Reviewer #3 (Public review):

Summary:

In this study, Hall and colleagues investigate how the coupling of activity from ACC to CA1is altered by fear learning, showing that during sleep immediately before learning, there is evidence for increased coupling of ACC activity with neurons that will subsequently be inhibited during the learning process. They go on to show that this effect seems to be mediated most by a subpopulation of neurons in the superficial layer of CA1. This fits with previous reports suggesting that these superficial neurons are key for the flexible updating of memory. The authors then go on to show that artificial activation of ACC using optogenetics results in varied effects in CA1, including a subtle decrease in activity of superficial neurons that lasts longer than the stimulus itself. Finally, the authors present some preliminary data suggesting that different interneurons may be recruited by this optogenetic stimulation in different ways and at different times.

Overall, this is an interesting paper, but much of the analysis is very preliminary, and much of the crucial data about the learning effects and alterations to cell firing are not presented clearly and fully. This is further confounded by a rather opaque description of the results and analysis in the text. Overall, there is something very interesting here, but there needs to be a substantial series of extra analyses to clearly say what this is. In many cases, more robust analysis may render the results underpowered, which could dramatically change the conclusions of the paper.

Strengths:

The authors performed difficult, dual-location recordings across a multi-day learning paradigm, which seems like it could be a really nice dataset. They delve into the circuit basis of an interesting finding regarding ACC to CA1 connectivity and how this changes before and after fear conditioning. They provide data to suggest this connectivity may be through specific and distinct subcircuits in CA1.

Weaknesses:

(1) There is essentially no information in the text or figures about what the actual learning was, how it was done, how individual animals performed, and how any of these metrics related to learning. Looking at the methods, the authors did a number of things never mentioned anywhere in the text or figures, including novel arena exposure, contextual reexposure in extinction after learning, etc. It seems that this is a very rich dataset that has not been presented at all. I would recommend at the very least:<br /> a) Plot all of the behavioural training data, and how each mouse relates to one another - did the mice learn? At this stage, we don't know!<br /> b) Explain in the text in detail exactly what was done and why, and what this tells us about the neuronal activity.<br /> c) If there is variance in learning and or conditioning, does this relate to features in the analysis, such as the GLM result.

(2) Along similar lines, a key metric for most of the paper is that neurons most coupled with ACC are more likely to be inhibited during training. However, there is nothing anywhere in the paper showing these data. How do neurons in general respond to contextual shocks? The methods describe this as the average firing rate during training, normalised to pre-sleep activity. This metric seems a bit coarse and may obscure really important task-relevant dynamics. Are the neurons active at specific times, are they tuned to relevant parts of the task, and do any of these features of the cell activity also relate to the coupling with ACC? Similarly, how did the authors mitigate the influence of electrical artefacts caused by the foot shock in their recordings? Again, there is a huge amount of data here that is not being described, and likely holds very valuable information about what is actually happening. The paper would really benefit from the inclusion of these data in an accessible form, such as heatmaps of spiking, how these patterns change over time, and around e.g., foot shock, etc. Also key is how these features are altered by the variability of learning across subjects.

(3) A number of the effects are presented by comparing a statistically significant effect to a non-statistically significant effect (e.g. in Figure 2b, Figure 2d, Figure 4 b,c, and others). This isn't really valid - the key test that the two groups are different is either with a direct test of the difference or an interaction term in an e.g., ANOVA test. In some places, I am not sure the same conclusions will be drawn from the data with these tests.

(4) To what extent is defining superficial and deep CA1 neurons solely by ripple waveform an accepted method? Of the two papers referenced for this approach, one is a 2-photon calcium imaging paper that does not do electrical recordings (as far as I am aware), and the second uses this as a descriptor after defining the positions of units on an array. It would be good to clarify how accepted this is, and also how robust this is. At the very least, some kind of metric or walkthrough in the supplement as to how this was done, and how well each cell was classified and with what confidence, or some metric of how distinct and separate the two populations were (or was it just a smudge).

(5) In the optogenetic experiment in Figure 5, the effect on the CA1 sup neurons seems to be driven by changes in a small subpopulation of this group, with no change in the others. Related to point 2, is there anything else in the data that can pull out what these cells are? More detailed analysis of the firing of these neurons might pull out something really interesting.

(6) Related to this - a number of comparisons simply pool neurons across mice and analyse them as if independent. This is done a lot in the past, but it would be better if an approach that included the interdependence of neurons recorded from the same mouse at the same time were used (such as a hierarchical model). While this is complex, a simpler approach would just be to plot the summary data also per mouse. For example, in Figure 5, how do the neurons inhibited by ACC activation spread across the different mice? Is the level of inhibition related to how well the mice learned the CS-US association?

(7) Figure 6 is interesting, but very preliminary. None of the effects are quantified, and one of the cell types is not identified. I think some proper analysis needs to be done, again across mice, to be able to draw conclusions from these data.

(8) Finally, in general, I felt that the way the paper was written was very hard to follow, often relying on very processed levels of analysis that were hard to relate back to the raw traces and their biological meaning. In general taking more words to really simply and fully explain each analysis, and taking the words and figures to walk through how each analysis was done and what it tells us about the neuronal data/biology would be really beneficial, especially to someone who is not an extracellular electrophysiologist or immersed in the immediate field.

In summary, while this manuscript explores an intriguing hypothesis about pre-learning circuit dynamics, it is currently held back by insufficient clarity in behavioural analysis, data presentation, and statistical quantification. Addressing these core issues would greatly improve interpretability and confidence in the findings.

Reviewer #1 (Public review):

Summary:

Zhang et al. addressed the question of whether hyperaltruistic preference is modulated by decision context and tested how oxytocin (OXT) may modulate this process. Using an adapted version of a previously well-established moral decision-making task, healthy human participants in this study undergo decisions that gain more (or lose less, termed as context) meanwhile inducing more painful shocks to either themselves or another person (recipient). The alternative choice is always less gain (or more loss) meanwhile less pain. Through a series of regression analyses, the authors reported that hyperaltruistic preference can only be found in the gain context but not in the loss context, however, OXT reestablished the hyperaltruistic preference in the loss context similar to that in the gain context.

Strengths:

This is a solid study that directly adapted a previously well-established task and the analytical pipeline to assess hyperaltruistic preference in separate decision contexts. Context-dependent decisions have gained more and more attention in literature in recent years, hence this study is timely. It also links individual traits (via questionnaires) with task performance, to test potential individual differences. The OXT study is done with great methodological rigor, including pre-registration. Both studies have proper power analysis to determine the sample size.

Weaknesses:

Despite the strengths, multiple analytical decisions have to be explained, justified, or clarified. Also, there is scope to enhance the clarity and coherence of the writing - as it stands, readers will have to go back and forth to search for information. Last, it would be helpful to add line numbers in the manuscript during the revision, as this will help all reviewers to locate the parts we are talking about.

Introduction:<br /> (1) The introduction is somewhat unmotivated, with key terms/concepts left unexplained until relatively late in the manuscript. One of the main focuses in this work is "hyperaltruistic", but how is this defined? It seems that the authors take the meaning of "willing to pay more to reduce other's pain than their own pain", but is this what the task is measuring? Did participants ever need to PAY something to reduce the other's pain? Note that some previous studies indeed allow participants to pay something to reduce other's pain. And what makes it "HYPER-altruistic" rather than simply "altruistic"? Plus, in the intro, the authors mentioned that the "boundary conditions" remain unexplored, but this idea is never touched again. What do boundary conditions mean here in this task? How do the results/data help with finding out the boundary conditions? Can this be discussed within wider literature in the Discussion section? Last, what motivated the authors to examine decision context? It comes somewhat out of the blue that the opening paragraph states that "We set out to [...] decision context", but why? Are there other important factors? Why decision context is more important than studying those others?

Experimental design:<br /> (2) The experiment per se is largely solid, as it followed a previously well-established protocol. But I am curious about how the participants got instructed? Did the experimenter ever mention the word "help" or "harm" to the participants? It would be helpful to include the exact instructions in the SI.

(3) Relatedly, the experimental details were not quite comprehensive in the main text. Indeed, Methods come after the main text, but to be able to guide readers to understand what was going on, it would be very helpful if the authors could include some necessary experimental details at the beginning of the Results section.

Statistical analysis<br /> (3) One of the main analyses uses the harm aversion model (Eq1) and the results section keeps referring to one of the key parameters of it (ie, k). However, it is difficult to understand the text without going to the Methods section below. Hence it would be very helpful to repeat the equation also in the main text. A similar idea goes to the delta_m and delta_s terms - it will be very helpful to give a clear meaning of them, as nearly all analyses rely on knowing what they mean.

(4) There is one additional parameter gamma (choice consistency) in the model. Did the authors also examine the task-related difference of gamma? This might be important as some studies have shown that the other-oriented choice consistency may differ in different prosocial contexts.

(5) I am not fully convinced that the authors included two types of models: the harm aversion model and logistic regression models. Indeed, the models look similar, and the authors have acknowledged that. But I wonder if there is a way to combine them? For example:<br /> Choice ~ delta_V * context * recipient (*Oxt_v._placebo)<br /> The calculation of delta_V follows Equation 1.<br /> Or the conceptual question is, if the authors were interested in the specific and independent contribution of dalta_m and dalta_s to behavior, as their logistic model did, why the authors examine the harm aversion first, where a parameter k is controlling for the trade-off? One way to find it out is to properly run different models and run model comparison. In the end, it would be beneficial to only focus on the "winning" model to draw inferences.

(6) The interpretation of the main OXT results needs to be more cautious. According to the operationalization, "hyperaltruistic" is the reduction of pain of others (higher % of choosing the less painful option) relative to the self. But relative to the placebo (as baseline), OXT did not increase the % of choosing the less painful option for others, rather, it decreased the % of choosing the less painful option for themselves. In other words, the degree of reducing other's pain is the same under OXT and placebo, but the degree of benefiting self-interest is reduced under OXT. I think this needs to be unpacked, and some of the wording needs to be changed. I am not very familiar with the OXT literature, but I believe it is very important to differentiate whether OXT is doing something on self-oriented actions vs other-oriented actions. Relatedly, for results such as that in Fig5A, it would be helpful to not only look at the difference, but also the actual magnitude of the sensitivity to the shocks, for self and others, under OXT and placebo.

Comments on revisions:

I did not change my original public review, as I think it can still be helpful for the field to see the reasoning and argument.

For the revision, the authors have done a thorough job of addressing my previous comments and questions.

The only aspect I would like to ask is that, it would still be great to have a clear definition of hyperaltruism. As it stands, hyperaltruism refers to "people's willingness to pay more to reduce other's pain than<br /> their own pain", ie, this means the "hyper" bit is considered with respect to "self". But shouldn't hyperaltruism be classified contrasting "normal" altruism?

It is fine that it follows a previously published work (Crockett et al., 2014), but it would still be necessary to explain/define the construct being tested in a standalone fashion rather than letting readers to go back to the original work.

Reviewer #3 (Public review):

Summary:

In this study, the authors aimed to index individual variation in decision-making when decisions pit the interests of the self (gains in money, potential for electric shock) against the interests of an unknown stranger in another room (potential for unknown shock). In addition, the authors conducted an additional study in which male participants were either administered intranasal oxytocin or placebo before completing the task to identify the role of oxytocin in moderating task responses. Participants' choice data was analyzed using a harm aversion model in which choices were driven by the subjective value difference between the less and more painful options.

Strengths:

Overall, I think this is a well-conducted, interesting, and novel set of research studies exploring decision-making that balances outcomes for the self versus a stranger, and the potential role of the hormone oxytocin (OT) in shaping these decisions. The pain component of the paradigm is well designed, as is the decision-making task, and overall the analyses were well suited to evaluating and interpreting the data. Advantages of the task design include the absence of deception, e.g., the use of a real study partner and real stakes, as a trial from the task was selected at random after the study and the choice the participant made were actually executed. 

Weaknesses:

The primary weakness of the paper concerns its framing. Although it purports to be measuring "hyper-altruism," which is the same term used in prior similar (although not identical) designs, I do not believe the task constitutes altruism, but rather the decision to engage, or not engage, in instrumental aggression.

I continue to believe that when in the "other" trials the only outcome possible for the study partner is pain, and the only outcome possible for the participant is monetary gain, these trials measure decisions about instrumental aggression. That is the exact definition of instrumental aggression is: causing others harm for personal gain. Altruism is not equivalent to refraining from engaging in instrumental aggression, although some similar mechanisms may support both. True altruism would be to accept shocks to the self for the other's benefit (e.g., money).  The interpretation of this task as assessing instrumental aggression is supported by the fact that only the Instrumental Harm subscale of the OUS was associated with outcomes in the task, but not the Impartial Benevolence subscale. By contrast, the IB subscale is the one more consistently associated with altruism (e.g,. Kahane et al 2018; Amormino at al, 2022) I believe it is important for scientific accuracy for the paper, including the title, to be rewritten to reflect what it is testing.

Although I recognize similar tasks have been previously characterized as "hyper-altruism" I do not believe that is sufficient justification for continuing to promulgate this descriptor without any caveats. I hope the authors will engage more seriously with the idea that this is what the task is measuring.

Relatedly, in the introduction, I believe it would be important to discuss the non-symmetry of moral obligations related to help/harm--we have obligations not to harm strangers but no obligation to help strangers. This is another reason I do not think the term "hyper altruism" is a good description for this task--given it is typically viewed as morally obligatory not to harm strangers, choosing not to harm them is not "hyper" altruistic (and again, I do not view it as obviously altruism at all).

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Reply to the reviewers

General Statement

*Our lab was totally destroyed on June 15th by an Iranian missile. All stocks, equipment and reagents were lost. While we performed many of the experiments requested by the reviewers, unfortunately some were never completed. We thank you for your understanding. *

We thank the three reviewers for their thoughtful comments and useful suggestions on how to improve our paper. Some of the reviewers claimed that the paper is “preliminary”. We would like to highlight that in our opinion “preliminary” has two possible meanings in this context: 1) the data does not yet support the claims that the authors wrote; 2) the story is short and should be extended. While we totally agree that type 1 “preliminary” should be addressed (and we have addressed that to the best of our abilities), type 2 “preliminary” is a matter of scope, the length of the paper/project and the publication home. We believe that this story, which has been led by an outstanding master’s student (and as such has had a limited timespan) is worthwhile of publication in its current scope.

2. Point-by-point description of the revisions

Reviewers’ comments are in BLUE while our responses are in BLACK.

Reviewer 1 Summary: This study reports a role for matrix metalloproteinases (MMPs) in the developmental pruning of gamma Kenyon cells (KCs) in the fruit fly Mushroom Body during larval-pupal metamorphosis. The authors show through gene expression studies that MMP genes are upregulated in late larval stages as part of the early program for this type of neuronal pruning. They show through cell-targeted RNAi studies of both secreted MMP-1 and membrane-anchored MMP-2, that both genes are required in glial cells and to a lesser extent within KCs.

Both MMPs have secreted and membrane-anchored isoforms and we did not assess whether the secreted/anchored isoforms are involved; e.g. see LaFever et al. 2017.

The authors show that MMP secreted from glial is required for normal levels of Mushroom Body developmental neuronal pruning. They mention that MMP genes have been identified in schizophrenic patient screens in patients, and that perhaps a comparable pruning mechanism could be involved in the loss of grey matter (loss of synapses) in patients. The authors propose that MMP levels may be a potential therapeutic marker in the future.

We thank the reviewer for his comments. We find it important to clarify that we do not think our work suggests that the MMPs levels may be a potential therapeutic marker without much additional work in the future. In the original text we added a claim from another paper suggesting MMPs as therapeutic target. However, due to the arising confusion, we decided to delete this statement from the text (original line 198). We also added a general disclaimer towards the end of the discussion regarding the genetic power of Drosophila but its limited implication into human health (new lines 276-278).

Major Comments: Overall, the work is of a reasonable standard, but very preliminary

Please see general note on two types of “preliminary” – we thank the reviewer for helping us substantiate our claims and strengthen our paper but we do not plan to significantly increase its scope.

The study lacks the substance to completely convince me of any of the results. There is SUBSTANTIAL work that needs to be done to make this publishable. There are a lot of writing mistakes; so many that I do not list them in detail here

We are not absolutely sure that we understand to which mistakes this reviewer is eluding. However, we carefully rewrote the manuscript, streamlined many of our claims and added many new and more recent references.

The references citations are fairly old, but I do not list update replacements here

Thanks – we added many newer and relevant citations.

The text is very brief, and the overall writing needs to include significantly more description and detail

We have included more descriptions and details, as will be elaborated later on, but – again - this is a short report and will remain as such.

This is evident in all aspects of the manuscript, but especially notable in the Methods and Figure Legends

Thanks for raising this comment, which was reverberated also by other reviewers – we have now included more details, with a particular focus on the genotypes (Table 2), that somehow were erroneously not included in the original submission, as well as more detailed figure legends.

None of the Figure Legends include full genotypes of any of the fly lines, and these full fly lines are also not included in the Methods. This is vital to compare the experimental lines to the controls

True – our apologies for this mistake, we now added the full genotypes in Table 2.

Major points are listed below:

1. Figure 2: It is important to note of the specific age of animals in these images when talking about the loss of genes in development. Are all the animals age-matched? High levels of synaptic pruning occur post-eclosion), and it is important to understand when these pruning defects occur. It is mentioned that that overlap for the gene expression data is upregulated during 6-18h APF is this when these images are taken? This is very important in the context of pruning as SCZ symptom presentation is very late relative to these early events.

We thank the reviewer for this comment which suggests we were not clear enough in our description. We do not claim to have generated an SCZ model and have clarified this better in the text (lines 275-278). Furthermore, axon pruning happens during pupal development, but in all the main figures in this manuscript we dissected young adult flies (3-5 days post eclosion) and show the remnants of unpruned axons (as we have done in numerous studies). To make sure that initial development occurred normally, we also include larval brains in the Figure S7. We now clarified the fact that we are imaging adult brains as a readout to investigate whether pruning occurred during metamorphosis or not (line 124-126).

1. Figure 2: In the figure legend, it is indicated that the arrows are unpruned axons, however in the controls these areas appear to be highly innervated. Further explanation is needed about the context of the arrows, as there are clear visual differences between these images and the controls, but they appear to have a more expansive phenotype than "unpruned axons". The data does not match the visual representation in comparison to the control.

We apologize for this confusion. Unfortunately, the driver which we use to label the γ-axons, R71G10-QF2, is not absolutely specific to the γ type KCs but also expressed (sometimes) in the ɑ/β KCs. As the ɑ/β axons are very stereotypic in shape and also express high levels of FasII (which we stain for), we can easily distinguish between the ɑ lobe and unpruned γ axons. To clarify this point, we now clearly demarcate all lobes in the control images and specifically the ɑ lobe in all panels. Additionally, we added new schemes in Figure 2A and 2O to better clarify the anatomy and experimental design.

1. Figure 2: There needs to be more descriptive definitions and clarifications to the defects labeled in panel K. This could be done in the figure legend, but it would be more useful to label the images provided. For example, if Mmp2 is a "mild pruning affect, put that in the pie chart somewhere, to help guide the description of the phenotype to what those confocal images look like.

We understand that the pie chart in Figure 2 was confusing and therefore simplified it in the current version (Fig. 2B and 2P). Also, thanks to this great point, we now include a new Figure S3 that includes examples for the ranking categories, which were now performed by two independent investigators in a blind manner.

Figure 3: The time points of the images of the Mushroom Body (MB) are vital to understanding the process and regulation of these genes.

Please see our comment to point #1 – unless specifically stated otherwise, all images are MBs of adult flies, as now clearly mentioned in the figure legends, in the text and in the Material and Methods section.

1. Figure 3D: Significant description of this graph needs to be added for clarity. What parameters separate each phenotypic defect? Labeling the images and showing images that belong in different groups would be very helpful and improve the paper significantly.

We now included a new Figure S3 (also see our response to comment #3).

1. Figure S1: Additional experiments would help answer the strength of the phenotype for the ALG-Gal 4 driver. The authors need to perform the rescue experiment. Use a MMP-2 null and then drive it back in the ALG-GAL4 to see if this is sufficient to rescue the neuron pruning. This also isolates the mechanisms to one subtype of glia.

These are excellent suggestions that are, unfortunately, not doable. To perform a rescue experiment, one would need a viable loss-of-function phenotype of an Mmp2 mutant. There is one published Mmp2 loss-of-function null allele which is lethal during pupal development (Page-McCaw et al, 2003). Our previous data, using tissue specific (ts)CRISPR, suggested the involvement of Mmp2 in neurons for their remodeling (Meltzer et al, 2019). We therefore independently generated an Mmp2 germline mutant using CRISPR (harboring an indel resulting in a premature stop codon and predicted to encode a truncated, 77 amino-acid long protein), now described in Fig. S5A (and in the Materials and Methods). This allele is, as expected, unfortunately also lethal. We attempted to overcome lethality by generating MARCM (mosaic) clones in neurons, but as expected, because Mmp2 is largely secreted, there was no pruning defect phenotype (Fig. S5B-C). Unfortunately, it is not yet possible to generate glial clones.

Figure 3 and 4: The other glial subtypes need to be analyze to make any conclusion about their involvement, as well as the involvement of the astrocytes. Running these exact same experiments on the cortex glial and ensheathing glia will provide essential insight into what glial subtype is involved. The presumed lack of phenotypes in these other glial subtypes will also strengthen the argument that the astrocytes are specifically involved in this process. These are vital experiments.

We currently limited our analysis (and conclusions) to astrocytes. Despite the fact that this experiment is beyond our initial scope, we obtained reagents and performed preliminary experiments (using the R77A03-Gal4 driver for cortex glia, and the R83E12-Gal4 for ensheathing glia). In both cases, we observed extremely mild pruning defects, not comparable to those with Repo- or Alrm-Gal4. In these preliminary experiments we lacked a proper control, and now, unfortunately, due to the loss of our lab, we are unable to complete these experiments in a reasonable amount of time.

1. Figure 4: Again, description of the phenotypes and examples of these would improve the quality of this figure substantially.

Absolutely agree – see our response to comment #3 (and Fig. S3).

1. Figure 5: An improvement on the quantifications of these phenotypes would strengthen the paper substantially. More detailed description of the phenotypes and how they related to the control would significantly improve the overall quality of the work.

Thanks again for highlighting that we neglected to include the full genotypes that are now added (Table 2). We also thank the reviewer for raising the point regarding quantification. First, we generated a new Fig. S3A-E to show examples of the ranking by two independent rankers. Second, ranking was performed by looking at TdTomato positive vertical axons that are outside of the ɑ lobe (high FasII) – this is now better explained in the materials and methods. Additionally, while we would love to have a better scoring, and automatic, system – and even published a semi-automated scoring algorithm in Alyagor et al. 2018 (Figure 3O in the Alyagor paper), because the driver also labels vertical axons (ɑ/β) and because unpruned γ axons often express FasII, this quantification method does not always work. What we have done in previous cases, as we have also done here, is to provide independent ranking by two investigators and compare their ranking (Fig. S3F-G). Finally, we are working with our AI hub to develop automatic scoring systems that will not require human ranking – however this is beyond the scope for this manuscript.

Minor Comments: 1. Figure 1A: I would suggest labeling the KC (gamma) and potentially one of the others (a/B, a'/B') to orient the reader to the differences between these two subsets of the KCs, and to emphasize which neurons are undergoing pruning and where the cell bodies are and where the axons project.

Thanks for the suggestions – we now better annotated the scheme in Figure 1A as well as additional schematics in Figure 2 and, finally, better annotations in selected panels. Specifically, the ɑ lobe is outlined in magenta throughout all relevant panels.

1. Figure 1C: This panel needs further labeling to explain the findings in the heat map. Labeling some of the genes that were found and where they were would be helpful. This could also be done in the figure legend, however without any further labeling or context the heatmap is confusing.

We apologize for the incomplete figure. We did not want to overload the figure with data, which is why we are showing only the important clusters and did not include gene names. To keep the figure simple, but at the same time provide the complete information, we now include the full data in Fig. S1 (that includes the original heatmap with all the dynamic clusters I-IX, and including all the gene names). For the full raw data, including non-dynamic clusters, the reader is referred to look in Supplemental excel file 1. We hope this provides the clarity that this reviewer rightfully asks for.

1. Figure 3B,C: The full genotypes need to be labeled. What is the exact genotype used for the control?

The full genotypes of all figure panels are now included in Table 2 in the Materials and Methods.

1. Figure S1: The stock number for the ALG-GAL4 is missing, there are multiple different drivers, therefore this could be helpful in understanding this phenotype, as some are better than others.

Indeed, Alrm-Gal4 comes on two chromosomes – we used BDSC #67032, which is on chromosome III and this is now clearly mentioned the Materials and Methods section.

1. Figures 3 and 4: Labeling needs to remain consistent; Figure 3 "Glia-Gal4", Figure 4 "glia-gal4".

Thanks, done.

Reviewer #1 (Significance (Required)):

General Assessment: An interesting study on MMP function during an unusual type of neural development (axon pruning). Most of the MMP function appears to be in glia, although the MMP role in this context in unclear. The MMP function in the neurons being pruned is unexpected and even less clear. The study is somewhat poorly described in terse language lacking essential information, which gives the overall impression of a preliminary report.

Advance: Glial MMP function has been described for neuronal clearance mechanisms following injury. The main advance here is to describe a similar function during normal development. Audience: Developmental neuroscientists, MMP biologists, possibly schizophrenia clinician researchers

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Neuropsychiatric conditions are often influenced by genetic factors. Schizophrenia is a complex mental disorder characterised by a mixture of hallucinations, delusions and disorganised thinking that causes lifelong problems in daily life. GWAS have identified a number of genes associated with the risk of developing schizophrenia, although genetic predisposition alone is not sufficient and additional environmental factors are required. In the current manuscript, the authors aim to exploit the strength of the Drosophila system to explore a link between schizophrenia-associated genes and neuronal remodelling during development. They focus on the mushroom body in the adult brain, where pronounced neuronal remodelling occurs during metamorphosis. To assess the potential role of the genes identified by the GWAS, they performed a targeted RNAi-based screen. They focus on the role of metalloproteases and find that they are required in neurons and in glia for the pruning of mushroom body axons. The study starts with a selection of 32 genes, 29 of which are listed (a bit hidden) in materials and methods and the identification of the Drosophila orthologs. The expression patterns of these genes in Kenyon cells are presented in Figure 1 - but unfortunately no information is given on who is expressed when

We apologize for the confusion. We attempted to keep Figure 1 simple but this resulted in the absence of critical information, as the reviewer suggests. We now include a Figure S1 that includes the entire heatmap of the dynamically expressed clusters I-IX with all the gene names. Additionally, we now augmented the information in Table 1 to include the screen phenotypes. Finally, Supplemental excel file 1, also included in our original submission, includes all the data, and is now better referred to throughout the text.

In a next step, Kenyon cell specific RNAi knockdown experiments are shown that identify a pruning phenotype for several genes. They demonstrate that Mmp2 (and similarly Mmp1) is also required in glia. Although Mmp2 was identified by neuronal RNAi-based knockdown, double knockdown experiments led the authors conclude that its primary function is in glia. The study emphasises the use of the advanced genetic model to understand complex human diseases. However, the paper does not go far enough in making use of the excellent genetics available. Basically, the report is about the identification of a few hits in a small RNAi screen, which is fine in itself, but leaves many questions unanswered. Do mmp1/2 mutants have a phenotype?

This is a very important question that cannot be answered, unfortunately. There is one published Mmp2 loss of function null allele which is lethal during pupal development (Page-MaCaw et al, 2003). Our previous data, using tissue specific (ts)CRISPR, suggested the involvement of Mmp2 in neurons for their remodeling (Meltzer et al, 2019). We therefore independently generated an Mmp2 germline mutant using CRISPR (harboring an indel resulting in a premature stop codon and predicted to encode a truncated, 77 amino-acid long protein), now described in Fig. S5A (and in the Materials and Methods). This allele is, as expected, unfortunately also lethal. We attempted to overcome lethality by generating MARCM (mosaic) clones in neurons, but as expected, because Mmp2 is largely secreted, there was no pruning defect phenotype (Fig. S5B-C). Unfortunately, it is not yet possible to generate glial clones. Additionally, available Mmp1 mutants are, sadly, also homozygous lethal. That said, in our revised manuscript we now include data demonstrating that expression of a dominant negative variant of Mmp1 inhibits pruning (Fig. 3J-K). We strengthened the evidence regarding the reliability of Mmp1 RNAi using an antibody mix (Fig. S4), and for Mmp2 – we refer to a manuscript that tested its efficiency (Harmansa et al., 2023). Lastly, we added new data using an additional RNAi line targeting Mmp2 from the VDRC collection (Fig. 3L).

Can the phenotype be rescued?

