

This is a very interesting, quite dense study that reports several new techniques of controlling cellular protein levels, as well as performing spatiotemporal image analysis. The strength of this study is the combination of various previously known approaches (like CRISPR knock-in, Degron, knock-sideways) to allow quite precise control of protein levels (by controlling degradation or expression), as well as imaging of endogenously tagged proteins. The ability to inactivate/reactivate proteins of interest is a huge achievement that will be very useful in many studies by this and other laboratories. Another big strength of this study is the fact that the authors took time to optimize and streamline these approaches making them much more user-friendly as compared to earlier versions of many of these approaches. The only very minor drawback of this manuscript is the fact that authors have chosen to perform proof-of-principal studies using Rab11 family of proteins (which is great) but in rather boring cell types. Rab11 family members are presumably involved in differentially regulating various aspects of cell polarity and recycling. Thus, it's not too surprising that authors did not see that many differences in rab11a, rab11b and rab25 functions since they used a single cargo (transferrin) and non-polarized cancer cells. However, I do realize that the main goal of this study is not to investigate Rab11 but rather to develop new techniques. Thus, this minor weakness should not stop this manuscript from being published.

We thank the Reviewer 2 for support and suggestions. A2780 ovarian cancer cells were selected as an established model of migration and invasion. They polarize in 3D matrix, so we can ask questions about the functions of Rab11 family members in these processes, and explore the full range of gene expression control (dox/degron/light). We anticipate our methods will be tractable to other cell types and look forward to ourselves and others using these in different biological contexts.

Author Response

Reviewer #1 (Public Review):

In the submitted manuscript, Sorrells and colleagues have characterized the shift in behavioral state female mosquitoes show after exposure to CO2. The authors have generated a mosquito line where CsChrimson is specifically expressed in the Gr3 expressing CO2 sensing neurons. Activation of these neurons through a 5s pulse of red light induced increased walking and probing behavior, which lasted 14 minutes.

All in all, a very interesting and well-executed study. The topic is important, and the successful use of optogenetics in Aedes is nice to see! The text is easy to follow, the figures all acceptable. The schematic drawings of the setups are, however, not the prettiest...nor that easy to interpret.

The submitted manuscript was accompanied by extensive reviewer comments from a previous submission. The main concern of those reviewers mostly centered around the novelty and broader importance of the work, issues which I believe are of no relevance here, or at least not to the same extent. The minor-ish technical concerns raised by the referees were all, in my view, addressed satisfactorily by the authors, and I see no reason for further experimentation. One point is perhaps worth repeating, namely whether the small size of the behavioral chambers could have influenced the results. Perhaps? It would clearly be interesting to see how the mosquitoes would behave in a larger arena. But that would be for another study.

We agree that carrying out these experiments in a larger arena will be important, and also agree that it is out of scope for the current study.

Reviewer #3 (Public Review):

In this work, the authors aimed to use new genetic tools to control the activity of olfactory neurons that sense carbon dioxide. These genetic tools specifically express Chrimson (a red-light activated channel rhodopsin) only in CO2-sensing neurons in the maxillary palp of the mosquito. Using this method, the authors could use red light to activate the CO2-sensing neurons as if these neurons had been stimulated by CO2. This 'fictive' CO2 activation allowed the authors to carefully and temporally control when these neurons would be activated in relation to other sensory cues such as heat or the presence of a blood-meal. CO2-sensing neurons could also now be activated in the absence of air flow. This simplifies the sensory stimuli presented to the mosquito so that behaviors induced by CO2 sensory neuron stimulation can be examined without the complicating factor of persistent mechanosensory stimulations. The behavioral experiments and new assays are clever and well designed, and the authors present robust evidence that fictive CO2-sensory neuron stimulation leads to a persistent host-seeking state in the female mosquito. This activated state lasts for many minutes and influences such behaviors as probing and blood-feeding. The genetic tools and data analyses methods introduced here will allow the authors and others in the field to make advances into investigating how activation of CO2 sensory neurons leads to potent changes in the nervous system of the mosquito. This work further pioneers the use of optogenetics to link neurons and behaviors in a mosquito system and paves the wave for similar studies in other non-model insects.

A weakness of the current work is the lack of direct neuronal activity measurements under the optogenetic stimulations. While the authors present strong evidence that their light stimulations can lead to behavior, it is not clear how these stimulations relate to activities induced by natural CO2 stimulations. These could be addressed by using their Gr3>Chrimson mosquitoes and performing single sensillum recordings from capitate peg sensilla (which house the CO2-sensing neurons), and examining how red light intensities change the activity of these neurons. This would ensure that the conditions used for fictive CO2 stimulations are a fair approximation of natural CO2 conditions.

Thank you for this suggestion. We agree that direct recordings of neural activity would give a direct relationship between light and CO2 concentration. We do not feel our conclusions depend on knowing this, but it is an important area for future investigation.

Alternatively, the authors could present evidence that their particular light stimulation parameters were chosen based on experimental behavioral experiments.

Thank you for this suggestion. We have added to the manuscript a light dose-response curve in Figure 1—figure supplement 1. The proportion of mosquitoes responding increases with light intensity. Notably, the duration of the response is relatively independent of the light intensity (when a detectable number of mosquitoes respond). We added the following sentences to the results section:

“The proportion of mosquitoes responding increased with light intensity (Figure 1—figure supplement 1B-D).”

“Varying the light intensity changed the proportion of mosquitoes responding but not the duration of the response (Figure 1—figure supplement 1).”

We also added additional details about the choice of intensity to the methods:

“The light intensity chosen was an intermediate intensity as determined by a light-behavior dose-response curve (Figure 1—figure supplement 1B-D) .”

“Red light stimuli were 627 nm at an intensity of 12 µW/mm2, chosen as an intermediate intensity that allowed the possibility of both an increase and decrease in the behavioral response.”

Author Response:

Reviewer #1:

This is a very interesting manuscript showing the contribution of intrinsic excitability in the formation of cortical neuronal ensembles. Using paired recordings from layer 2/3 neurons from the visual cortex, the authors show that co-activation of neurons by optogenetic or electrical stimuli leads to persistent synaptic potentiation preceded by a transient synaptic depression. The stimulation of neurons induces, in addition, persistent plasticity of intrinsic neuronal excitability that is associated with an enhancement of membrane resistance and a hyperpolarization of the spike threshold. The authors conclude that intrinsic plasticity allows to persistently maintain activated circuits according to an iceberg-like effect, and thus to generate a new neuronal ensemble.

This study is interesting as it integrates synaptic and intrinsic plasticity in the frame of the formation of cortical neuronal ensembles. However, it is unclear whether intrinsic plasticity occurs at pre- and post-synaptic neurons as illustrated in the final iceberg scheme. This has been shown by Ganguly et al., Nat Neurosci 2000 & Li et al., Neuron (2004). Nevertheless, this paper will have a strong impact in the field because of its conceptual clarity and the quality of the data.

We thank the reviewer for the comments and have incorporated the references to the previous work. Also, the synaptic depression and potentiation observed is consistent with the well-described exhaustion and recovery of the ready releasable pool of presynaptic neurotransmitter.

We have clarified our argument and modified the interpretation. In our model, we propose that after the optogenetic or electrical stimulation neurons shift to a more excitable state, therefore, neuronal responses would be amplified. Indeed, our findings show that stimulated pyramidal cells in layer 2/3 from visual cortex, whether they are presynaptic and postsynaptic, become more excitable. This happens even electrically stimulated single neurons. These changes confound the interpretation of potential synaptic plasticity, as EPSPs will be increased in size by the increased excitability.

We also added the follow clarification to the footnote in Figure 8:

" Neurons shift to a more excitable state after stimulation, so neuronal responses are amplified and the circuit now responds to an external input by activating a neuronal ensemble.", "All stimulated neurons become more excitable, ..."

Reviewer #2:

This is a potentially very impactful manuscript. The reason is that plasticity of membrane excitability (intrinsic plasticity) is largely understood as a mechanism that merely aids synaptic plasticity (in cortex: LTP) in its role in the formation of memory engrams and in learning. For example, one prominent hypothesis (Josselyn/Silva) suggests that intrinsic plasticity might enhance the probability for subsequent LTP induction and form/stabilize engrams in this way. A somewhat different view has been presented by Brunel/Hansel, who argue that under some conditions, intrinsic plasticity can integrate neurons into engrams, even when synaptic weights remain frozen. Importantly, the current work might provide evidence for this latter intrinsic theory of learning. However, in this in vitro study, the application of optogenetic or electric protocols to drive correlated neuronal activity in a defined ensemble does not only lead to strong changes in membrane excitability but also causes a biphasic change in synaptic weights. Below, I will make suggestions on how these synaptic and intrinsic effects could be further separated (this should be done if the goal of this study is to show that excitability changes alone can promote ensemble integration).

Major comments:

Line 79 f: It is not clear from this paragraph, which of the cited papers provide experimental details and which one presents the 'alternative hypothesis' (Titley et al., 2017; see above). This should be described more accurately to share the precise status quo of this research field with the audience.

We thank the reviewer for the suggestion. We have adjusted and incorporated the references that explain the alternative hypothesis and the segments corresponding to experimental details.

Figure 2: This is the critical point, and my experimental comments will focus on this: the authors show in this figure that both the optical stimulation as well as the electrical stimulation trigger synaptic plasticity, consisting of an immediate depression, followed after a pause by a potentiation. This potentiation is - in the case of electrical stimulation - significantly different from the baseline values (not significant for the opto group, but the number of recordings is quite low). It thus is conceivable that this effect contributes to the enhanced correlation of activity in the network that is shown in Figure 1.

This is a physiological observation, but attempts should be made to block/prevent the synaptic change and to assess whether enhanced correlation can persist with only excitability changes being available as a cellular mechanism. One way to do this is to perform recordings with physiological calcium and magnesium concentrations in the ACSF. As stated in the methods, the authors used 2mM Calcium and 1mM Magnesium. The physiological concentrations are about 1.2 mM Calcium and 1 mM Magnesium, thus creating an ionic milieu that is likely to be less permissive for LTP. The authors should try whether under these conditions the biphasic synaptic change is gone/reduced and the excitability change persists. If so, they can then test whether the enhanced activity correlation is still seen. Also, these recordings should be performed at physiological temperature.

If this is not successful (or as an alternative to start with), the authors might try pharmacological or genetic LTP blockade (e.g. targeting NMDA receptors or CaMKII) or use weaker stimulation protocols (intrinsic plasticity has a lower induction threshold than LTP).

Thanks for this important point. In order to separate synaptic effects, we measured synaptic activation of neighbor neurons (local circuit, Figure 4) from neurons without opsin expression. Synaptic inputs in non-expressing cells did not change: spontaneous EPSP amplitude or intrinsic excitability were similar before and after (Figure 4C). This can be explained because presynaptic activation did not increase firing probability in non- expressing cells. Neurons only became more excitable state when action potentials were evoked. This explains why we also observed increase in intrinsic excitability under electrically stimulated of single cells.

It would be very interesting to dissect whether synaptic changes were influenced by changes in excitability of presynaptic neuron. However, the number of unitary connections is already small and these connections are weak, and, due to the experimental difficulties, we had very few opportunities to test them. But still, according to our observation, changes in the synapses are temporally independent from intrinsic excitability. While we observed changes in membrane excitability after 3 min of stimulation, recovery from synaptic depression and partial potentiation took at least 20 min.

While the suggestion to repeat these experiments with altered ACSF is a good one, our plan is to explore this phenomenon in vivo. We have recently succeeded in obtaining high- quality whole-cell recordings in vivo and hope to directly reveal the role of increased excitability in the generation of ensembles in a physiological setting.

Author Response

Reviewer #1 (Public Review):

In this paper, the authors investigate the tuning of visual neurons in primate area MT to motion parallax signals and to binocular disparity. Among this class of neurons, some are tuned incongruently to depth using these two cues - that is, neurons can be tuned to more distant objects through motion parallax but closer ones through binocular disparity. Using carefully designed visual stimuli, the authors investigate the tuning properties of these neurons and how they relate to a psychophysical task in which a monkey distinguishes world-frame-moving objects from world-frame-stationary objects during self-motion of the monkey.

The experiments and stimuli are expertly designed and the analyses are careful.

We thank the reviewer for their supportive comments and for raising good questions.

My primary question, in reading this paper, is how much of the psychophysical effect can be attributed to these incongruently tuned neurons, rather than simply having a population of neurons with a relatively wide range of tunings. The analyses and simulations as presented don't back up the central claim as strongly as they could that it's these incongruent neurons in particular that facilitate these psychophysical percepts.

We appreciate the reviewer raising this issue, which has led to us digging into the data further.

Reviewer #3 (Public Review):

The authors investigated how the visual system solves the important and challenging problem of detecting independently moving objects while the observer undergoes self-motion. The paper focuses on a certain population of neurons in brain area MT ('opposite cells') that exhibit tuning to combinations of motion parallax (i.e. speed and direction) and binocular disparity that would generally not be compatible with the retinal motion created by stationary objects in the environment during self-motion. One example is tuning to fast speeds and far away depth through disparity. Such combinations of signals that preferentially activate opposite cells are more likely to arise from an independently moving object than self-motion relative to a stationary environment, assuming both sources of information are available. The main hypothesis tested in this paper is whether opposite cells could be used as a neural mechanism to detect independently moving objects. Consistent with their tuning properties, the authors found that opposite cells demonstrate stronger activation to moving objects than stationary objects. More generally, there was an inverse correlation between congruence in motion parallax+disparity tuning and the preference for moving objects. In support of the main hypothesis, an ROC analysis revealed that opposite cells were more effective in detecting moving from stationary objects through a difference in firing rate when the object was labeled as moving either according to the ground truth or monkey judgments. The estimates of a linear classifier trained on model fits of the MT data reinforced the authors' findings.

The investigated topic is very interesting and the work is a valuable contribution to the field. The paper is well written. The experiments were well-designed and controlled. The analyses were appropriate and support the hypothesis.

We thank the reviewer for their supportive comments.

The proposed local mechanism has a few limitations, mainly in its scope. First, the proposed local mechanism critically depends on the availability of binocular disparity. Humans are capable of detecting moving objects based on monocular optic flow, even when the moving object is aligned with the motion due to self-motion and varies based on speed alone (Royden & Moore, 2012). This scenario would not engage the proposed mechanism because disparity is not available and thus another mechanism like flow parsing would be needed. Second, while the proposed local mechanism may be more 'economical' (p. 3) than flow parsing, flow parsing addresses more phenomena than moving object detection. For example, flow parsing implicates the estimation of the world-relative direction (Warren & Rushton 2009; Fajen et al., 2013) and speed (Jörges & Harris, 2021) of independently moving objects. Layton & Fajen (2020) showed that a neural model of flow parsing can be used to detect moving objects in both monocular and binocular optic flow fields. The visual system may require a more 'complicated mechanism' (p. 28) to robustly perform the broader range of tasks, in situations where disparity may or may not be available and informative.

We have no disagreement with the reviewer regarding these broader issues. Indeed, in work still to be published, we have found effects of flow parsing in MT and we consider that to be a different mechanism. Indeed, the two are likely to be complementary, and we certainly did not mean to imply that our findings obviate the need for a flow parsing mechanism. We have made text revisions throughout the manuscript to clarify this, and have added text to the Discussion (pp. 17-18) to specifically address the points raised here.

Author Response

Reviewer #1 (Public Review):

Nandan et al. attempt to demonstrate how a phenomenology in the molecular signaling network inside a cell could translate to changes in the behavior of the cell and its ability to respond/adapt to changes in the environment over time and space. While this investigation is performed in the context of mammalian cells, the result holds significance for eukaryotic cells at large and demonstrates a mechanism by which cells may use transient memory states to respond robustly to complex environmental cues. To study such mechanisms, it is important to show how the cell may encode such transient memory, how this memory is generated from environmental cues, how it translates to cellular motion, and how it enables cells to have persistent directional motion in the case of transient disruptions in the signal while responding to significant and long-lasting disruptions. The authors attempt to answer all of these questions.

Strengths:<br /> The manuscript attempts to combine mathematical theory, mechano-chemical models, numerical simulations, and experimental evidence. Thus, the investigation spans diverse methods and spatio-temporal scales (from receptors to continuum mechanical models to whole-cell motion) to answer a unified question. The mathematical theory of dynamic states and bifurcation theory provides the basis for the generation of "ghost" states that can encode transient memory; the mechano-chemical models show how such dynamical states can be realized in the EGFR signaling network; the numerical simulations show both how cells can respond to environmental cues by generating polarised states, and by navigating complex environmental cues, and experiments provide evidence that this may be the case for epithelial cells in the presence of growth factors. The manuscript is well-structured with the main conclusions clearly identified and separated from each other in the different sections. The theoretical investigation is thorough and the main text provides an intuition as to what the authors are trying to convey, while the Methods reveal the calculations performed and the approximations made. The modeling and numerical simulations are detailed and provide a baseline expectation for the system in different parameter regimes. The experiments and the analysis extensively characterize the system. I commend the authors for having delved into so many methods to answer this problem, and the authors demonstrate significant knowledge of the different methods with many novel contributions.

Weaknesses:<br /> The key weakness of the results is in establishing clear distinctions between what would be expected (naively and based on results from other groups) from alternate explanations, and what is realized in the experimental results that support the hypothesis put forward by the authors. For example, the authors quote a relatively long time scale of persistence of polarisation, but it is unclear if this is longer than is expected from slow dephosphorylation to provide evidence for the existence of the "ghost" state from the saddle-node bifurcation. Further, key experimental results regarding the persistence of motion following gradient washout seem to differ from the authors' own predictions from simulations.<br /> There are several other models that attempt to describe eukaryotic chemotactic motion that persists despite brief disruptions and is able to adapt to changes in the environment over longer timescales. In my opinion, the main strength of the paper does not lie in providing another such model, but in providing a mechanistic understanding that bridges several scales. However, this places the burden on the authors to justify the link between the different scales.<br /> This is an ambitious manuscript and the authors are clearly very bold for attempting such a comprehensive treatment of such a complex system. The authors provide an excellent framework to understand mammalian cellular chemotaxis on multiple scales and attempt to justify the framework using several experiments and extensive analysis. However, they require further analysis and characterization to demonstrate that their experimental results provide the necessary justification for their conclusions as opposed to alternate possibilities.

We thank the referee for his/her in-depth suggestions and valuable comments how to improve the manuscript, that we implemented in details in the amended version. We have especially focused on providing the necessary justification for working memory emerging from a “ghost” signaling state as opposed to slow dephosphorylation mechanism. For this, we have fitted the single-cell EGFRp temporal profiles after gradient wash-out with and without Lapatnib inhibition, with an inverse sigmoid function and quantified the respective half-life and the Hill coefficient. The analysis included in the new Figure 2 – figure supplement 2 shows that under Lapatinib treatment which inhibits the kinase activity of the receptor and thereby the dynamics of the system is guided by the dephosphorylating activity of the phosphatases, the system relaxes to the basal state in an almost exponential process (half-life ~10min., Hill coefficient ~1.3). In contrast, under normal conditions EGFR phosphorylation relaxes to the basal state in ~30min, corroborating that the system remains trapped in the “ghost” state. Moreover, the transition from the memory to the basal state is rapid, as reflected in an estimated Hill coefficient ~ 3. Additionally, we also discuss how the identified slow-time scale that emerges from the “ghost” state serves as a possible mechanistic link between the rapid phosphorylation/de-phosphorylation events and the ~40min of memory in cell shape polarization/directional cell migration after growth factor removal.

Moroever, we include additional quantification of memory in single-cell directional motility in the cases with and without EGFR inhibitor (Figure 3 – figure supplement 3), and relate these results to previously proposed mechanisms on memory in directional migration from cytoskeletal asymmetries, but also highlight the importance of memory in polarized receptor signaling as a necessary means to couple cellular processes that occur on different time-scales. We have further expanded the manuscript by providing theoretical predictions how the organization at criticality uniquely enables resolving simultaneous signals. We address the referee’s comments as outlined below:

Reviewer #2 (Public Review):

Nandan, Das et al. set out to study the mechanism by which single cells are able to follow extracellular signals in variable environments generate persistent directional migration in the presence of changing chemoattractant fields. Importantly, cells are able to (1) maintain the orientation acquired during the initial signal despite disruptions or noise while still (2) adapting migrational direction in response to newly-encountered signals. Previous models have accounted for either of these properties, but not both simultaneously. To reconcile these observations, this work proposes an underlying mechanism in which cells utilize a form of working memory.

The authors present a dynamical systems framework in which the presence of dynamical 'ghosts' in an underlying signaling network allow the cell to retain a memory of previously encountered signals. These are generated as follows: a pitchfork bifurcation confers a symmetry-breaking transition from a non-polarised to polarised signaling state/ direction-oriented cell shape. After a subsequent saddle-node bifurcation, a 'ghost' of the stable attractor emerges. This 'ghost' state is metastable, however, which is what allows cells to integrate new signals as well as to adapt their direction of migration.

The authors demonstrate these dynamics in the Epidermal Growth Factor Receptor (EGFR) signaling network. This pathway is central in many embryonic and adult processes conserved in most animal groups, making it an ideal choice to characterise a phenomenon observed in such a diverse range of cells. The authors couple a mechanical model of the cell with the biochemical signaling model for EGFR, which nicely allows them to thoroughly simulate cellular deformations that they predict will occur during polarization and motility.

Key features of the model are well-supported by empirical data from experiments: (1) quantitative live-cell imaging of polarised EGFR signaling shows the existence of a distinct polarised 'ghost' state after removal of extracellular signals and (2) motility experiments confirm the manifestation of this memory in allowing for persistent cell migration upon loss of a signal. In an extension of the latter experiment, the authors also show that cells displaying this working memory are still able to respond to changes in the chemoattractant field as necessary.

The experiments using Lapatinib to disrupt the EGFR dynamics are less convincing. The authors show that subjecting cells to this inhibitor results in the absence of memory and removes the ability of cells to maintain their orientation after the gradient was disrupted. Clarification of which aspect(s) of the EGFR network within the context of the model are precisely disrupted by Lapatinib would be helpful in strengthening the authors' claims here that it is the mechanism of working memory and not other features of the EGFR network, that is responsible for the results shown.

We thank the referee for the detailed comments and suggestions that helped us to improve the manuscript. In the amended version of the manuscript, we describe that Lapatinib hinders EGFR kinase activity, thus in the model, this will mainly affect the autocatalytic rate constant. We have performed numerical simulations where the autocatalytic rate constant is decreased after gradient removal, and show that the EGFRp temporal profile shows a slow decay after gradient removal, whereas the state-space trajectory directly transits from the polarized to the basal state without intermidate state-space trapping, thereby qualitatively resembling the experimental observations under Lapatinib treatment (compare Figure 2 – figure supplement 2C, D with Figure 2G in the amended version of the manuscript).

Reviewer #3 (Public Review):

Cell navigation in chemoattractant fields is important to many physiological processes, including in development and immunity. However, the mechanisms by which cells break symmetry to navigate up concentration gradients, while also adapting to new gradient directions, remain unclear. In this study, the authors propose a new theoretical model for this process: cells are poised near a subcritical pitchfork bifurcation, which allows them to simultaneously maintain the memory of a polarized state over intermediate timescales and respond to new cues. They show analytically that a model of EGFR phosphorylation dynamics has a subcritical pitchfork bifurcation, and use simulations of in silico cells to demonstrate both memory and adaptability in this system. They further measure EGFR phosphorylation profiles, as well as migration tracks under external gradients, in real cells.

This work contributes an interesting new theoretical framework, bolstered by substantial analysis and simulations, as well as valuable measurements of cell behavior and polarization. Both the modeling and the measurements are careful and thorough, and each represents a substantial contribution to decoding the complex problem of cell navigation. The measurements support and quantify the phenomenon of directional memory. The main weakness is that it is not clear that they also support the mechanism proposed by the model.

Theoretical framework

One of the main strengths of this work is the thorough theoretical analysis of a model of symmetry breaking in EGFR phosphorylation. The authors perform linear stability analysis and a weakly nonlinear amplitude equation analysis to characterize the transition. Additionally, they convincingly demonstrate in simulations that this model can generate robust polarization, with memory over intermediate timescales and responsiveness to new gradient directions. However, the relationship between the full dynamical system and the bifurcation diagrams shown in Figure 1A and Figure 1-Figure Supplement 1B is not clear. In particular, there is an implicit reduction from an infinite dimensional system (continuous in space) to an ODE system.<br /> From Methods 5.15, it appears that this was accomplished by approximating the continuous cell perimeter as a diffusively-coupled two-component system, representing the left and right halves of the cell (Methods 5.15 Equation 18 to Equation 19). However, this is not stated explicitly in the methods, and not at all in the main text, making the argument difficult to follow. Additionally, the main text and methods describe the emergence of an unstable odd spatial eigenmode as the key requirement for the pitchfork bifurcation. It is not clear why it is sufficient to show this emergence in the two-component system.

We thank the referee for the detailed and insightful comments which we implemented in details in the amended version of the manuscript. Indeed, as the referee commented, we have assumed a simplified one-dimensional geometry composed of two compartments (front and back), resembling a projection of the membrane along the main diagonal of the cell. The standard approach of modeling the diffusion along the membrane in this case is simple exchange of the diffusing components. The one-dimensional projection, as demonstrated in the analysis, preserves all of the main features of the PDE model. The numerical bifurcation analysis was only performed for comparative purposes. In the amended version of the manuscript we thus extend the description of this simplification, as well as the purpose of its implementation. Additionally, one of the reasons for developing the theoretical network for us was to provide a method how subcritical PB can be identified in general in PDE models.

The schematic of the bifurcation in Figure 1A / now in Figure 1 – figure supplement 1A, as well as the numerical bifurcation analysis of the EGFR model in Figure 1-Supplement 1C represent a subcritical pitchfork bifurcation, but the alignment of IHSS branches is slightly different in the EGFR model. This however has no influence on the full dynamics of the system, or the proposed hypothesis. Moreover, in order to explain in details the dynamical transitions - how the unfolding of the PB results in robust polarization and how the organization at criticality enables temporal memory in polarization to be maintained, we included a revised schematic in Figure1 – figure supplement 1A that shows the signal induced transitions that were previously depicted in a compact way in Figure1A, and included respective description in Methods, Section 5.15. The corresponding transitions for the one-dimensional projection EGFR model is also included in the detailed response (Figure 2) for comparison.

Relationship between the measurements and model

The second main strength of this work is the contribution of controlled measurements of cell motility, polarization, and phosphorylated EGFR profiles. The measurements of cell migration presented here support the claim that the cells have a memory of past gradients. Additionally, the authors contribute very nice quantifications of the memory timescale. The Lapatinib experiments also support the claim that this memory is related to EGFR activity. However, there are a number of ways in which the real cells appear not to behave like the in silico cells. Polarization in phosphorylated EGFR is present only some of the time in the data, and if present, appears to be weak and/or variable, in magnitude and direction (phosphorylated EGFR profiles, figure 2C, Figure 2-Figure supplement 1D, E). Even for the subset of cells that display polarized EGFR phosphorylation profiles, the average profile is shown after aligning to the peak for each cell (Figure 2-Figure Supplement 1C), so it is not clear that they polarize in the direction of the gradient.

We thank the referee for these comments which we used as a basis to improve the presentation of the results in the amended version of the manuscript. In order to demonstrate that cells polarize in the direction of the maximal EGF concentration, we have used the EGF647 intensity to quantify the growth factor distribution around each cell and calculated the angle between the maximum of the EGF647 distribution and projection of EGFRp spatial distribution (summarized in Figure 2 – figure supplement 1F and Methods). In brief, for quantification of EGF647 distribution outside each cell, the cell masks were extended by 23 pixels, and the outer rim of 15 pixels was used for the quantification. A radial histogram of the obtained angles confirms that the polarization of EGFRp is in the direction of maximal EGF647, with the variability arising from the positioning of the cells within the gradient chamber. That cells polarize in direction of the gradient can be indirectly inferred also from the migration data (Fig. 3C), where we have estimated the projection of the relative displacement angles with respect to the gradient direction. The cos 𝜃 values during and for ~50min after gradient removal are maintained around 1 (cells migrate in direction of the gradient), before re-setting to 0, which is characteristic for the no-stimulus case.