Unfortunately, without a viable mutant LOF phenotype, a rescue experiment is impossible. Regardless, in an attempt to rescue the RNAi phenotype, we designed and generated an RNAi-resistant Mmp2 overexpression transgene. Unfortunately, due to the destruction of our lab – several days after we received this transgenic line from Bestgene – this experiment is not included in the revision.

Does TIMP expression lead to similar phenotypes?

This is an interesting question which we addressed in our experiments but did not include in the text. Unfortunately, overexpression of TIMP did not have any effect on MB development. We are adding this figure here as Reviewer Figure 1, but we think that adding this information to the paper will not improve it for several reasons. The lack of phenotype by overexpression of Timp can result from a technical issue such as low expression or mislocalization of the protein, or a biological issue such as more complicated involvement of TIMP or other MMP inhibitors.

What is the temporal requirement for Mmp1/2?

This is an excellent suggestion, not an easy experiment, but one that we initiated, using a temperature sensitive Gal80 to control the expression of the RNAi only during metamorphosis. However, to the unfortunate destruction of our lab, this experiment was never completed.

What are the target proteins of Mmp2?

This is the million-dollar question – but unfortunately is beyond the scope of this short report.

Is Mmp2 still required when astrocyte motility is blocked? What is the morphology of glia after Mmp1/2 knockdown?

Thank you for this wonderful suggestion. We initiated two types of experiments using sparse labeling techniques (both MARCM and SPARC) to identify the morphology of single astrocytes in WT vs. MMP KD. However, these are complicated crosses that were not completed prior to the destruction of our lab.

Reviewer #2 (Significance (Required)):

The strength of the study is to identify a pruning phenotype after RNAi-based knockdown. The limitations is that this study is very superficial, it is the beginning of a paper. The initial claim to use Drosophila because to its advanced genetics is not met. The results section is shorter than the discussion.

While we agree with much of the reviewer’s statement this also relates to our general comment about “preliminary” type 1 and type 2 – True, this could be the beginning of a big paper and it would definitely be a more comprehensive and deep story. Most of the papers from my lab are indeed a 5 year endeavor. However, this short report (which is now longer, more detailed, and includes additional experiments) is a result of the work of an outstanding master’s student who came up with the idea for the project entirely by herself. Thus – given the data that she has acquired, and the fact that my lab will not continue to study MMPs or schizophrenia, the question needs to be whether the data supports the claims and whether this is an advance of science worthwhile of publication in a respectable journal. Our clear and decisive opinion is that the answer to that question is yes.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

In this work, Schuldiner and colleagues explore the role of Mmp1 and Mmp2 in neuronal remodeling in the mushroom body of Drosophila. Overall, this work is very interesting, but in its current form seems quite preliminary. The biggest limitation of the study is that single RNAi lines are used with no validation that the lines are working, despite the fact that Mmp antibodies are available as are endogenously tagged Mmp lines that could have been used to validate the genetic manipulations. Specific concerns are listed below.

We thank reviewer 3 for his generally positive assessment of our work and we now performed additional experiments to strengthen and validate the original RNAi findings – for specifics see our reply to the points below.

Major concerns 1) The scoring system for pruning of mushroom body neurons seems very variable, even in controls (where scoring can range from very mild to moderate), and it is very hard to assess from the images what one is looking at (rather than using our own judgment, we rely on the authors' words). It would be necessary to have better labeling and examples of what phenotypes are considered "mild", "severe", "wild type-like". It would also help to understand how phenotype assessment is guided by the overlap between the signals from TdTomato fluorescence and FasII stain.

We thank the reviewer for raising this point, that has also been highlighted by other reviewers in some form. First, we have generated Figure S3A-E to show examples of the ranking, which was now performed by two independent investigators. Second, ranking was performed by looking at TdTomato positive vertical axons that are outside of the αlobe (high FasII) – this is now better explained in the materials and methods. Additionally, while we would love to have a better scoring, and automatic, system – and even published a semi-automated scoring algorithm in Alyagor et al. 2018 (Figure 3O in the Alyagor paper), because the driver also labels vertical axons (ɑ/β) and because unpruned γ axons often express FasII, this quantification method does not always work. What we have done in previous cases, as we have also done here, is to provide independent ranking by two investigators and compare their ranking (Fig. S3F-G). Finally, we are working with our AI hub to develop automatic scoring systems that will not require human ranking – however this is beyond the scope for this manuscript.

2) The biggest limitations of the approach are that single RNAi lines are used to screen, with no accompanying validation of the tool (see above)

We agree. Unfortunately not all RNAis are “equal” and thus not all of them work. To support the RNAi data, we have better clarified previous experiments that demonstrate the importance of neuronal Mmp2 via tissue specific (ts) CRISPR (Meltzer, et al, 2019). Unfortunately, the Mmp2 null mutant that is available is lethal during pupal development (Page-MaCaw et al, 2003). We therefore independently generated an Mmp2 germline mutant using CRISPR (harboring an indel resulting in a premature stop codon and predicted to encode a truncated, 77 amino-acid long protein), now described in Fig. S5A (and in the Materials and Methods). This allele is, as expected, unfortunately also lethal. We attempted to overcome lethality by generating MARCM (mosaic) clones in neurons, but as expected, because Mmp2 is largely secreted, there was no pruning defect phenotype (Fig. S5B-C). Unfortunately, it is not yet possible to generate glial clones. Additionally, available Mmp1 mutants are, sadly, also homozygous lethal. That said, in our revised manuscript we now include data demonstrating that expression of a dominant negative variant of Mmp1 inhibits pruning (Fig. 3J-K). We strengthened the evidence regarding the reliability of Mmp1 RNAi using an antibody mix (Fig. S4), and for Mmp2 – we refer to a manuscript that tested its efficiency (Harmansa et al., 2023). Lastly, we added new data using an additional RNAi line targeting Mmp2 from the VDRC collection (Fig. 3L).

3) RNAi-based knockdown is used to infer epistatic information-this is not appropriate as epistasis experiments need to be done with null alleles to make firm conclusions. Additional concerns: ● Even with the same driver, knockdown efficiency for 2 different genes could be variable and dependent of the specific RNAi used. ● The comparison between drivers is even harder, as driver strength varies greatly. ● The knockdown efficiency drops with increasing numbers of RNAi used. ● The specific genotypes used for this experiment should be clarified, as it would be very important to ensure that the UAS dosage is equal across conditions.

We agree that RNAi is not optimal to assess epistasis. And indeed, we did not mean to claim epistasis relationship between Mmp1 and Mmp2, nor between neurons and glia. We now use better language to clarify this. To define epistatic relationships, the use of mutants would be required, unfortunately the use of nulls is not possible because they are lethal and secreted (thus not enabling mosaic analyses). We agree that increasing the number of RNAi lines is expected to reduce their efficiency – this is why it is even more significant when we see an increased defective phenotype in the double knockdown experiments. Finally, we totally agree about the genotype comment and apologize that it was erroneously omitted in the original submission– all of which have been now added (Table 2 in materials and methods).

4) To further deepen the rigor of this work, a few simple yet important things could have been done. First, it would be important to rule out that knocking down Mmps does not affect astrocyte numbers and health (could be assessed by counting numbers and observing their morphology). Also, the authors previously showed that astrocytes actively infiltrate the axon bundle prior to pruning to facilitate axon defasciculation and pruning (Marmor-Kollet et al., 2023). It would have provided an important insight to examine if astrocytes can infiltrate the axon bundle if Mmp2 and/or Mmp1 are knocked down.

Thank you for these wonderful suggestions. We embarked on a few experiments as detailed below, unfortunately these are complicated crosses that were not completed prior to the destruction of our lab. 1) We initiated two types of experiments using sparse labeling techniques (both MARCM and SPARC) to identify the morphology of single astrocytes in WT vs. MMP KD. 2) Testing astrocytic infiltrations requires three binary systems, we obtained and generated stocks required for these experiments, but these were prematurely terminated. 3) We initiated experiments to count the number of glial nuclei in the vicinity of the degenerating axonal lobe (at the onset of pruning). Preliminary experiments with a small n (3 controls, 4 Mmp1 RNAi, and 5 Mmp2 RNAi) suggest that the number of glial nuclei is not significantly different between these conditions.

Minor The introduction puts big emphasis on the role of glia, but then to narrows down candidate genes for the screen a γ-KCs transcriptional data set is used, and the initial screen is done via knockdown of those candidates in neurons (there is a disconnect between rationale and approach).

We totally agree with this reviewer which is why we now changed the paper to include both neuronal and glial loss-of-function screens. Figure 1 is now augmented with the glial data.

Rationale for looking into axon pruning and how that translates into insights about synaptic pruning defects in schizophrenia should be more clearly stated.

Indeed, our belief that synapse pruning and axon pruning share molecular mechanisms remains yet unproven. However, both are steps during neuronal remodeling, which has been previously implicated in schizophrenia. That said, we now added an additional disclaimer to acknowledge the limitation of our findings in the context of human disease and synapse elimination (lines 275-279).

Figure 1C: data visualization for this heat map should be improved. Parts of the data are faded, and the differences between gene clusters are unclear.

We apologize for the incomplete figure. We did not want to overload the figure with data, which is why we are showing only the important clusters and did not include gene names. To keep the figure simple, but at the same time provide the complete information, we now include the full data in Fig. S1 (that includes the original heatmap with all the dynamic clusters I-IX, and including all the gene names). For the full raw data, including non-dynamic clusters, the reader is referred to look in Supplemental excel file 1. We hope this provides the clarity that this reviewer rightfully asks for.

Reviewer #3 (Significance (Required)):

In this work, Schuldiner and colleagues explore the role of Mmp1 and Mmp2 in neuronal remodeling in the mushroom body of Drosophila. Overall, this work is very interesting, but in its current form seems quite preliminary. The biggest limitation of the study is that single RNAi lines are used with no validation that the lines are working, despite the fact that Mmp antibodies are available as are endogenously tagged Mmp lines that could have been used to validate the genetic manipulations.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

We thank the reviewers for providing us the opportunity to revise our manuscript titled “Identifying regulators of associative learning using a protein-labelling approach in C. elegans.” We appreciate the insightful feedback that we received to improve this work. In response, we have extensively revised the manuscript with the following changes: we have (1) clarified the criteria used for selecting candidate genes for behavioural testing, presenting additional data from ‘strong’ hits identified in multiple biological replicates (now testing 26 candidates, previously 17), (2) expanded our discussion of the functional relevance of validated hits, including providing new tissue-specific and neuron class-specific analyses, and (3) improved the presentation of our data, including visualising networks identified in the ‘learning proteome’, to better highlight the significance of our findings. We also substantially revised the text to indicate our attempts to address limitations related to background noise in the proteomic data and outlined potential refinements for future studies. All revisions are clearly marked in the manuscript in red font. A detailed, point-by-point response to each comment is provided below.

1. Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Summary:

Rahmani et al., utilize the TurboID method to characterize the global proteome changes in the worm's nervous system induced by a salt-based associative learning paradigm. Altogether, Rahmani et al., uncover 706 proteins that are tagged by the TurboID method specifically in samples extracted from worms that underwent the memory inducing protocol. Next, the authors conduct a gene enrichment analysis that implicates specific molecular pathways in salt-associative learning, such as MAP-kinase and cAMP-mediated pathways. The authors then screen a representative group of the hits from the proteome analysis. The authors find that mutants of candidate genes from the MAP-kinase pathway, namely dlk-1 and uev-3, do not affect the performance in the learning paradigm. Instead multiple acetylcholine signaling mutants significantly affected the performance in the associative memory assay, e.g., acc-1, acc-3, gar-1, and lgc-46. Finally, the authors demonstrate that the acetylcholine signaling mutants did not exhibit a phenotype in similar but different conditioning paradigms, such as aversive salt-conditioning or appetitive odor conditioning, suggesting their effect is specific to appetitive salt conditioning.

Major comments:

1. The statistical approach and analysis of the behavior assay: The authors use a 2-way ANOVA test which assumes normal distribution of the data. However, the chemotaxis index used in the study is bounded between -1 and 1, which prevents values near the boundaries to be normally distributed.

Since most of the control data in this assay in this study is very close to 1, it strongly suggests that the CI data is not normally distributed and therefore 2-way ANOVA is expected to give skewed results.

I am aware this is a common mistake and I also anticipate that most conclusions will still hold also under a more fitting statistical test.

We appreciate the point raised by Reviewer 1 and understand the importance of performing the correct statistical tests.

The statistical tests used in this study were chosen since parametric tests, particularly ANOVA tests to assess differences between multiple groups, are commonly used to assess behaviour in the C. elegans learning and memory field. Below is a summary of the tests used by studies that perform similar behavioural tests cited in this work, as examples:

Table 1 | A summary for the statistical tests performed by similar studies for chemotaxis assay data. References (listed in the leftmost column) were observed to (A) use parametric tests only or (B) performed either a parametric or non-parametric test on each chemotaxis assay dataset depending on whether the data passed a normality test. Listings for ANOVA tests are in bold to demonstrate their common use in the C. elegans learning and memory field.

Reference

Parametric test/s used in the reference

Non-parametric test/s used in the reference

Beets et al., 2020

Two-way ANOVA

None

Hiroki & Iino 2022

One-way ANOVA

None

Hiroki et al., 2022

One-way ANOVA

None

Hukema et al., 2006

T-tests

None

Hukema et al., Learn. Mem. 2008

T-tests

None

Jang et al., 2019

ANOVA

None

Kitazono et al., 2017

Two-way ANOVA and t-tests

None

Lans et al., 2004

One-way ANOVA

None

Lim et al., 2018

Two-way ANOVA

Wilcoxon rank sum test adjusted with the Benjamini–Hochberg method

Lin et al., 2010

Two-way or three-way ANOVA

None

Nagashima et al., 2019

One-way ANOVA

None

Ohno et al., 2014

None

Sakai et al., 2017

One-way ANOVA or t-tests

None

Stein & Murphy 2014

Two-way ANOVA and t-tests

None

Tang et al., 2023

One-way ANOVA or t-tests

None

Tomioka et al., 2006

T tests

None

Watteyne et al., 2020

One-way ANOVA

Two-sided Kruskal–Wallis

We note Reviewer 1's concern that this may stem from a common mistake. As stated, Two-way ANOVA generally relies on normally distributed data. We used GraphPad Prism to perform the Shapiro-Wilk normality test on our chemotaxis assay data as it is generally appropriate for sample sizes Table 2 | Shapiro-Wilk normality test results for chemotaxis assay data in Figure S8C. Chemotaxis assay data was generated to assess salt associative learning capacity for wild-type (WT) versus lgc-46(-) mutant C. elegans. Three experimental groups were prepared for each C. elegans strain (naïve, high-salt control, and trained). From top-to-bottom, the data below displays the ‘W’ value, ‘P value’, a binary yes/no for whether the data passes the Shapiro-Wilk normality test, and a ‘P value summary’ (ns = non-significant). W values measure the similarity between a normal distribution and the chemotaxis assay data. Data is considered normal in the Shapiro-Wilk normality test when a W value is near 1.0 and the null hypothesis is not rejected (i.e., P value > 0.05).*

WT naïve

WT high-salt control

WT trained

lgc-46 naïve

lgc-46 high-salt control

lgc-46 trained

W

0.9196

0.9114

0.8926

0.8334

0.8151

0.8769

P value

0.5272

0.4758

0.3705

0.1475

0.1070

0.2954

Passed normality test (alpha=0.05)?

Yes

Yes

Yes

Yes

Yes

Yes

P value summary

ns

ns

ns

ns

ns

ns

The manuscript now includes the use of the Shapiro-Wilk normality test to assess chemotaxis assay data before using two-way ANOVA on page 51.

Nevertheless an appropriate statistical analysis should be performed. Since I assume the authors would wish to take into consideration both the different conditions and biological repeats, I can suggest two options:

• Using a Generalized linear mixed model, one can do with R software.

• Using a custom bootstrapping approach. We thank Reviewer 1 for suggesting these two options. We carefully considered both approaches and consulted with the in-house statistician at our institution (Dr Pawel Skuza, Flinders University) for expert advice to guide our decision. In summary:

• Generalised linear mixed models: Generalised linear mixed models (GLMMs) are generally most appropriate for nested/hierarchal data. However, our chemotaxis assay data does not exhibit such nesting. Each biological replicate (N) consists of three technical replicates, which are averaged to yield a single chemotaxis index per N. Our statistical comparisons are based solely on these averaged values across experimental groups, making GLMMs less applicable in this context.

• __Bootstrapping: __Based on advice from our statistician, while bootstrapping can be a powerful tool, its effectiveness is limited when applied to datasets with a low number of biological replicates (N). Bootstrapping relies on resampling existing data to simulate additional observations, which may artificially inflate statistical power and potentially suggest significance where the biological effect size is minimal or not meaningful. Increasing the number of biological replicates to accommodate bootstrapping could introduce additional variability and compromise the interpretability of the results. The total number of assays, especially controls, varies quite a bit between the tested mutants. For example compare the acc-1 experiment in Figure 4.A., and gap-1 or rho-1 in Figure S4.A and D. It is hard to know the exact N of the controls, but I assume that for example, lowering the wild type control of acc-1 to equivalent to gap-1 would have made it non significant. Perhaps the best approach would be to conduct a power analysis, to know what N should be acquired for all samples.

We thoroughly evaluated performing the power analysis: however, this is typically performed with the assumption that an N = 1 represents a singular individual/person. An N =1 in this study is one biological replicate that includes hundreds of worms, which is why it is not typically employed in our field for this type of behavioural test.

Considering these factors, we have opted to continue using a two-way ANOVA for our statistical analysis. This choice aligns with recent publications that employ similar experimental designs and data structures. Crucially, we have verified that our data meet the assumptions of normality, addressing key concerns regarding the suitability of parametric testing. We believe this approach is sufficiently rigorous to support our main conclusions. This rationale is now outlined on page 51.

To be fully transparent, our aim is to present differences between wild-type and mutant strains that are clearly visible in the graphical data, such that the choice of statistical test does not become a limiting factor in interpreting biological relevance. We hope this rationale is understandable, and we sincerely appreciate the reviewer’s comment and the opportunity to clarify our analytical approach.

We hope that Reviewer 1 will appreciate these considerations as sufficient justification to retain the statistical tests used in the original manuscript. Nevertheless, to constructively address this comment, we have performed the following revisions:

1. __Consistent number of biological replicates: __We performed additional biological replicates of the learning assay to confirm the behavioural phenotypes for the key candidates described (KIN-2 , F46H5.3, ACC-1, ACC-3, LGC-46). We chose N = 5 since most studies cited in this paper that perform similar behavioural tests do the same (see the table below). Table 3 | A summary for sample sizes generated by similar studies for chemotaxis assay data. References (listed in the leftmost column) were observed to the sample sizes (N) below corresponding to biological replicates of chemotaxis assay data. N values are in bold when the study uses N ≤ 5.

Reference

N used in the study for chemotaxis assay data

Beets et al., 2020

8

Hiroki & Iino 2022

5-8

Hiroki et al., 2022

6-7

Hukema et al., 2006

≥ 4

Hukema et al., Learn. Mem. 2008

≥ 4

Jang et al., 2019

≥ 4

Kitazono et al., 2017

≥ 4

Kauffman et al., 2010

≥ 3

Kauffman et al., J. Vis. Exp. 2011

≥ 3

Lans et al., 2004

2

Lim et al., 2018

2-4

Lin et al., 2010

≥ 4

Nagashima et al., 2019

≥ 7

Ohno et al., 2014

≥ 11

Sakai et al., 2017

≥ 4

Stein & Murphy 2014

3-5

Tang et al., 2023

≥ 9

Watteyne et al., 2020

≥ 10

__Grouped presentation of behavioural data: __We now present all behavioural data by grouping genotypes tested within the same biological replicate, including wild-type controls, rather than combining genotypes tested separately. This ensures that each graph displays data from genotypes sharing the same N, also an important consideration for performing parametric tests. Accordingly, we re-performed statistical analyses using this reduced Nfor relevant graphs. As anticipated, this rendered some comparisons non-significant. All statistical comparisons are clearly indicated on each graph. Improved clarity of figure legends: __We revised figure legends for __Figures 5, 6, S7, S8, & S9 to make clear how many biological replicates have been performed for each genotype by adding N numbers for each genotype in all figures.

The authors use the phrasing "a non-significant trend", I find such claims uninterpretable and should be avoided. Examples: Page 16. Line 7 and Page 18, line 16.

This is an important point. While we were not able to find the specific phrasing "a non-significant trend" from this comment in the original manuscript, we acknowledge that referring to a phenotype as both a trend and non-significant may confuse readers, which was originally stated in the manuscript in two locations.

The main text has been revised on pages 27 & 28 when describing comparisons between trained groups between two C. elegans lines, by removing mentions of trends and retaining descriptions of non-significance.

Neuron-specific analysis and rescue of mutants:

Throughout the study the authors avoid focusing on specific neurons. This is understandable as the authors aim at a systems biology approach, however, in my view this limits the impact of the study. I am aware that the proteome changes analyzed in this study were extracted from a pan neuronally expressed TurboID. Yet, neuron-specific changes may nevertheless be found. For example, running the protein lists from Table S2, in the Gene enrichment tool of wormbase, I found, across several biological replicates, enrichment for the NSM, CAN and RIG neurons. A more careful analysis may uncover specific neurons that take part in this associative memory paradigm. In addition, analysis of the overlap in expression of the final gene list in different neurons, comparing them, looking for overlap and connectivity, would also help to direct towards specific circuits.

This is an important and useful suggestion. We appreciate the benefit in exploring the data from this study from a neuron class-specific lens, in addition to the systems-level analyses already presented.

The WormBase gene enrichment tool is indeed valuable for broad transcriptomic analyses (the findings from utilising this tool are now on page 16); however, its use of Anatomy Ontology (AO) terms also contains annotations from more abundant non-neuronal tissues in the worm. To strengthen our analysis and complement the Wormbase tool, we also used the CeNGEN database as suggested by Reviewer 3 Major Comment 1 (Taylor et al., 2021), which uses single cell RNA-Seq data to profile gene expression across the C. elegans nervous system. We input our learning proteome data into CeNGEN as a systemic analysis, identifying neurons highly represented by the learning proteome (on pages 16-20). To do this, we specifically compared genes/proteins from high-salt control worms and trained worms to identify potential neurons that may be involved in this learning paradigm. Briefly, we found:

• WormBase gene enrichment tool: Enrichment for anatomy terms corresponding to specific interneurons (ADA, RIS, RIG), ventral nerve cord neurons, pharyngeal neurons (M1, M2, M5, I4), PVD sensory neurons, DD motor neurons, serotonergic NSM neurons, and CAN.
• CeNGEN analysis: Representation of neurons previously implicated in associative learning (e.g., AVK interneurons, RIS interneurons, salt-sensing neuron ASEL, CEP & ADE dopaminergic neurons, and AIB interneurons), as well as neurons not previously studied in this context (pharyngeal neurons I3 & I6, polymodal neuron IL1, motor neuron DA9, and interneuron DVC). Methods are detailed on pages 50 & 51. These data are summarised in the revised manuscript as Table S7 & Figure 4.

To further address the reviewer’s suggestion, we examined the overlap in expression patterns of the validated learning-associated genes acc-1, acc-3, lgc-46, kin-2, and F46H5.3 across the neuron classes above, using the CeNGEN database. This was done to explore potential neuron classes in which these regulators may act in to regulate learning. This analysis revealed both shared and distinct expression profiles, suggesting potential functional connectivity or co-regulation among subsets of neurons. To summarise, we found:

• All five learning regulators are expressed in RIM interneurons and DB motor neurons.
• KIN-2 and F46H5.3 share the same neuron expression profile and are present in many neurons, so they may play a general function within the nervous system to facilitate learning.
• ACC-3 is expressed in three sensory neuron classes (ASE, CEP, & IL1).
• In contrast, ACC-1 and LGC-46 are expressed in neuron classes (in brackets) implicated in gustatory or olfactory learning paradigms (AIB, AVK, NSM, RIG, & RIS) (Beets et al., 2012, Fadda et al., 2020, Wang et al., 2025, Zhou et al., 2023, Sato et al., 2021), neurons important for backward or forward locomotion (AVE, DA, DB, & VB) (Chalfie et al., 1985), and neuron classes for which their function is yet detailed in the literature (ADA, I4, M1, M2, & M5). These neurons form a potential neural circuit that may underlie this form of behavioural plasticity, which we now describe in the main text on pages 16-20 & 34-35 and summarise in Figure 4.

OPTIONAL: A rescue of the phenotype of the mutants by re-expression of the gene is missing, this makes sure to avoid false-positive results coming from background mutations. For example, a pan neuronal or endogenous promoter rescue would help the authors to substantiate their claims, this can be done for the most promising genes. The ideal experiment would be a neuron-specific rescue but this can be saved for future works.

We appreciate this suggestion and recognise its potential to strengthen our manuscript. In response, we made many attempts to generate pan-neuronal and endogenous promoter re-expression lines. However, we faced several technical issues in transgenic line generation, including poor survival following microinjection likely due to protein overexpression toxicity (e.g., C30G12.6, F46H5.3), and reduced animal viability for chemotaxis assays, potentially linked to transgene-related reproductive defects (e.g., ACC-1). As we have previously successfully generated dozens of transgenic lines in past work (e.g. Chew et al., Neuron 2018; Chew et al., Phil Trans B 2018; Gadenne/Chew et al., Life Science Alliance 2022), we believe the failure to produce most of these lines is not likely due to technical limitations. For transparency, these observations have been included in the discussion section of the manuscript on pages 39 & 40 as considerations for future troubleshooting.

Fortunately, we were able to generate a pan-neuronal promoter line for KIN-2 that has been tested and included in the revised manuscript. This new data is shown in Figure 5B __and described on __pages 23 & 24. Briefly, this shows that pan-neuronal expression of KIN-2 from the ce179 mutant allele is sufficient to reproduce the enhanced learning phenotype observed in kin-2(ce179) animals, confirming the role of KIN-2 in gustatory learning.

To address the potential involvement of background mutations (also indicated by Reviewer 4 under ‘cross-commenting’), we have also performed experiments with backcrossed versions of several mutants. These experiments aimed to confirm that salt associative learning phenotypes are due to the expected mutation. Namely, we assessed kin-2(ce179) mutants that had been backcrossed previously by another laboratory, as well as C30G12.6(-) and F46H5.3(-) animals backcrossed in this study. Although not all backcrossed mutants retained their original phenotype (i.e., C30G12.6) (Figure 6D, a newly added figure), we found that backcrossed versions of KIN-2 and F46H5.3 both robustly showed enhanced learning (Figures 5A & 6B). This is described in the text on pages 23-26.

__Minor comments: __

1. Lack of clarity regarding the validation of the biotin tagging of the proteome. The authors show in Figure 1 that they validated that the combination of the transgene and biotin allows them to find more biotin-tagged proteins. However there is significant biotin background also in control samples as is common for this method. The authors mention they validated biotin tagging of all their experiments, but it was unclear in the text whether they validated it in comparison to no-biotin controls, and checked for the fold change difference.

This is an important point: We validated our biotin tagging method prior to mass spectrometry by comparing ‘no biotin’ and ‘biotin’ groups. This is shown in Figure S1 in the revised manuscript, which includes a western blot comparing untreated and biotin treated animals that are non-transgenic or expressing TurboID. As expected, by comparing biotinylated protein signal for untreated and treated lanes within each line, biotin treatment increased the signal 1.30-fold for non-transgenic and 1.70-fold for TurboID C. elegans. This is described on __page 8 __of the revised manuscript.

To clarify, for mass spectrometry experiments, we tested a no-TurboID (non-transgenic) control, but did not perform a no-biotin control. We included the following four groups: (1) No-TurboID ‘control’ (2) No-TurboID ‘trained’, (3) pan-neuronal TurboID ‘control’ and (4) pan-neuronal TurboID ‘trained’, where trained versus control refers to whether ‘no salt’ was used as the conditioned stimulus or not, respectively (illustrated in Figure 1A). Due to the complexity of the learning assay (which involves multiple washes and handling steps, including a critical step where biotin is added during the conditioning period), and the need to collect sufficient numbers of worms for protein extraction (>3,000 worms per experimental group), adding ‘no-biotin’ controls would have doubled the number of experimental groups, which we considered unfeasible for practical reasons. This is explained on __pages 8 & 9 __of the revised manuscript.

Also, it was unclear which exact samples were tested per replicate. In Page 9, Lines 17-18: "For all replicates, we determined that biotinylated proteins could be observed ...", But in Page 8, Line 24 : "We then isolated proteins from ... worms per group for both 'control' and 'trained' groups,... some of which were probed via western blotting to confirm the presence of biotinylated proteins".

• Could the authors specify which samples were verified and clarify how?

Thank you for pointing out these unclear statements: We have clarified the experimental groups used for mass spectrometry experiments as detailed in the response above on pages 8 &____ 9. In addition, western blots corresponding to each biological replicate of mass spectrometry data described in the main text on page 10 and have been added to the revised manuscript (as Figure S3). These western blots compare biotinylation signal for proteins extracted from (1) No-TurboID ‘control’ (2) No-TurboID ‘trained’, (3) pan-neuronal TurboID ‘control’ and (4) pan-neuronal TurboID ‘trained’. These blots function to confirm that there were biotinylated proteins in TurboID samples, before enrichment by streptavidin-mediated pull-down for mass spectrometry.

OPTIONAL: include the fold changes of biotinylated proteins of all the ones that were tested. Similar to Figure 1.C.

This is an excellent suggestion. As recommended by the reviewer, we have included fold-changes for biotinylated protein levels between high-salt control and trained groups (on pages 9 & 10 for replicate #1 and in __Table S2 __for replicates #2-5). This was done by measuring protein levels in whole lanes for each experimental group per biological replicate within western blots (__Figure 1C __for replicate #1 and __Figure S3 __for replicates #2-5) of protein samples generated for mass spectrometry (N = 5).

Figure 2 does not add much to the reader, it can be summarized in the text, as the fraction of proteins enriched for specific cellular compartments.

• I would suggest to remove Figure 2 (originally written as figure 3) to text, or transfer it to the supplementry material.

As noted in cross-comment response to Reviewer 4, there were typos in the original figure references, we have corrected them above. Essentially, this comment is referring to Figure 2.

We appreciate this feedback from Reviewer 1. We agree that the original __Figure 2 __functions as a visual summary from analysis of the learning proteome at the subcellular compartment level. However, it also serves to highlight the following:

• Representation for neuron-specific GO terms is relatively low, but even this small percentage represents entire protein-protein networks that are biologically meaningful, but that are difficult to adequately describe in the main text.
• TurboID was expressed in neurons so this figure supports the relevance of the identified proteome to biological learning mechanisms.

• Many of these candidates could not be assessed by learning assay using single mutants since related mutations are lethal or substantially affect locomotion. These networks therefore highlight the benefit in using strategies like TurboID to study learning. We have chosen to retain this figure, moving it to the supplementary material as Figure S4 in the revised manuscript, as suggested.

• OPTIONAL- I would suggest the authors to mark in a pathway summary figure similar to Figure 3 (originally written as Figure 4) the results from the behavior assay of the genetic screen. This would allow the reader to better get the bigger picture and to connect to the systemic approach taken in Figures 2 and 3.

We think this is a fantastic suggestion and thank Reviewer 1 for this input. In the revised manuscript, we have added Figure 7, which summarises the tested candidates that displayed an effect on learning, mapped onto potential molecular pathways derived from networks in the learning proteome. This figure provides a visual framework linking the behavioural outcomes to the network context. This is described in the main text on pages 32-33.

Typo in Figure 3: the circle of PPM1: The blue right circle half is bigger than the left one.

We thank the Reviewer for noticing this, the node size for PPM-1.A has been corrected in what is now Figure 2 in the revised work.

Unclarity in the discussions. In the discussion Page 24, Line 14, the authors raise this question: "why are the proteins we identified not general learning regulators?. The phrasing and logic of the argumentation of the possible answers was hard to follow. - Can you clarify?

We appreciate this feedback in terms of unclarity, as we strive to explain the data as clearly and transparently as possible. Our goal in this paragraph was to discuss why some candidates were seen to only affect salt associative learning, as opposed to showing effects in multiple learning paradigms (i.e., which we were defining as a ‘general learning regulator’). We have adjusted the wording in several places in this paragraph now on pages 36 & 37 to address this comment. We hope the rephrased paragraph provides sufficient rationalisation for the discussion regarding our selection strategy used to isolate our protein list of potential learning regulators, and its potential limitations.

***Cross-Commenting** *

Firstly, we would like to express our appreciation for the opportunity for reviewers to cross-comment on feedback from other reviewers. We believe this is an excellent feature of the peer review process, and we are grateful to the reviewers for their thoughtful engagement and collaborative input.

I would like to thank Reviewer #4 for the great cross comment summary, I find it accurate and helpful.

I also would like to thank Reviewer #4 for spotting the typos in my minor comments, their page and figure numbers are the correct ones.

We have corrected these typos in the relevant comments, and have responded to them accordingly.

Small comment on common point 1 - My feeling is that it is challanging to do quantitative mass spectrometry, especially with TurboID. In general, the nature of MS data is that it hints towards a direction but a followup validation work is required in order to assess it. For example, I am not surprised that the fraction of repeats a hit appeared in does not predict well whether this hit would be validated behavioraly. Given these limitations, I find the authors' approach reasonable.

We thank Reviewer 1 for this positive and thoughtful feedback. We also appreciate Reviewer 4’s comment regarding quantitative mass spectrometry and have addressed this in detail below (see response to Reviewer 4). However, we agree with Reviewer 1 that there are practical challenges to performing quantitative mass spectrometry with TurboID, primarily due to the enrichment for biotinylated proteins that is a key feature of the sample preparation process.

Importantly, we whole-heartedly agree with Reviewer 1’s statement that “In general, the nature of MS data is that it hints towards a direction but a follow-up validation work is required in order to assess it”. This is the core of our approach: however, we appreciate that there are limitations to a qualitative ‘absent/present’ approach. We have addressed some of these limitations by clarifying the criteria used for selecting candidate genes, based additionally on the presence of the candidate in multiple biological replicates (categorised as ‘strong’ hits). Based on this method, we were able to validate the role of several novel learning regulators (Figures 5, 6, & S7). We sincerely hope that this manuscript can function as a direction for future research, as suggested by this Reviewer.

I also would like to highlight this major comment from reviewer 4:

"In Experimental Procedures, authors state that they excluded data in which naive or control groups showed average CI 0.5499 for N2 (page 36, lines 5-7). "

This threshold seems arbitrary to me too, and it requires the clarifications requested by reviewer 4.

As detailed in our response to Reviewer 4, Major Comment 2, data were excluded only in rare cases, specifically when N2 worms failed to show strong salt attraction prior to training, or when trained N2 worms did not exhibit the expected behavioural difference compared to untrained controls – this can largely be attributed to clear contamination or over-population issues, which are visible prior to assessing CTX plates and counting chemotaxis indices.

These criteria were initially established to provide an objective threshold for excluding biological replicates, particularly when planning to assay a large number of genetic mutants. However, after extensive testing across many replicates, we found that N2 worms (that were not starved, or not contaminated) consistently displayed the expected phenotype, rendering these thresholds unnecessary. We acknowledge that emphasizing these criteria may have been misleading, and have therefore removed them from page 50 in the revised manuscript to avoid confusion and ensure clarity.

Reviewer #1 (Significance (Required)):

This study does a great job to effectively utilize the TurboID technique to identify new pathways implicated in salt-associative learning in C. elegans. This technique was used in C. elegans before, but not in this context. The salt-associative memory induced proteome list is a valuable resource that will help future studies on associative memory in worms. Some of the implicated molecular pathways were found before to be involved in memory in worms like cAMP, as correctly referenced in the manuscript. The implication of the acetylcholine pathway is novel for C. elgeans, to the best of my knowledge. The finding that the uncovered genes are specifically required for salt associative memory and not for other memory assays is also interesting.

However overall I find the impact of this study limited. The premise of this work is to use the Turbo-ID method to conduct a systems analysis of the proteomic changes. The work starts by conducting network analysis and gene enrichment which fit a systemic approach. However, since the authors find that ~30% of the tested hits affect the phenotype, and since only 17/706 proteins were assessed, it is challenging to draw conclusive broad systemic claims. Alternatively, the authors could have focused on the positive hits, and understand them better, find the specific circuits where these genes act. This could have increased the impact of the work. Since neither of these two options are satisfied, I view this work as solid, but not wide in its impact and therefore estimate the audience of this study would be more specialized.

My expertise is in C. elegans behavior, genetics, and neuronal activity, programming and machine learning.

We thank the Reviewer for these comments and appreciate the recognition of the value of the proteomic dataset and the identification of novel molecular pathways, including the acetylcholine pathway, as well as the specificity of the uncovered genes to salt-associative memory.

Regarding the reviewer’s concern about the overall impact and scope of the study, we respectfully offer the following clarification. Our aim was to establish a systems-level approach for investigating learning-related proteomic changes using TurboID, and we acknowledge that only a subset of the identified proteins was experimentally tested (now 26/706 proteins in the revised manuscript). Although only five of the tested single gene mutants showed a robust learning phenotype in the revised work (after backcrossing, more stringent candidate selection, improved statistical analysis in addressing reviewer comments), our proteomic data provides us a unique opportunity to define these candidates within protein-protein networks (as illustrated in Figure 7). Importantly, our functional testing focused on single-gene mutants, which may not reveal phenotypes for genes that act redundantly (now mentioned on pages 28-30). This limitation is inherent to many genetic screens and highlights the value of our proteomic dataset, which enables the identification of broader protein-protein interaction networks and molecular pathways potentially involved in learning.

To support this systems-level perspective, we have added Figure 7, which visually integrates the tested candidates into molecular pathways derived from the learning proteome for learning regulators KIN-2 and F46H5.3. We also emphasise more explicitly in the text (on pages 32-33) the value of our approach by highlighting the functional protein networks that can be derived from our proteomics dataset.

We fully acknowledge that the use of TurboID across all neurons limits the resolution needed to pinpoint individual neuron contributions, and understand the benefit in further experiments to explore specific circuits. Many circuits required for salt sensing and salt-based learning are highly explored in the literature and defined explicitly (see Rahmani & Chew, 2021), so our intention was to complement the existing literature by exploring the protein-protein networks involved in learning, rather than on neuron-neuron connectivity. However, we recognise the benefit in integrating circuit-level analyses, given that our proteomic data suggests hundreds of candidates potentially involved in learning. While validating each of these candidates is beyond the scope of the current study, we have taken steps to suggest candidate neurons/circuits by incorporating tissue enrichment analyses and single-cell transcriptomic data (Table S7 & Figure 4). These additions highlight neuron classes of interest and suggest possible circuits relevant to learning.

We hope this clarification helps convey the intended scope and contribution of our study. We also believe that the revisions made in response to Reviewer 1’s feedback have strengthened the manuscript and enhanced its significance within the field.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

__Summary: __

In this study by Rahmani in colleagues, the authors sought to define the "learning proteome" for a gustatory associative learning paradigm in C. elegans. Using a cytoplasmic TurboID expressed under the control of a pan-neuronal promoter, the authors labeled proteins during the training portion of the paradigm, followed by proteomics analysis. This approach revealed hundreds of proteins potentially involved in learning, which the authors describe using gene ontology and pathways analysis. The authors performed functional characterization of some of these genes for their requirement in learning using the same paradigm. They also compared the requirement for these genes across various learning paradigms, and found that most hits they characterized appear to be specifically required for the training paradigm used for generating the "learning proteome".

Major Comments:

1. The definition of a "hit" from the TurboID approach is does not appear stringent enough. According to the manuscript, a hit was defined as one unique peptide detected in a single biological replicate (out of 5), which could give rise to false positives. In figure S2, it is clear that there relatively little overlap between samples with regards to proteins detected between replicates, and while perhaps unintentional, presenting a single unique peptide appears to be an attempt to inflate the number of hits. Defining hits as present in more than one sample would be more rigorous. Changing the definition of hits would only require the time to re-list genes and change data presented in the manuscript accordingly. We thank Reviewer 2 for this valuable comment, and the following related suggestion. We agree with the statement that “Defining hits as present in more than one sample would be more rigorous”. Therefore, to address this comment, we have now separated candidates into two categories in Table 2 __in the revised manuscript: ‘__strong’ (present in 3 or more biological replicates) and ‘weak’ candidates (present in 2 or fewer biological replicates). However, we think these weaker candidates should still be included in the manuscript, considering we did observe relationships between these proteins and learning. For example, ACC-1, which influences salt associative learning in C. elegans, was detected in one replicate of mass spectrometry as a potential learning regulator (Figure S8A). We describe this classification in the main text on pages 21-22.

We also agree with Reviewer 2 that the overlap between individual candidate hits is low between biological replicates; the inclusion of Figure S2 __in the original manuscript serves to highlight this limitation. However, it is also important to consider that there is notable overlap for whole molecular pathways between biological replicates of mass spectrometry data as shown in __Figure 2 __in the revised manuscript (this consideration is now mentioned on __pages 13-14). We have included Figure 3 to illustrate representation for two metabolic processes across several biological replicates normally indispensable to animal health, as an example to provide additional visual aid for the overlap between replicates of mass spectrometry. We provide this figure (described on pages 13 & 15) to demonstrate the strength of our approach in that it can detect candidates not easily assessable by conventional forward or reverse genetic screens.

We also appreciate the opportunity to explain our approach. The criteria of “at least one unique peptide” was chosen based on a previous work for which we adapted for this manuscript (Prikas et al., 2020). It was not intended to inflate the number of hits but rather to ensure sensitivity in detecting low-abundance neuronal proteins. We have clarified this in our Methods (page 46).

The "hits" that the authors chose to functionally characterize do not seem like strong candidate hits based on the proteomics data that they generated. Indeed, most of the hits are present in a single, or at most 2, biological replicate. It is unclear as to why the strongest hits were not characterized, which if mutant strains are publicly available, would not be a difficult experiment to perform.

We thank the reviewer for this important suggestion. To address this, we have described two molecular pathways with multiple components that appear in more than one biological replicate of mass spectrometry data in Figure 3 (main text on page 13). In addition, we have included __Figures 6 & S7 __where 9 additional single mutants corresponding to candidates in three or more biological replicates of mass spectrometry were tested for salt associative learning. Briefly, we found the following (number of replicates that a protein was unique to TurboID trained animals is in brackets):

• Novel arginine kinase F46H5.3 (4 replicates) displays an effect in both salt associative learning and salt aversive learning in the same direction (Figures 6A, 6B, & S9A, pages 31-32 & 37-38).
• Worms with a mutation for armadillo-domain protein C30G12.6 (3 replicates) only displayed an enhanced learning phenotype when non-backcrossed, not backcrossed. This suggests the enhanced learning phenotype was caused by a background mutation (Figure 6, pages 24-25).
• We did not observe an effect on salt associative learning when assessing mutations for the ciliogenesis protein IFT-139 (5 replicates), guanyl nucleotide factors AEX-3 or TAG-52 (3 replicates), p38/MAPK pathway interactor FSN-1 (3 replicates), IGCAM/RIG-4 (3 replicates), and acetylcholine components ACR-2 (4 replicates) and ELP-1 (3 replicates) (Figure S7, on pages 27-30). However, we note throughout the section for which these candidates are described that only single gene mutants were tested, meaning that genes that function in redundant or compensatory pathways may not exhibit a detectable phenotype. Because of the lack of strong evidence that these are indeed proteins regulated in the context of learning based on proteomics, including evidence of changes in the proteins (by imaging expression changes of fluorescent reporters or a biochemical approach), would increase confidence that these hits are genuine.

We thank Reviewer 2 for this suggestion – we agree that it would have been ideal to have additional evidence suggesting that changes in candidate protein levels are associated directly with learning. Ideally, we would have explored this aspect further; however, as outlined in response to Reviewer 1 Major Comment 2 (OPTIONAL), this was not feasible within the scope of the current study due to several practical challenges. Specifically, we attempted to generate pan-neuronal and endogenous promoter rescue lines for several candidates, but encountered significant challenges, including poor survival post-microinjection (likely due to protein overexpression toxicity) and reduced viability for behavioural assays, potentially linked to transgene-related reproductive defects. This information is now described on pages 39 & 40 of the revised work.

To address these limitations, we performed additional behavioural experiments where possible. We successfully generated a pan-neuronal promoter line for kin-2, which was tested and included in the revised manuscript (Figure 5B, pages 30 & 31). In addition, to confirm that observed learning phenotypes were due to the expected mutations and not background effects, we conducted experiments using backcrossed versions of several mutant lines as suggested by Reviewer 4 Cross Comment 3 (Figure 6, pages 23-24 & 24-26). Briefly, this shows that pan-neuronal expression of KIN-2 from the ce179 mutant allele is sufficient to repeat the enhanced learning phenotype observed in backcrossed kin-2(ce179) animals, providing additional evidence that the identified hits are required for learning. We also confirmed that F46H5.3 modulates salt associative learning, given both non-backcrossed and backcrossed F46H5.3(-) mutants display a learning enhancement phenotype. The revised text now describes this data on the page numbers mentioned above.

Minor Comments:

1. The authors highlight that the proteins they discover seem to function uniquely in their gustatory associative paradigm, but this is not completely accurate. kin-2, which they characterize in figure 4, is required for positive butanone association (the authors even say as much in the manuscript) in Stein and Murphy, 2014. We appreciate this correction and thank the Reviewer for pointing this out. We have amended the wording appropriately on page 31 to clarify our meaning.

2. “Although kin-2(ce179) mutants were not shown to impact salt aversive learning, they have been reported previously to display impaired intermediate-term memory (but intact learning and short-term memory) for butanone appetitive learning (Stein and Murphy, 2014).”*

Reviewer #2 (Significance (Required)):

• General Assessment: The approach used in this study is interesting and has the potential to further our knowledge about the molecular mechanisms of associative behaviors. Strengths of the study include the design with carefully thought out controls, and the premise of combining their proteomics with behavioral analysis to better understand the biological significance of their proteomics findings. However, the criteria for defining hits and prioritization of hits for behavioral characterizations were major wweaknesses of the paper.
• Advance: There have been multiple transcriptomic studies in the worm looking at gene expression changes in the context of behavioral training (Lakhina et al., 2015, Freytag 2017). This study compliments and extends those studies, by examining how the proteome changes in a different training paradigm. This approach here could be employed for multiple different training paradigms, presenting a new technical advance for the field.
• Audience: This paper would be of interest to the broader field of behavioral and molecular neuroscience. Though it uses an invertebrate system, many findings in the worm regarding learning and memory translate to higher organisms.
• I am an expert in molecular and behavioral neuroscience in both vertebrate and invertebrate models, with experience in genetics and genomics approaches. We appreciate Reviewer 2’s thoughtful assessment and constructive feedback. In response to concerns regarding definition and prioritisation of hits, we have revised our approach as detailed above to place more consideration on ‘strong’ hits present in multiple biological replicates. We have also added new behavioural data for additional mutants that fall into this category (Figures 6 & S7). We hope these revisions strengthen our study and enhance its relevance to the behavioural/molecular neuroscience community.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

__Summary: __

In the manuscript titled "Identifying regulators of associative learning using a protein-labelling approach in C. elegans" the authors attempted to generate a snapshot of the proteomic changes that happen in the C. elegans nervous system during learning and memory formation. They employed the TurboID-based protein labeling method to identify the proteins that are uniquely found in samples that underwent training to associate no-salt with food, and consequently exhibited lower attraction to high salt in a chemotaxis assay. Using this system they obtained a list of target proteins that included proteins represented in molecular pathways previously implicated in associative learning. The authors then further validated some of the hits from the assay by testing single gene mutants for effects on learning and memory formation.

Major Comments:

In the discussion section, the authors comment on the sources of "background noise" in their data and ways to improve the specificity. They provide some analysis on this aspect in Supplementary figure S2. However, a better visualization of non-specificity in the sample could be a GO analysis of tissue-specificity, and presented as a pie chart as in Figure 2A. Non-neuronal proteins such as MYO-2 or MYO-3 repeatedly show up on the "TurboID trained" lists in several biological replicates (Tables S2 and S3). If a major fraction of the proteins after subtraction of control lists are non-specific, that increases the likelihood that the "hits" observed are by chance. This analysis should be presented in one of the main figures as it is essential for the reader to gauge the reliability of the experiment.

We agree with this assessment and thank Reviewer 3 for this constructive suggestion. In response, we have now incorporated a comprehensive tissue-specific analysis of the learning proteome in the revised manuscript. Using the single neuron RNA-Seq database CeNGEN, we identified the proportion of neuronal vs non-neuronal proteins from each biological replicate of mass spectrometry data. Specifically, we present Table 1 __on page 17 (which we originally intended to include in the manuscript, but inadvertently left out), which shows that 87-95% (i.e. a large majority) of proteins identified across replicates corresponded to genes detected in neurons, supporting that the TurboID enzyme was able to target the neuronal proteome as expected. __Table 1 is now described in the main text of the revised work on page 16.

In addition, we performed neuron-specific analyses using both the WormBase gene enrichment tool and the CeNGEN single-cell transcriptomic database, which we describe in detail on our response to Reviewer 1 Major Comment 2. To summarise, these analyses revealed enrichment of several neuron classes, including those previously implicated in associative learning (e.g., ASEL, AIB, RIS, AVK) as well as neurons not previously studied in this context (e.g., IL1, DA9, DVC) (summarised in Table S7). By examining expression overlap across neuron types, we identified shared and distinct profiles that suggest potential functional connectivity and candidate circuits underlying behavioural plasticity (Figure 4). Taken together, these data show that the proteins identified in our dataset are (1) neuronal and (2) expressed in neurons that are known to be required for learning. Methods are detailed on pages 50-51.

Other than the above, the authors have provided sufficient details in their experimental and analysis procedures. They have performed appropriate controls, and their data has sufficient biological and technical replaictes for statistical analysis.

We appreciate this positive feedback and thank the Reviewer for acknowledging the clarity of our experimental and analysis procedures.

Minor Comments:

There is an error in the first paragraph of the discussion, in the sentences discussing the learning effects in gar-1 mutant worms. The sentences in lines 12-16 on page 22 says that gar-1 mutants have improved salt-associative learning and defective salt-aversive learning, while in fact the data and figures state the opposite.

We appreciate the Reviewer noting this discrepancy. As clarified in our response to Reviewer 1, Major Comment 1 above, we reanalysed the behavioural data to ensure consistency across genotypes by comparing only those tested within the same biological replicates (thus having the same N for all genotypes). Upon this reanalysis, we found that the previously reported phenotype for gar-1 mutants in salt-associative learning was not statistically different from wild-type controls. Therefore, we have removed references to GAR-1 from the manuscript.

__Reviewer #3 (Significance (Required)): __Strengths and limitations: This study used neuron-specific TurboID expression with transient biotin exposure to capture a temporally restricted snapshot of the C. elegans nervous system proteome during salt-associative learning. This is an elegant method to identify proteins temporally specific to a certain condition. However, there are several limitations in the way the experiments and analyses were performed which affect the reliability of the data. As the authors themselves have noted in the discussion, background noise is a major issue and several steps could be taken to improve the noise at the experimental or analysis steps (use of integrated C. elegans lines to ensure uniformity of samples, flow cytometry to isolate neurons, quantitative mass spec to detect fold change vs. strict presence/absence). Advance: Several studies have demonstrated the use of proximity labeling to map the interactome by using a bait protein fusion. In fact, expressing TurboID not fused to a bait protein is often used as a negative control in proximity labeling experiments. However, this study demonstrates the use of free TurboID molecules to acquire a global snapshot of the proteome under a given condition. Audience: Even with the significant limitations, this study is specifically of interest to researchers interested in understanding learning and memory formation. Broadly, the methods used in this study could be modified to gain insights into the proteomic profiles at other transient developmental stages. The reviewer's field of expertise: Cell biology of C. elegans neurons.

We thank the reviewer for their thoughtful evaluation of our work. We appreciate the recognition of the novelty and potential of using neuron-specific TurboID to capture a temporally restricted snapshot of the C. elegans nervous system proteome during learning. We agree that this approach offers a unique opportunity to identify proteins associated with specific behavioural states in future studies.

We also appreciate the reviewer’s comments regarding limitations in experimental and analytical design. In revising the manuscript, we have taken several steps to address these concerns and improve the clarity, rigour, and interpretability of our data. Specifically:

• We now provide a frequency-based representation of proteomic hits (Table 2), which helps clarify how candidate proteins were selected and highlights differences between trained and control groups.
• We have added neuron-specific enrichment analyses using both WormBase and CenGEN databases (Table S7 & Figure 4), which help identify candidate neurons and potential circuits involved in learning (methods on pages 50-51).
• We have clarified the rationale for using qualitative proteomics in the context of TurboID, in addition to acknowledging the challenges of integrating quantitative mass spectrometry with biotin-based enrichment (page 39). Additional methods for improving sample purity, such as using integrated lines or FACS-enrichment of neurons, could further refine this approach in future studies. For transparency, we did attempt to integrate the TurboID transgenic line to improve the strength and consistency of biotinylation signals. However, despite four rounds of backcrossing, this line exhibited unexpected phenotypes, including a failure to respond reliably to the established training protocol. As a result, we were unable to include it in the current study. Nonetheless, we believe our current approach provides a valuable proof-of-concept and lays the groundwork for future refinement. By addressing the major concerns of peer reviewers, we believe our study makes a significant and impactful contribution by demonstrating the feasibility of using TurboID to capture learning-induced proteomic changes in the nervous system. The identification of novel learning-related mutants, including those involved in acetylcholine signalling and cAMP pathways, provides new directions for future research into the molecular and circuit-level mechanisms of behavioural plasticity.

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

Summary:

In this manuscript, authors used a learning paradigm in C. elegans; when worms were fed in a saltless plate, its chemotaxis to salt is greatly reduced. To identify learning-related proteins, authors employed nervous system-specific transcriptome analysis to compare whole proteins in neurons between high-salt-fed animals and saltless-fed animals. Authors identified "learning-specific genes" which are observed only after saltless feeding. They categorized these proteins by GO analyses and pathway analyses, and further stepped forward to test mutants in selected genes identified by the proteome analysis. They find several mutants that are defective or hyper-proficient for learning, including acc-1/3 and lgc-46 acetylcholine receptors, gar-1 acetylcholine receptor GPCR, glna-3 glutaminase involved in glutamate biosynthesis, and kin-2, a cAMP pathway gene. These mutants were not previously reported to have abnormality in the learning paradigm.

Major comments:

1) There are problems in the data processing and presentation of the proteomics data in the current manuscript which deteriorates the utility of the data. First, as the authors discuss (page 24, lines 5-12), the current approach does not consider amount of the peptides. Authors state that their current approach is "conservative", because some of the proteins may be present in both control and learned samples but in different amounts. This reviewer has a concern in the opposite way: some of the identified proteins may be pseudo-positive artifacts caused by the analytical noise. The problem is that authors included peptides that are "present" in "TurboID, trained" sample but "absent" in the "Non-Tg, trained" and "TurboID, control" samples in any one of the biological replicates, to identify "learning proteome" (706 proteins, page 8, last line - page 9, line 8; page 32, line 21-22). The word "present" implies that they included even peptides whose amounts are just above the detection threshold, which is subject to random noise caused by the detector or during sample collection and preparation processes. This consideration is partly supported by the fact that only a small fraction of the proteins are common between biological replicates (honestly and respectably shown in Figure S2). Because of this problem, there is no statistical estimate of the identity in "learning proteome" in the current manuscript. Therefore, the presentation style in Tables S2 and S3 are not very useful for readers, especially because authors already subtracted proteins identified in Non-Tg samples, which must also suffer from stochastic noise. I suggest either quantifying the MS/MS signal, or if authors need to stick to the "present"/"absent" description of the MS/MS data, use the number of appearances in biological replicates of each protein as estimate of the quantity of each protein. For example, found in 2 replicates in "TurboID, learned" and in 0 replicates in "Non-Tg, trained". One can apply statistics to these counts. This said, I would like to stress that proteins related to acquisition of memory may be very rare, especially because learning-related changes likely occur in a small subset of neurons. Therefore, 1 time vs 0 time may be still important, as well as something like 5 times vs 1 time. In summary, quantitative description of the proteomics results is desired.

We thank the reviewer for these valuable comments and suggestions.

We acknowledge that quantitative proteomics would provide beneficial information; however, as also indicated by Reviewer 1 (in cross-comment), it is practically challenging to perform with TurboID. We have included discussion of potential future experiments involving quantitative mass spectrometry, as well as a comprehensive discussion of some of the limitations of our approach as summarised by this Reviewer, in the Discussion section (page 39). However, we note that our qualitative approach also provides beneficial knowledge, such as the identification of functional protein networks acting within biological pathways previously implicated in learning (Figure 2), and novel learning regulators ACC-1/3, LGC-46, and F46H5.3.

We agree with the assessment that the frequency of occurrence for each candidate we test per biological replicate is useful to disclose in the manuscript as a proxy for quantification. This was also highlighted by Reviewer 2 (Major Comment 1). As detailed above in response to R2, we have now separated candidates into two categories: ‘strong’ (present in 3 or more biological replicates) and ‘weak’ candidates (present in 2 or fewer biological replicates). We have also added behavioural data after testing 9 of these strong candidates in Figures 6 & S7.