The length of the memory in EGFRp polarization is indeed variable in single cells, being on average ~40-50min. The length of the memory is directly related to the total EGFR concentration on the plasma membrane – the closer EGFRt is to the value for which the SNPB is exhibited, the longer the duration of the memory is, and in theory

𝑀𝑒𝑚𝑜𝑟𝑦 𝑑𝑢𝑟𝑎𝑡𝑖𝑜𝑛 ∝ 𝐸𝐺𝐹𝑅𝑡1/2. From the experimental measurments we have indeed observed a correlation between these two quantities, which we include here for the referee’s perusal (Figure 1). However, direct fitting to the experimental data with the given dependency could not be performed because of the following reasons: In general, the fitting function is 𝑓(𝐸𝐺𝐹𝑅𝑇) = 𝑐 ∗ (𝑐𝐸𝐺𝐹𝑅𝑇,𝑆𝑁−𝐸𝐺𝐹𝑅𝑇)n, where c= const. and 𝑐𝐸𝐺𝐹𝑅𝑇,𝑆𝑁 is the total EGFR concentration at the plasma membrane that marks the position of the SNPB. This value however cannot be identified with certainty from the experiments. Thus, we have chosen a fixed value based on the spread of the data and in this case, the fitting resulted to n = 0.49, which approximates well the theoretical value. However, since one of the parameters must be arbitrarily chose, we refrain from presenting the fit.

*Figure 1: Correlation between single-cell transient memory duration and plasma membrane abundance of 𝐸𝐺𝐹𝑅𝑚𝐶𝑖𝑡𝑟𝑖𝑛𝑒. *

The real cells also appear to track the gradient far less reliably than the in silico cells (e.g. Figure 4B vs. 4C). Thus the measurements demonstrate and quantify the phenomenon of directional memory, but it is not clear that they support the mechanism proposed by the model, i.e. a symmetry-breaking transition in phosphorylated EGFR.

We would like to emphasize here that the symmetry-breaking transition via a subcritical pitchfork bifurcation gives rise to robust polarization in the direction of the growth factor signal, whereas critical organization at the SNPB – temporal memory of the polarized state, as well as capability for integration of signals that change both over time and space. The analytical as well as the numerical analysis of the experimentally identified EGFR network verifies that this network exhibits a subcritical PB. In the amended version of the manuscript, we have also included quantification of the directionality of polarization (Figure 2 – figure supplement 1F).

We would like to note however, that the difference between the simulations and the experiments in Figure 4 lies in the fact that the directional migration in the physical model of the cell, due to the complexity of connecting the signaling with the physical model, is realized as a ballistic movement, whereas experimentally we have identified that cells perform persistent biased random walk (Figure 3D). In the amended version of the manuscript we have discussed these differences in relation to Fig.4.

Moreover, in the experiments, the EGF647 gradient is established from the top of the microfluidic chamber, and therefore there will be variability due to the position of cells within the chamber, the disruption of the gradient due to the presence of neighboring cells etc. The single cell trajectories (several examples shown in Figure 4 – figure supplement 1F) and the quantification of the relative displacement angles (Figure 4D,E) however clearly depict that cells migrate in the gradient direction and rapidly adapt to the changes in the external cues.

Additionally, in the authors' model, the features of memory and adaptability in cell navigation depend on the system being poised near a critical point. Thus, in silico, the sensing system 'breaks' when the system parameters are moved away from this point. In particular, cells with increased receptor concentration on their surface cannot adapt to new gradient directions (Section 1, final paragraph; Figure 1-Figure Supplement 1E-G). Based on this, the authors' theoretical framework makes a nonintuitive prediction: overexpression of the surface receptor EGFR in real cells should render them insensitive to changes in the concentration gradient. The fact that the model suggests a surprising, testable prediction is a strength of the framework. A weakness is that the consistency of this prediction with empirical data is not discussed (though the authors note similarities between this regime and unrealistic features of previous models).

The organization at criticality is indeed dependent on the total concentration of receptors at the plasma membrane. The trafficking of the epidermal growth factor receptors has been previously characterized in details and demonstrated that the ligandless receptors continuously recycle to the plasma membrane, whereas the ligandbound receptors are unidirectionally removed and are trafficked to the lysosome where they await degradation [5]. Thus, how quickly the system will move away from criticality depends directly on the dose and the duration of the EGF stimulus, as this is directly proportional to the fraction of liganded receptors; whereas re-setting of the system at criticality will be afterwards depended on the time scale for biosynthesis of new receptors [17].<br /> Overexpression of EGFR receptors will cause the system to display either permanent polarization (organization in the stable IHSS state) or uniform activation (high HSS branch). We have tested numerically the features of the system when it displays permanent memory (Figure 4 – figure supplement 1C,D) and demonstrated that in this case, cells are not able to resolve signals from opposite directions and therefore migration will be halted. Additionally we also now tested numerically the capability of the cells for resolving simultaneous signals with different amplitudes from opposite direction, and demonstrate that permanent memory as resulting from receptor organization hinders the cells in this comparison task, in contrast to organization at criticality (Figure 4 – figure supplement 2). In the amended version of the manuscript we included a discussion of these points raised by the referee and hope that this allows for more clear presentation of our findings and their implications.

Author Response

Reviewer #2 (Public Review):

Studying the olfactory encoding strategies of moths using ecologically relevant odors collected from the actual habitat is remarkably ambitious. The manuscript is well written and the design of the experiment is clear.

We thank the reviewer for this positive evaluation of our study.

The authors collected the nocturnal emission of 16 plant species and systematically analyzed the constitution of the headspace of these plants. Then, they used GC-EAD to identify the active compounds and found 77 EAD-active ones in total. Subsequently, they used in vivo calcium imaging to study the representation of these active compounds in antennal lobes. A weakness is the absence of behavioral data.

The plants that are of ecological relevance for M. sexta as nectar sources and oviposition sites are known and well documented both from observations in the field and behavioral experiments in the lab (see references in the introduction of our manuscript). We use headspace of these plants with known ecological meaning and of many other plants present in the direct neighborhood to test how female hawkmoths perceive relevant and irrelevant plant bouquets at the antenna and how these headspaces are spatially coded in the antennal lobe. It is, therefore, difficult to understand in which respect the unspecified ‘behavioral data’ the reviewer asked for might add further information to our study.

Author Response

*Reviewer #2 (Public Review):

This manuscript describes studies on the structural determinants of activation for the adhesion GPCR (aGPCR) GPR116 both in vitro and in vivo. The authors define key residues for activation on the receptors' N-terminus (the "tethered agonist") and the extracellular loops. Thus, the studies provide novel insights into the structural determinants of GPR116 activation. However, some interpretational issues (detailed below) complicate some of the authors' conclusions. Specific comments are as follows:

1. Results section, first paragraph, last sentence: The authors write, "These results taken together indicate that the H991A mutant is capable of proper trafficking to the membrane, is able to response to exogenous peptide, but is unable to be cleaved and activated by endogenous ligands in vivo." The last part of this sentence represents an over-interpretation, as the data shown in Figure 1 do NOT show that the non-cleavable receptor is unable to be activated by endogenous ligands in vivo. It is entirely conceivable that a non-cleavable aGPCR could still be activated by endogenous adhesive ligands if those ligands were to change the position of the tethered agonist in manner that alters receptor signaling activity.

Thank you for highlighting this misleading wording. We rephrased the sentence to read as follows: Taken together, these results demonstrate that the H991 residue within the GAIN domain is critical for cleavage of GPR116 into NTF and CTF fragments but dispensable for trafficking of the receptor to the plasma membrane and response to exogenous peptide activation in vitro.

1. The data shown in Fig. 1B (surface expression of non-cleavable H991A mutant) need to be quantified in some way in order to be interpretable.

As the H991A construct does not contain a cell surface epitope tag, it is difficult to directly quantitate surface expression of this protein. The data in transiently transfected HEK293 cells (Figure 1, panels C and D) and in primary alveolar epithelial cells (Figure 2, panels C&D) clearly demonstrate that the H991A mutant is activated to comparable levels as the wild-type receptor in response to exogenous peptide stimulation. In light of these functional data, we are confident that the surface expression of H991A is comparable to that of the WT receptor in vitro and in vivo.

1. Results section, second paragraph, penultimate sentence: The authors write, "These data demonstrate that while the non-cleavable receptor is fully activated in vitro by exogenous peptides corresponding to the tethered agonist sequence, cleavage of the receptor and unmasking of the tethered agonist sequence is critical for GPR116 activation in vivo." However, the non-cleavable GPR116 mutant actually has two key differences from WT: i) lack of full liberation of the tethered agonist sequence, and ii) lack of liberation of a free NTF, which might dissociate from the CTF and have important in vivo physiological actions on its own. Isn't it conceivable that the lack of a freely mobile NTF contributes to the similarity in lung phenotype between the non-cleavable knock-in mutant and the GPR116 knockout? Based on the data shown in Figure 2, how can the authors claim these data demonstrate that unmasking of the tethered agonist is critical for GPR116 activation? The data could equally be interpreted as showing that liberation of a free NTF is critical for the physiological effects of GPR116 in vivo.

We thank the reviewer for this comment and, in retrospect, agree that we may have overstated the interpretation of our results for the H991A transgenic mouse. While it is possible that the free NTF may be responsible for the physiological effects of GPR116 in vivo, in light of recently published data by Mitgau et al. (BioRxiv https://doi.org/10.1101/2021.09.13.460127), we believe this not to be the case for the following reasons. First, the H991A and WT receptors are activated to an identical level by exogenous peptide stimulation in a transformed cell line (HEK293) and in primary alveolar type 2 epithelial cells (Figures 1 and 2), irrespective of if the NTF is free floating in solution in the context of the WT receptor. These data would argue against a role of the free NTF in receptor activity. Second, in a recent publication by Mitgau et al., the authors clearly demonstrate that activation of GPR126, an adhesion GPCR that is also cleaved at the GPS and activated by exogenous peptides corresponding to the tethered agonist, by antibodies that bind and crosslink the NTF is completely dependent on cleavage at the GPS. They further demonstrate that antibody-mediated activation does not lead to liberation of the NTF from the CTF. Rather, they postulate that proper GPS processing, as occurs for the WT receptor, leads to a favorable protein confirmation of the tethered agonist, which is indispensable for GPR126 activity. Given these results, we postulate that cleavage at the GPS of WT GPR116 results in a conformation that is critical for the tethered agonist sequence to reach and bind the ECLs, resulting in activation of the receptor, similar to that observed with GPR126. We have edited our interpretation of these data in the revised manuscript.

1. Figure 3: If the authors' hypothesis is that the tethered agonist must be liberated in order to allow activation of GPR116, then why do ANY of the Flag-tagged mutant constructs exhibit constitutive signaling activity? Doesn't the N-terminal Flag tag prevent the tethered agonist from being exposed? How can these data be reconciled with the authors' model?

It is unlikely that the 27 amino acid N-terminal FLAG epitope tag envelopes the tethered agonistic peptide to the same extent as the tertiary structure of the carboxy terminus of the NTF (based on published structures for other aGPCRs). Additionally, we provided data demonstrating that an untagged version of the CTF protein is activated to a similar extent at FLAG-tagged CTF in response to activating peptides (Supplemental Figure 2A). Based on our data from mutagenesis experiments and modeling of GPR116 with the agonist, we do not believe the tethered agonist dives deeply within the binding pocket but rather interacts with critical amino acids at the surface of ECL2 to induce conformational changes to the receptor and downstream activation.

1. The data shown in Fig. 3D are lacking statistical comparisons, so it is not possible to tell whether any of the differences between the mutants are statistically significant.

Statistical analyses for data in this panel have been added

1. The data shown in Fig. 4D (surface expression of the ECL mutants) need to be quantified in some way.

We have added additional data to this figure (Fig4 F-G-H) using the V5-tagged mFL construct as control. As the tag is C-terminal, we quantified by flow cytometry the total expression using an anti-V5 antibody, to complement to immunocytochemistry data showing membrane expression.

1. In interpreting the results of the ECL mutations on GPR116 signaling activity, it is unclear why the authors so explicitly propose that these data demonstrate that the tethered agonist must be interacting with ECL2. Isn't it possible that ECL2 mutants with impaired receptor signaling activity simply lock the receptor in an inactive state? In this way, the effects of the ECL2 mutations could be explained without invoking a physical interaction between the putative tethered agonist and ECL2.

Yes, this interpretation is also possible. We have rephrased the Results and Discussion sections accordingly to reflect this possibility.

Author Response

Reviewer #1 (Public Review):

The manuscript contrasts the role of non-specific PAG neurons to PAG cck+ neurons in threat perception using a variety of low and high threat tasks including open field, elevated plus maze, a latency to enter a dark box assay, real-time place preference task, live predatory exposure, fear conditioning. cck neuronal activity in the PAG was examined used gain and loss of function approaches using optogenetics, chemogenetics and fiber photometry. The data show that cck PAG neurons have a dissociable function to the global PAG neuronal response in threatening situations with cck neurons consistently enhancing flight to safety. Specifically, activation of cck PAG neurons decreased time spend in the center of an open field, increased speed and number of corner entries, reduced latency to enter a dark box, reduced time in a chamber paired with cck-activation, reduced time spend in the open arms in the elevated plus maze, increasing pupil dilation, enhance avoidance of a live predator, and cck PAG inhibition having the opposite effect to that of activation. Fiber photometry data showed a ramping up upon initiation to escape a live predator, as well as a sustained activity post escape that increased with greater distance from the predator.

The experiments are well executed, the data are clear and convincing. The approach is thorough, and appropriate. The insight is significant and of value beyond the study of threat perception.

No major weaknesses were detected other than the lack of statistical reporting. The conclusion regarding a lack of role for PAG cck neurons in fear learning should be dampened as this would require a more thorough investigation.

We are pleased that the Reviewer finds that our data are “clear”, “convincing” and “appropriate”, and we are heartened that the Reviewer believes the insight provided by this manuscript is “significant.” We apologize for the oversight in statistical reporting. We have now largely expanded our statistical reporting to include complete descriptive statistics throughout the main text and figure legends, including the statistical test used, n’s for each group, and exact p-values. We agree with the Reviewer’s suggestion regarding fear learning and have dampened our interpretation of the involvement of PAG-cck neurons in fear learning in the main text.

Reviewer #2 (Public Review):

This manuscript investigates the role of cck-releasing neurons in ventral regions of the PAG in mediating defensive responses. While prior work in the field has identified columnar organization of mediating defensive responding (i.e., ventral versus dorsal PAG are implicated in freezing and flight, respectively), this work uses several approaches to parse the role of specific cell ensembles in defensive responding.