We have also added Table 2 to the revised manuscript, which summarises the frequency-based representation of the proteomics results, as suggested. This is described on pages 22-23. Briefly, this shows the range of candidates further explored using single mutant testing. Specifically, this data showed that many of the tested candidates were more frequently detected in trained worms compared to high-salt controls. This includes both strong and weak candidates, providing a clearer view of how proteomic frequency informed our selection for functional testing.

2) There is another problem in the treatment of the behavioural data. In Experimental Procedures, authors state that they excluded data in which naive or control groups showed average CI 0.5499 for N2 (page 36, lines 5-7). How were these values determined? One common example for judging a data point as an outlier is > mean + 1.5, 2 or 3 SD, or Thank you for pointing this out. As mentioned by both Reviewer 1 and Reviewer 4, the original manuscript states the following: “Data was excluded for salt associative learning experiments when wild-type N2 displayed (1) an average CI ≤ 0.6499 for naïve or control groups and/or (2) an average CI either 0.5499 for trained groups.”

To clarify, we only excluded experiments in rare cases where N2 worms did not display robust high salt attraction before training, or where trained N2 did not display the expected behavioural difference compared to untrained or high-salt control N2. These anomalies were typically attributable to clear contamination or starvation issues that could clearly be observed prior to counting chemotaxis indices on CTX plates.

We established these exclusion criteria in advance of conducting multiple learning assays to ensure an objective threshold for identifying and excluding assays affected by these rare but observable issues. However, these criteria were later found to be unnecessary, as N2 worms robustly displayed the expected untrained and trained phenotypes for salt associative learning when not compromised by starvation or contamination.

We understand that the original criteria may have appeared to introduce arbitrary bias in data selection. To address this concern, we have removed these criteria from the revised manuscript from page 50.

Minor comments:

1) Related to Major comments 1), the successful effect of neuron-specific TurboID procedure was not evaluated. Authors obtained both TurboID and Non-Tg proteome data. Do they see enrichment of neuron-specific proteins? This can be easily tested, for example by using the list of neuron-specific genes by Kaletsky et al. (http://dx.doi.org/10.1038/nature16483 or http://dx.doi.org/10.1371/journal.pgen.1007559), or referring to the CenGEN data.

We thank this Reviewer for this helpful suggestion, which was echoed by Reviewer 3 (Major Comment 1). As indicated in the response to R3 above, the revised manuscript now includes Table 1 as a tissue-specific analysis of the learning proteome, using the single neuron RNA-Seq database CeNGEN to identify the proportion of neuronal proteins from each biological replicate of mass spectrometry data. Generally, we observed a range of 87-95% of proteins corresponded to genes from the CeNGEN database that had been detected in neurons, providing evidence that the TurboID enzyme was able to target the neuronal proteome as expected. Table 1 is now described in the main text of the revised work on pages 16 & 17.

2) The behavioural paradigm needs to be described accurately. Page 5, line 16-17, "C. elegans normally have a mild attraction towards higher salt concentration": in fact, C. elegans raised on NGM plates, which include approximately 50mM of NaCl, is attracted to around 50mM of NaCl (Kunitomo et al., Luo et al.) but not 100-200 mM.

We thank the Reviewer for pointing this out. We agree that clarification is necessary. The revised text reads as follows on page 5: “C. elegans are typically grown in the presence of salt (usually ~ 50 mM) and display an attraction toward this concentration when assayed for chemotaxis behaviour on a salt gradient (Kunitomo et al., 2013, Luo et al., 2014). Training/conditioning with ‘no salt + food’ partially attenuates this attraction (group referred to ‘trained’).”

Authors call this assay "salt associative learning", which refers to the fact that worms associate salt concentration (CS) and either presence or absence of food (appetitive or aversive US) during conditioning (Kunitomo et al., Luo et al., Nagashima et al.) but they are looking at only association with presence of food, and for proteome analysis they only change the CS (NaCl concentration, as discussed in Discussion, p24, lines 4-5). It is better to attempt to avoid confusion to the readers in general.

Thank you Reviewer 4 for highlighting this clarity issue. We clarify our definition of “salt associative learning” for the purpose of this study in the revised manuscript on page 6 with the following text:

“Similar behavioural paradigms involving pairings between salt/no salt and food/no food have been previously described in the literature (Nagashima et al. 2019). Here, learning experiments were performed by conditioning worms with either ‘no salt + food’ (referred to as ‘salt associative learning’) or ‘salt + no food’ (called ‘salt aversive learning’).”

3) page 32, line 23: the wording "excluding" is obscure and misleading because the elo-6 gene was included in the analysis.

We appreciate this Reviewer for pointing out this misleading comment, which was unintentional. We have now removed it from the text (on page 21).

4) Typo at page 24, line 18: "that ACC-1" -> "than ACC-1".

This has been corrected (on page 37).

5) Reference. In "LEO, T. H. T. et al.", given and sir names are flipped for all authors. Also, the paper has been formally published (http://dx.doi.org/10.1016/j.cub.2023.07.041).

We appreciate the Reviewer drawing our attention to this – the reference has been corrected and updated.

I would like to express my modest cross comments on the reviews:

1) Many of the reviewers comment on the shortage in the quantitative nature of the proteome analysis, so it seems to be a consensus.

Thank you Reviewer 4 for this feedback. We appreciate the benefit in performing quantitative mass spectrometry, in that it provides an additional way to parse molecular mechanisms in a biological process (e.g., fold-changes in protein expression induced by learning). However, we note that quantitative mass spectrometry is challenging to integrate with TurboID due to the requirement to enrich for biotinylated peptides during sample processing (we now mention this on page 39). Nevertheless, it would be exciting to see this approach performed in a future study.

To address the limitations of our original qualitative approach and enhance the clarity and utility of our dataset, we have made the following revisions in the manuscript:

• Candidate selection criteria: We now clearly define how candidates were selected for functional testing, based on their frequency across biological replicates. Specifically, “strong candidates” were detected in three or more replicates, while “weak candidates” appeared in two or fewer.
• Frequency-based representation (_Table 2_):__We appreciate the suggestion by Reviewer 4 (Major Comment 1) to quantify differences between high-salt control and trained groups. We now provide the frequency-based representation of the candidates tested in this study within our proteomics data in __Table 2. This data showed that many of the tested candidates were more frequently detected in trained worms compared to high-salt controls. This includes both strong and weak candidates We hope these additions help clarify our approach and demonstrate the value of the dataset, even within the constraints of qualitative proteomics.

2) Also, tissue- or cell-specificity of the identified proteins were commonly discussed. In reviewer #3's first Major comment, appearance of non-neuronal protein in the list was pointed out, which collaborate with my (#4 reviewer's) question on successful identification of neuronal proteins by this method. On the other hand, reviewer #1 pointed out subset neuron-specific proteins in the list. Obviously, these issues need to be systematically described by the authors.

We agree with Reviewer 4 that these analyses provide a critical angle of analysis that is not explored in the original manuscript.

Tissue analysis (Reviewer 3 Major Comment 1): We have used the single neuron RNA-Seq database CeNGEN, to identify that 87-95% (i.e. a large majority) of proteins identified across replicates corresponded to genes detected in neurons. These findings support that the TurboID enzyme was able to target the neuronal proteome as expected. Table 1 provides this information as is now described in the main text of the revised work on page 16.

__Neuron class analyses (Reviewer 1 Major Comment 2): __In response, we have used the suggested Wormbase gene enrichment tool and CeNGEN. We specifically input proteins from the learning proteome into Wormbase, after filtering for proteins unique to TurboID trained animals. For CeNGEN, we compared genes/proteins from control worms and trained worms to identify potential neurons that may be involved in this learning paradigm.

Briefly, we found highlight a range of neuron classes known in learning (e.g., RIS interneurons), cells that affect behaviour but have not been explored in learning (e.g., IL1 polymodal neurons), and neurons for which their function/s are unknown (e.g., pharyngeal neuron I3). Corresponding text for this new analysis has been added on pages 16-20, with a new table and figure added to illustrate these findings (Table S7 & Figure 4). Methods are detailed on pages 50-51.

3) Given reviewer #1's OPTIONAL Major comment, as an expert of behavioral assays in C. elegans, I would like to comment based on my experience that mutants received from Caenorhabditis Genetics Center or other labs often lose the phenotype after outcrossing by the wild type, indicating that a side mutation was responsible for the observed behavioral phenotype. Therefore, outcrossing may be helpful and easier than rescue experiments, though the latter are of course more accurate.

Thank you for this suggestion. To address the potential involvement of background mutations, we have done experiments with backcrossed versions of mutants tested where possible, as shown in Figure 6. We found that F46H5.3(-) mutants maintained enhanced learning capacity after backcrossing with wild type, compared to their non-backcrossed mutant line. This was in contrast to C30G12.6(-) animals which lost their enhanced learning phenotype following backcrossing using wild type worms. This is described in the text on pages 24-26.

4) Just let me clarify the first Minor comment by reviewer #2. Authors described that the kin-2 mutant has abnormality in "salt associative learning" and "salt aversive learning", according to authors' terminology. In this comment by reviewer #2, "gustatory associative learning" probably refers to both of these assays.

Reviewer 4 is correct. We have amended the wording appropriately on page 31 to clarify our meaning to address Reviewer 2’s comment.

• “Although kin-2(ce179) mutants were not shown to impact salt aversive learning, they have been reported previously to display impaired intermediate-term memory (but intact learning and short-term memory) for butanone appetitive learning (Stein and Murphy, 2014).”*

5) There seem to be several typos in reviewer #1's Minor comments.

"In Page 9, Lines 17-18" -> "Page 8, Lines 17-18".

"Page 8, Line 24" -> "Page 7, Line 24".

"I would suggest to remove figure 3" -> "I would suggest to remove figure 2"

"summary figure similar to Figure 4" -> "summary figure similar to Figure 3"

"In the discussion Page 24, Line 14" -> "In the discussion Page 23, Line 14"

(I note that because a top page was inserted in the "merged" file but not in art file for review, there is a shift between authors' page numbers and pdf page numbers in the former.)

It would be nice if reviewer #1 can confirm on these because I might be wrong.

We appreciate Reviewer 4 noting this, and can confirm that these are the correct references (as indicated by Reviewer 1 in their cross-comments)

Reviewer #4 (Significance (Required)):

1) Total neural proteome analysis has not been conducted before for learning-induced changes, though transcriptome analysis has been performed for odor learning (Lakhina et al., http://dx.doi.org/10.1016/j.neuron.2014.12.029). This guarantees the novelty of this manuscript, because for some genes, protein levels may change even though mRNA levels remain the same. We note an example in which a proteome analysis utilizing TurboID, though not the comparison between trained/control, has led to finding of learning related proteins (Hiroki et al., http://dx.doi.org/10.1038/s41467-022-30279-7). As described in the Major comments 1) in the previous section, improvement of data presentation will be necessary to substantiate this novelty.

We appreciate this thoughtful feedback. We agree that while the neuronal transcriptome has been explored in Lakhina et al., 2015 for C. elegans in the context of memory, our study represents the first to examine learning-induced changes in the total neuronal proteome. We particularly agree with the statement that “for some genes, protein levels may change even though mRNA levels remain the same”. This is essential rationale that we now discuss on page 42.

Additionally, we acknowledge the relevance of the study by Hiroki et al., 2022, which used TurboID to identify learning-related proteins, though not in a trained versus control comparison. Our work builds on this by directly comparing trained and control conditions, thereby offering new insights into the proteomic landscape of learning. This is now clarified on page 36.

To substantiate the novelty and significance of our approach, we have revised the data presentation throughout the manuscript, including clearer candidate selection criteria, frequency-based representation of proteomic hits (Table 2), and neuron-specific enrichment analyses (Table S7 & Figure 4). We hope these improvements help convey the unique contribution of our study to the field.

2) Authors found six mutants that have abnormality in the salt learning (Fig. 4). These genes have not been described to have the abnormality, providing novel knowledge to the readers, especially those who work on C. elegans behavioural plasticity. Especially, involvement of acetylcholine neurotransmission has not been addressed. Although site of action (neurons involved) has not been tested in this manuscript, it will open the venue to further determine the way in which acetylcholine receptors, cAMP pathway etc. influences the learning process.

Thank you Reviewer 4, for this encouraging feedback. To further strengthen the study and expand its relevance, we have tested additional mutants in response to Reviewer 3’s comments, as shown in Figures 6 & S7. These results provide even more candidate genes and pathways for future exploration, enhancing the significance and impact of our study.

I think it is very important to remember this as an educator and parent. We have to be sure to maximize use and make it beneficial and worthwhile, not just replacing other instruction.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

A) The presentation of the paper must be strengthened. Inconsistencies, mislabelling, duplicated text, typos, and inappropriate colour code should be changed.

We spotted and corrected several inconsistencies and mislabelling issues throughout the text and figures. Thanks!  

B) Some claims are not supported by the data. For example, the sentence that says that "adolescent mice showed lower discrimination performance than adults (l.22) should be rewritten, as the data does not show that for the easy task (Figure 1F and Figure 1H).

We carefully reviewed the specific claims and fixed some of the wording so it adheres to the data shown.

C) In Figure 7 for example, are the quantified properties not distinct across primary and secondary areas?

We now carried out additional analysis to test this. We found that while AUDp and AUDv exhibit distinct tuning properties, they show similar differences between adolescent and adult neurons (see Supplementary Table 6, Fig. S7-1a-h). Note that TEa and AUDd could not be evaluated due to low numbers of modulated neurons in this protocol.

D) Some analysis interpretations should be more cautious. (..) A lower lick rate in general could reflect a weaker ability to withhold licking- as indicated on l.164, but also so many other things, like a lower frustration threshold, lower satiation, more energy, etc).

That is a fair comment, and we refined our interpretations. Moreover, we also addressed whether impulsiveness impacted lick rates. In the Educage, we found that adolescent mice had shorter ITIs only after FAs (Fig. S2-1). In the head-fixed setup, we examined (1) the proportion of ITIs where licks occurred (Fig. S3-1c) and (2) the number of licks in these ITIs (Fig. S3-1d). We found no differences between adolescents and adults, indicating that the differences observed in the main task are not due to general differences in impulsiveness (Fig. S2-1, Fig. S3-1c, d). Finally, we note that potential differences in satiation were already addressed in the original manuscript by carefully examining the number of trials completed across the session. See also Review 3, comment #1 below.

Reviewer #2 (Public review):

A) For some of the analyses that the authors conducted it is unclear what the rationale behind them is and, consequently, what conclusion we can draw from them.

We reviewed the manuscript carefully and revised the relevant sections to clarify the rationale behind the analyses. See detailed responses to all the reviewer’s specific comments.

B) The results of optogenetic manipulation, while very interesting, warrant a more in-depth discussion.

We expanded our discussion on these experiments (L495-511) and also added an additional analysis to strengthen our findings (Fig. S3-2e).

Reviewer #3 (Public review):

(1) The authors report that "adolescent mice showed lower auditory discrimination performance compared to adults" and that this performance deficit was due to (among other things) "weaker cognitive control". I'm not fully convinced of this interpretation, for a few reasons. First, the adolescents may simply have been thirstier, and therefore more willing to lick indiscriminately. The high false alarm rates in that case would not reflect a "weaker cognitive control" but rather, an elevated homeostatic drive to obtain water. Second, even the adult animals had relatively high (~40%) false alarm rates on the freely moving version of the task, suggesting that their behavior was not particularly well controlled either. One fact that could help shed light on this would be to know how often the animals licked the spout in between trials. Finally, for the head-fixed version of the task, only d' values are reported. Without the corresponding hit and false alarm rates (and frequency of licking in the intertrial interval), it's hard to know what exactly the animals were doing.

irst, as requested, we added the Hit rates and FA rates for the head-fixed task (Fig. S3-1a). Second, as requested by the reviewr, we performed additional analyses in both the Educage and head-fixed versions of the task. Specifically, we analyzed the ITI duration following each trial outcome. We found that adolescent mice had shorter ITIs only after Fas (Fig. S2-1). In the head-fixed setup, we examined (1) the proportion of ITIs during which licks occurred (Fig. S3-1c) and (2) the number of licks in these ITIs (Fig. S3-1d). We found no differences between adolescents and adults, indicating that the differences observed in the main task are not due to general differences in impulsiveness (Fig. S2-1, Fig. S3-1c, d). See also comment #D of reviewer #1 above.

B) There are some instances where the citations provided do not support the preceding claim. For example, in lines 64-66, the authors highlight the fact that the critical period for pure tone processing in the auditory cortex closes relatively early (by ~P15). However, one of the references cited (ref 14) used FM sweeps, not pure tones, and even provided evidence that the critical period for this more complex stimulus occurred later in development (P31-38). Similarly, on lines 72-74, the authors state that "ACx neurons in adolescents exhibit high neuronal variability and lower tone sensitivity as compared to adults." The reference cited here (ref 4) used AM noise with a broadband carrier, not tones.

We carefully checked the text to ensure that each claim is accurately supported by the corresponding reference.

C) Given that the authors report that neuronal firing properties differ across auditory cortical subregions (as many others have previously reported), why did the authors choose to pool neurons indiscriminately across so many different brain regions?

We appreciate the reviewer’s concern. While we acknowledge that pooling neurons across auditory cortical subregions may obscure region-specific effects, our primary focus in this study is on developmental differences between adolescents and adults, which were far more pronounced than subregional differences.

To address this potential limitation: (1) We analyzed firing differences across subregions during task engagement (see Fig. S4-1, S4-2, S4-3; Supplementary Tables 2 and 3). (2) We have now added new analyses for the passive listening condition in AUDp and AUDv (Fig. S7-1; Supplementary Table 6).

These analyses support our conclusion that developmental stage has a greater impact on auditory cortical activity than subregional location in the contexts examined. For clarity and cohesion, the main text emphasizes developmental differences, while subregional analyses are presented in the Supplement.

D) And why did they focus on layers 5/6? (Is there some reason to think that age-related differences would be more pronounced in the output layers of the auditory cortex than in other layers?)

We agree that other cortical layers, particularly supragranular layers, are important for auditory processing and plasticity. Our focus on layers 5/6 was driven by both methodological and biological considerations. Methodologically, our electrode penetrations were optimized to span multiple auditory cortical areas, and deeper layers provided greater mechanical stability for chronic recordings. Biologically, layers 5/6 contain the principal output neurons of the auditory cortex and are well-positioned to influence downstream decision-making circuits. We acknowledge the limitation of our recordings to these layers in the manuscript (L268; L464-8).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The presentation of the paper must be strengthened. As it is now, it makes it difficult to appreciate the strengths of the results. Here are some points that should be addressed:

a) The manuscript is full of inconsistencies that should be fixed to improve the reader's understanding. For example, the description on l.217 and the Figure. S3-1b, the D' value of 0 rounded to 0.01 on l. 735 (isn't it rather the z-scored value that is rounded? A D' of 0 is not a problem), the definition of lick bias on l. 750 and the values in Fig.2, the legend of Figure 7F and what is displayed on the graph (is it population sparseness or responsiveness?), etc.

We adjusted the legend and description of former Fig. S3-1b (now Fig. S3-2b).

We now clarify that the rounded values refer to z-scored hit and false alarm rates that we used in the d’ calculation. We adjusted the definition of the lick bias in Fig. 2 and Fig. S3-1b (L804).

We replaced ‘population responsiveness’ with ‘population sparseness’ throughout the figures, legend and the text.

b) References to figures are sometimes wrong (for example on l. 737,739).

c) Some text is duplicated (for example l. 814 and l. 837).

d) Typos should be corrected (for example l. 127, 'the', l. 787, 'upto').

We deleted the incorrect references of this section, removed the duplicated text, and corrected the typos.

e) Color code should be changed (for example the shades of blue for easy and hard tasks - they are extremely difficult to differentiate).

After consideration, we decided to retain the blue color code (i.e., Fig. 1d, Fig. 3d, Fig. 4e-g, Fig. 5c, Fig. 6d–g), where the distinction between the shades of blue appears sufficiently clear and maintains visual consistency and aesthetic appeal. We did however, made changes in the other color codes (Fig. 4, Fig. 5, Fig. 6, Fig. 7).

f) Figure design should be improved. For example, why is a different logic used for displaying Figure 5A or B and Figure 1E?

We adjusted the color scheme in Fig. 5. We chose to represent the data in Fig. 5 according to task difficulty, as this arrangement best illustrates the more pronounced deficits in population decoding in adolescents during the hard task.

f) Why use a 3D representation in Figure 4G? (2)

The 3D representation in Fig. 4g was chosen to illustrate the 3-way interactions between onset-latency, maximal discriminability, and duration of discrimination.

g) Figure 1A, lower right panel- should "response" not be completed by "lick", "no lick"?

We changed the labels to “Lick” and “No Lick” in Fig. 1a.

h) l.18 the age mentioned is misleading, because the learning itself actually started 20 days earlier than what is cited here.

Corrected.

i) Explain what AAV5-... is on l.212.

We added an explanation of virus components (see L216-220).

(2) The comparison of CV in Figure 2 H-J is interesting. I am curious to know whether the differences in the easy and hard tasks could be due to a decrease in CV in adults, rather than an increase in CV in adolescents? Also, could the difference in J be due to 3 outliers?

We agree that the observed CV differences may reflect a reduction in variability in adults rather than an increase in adolescents. We have revised the Results section accordingly to acknowledge this interpretation.

Regarding the concern about potential outliers in Fig. 2J, we tested the data for outliers using the isoutlier function in MATLAB (defining outliers as values exceeding three standard deviations from the mean) and found no such cases.

(3) Figure 2c shows that there is no difference in perceptual sensitivity between adolescents and adults, whereas the conclusion from Figure 4 is that adolescents exhibit lower discriminability in stimulus-related activity. Aren't these results contradictory?

This is a nuanced point. The similar slopes of the psychometric functions (Fig. 2c) indicating comparable perceptual sensitivity and the lower AUC observed in the ACx of adolescents (Fig. 4) do not necessarily contradict each other. These two measures capture related but distinct issues: psychometric slopes reflect behavioral output, which integrates both sensory encoding and processing downstream to ACx, while the AUC analysis reflects stimulus-related neural activity in ACx, which may still include decision-related components.<br /> Note that stimulus-related neural discriminability outside the context of the task is not different between adolescent and adult experts (Fig. 7h; p = 0.9374, Kruskal Willis Test after Tukey-Kramer correction for multiple comparisons; not discussed in the manuscript). This suggests that there are differences that emerge when we measure during behavior. Also note that behavior may rely on processing beyond ACx, and it is possible that downstream areas compensate for weaker cortical discriminability in adolescents — but this issue merits further investigation.

(4) Why do you think that the discrimination in hard tasks decreases with learning (Figure 6D vs Figure 6F)?

This is another nuanced point, and we can only speculate at this stage. While it may appear counterintuitive that single-neuron discriminability (AUC) for the hard task is reduced after learning (Fig. 6D vs. 6F), we believe this may reflect a shift in sensory coding in expert animals. In a recent study (Haimson et al., 2024; Science Advances), we found that learning alters single-neuron responses in the easy versus hard task in complex and distinct ways, which may account for this result. It is also possible that, in expert mice, top-down mechanisms such as feedback from higher-order areas act to suppress or stabilize sensory responses in auditory cortex, reducing the apparent stimulus selectivity of single neurons (e.g., AUC), even as behaviorally relevant information is preserved or enhanced at the population level.

Reviewer #2 (Recommendations for the authors):

This is very interesting work and I enjoyed reading the manuscript. See below for my comments, queries and suggestions, which I hope will help you improve an already very good paper.

We thank the reviewer for the meticulous and thoughtful review.

(1) Line 107: x-axis of panel 1e says 'pre-adolescent'.

(2) Line 130: replace 'less' with 'fewer'.

(3) Line 153: 'both learned and catch trials': I find the terminology here a bit confusing. I would typically understand a catch trial to be a trial without a stimulus but these 'catch' trials here have a stimulus. It's just that they are not rewarded/punished. What about calling them probe trials instead?

We corrected the labelling (1), reworded to ‘fewer’ and ‘probe trials’ (2,3).

(4) Line 210: The results of the optogenetics experiments are very interesting. In particular, because the effect is so dramatic and much bigger than what has been reported in the literature previously, I believe. Lick rates are dramatically reduced suggesting that the mice have pretty much stopped engaging in the task and the authors very rightly state that the 'execution' of the behavior is affected. I think it would be worth discussing the implications of these results more thoroughly, perhaps also with respect to some of the lesion work. Useful discussions on the topic can be found, for instance, in Otchy et al., 2015; Hong et al., 2018; O'Sullivan et al., 2019; Ceballo et al., 2019 and Lee et al., 2024. Are the mice unable to hear anything in laser trials and that is why they stopped licking? If they merely had trouble distinguishing them then we would perhaps expect the psychometric curves to approach chance level, i.e. to be flat near the line indicating a lick rate of 0.5. Could the dramatic decrease in lick rate be a motor issue? Can we rule out spillover of the virus to relevant motor areas? (I understand all of the 200nL of the virus were injected at a single location) Or are the effects much more dramatic than what has been reported previously simply because the GtACR2 is much more effective at silencing the auditory cortex? Could the effect be down to off-target effects, e.g. by removing excitation from a target area of the auditory cortex, rather than the disruption of cortical processing?

We have now expanded the discussion in the manuscript to more thoroughly consider alternative interpretations of the strong behavioral effect observed during ACx silencing (L495–511). In particular, we acknowledge that the suppression of licking may reflect not only impaired sensory discrimination but also broader disruptions to arousal, motivation, or motor readiness. We also discuss the potential impact of viral spread, circuit-level off-target effects, and the potency of GtACR2 as possible contributors. We highlight the need for future work using more graded or temporally precise manipulations to resolve these issues.

(5) Line 226: Reference 19 (Talwar and Gerstein 2001) is not particularly relevant as it is mostly concerned with microstimulation-induced A1 plasticity. There are, however, several other papers that should be cited (and potentially discussed) in this context. In particular, O'Sullivan et al., 2019 and Ceballo et al., 2019 as these papers investigate the effects of optogenetic silencing on frequency discrimination in head-fixed mice and find relatively modest impairments. Also relevant may be Kato et al., 2015 and Lee et al., 2024, although they look at sound detection rather than discrimination.

We changed the references and pointed the reader to the (new section) Discussion.

(6) Line 253: 'engaged [in] the task.

(7) Figure 4: It appears that panel S4-1d is not referred to anywhere in the main text.

Fixed.

(8) Line 260: Might be useful to explain a bit more about the motivation behind focusing on L5/L6. Are there mostly theoretical considerations, i.e. would we expect the infragranular layers to be more relevant for understanding the difference in task performance? Or were there also practical considerations, e. g. did the data set contain mostly L5/L6 neurons because those were easier to record from given the angle at which the probe was inserted? If those kinds of practical considerations played a role, then there is nothing wrong with that but it would be helpful to explain them for the benefit of others who might try a similar recording approach.

There were no deep theoretical considerations for targeting L5/6.  Our focus on layers 5/6 was driven by both methodological and biological considerations. Methodologically, our electrode penetrations were optimized to span multiple auditory cortical areas, and deeper layers provided greater mechanical stability for chronic recordings. Biologically, layers 5/6 contain the principal output neurons of the auditory cortex and are well-positioned to influence downstream decision-making circuits. We acknowledge the limitation of our recordings to these layers in the manuscript (L268; L463–467). See also comment D of reviewer 3.

(9) Supplementary Table 2: The numbers in brackets indicate fractions rather than percentages.

Fixed.

(10) Figure S4-3: The figure legend implies that the number of neurons with significant discriminability for the hard stimulus and significant discriminability for choice was identical. (adolescent neurons = 368, mice = 5, recordings = 10; adult n = 544, mice = 6, recordings = 12 in both cases). Presumably, that is not actually the case and rather the result of a copy/paste operation gone wrong. Furthermore, I think it would be helpful to state the fractions of neurons that can discriminate between the stimuli and between the choices that the animal made in the main text.

Thank you for spotting the mistake. We corrected the n’s and added the percentage of neurons that discriminate stimulus and choice in the main text and the figure legend.

(11) Line 301: 'We used a ... decoder to quantify hit versus correct reject trial outcomes': I'm not sure I understand the rationale here. For the single unit analysis hit and false alarm trials were compared to assess their ability to discriminate the stimuli. FA and CR trials were compared to assess whether neurons can encode the choice of the mice. But the hit and CR trials which are contrasted here differ in terms of both stimulus and behavior/choice so what is supposed to be decoded here, what is supposed to be achieved with this analysis?

Thank you for this important point. You're correct that comparing hit and CR trials captures differences in both stimulus and choice, or task-related differences. We chose this contrast for the population decoding analysis to achieve higher trial counts per session and similar number of trials which are necessary for the reliability of the analysis. While this approach does not isolate stimulus from choice encoding, it provides an overall measure of how well population activity distinguishes task-relevant outcomes. We explicitly acknowledge this issue in L313-314.

(12) Line 332: What do you mean when you say the novice mice were 'otherwise fully engaged' in the task when they were not trained to do the task and are not doing the task?

By "otherwise fully engaged," we mean that novice mice were actively participating in the task environment, similar to expert mice — they were motivated by thirst and licked the spout to obtain water. The key distinction is that novice mice had not yet learned the task rules and likely relied on trial-and-error strategies, rather than performing the task proficiently.

(13) Line 334: 'regardless of trial outcome': Why is the trial outcome not taken into account? What is the rationale for this analysis? Furthermore, in novice mice a substantial proportion of the 'go' trials are misses. In expert mice, however, the proportion of 'miss trials' (and presumably false alarms) will by definition be much smaller. Given this, I find it difficult to interpret the results of this section.

This approach was chosen to reliably decode a sufficient number of trials for each task difficulty (i.e. expert mice predominantly performed CRs on No-Go trials and novice mice often showed FAs). Utilizing all trial outcomes ensured that we had enough trials for each stimulus type to accurately estimate the AUCs. This approach avoids introducing biases due to uneven trial numbers across learning stages.

(14) Line 378: 'differences between adolescents and adults arise primarily from age': Are there differences in any of the metrics shown in 7e-h between adolescents and adults?

We confirm that differences between adolescents and adults are indeed present in some metrics but not others in Figure 7e–h. Specifically, while tuning bandwidth was similar in novice animals, it was significantly lower in adult experts (Fig. 7e; novice: p = 0.0882; expert: p = 0.0001 Kruskal Willis Test after Tukey-Kramer correction for multiple comparisons; not discussed in the manuscript). The population sparseness was similar in both novice and expert adolescent and adult neurons (Fig. 7f; novice: p = 0.2873; expert: p = 0.1017, Kruskal Willis Test after Tukey-Kramer correction for multiple comparisons; not discussed in the manuscript). The distance to the easy go stimulus was similar in novice animals, but lower in adult experts (Fig. 7g; novice: p = 0.7727; expert: p = 0.0001, Kruskal Willis Test after Tukey-Kramer correction for multiple comparisons; not discussed in the manuscript). The neuronal d-prime was similar in both novice and expert adolescent and adult neurons (Fig. 7h; novice: p = 0.7727; expert: p = 0.0001, Kruskal Willis Test after Tukey-Kramer correction for multiple comparisons; not discussed in the manuscript).

(15) Line 475: '...well and beyond...': something seems to be missing in this statement.

(16) Line 487: 'onto' should be 'into', I think.

(17) Line 610 and 613: '3 seconds' ... '2.5 seconds': Was the response window 3s or 2.5s?

(18) Line 638: 'set' should be 'setup', I believe.

All the mistakes mentioned above, were fixed. Thanks.

(19) Line 643: 'Reward-reinforcement was delayed to 0.5 seconds after the tone offset': Presumably, if they completed their fifth lick later than 0.5 seconds after the tone, the reward delivery was also delayed?

Apologies for the lack of clarity. In the head-fixed version, there was no lick threshold. Mice were reinforced after a single lick. If that lick occurred after the 0.5-second reinforcement delay following tone offset, the reward or punishment was delivered immediately upon licking.

(20) Line 661: 'effect [of] ACx'.

(21) Line 680: 'a base-station connected to chassis'. The sentence sounds incomplete.

(22) Line 746: 'infliction', I believe, should say 'inflection'.

(23) Line 769: 'non-auditory responsive units': Shouldn't that simply say 'non-responsive units'? The way it is currently written I understand it to mean that these units were responsive (to some other modality perhaps) but not to auditory stimulation.

(24) Line 791: 'bins [of] 50ms'.

(25) Line 811: 'all of' > 'of all'.

(26) Line 814: Looks like the previous paragraph on single unit analysis was accidentally repeated under the wrong heading.

(27) Line 817: 'encoded' should say 'calculated', I believe.

All the mistakes mentioned above were fixed. Thanks.

(28) Line 869: 'bandwidth of excited units': Not sure I understand how exactly the bandwidth, i.e. tuning width was measured.

We acknowledge that our previous answer was unclear and expanded the Methods section. To calculate bandwidth, we identified significant tone-evoked responses by comparing activity during the tone window to baseline firing rates at 62 dB SPL (p < 0.05). For each neuron, we counted the number of contiguous frequencies with significant excitatory responses, subtracting isolated false positives to correct for chance. We then converted this count into an octave-based bandwidth by multiplying the number of frequency bins by the octave spacing between them (0.1661 octaves per step).

(29) Line 871: 'population sparseness': Is that the fraction of tone frequencies that produced a significant response? I would have thought that this measure is very highly correlated to your measure of bandwidth, to the point of being redundant, but I may have misunderstood how one or the other is calculated. Furthermore, the Y label of Figure 7f says 'responsiveness' rather than sparseness and that would seem to be the more appropriate term because, unless I am misunderstanding this, a larger value here implies that the neuron responded to more frequencies, i.e. in a less sparse manner.

We have clarified the use of the term "population sparseness" and updated the Y-axis label in Figure 7f to better reflect this measure. This metric reflects the fraction of tone–attenuation combinations that elicited a significant excitatory response across the entire population of neurons, not within individual units.

While this measure is related to bandwidth, it captures a distinct property of the data. Bandwidth quantifies how broadly or narrowly a single neuron responds across frequencies at a fixed intensity, whereas population sparseness reflects how distributed responsiveness is across the population as a whole. Although the two measures are related, since broadly tuned neurons often contribute to lower population sparseness, they capture distinct aspects of neural coding and are not redundant.

(30) Line 881: I think this line should refer to Figure 7h rather than 7g.

Fixed.

Reviewer #3 (Recommendations for the authors):

(1) In the Educage, water was only available when animals engaged in the task; however, there is no mention of whether/how animal weight was monitored.

In the Educage, mice had continuous access to water by voluntarily engaging in the task, which they could perform at any time. Although body weight was not directly monitored, water access was essentially ad libitum, and mice performed hundreds of trials per day, thereby ensuring sufficient daily intake. This approach allowed us to monitor hydration (ad libitum food is supplied in the home cage). The 24/7 setup, including automated monitoring of trial counts and water consumption, was reviewed and approved by our institutional animal care and use committee (IACUC).

(2) In Figure 2B-C and Figure 2E, the y-axis reads "lick rate". At first glance, I took this to mean "the frequency of licking" (i.e. an animal typically licks at a rate of 5 Hz). However, what the authors actually are plotting here is the proportion of trials on which an animal elicited >= 5 licks during the response window (i.e. the proportion of "yes" responses). I recommend editing the y-axis and the text for clarity.

We replaced the y-label and adjusted the figure legend (Fig. 2).

(3) I didn't see any examples of raw (filtered) voltage traces. It would be worth including some to demonstrate the quality of the data.

We have added an example of a filtered voltage trace aligned to tone onset in Fig. S4-1a to illustrate data quality. In addition, all raw and processed voltage traces, along with relevant analysis code, are available through our GitHub repository and the corresponding dataset on Zenodo.

(4) The description of the calculation of bias (C) in the methods section (lines 749-750) is incorrect. The correct formula is C = -0.5 * [z(hit rate) + z(fa rate)]. I believe this is the formula that the authors used, as they report negative C values. Please clarify or correct.

Thanks for spotting this. It is now corrected.

(5) The authors use the terms 'naïve' and 'novice' interchangeably. I suggest sticking with one term to avoid potential confusion.

(6) Multiple instances: "less trials/day" should be "fewer trials/day"

(7) Supplementary Table 2: The values reported are proportions, not percentages. Please correct.

(8) Line 270: Table 2 does not show the number of neurons in the dataset categorized by region. Perhaps the authors meant Supplementary Table 2?

Fixed. Thank you for pointing these mistakes out.

(9) Figure 5C: the data from the hard task are entirely obscured by the data from the easy task. I recommend splitting it into two different plots.

We agree and split the decoding of the easy and the hard task into two graphs (left: easy task; right: hard task). Thank you!

(10) How many mice contributed to each analyzed data set? Could the authors provide a breakdown in a table somewhere of how many neurons were recorded in each mouse and which ones were included in which analyses?

We added an overview of the analyzed datasets in supplementary Table 7. Please note that the number of mice and neurons used in each analysis is also reported in the main text and legends. Importantly, all primary analyses were conducted using LME models, which explicitly account for hierarchical data structure and inter-mouse variability, thereby addressing potential concerns about data imbalance or bias.

Author Response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review): 

Summary:

The authors use analysis of existing data, mathematical modelling, and new experiments, to explore the relationship between protein expression noise, translation efficiency, and transcriptional bursting.

Strengths:

The analysis of the old data and the new data presented is interesting and mostly convincing.

Thank you for the constructive suggestions and comments. We address the individual comments below. 

Weaknesses:

(1) My main concern is the analysis presented in Figure 4. This is the core of mechanistic analysis that suggests ribosomal demand can explain the observed phenomenon. I am both confused by the assumptions used here and the details of the mathematical modelling used in this section. Firstly, the authors' assumption that the fluctuations of a single gene mRNA levels will significantly affect ribosome demand is puzzling. On average the total level of mRNA across all genes would stay very constant and therefore there are no big fluctuations in the ribosome demand due to the burstiness of transcription of individual genes. Secondly, the analysis uses 19 mathematical functions that are in Table S1, but there are not really enough details for me to understand how this is used, are these included in a TASEP simulation? In what way are mRNA-prev and mRNA-curr used? What is the mechanistic meaning of different terms and exponents? As the authors use this analysis to argue ribosomal demand is at play, I would like this section to be very much clarified.

Thank you for raising two important points. Regarding the first point, we agree that the overall ribosome demand in a cell will remain mostly the same even with fluctuations in mRNA levels of a few genes. However, what we refer to in the manuscript is the demand for ribosomes for translating mRNA molecules of a single gene. This demand will vary with the changes in the number of mRNA molecules of that gene. When the mRNA copy number of the gene is low, the number of ribosomes required for translation is low. At a subsequent timepoint when the mRNA number of the same gene goes up rapidly due to transcriptional bursting, the number of ribosomes required would also increase rapidly. This would increase ribosome demand. The process of allocation of ribosomes for translation of these mRNA molecules will vary between cells, and this process can lead to increased expression variation of that gene among cells. We have now rephrased the section between the lines 321 and 331 to clarify this point.

Regarding the second point, each of the 19 mathematical functions was individually tested in the TASEP model and stochastic simulation. The parameters ‘mRNA-curr’ and ‘mRNA-prev’ are the mRNA copy numbers at the present time point and the previous time point in the stochastic simulations, respectively. These numbers were calculated from the rate of production of mRNA, which is influenced by the transcriptional burst frequency and the burst size, as well as the rate of mRNA removal. We have now incorporated more details about the modelling part along with explanation for parameters and terms in the revised manuscript (lines 390 to 411; lines 795 to lines 807). 

(2) Overall, the paper is very long and as there are analytical expressions for protein noise (e.g. see Paulsson Nature 2004), some of these results do not need to rely on Gillespie simulations. Protein CV (noise) can be written as three terms representing protein noise contribution, mRNA expression contribution, and bursty transcription contribution. For example, the results in panel 1 are fully consistent with the parameter regime, protein noise is negligible compared to transcriptional noise. 

Thank you for referring to the paper on analytical expressions for protein noise. We introduced translational bursting and ribosome demand in our model, and these are linked to stochastic fluctuations in mRNA and ribosome numbers. In addition, our model couples transcriptional bursting with translational bursting and ribosome demand. Since these processes are all stochastic in nature, we felt that the stochastic simulation would be able to better capture the fluctuations in mRNA and protein expression levels originating from these processes. For consistency, we used stochastic simulations throughout even when the coupling between transcription and translation were not considered. 

Reviewer #1 (Recommendations for the authors):  

(1) Figure 1B shows noise as Distance to Median (DM) that can be positive or negative. It is therefore misleading that the authors say there is a 10-fold increase in noise (this would be relevant if the quantity was strictly positive). How is the 10-fold estimated? Similar comments apply to Figure 1F and the estimated 37-fold. I also wonder if the datasets combined from different studies are necessarily compatible.

We have now changed the statements and mentioned the actual noise values for different classes of genes rather than the fold-changes (lines 111-113 and 143-145). We agree that the measurements for mRNA expression levels, protein synthesis rates and protein noise were obtained from experiments done by different research labs, and this could introduce more variation in the data. However, it is unlikely the experimental variations are likely to be random and do not bias any specific class of genes (in Fig. 1B and Fig. 1F) more than others.  

(2)   How Figure 1D has been generated seems confusing, the authors state this is based on the Gillespie algorithm, but in panel 1C and also in the methods, they are writing ODEs and Equations 3 and 4 stating the Euler method for the solution of ODEs. Also, I am concerned if this has been done at steady-state. The protein noise for the two-state model can be analytically obtained, and instead of simulations, the authors could have just used the expression. Also, Figure 1D shows CV while the corresponding data Figure 1B is showing mean adjusted DM. So, I am not sure if the comparison is valid. I am also very confused about the fact that the authors show CV does not depend on the mean expression of proteins and mRNA. Analytical solutions suggested there is always an inverse relationship exists between CV and mean and this has also been experimentally observed (see for example Newman et al 2006).

We used Gillespie algorithm for stochastic simulations and identified the time points when an event (for example, switching to ON or OFF states during transcriptional bursting) occurred. If an event occurred at a time point, the rates of the reactions were guided by the equations 3 and 4, as the rates of reactions were dependent on the number of mRNA (or protein) molecules present, production rates and removal rates. 

For all published datasets where we had measurements from many genes/promoters, we used the measures of adjusted noise (for mRNA noise) and Distance-to-median (DM, for protein noise). These measures of noise are corrected mean-dependence of expression noise (Newman et al., 2006). For simulations, which we performed for a single gene, and for experiments that we performed on a limited number of promoters, we used the measure of coefficient of variation (CV) to quantify noise, as calculation of adjusted noise or DM was not possible for a single gene. 

The work of Newman et al. (2006) measures noise values of different genes with different transcriptional burst characteristics and different mRNA and protein removal rates. We also see similar results in our simulations (Fig. 1E), where as we increase the mean expression by changing the transcriptional burst frequency, the protein noise goes down.     

(3) Estimating parameters of gene expression using reference 44 ignores the effect of variability in capture efficiency and cell size. In a recent paper, Tang et al Bioinformatics 39 (7), btad395 2023 addressed this issue.

Thank you for referring to the work of Tang et al. (2023). We note that the cell size and capture efficiency have a small effect on the burst frequency (Kon) but has a more pronounced effect on burst size (Tang et al., 2023). In our analysis, we considered only burst frequency and even with likely small inaccuracies in our estimation of Kon, we can capture interesting association of burst frequency with noise trends. 

(4) In the methods "αp = 0.007 per mRNA molecule per unit time", I believe it should be per protein molecule per unit time.

Corrected.

(5)  Figure 3 uses TASEP modelling but the details of this modelling are not described well.

We have now expanded the description of the modelling approach in the revised manuscript (lines 391-412; lines 693-776 and lines 797-809). In addition, we have also added more details in the figure captions. 

(6) Another overall issue is that when the authors talk about changes in burst frequency or changes in translation efficiency, it is not always clear, is this done while keeping all the other parameters constant therefore changing mean expressions, or is this done by keeping the mean expressions constant?

To test for the association between mean protein expression and protein noise, we have varied the mean expression by changing the translation initiation rate (TLinit) for the most part of the manuscript while keeping other parameters constant. In figure 5, where we decoupled TLinit from ribosome traversal rate (V), we changed the mean protein expression by changing the ribosome traversal rate while keeping other parameters constant. We have now mentioned this in the manuscript. 

(7)   I believe Figures 5 and 6 present the same data in different ways, I wonder if these can be combined or if some aspect of the data in Figure 5 could go to supplementary. Also, the statistical tests in Figure 5E and F are not clear what they are testing.

We have now moved figures 5E and 5F to the supplement (Fig. S20). We have also added details of the statistical test in the figure caption. 

Reviewer #2 (Public review): 

This work by Pal et al. studied the relationship between protein expression noise and translational efficiency. They proposed a model based on ribosome demand to explain the positive correlation between them, which is new as far as I realize. Nevertheless, I found the evidence of the main idea that it is the ribosome demand generating this correlation is weak. Below are my major and minor comments.

Thank you for your helpful suggestions and comments. We note that the direct experimental support required for the ribosome demand model would need experimental setups that are beyond the currently available methodologies. We address the individual comments below. 

Major comments: 

(1) Besides a hypothetical numerical model, I did not find any direct experimental evidence supporting the ribosome demand model. Therefore, I think the main conclusions of this work are a bit overstated.

Direct experimental evidence of the hypothesis would require generation of ribosome occupancy maps of mRNA molecules of specific genes at the level of single cells and at time intervals that closely match the burst frequency of the genes. This is beyond the currently available methodologies. However, there are other evidences that support our model. For example, earlier work in cell-free systems have showed that constraining cellular resources required for transcription or translation can increase expression heterogeneity (Caveney et al., 2017). In addition, the ribosome demand model had two predictions both of which could be validated through modelling as well as from our experiments. 

To further investigate whether removing ribosome demand from our model could eliminate the positive mean-noise correlation for a gene, we have now tested two additional sets of models where we decoupled the translation initiation rate (TLinit) from the ribosome traversal speed (V). In the first model, we changed the mean protein expression by changing the translation initiation rate but keeping the ribosome traversal speed constant. Thus, in this scenario, ribosome demand varied according to the variation in the translation initiation rate. As expected, the positive correlation between mean expression and protein noise was maintained in this condition (Fig. 5B). In the second model, we changed the mean expression by changing the ribosome traversal speed but keeping the translation initiation rate (and therefore, the ribosome demand) constant. In this situation, the relationship between mean expression and protein noise turned negative (Fig. 5B and fig. S16). These results further pointed that the ribosome demand was indeed driving the positive relationship between mean expression and protein noise. 

(2) I found that the enhancement of protein noise due to high translational efficiency is quite mild, as shown in Figure 6A-B, which makes the biological significance of this effect unclear.

We agree with the reviewer’s comment that the effect of translational efficiency on protein noise may not be as substantial as the effect of transcriptional bursting, but it has been observed in studies across bacteria, yeast, and Arabidopsis (Ozbudak et al., 2003; Blake et al., 2003; Wu et al., 2022). In addition, the relationship between translational efficiency and protein noise is in contrast with the inverse relationship observed between mean expression and noise (Newman et al., 2006; Silander et al., 2012). We also note that the goal of the manuscript was not to evaluate the relative strength of these associations, but to understand the molecular basis of the influence of translational efficiency on protein noise. 

(3) The captions for most of the figures are short and do not provide much explanation, making the figures difficult to read.

We have revised the figure captions to include more details as per the reviewer’s suggestion. 

(4)  It would be helpful if the authors could define the meanings of noise (e.g., coefficient of variation?) and translational efficiency in the very beginning to avoid any confusion. It is also unclear to me whether the noise from the experimental data is defined according to protein numbers or concentrations, which is presumably important since budding yeasts are growing cells. 

For all published datasets where we had measurements from many genes/promoters, we used the measures of adjusted noise (for mRNA noise) and Distance-tomedian (DM, for protein noise). These measures of noise are corrected mean-dependence of expression noise. For simulations, which we performed for a single gene, and for experiments that we performed on a limited number of promoters, we used the measure of coefficient of variation (CV) to quantify noise, as calculation of adjusted noise or DM was not possible for a single gene. We now mention this in line 123-124. We used the measure of protein synthesis rate per mRNA as the measure of translational efficiency (Riba et al., 2019; line 100). Alternatively, we also used tRNA adaptation index (tAI) as a measure of translational efficiency, as codon choice could also influence the translation rate per mRNA molecule (Tuller et al., 2010) (line 193). 

The protein noise was quantified from the signal intensity of GFP tagged proteins (Newman et al., 2006; and our data), which was proportional to protein numbers without considering cell volume. For quantification of noise at the mRNA level, single-cell RNA-seq data was used, which provided mRNA numbers in individual cells.  

(5) The conclusions from Figures 1D and 1E are not new. For example, the constant protein noise as a function of mean protein expression is a known result of the two-state model of gene expression, e.g., see Equation (4) in Paulsson, Physics of Life Reviews 2005.

Yes, they may not be new, but we included these results for setting the baseline for comparison with simulation results that appear in the later part of the manuscript where we included translational bursting and ribosome demand in our models. 

(6) In Figure 4C-D, it is unclear to me how the authors changed the mean protein expression if the translation initiation rate is a function of variation in mRNA number and other random variables.

The translation initiation rate varied from a basal translation initiation rate depending on the mRNA numbers and other variables. We changed the basal translation initiation rate to alter the mean protein expression levels. We have now elaborated the modelling section to incorporate these details in the revised manuscript (lines 404 to 412). 

(7) If I understand correctly, the authors somehow changed the translation initiation rate to change the mean protein expression in Figures 4C-D. However, the authors changed the protein sequences in the experimental data of Figure 6. I am not sure if the comparison between simulations and experimental data is appropriate.

It is an important observation. Even though we changed the basal translation initiation rate to change the mean expression (Fig. 4C-D), we noted in the description of the model that the changes in the translation initiation rate were also linked to changes in the translation elongation rate (Fig. 3D). Thus, an increase in the translation initiation rate was associated with faster ribosome traversal through an mRNA molecule. This has also been observed in an experimental study by Barrington et al. (2023). Therefore, the models can also be expressed in terms of the translation elongation rate or ribosome traversal speed, instead of the translation initiation rate, and this modification will not change the results of the simulations due to interconnectedness of the initiation rate and the elongation rate.  

Reviewer #2 (Recommendations for the authors):

Minor comments:

(1)  The discussion from lines 180 to 182 appears consistent with Figure 1E. It seems that the twostate model can already explain why the genes with high burst frequency and high protein synthesis rate showed a small protein noise. It is unclear to me the purpose of this discussion.

Yes, the results from Fig. 1E were from stochastic simulations, whereas the results discussed in the lines 191 to 193 (in the revised manuscript) were based on our analysis of experimental data that is shown in Fig. 2D.

(2)  If I understand correctly, "translational efficiency" is the same as "protein synthesis rate" in this work. It would be helpful if the authors could keep the same notation throughout the paper to avoid confusion.

The protein synthesis rate per mRNA molecule is the best measure of translational efficiency, and we used the experimental data from Riba et al. (2019) for this purpose (line 99-100). Alternatively, we also used tRNA Adaptation Index (tAI) as a measure of translational efficiency, as the codon choice also influences the rate at which an mRNA molecule is translated (Tuller et al., 2010) (line 192). 

(3) On line 227, does "higher translation rate" mean "higher translation initiation rate"? The same issues happen in a few places in this paper.

Corrected now (line 243 in the revised manuscript and throughout the manuscript). 

(4) The discussion from lines 296 to 301 is unclear. It is not obvious to me how the authors obtained the conclusion that lowering translational efficiency would decrease the protein expression noise.

High translational efficiency will require more ribosomes and hence, will increase ribosome demand. If ribosome demand is the molecular basis of high expression noise for genes with bursty transcription and high translational efficiency, then we can expect a reduction in ribosome demand and a reduction in noise if we lower the translational efficiency. We have rephrased this section for clarity between the lines 334 and 339 in the revised manuscript.   

(5)  On line 324, should slower translation mean a shorter distance between neighboring ribosomes? One can imagine the extreme limit in which ribosomes move very slowly so that the mRNA is fully packed with ribosomes. 

Slower translation or ribosome traversal rate would also lower the translation initiation rate (Barrington et al., 2023). Slower traversal of ribosomes reduces the chances of collision in case of transient slow-down of ribosomes due to occurrence of one or more non-preferred codons. We have now clarified this part in the lines 360 to 369 in the revised manuscript.

(6) The text from lines 423 to 433 can be put in Methods.

We have already added this part to the methods section (lines 900 to 910) and now minimize this discussion in the results section. 

(7)  The discussion from lines 128 to 130 is unclear, and the statement appears to be consistent with the two-state model (see Figure 1E). The meaning of "initial mRNA numbers" is also unclear.

An earlier study has proposed that essential genes in yeast employs high transcription and low translation strategy for expression, likely to maintain low expression noise in these genes and to prevent detrimental effects of high expression noise (Fraser et al., 2004). However, there has been no direct supportive evidence. Therefore, we were testing whether the differences in mRNA levels and translational efficiency of genes can lead to differences in protein noise through stochastic simulations. The discussion between the lines 130 and 132 in the revised manuscript summarises the results of the simulations. 

Initial mRNA numbers - mRNA copy numbers that are present in the cell at the start of stochastic simulations. However, we have now changed it to ‘mRNA levels’ in the revised manuscript for clarity (line 131 in the revised manuscript).

(8)  On line 212, is the translation initiation rate TL_init the same thing as beta_p in Figure 3A?

βp refers to the rate of protein synthesis, which is influenced by the translational burst kinetics as well as the translation initiation rate, whereas TLinit refers to the translation initiation rate. So, these parameters are related, but are not the same.

Author Response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Summary:

In this study, Floedder et al report that dopamine ramps in both Pavlovian and Instrumental conditions are shaped by reward interval statistics. Dopamine ramps are an interesting phenomenon because at first glance they do not represent the classical reward prediction errors associated with dopamine signaling. Instead, they seem somewhat to bridge the gap between tonic and phasic dopamine, with an intense discussion still being held in the field about what is their actual behavioral role. Here, in tests with head-fixed mice, and dopamine being recorded with a genetically encoded fluorescent sensor in the nucleus accumbens, the authors find that dopamine ramps were only present when intertrial intervals were relatively short and the structure of the task (Pavlovian cue or progression in a VR corridor) contained elements that indicated progression towards the reward (e.g., a dynamic cue). The authors show that these findings are well explained by their previously published model of Adjusted Net Contingency of Causal Relation (ANCCR).

Strengths:

This descriptive study delineates some fundamental parameters that define dopamine ramps in the studied conditions. The short, objective, and to-the-point format of the manuscript is great and really does a service to potential readers. The authors are very careful with the scope of their conclusions, which is appreciated by this reviewer.

We thank the reviewer for their overall support of the formatting and scope of the manuscript. 

Weaknesses:

The discussion of the results is very limited to the conceptual framework of the authors' preferred model (which the authors do recognize, but it still is a limitation). The correlation analysis presented in panel l of Figure 3 seems unnecessary at best and could be misleading, as it is really driven by the categorical differences between the two conditions that were grouped for this analysis. There are some key aspects of the data and their relationship with each other, the previous literature, and the methods used to collect them, that could have been better discussed and explored.

We agree with the reviewer that a weakness of the discussion was the limited framing of the results within the ANCCR model. To address this, we have expanded our introduction and discussion sections to provide a more thorough explanation of our model and possible leading alternatives.

We thank the reviewer for pointing out that Figure 3l may be misleading for readers; we removed this panel from the revised Figure 4.

We have further addressed the specific concerns raised by the reviewer in their comments to the authors. Indeed, we agree with the reviewer that the original manuscript was narrow in its focus regarding relationships between different aspects of the data. To more thoroughly explore how key variables – including dopamine ramp slope and onset response as well as licking behavior slope – could relate to each other, we have added Extended Data Figure 8. In this figure, we show that no correlations exist between any of these key variables in either dynamic tone condition; it is our hope that this additional analysis highlights the significance of the clear relationship between dopamine ramp slope and ITI duration. 

Reviewer #2 (Public Review):

In this manuscript by Floeder et al., the authors report a correlation between ITI duration and the strength of a dopamine ramp occurring in the time between a predictive conditioned stimulus and a subsequent reward. They found this relationship occurring within two different tasks with mice, during both a Pavlovian task as well as an instrumental virtual visual navigation task. Additionally, they observed this relationship only in conditions when using a dynamic predictive stimulus. The authors relate this finding to their previously published model ANCCR in which the time constant of the eligibility trace is proportionate to the reward rate within the task.

The relationship between ITI duration and the extent of a dopamine ramp which the authors have reported is very intriguing and certainly provides an important constraint for models for dopamine function. As such, these findings are potentially highly impactful to the field. I do have a few questions for the authors which are written below.

We thank the reviewer for their interest in our findings and belief in their potential to be impactful in the field. 

(1) I was surprised to see a lack of counterbalance within the Pavlovian design for the order of the long vs short ITI. Ramping of the lick rate does increase from the long-duration ITIs to the short-duration ITI sessions. Although of course, this increase in ramping of the licking across the two conditions is not necessarily a function of learning, it doesn't lend support to the opposite possibility that the timing of the dynamic CS hasn't reached asymptotic learning by the end of the long-duration ITI. The authors do reference papers in which overtraining tends to result in a reduction of ramping, which would argue against this possibility, yet differential learning of the dynamic CS would presumably be required to observe this effect. Do the authors have any evidence that the effect is not due to heightened learning of the timing of the dynamic CS across the experiment?