Through a series of expertly designed studies, the authors have provided compelling evidence that while there are many studies evidencing a role for l/vlPAG in freezing behavior, there may be a more nuanced role for l/vlPAG when considering cell-specific populations. Specifically, cck neurons in l/vlPAG may drive organized escape/ avoidance of threat. Further, activation patterns and behaviors resulting from l/vlPAG manipulation seem to oppose those observed when interrogating l/vlPAG in a non cell type specific manner. These findings underscore the importance of not only neuroanatomical designation of function, but also molecular identification to fully understand the role of defensive response systems.

The identification of a sparse population of cck cells that seem to oppose canonical role for ventral regions of PAG in defensive responding will be of importance to the field. However, there are some caveats that could be made more clear. For example, if l/vlPAG cck neurons initiate escape to safety, it is not fully clear why these cells exhibit greater activity in safe versus threatening locations. One might expect greater activation upon initial escape if this population is the driving force behind the behavior. This raises the possibility that l/vlPAG cck cells coordinate behavioral responses with another population of cells, such as one in the more dorsal regions described by many others to be important for escape and defensive flight. Addressing this would increase the value of the findings presented.

We greatly appreciate the Reviewer’s statement that our “expertly designed studies” “underscore the importance of …. molecular identification to fully understand the role of defensive response systems.”

We believe the Reviewer brings attention to an excellent point regarding why cck+ cells exhibit greater activity in safer locations despite our activation studies driving escape to safety. We interpret these findings in the context of threat avoidance – optogenetic activation induced avoidance of open spaces in low-threat situations and avoidance of a live predator in a high-threat situation. Similarly, we observed enhanced endogenous activity when mice engaged in avoidance from a predator, either by occupying a safe zone most distal from the predator, or actively fleeing from the predator.

The Reviewer is correct to observe that if the population is the driving force behind the behavior, then greater activation should be largely upon the initial portion of escapes. However, we point out that the “safe” zone in the rat assay was not danger-free but was only safer in relation to the threat zone. Even in the safe zone, it is likely that the mouse, in an avoidance state, was motivated to further increase distance from the rat, and this motivation may be related to the increased cck+ activity seen away from the rat.

As this is an extremely important point, we write about this at length in the new Discussion section, ‘l/vlPAG cck cell activity may drive the threat avoidance behavioral state.’

Reviewer #3 (Public Review):

A major role of the PAG in mediating defensive reactions is supported by early microinjection and lesion studies as well as more recent circuit neuroscience studies. By showing that cck neuron activation promoted flight to a burrow, and a global preference for lower threat areas on one hand, and that their activity was correlated with distance to threat on the other, the present study adds to our knowledge of functionally specific circuit elements within the PAG that control different defensive behaviors. Importantly, some of the findings appear contradictory at first glance, and would need to be reconciled via further analyses and/or conceptualization.

The authors systematically performed similar experiments not only with a focus on the l/vlPAG cck neurons, but also on the global neuronal population of the same area. This second aspect mainly recapitulates earlier findings, but most importantly, allows for a direct comparison between a molecularly defined population and the overall neuronal population. This critically highlights that although canonical delineations of the anatomical subregions were adopted based on some neurochemical markers, they do not present an absolute functional and molecular homogeneity, and therefore emphasizes the importance of using specific subpopulations to draw finer conclusions.

The study employs several behavioral paradigms, which are, in the case of the rat exposure test, highly relevant from an ethological point of view, even though conceptual flaws might be present in some aspects of the others.

The experiments, incorporating state-of-the-are techniques are conducted rigorously, and the results are described thoroughly and without overreach. Some analytical approaches need to be described better. Some general points feel like they are not interpreted and conceptualized consequentially enough, including the seemingly contradictory findings. A global picture uniting the different results is missing, which leaves some parts disconnected, yet the data might offer enough elements to develop on that side. The results are well discussed on a higher level and integrated with fitting references for the different aspects of the study, however, the discussion of individual results should be enhanced.

The main weakness of the study is that the perturbational and observational approaches are not easily reconciled. While this is a common phenomenon in circuit research, it hampers a conclusive attribution of the functional role of PAG cck cells and is in contrast to the study's major goal. This discrepancy needs to be resolved both, experimentally and conceptually.

We are pleased that the Reviewer highlights that our “systematically performed” experimentation allows for a “direct comparison between a molecularly defined population and the overall neuronal population.”

We agree with the Reviewer’s assessment that the manuscript would benefit from a “global picture uniting the different results” particularly in the context of the “perturbational and observational” results, and we thankfully use this opportunity to strengthen our manuscript.

To address this need, we have incorporated throughout the main text and in a pointed manner in the Discussion section a global picture that reconciles our perturbational and observational results. We highlight that our results fit with the interpretation that PAG cck+ cells are driving and reflecting threat avoidance states. In this state mice stay away from threat and initiate evasive escape from threat. We show in our perturbational studies that cck+ activity can bidirectionally control threat avoidance measures. In accordance, our observational studies of endogenous cck+ activity show increased activity when mice are engaged in measures of threat avoidance, both by escaping from threat and occupying the zone furthest from threat.

Author Response

Reviewer #1 (Public Review):

The weakness of the paper is that the analysis is based on a self-report survey which may not be an accurate method of determining cancer screening rates due to recall.

Claim data or medical records may provide a more reliable "gold standard" than self-reports

We agree. Many data sources, including prospective collection, electronic health record downloads, survey sources, and payment-related databases, can tally screenings per patient. The first sentence of our limitations section states this.

It is a cross-sectional self-report survey whose responses are not equivalent to validated medical records or claims data (St Clair 2017 (36)).

We also provide evidence of the accuracy of self-report in the subsequent two sentences of the limitations section, which we addressed in the above comment (Anderson 2019).

In general, surveys are critical for providing rich information about the individuals and for observations regarding population health and it could help to better understand some measures. However, it is necessary to discuss better that this kind of information may be biased.

We agree with the reviewer. BRFSS has been extensively studied by the CDC, as seen in Anderson 2019, definitively showing that those who are screened DO accurately report this in a self-report survey. We have stated this in the limitations section of the discussion section.

Those who do not screen will inaccurately report by about 50% that they did screen.

For future analysis, it could be useful to perform an analysis where self-report data and claim report information serve as a source of information together, it means to perform an analysis to compare self-reported information with objectively recorded participation in colorectal and cervical cancer screening in the national screening programme in the United States. It will allow to verify whether self-reported ever uptake corresponds with recorded ever uptake among survey respondents

We agree that comparing self-report to claims data would be interesting. We point out to the reviewer that both datasets are samplings of the whole population, not the entire population. Claims data is subject to significant miscoding errors in the clinic that make it not as reliable as would be desired. The US does not have a population registry as other countries do. Our BRFSS is the best we have, and it drives our health programs and expenditures for public health.

Reviewer #3 (Public Review):

Weaknesses:

1) The CRC testing stated is not the 'routine' recommendations.

Our statement: "CRC screening is defined as using a home kit for blood stool tests including fecal occult blood test (FOBT) or fecal immunochemical test (FIT) or office-based procedures including sigmoidoscopy or colonoscopy" accurately represents the current routine screening recommendations in the US.

Also, since it is self-reported, a patient might have under-reported obtaining a Pap or HPV test when she only received a speculum exam

We agree with you. We address this in the limitations section.

2) Significant difference between those that were identified and those included in eligibility suggesting elements of selection bias and potential generalizability of respondents to the population

Please see the supplemental figure where we enumerate the exclusion reasons.

We appreciate the reviewer’s concern about the bias of non-responders. Because of this remark, we repeated our analyses, using propensity scoring of missing information to create missingness weights. Combining the survey weight with the missingness weights allowed re-calculations of all analyses. The new results are presented in Tables 1-4. The adjustment did not change the interpretation of any analysis, but slightly changed the aOR and 95% confidence limits. Our conclusions remain strong.

3) Data does not take into account the payer mix and potential for health insurance limitations of access

We appreciate the reviewer's concern. This distribution of data is not available in BRFSS. 90% of the BRFSS respondents reported some form of insurance without identifying private vs. public sources. Our past work shows that the largest stratifier is among those with no insurance vs. any other type (Harper DM, Plegue M, Harmes KM, Jimbo M, SheinfeldGorin S. Three large scale surveys highlight the complexity of cervical cancer under-screening among women 45-65years of age in the United States. Prev Med. 2020 Jan;130:105880. doi: 10.1016/j.ypmed.2019.105880. Epub 2019 Nov 1. PMID: 31678587; PMCID: PMC8088237.). In addition, after the ACA passed, there are no longer any copays for any cancer screening test for any person of any age in the US.

Author Response

Reviewer #1 (Public Review):

Weaknesses:

• The causal relationship between ARSB treatment and neurite outgrowth phenomena the authors observe after MI are weak. Specifically, the co-culture assay does not seem to fully replicate the nerve/myocardial interface after MI. It is unclear why NGF needed to be added to the media to induce neurite outgrowth when it is established that multiple neurotrophic and neurotropic factors are already expressed in the myocardium after MI (Habecker et al., J Physiol 594.14 (2016) pp 3853-3875). By visual estimation, it also appears difficult to control for spatial distance between the sympathetic ganglion and myocardial explants in this culture system, a problem which may significantly affect the diffusion of axon guidance and other signaling molecules. Additionally, because ARSB is added to both the sympathetic ganglion and the myocardial explants, it is unclear where exactly it is disrupting CSPG sulfation. It has been shown that glia also secrete CSPGs (Yiu & He, Nature Reviews Neuroscience volume 7, pp617-627 (2006)) after CNS injury, preventing axon regeneration. Thus, inhibition of 4-sulfation by ARSB within the sympathetic ganglion explant should be taken into account as well when considering experimental specificity. This particular experiment is perhaps the least convincing in this work overall.

NGF: It is standard practice to add NGF to these types of explant studies. We used neonatal ganglia, which require NGF for survival, and we did not want significant differences in NGF content in the culture to be the reason why axon growth differed between groups, as infarcted myocardium produces more NGF than control myocardium. We want sufficient NGF present to stimulate growth in all directions so we could assess the ability of explant derived CSPGs to inhibit growth. We have clarified this in the methods (lines 355-361 in the “clean” version of the revision).

Spatial variability: We marked TC dishes before plating the tissue and were as consistent as possible with the plating although it certainly was not perfect. We detected inhibition of outgrowth consistently in every ganglion co-cultured with infarcted heart, and ARSB treatment consistently abolished outgrowth inhibition. Thus, we believe this is a reliable assay for axon outgrowth and its inhibition by target-derived CSPGs. We added further detail to the methods (lines 355-356 in the “clean” version of the revision).

ARSB: It is true that multiple cell types, including glia and neurons, can produce CSPGs. Two different controls suggest ARSB is acting on CSPGs produced by the cardiac scar rather than ganglionic CSPGs. First, ganglia co-cultured with control heart tissue exhibited identical growth in the presence or absence of ARSB. Second, addition of ARSB did not change the growth of axons extending away from infarcted tissue explants, it only altered growth toward the scar tissue. We have clarified this in the text (lines 130-134).

• The underlying mechanism of the therapeutic potential of inhibiting 4-sulfation of CSPG is unclear. There is immunohistochemistry showing increased sympathetic nerve fibers by TH labeling, co-localized with fibronectin staining to delineate scar. However, how this phenomenon then leads to decreased arrhythmia is a bit of a black box, especially considering that scar tissue is electrophysiologically and mechanically discontinuous from working myocardium.

Overall, the authors demonstrated very interesting dynamics of CSPG sulfation after MI and its correlation with sympathetic innervation of the MI scar. They also demonstrated knockdown of CHST15 reduces PVCs in a mouse model of MI. The causal relationship between CSPG sulfation, reinnervation of scar, and arrhythmogenesis is less convincingly demonstrated as there is no clear functional pathway suggested by which reinnervating scar alters electrophysiology. The authors perhaps realize this issue and thus were careful to be measured in the title of their manuscript, which omits the pathophysiological consequences of sympathetic nerve regeneration.

We agree that this study has not identified the mechanisms by which reinnervation alters arrhythmia susceptibility. That was not the purpose of the study. Our purpose was to test the role of CSPG sulfation in preventing nerve regeneration into the cardiac scar. We agree that it will be very interesting to elucidate the mechanisms of arrhythmia suppression in another study.

Reviewer #2 (Public Review):

The study by Blake et al. tested an interesting hypothesis that chondroitin sulfate proteoglycan (CSPG) 4, 6 sulfation plays a critical role in mediating sympathetic denervation and cardiac arrhythmia post-ischemia-reperfusion (I/R) in a mouse model. They provided solid molecular evidence showing CSPG 4, 6 sulfation in cardiac scar tissues post-I/R. They also suggest upregulated CHST15 and downregulated ARSB as a mechanism for the production and maintenance of sulfated CSPGs. Most importantly, in vivo siRNA knockdown of chst15 at the early time window of I/R prevented sulfated CSPGs and sympathetic denervation in cardiac scar tissue, which eventually improved cardiac arrhythmia. The strengths of this study come from the focus on a novel CSPG pathway as well as the solid molecular/animal data. It is clear from this study that CSPGs could be a promising therapeutic target to treat cardiac arrhythmia post-myocardial damage.

We appreciate the careful reading of the manuscript and the positive comments. We added data to the supplement and revised the text to address the specific issues raised in the detailed review.

Reviewer #3 (Public Review):

The authors' prior work demonstrated that inhibiting CSPG signaling following myocardial infarction (MI) enabled sympathetic axon outgrowth into the post-MI scar and reduced ventricular arrhythmogenesis. In this study, the authors sought to determine if CSPG sulfation prevented sympathetic axon outgrowth into the post-MI scar.

The strengths of the study include its depth, multimodal tools, in vitro and ex vivo experimentation, and translatability of its findings to large animals and humans.

Minor weaknesses include limited rigor in experimental design supporting some of the conclusions.

The impact of this work is likely to be in the translation to large animals and humans, where scar modifying therapies may come to the forefront of post-MI treatments. The antiarrhythmic potential of this approach is potentially significant, as no current therapies improve the innervation of myocardial scar.

We appreciate the positive comments, and hope that our revised text clarifies issues related to experimental rigor.

Author Response

Reviewer #1 (Public Review):

Kwon, Huxlin and Mitchell compared motion perception and oculomotor responses in eight patients with post-stroke lesions in the primary visual cortex (V1). Motion perception was measured as peripheral motion discrimination thresholds (NDR) separately in the affected and the intact visual field. Due to restoration training, the NDR thresholds were below chance even in the affected visual field, indicating that some residual motion discrimination was possible. Oculomotor responses were measured as the gain of eye drifts (PFR) after saccades to dot patterns that are coherently drifting inside peripheral, stationary apertures. The authors distinguish between a predictive, open loop component up to 100 ms after the saccade that is entirely based on presaccadic motion processing in the peripheral visual field and a visually-driven component from 100 ms after the saccade that is based on postsaccadic motion processing in the fovea. While the PFR gain of patients in the intactfield was comparable to the data of healthy control subjects from a previous study (Kwon et al., 2019), the predictive, open-loop PFR gain of patients in the affected field was close to zero. This was not the case for the visually-driven PFR. The authors interpret their findings in terms of a dissociation between residual motion perception and absent predictive oculomotor control in patients with V1 lesions.

Strengths:<br /> The study contains a rare and valuable set of perceptual and oculomotor data from eight patients with lesions in V1, who underwent restoration training. The direct comparison between peripheral motion discrimination and predictive oculomotor responses is interesting and innovative. Also, the distinction between the predictive, open-loop and the closed-loop component of PFR is important. A potential dissociation between motion perception and oculomotor control would be very relevant for the understanding of different pathways of motion processing for perception and oculomotor control and also for the understanding of the effects of restoration trainings after lesions of V1.

Weaknesses:<br /> The dissociation between perception and oculomotor control in the affected field is primarily based on two results: First, the combination of low PFR gain (Figure 4A) on the one hand and low to medium NDR thresholds (Table 1) on the other hand. Second, the absence of a correlation between NDR thresholds and PFR gain (Figure 4B). However, the data are not as clear-cut. The regression of PRF gain on NDR thresholds in the intact-field predicts that there should be a substantial PRF gain only at NDR thresholds below about 0.3. For the affected field this applies only to three data points of which one shows a substantial PFR and is fully compatible with the data in the intact-field. Hence, the evidence of a dissociation between motion perception and oculomotor control is based on a very small number of data points. This also allows for a different interpretation: instead of assuming separate pathways for motion perception and oculomotor control in patients, the results might also be explained by a different read-out of the same motion signal for perception and oculomotor control, where oculomotor control applies a more conservative threshold and requires a higher internal signal strength than the motion perception.

The comparison of the patients' data to the data in the previous study (Kwon et al., 2019) is not very informative. First, the patients were considerably older than the participants in the previous study, and an age-matched control group would be favourable. That being said, the fact that the PFR gain was comparable for the intact-field of the patients and the previous study renders age-effects rather unlikely.

Second, there is no control data for the motion discrimination task, so we don't know what the NDR thresholds and even more importantly what the relationship between NDR thresholds and PFR gain in healthy observers would be.

We thank the reviewer for their evaluation. We have attempted to address concerns about sufficient sampling from blind-fields with recovery that reached the normal range by collecting additional data, doubling our sample size within that range. This is discussed above in “Essential revisions”, along with the alternative interpretation that perception and oculomotor control might rely on a different threshold in readout. The role of age differences was considered in the original manuscript, but this remains an unlikely factor, as the reviewer notes. With regard to normative NDR threshold data, surprisingly, this has not been published in visually-intact controls in a manner that is identical to that in the present study. However, prior work has established that performance in CB patients’ intact visual fields is normal across a wide range of behavioral measures that include luminance contrast sensitivity, processing of form, color and motion, as well as spatial and temporal frequencies (e.g. Barbur et al., 1980; Morland et al., 1999; Sahraie et al., 2006; Huxlin et al., 2009; Das et al., 2014; Levi et al., 2015). In the present study, we have thus used the intact-field as an internal control for blind-field performance in the same participant, as is standard in the field, expecting that intact-field NDR thresholds should be within the normal range. Verifying this is outside the scope of the present paper, but is now planned for our subsequent studies. Other detailed responses appear below to point by point for the reviewer’s “Recommendations for authors”.

Reviewer #2 (Public Review):

This study addresses the oculomotor behaviour of cortically-blind patients (with lesions in V1) who are instructed to perform a saccade toward a cued target placed either in their intact or in the blind visual field. The saccadic target consists in an aperture containing random-dot motion at 75% direction discrimination threshold ("NDR"), and is presented with iso-eccentric similar distractor apertures: with this kind of stimulus, the gaze of normally-sighted participants drifts smoothly in the direction of the target random dot motion immediately after the end of the saccade. Importantly, for some patients, a perceptual training had led to a good recovery of perceptual performance in the blind-field, as documented by the reduction of motion direction discrimination threshold to levels similar to the control healthy participants. Cortically-blind (CB) patients are shown to perform very similarly to control participants in terms of saccade accuracy, but they have longer latency. As for the postsaccadic ocular following response ("PFR"), the eye velocity component projected on the random-dot motion direction Is comparable to controls when the saccade was directed to the intactfield, but the mean PFR is significantly lower for saccades directed toward the blind-field. The authors conclude that V1 lesions result in a previously ignored selective impairment of the automatic transaccadic transmission of visual information that drive the ocular following response. In the supplementary information, it is also shown and the shift of saccadic landing position which is induced by the presaccadic target motion is strongly reduced (yet different from zero) for saccades to the blind-field locations in CB patients.

The manuscript is very well written and illustrated, and the addressed question is novel and highly interesting. The inclusion in the experiment of locations of the patients' blind-field for which some perceptual abilities had been recovered is particularly interesting. However some major weaknesses fragilize part of the results and undermine the interpretation of results (see below). I also list a series of other minor issues to be clarified or improved.

Main weaknesses:<br /> 1) Unfortunately, the present data do not allow to strongly support the conclusion that the reduced PFR gain in patients is decorrelated from the motion discrimination performance. As a matter of fact, in Figure 4B the function describing the relation between PFR gain and NDR is reasonably linear in a very limited interval of NDR values (say <0.3), and it should rather be described as a decreasing exponential, or similar, approaching 0 already for NDR~0.3. On the other hand, it is presumably hard to appropriately fit a similar exponential function to the blind-field datapoints, as the majority of the latter lay in the range of NDR threshold (say > 0.4) where the PFR gain would in any case be flat and close to 0. In other terms, in my view there aren't enough blind-field datapoints with low NDR threshold to assess a quantitative difference in the relation between PFR and NDR between CB patients and Control participants.

Finally, and probably just a misunderstanding of mine, shouldn't the empty circles in Figure 4A and 4B have the same y-coordinate (the PFR gain value)? It does not seem so when looking at these figures.

2) A second weak point, in my opinion, concerns the interpretation of the results and in particular the exclusion of a role for presaccadic attentional mechanisms. The authors claim (lines 356-358): "That the FEF and its projections to area MT are intact in V1-stroke patients suggests preservation of presaccadic planning and attention selection for the saccade target even when visual input is weak or abnormal in a blind-field" and this is definitely a valuable point. However a number of other physiological mechanisms involving V1 could play a role in the spatially-selective processing of motion and the argument that (lines 368 and ff) "other aspects of saccade pre-planning related to perceptual shifts in the position of motion targets, remain in the blind-field" is not very robust here, considering that the reduction in the angular deviation is very strong in the blind-field (Supplementary Figure 2).

Here is a speculative alternative interpretation: V1-lesioned patients suffer among others of a specific impairment for spatially-selective motion processing. Unfortunately, the training in peripheral motion discrimination does not test this particular possibility, if I understand correctly, as there was no other distractor aperture containing distracting motion information (see Fig 2A). In contrast, in the main experiment, a lack of spatial selectivity for motion integration may have strongly affected the presaccadic motion discrimination (being more global than local) as well as PFR and postsaccadic landing position shift (although the latter was partly spared). According to this possibility, a simple prediction is that depending on the (randomly determined) motion direction in the distracting apertures, the PFR (the true eye movement, not the projection according to the stimulus motion axis) should be deviated in different directions, coherent with a global integration of motion. Do the available data allow to verify this possibility? In general, I think that it would be interesting to analyse post-saccadic smooth eye velocity beyond the "projected" velocity.

We thank the reviewer for their evaluation, several parts of which overlap with Reviewers 1 and 3. In particular, the concerns about sufficient sampling from blind-fields that recover motion integration (NDR < 0.35) have been addressed by collecting additional data and performing new analyses, and we have also addressed possible impairments to spatial attention (see above in “Essential revisions”). The discrepancy noted in the y-ordinate between 4A and B is related to those analyses being by subject (4A) versus by visual field location (4B), which we already addressed above, in response to Reviewer 1. Other detailed responses appear below.

Reviewer #3 (Public Review):

The human visual system comprises a tangle of neural pathways that subserve different perceptual, cognitive, and motor functions. Unfortunate cases of brain damage can reveal surprising dissociations between the functions of damaged and spared tissue. Perhaps the most famous example is blindsight, when damage to visual regions of occipital cortex leads to subjective blindness in parts of the visual field while sparing some visually-guided actions. Kwon, Huxlin and Mitchell had a rare opportunity to study eight individuals with that type of cortical blindness due to stroke, and put them through a carefully designed regimen of visual training and oculomotor testing.

The main focus was a particular oculomotor behavior that they term the "post-saccadic following response": when a neurotypical person makes a saccade to an object moving in the periphery, their eyes immediately begin smoothly following the stimulus motion, due to an oculomotor plan made before the saccade began. In this case, the stroke patients were able to regain their ability to discriminate stimulus motion in the "blind" parts of the visual field, but upon saccading to those stimuli they did not show the immediate post-saccadic following response. This surprising result shows yet another splintering dissociation between perception and action, demonstrating that the effects of stroke can be very specific to certain motor actions.

Strengths:<br /> - The authors masterfully combined several techniques in a rare and carefully chosen sample of participants: neuropsychiatric evaluations, rehabilitation training, psychophysics and eye-movement analyses.<br /> - The analyses that link all those measures together, while complicated and precise, and elegantly and clearly presented.<br /> The study provides a twist on blindsight that is interesting philosophically, while also constraining our models of neural circuitry and informing approaches to rehabilitation after stroke.

Weakness:<br /> - The unique nature of this study is a strength but also potentially limits its impact: the authors studied one particular type of eye movement with a complicated, unnatural stimulus arrangement. For example, the stimuli were groups of random moving dots windowed through static apertures. These stimuli, which move but also don't, are quite different from real moving objects that people track with their eyes (flying birds, for example). A related issue, which the authors briefly acknowledge, is that the training was specifically directed towards explicit perceptual reports. We therefore don't know if the oculomotor behavior (the PFR) could also be trained.<br /> - The authors rely on traditional null-hypothesis tests (t-tests and correlations) to make binary judgements of whether each effect or difference is "significant" (p<0.05). Some of the conclusions would be more convincing if supplemented with power analyses, bootstrapped confidence intervals, and Bayes factors to evaluate the strength of evidence.

We thank Reviewer 3 for their evaluation. The choice of stimuli/task and their “naturalness” is addressed in our point by point responses to the “Recommendations for authors” below. We have also revised the manuscript to include boot-strapped confidence intervals, along with other statistics suggested by other reviewers, as noted under “Essential revisions for authors”. Other detailed responses appear below point by point.

Author Response

Reviewer #3 (Public Review):

Phillips and colleagues present results obtained by generating loss-of-function mutations in the YAP/TAZ ortholog of the unicellular holozoan Capsaspora owczarzaki. In previous work published collaboratively by the Pan and Ruiz-Trillo labs, the authors had shown that Capsaspora has orthologs of yorkie (yki) and hippo (hpo) and that when these genes were expressed in Drosophila they functioned in a way that was consistent with the well-characterized function of the Hippo pathway in regulating cell proliferation.

Characterizing the role of the pathway in Capsaspora required the ability to manipulate gene expression in that organism. In this manuscript, the authors describe remarkable progress in that area. They generate lines that stably express fluorescent proteins. Excitingly, they are able to use CRISPR/Cas9 and generate loss-of-function alleles using a donor-template strategy. These accomplishments pave the way for the study of Capsaspora using molecular tools.

The authors then use these technologies to generate biallelic loss of function mutations in Capsaspora. They find no evidence of defects in cell proliferation either when these cells are cultured by themselves or when they are mixed with wild-type cells. However, they do find evidence of abnormalities in the cytoskeleton. They find that the cells themselves, and the multicellular aggregates that they form are more irregular in shape. The cells appear to adhere to substrates better than wild-type cells. They show surface blebbing that changes in the cell cortex with evidence for altered actin dynamics.

From these experiments, the authors conclude that the ancestral function of the Hippo pathway is to regulate the cytoskeleton and that its ability to regulate cell proliferation was acquired more recently in evolution.

The technical achievements are impressive, the experiments are well designed and executed, and are presented clearly. I have no issues with them. However, I feel that two of the main conclusions that the authors make are not justified by the results.

1) The authors seem convinced that CoYki functions as a transcriptional regulator. They seem to suggest that it is primarily a regulator of cytoskeletal genes. There is a body of work from the Fehon laboratory that Yki has a function at the cell cortex in Drosophila that is independent of its function as a transcriptional regulator. See the work by Xu et al. 2018; PMID30032991 (not cited in this paper). In the absence of data that shows the localization of CoYki, I don't see how the authors can tell where it is working (in the nucleus or at the cell cortex) to regulate the cytoskeleton.

To provide support for asserting that coYki is transcriptional regulator, we have done the following:

• We have cited previous results showing that coYki and its binding partner coSd can, when expressed together in the Drosophila eye, induce transcription of Hippo pathway genes, indicating a role for coYki in transcriptional regulation

• We have examined the localization fluorescent fusions of coYki and a coYki (coYki 4SA) mutant predicted to be nonphosphorylatable by upstream Hippo pathway kinases. Enrichment of coYki at the cell cortex was not detected. However, the 4SA mutant showed increased localization in the nucleus relative to the WT coYki protein, arguing for a nuclear function of coYki.

These data are therefore consistent with the prevailing view of Yki/YAP/TAZ as a transcriptional regulator in other species. Nevertheless, we cannot formally exclude the possibility that coYki may also affect the cytoskeleton through a non-transcriptional manner as described by Xu et al., which we have now stated in the Results section of our manuscript.

2) Capsaspora and animals such as ourselves are equally separated by time from our last common ancestor. There is no reason to think that the function of signaling pathways in the Capsaspora lineage has been frozen in time while ours have evolved. Indeed, the amazing diversity of protists is consistent with lots of evolution in every lineage. One could easily argue from the same data that the ancestral function of the Hippo pathway was to regulate cell proliferation and that this was lost in the lineage that led to Capsaspora. As we learn more about the function of the Hippo pathway in diverse organisms, we will be in a better position to guess what the ancestral function was.