We appreciate the reviewer expressing their surprise regarding the lack of counterbalance in our Pavlovian experimental design. We previously did not explicitly do this because the ramps disappeared in the short ITI/fixed tone condition, indicating that their presence is not just a matter of total experience in the task. However, we agree that this is incidental, but not direct evidence. To address this drawback, we repeated the Pavlovian experiment in a new cohort of animals with a revised training order, switching conditions such that the short ITI/dynamic tone (SD) condition preceded the long ITI/dynamic tone (LD) condition (see revised Figure 2a). Despite this change in the training order, the main findings remain consistent: positive dLight slopes (i.e., dopamine ramps) are only observed in the SD condition (Figure 2b-d). 

We thank the reviewer for raising these questions regarding licking behavior and learning and their relationship with dopamine ramps. Indeed, a closer look at the average licking behavior reveals subtle differences across conditions (Figure 1f and Extended Data Figure 5a). While the average lick rate during the ramp window does not differ across conditions (Extended Data Figure 5c), the ramping of the lick rate during this window is higher for dynamic tone conditions compared to fixed tone conditions (Extended Data Figure 5d). Despite these differences, we still believe that the main comparison between the dopamine slope in the SD vs LD condition remains valid given their similar lick ramping slopes. Furthermore, our primary measure of learning is not lick slope, but anticipatory lick rate during the 1 s trace preceding reward delivery, which is robustly nonzero across cohorts and conditions (Figure 1g and Extended Data Figure 5b). 

Taken together, we hope that the results from our counterbalanced Pavlovian training and more rigorous analysis of lick behavior across conditions provide sufficient evidence to assuage concerns that the differences in ramping dopamine simply reflect differences in learning. 

(2) The dopamine response, as measured by dLight, seems to drop after the reward is delivered. This reduction in responding also tends to be observed with electrophysiological recordings of dopamine neurons. It seems possible that during the short ITI sessions, particularly on the shorter ITI duration trials, that dopamine levels may still be reduced from the previous trial at the onset of the CS on the subsequent trial. Perhaps the authors can observe the dynamics of the recovery of the dopamine response following a reward delivery on longer-duration ITIs in order to determine how quickly dopamine is recovering following a reward delivery. Are the trials with very short ITIs occurring within this period that dopamine is recovering from the previous trial? If so, how much of the effect may be due to this effect? It should be noted that the lack of observance of a ramp on the condition of shortduration ITIs with fixed CSs provides a potential control for this effect, yet the extent to which a natural ramp might occur following sucrose deliveries should be investigated.

We thank the reviewer for highlighting the possibility that ramps may be due to the dopamine response recovery following reward delivery. Given that peak reward dopamine responses tend to be larger in long ITI conditions, however, we felt that it was inappropriate to compare post-reward dopamine recovery times across conditions. Instead, we decided to directly compare the dLight slope 2s before cue onset (“pre-cue window,” a proxy for recovery from previous trial) with the dLight slope during our ramp window from 3 to 8s after cue onset (Extended Data Figure 6a). There were no significant differences in pre-cue dLight slope across conditions (Extended Data Figure 6b); this suggests that the ramping slopes seen in the SD condition, but not other conditions, is not simply due to the natural dopamine recovery response following reward delivery. Furthermore, if the dopamine ramps observed in the SD condition were a continuation of the post-reward dopamine recovery from the previous trial, we would expect to see a positive correlation between the dLight slope before and during the cue. However, there is no such correlation between the dLight slopes in the ramp window vs. pre-cue window in the SD condition (Extended Data Figure 6c-d). We believe that this observation, along with the builtin control of the SF condition mentioned by the reviewer, serves as evidence against the possibility of our ramp results being due to a natural ramp after reward delivery.

(3) The authors primarily relate the finding of the correlation between the ITI and the slope of the ramp to their ANCCR model by suggesting that shorter time constants of the eligibility trace will result in more precisely timed predictors of reward across discrete periods of the dynamic cue. Based on this prediction, would the change in slope be more gradual, and perhaps be more correlated with a broader cumulative estimate of reward rate than just a single trial?

To clarify, we do not propose that a smaller eligibility trace time constant results in more precise timing per se. Instead, we believe that the rapid eligibility trace decay from smaller time constants gives greater causal predictive power for later periods in the dynamic cue (see Extended Data Figure 1) since the memory of the earlier periods of the cue is weaker. 

We appreciate the reviewer’s curiosity regarding the influence of a broader cumulative estimate of reward vs. only the immediately preceding ITI on dopamine ramp slopes. Indeed, in several instrumental tasks (e.g., Krausz et al., Neuron, 2023), recent reward rate modulates the magnitude of dopamine ramps, making this an important variable to investigate. We chose to use linear regression for each mouse separately to analyze the relationship between the trial dopamine slope and the average previous ITI for the past 1 through 10 most recent trials. In the SD condition, as reported in our earlier manuscript, there was a significantly negative dependence of trial dopamine slope with the single previous ITI (i.e., if the previous ITI was long, the next trial tends to have a weaker ramp). This negative dependence, however, only held for a single previous trial; there was no clear relationship between the per-trial dopamine slope and the average of the past 2 through 10 ITIs (Extended Data Figure 7a). For the LD condition, on the other hand, there is no clear relationship between the per-trial dopamine slope and the average previous ITI for any of the past 1 through 10 trials, with one exception: there is a significantly negative dependence of trial dopamine slope with the average ITI of the previous 2 trials (Extended Data Figure 7b). This longer timescale relationship in the LD condition suggests that the adaptation of the eligibility trace time constant is nuanced and depends on the general ITI length. 

In general, though we reason that the eligibility trace time constant should depend on overall event rates, we do not currently propose a real-time update rule for the eligibility trace time constant depending on recent event rates. Accordingly, we are currently agnostic about the actual time scale of history of recent event rate calculation that mediates the eligibility trace time constant. Our experimental results suggest that when the ITI is generally short for Pavlovian conditioning, the eligibility trace time constant adapts to ITI on a rapid timescale. However, only a small fraction of the variability of this rapid fluctuation is captured by recent ITI history. A more thorough investigation of this real-time update rule would need to be done in the future.

Reviewer #3 (Public Review):

Summary:

Floeder and colleagues measure dopamine signaling in the nucleus accumbens core using fiber photometry of the dLight sensor, in Pavlovian and instrumental tasks in mice. They test some predictions from a recently proposed model (ANCCR) regarding the existence of "ramps" in dopamine that have been seen in some previous research, the characteristics of which remain poorly understood.

They find that cues signaling a progression toward rewards (akin to a countdown) specifically promote ramping dopamine signaling in the nucleus accumbens core, but only when the intertrial interval just experienced was short. This work is discussed in the context of ongoing theoretical conceptions of dopamine's role in learning.

Strengths:

This work is the clearest demonstration to date of concrete training factors that seem to directly impact whether or not dopamine ramps occur. The existence of ramping signals has long been a feature of debates in the dopamine literature and this work adds important context to that. Further, as a practical assessment of the impact of a relatively simple trial structure manipulation on dopamine patterns, this work will be important for guiding future studies. These studies are well done and thoughtfully presented.

We thank the reviewer for recognizing the context that our study adds to the dopamine literature and the potential for our experiments to guide future work. 

Weaknesses:

It remains somewhat unclear what limits are in place on the extent to which an eligibility trace is reflected in dopamine signals. In the current study, a specific set of ITIs was used, and one wonders if the relative comparison of ITI/history variables ("shorter" or "longer") is a factor in how the dopamine signal emerges, in addition to the explicit length ("short" or "long") of the ITI. Another experimental condition, where variable ITIs were intermingled, could perhaps help clarify some remaining questions.

Though we used ITIs of fixed means, due to the exponential nature of their distribution, we did intermingle ITIs of various durations in both our long and short ITI conditions. The distribution of ITI durations is visualized in Figure 1c for Pavlovian conditioning and Extended Data Figure 9b for VR navigation. 

The relative comparison between consecutive ITIs was not something we originally explored, so we thank the reviewer for wondering how it impacts the dopamine signal. To investigate this, we quantified both the change in ITI (+ or - Δ ITI for relatively longer or shorter, respectively) and the change in dopamine ramp slope between consecutive trials in the SD condition (Figure 3d). Across each mouse separately, we found a significantly negative relationship between Δ slope and Δ ITI (Figure 3e-f). Also, the average Δ slope was significantly greater for consecutive trials with a Δ ITI below -1 s compared to trials with a Δ ITI above +1 s (Figure 3g). Altogether, these findings suggest that relative comparison of ITIs does correlate with changes in the dopamine signal; a relatively longer ITI tends to have a weaker ramp, which fits in nicely with the expected inverse relationship between ITI and dopamine ramp slope from our ANCCR model.

In both tasks, cue onset responses are larger, and longer on long ITI trials. One concern is that this larger signal makes seeing a ramp during the cue-reward interval harder, especially with a fluorescence method like photometry. Examining the traces in Figure 1i - in the long, dynamic cue condition the dopamine trace has not returned to baseline at the time of the "ramp" window onset, but the short dynamic trace has. So one wonders if it's possible the overall return to baseline trend in the long dynamic conditions might wash out a ramp.

This is a good point, and we thank the reviewer for raising it. Certainly, the cue onset response is significantly larger in long ITI conditions (see Figure 1i-j and Figure 4h-j). To avoid any bleed over effect, we intentionally chose ramp window periods during later portions of the trial (in line with work from others e.g., Kim et al., Cell, 2020). While the cue onset dopamine pulse seems to have flatlined by the start of the ramp window period, the dopamine levels clearly remain elevated relative to pre-cue baseline. This type of signal has been observed with fiber photometry in other Pavlovian conditioning paradigms with long cue durations (e.g., Jeong et al., Science, 2022). Because of the persistently elevated dopamine levels, it is certainly possible that a ramping signal during the cue is getting washed out; with the bulk fluorescence photometry technique we employed in this study, this possibility is unfortunately difficult to completely rule out. However, the long ITI/fixed tone (LF) condition could serve as a potential control given the overall similarity in the dopamine signal between the LF and LD conditions: both conditions have large cue onset responses with elevated dopamine throughout the duration of the cue (see Extended Data Figures 2c and 3c). Critically, the LD condition lacks a noticeable ramp despite the dynamic tone providing information on temporal proximity to reward, which is thought to be necessary for dopamine ramps to occur. Importantly, regardless of whether a ramp is masked in the long ITI dynamic condition, most studies investigate such a condition in isolation and would report the absence of dopamine ramps. Thus, at a descriptive level, we believe it remains true that observable dopamine ramps are only present when the ITI is short. 

Not a weakness of this study, but the current results certainly make one ponder the potential function of cue-reward interval ramps in dopamine (assuming there is a determinable function). In the current data, licking behavior was similar on different trial types, and that is described as specifically not explaining ramp activity.

We agree that this work naturally raises the question of the function of dopamine ramps. However, selective and precise manipulation of only the dopamine ramps without altering other features such as phasic responses, or inducing dopamine dips, is highly technically challenging at this moment; due to this challenge, we intentionally focused on the conditions that determine the presence or absence of dopamine ramps rather than their function. We agree with the reviewer that studying the specific function of dopamine ramps is an interesting future question. 

Reviewing Editor:

The reviewers felt the results are of considerable and broad interest to the neuroscience community, but that the framing in terms of ANCCR undermined the scope of the findings as did the brief nature of the formatting of the manuscript. In addition, the reviewers felt that the relationship between ramp dynamics, behavior, and ITI conditions requires more in-depth analyses. Relatedly, the lack of counterbalancing of the ITI durations was considered to be a drawback and needs to be addressed as it may affect the baseline. Addressing these issues in a satisfactory manner would improve the assessment of the manuscript to important/convincing.

We truly appreciate the valuable feedback provided on this manuscript by all three reviewers and the reviewing editor. Based on this input, we have significantly revised the manuscript to address the issues brought up by the reviewers. Firstly, we have conducted additional experiments to counterbalance the ITI conditions for Pavlovian conditioning; this strengthened our results by confirming our original findings that ITI duration, rather than training order, is the key variable controlling the presence or absence of dopamine ramps. Secondly, we completed more rigorous analyses to further explore the relationship between dopamine dynamics, animal behavior, and ITI duration; we generally found no significant correlations between these variables, with a notable exception being our main finding between ITI duration and dopamine ramp slope. Finally, we revised and expanded our writing to both explain predictions from our ANCCR model in less technical language and explore how alternative theoretical frameworks could potentially explain our findings. In doing so, we hope that our manuscript is now more accessible and of interest to a broad audience of neuroscience readers.

Reviewer #1 (Recommendations For The Authors):

The study could be improved if the authors performed a more detailed comparison of how other theoretical frameworks, beyond ANCCR could account for the observed findings. Also, the correlation analysis presented in the panel I of Figure 3 seems unnecessary and potentially spurious, as the slope of the correlation is clearly mostly driven by the categorical differences between the two ITI conditions, which were combined for the analysis - it's not clear what is the value of this analysis beyond the group comparison presented in the following panel.

Again, we thank the reviewer for elaborating on their concern regarding Figure 3l – we have removed it from the revised Figure 4. 

The relationship between ramp dynamics with the behavior and the large differences in cue onset responses between short and long ITI conditions could have been better explored. If I understand correctly the overarching proposal of this and other publications by this group, then the differences in cue responses is determined by the spacing of rewards in a somewhat similar way that the ramps are. So, is there a trial-by-trial correlation between the amplitude of the cue responses and the slope of the ramps? Is there a correlation between any of these two measures with the licking behavior, and if so, does it change with the ITI condition? A more thorough exploration of these relationships would help support the proposal of the primacy of inter-event spacing in determining the different types of dopamine responses in learning.

There are certainly interesting relationships between dopamine dynamics, behavior, and ITI that we failed to explore in our original manuscript – we appreciate the reviewer bringing them up. We found no correlation between dopamine ramp slope and cue onset response in either the SD or LD condition (Extended Data Fig 8a-b). Moreover, we found no correlation between either of these variables and the trial-by-trial licking behavior (Extended Data Fig 8c-f). Finally, there is no relationship between licking behavior and previous ITI duration (Extended Data Fig 8g-h), suggesting that behavioral differences do not account for differences in the dopamine ramp slope. Together, the lack of significant relationships between these other variables highlights the specific, clear relationship between ITI duration and dopamine ramp slope. 

Finally, another issue I feel could have been better discussed is how the particular settings of both tasks might be biasing the results. For example, there is an issue to be considered about how the dopamine ramp dynamics reported here, especially the requirement of a dynamic cue for ramps to be present, square with the previous published results by one of the authors - Mohebi et al, Nature, 2019. In that manuscript, rats were executing a bandit task where, to this reviewer's understanding, there was no explicit dynamic cue aside from the standard sensory feedback of the rats moving around in the behavior boxes to approach a nose poke port. Is the idea that this sensory feedback could function as a dynamic cue? If that's the case, then this short-scale, movement-related feedback should also function as a dynamic cue in a freely moving Pavlovian condition, when the animals must also move towards a reward delivery port, right? Therefore, could it be that the experimental "requirement" of a dynamic cue is only present in a head-fixed condition? One could phrase this in a different way to Steelman and potentially further the authors' proposal: perhaps in any slightly more naturalistic setting, the interaction of the animals with their environment always functions as a dynamic cue indicating proximity to reward, and this relationship was experimentally isolated by the use of head fixation (but not explicitly compared with a freely moving condition) in the present study. I think that would be an interesting alternative to consider and discuss, and perhaps explore experimentally at some point.

We thank the reviewer for raising this important point regarding the influence of our experimental settings on our results. At first glance, it could appear that our results demonstrating the necessity of a dynamic cue for ramps in a head-fixed setting do not fit neatly with other results in a freely moving setup (e.g., Collins et al., Scientific Reports, 2016; Mohebi et al., Nature, 2019). Exactly as the reviewer states though, we believe that sensory feedback from the environment in freely moving preparations serves the same function as a dynamic progression of cues. We have considered the implications of methodological differences between head-fixed and freely moving preparations in the discussion section. 

Reviewer #2 (Recommendations For The Authors):

This comment relates indirectly to comment 3, in that the authors intermix theory throughout the manuscript. I think this would be fine if the experiment was framed directly in terms of ANCCR, but the authors specifically mention that this experiment wasn't developed to distinguish between different theories. As such, it seems difficult to assess the scope of the comments regarding theory within the paper because they tend to be specifically related to ANCCR. For instance, the last comment has broad implications of how the ramp might be related to the overall reward rate, an interesting finding that constrains classes of dopamine models rather than evidence just for ANCCR. Perhaps adding a discussion section that allows the authors to focus more on theory would be beneficial for this manuscript.

We appreciate this suggestion by the reviewer. We have updated both our introduction and discussion sections to elaborate more thoroughly on theory.

Reviewer #3 (Recommendations For The Authors):

The paper could potentially benefit from the use of more accessible language to describe the conceptual basis of the work, and the predictions, and a bit of reformatting away from the brief structure with lots of supplemental discussion.

For example, in the introduction, the line - "Varying the ITI was critical because our theory predicts that the ITI is a variable controlling the eligibility trace time constant, such that a short ITI would produce a small time constant relative to the cue-reward interval (Supplementary Note 1)". As far as I can tell, this is meant to get across the notion that dopamine represents some aspect of the time between rewards - dopamine signals will differ for cues following short vs long intervals between rewards.

As written, the language of the paper takes a fair bit of parsing, but the notions are actually pretty simple. This is partly due to the brief format the paper is written in, where familiarity with the previous papers describing ANCCR is assumed.

From a readability standpoint, and the potential impact of the paper on a broad audience, perhaps this could be considered as a point for revision.

We thank the reviewer for pointing out the drawbacks of our technical language and brief formatting. To address this, we have removed the majority of the supplementary notes and expanded our introduction and discussion sections. In doing so, we hope that the conceptual foundations of this work, and potential alternative theoretical explanations, are accessible and impactful for a broad audience of readers.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review): 

Summary: 

Early and accurate diagnosis is critical to treating N. fowleri infections, which often lead to death within 2 weeks of exposure. Current methods-sampling cerebrospinal fluid are invasive, slow, and sometimes unreliable. Therefore, there is a need for a new diagnostic method. Russell et al. address this need by identifying small RNAs secreted by Naegleria fowleri (Figure 1) that are detectable by RT-qPCR in multiple biological fluids including blood and urine. SmallRNA-1 and smallRNA-2 were detectable in plasma samples of mice experimentally infected with 6 different N. fowleri strains, and were not detected in uninfected mouse or human samples (Figure 4). Further, smallRNA-1 is detectable in the urine of experimentally infected mice as early as 24 hours post-infection (Figure 5). The study culminates with testing human samples (obtained from the CDC) from patients with confirmed N. fowleri infections; smallRNA-1 was detectable in cerebrospinal fluid in 6 out of 6 samples (Figure 6B), and in whole blood from 2 out of 2 samples (Figure 6C). These results suggest that smallRNA-1 could be a valuable diagnostic marker for N. fowleri infection, detectable in cerebrospinal fluid, blood, or potentially urine. 

Strengths: 

This study investigates an important problem, and comes to a potential solution with a new diagnostic test for N. fowleri infection that is fast, less invasive than current methods, and seems robust to multiple N. fowleri strains. The work in mice is convincing that smallRNA1 is detectable in blood and urine early in infection. Analysis of patient blood samples suggest that whole blood (but not plasma) could be tested for smallRNA-1 to diagnose N. fowleri infections. 

Thank you for comments regarding the strengths of this study. We agree that our data for detecting the biomarker in biofluids from mice is convincing. In addition, our spike-in studies with human cerebrospinal fluid, plasma, and urine (Figure 6) suggest these biofluids from humans could be used for diagnosis.

We appreciate the comment regarding plasma and recognize this was not fully explained in the manuscript. We do believe that plasma can be used to assess the biomarker. Firstly, we demonstrated equivalent sensitivity of the method to detect smallRNA-1 in plasma and urine in mice with end-stage PAM (Figure 5). In addition, spike in samples of human plasma, cerebrospinal fluid, and urine demonstrated equivalent sensitivity of detecting the biomarker (Figure 6). 

The negative result for human plasma in Figure 6C requires clarification; this sample was convalescent plasma from a survivor. The patient presented to the hospital on August 7, 2016, was treated, made a remarkable recovery, and was released from the hospital later that month. The plasma sample in Figure 6C was collected September 7, 2016, which is a month after treatment was initiated and weeks after the patient was symptom free. Our interpretation of the convalescent plasma result is the patient had cleared the active amoeba infection and that is why we did not detect the biomarker. We have added text in the discussion and in the legend for Figure 6 to clarify the convalescent plasma result. 

One additional caveat for consideration is that many of the samples we received from amoebaeinfected humans were stored at room temperatures for undefined periods of time before being moved to <-20°C (see details in Table S9). We can’t rule out possible sample degradation, but this is an unfortunate reality of obtaining human samples from individuals later confirmed to be infected with pathogenic free-living amoebae.

Weaknesses: 

(1) There are not many N. fowleri cases, so the authors were limited in the human samples available for testing. It is difficult to know how robust this biomarker is in whole blood (only 2 samples were tested, both had detectable smallRNA-1), serum (1 out of 1 sample tested negative), or human urine (presumably there is no material available for testing). This limitation is openly discussed in the last paragraph of the discussion section. 

We agree the extremely limited availability of human samples is a limitation of this study. Given the rarity of these infections in the United States, even prospective studies to systematically collect samples would be very challenging. We hope that by publishing the details of this biomarker detection is that the method can be used by diagnostic reference centers, especially in areas where outbreaks of multiple cases per year have been reported.

(2) There seems to be some noise in the data for uninfected samples (Figures 4B-C, 5B, and 6C), especially for those with serum (2E). While this is often orders of magnitude lower than the positive results, it does raise questions about false positives, especially early in infection when diagnosis would be the most useful. A few additional uninfected human samples may be helpful. 

We agree; however, we would like to point out the progression of disease in humans and mice are similar. Typically, patients survive between 10-14 days after presumed exposure and mice have similar survival times following instillation of N. fowleri amoebae into a nare of the mouse. Therefore, detection of this biomarker as early as 72 h in mice is seemingly equivalent to the onset of initial symptoms in humans.  

Reviewer #2 (Public review): 

Summary: 

The authors sought to develop a rapid and non-invasive diagnostic method for primary amoebic meningoencephalitis (PAM), a highly fatal disease caused by Naegleria fowleri. Due to the challenges of early diagnosis, they investigated extracellular vesicles (EVs) from N. fowleri, identifying small RNA biomarkers. They developed an RT-qPCR assay to detect these biomarkers in various biofluids. 

Strengths: 

(1)  This study has a clear methodological approach, which allows for the reproducibility of the experiments. 

(2) Early and Non-Invasive Diagnosis - The identification of a small RNA biomarker that can be detected in urine, plasma, and cerebrospinal fluid (CSF) provides a non-invasive diagnostic approach, which is crucial for improving early detection of PAM. 

(3) High Sensitivity and Rapid Detection - The RT-qPCR assay developed in the study is highly sensitive, detecting the biomarker in 100% of CSF samples from human PAM cases and in mouse urine as early as 24 hours post-infection. Additionally, the test can be completed in ~3 hours, making it feasible for clinical use. 

(4)  Potential for Disease Monitoring - Since the biomarker is detectable throughout the course of infection, it could be used not only for early diagnosis but also for tracking disease progression and monitoring treatment efficacy. 

(5)  Strong Experimental Validation - The study demonstrates biomarker detection across multiple sample types (CSF, urine, whole blood, plasma) in both animal models and human cases, providing robust evidence for its clinical relevance. 

(6) Addresses a Critical Unmet Need - With a >97% case fatality rate, PAM urgently requires improved diagnostics. This study provides one of the first viable liquid biopsy-based diagnostic approaches, potentially transforming how PAM is detected and managed. 

Thank you for summarizing the strengths of the study.

Weaknesses: 

(1) Limited Human Sample Size - While the biomarker was detected in 100% of CSF samples from human PAM cases, the number of human samples analyzed (n=6 for CSF) is relatively small. A larger cohort is needed to validate its diagnostic reliability across diverse populations. 

As noted in response to Reviewer #1 above, we agree this is a limitation of the study; however, we were fortunate to obtain even 15 µL samples of cerebrospinal fluid, plasma, serum, or whole blood from as many patients as we did. There is an urgent need for more systematic collection and storage of samples for rare diseases like primary amoebic meningoencephalitis so that advancements in diagnostics and biomarker discovery can be conducted. It is our sincere hope that by publishing our detailed methods and experimental results in this manuscript, that additional hospitals and research centers can replicate our studies and help advance this or other techniques for early diagnosis of PAM.

(2) Lack of Pre-Symptomatic or Early-Stage Human Data - Although the biomarker was detected in mouse urine as early as 24 hours post-infection, there is no data on whether it can be reliably detected before symptoms appear in humans, which is crucial for early diagnosis and treatment initiation. 

It is difficult to envision a method to obtain these biofluids from infected humans prior to onset of symptoms. More likely the best we can hope for is that physicians include primary amoebic meningoencephalitis in their assessment of patients that present with prodromal symptoms of meningitis.

(3)  Plasma Detection Challenges - While the biomarker was detected in whole blood, it was not detected in human plasma, which could limit the ease of clinical implementation since plasma-based diagnostics are more common. Further investigation is needed to understand why it is absent in plasma and whether alternative blood-based approaches (e.g., whole blood assays) could be optimized. 

See response to Reviewer #1 above.

Reviewer #1 (Recommendations for the authors): 

(1) What is the evidence that these small RNAs are secreted specifically in EVs? I believe that they are, and ultimately it doesn't impact the conclusions, but I think the evidence here could be either stronger or presented in a more obvious way. 

Our data demonstrates that smallRNA-1 is present in N. fowleri-derived EVs (Figures 2 and Supplemental Figure 7) and in the intact amoebae (Figure 3B).  Initial sequencing data to identify these smallRNA biomarkers came from PEG-precipitated EVs (Figure S1), by using methods we previously published (22). The PEG-precipitated EVs were extracted specifically for spike in studies. Finally, the smallRNAs in EVs were confirmed after extraction of EVs from 7 N. fowleri strains (Figure 2). We do not have evidence that they are secreted outside of EVs.

(2) The figure legends would be more useful with some additional information. For example: why are there two points for Nf69 in Fig 2B? In Figure 3A-B, please add more detail as to what the graphs are showing (are they histograms binned by a number of amoebae? This does not seem obvious to me). 

We agree the Figure legends should be edited for clarity and to add additional information. Both Figure legends have been updated.

In Figure 2B, each point represents the mean of three technical replicates of EV preps for each N. fowleri strain.

In Figure 3 the points indicate the Copy#/µL of a well from a 96-well plate. The histograms show the mean of these observations for each condition. 

(3)  In Figure 2E, the FBS seems like it has near detectable levels of smallRNA-1 compared to Ac and Bm (albeit N. fowleri has 4 orders of magnitude higher levels than the FBS). Because cows are likely exposed to N. fowleri and have documented infections (e.g. doi: 10.1016/j.rvsc.2012.01.002), is it possible this signal is real? 

Thank you for making this interesting observation. We agree that cows are likely to have significant exposure to N. fowleri, yet documented infections are rare. In this case we do not believe the near detectable levels of smallRNA-1 in FBS was due to an infected donor animal. This noise was likely due to extracting RNA from concentrated FBS rather than FBS diluted in cell culture media. In addition, as shown in Supplemental Figure 4, the qPCR product from EVs extracted from FBS were not the same as that from the N. fowleri-derived EVs. Please note we used a PEG extraction reagent that separates lipid particles, so this is additional evidence the smallRNAs are present in EVs.

(4)  In Figure 6A, why was the sample size greater for water and unspiked urine? Similarly, why is the number of infected mice so variable in Figure 4B? 

In Figure 6A we assayed de-identified biofluids provided by Advent Hospital in Orlando, Florida. The plasma and serum samples were pooled from multiple individuals; whereas, individual urine samples (n=8) were provided for this experiment. We have updated the legend for Figure 6A to include these details.

For Figure 4B we used plasma collected at the end-stage of disease following infections with five different strains of N. fowleri. The sample sizes varied for two reasons. First, Nf69 was the strain used most by our lab and we had plasma from several in vivo experiments. The lower sample sizes for the other strains came from an experiment with 8 mice per group. Some of these strains were less virulent and did not succumb to disease with the number of amoebae inoculated in this experiment. Thus, plasma was only collected from animals that were euthanized due to severe N.

fowleri infections. In follow up studies (e.g., Figure 5B), plasma was collected every 24 hr for analysis.