We agree that the function of signaling pathways in modern protists and their ancestors may not necessarily be identical, and that studies of Hippo signaling in other organisms, especially unicellular holozoans, may clarify which functions may have been ancestral, as we make a point to state at the end of our discussion. However, given that in animals Hippo signaling regulates the cytoskeleton and proliferation, and we find that in Capsaspora coYki affects the cytoskeleton but apparently not proliferation, it seems reasonable to us to suggest a model where cytoskeletal regulation was an ancient function, and the pathway was later co-opted for regulation of proliferation. We have added a section in the Discussion pointing out that we cannot, from our results, definitively conclude an ancestral Hippo pathway function.

In summary, this manuscript describes technological innovations that will have a big impact on those who want to study this organism. They also provide convincing data to show that the Capsaspora Yorkie ortholog regulates cytoskeletal dynamics and not cell proliferation. However, as described above, the authors would need to tone down some of their conclusions.

Author Response

Reviewer #2 (Public Review):

The authors provide evidence that the small G protein Arl15 binds to the MH2 domain of Smad4, and propose, primarily on the basis of biochemical experiments that Arl15 controls the assembly of the heteromeric Smad (Smad4:R-Smad) complexes that form in response to TGF-b or BMP. They also propose that the Smad complex enhances the GAP activity of Smad4 toward Arl15. Finally, they propose that Arl15 acts as a global regulator of TGF-b family responses.

The initial observation that Arl15 interacts with the MH2 domain of Smad4 is intriguing and so are some of the biochemical interaction data. However, in the end, the proposed role of Arl15 in Smad complex formation in response to TGF-b or BMP and the proposed scenario are insufficiently supported by in vivo (in cells) data on the extent to which Arl15 controls the Smad complex formation and its activity. Indeed, experiments that I would intuitively see as the first and key questions to be addressed have not been done (or not been shown). More specifically: (1) Does Arl15 control/enhance the association of endogenous Smad4 with Smad2/3 or Smad1/5 in response to TGF-b or BMP, respectively? (2) Does Arl15 enhance the TGF-b- or BMP-induced nuclear localization of these endogenous complexes? (3) Since Arl15 enhances the direct target gene responses, does Arl15 enhance the TGF-b-induced binding of endogenous Smad complexes to regulatory sequences of target genes?

We would like to thank this reviewer for these insightful comments and constructive suggestions.

(1) Regarding whether "Arl15 controls/enhances the association of endogenous Smad4 with Smad2/3 or Smad1/5 in response to TGF-b or BMP, respectively", we found that, upon the depletion of Arl15, TGFβ1-induced interaction between Smad4 and phospho-Smad2/3 decreased substantially (see our response to point 8 of Reviewer #2's comments). Our finding supports our model that Arl15 promotes the assembly of the Smad-complex.

(2) Regarding whether "Arl15 enhances the TGF-b- or BMP-induced nuclear localization of these endogenous complexes", we demonstrated that depletion of Arl15 reduced the TGFβ1-induced nuclear localization of endogenous Smad-complex consisting of Smad4 and phospho-Smad2/3 (see our response to point 9 of Reviewer #2's comments).

(3) However, regarding whether "Arl15 enhances the TGF-b-induced binding of endogenous Smad-complexes to regulatory sequences of target genes", we did not produce experimental evidence since we think that the proposed experiment, e.g., CHIP of the Smad-complex, should not fall within the scope of our study. Please see our response to point 11 of Reviewer #2's comments.

Author Response

Reviewer #1 (Public Review):

Morck et al. report the effect of five HCM causing lever arm mutations - two in the light chain binding region and three in the pliant region - on beta-cardiac myosin motor function and autoinhibition. Overall, this is a strong and very interesting work, especially since the functional consequences of mutations in the lever arm are understudied. The authors carefully compared light chain binding stoichiometries to the myosin heavy chain, steady-state ATPases, in vitro gliding velocities, and single ATP turnover kinetics of lever arm mutants in the context of short-tailed and long-tailed double-headed myosin constructs to investigate their effect on motor function and autoinhibition. They additionally used harmonic force spectroscopy to measure load-dependent detachment rates and step sizes of single-headed pliant region mutants and then calculate parameters including ensemble force, power output, and duty ratio. Finally, the authors discuss their findings with a structural model of the autoinhibited state of beta-cardiac myosin and conclude that mutations in the light chain binding region lead to changes in myosin motor activity and the formation of the autoinhibited state whereas mutations in the pliant region impact the ability of myosin to form the autoinhibited state. In summary, this work makes a significant contribution to the mechanisms of disease-causing mutations in beta-cardiac myosin and SRX myosin biology and will be of wide general interest.

We thank the reviewer for their kind comments and wish to point out a minor typo in the above public review–the reviewer states, “the authors…conclude that mutations in the light chain binding region lead to changes in myosin motor activity and the formation of the autoinhibited state whereas mutations in the pliant region impact the ability of myosin to form the autoinhibited state.” The statement should be reversed to read, “the authors…conclude that mutations in the light chain binding pliant region lead to changes in myosin motor activity and the formation of the autoinhibited state whereas mutations in the pliant light chain binding region impact the ability of myosin to form the autoinhibited state.”

The strengths of this work are the rigorous and well controlled experimental design and data analysis in addition to the use of human proteins to study human disease-causing mutations.

A weakness of this work is that the interpretation/discussion of the experimental results heavily relies on previous homology models of beta-cardiac myosin (e.g. Fig. S3) rather than the relevant parts of the recent high-resolution structures of smooth muscle myosin in the autoinhibited state (PMIDs: 34936462, 33268893, 33268888). For example, one of these studies showed a previously unknown conformation of the RLC bound to the lever arms of autoinhibited myosin. The same study also showed that the C-terminus of the RLC interacts with the hook to stabilize the autoinhibited state and that the RLC interacts with the ELC. It would be insightful to analyze or comment if the studied lever arm mutations may change these interactions and possibly alter an allosteric pathway that operates between the light chain bound lever arm and the motor domain.

While we have cited and discussed the structures from PMIDs 33268893 and 33268888 (references 42 and 43), we are grateful to the reviewer for bringing to our attention our omission of the structure from PMID 34936462 and apologize for this oversight. We have now included this citation whenever we refer to smooth muscle myosin structures and have added a comment on the interaction of the RLC with the hook (pg. 25 line 7 - 9). We thank the reviewer for this comment.

We have also added these three experimentally solved structures to figure S7 (previously fig. S3) and added commentary on how these structures differ from the homology-modeled structures. We thank the reviewer for this comment.

We wish to point out that the reason homology-modeled structures are also included in figure S7 (previously S3) is because the sequence of the smooth muscle myosin differs from the sequence of human β-cardiac myosin; thus, assessing the impact of an individual point mutation in the background of many baseline mutations becomes difficult. Ideally, a new modeled structure of human β-cardiac myosin should be created based on the newly available structures of the smooth muscle myosin in the autoinhibited state or an atomic structure of human β-cardiac myosin in the off state should be determined experimentally, but we believe that this is outside the scope of the present work. Additionally, it is possible that the autoinhibited structure of human β-cardiac myosin will differ from the autoinhibited structure of smooth muscle myosin in meaningful ways because smooth muscle myosin forms the autoinhibited state outside of sarcomeres, whereas human β-cardiac myosin would experience autoinhibition within the context of sarcomeres. The goal of including the modeled structures is, in essence, to show that they are all likely incorrect with regards to the real lever arm conformation and to highlight how they differ from the lever arm structures in the aforementioned smooth muscle myosin structures. This point has been clarified in the figure legend and text (pg. 25 line 19 - 22).

Reviewer #3 (Public Review):

The paper by Morck et al. explores the functional consequences of a group of single mutations in the lever arm of myh7 that are associated with hypertrophic cardiomyopathy (HCM). The underlying hypothesis is that these mutations affect the population of the super-relaxed state of myosin. The investigators use range of biochemical and biophysical techniques to explore the activities of these myosins. They conclude that the mutations have a range of effects on the motors, and there is not a single mechanism that can account for hypercontractility that leads to HCM. Although there is not a straightforward connection between the mutations and HCM, the study is important in that it reveals the range of functional effects of the mutations.

A strength of the paper is the range of techniques used to examine the functional consequences of a range of myh7 mutations. Using single-molecule and ensemble techniques, they conclude the lever-arm mutations affect SRX to various extents, in addition to affecting force-dependent actin detachments, actin-activated ATPase activities, and power output. The effort required to express, purify, and characterize the six constructs (WT + 5 mutants) is considerable. A unified mechanism is not proposed as to how these mutants drive HCM, but the work remains significant in showing the range of functional effects that should be considered when modeling SRX, thin-filament activation, and interaction with other sarcomeric proteins.

A weakness in the paper is the variability in the reported ATPase activities as outlined below. This variability leads one to question the validity of the conclusions about actin-activation of the ATPase activity. Additionally, the paper does not show primary single-molecule data, and it does not adequately discuss limitations of the harmonic force spectroscopy method. To be clear, this method is appropriate for this study, but its model-dependent limitations need to be stated.

Specific Points:

The authors ability to conclude that there are differences in the ATPase activities among the isoforms is not convincing. The authors are to be commended for providing the detailed data summary in Table S1, but it is these data that raise concerns. For example, the ranges in the values of kcat's (3.8 - 6.1 s-1) and Km's (1.5 - 13.6 uM) in Table S1 obtained from the different WT-control experiments are very large. In a well-controlled ATPase assay, these numbers should be very similar. It makes one question the health of the proteins and the ability to know the active site concentrations. Normalizing each mutant to the paired WT protein provides a control for assay variability, but it does not control for variability in the health of the proteins. The reader is left to wonder if the percent differences reported for the mutants are meaningful.

We hope that the analysis and adjustments described in the “essential revisions” section help to alleviate these concerns.

Readers need to see primary optical trapping data. Only the results of analyses are shown. It would be helpful to see single interactions, and it would be useful to see displacement distributions. Given the mutations are in the myosin lever, one might expect changes in average displacements or changes in the width of the displacement. These data are not provided.

We thank the reviewer for this comment. We have now added a figure (Figure S3) that includes representative raw optical trapping data (S3 A, B, C, and D) and the process of identification of the respective stroking events from the changes in phase and amplitudes of oscillation of the trapped beads. We have also added displacement distribution for one representative single molecule (Figure S3 Q, R, S, and T).

It is surprising that the authors do not show lifetimes of attachment durations from the optical trapping in the absence of force. Figure 3B is from the model-dependent fitting of the harmonic force spectroscopy experiment.

We have now added representative raw data as obtained from HFS experiments (Figure S3 A, B, C, D) and the analysis of the HFS data for one representative molecule for each myosin type (Figure S3 E, F, G, H, I, J, K, L). In the HFS experiments, due to oscillation of the sample stage, an actin interacting myosin molecule experiences a sinusoidally oscillating load with a definite mean force for each stroking event. In this manner, some of the stroking events occur against zero or near zero mean external force (3rd force bin from the left in Figure S3 I, J, K, L). We thank the reviewer for pointing this out. We hope with the inclusion of the raw data, this concern is now addressed.

**Author Response"

Reviewer #1 (Public Review):

This paper is a technical tour de force, as demonstrated best in the many videos associated with the text. They reveal the huge amount of microtubule tracking that has been achieved and show HeLa spindles with more clarity and detail than has previously been accomplished. Thus, the paper is a landmark in spindle study. In its current form, however, the paper contains some technical errors and some issues with interpretations, and their remedy would make this paper an important classic in structural cell biology. These issues include: taking account of the collapse in section thickness that is brought about by the electron beam; recognizing that the great number of non-KMTs near the pole will bias the probability of MT-MT interactions in ways that should be taken into account; and re-examining the data to see if additional issues, such as the opened or closed status of KMTs at their polar ends can be determined. With these and other improvements, the paper will become a classic in the field.

Thank you for your positive feedback and your detailed recommendations. Taking care of your comments will certainly contribute to an improvement in the presentation of our data. Briefly, we applied a z-factor to our tomographic stacks. As for the probability of MT-MT interactions, we normalized our data against the density of surrounding MTs. The morphology of the (K)MT ends, however, will be subject to a parallel collaborative publication. In this separate publication, we will report on MT minus-end morphology in both untreated and MCRS1-depleted HeLa cells. This separate publication will be submitted also to Elife very soon, and the data will be available then on bioRxiv.

Author Response

Reviewer #1 (Public Review):

Previous studies have indicated that neurons in different cortical areas have different intrinsic timescales. However, the functional significance of the difference in intrinsic timescales remains to be established. In this study, Pinto and colleagues addressed this question using optogenetic silencing of cortical areas in an evidence accumulation task in mice. While head-fixed mice performed in an accumulating-towers task in visual virtual reality, the authors silenced specific cortical regions by locally activating inhibitory neurons optogenetically. The weight of sensory evidence from different positions in the maze was estimated using logistic regressions. The authors observed that optogenetic silencing reduced the weight of sensory evidence primarily during silencing, but also preceding time windows in some cases. The authors also performed a wide-field calcium imaging and derived auto-regressive term based on a linear encoding model which include a set of predictors including various task events, coupling predictors from other brain regions in addition to auto-regressive predictors. The results indicated that inactivation of frontal regions reduced the weight of evidence accumulation on longer timescales than posterior cortical areas, and the autoregressive terms also supported the different timescales of integration.

The question that this study addresses is very important, and the authors used elegant experimental and analytical approaches. While the results are of potential interest, some of the conclusions are not very convincing based on the presented data. Some of these issues need to be addressed before publication of this work.

We thank the reviewer for their kind words and constructive feedback. In hindsight, we agree that some conclusions were unwarranted based on the original analysis. We have revamped our analytical approach to address these issues, as detailed below.

Major issues:

1. There are several issues that reduce the strength of the main conclusion regarding the timescale of integration using cortical silencing. 1a. The main analysis relied on the data pooled across multiple animals although individual animals exhibited a large amount of variability in the weights of integration across different time windows. Also, some mice which did not show a flat integration over time were excluded. This might also affect the interpretation of the analysis based on the pooled (and selected) data. How the individual variability affected the main conclusion needs to be discussed carefully.

We have entirely replaced the pooled model for a mixed-effects logistic regression approach in which we explicitly modeled the variability introduced by individual animals (as well as different inactivation conditions). Because of this more principled approach, we added back the previously excluded mice. We also devised a shuffling procedure to further take that variability into account when reporting the statistical significance of the effects, as we now explain in Materials and Methods (line 652):

“For the models in Figure 2, we also computed coefficients for shuffled data, where we randomized the laser-on labels 30 times while keeping the mouse and condition labels constant, such that we maintained the underlying statistics for these sources of variability. This allowed us to estimate the empirical null distributions for the laser-induced changes in evidence weighting terms.”

Finally, we have also added text to be more explicit about this variability and how it informed the new analytical approach (line 169):

“(...) to account for the inter-animal variability we observed, we used a mixed-effects logistic regression approach, with mice as random effects (see Materials and Methods for details), thus allowing each mouse to contribute its own source of variability to overall side bias and sensitivity to evidence at each time point, with or without the inactivations. We first fit these models separately to inactivation epochs occurring in the early or late parts of the cue region, or in the delay (y ≤ 100 cm, 100 < y ≤ 200 cm, y > 200 cm, respectively). We again observed a variety of effect patterns, with similar overall laser-induced changes in evidence weighting across epochs for some but not all tested areas (Figure 2–figure supplement 1). Such differences across epochs could reflect dynamic computational contributions of a given area across a behavioral trial. However, an important confound is the fact that we were not able to use the same mice across all experiments due to the large number of conditions (Figure 1–table supplement 1), such that epoch differences (where epoch is defined as time period relative to trial start) could also simply reflect variability across subjects. To address this, for each area we combined all inactivation epochs in the same model, adding them as additional random effects, thus allowing for the possibility that inactivation of each brain region at each epoch would contribute its own source of variability to side bias; different biases from mice perturbed at different epochs would then be absorbed by this random-effects parameter. We then aligned the timing of evidence pulses to laser onset and offset within the same models, as opposed to aligning with respect to trial start. This alignment combined data from mice inactivated at different epochs together, further ameliorating potential confounds from any mouse x epoch-specific differences. (...) This approach allowed us to extract the common underlying patterns of inactivation effects on the use of sensory evidence towards choice, while simultaneously accounting for inter-subject and inter-condition variability.”

1b. The main conclusion that the frontal areas had longer integration windows largely depends on a few data points which relied on a very small number of samples (n = 4 or 3). This is, in part, because of the use of pooled data and because the number of samples comes from the alignment of the data with different timing of inactivation. This analysis also appears to suffer from the fact that the number of sample is biased toward the time of inactivation (y = 0 which had n = 6) compared to the preceding time windows (y = 50 and 100, which had n = 4 and 3, respectively).

We agree with this assessment. As explained above, our new mixed-effects logistic regression approach explicitly models the variability introduced by mice and conditions, which allows us to focus on the effects that are common across mice and conditions. Because of these changes, we were now able to perform statistical analyses on coefficients using metrics based on their error estimates from the model fitting procedure, such that all estimates come from the same sample size and take into account the full data (t- and z-tests, as explained in more detail in Materials and Methods, line 665). This new analysis approach confirmed, and we believe strengthened, our main conclusions.

1c. The clustering analysis uses only 7 data points corresponding to the cortical areas examined. The conclusions regarding the three clusters appear to be preliminary.

We agree. The clustering analysis was more meant as a way to summarize the data rather than provide a strong statement of area groupings. Because this analysis requires clustering on only 7 data points, as the reviewer points out, and because it is in no way central to our claims, we have decided to drop it. Instead, we now present a direct comparison between frontal and posterior areas, which is more directly related to our claims (Figs. 2C, 3).

1. The authors' conclusion that "the inactivation of different areas primarily affected the evidence-accumulation computation per se, rather than other decision-related processes" can be a little misleading. First, as the authors point out in the Results, the effect can be "the processing and/or memory of the evidence". Given that the reduction in the weight of evidence occurs during the inactivation period, the effect can be an impairment of passing the evidence to an integration process, and not accumulation process itself. Second, as discussed above (1b), the evidence supporting a longer timescale process (characterized as "memory" here) is not necessarily convincing. Additionally, the authors' analysis on "other decision-related processes" is limited (e.g. speed of locomotion), and it remains unclear whether the authors can make such a conclusion. Overall, whether the inactivation affected the evidence accumulation process and whether the inactivation did not affect other cortical functions remain unclear from the data.

We agree with the reviewer that our previous modeling approach did not allow us to adequately separate between these different processes. However, we believe that our new approach addresses some of these shortcomings by being done in time rather than space (thus controlling for running speed effects), and separating evidence occurring before, during or after inactivation within the same model. As we now explain in the main text (line 156):

“We reasoned that changes in the weighting of sensory evidence occurring before laser onset would primarily reflect effects on the memory of past evidence, while changes in evidence occurring while the laser was on would reflect disruption of processing and/or very short-term memory of the evidence. Finally, changes in evidence weighting following laser offset would potentially indicate effects on processes beyond accumulation per se, such as commitment to a decision. For example, a perturbation that caused a premature commitment to a decision would lead to towers that appeared subsequent to the perturbation having no weight on the animal’s choice. Although our inactivation epochs were defined in terms of spatial position within the maze, small variations in running speed across trials, along with the moderate increases in running speed during inactivation, could have introduced confounds in the analysis of evidence as a function of maze location (Figure 1–figure supplement 2). Thus, we repeated the analysis of Figure 1C but now with logistic regression models, built to describe inactivation effects for each area, in which net sensory evidence was binned in time instead of space. (...) We then aligned the timing of evidence pulses to laser onset and offset within the same models, as opposed to aligning with respect to trial start.”

Throughout our description of results, we now more carefully outline whether the findings support a role in sensory-evidence processing, memory, or both, as well as post-accumulation processes manifesting as decreases in the weight of sensory evidence after laser offset. For example, our new analyses have more clearly shown prospective changes in evidence use when M1 and mM2 were silenced, compatible with the latter. We also agree with the reviewer that we cannot completely rule out other untested sources of behavioral deficits beyond the aforementioned decision processes. Thus, we have removed all statements to the effect that only evidence accumulation per se was affected. Importantly, though, we believe the new analyses do support the claims that the inactivation of all tested areas strongly affects the accumulation process, even if not exclusively.

1. Different shapes of the autoregressive term may result from different sensory, behavioral or cognitive variables by which neurons in each brain area are modulated. In other words, if a particular brain area tracks specific variables that change on a slow timescale, the present analysis might not distinguish whether a slow autoregressive term is due to the intrinsic properties of neurons or circuits (as the authors conclude), or neuronal activities are modulated by a slowly-varying variable which was not included in the present model.

We note that many of our task-related predictors, in particular ones related to sensory evidence, had lags that matched the timescales of the auto-regressive coefficients. Along with our regularization procedures, this would argue against variance misattribution to coefficients included in the model. We have now added an analysis of sensory-evidence coefficients to Figure 4–figure supplement 1, which did not reveal any significant differences between areas.

Of course, as the reviewer suggests, it is possible that, despite our extensive parameterization of behavioral events, we failed to model some task component that would display timescale differences across areas. We have added a discussion to acknowledge this possibility (line 332):

“Nevertheless, a caveat here is that the auto-regressive coefficients of the encoding model could conceivably be spuriously capturing variance attributable to other behavioral variables not included in the model. For example, our model parameterization implicitly assumes that evidence encoding would be linearly related to the side difference in the number of towers. Although this is a common assumption in evidence-accumulation models (e.g., Bogacz et al., 2006; Brunton et al., 2013), it could not apply to our case. At face value, however, our findings could suggest that the different intrinsic timescales across the cortex are important for evidence-accumulation computations.”

Reviewer #2 (Public Review):

Pinto et al use temporally specific optogenetic inactivation across the dorsal cortex during a navigation decision task to examine distinct contributions of cortical regions. Consistent with their previous findings (Pinto et al 2019), inactivation of most cortical regions impairs behavioral performance. A logistic regression is used to interpret the behavioral deficits. Inactivation of frontal cortical regions impairs the weighting of prior sensory evidence over longer timescale compared to posterior cortical regions. Similarly, the autocorrelation of calcium dynamics also increases across the cortical hierarchy. The study concludes that distributed brain regions participate in evidence accumulation and the accumulation process of each region is related to the hierarchy of timescales.

Identify the neural substrate of evidence accumulation computation is a fundamentally important question. The authors assembled a large dataset probing the causal contributions of many cortical regions. The data is thus of interest. However, I have major concerns regarding the analysis and interpretation. I feel the results as presented currently do not fully support the conclusion that the behavioral deficit is related to evidence accumulation. Alternative interpretations should be ruled out. Another major concern is the variability of the inactivation effect across conditions. The assumptions for pooling inactivation conditions should be better justified. Finally, some framing in the text should more closely mirror the data. Most notably, the data does not casually demonstrate that the hierarchy of timescales across cortical regions is related to evidence accumulation since the experiments do not manipulate the timescales of cortical regions. The two phenomena might be related, but this is a correlation based on the present findings.

We thank the reviewer for their thorough review and constructive suggestions. As we expand on below, we have changed our modeling approach to better account for data variability, and more explicitly justified the choice to pool across conditions. The modeling approach also allowed us to better pinpoint the different decision processes affected by cortical inactivation. Finally, we have also toned down our claims throughout the manuscript, and removed the claims of causality altogether.

Reviewer #3 (Public Review):

This study examines how the timescale over which sensory evidence is accumulated varies across cortical regions, and whether differences in timescales are causally relevant for sensory decisions. The authors leverage a powerful behavioral paradigm that they have previously described (Pinto et al., 2018; 2019) in which mice make a left vs. right decision in a virtual reality environment based on which side contains the larger number of visual cue "towers" passed by the "running" head-fixed mouse. The probability of tower presentation varies over time/space and between the left and right sides, requiring the mice to integrate tower counts over the course of the trial (several seconds/meters). To examine the contribution of a particular cortical region to sensory evidence accumulation, the authors optogenetically inactivated activity during several sub-epochs of the task, and examined the effect of inhibition on a) behavioral performance (% correct choices) and b) the strength of the contribution of sensory evidence to the decision as a function of time/space from the inhibition onset. Finally, the authors qualitatively compared the timescale of evidence accumulation identified for each region to the autocorrelation of activity in that region, calculated from reanalyzing the author's published calcium imaging data set (Pinto et al., 2019) with a more sophisticated regression model.

The methodology and analyses are leading edge, ultimately allowing for a comparison of evidence accumulation dynamics across multiple cortical regions in a well-controlled behavioral task, and this is a nice extension of the authors' previous studies along these lines. The study can potentially be built on in two broad directions: a) examining how circuits within any of the regions studied here function to accumulate sensory evidence, and b) addressing how these regions coordinate to guide behavior. Overall, while the study is generally strong, addressing some points would increase confidence in the interpretation of the results.

We thank the reviewer for their kind words and very helpful suggestions. As we expand on below, we now fit our model explicitly in the time domain and use mixed-effects regression to account for inter-mouse variability. We also expanded our discussion on interpretation caveats about the inactivation approach.

Specifically:

In describing the contribution of evidence to the decision, and how it is affected by inhibition (primarily Fig. 2), there is a confusing conflation of time and space. These are of course related by the mouse's running speed. But given that inactivation appears to consistently cause faster speeds (Fig. 2-Fig. S1), describing the effect of inhibition on the change of the weight of evidence as a function of space does not seem like the optimal way to examine how inactivation changes the timescale of evidence accumulation. The authors note in Fig. 2-Fig S1 that inactivation does not decrease speed, but it still would confound the results if inactivation increases speed (as appears to be the case; if not, it would be helpful for the authors to state it). Showing the data (e.g., in Fig. 2) as a function of time, and not distance, from laser on would allow the authors to achieve their aim of examining the timescale of evidence accumulation.

Indeed, we do observe significant, though minor, increases in speed. We had originally only considered the confounds of decreases in speed, but we agree that increases could likewise confound the analysis. Following the reviewer’s suggestion, we devised a new model that bins evidence in time rather than in space. Moreover, the time of evidence occurrence is aligned to laser onset or offset within the same model, which allows us to compare more directly the changes in weighting of evidence occurring before, during or after inactivation. The results from these new models are now presented in Figs. 2, 3, 2-S1, 2-S2, and largely confirm the findings from our previous analysis in the space domain.

Performing the analyses mouse by mouse, instead of on data aggregated across mice, would increase confidence in the conclusions and therefore strengthen the study. Mice clearly exhibit individual differences in how they weight evidence (Fig. 1C), as the authors note (line 81). It therefore would make sense to compare the effect of inactivation in a given mouse to its own baseline, rather than the average (flat) baseline. If the analyses must be performed on data aggregated across mice, some justification should be given, and the resulting limitations in how the results should be interpreted should be discussed. For example, perhaps there are an insufficient number of trials for such within-mouse comparisons (which would be understandable given the ambitious number of inactivated regions and epochs)?

As the reviewer suggests, we prioritized the number of conditions and mice per condition rather than the number of trials each mouse had, which complicates a per-mouse analysis of changes in evidence weights. This is particularly true for fitting logistic regressions with multiple coefficients, as was our goal here. Regardless, we still agree that the inter-animal variability should be accounted for in the analysis. Rather than doing a per-mouse regression, however, we implemented a mixed-effects logistic regression, which estimates random effects for all mice together in the same model, accounting for that when estimating the fixed-effects coefficients. Indeed, this approach is recommended for statistical problems such as ours (e.g., Yu et al., Neuron, 2021, In press, https://doi.org/10.1016/j.neuron.2021.10.030). While the overall statistics were still computed from the estimates of the fixed effects, this allowed us to also display per-mouse data when reporting the models (e.g. Figures 2, 3), which hopefully will give readers a greater appreciation for inter-mouse variability in the data, showing variations in their baseline, as the reviewer suggests. Finally, in order to more explicitly account for non-flat baselines, we now report laser-induced changes in evidence weights normalized by the baseline, rather than simply subtracted, as we did previously.

The method of inactivating cortical regions by activating local inhibitory neurons is quite common, and the authors' previous paper (Pinto et al., 2019) performed experiments to verify that light delivery produced the desired effect with minimal rebound or other off-target effects. Since this method is central to interpreting the results of the current study, adding more detail about these previous experiments and results would reassure the reader that the results are not due to off-target effects. Given that the cortical regions under study are interconnected, do the previous experiments (in Pinto et al., 2019) rule out the possibility that inactivating a given target region does not meaningfully affect activity in the other regions? This is particularly important given that activity is inhibited in multiple distinct epochs in this study.