Very minor points: 

(1)  The number of acronyms (FLA, PAM, EVs, CNS, CSF, LOD) could be reduced to make this paper more reader-friendly. 

Acronyms that were used infrequently in the manuscript (FLA, CNS, LOD, mNGS, UC) have been edited to spell out the complete names. We kept the acronyms EVs and CSF because they are each used more than twenty times in the manuscript.

(2)  The decimal point in the Cq values is formatted strangely. 

The decimal points have been edited to normal format in both the manuscript and supplementary material.

(3)  Figure 3C is not intuitive. I do not understand the logic for the placement of the different samples (was row A only amoebae, B only Veros, C blank, D a mix, and F more Veros?). 

Thank you for this comment; we agree the microtiter plate schematic (Fig 3C) was misleading. We have revised Figure 3C to make the point that we tested amoebae alone, Vero cells alone, and we combined supernatants from Vero cells (alone) plus amoebae (alone) to confirm that 1) smallRNA-1 was only detected in amoeba-conditioned media, and 2) that Vero-conditioned media does not affect detection of smallRNA-1.

Reviewer #2 (Recommendations for the authors): 

Minor corrections: 

The abbreviation 'Nf' for Naegleria fowleri is not appropriate in a scientific publication. According to taxonomic conventions, the correct way to abbreviate a scientific name is as follows: 

The first mention should be written in full: Naegleria fowleri. 

In subsequent mentions, the genus name should be abbreviated to its initial in uppercase, followed by a period, while the species name remains in lowercase: N. fowleri. 

The same rule applies to Balamuthia mandrillaris and Acanthamoeba species, which should be abbreviated as B. mandrillaris and Acanthamoeba spp. after their first mention. 

We agree and each of the scientific names have been updated to the proper format. Please note Nf69 is the accepted nomenclature for this N. fowleri strain, so no changes were made when referring to this specific strain.

Temperatures should be expressed in international units (°C). Please update the temperatures reported in Fahrenheit (°F) in the 'Materials and Methods' section, specifically in the 'Animal Studies' subsection. 

These changes were made in the revised manuscript.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary

This paper summarises responses from a survey completed by around 5,000 academics on their manuscript submission behaviours. The authors find several interesting stylised facts, including (but not limited to):

- Women are less likely to submit their papers to highly influential journals (*e.g.*, Nature, Science and PNAS).

- Women are more likely to cite the demands of co-authors as a reason why they didn't submit to highly influential journals.

- Women are also more likely to say that they were advised not to submit to highly influential journals.

Recommendation

This paper highlights an important point, namely that the submissions' behaviours of men and women scientists may not be the same (either due to preferences that vary by gender, selection effects that arise earlier in scientists' careers or social factors that affect men and women differently and also influence submission patterns). As a result, simply observing gender differences in acceptance rates---or a lack thereof---should not be automatically interpreted as as evidence of for or against discrimination (broadly defined) in the peer review process. I do, however, make a few suggestions below that the authors may (or may not) wish to address.

We thank the author for this comment and for the following suggestions, which we take into account in our revision of the manuscript.

Major comments

What do you mean by bias?

In the second paragraph of the introduction, it is claimed that "if no biases were present in the case of peer review, then 'we should expect the rate with which members of less powerful social groups enjoy successful peer review outcomes to be proportionate to their representation in submission rates." There are a couple of issues with this statement.

- First, the authors are implicitly making a normative assumption that manuscript submission and acceptance rates *should* be equalised across groups. This may very well be the case, but there can also be important reasons why not -- e.g., if men are more likely to submit their less ground-breaking work, then one might reasonably expect that they experience higher rejection rates compared to women, conditional on submission.

We do assume that normative statement: unless we believe that men’s papers are intrinsically better than women’s papers, the acceptance rate should be the same. But the referee is right: we have no way of controlling for the intrinsic quality of the work of men and women. That said, our manuscript does not show that there is a different acceptance rate for men and women; it shows that women are less likely to submit papers to a subset of journals that are of a lower Journal Impact Factor, controlling for their most cited paper, in an attempt to control for intrinsic quality of the manuscripts.

- Second, I assume by "bias", the authors are taking a broad definition, i.e., they are not only including factors that specifically relate to gender but also factors that are themselves independent of gender but nevertheless disproportionately are associated with one gender or another (e.g., perhaps women are more likely to write on certain topics and those topics are rated more poorly by (more prevalent) male referees; alternatively, referees may be more likely to accept articles by authors they've met before, most referees are men and men are more likely to have met a given author if he's male instead of female). If that is the case, I would define more clearly what you mean by bias. (And if that isn't the case, then I would encourage the authors to consider a broader definition of "bias"!)

Yes, the referee is right that we are taking a broad definition of bias. We provide a definition of bias on page 3, line 92. This definition is focused on differential evaluation which leads to differential outcomes. We also hedge our conversation (e.g., page 3, line 104) to acknowledge that observations of disparities may only be an indicator of potential bias, as many other things could explain the disparity. In short, disparities are a necessary but insufficient indicator of bias. We add a line in the introduction to reinforce this. The only other reference to the term bias comes on page 10, line 276. We add a reference to Lee here to contextualize.

Identifying policy interventions is not a major contribution of this paper

In my opinion, the survey evidence reported here isn't really strong enough to support definitive policy interventions to address the issue and, indeed, providing policy advice is not a major -- or even minor -- contribution of your paper, so I would not mention policy interventions in the abstract. (Basically, I would hope that someone interested in policy interventions would consult another paper that much more thoughtfully and comprehensively discusses the costs and benefits of various interventions!)

We thank the referee for this comment. While we agree that our results do not lead to definitive policy interventions, we believe that our findings point to a phenomenon that should be addressed through policy interventions. Given that some interventions are proposed in our conclusion, we feel like stating this in the abstract is coherent.

Minor comments

- What is the rationale for conditioning on academic rank and does this have explanatory power on its own---i.e., does it at least superficially potentially explain part of the gender gap in intention to submit?

The referee is right: academic rank was added to control for career age of researchers, with the assumption that this variable would influence submission behavior. However, the rank information we collected was for the time that the individual respondent took the survey, which could be different from the rank they held concerning their submission behaviors mentioned in the survey. That is why we didn't consider rank as an independent variable of interest. But I do also agree with the reviewer that it could be related to their submission behaviors in some cases. Our initial analysis shows that academic rank is not a significant predictor of whether researchers submitted to SNP, but does contribute significantly to the SNP acceptance rates and desk rejection rates of individuals in Medical Sciences.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Basson et al. study the representation of women in "high-impact" journals through the lens of gendered submission behavior. This work is clear and thorough, and it provides new insights into gender disparities in submissions, such as that women were more likely to avoid submitting to one of these journals based on advice from a colleague/mentor. The results have broad implications for all academic communities and may help toward reducing gender disparities in "high-impact" journal submissions. I enjoyed reading this article, and I have several recommendations regarding the methodology/reporting details that could help to enhance this work.

We thank the referee for their comments.

Strengths:

This is an important area of investigation that is often overlooked in the study of gender bias in publishing. Several strengths of the paper include:

(1) A comprehensive survey of thousands of academics. It is admirable that the authors retroactively reached out to other researchers and collected an extensive amount of data.

(2) Overall, the modeling procedures appear thorough, and many different questions are modeled.

(3) There are interesting new results, as well as a thoughtful discussion. This work will likely spark further investigation into gender bias in submission behavior, particularly regarding the possible gendered effect of mentorship on article submission.

Thank you for those comments.

Weaknesses:

(1) The GitHub page should be further clarified. A detailed description of how to run the analysis and the location of the data would be helpful. For example, although the paper says that "Aggregated and de-identified data by gender, discipline, and rank for analyses are available on GitHub," I was unable to find such data.

We added the link to the Github page, as well as more details on the how to run the statistical analysis. Unfortunately, our IRB approval does not allow for the sharing of the raw data.

(2) Why is desk rejection rate defined as "the number of manuscripts that did not go out for peer review divided by the number of manuscripts rejected for each survey respondent"? For example, in your Grossman 2020 reference, it appears that manuscripts are categorized as "reviewed" or "desk-rejected" (Grossman Figure 2). If there are gender differences in the denominator, then this could affect the results.

We thank the referee for pointing this out. Actually, what the referee is proposing is how we calculated it in the manuscript; the calculation mentioned in the manuscript was a mistake. We corrected the manuscript.

(3) Have you considered correcting for multiple comparisons? Alternatively, you could consider reporting P-values and effect sizes in the main text. Otherwise, sometimes the conclusions can be misleading. For example, in Figure 3 (and Table S28), the effect is described as significant in Social Sciences (p=0.04) but not in Medical Sciences (p=0.07).

We highly appreciate the suggestion. We’ve added Odds Ratio values and p-values to the main manuscript.

(4) More detail about the models could be included. It may be helpful to include this in each table caption so that it is clear what all the terms of the model were. For instance, I was wondering if journal or discipline are included in the models.

We appreciate the suggestion. We’ve added model details to the figure and table captions in the manuscript and the supplemental materials.

Reviewer #3 (Public Review):

Summary:

This is a strong manuscript by Basson and colleagues which contributes to our understanding of gender disparities in scientific publishing. The authors examine attitudes and behaviors related to manuscript submission in influential journals (specifically, Science, Nature and PNAS). The authors rightly note that much attention has been paid to gender disparities in work that is already published, but this fails to capture the unseen hurdles that occur prior to publication (which include decisions about where to publish, desk rejections, revisions and resubmissions, etc.). They conducted a survey study to address some of these components and their results are interesting:

They find that women are less likely to submit their manuscript to Science, Nature or PNAS. While both men and women feel their work would be better suited for more specialized journals, women were more likely to think their work was 'less novel or groundbreaking.'

A smaller proportion of respondents indicated that they were actively discouraged from submitting their manuscripts to these journals. In this instance, women were more likely to receive this advice than men.

Lastly, the authors also looked at self-reported acceptance and rejection rates and found that there were no gender differences in acceptance or rejection rates.

These data are helpful in developing strategies to mitigate gender disparities in influential journals.

We thank the referee for their comments

Comments:

The methods the authors used are appropriate for this study. The low response rate is common for this type of recruitment strategy. The authors provide a thoughtful interpretation of their data in the Discussion.

We thank the referee for their comments

Reviewer #4 (Public Review):

This manuscript covers an important topic of gender biases in the authorship of scientific publications. Specifically, it investigates potential mechanisms behind these biases, using a solid approach, based on a survey of researchers.

Main strengths

The topic of the MS is very relevant given that across sciences/academia representation of genders is uneven, and identified as concerning. To change this, we need to have evidence on what mechanisms cause this pattern. Given that promotion and merit in academia are still largely based on the number of publications and impact factor, one part of the gap likely originates from differences in publication rates of women compared to men.

Women are underrepresented compared to men in journals with high impact factor. While previous work has detected this gap, as well as some potential mechanisms, the current MS provides strong evidence, based on a survey of close to 5000 authors, that this gap might be due to lower submission rates of women compared to men, rather than the rejection rates. The data analysis is appropriate to address the main research aims. The results interestingly show that there is no gender bias in rejection rates (desk rejection or overall) in three high-impact journals (Science, Nature, PNAS). However, submission rates are lower for women compared to men, indicating that gender biases might act through this pathway. The survey also showed that women are more likely to rate their work as not groundbreaking, and be advised not to submit to prestigious journals

With these results, the MS has the potential to inform actions to reduce gender bias in publishing, and actions to include other forms of measuring scientific impact and merit.

We thank the referee for their comments.

Main weakness and suggestions for improvement

(1) The main message/further actions: I feel that the MS fails to sufficiently emphasise the need for a different evaluation system for researchers (and their research). While we might act to support women to submit more to high-impact journals, we could also (and several initiatives do this) consider a broader spectrum of merits (e.g. see https://coara.eu/ ). Thus, I suggest more space to discuss this route in the Discussion. Also, I would suggest changing the terms that imply that prestigious journals have a better quality of research or the highest scientific impact (line 40: journals of the highest scientific impact) with terms that actually state what we definitely know (i.e. that they have the highest impact factor). And think this could broaden the impact of the MS

We agree with the referee. We changed the wording on impact, and added a few lines were added on this in the discussion.

(2) Methods: while methods are all sound, in places it is difficult to understand what has been done or measured. For example, only quite late (as far as I can find, it's in the supplement) we learn the type of authorship considered in the MS is the corresponding authorship. This information should be clear from the very start (including the Abstract).

We performed the suggested edits.

Second, I am unclear about the question on the perceived quality of research work. Was this quality defined for researchers, as quality can mean different things (e.g. how robust their set-up was, how important their research question was)? If researchers have different definitions of what quality means, this can cause additional heterogeneity in responses. Given that the survey cannot be repeated now, maybe this can be discussed as a limitation.

We agree that this can mean something different for researchers—probably varies by discipline, but also by gender. But that was precisely the point: whether men/women considered their “best work” to be published in higher impact venue. While there may be heterogeneity in those perceptions, the fact that 1) men and women rate their research at the same level and 2) we control for disciplinary differences should mitigate some of that.

I was surprised to see that discipline was considered as a moderator for some of the analyses but not for the main analysis on the acceptance and rejection rates.

We appreciate the attention to detail. In our analysis of acceptance and rejection rates, we conducted separate regression analyses for each discipline to capture any field-specific patterns that might otherwise be obscured.

We added more details on this to clarify.

I was also suppressed not to see publication charges as one of the reasons asked for not submitting to selected journals. Low and middle-income countries often have more women in science but are also less likely to support high publication charges.

That is a good point. However, both Science and Nature have subscription options, which do not require any APCs.

Finally, academic rank was asked of respondents but was not taken as a moderator.

Academic rank is included in the regression as a control variable (Figure 1).

Reviewer #2 (Recommendations For The Authors):

In addition to the points in the "Weaknesses" section of the my Public Review above, I have several suggestions to improve this work.

(1) Can you please indicate what the error bars mean in each plot? I am assuming that they are 95% confidence intervals.

We appreciate the attention to detail. Yes, they are 95% confidence intervals. We’ve clarified this in the captions of the corresponding figures. 

(2) Can you provide a more detailed explanation for why the 7 journals were separated? I see that on page 3 of the supporting information you write that "Due to limited responses, analysis per journal was not always viable. The results pertaining to the journals were aggregated, with new categories based on the shared similarities in disciplinary foci of the journals and their prestige." Specifically, why did you divide the data into (somewhat arbitrary) categories as opposed to using all the data and including a journal term in your model?

The survey covered 7 journals:

• Science, Nature, and PNAS (S.N.P.)

• Nature Communications and Science Advances (NC.SA.)

• NEJM and Cell (NEJM.C.)

We believe that the first three are a class of their own: they cover all fields (while NEJM and Cell are limited to (bio)medical sciences), and have a much higher symbolic capital than both Nature Comms and Science Advances (which are receiving cascading papers from Nature and Science, respectively). We believe that factors leading to submission to S.N.P. are much different than those leading to submission to the other groups of journals, which is why we separated the analysis in that manner.

(3) You included random effects for linear regression but not for logistic regression. Please justify this choice or include additional logistic regression models with random effects.

We used mixed-effect models for linear regressions (where number of submissions, acceptance rate, or rejection rate is the dependent variable). As mentioned in the previous comment, we tested using rank as the control variable and found it had a potential impact on the variables we analyzed using linear regressions in some disciplines. Therefore, we introduced it as a random effect for all the linear regression models.

Reviewer #3 (Recommendations For The Authors):

The limitations of this work are currently described in the Supplement. It may be helpful to bring several of these items into the Discussion so that they can be addressed more prominently.

Added content

Reviewer #4 (Recommendations For The Authors):

(1) Line 40: add 'as leading authors of papers published in' before ' 'journals'

Done

(2) Explain what the direction in the ' relationship between' line 62 is

Added

(3) Lines 101-102 - this is a bit unclear. Please, provide some more info, also including what did these studies find.

Added

(4) Is 'sociodemographic' the best term in line 120

Yes, we believe so.

(5) Results would benefit from a short intro with the info on the number of respondents, also by gender.

Those are present at the end of the intro (and in the methods, at the end). We nonetheless added gender.

(6) Line 134 add how many woman and man did submit to Science, Nature, and PNAS

Added. In all disciplines combined, 552 women and 1,583 men ever submitted to these three elite journals. More details can be found in SI Table 9

(7) Add 'Self-' before reported, line 141

Added

(8) Add sample sizes to Figs 1 and 2

Those are in the appendix

(9) Line 168 - unclear if this is ever or as their first choice

We do not discriminate – it is whether the considered it at all.

(10) Add sample size in line 177

Added. 480 women and 1404 men across all disciplines reported desk rejections by S.N.P. journals.

(11) I would like to see some discussion on the fact that the highest citation paper will also be a paper that the authors have submitted earlier in their careers given that citations will pile up over time.

Those are actually quite evenly distributed. We modified the supplementary materials.

(12) Data availability - be clear that supporting info contains only summary data. Also, while the Data availability statement refers to de-identified data on Github, the Github page only contains the code, and the note that 'The STAT code used for our analyses is shared.

We are unable to share the survey response details publicly per IRB protocols.' Why were de-identified data shared? This is extremely important to allow for the reproducibility of MS results. I would also suggest sharing data in a trusted repository (e.g. Dryad, ZENODO...) rather than on Github, as per current recommendations on the best practices for data sharing.

Thank you for your careful reading and for highlighting the importance of clear data availability. We will revise our Data Availability Statement to explicitly state that the supporting information contains only summary data and that the complete analysis code is available on GitHub.

We understand the importance of sharing de-identified data for reproducibility. However, our IRB strictly prohibits the sharing of any individual-level data, including de-identified files, to protect participant confidentiality. Consequently, the summary data included in the supporting information, together with the provided code, is intended to facilitate the verification of our core findings. Our previous statement regarding “de-identified” data sharing was inaccurate and thus has been removed. We apologize for the confusion.

In light of your suggestion, we are also exploring depositing the summary data and code in a trusted repository (e.g., Dryad or Zenodo) to further align with current best practices for data sharing.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Functional lateralization between the right and left hemispheres is reported widely in animal taxa, including humans. However, it remains largely speculative as to whether the lateralized brains have a cognitive gain or a sort of fitness advantage. In the present study, by making use of the advantages of domestic chicks as a model, the authors are successful in revealing that the lateralized brain is advantageous in the number sense, in which numerosity is associated with spatial arrangements of items. Behavioral evidence is strong enough to support their arguments. Brain lateralization was manipulated by light exposure during the terminal phase of incubation, and the left-to-right numerical representation appeared when the distance between items gave a reliable spatial cue. The light-exposure induced lateralization, though quite unique in avian species, together with the lack of intense inter-hemispheric direct connections (such as the corpus callosum in the mammalian cerebrum), was critical for the successful analysis in this study. Specification of the responsible neural substrates in the presumed right hemisphere is expected in future research. Comparable experimental manipulation in the mammalian brain must be developed to address this general question (functional significance of brain laterality) is also expected.

We sincerely appreciate the Reviewer's insightful feedback and his/her recognition of the key contributions of our study.

Reviewer #2 (Public review):

Summary:

This is the first study to show how a L-R bias in the relationship between numerical magnitude and space depends on brain lateralisation, and moreover, how is modulated by in ovo conditions.

Strengths:

Novel methodology for investigating the innateness and neural basis of an L-R bias in the relationship between number and space.

We would like to thank the Reviewer for their valuable feedback and for highlighting the key contributions of our study.

Weaknesses:

I would query the way the experiment was contextualised. They ask whether culture or innate pre-wiring determines the 'left-to-right orientation of the MNL [mental number line]'.

We thank the Reviewer for raising this point, which has allowed us to provide a more detailed explanation of this aspect. Rather than framing the left-to-right orientation of the mental number line (MNL) as exclusively determined by either cultural influences or innate pre-wiring, our study highlights the role of environmental stimulation. Specifically, prenatal light exposure can shape hemispheric specialization, which in turn contributes to spatial biases in numerical processing. Please see lines 115-118.

The term, 'Mental Number Line' is an inference from experimental tasks. One of the first experimental demonstrations of a preference or bias for small numbers in the left of space and larger numbers in the right of space, was more carefully described as the spatial-numerical association of response codes - the SNARC effect (Dehaene, S., Bossini, S., & Giraux, P. (1993). The mental representation of parity and numerical magnitude. Journal of Experimental Psychology: General, 122, 371-396).

We have refined our description of the MNL and SNARC effect to ensure conceptual accuracy in the revised manuscript; please see lines 53-59.

This has meant that the background to the study is confusing. First, the authors note, correctly, that many other creatures, including insects, can show this bias, though in none of these has neural lateralisation been shown to be a cause. Second, their clever experiment shows that an experimental manipulation creates the bias. If it were innate and common to other species, the experimental manipulation shouldn't matter. There would always be an L-R bias. Third, they seem to be asserting that humans have a left-to-right (L-R) MNL. This is highly contentious, and in some studies, reading direction affects it, as the original study by Dehaene et al showed; and in others, task affects direction (e.g. Bachtold, D., Baumüller, M., & Brugger, P. (1998). Stimulus-response compatibility in representational space. Neuropsychologia, 36, 731-735, not cited). Moreover, a very careful study of adult humans, found no L-R bias (Karolis, V., Iuculano, T., & Butterworth, B. (2011), not cited, Mapping numerical magnitudes along the right lines: Differentiating between scale and bias. Journal of Experimental Psychology: General, 140(4), 693-706). Indeed, Rugani et al claim, incorrectly, that the L-R bias was first reported by Galton in 1880. There are two errors here: first, Galton was reporting what he called 'visualised numerals', which are typically referred to now as 'number forms' - spontaneous and habitual conscious visual representations - not an inference from a number line task. Second, Galton reported right-to-left, circular, and vertical visualised numerals, and no simple left-to-right examples (Galton, F. (1880). Visualised numerals. Nature, 21, 252-256.). So in fact did Bertillon, J. (1880). De la vision des nombres. La Nature, 378, 196-198, and more recently Seron, X., Pesenti, M., Noël, M.-P., Deloche, G., & Cornet, J.-A. (1992). Images of numbers, or "When 98 is upper left and 6 sky blue". Cognition, 44, 159-196, and Tang, J., Ward, J., & Butterworth, B. (2008). Number forms in the brain. Journal of Cognitive Neuroscience, 20(9), 1547-1556.

We sincerely appreciate the opportunity to discuss numerical spatialization in greater detail. We have clarified that an innate predisposition to spatialize numerosity does not necessarily exclude the influence of environmental stimulation and experience. We have proposed an integrative perspective, incorporating both cultural and innate factors, suggesting that numerical spatialization originates from neural foundations while remaining flexible and modifiable by experience and contextual influences. Please see lines 69–75.

We have incorporated the Reviewer’s suggestions and cited all the recommended papers; please see lines 47–75.

If the authors are committed to chicks' MN Line they should test a series of numbers showing that the bias to the left is greater for 2 and 3 than for 4, etc.

What does all this mean? I think that the paper should be shorn of its misleading contextualisation, including the term 'Mental Number Line'. The authors also speculate, usefully, on why chicks and other species might have a L-R bias. I don't think the speculations are convincing, but at least if there is an evolutionary basis for the bias, it should at least be discussed.

In the revised version of the manuscript, we have resorted to adopt the Spatial Numerical Association (SNA). We thank the Reviewer for this valuable comment.

We appreciated the Reviewer’s suggestion regarding the evolutionary basis of lateralization and have included considerations of its relevance in chicks and other species; please see lines 143-151 and 381-386.

This paper is very interesting with its focus on why the L-R bias exists, and where and why it does not.

We wish to thank the Reviewer again for his/her work.

Reviewer #1(Public review)

(1) Introduction needs to be edited to make it much more concise and shorter. Hypotheses (from line 67 to 81) and predictions (from line 107 to 124) must be thoroughly rephrased, because (a) general readers are not familiar with the hypotheses (emotional valence and BAFT), (b) the hypotheses may or may not be mutually exclusive, and therefore (c) the logical linkage between the hypotheses and the predicted results are not necessarily clear. Most general readers may be embarrassed by the apparently complicated logical constructs of this study. Instead, it is recommended that focal spotlight should be given to the issue of functional contributions of brain lateralization to the cognitive development of number sense.

We thank the Reviewer for these comments, which allowed us to improve the clarity of our hypotheses and predictions. We thoroughly rephrased them to ensure they are accessible to general readers and specified that the models may or may not be mutually exclusive. Additionally, we highlighted the functional contributions of brain lateralization to the cognitive development of number sense, addressing the suggested focal point. While we have shortened the introduction, we opted to retain essential background information to ensure readers are well-informed about the relevant scientific literature. Please review the entire introduction, particularly lines 84–118 and 218.

(2) In relation to the above (a), abbreviations need to be reexamined. MNL (mental number line) appears early on lines 27 and 49, whereas the possibly related conceptual term SNA appeared first on line 213, without specification to "spatial numerical association".

We thank the Reviewer for bringing this to our attention. We have addressed the suggestions, and the term SNA has been used specifically to refer to numerical spatialization in non-human animals. Please see lines 27-30.

(3) By the way, what difference is there between MNL and SNA? Please specify the difference if it is important. If not important, is it possible that one of these two is consistently used in this report, at least in the Introduction?

We clarified the distinction between MNL and SNA and have consistently used SNA in this report; please see lines 47-75.

(4) In relation to the above (a and b), clarification of the hypotheses and their abbreviations in the form of a table or a graphical representation will strongly reinforce the general readers' understanding. It is also possible that some of these hypotheses are discussed later in the Discussion, rather than in Introduction.

We appreciated this suggestion and have now clarified the hypotheses, also providing a table/graphical representation, aiming to enhance accessibility for general readers; please see lines 110-118, and 218.

(5) Figures 1 and 2 are transparent and easily understandable; however, the statistical details in the Results may bother the readers as the main points are doubly represented in Figures 1, 2, and Table 1. These (statistics and Table 1) may go to the supplementary file, if the editor agrees.

We would prefer to keep Table 1 and the statistical details as part of the main article to provide readers with a comprehensive overview of the experimental results. However, if the editors also suggest to move them to the supplementary file, we are open to making this adjustment.

(6) In Figure 1D and E, and text lines 139-140. Figure 1D shows that the chick is looking monocularly by the right eye, but the text (line 139) says "left eye in use. Is it correct?

We thank the reviewer for pointing out this incongruity. We have corrected the text to align with Figure 1D and E; please see lines 180-181.

(7) Methods. The behavioral experiment was initiated on Wednesday (8 a.m.; line 479), but at what age? At what post-hatch day was the experiment terminated? A simple graphical illustration of the schedule will be quite helpful.

We have added the requested details, specifying that experiments began on the third post-hatch day and ended on the fifth day; please see lines 533-539.

Additionally, we have included a graphical illustration of the schedule to enhance clarity; please see line 666.  

(8) Methods. How many chicks were excluded from the study in the course of Pre-training (line 525) and Training (line 535-536)? Was the exclusion rate high, or just negligible?

We appreciate the reviewer's suggestion. We have now included the number of subjects excluded during the training phase; please see lines 593-597.

We wish to thank the Reviewer again for his/her work.

Author response:

The following is the authors’ response to the original reviews

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

This work integrates two timepoints from the Adolescent Brain Cognitive Development (ABCD) Study to understand how neuroimaging, genetic, and environmental data contribute to the predictive power of mental health variables in predicting cognition in a large early adolescent sample. Their multimodal and multivariate prediction framework involves a novel opportunistic stacking model to handle complex types of information to predict variables that are important in understanding mental health-cognitive performance associations. 

Strengths: 

The authors are commended for incorporating and directly comparing the contribution of multiple imaging modalities (task fMRI, resting state fMRI, diffusion MRI, structural MRI), neurodevelopmental markers, environmental factors, and polygenic risk scores in a novel multivariate framework (via opportunistic stacking), as well as interpreting mental health-cognition associations with latent factors derived from partial least squares. The authors also use a large well-characterized and diverse cohort of adolescents from the ABCD Study. The paper is also strengthened by commonality analyses to understand the shared and unique contribution of different categories of factors (e.g., neuroimaging vs mental health vs polygenic scores vs sociodemographic and adverse developmental events) in explaining variance in cognitive performance 

Weaknesses: 

The paper is framed with an over-reliance on the RDoC framework in the introduction, despite deviations from the RDoC framework in the methods. The field is also learning more about RDoC's limitations when mapping cognitive performance to biology. The authors also focus on a single general factor of cognition as the core outcome of interest as opposed to different domains of cognition. The authors could consider predicting mental health rather than cognition. Using mental health as a predictor could be limited by the included 9-11 year age range at baseline (where many mental health concerns are likely to be low or not well captured), as well as the nature of how the data was collected, i.e., either by self-report or from parent/caregiver report. 

Thank you so much for your encouragement.