We agree that the issue of off-target effects is important to the interpretation of any inactivation experiment, and one that we have yet to adequately grapple with as a field. Our previous experiments only measured local spread of inactivation effects. Thus, while we did rule out rebound excitation, we cannot rule out possible off-target effects in distal regions that are connected with the region being inactivated. Experiments to measure this would involve measuring from a single area while systematically inactivating distal areas connected to it or not or, more ideally, measuring from multiple areas simultaneously while performing these systematic inactivations. These experiments themselves would constitute a whole project and therefore fall outside the scope of the present manuscript. Following the reviewer’s suggestion, we have expanded the discussion of these experiments and potential caveats.

Line 145, Results: “Although our previous measurements indicate inactivation spreads of at least 2 mm (Pinto et al., 2019), we observed different effects even comparing regions that were in close physical proximity.”

Line 223, Results: “However, the possibility remains that these effects are related to lingering effects of inactivation on population dynamics in frontal regions, which we have found to evolve on slower timescales (see below). Although we have previously verified in an identical preparation that our laser parameters lead to near-immediate recovery of pre-laser firing rates of single units, with little to no rebound (Pinto et al., 2019), these measurements were not done during the task, such that we cannot completely rule out this possibility.”

Line 375, Discussion: “This could be in part due to technical limitations of the experiments. First, the laser powers we used result in large inactivation spreads, potentially encompassing neighboring regions. Moreover, local inactivation could result in changes in the activity of interconnected regions (Young et al. 2000), a possibility that should be evaluated in future studies using simultaneous inactivation and large-scale recordings across the dorsal cortex.”

Line 516, Materials and Methods: “We used a 40-Hz square wave with an 80% duty cycle and a power of 6 mW measured at the level of the skull. This corresponds to an inactivation spread of ~ 2 mm (Pinto et al., 2019). While this may introduce confounds regarding ascribing exact functions to specific cortical areas, we have previously shown that the effects of whole-trial inactivations at much lower powers (corresponding to smaller spatial spreads) are consistent with those obtained at 6 mW. To minimize post-inactivation rebounds, the last 100 ms of the laser pulse consisted of a linear ramp-down of power (Guo et al., 2014; Pinto et al., 2019)”

Author Response

Reviewer #2 (Public Review):

Rizo et al. present all-atom (AA) molecular dynamics simulations of molecular components of the neurotransmitter (NT) release machinery. Evoked NT release is triggered by machinery that senses calcium and responds by fusing the vesicular and plasma membranes to release NTs via a fusion pore. Synaptotagmin is the calcium sensor and the SNARE proteins are the core of the fusion machinery. Complexin is another molecular component, among others.

Simulations were performed with 4 trans-SNARE complexes bridging 2 membranes with realistic lipid compositions, either 2 planar, or 1 planar and 1 vesicular. Other simulations incorporate also the C2A and C2B domains of Synaptotagmin-1 (Syt), and the accessory and central helices of Complexin-1 (Cpx). The authors' aim is to study the vesicle-release machinery system in its "primed" state, in which fusion is blocked ("clamped") before the influx of calcium which triggers fusion of the membranes and release. The planar membrane is 26 nm x 26 nm (sometimes a little larger) and the vesicle diameter 26 nm. The duration of each of the simulations of 2-5 million atoms was typically about 0.5 µsec.

Some of the major conclusions the authors declare are as follows. (i) The juxtamembrane domains (linker domains, LDs) are unstructured in the trans-SNARE complexes. (ii) SNAREs on their own pull the membranes together and squash them into an extended contact zone (ECZ) (observed in simulations with SNAREs only) as seen in experiments (Hernandez et al, 2012). (iii) Their AA simulations are argued to support a model previously proposed by this group (voleti et al., 2020) of the primed state that clamps the fusion machinery, in which C2B binds the SNARE complex via the primary interface from the crystal structure (Zhou et al., 2015), with the C2B polybasic face binding the planar membrane, while a Cpx fragment binds the opposite side of the SNARE complex, based on an earlier crystal structure (Chen et al, 2002). In simulations, the structure was robust on the timescales probed. An orientation with the Cpx accessory helix impinging on the vesicle emerged, suggestive of a role in clamping fusion. The simulations implicate several residues as critical, consistent with earlier mutation studies. Two runs produced similar results.

This is a very nice study which offers important information and insights about possible structures in the primed NT release machinery. To my knowledge, this is the most extensive AA model of a plausible NT machinery to date. The conclusion that the LDs are unstructured is interesting, contradicting prior MARTINI studies assuming helices were continuous from the SNARE complex into the LDs, and equally interesting is the finding of an ECZ with SNAREs pushed aside, in accord with previous coarse-grained studies. The outcome of the simulations of the voleti et al. C2B-SNARE-Cpx model is informative, yielding the preferred orientation and supporting the primary interface and Cpx-SNARE interactions implied by crystal structures.

My main concerns are about the validity of the conclusions presented, given the AA results. AA simulations are extremely valuable, but have limited ability to probe the big questions about how the multi-component NT machinery cooperatively unclamps, fuses and releases on msec and greater timescales. I do believe a marriage of very short timescale methods (AA, MARTINI etc) and ultra coarse-grained methods is needed to understand these fascinating systems. This manuscript makes no reference to methods that probe these long timescales, and may sometimes overstate what can be concluded from their AA results. For example, their findings for the voleti C2B-SNARE-Cpx model do not, as far as I can see, obviously suggest that this structure clamps fusion. Similarly, simulations with Cpx removed and Ca2+ bound to the C2 domains were clearly worthwhile but inconclusive, as SNAREs were not released after ~ 400 ns of simulation. In both cases, uncertainties originate in the running time limitations of AA methods.

We very much appreciate the summary of the paper and agree with these criticisms. We had already highlighted the limitations of our simulations and have further emphasized these limitations by pointing out the absence of key components in the revised manuscript (see response to point 2a of Essential Revisions). We also agree that coarse-grained simulations can offer important insights and allow simulations at much longer time scales, which makes them complementary to all-atom simulations. We realize that, in our attempt to emphasize the advantages of all-atom simulations, we did not do justice to the work on SNARE-mediate membrane fusion performed with continuum and coarsegrained simulations, and failed to mention important contributions in this field. We now mention several of these contributions and discuss the complementary role that distinct types of simulations of this system can play in the future (see our answer to point 1b of Essential Revisions above).

Reviewer #3 (Public Review):

Rizo and colleagues revisit several mechanistic questions centered on the roles of SNARE proteins, synaptotagmin 1 and complexin in catalyzing membrane fusion. This effort is purely simulation based with several impressive all-atom simulations of two closely apposed lipid bilayers harboring 4 mostly assembled SNARE complexes with and without Cpx1 and Syt1. The simulations explore only about half a microsecond of elapsed time and fail to capture the act of membrane fusion itself, perhaps due to this short time window imposed by computational limitations. The authors discuss various behaviors of the SNARE proteins and accessory proteins, comparing and contrasting their conformations with those derived from past crystallographic and NMR studies.

Strengths: There are several attractive features of this study. All-atom simulations of SNARE-mediated fusion will necessarily involve many millions of atoms and thus few if any studies of this ambitious scope have been published. Most past computational work in this arena has either been at the coarse-grained level (which has limitations as pointed out by the authors) or has focused purely on a single SNARE complex rather than trying to capture a more realistic fusion/pre-fusion state. And the questions posed in this study are extremely difficult if not impossible to answer via conventional structural, in vitro biochemical and in vivo functional experimental approaches.

Weaknesses: As is the case with all simulations, many realistic aspects of SNAREmediated fusion and the various proteins involved were omitted from the simulations for practical reasons. And several of these omissions may have large impacts on the results and conclusions. These omissions include pieces of the SNARE proteins, Cpx1, and Syt1 that are known to impact synaptic transmission but were not included to minimize the number of atoms simulated. Divalent cation interactions with anionic phospholipids were omitted even though these interactions likely have a large influence on the energy barrier for membrane fusion. Also, each simulation was performed only once, so the reader has no sense of how representative or accurate the presented results are. And importantly, the simulations never captured a bone fide fusion event, which seems like a critical aspect of modeling the prefusion state. Given that even the fastest known synapses require 50100 microseconds to convert a calcium influx into vesicle fusion, it is perhaps not surprising that no fusion events were observed in a 200-700 nanosecond simulation window across the handful of simulations performed in this study. Regardless of these omissions, the authors generated a large amount of simulated data and attempted to reconcile interesting observations with known protein structures and past functional data.

We agree that our simulations have multiple caveats and in the revised version we now mention the absence of key components (see response to point 2a of Essential Revisions). However, as explained above, the simulations do reveal several interesting observations, and we place particular emphasis on those that correlate with experimental data. We note that the observation of an extended vesicle-flat bilayer interface correlates with EM data and that in this case we performed two simulations, one of 520 ns at 310 K and another of 454 ns simulation at 325 K. For the primed synaptotagmin-1-SNARE-complexin-1 complex, we performed two simulations with four complexes each, for a total of eight complexes, and the key features that we highlight were observed in all of these eight complexes.

Author Response

Reviewer #3 (Public Review):

In this manuscript, authors are reporting identification of a compound, VAC1, which affects localization of vacuolar SNARE proteins in Arabidopsis root cells. Authors then examined the effect of VAC1 on other markers, and found that VAC1 affects localization/transport of plasma membrane proteins and FM4-64 but not early and late endosomal proteins, CLC, and actin microfilaments. Authors then examined the effects of VAC1 on expansion of the cell and vacuole and endocytic transport, based on which they concluded that endocytic transport from the PM to vacuole is enhanced during cell elongation, which could coordinate expansion of surface areas of the cell and vacuole.

It is firmly demonstrated in this work that VAC1 treatment resulted in abnormal localization of vacuolar SNARE proteins. In pictures presented in Figure 2C, vacuolar SNAREs seem to be accumulating in aster-like structures. Given that the SNARE proteins are membrane-anchored proteins, the SNARE-positive aster-like structures should be membranous structures. However, the lipophilic dye FM4-64 does not seem to reach the SNARE-positive spikes, accumulating inside the structure. It would be helpful to understand which step is affected by VAC1 more precisely if the detailed structure of the VAC1 body is investigated, e.g., by TEM.

We followed your suggestions and utilized electron microscopy to compare VAC1 and DMSO (solvent control) treated epidermal root cells. Thereby, we revealed that VAC1 induces accumulations of vesicles in the proximity of the vacuoles. Moreover, we observed morphological alterations of the vacuole, which appear to correlate to the mentioned “aster-like” structure. We added this set of data to the revised manuscript (see Figure 2).

It would be also informative to test whether non-SNARE vacuolar proteins are also affected by VAC1 to see the effect of VAC1 is specific to SNARE proteins or not.

We followed your suggestion and addressed the VAC1 effect on VHAa3-GFP, a commonly used tonoplast marker. VAC1 affected the distribution of VHAa3-GFP and the tonoplast marker was seemingly not excluded from the region of highest SNARE protein accumulation. We included this set of data into the revised version of this manuscript.

Related to the comment above, in some figures (e.g., Figure 3E), VAC1 bodies seem to be located inside the vacuole. It would be good to explain whether this consistent with the proposed mode of action of VAC1.

We also got the impression that VAC1 bodies are not only found near the vacuole, but possibly also inside the vacuole. We hypothesize that secondary effects, such as autophagic processes, could lead to “VAC1 body” clearance. Accordingly, we assume that VAC1 could possibly guide researchers to address SNARE-dependent and SNARE independent autophagy in plants.

Author Response

Evaluation Summary:

This manuscript reports advances in the image analysis software package MorphGraphX (MGX). designed to capture the developmental dynamics of growing tissues at cellular resolution. This version, MGX2.0, includes new tools for precise quantitation of cellular behaviors, such as cell division and expansion, within the context of positional information in the growing organs. To illustrate multiple functionalities of MGX2.0, various tissues are analyzed. This presentation style highlights the power and broad applicability of MGX2.0, but leads to a somewhat disjointed narrative, and how it can provide insight into specific biological questions is less clear.

There has been so much added to MGX since the initial version that is was a bit tough to decide how to present it all. One unifying theme for the work that seemed the most scientifically enabling was the notion of coordinate systems for the annotation and interpretation of spatial data. With this in mind, the story follows the development of the presentation of coordinate systems of increasing complexity, starting from simple gradients to more sophisticated methods such as Beziers, compound systems and deformation maps. Unfortunately, as the reviewers and editor have mentioned, this does make it a bit chaotic from the “biological story” perspective, as the same story may come and go at different parts of the paper when illustrating different tools, or the same dataset may come and go as different techniques are applied to it. To address this problem, we have done as the editor and reviewers have suggested to rearrange some of the text and figures where possible and have tried to provide more context and backup for the biological story and relevance to better demonstrate its utility in specific cases.

Reviewer #1 (Public Review):

The work presented here describes the application of a tool (MorphographX 2.0) that opens up possibilities for new image analyses. MorphographX 1.0 is already a valuable tool in the field and the improvements and new functionalities, and approaches presented in this paper allow for the integration and analysis of more positional and temporal information. Specifically, adding positional annotation to analyze the distribution of cell properties across a plant organ will be of great use for the community. The case studies used to showcase MorphographX 2.0's applications highlight the diversity in questions that can be addressed using this tool. As a result, we expect to see MorphographX 2.0 applied in a variety of future plant biology stories. In addition, we believe this tool could also be useful to those outside the plant community. While probably less of use in tissues where there is extensive migration, it can be applied to any system with clearly visible cell membranes.

We agree that the notion of 2.5D image processing could also prove to be very useful in animal systems, as a great many biological processes happen on layers of cells in animal as well, such as epithelia.

The examples presented in this story highlight some great applications of the MorphographX 2.0 software. Analyses using more positional, temporal and 3D information will enable new findings across plant tissues and potentially across species. It is however important to be aware that for optimal use this software is designed to analyze high quality, high contrast stacks that can be difficult and time-intensive to acquire. MorphographX 2.0 also requires a powerful computer setup. The presence of both Linux and Windows versions that do not require a nVidia graphics card does open up possibilities. In addition, extensive documentation and the presence of a community forum allow use of the software without intensive training.

We have added mention of the user forum (forum.image.sc) for MorphoGraphX in the text.