We appreciate your comments on the strengths of our manuscript.

Regarding the weaknesses, the reliance on the RDoC framework is by design. Even with its limitations, following RDoC allows us to investigate mental health holistically. In our case, RDoC enabled us to focus on a) a functional domain (i.e., cognitive ability), b) the biological units of analysis of this functional domain (i.e., neuroimaging and polygenic scores), c) potential contribution of environments, and d) the continuous individual deviation in this domain (as opposed to distinct categories). We are unaware of any framework with all these four features.

Focusing on modelling biological units of analysis of a functional domain, as opposed to mental health per se, has some empirical support from the literature. For instance, in Marek and colleagues’ (2022) study, as mentioned by a previous reviewer, fMRI is shown to have a more robust prediction for cognitive ability than mental health. Accordingly, our reasons for predicting cognitive ability instead of mental health in this study are motivated theoretically (i.e., through RDoC) and empirically (i.e., through fMRI findings). We have clarified this reason in the introduction of the manuscript.

We are aware of the debates surrounding the actual structure of functional domains where the originally proposed RDoC’s specific constructs might not fit the data as well as the data-driven approach (Beam et al., 2021; Quah et al., 2025). However, we consider this debate as an attempt to improve the characterisation of functional domains of RDoC, not an effort to invalidate its holistic, neurobiological and basicfunctioning approach. Our use of a latent-variable modelling approach through factor analyses moves towards a data-driven direction. We made the changes to the second-to-last paragraph in the introduction to make this point clear:

“In this study, inspired by RDoC, we a) focused on cognitive abilities as a functional domain, b) created predictive models to capture the continuous individual variation (as opposed to distinct categories) in cognitive abilities, c) computed two neurobiological units of analysis of cognitive abilities: multimodal neuroimaging and PGS, and d) investigated the potential contributions of environmental factors. To operationalise cognitive abilities, we estimated a latent variable representing behavioural performance across various cognitive tasks, commonly referred to as general cognitive ability or the gfactor (Deary, 2012). The g-factor was computed from various cognitive tasks pertinent to RDoC constructs, including attention, working memory, declarative memory, language, and cognitive control. However, using the g-factor to operationalise cognitive abilities caused this study to diverge from the original conceptualisation of RDoC, which emphasises studying separate constructs within cognitive abilities (Morris et al., 2022; Morris & Cuthbert, 2012). Recent studies suggest an improvement to the structure of functional domains by including a general factor, such as the g-factor, in the model, rather than treating each construct separately (Beam et al., 2021; Quah et al., 2025). The g-factor in children is also longitudinally stable and can forecast future health outcomes (Calvin et al., 2017; Deary et al., 2013). Notably, our previous research found that neuroimaging predicts the g-factor more accurately than predicting performance from separate individual cognitive tasks (Pat et al., 2023). Accordingly, we decided to conduct predictive models on the g-factor while keeping the RDoC’s holistic, neurobiological, and basic-functioning characteristics.”

Reviewer #2 (Public review):

Summary: 

This paper by Wang et al. uses rich brain, behaviour, and genetics data from the ABCD cohort to ask how well cognitive abilities can be predicted from mental-health-related measures, and how brain and genetics influence that prediction. They obtain an out-ofsample correlation of 0.4, with neuroimaging (in particular task fMRI) proving the key mediator. Polygenic scores contributed less. 

Strengths: 

This paper is characterized by the intelligent use of a superb sample (ABCD) alongside strong statistical learning methods and a clear set of questions. The outcome - the moderate level of prediction between the brain, cognition, genetics, and mental health - is interesting. Particularly important is the dissection of which features best mediate that prediction and how developmental and lifestyle factors play a role. 

Thank you so much for the encouragement. 

Weaknesses: 

There are relatively few weaknesses to this paper. It has already undergone review at a different journal, and the authors clearly took the original set of comments into account in revising their paper. Overall, while the ABCD sample is superb for the questions asked, it would have been highly informative to extend the analyses to datasets containing more participants with neurological/psychiatric diagnoses (e.g. HBN, POND) or extend it into adolescent/early adult onset psychopathology cohorts. But it is fair enough that the authors want to leave that for future work. 

Thank you very much for providing this valuable comment and for your flexibility.

For the current manuscript, we have drawn inspiration from the RDoC framework, which emphasises the variation from normal to abnormal in normative samples (Morris et al., 2022). The ABCD samples align well with this framework.

We hope to extend this framework to include participants with neurological and psychiatric diagnoses in the future. We have begun applying neurobiological units of analysis for cognitive abilities, assessed through multimodal neuroimaging and polygenic scores (PGS), to other datasets containing more participants with neurological and psychiatric diagnoses. However, this is beyond the scope of the current manuscript. We have listed this as one of the limitations in the discussion section:

“Similarly, our ABCD samples were young and community-based, likely limiting the severity of their psychopathological issues (Kessler et al., 2007). Future work needs to test if the results found here are generalisable to adults and participants with stronger severity.”

In terms of more practical concerns, much of the paper relies on comparing r or R2 measures between different tests. These are always presented as point estimates without uncertainty. There would be some value, I think, in incorporating uncertainty from repeated sampling to better understand the improvements/differences between the reported correlations. 

This is a good suggestion. We have now included bootstrapped 95% confidence intervals in all of our scatter plots, showing the uncertainty of predictive performance.

The focus on mental health in a largely normative sample leads to the predictions being largely based on the normal range. It would be interesting to subsample the data and ask how well the extremes are predicted. 

We appreciate this comment. Similar to our response to Reviewer 2’s Weakness #1, our approach has drawn inspiration from the RDoC framework, which emphasises the variation from normal to abnormal in normative samples (Morris et al., 2022). Subsampling the data would make us deviate from our original motivation. 

Moreover, we used 17 mental healh variables in our predictive models: 8 CBCL subscales, 4 BIS/BAS subscales and 5 UPSS subscales. It is difficult to subsample them. Perhaps a better approach is to test the applicability of our neurobiological units of analysis for cognitive abilities (multimodal neuroimaging and PGS) in other datasets that include more extreme samples. We are working on this line of studies at the moment, and hope to show that in our future work. 

Reviewer 2’s Weakness #4

A minor query - why are only cortical features shown in Figure 3? 

We presented both cortical and subcortical features in Figure 3. The cortical features are shown on the surface space, while the subcortical features are displayed on the coronal plane. Below is an example of these cortical and subcortical features from the ENBack contrast. The subcortical features are presented in the far-right coronal image.

We separated the presentation of cortical and subcortical features because the ABCD uses the CIFTI format (https://www.humanconnectome.org/software/workbenchcommand/-cifti-help). CIFTI-format images combine cortical surface (in vertices) with subcortical volume (in voxels). For task fMRI, the ABCD parcellated cortical vertices using Freesurfer’s Destrieux atlas and subcortical voxels using Freesurfer’s automatically segmented brain volume (ASEG).

Due to the size of the images in Figure 3, it may have been difficult for Reviewer 2 to see the subcortical features clearly. We have now added zoomed-in versions of this figure as Supplementary Figures 4–13.

Recommendations for the authors:

Reviewer #1 (Recommendations for the autors):

(1) In the abstract, could the authors mention which imaging modalities contribute most to the prediction of cognitive abilities (e.g., working memory-related task fMRI)? 

Thank you for the suggestion. Following this advice, we now mention which imaging modalities led to the highest predictive performance. Please see the abstract below.

“Cognitive abilities are often linked to mental health across various disorders, a pattern observed even in childhood. However, the extent to which this relationship is represented by different neurobiological units of analysis, such as multimodal neuroimaging and polygenic scores (PGS), remains unclear. 

Using large-scale data from the Adolescent Brain Cognitive Development (ABCD) Study, we first quantified the relationship between cognitive abilities and mental health by applying multivariate models to predict cognitive abilities from mental health in children aged 9-10, finding an out-of-sample r\=.36 . We then applied similar multivariate models to predict cognitive abilities from multimodal neuroimaging, polygenic scores (PGS) and environmental factors. Multimodal neuroimaging was based on 45 types of brain MRI (e.g., task fMRI contrasts, resting-state fMRI, structural MRI, and diffusion tensor imaging). Among these MRI types, the fMRI contrast, 2-Back vs. 0-Back, from the ENBack task provided the highest predictive performance (r\=.4). Combining information across all 45 types of brain MRI led to the predictive performance of r\=.54. The PGS, based on previous genome-wide association studies on cognitive abilities, achieved a predictive performance of r\=.25. Environmental factors, including socio-demographics (e.g., parent’s income and education), lifestyles (e.g., extracurricular activities, sleep) and developmental adverse events (e.g., parental use of alcohol/tobacco, pregnancy complications), led to a predictive performance of r\=.49. 

In a series of separate commonality analyses, we found that the relationship between cognitive abilities and mental health was primarily represented by multimodal neuroimaging (66%) and, to a lesser extent, by PGS (21%). Additionally, environmental factors accounted for 63% of the variance in the relationship between cognitive abilities and mental health. The multimodal neuroimaging and PGS then explained 58% and 21% of the variance due to environmental factors, respectively. Notably, these patterns remained stable over two years. 

Our findings underscore the significance of neurobiological units of analysis for cognitive abilities, as measured by multimodal neuroimaging and PGS, in understanding both a) the relationship between cognitive abilities and mental health and b) the variance in this relationship shared with environmental factors.”

(2) Could the authors clarify what they mean by "completing the transdiagnostic aetiology of mental health" in the introduction? (Second paragraph). 

Thank you. 

We intended to convey that understanding the transdiagnostic aetiology of mental health would be enhanced by knowing how neurobiological units of cognitive abilities, from the brain to genes, capture variations due to environmental factors. We realise this sentence might be confusing. Removing it does not alter the intended meaning of the paragraph, as we clarified this point later. The paragraph now reads:

“According to the National Institute of Mental Health’s Research Domain Criteria (RDoC) framework (Insel et al., 2010), cognitive abilities should be investigated not only behaviourally but also neurobiologically, from the brain to genes. It remains unclear to what extent the relationship between cognitive abilities and mental health is represented in part by different neurobiological units of analysis -- such as neural and genetic levels measured by multimodal neuroimaging and polygenic scores (PGS). To fully comprehend the role of neurobiology in the relationship between cognitive abilities and mental health, we must also consider how these neurobiological units capture variations due to environmental factors, such as sociodemographics, lifestyles, and childhood developmental adverse events (Morris et al., 2022). Our study investigated the extent to which a) environmental factors explain the relationship between cognitive abilities and mental health, and b) cognitive abilities at the neural and genetic levels capture these associations due to environmental factors. Specifically, we conducted these investigations in a large normative group of children from the ABCD study (Casey et al., 2018). We chose to examine children because, while their emotional and behavioural problems might not meet full diagnostic criteria (Kessler et al., 2007), issues at a young age often forecast adult psychopathology (Reef et al., 2010; Roza et al., 2003). Moreover, the associations among different emotional and behavioural problems in children reflect transdiagnostic dimensions of psychopathology (Michelini et al., 2019; Pat et al., 2022), making children an appropriate population to study the transdiagnostic aetiology of mental health, especially within a framework that emphasises normative variation from normal to abnormal, such as the RDoC (Morris et al., 2022).“

(3) It is unclear to me what the authors mean by this statement in the introduction: "Note that using the word 'proxy measure' does not necessarily mean that the predictive model for a particular measure has a high predictive performance - some proxy measures have better predictive performance than others". 

We added this sentence to address a previous reviewer’s comment: “The authors use the phrasing throughout 'proxy measures of cognitive abilities' when they discuss PRS, neuroimaging, sociodemographics/lifestyle, and developmental factors. Indeed, the authors are able to explain a large proportion of variance with different combinations of these measures, but I think it may be a leap to call all of these proxy measures of cognition. I would suggest keeping the language more objective and stating these measures are associated with cognition.” 

Because of this comment, we assumed that the reviewers wanted us to avoid the misinterpretation that a proxy measure implies high predictive performance. This term is used in machine learning literature (for instance, Dadi et al., 2021). We added the aforementioned sentence to ensure readers that using the term 'proxy measure' does not necessarily mean that the predictive model for a particular measure has high predictive performance. However, it seems that our intention led to an even more confusing message. Therefore, we decided to delete that sentence but keep an earlier sentence that explains the meaning of a proxy measure (see below).

“With opportunistic stacking, we created a ‘proxy’ measure of cognitive abilities (i.e., predicted value from the model) at the neural unit of analysis using multimodal neuroimaging.”

(4) Overall, despite comments from reviewers at another journal, I think the authors still refer to RDoC more than needed in the intro given the restructuring of the manuscript. For instance, at the end of page 4 and top of page 5, it becomes a bit confusing when the authors mention how they deviated from the RDoC framework, but their choice of cognitive domains is still motivated by RDoC. I think the chosen cognitive constructs are consistent with what is in ABCD and what other studies have incorporated into the g factor and do not require the authors to further justify their choice through RDoC. Also, there is emerging work showing that RDoC is limited in its ability to parse apart meaningful neuroimaging-based patterns; see for instance, Quah et al., Nature 2025 (https://doi.org/10.1038/s41467-025-55831-z). 

Thank you very much for your comment. We have addressed it in our Response to Reviewer 1’s summary, strengths, and weaknesses above. We have rewritten the paragraph to clarify the relevance of our work to the RDoC framework and to recent studies aiming to improve RDoC constructs (including that from Quah and colleagues).

(5) I am still on the fence about the use of 'proxy measures of cognitive abilities' given that it is defined as the predictive performance of mental health measures in predicting cognition - what about just calling these mental health predictors? Also, it would be easier to follow this train of thought throughout the manuscript. But I leave it to the authors if they decide to keep their current language of 'proxy measure of cognition'. 

Thank you so much for your flexibility. As we explained previously, this ‘proxy measures’ term is used in machine learning literature (for instance, Dadi et al., 2021). We thought about other terms, such as “score”, which is used in genetics, i.e., polygenic scores (Choi et al., 2020). and has recently been used in neuroimaging, i.e., neuroscore (Rodrigue et al., 2024). However, using a ‘score’ is a bit awkward for mental health and socio-demographics, lifestyle and developmental adverse events. Accordingly, we decided to keep the term ‘proxy measures’.

(6) It is unclear which cognitive abilities are being predicted in Figure 1, given the various domains that authors describe in their intro. Is it the g-factor from CFA? This should be clarified in all figure captions. 

Yes, cognitive abilities are operationalised using a second-order latent variable, the g-factor from a CFA. We now added the following sentence to Figure 1, 2, 4 to make this point clearer. Thank you for the suggestion:

“Cognitive abilities are based on the second-order latent variable, the g-factor, based on a confirmatory factor analysis of six cognitive tasks.”

(7) I think it may also be worthwhile to showcase the explanatory power cognitive abilities have in predicting mental health or at least comment on this in the discussion. Certainly, there may be a bidirectional relationship here. The prediction direction from cognition to mental health may be an altogether different objective than what the paper currently presents, but many researchers working in psychiatry may take the stance (with support from the literature) that cognitive performance may serve as premorbid markers for later mental health concerns, particularly given the age range that the authors are working with in ABCD. 

Thank you for this comment. 

It is important to note that we do not make a directional claim in these cross-sectional analyses. The term "prediction" is used in a machine learning sense, implying only that we made an out-of-sample prediction (Yarkoni & Westfall, 2017). Specifically, we built predictive models on some samples (i.e., training participants) and applied our models to test participants who were not part of the model-building process. Accordingly, our predictive models cannot determine whether mental health “causes” cognitive abilities or vice versa, regardless of whether we treat mental health or cognitive abilities as feature/explanatory/independent variables or as target/response/outcome variables in the models. To demonstrate directionality, we would need to conduct a longitudinal analysis with many more repeated samples and use appropriate techniques, such as a cross-lagged panel model. It is beyond the scope of this manuscript and will need future releases of the ABCD data.

We decided to use cognitive abilities as a target variable here, rather than a feature variable, mainly for theoretical reasons. This work was inspired by the RDoC framework, which emphasises functional domains. Cognitive abilities is the functional domain in the current study. We created predictive models to predict cognitive abilities based on a) mental health, b) multimodal neuroimaging, c) polygenic scores, and d) environmental factors. We could not treat cognitive abilities as a functional domain if we used them as a feature variable. For instance, if we predicted mental health (instead of cognitive abilities) from multimodal neuroimaging and polygenic scores, we would no longer capture the neurobiological units of analysis for cognitive abilities.

We now made it clearer in the discussion that our use of predictive models cannot provide the directional of the effects

“Our predictive modelling revealed a medium-sized predictive relationship between cognitive abilities and mental health. This finding aligns with recent meta-analyses of case-control studies that link cognitive abilities and mental disorders across various psychiatric conditions (Abramovitch et al., 2021; East-Richard et al., 2020). Unlike previous studies, we estimated the predictive, out-of-sample relationship between cognitive abilities and mental disorders in a large normative sample of children. Although our predictive models, like other cross-sectional models, cannot determine the directionality of the effects, the strength of the relationship between cognitive abilities and mental health estimated here should be more robust than when calculated using the same sample as the model itself, known as in-sample prediction/association (Marek et al., 2022; Yarkoni & Westfall, 2017). Examining the PLS loadings of our predictive models revealed that the relationship was driven by various aspects of mental health, including thought and externalising symptoms, as well as motivation. This suggests that there are multiple pathways—encompassing a broad range of emotional and behavioural problems and temperaments—through which cognitive abilities and mental health are linked.”

(8) There is a lot of information packed into Figure 3 in the brain maps; I understand the authors wanted to fit this onto one page, and perhaps a higher resolution figure would resolve this, but the brain maps are very hard to read and/or compare, particularly the coronal sections. 

Thank you for this suggestion. We agree with Reviewer 1 that we need to have a better visualisation of the feature-importance brain maps. To ensure that readers can clearly see the feature importance, we added a Zoom-in version of the feature-importance brain maps as Supplementary Figures 4 – 13.

(9) It would be helpful for authors to cluster features in the resting state functional connectivity correlation matrices, and perhaps use shorter names/acronyms for the labels. 

Thank you for this suggestion. 

We have now added a zoomed-in version of the feature importance for rs-fmri as Supplementary Figure 7 (for baseline) and 12 (for follow-up).

(10) Figures 4a) and 4b): please elaborate on "developmental adverse" in the title. I am assuming this is referring to childhood adverse events, or "developmental adversities". 

Thank you so much for pointing this out. We meant ‘developmental adverse events’. We have made changes to this figure in the current manuscript.

(11) For the "follow-up" analyses, I would recommend the authors present this using only the features that are indeed available at follow-up, even if the list of features is lower, otherwise it becomes a bit confusing with the mix of baseline and follow-up features. Or perhaps the authors could make this more clear in the figures by perhaps having a different color for baseline vs follow-up features along the y-axis labels. 

Thank you for this advice. We have now added an indicator in the plot to show whether the features were collected in the baseline or follow-up. We also added colours to indicate which type of environmental factors they were. It is now clear that the majority of the features that were collected at baseline, but were used for the followup predictive model, were developmental adverse events.

(12) Minor: Makowski et al 2023 reference can be updated to Makowski et al 2024, published in Cerebral Cortex. 

Thank you for pointing this out. We have updated the citation accordingly. 

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Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Perlee et al. sought to generate a zebrafish line where CRISPR-based gene editing is exclusively limited to the melanocyte lineage, allowing assessment of cell-type restricted gene knockouts. To achieve this, they knocked in Cas9 to the endogenous mitfa locus, as mitfa is a master regulator of melanocyte development. The authors use multiple candidate genes - albino, sox10, tuba1a, ptena/ptenb, tp53 - to demonstrate their system induces lineagerestricted gene editing. This method allows researchers to bypass embryonic lethal and non-cell autonomous phenotypes emerging from whole body knockout (sox10, tuba1a), drive directed phenotypes, such as depigmentation (albino), and induce lineage-specific tumors, such as melanomas (ptena/ptenb, tp53, when accompanied with expression of BRAFV600E). While the genetic approaches are solid, the argued increase in efficiency of this model compared to current tools was untested, and therefore unable to be assessed. Furthermore, the mechanistic explanations proposed to underlie their phenotypes are mostly unfounded, as discussed further in the Weaknesses section. Despite these concerns, there is still a clear use for this genetic methodology and its implementation will be of value to many in vivo researchers.

Strengths:

The strongest component of this manuscript is the genetic control offered by the mitfa:Cas9 system and the ability to make stable, lineage-specific knockouts in zebrafish. This is exemplified by the studies of tuba1a, where the authors nicely show non-cell autonomous mechanisms have obfuscated the role of this gene in melanocyte development. In addition, the mitfa:Cas9 system is elegantly straightforward and can be easily implemented in many labs. Mostly, the figures are clean, controls are appropriate, and phenotypes are reproducible. The invented method is a welcomed addition to the arsenal of genetic tools used in zebrafish.

Weaknesses:

The major weaknesses of the manuscript include the overly bold descriptions of the value of the model and the superficial mechanistic explanations for each biological vignette.

The authors argue that a major advantage of this system is its high efficiency. However, no direct comparison is made with other tools that achieve the same genetic control, such as MAZERATI. This is a missed opportunity to provide researchers the ability to evaluate these two similar genetic approaches. In addition, Fig.1 shows that not all melanocytes express Cas9. This is a major caveat that goes unaddressed. It is of paramount importance to understand the percentage of mitfa+ cells that express Cas9. The histology shown is unclear and too zoomed out of a scale to make any insightful conclusions, especially in Fig.S1. It would also be beneficial to see data regarding Cas9 expression in adult melanocytes, which are distinct from embryonic melanocytes in zebrafish. Moreover, this system still requires the injection of a plasmid encoding gRNAs of interest, which will yield mosaicism. A prime example of this discrepancy is in Fig.6, where sox10 is clearly still present in "sox10 KO" tumors.

We agree with these points. While our method has the advantage of endogenous knockin (thus keeping all regulatory elements), you are correct that we did not make a direct comparison with existing technologies like MAZERATI, and therefore we cannot make comparative claims about efficiency. Based on this, we have revised the manuscript to remove these points, reduce the strength/boldness of the claims, and make it more clear what our system achieves in comparison to existing systems. In reference to the other specific points you raise above about mosaicism and extent of Cas9 expression:

- We have added a paragraph to address the advantages and disadvantages of mitfaCas9 compared to expression of Cas9 with lineage-specific promoters including MAZERATI in the discussion.  

- Figure 1C has been revised to more clearly show the overlap of mitfa and Cas9 in melanocytes. 

- We then quantified the percentage of mitfa+ cells expressing Cas9 from the in situ hybridizations (Supplemental Figure S1D). We did attempt to look at Cas9 protein expression in both embryonic and adult melanocytes by immunofluorescence. Unfortunately, the Cas9 antibodies commercially available did not work on the zebrafish embryos or adult tailfins, so we are limited in proper quantification to the in situs in the embryos.

The authors argue that their model allows rapid manipulation of melanocyte gene expression. Enthusiasm for the speed of this model is diminished by minimal phenotypes in the F0, as exemplified in Fig.2. Although the authors say >90% of fish have loss of pigmentation, this is misleading as the phenotype is a very weak, partial loss. Only in the F1 generation do robust phenotypes emerge, which takes >6 months to generate. How this is more efficient than other tools that currently exist is unclear and should be discussed in more detail.

This needed clarification, and we have now modified the Discussion to reflect this more accurately. What we were trying to show is that both F0 and F1 fish can be useful in screening for the effect of any given gene. In the F0, while you are correct that the phenotype is indeed weak/partial, it is also quantifiable and therefore can be used as a rapid screen for potential effects of knockout, so it can help with speed. The major advantage of the F1 generation is that we can generate fully penetrant phenotypes for recessive genes since the fish just needs to have 1 copy of the Cas9/sgRNA instead of 2. This means we do not have to go to F2 or F3 generations, which really does save time. But we agree this could be achieved using MAZERATI, and so we have added these considerations to the manuscript, as we feel these are important.

In Figure 3, the authors find that melanocyte-specific knockout of sox10 leads to only a 25% reduction in melanocytes in the F1 generation. This is in contradiction to prior literature cited describing sox10 as indispensable for melanocyte development. In addition, the authors argue that sox10 is required for melanocyte regeneration. This claim is not accurate, as >50% of melanocytes killed upon neocuproine treatment can regenerate. This data would indicate that sox10 is required for only a subset of melanocytes to develop (Fig.3C) and for only a subset to regenerate (Fig.3G). This is an interesting finding that is not discussed or interrogated further.

We too were initially very puzzled by this result. We do not completely understand it, but we have two thoughts about it. First could be timing. sox10 usually starts to be expressed around the 1-somite stage, and so in the original sox10/colourless mutant (which truly has no melanocytes), sox10 will be lost during those early stages. In contrast, mitf comes on later (around 18hpf) so this might indicate that there is a subset of melanocytes that are dependent upon this early expression of sox10. This may indicate that there could be different functions of sox10 early in melanocyte development versus later timepoints after melanocytes have already been specified. This might also help explain our findings during regeneration.  Second could be genetic compensation. Since in the other parts of the paper we seem to see a somewhat reciprocal relationship between sox10 and sox9, it is conceivable that loss of sox10 in the melanocytes could be compensated for by sox9 (or even other genes) in our CRISPR approach (as opposed to the ENU allele in colourless). Since we really do not fully understand this, we have added a section to the Discussion about this issue, mentioning these possibilities but leaving open other yet to be defined mechanisms.

Tumor induction by this model is weak, as indicated by the tumor curves in Figs.5,6. This might be because these fish are mitfa heterozygous. Whereas the avoidance of mitfa overexpression driven by other models including MAZERATI is a benefit of this system, the effect of mitfa heterozygosity on tumor incidence was untested. This is an essential question unaddressed in the manuscript.

We agree that in the BRAF;p53 group especially tumor incidence is very low, although PTEN loss does accelerate it. One possibility is exactly as you stated, and that mitfa heterozygosity is the etiology. The other possibility is that in the MAZERATI approach (https://pubmed.ncbi.nlm.nih.gov/30385465/) the authors used the casper background as opposed to the wild-type T5D as we did in our study. In unpublished observations, we have found that casper (with miniCoopR rescue) is markedly more sensitive to melanoma induction compared to WT fish in this setting. In fact, in looking at our BRAF;p53 curves compared to the original Patton paper curves (https://pubmed.ncbi.nlm.nih.gov/15694309/) which were also done in a WT background with no miniCoopR, they are fairly similar. This might indicate that casper + miniCoopR particularly sensitizes the fish to melanoma. However, because we do not fully know the reasons for this, we have now included both of these possible reasons in the Discussion.

In Fig.6, the authors recapitulate previous findings with their model, showing sox10 KO inhibits tumor onset. The tumors that do develop are argued to be highly invasive, have mesenchymal morphology, and undergo phenotypic switching from sox10 to sox9 expression. The data presented do not sufficiently support these claims. The histology is not readily suggestive of invasive, mesenchymal melanomas. Sox10 is still present in many cells and sox9 expression is only found in a small subset (<20%). Whether sox10-null cells are the ones expressing sox9 is untested. If sox9-mediated phenotypic switching is the major driver of these tumors, the authors would need to knockout sox9 and sox10 simultaneously and test whether these "rare" types of tumors still emerge. Additional histological and genetic evaluation is required to make the conclusions presented in Fig.6. It feels like a missed opportunity that the authors did not attempt to study genes of unknown contribution to melanoma with their system.

We did not mean to overstate the admittedly early observations from these fish. Invasiveness in the fish models can be difficult to precisely quantify, and therefore is somewhat qualitative. While we did not mean to imply that every cell that loses sox10 will become sox9 positive (which is clearly not the case), the human single-cell RNA-seq data does suggest these are somewhat mutually exclusive populations (https://pubmed.ncbi.nlm.nih.gov/32753671/). This phenomenon has also long been observed even prior to single-cell approaches (https://pubmed.ncbi.nlm.nih.gov/25629959/). So while we agree our data is not definitive in this regard, it is consistent with the literature and was presented mainly to provide areas for future exploration with the model. 

Overall, this manuscript introduces a solid method to the arsenal of zebrafish genetic tools but falls short of justifying itself as a more efficient and robust approach than what currently exists. The mechanisms provided to explain observed phenotypes are tenuous. Nonetheless, the mitfa:Cas9 approach will certainly be of value to many in vivo biologists and lays the foundation to generate similar methods using other tissue-specific regulators and other Cas proteins.

We hope that by toning down the language around what we have observed, and providing as honest an assessment as possible as to what might be occurring, that the manuscript will be helpful for future studies aiming to knock out genes in the melanocyte lineage.

Reviewer #2 (Public review):

Summary:

This manuscript describes a genetic tool utilizing mutant mitfa-Cas9 expressing zebrafish to knockout genes to analyze their function in melanocytes in a range of assays from developmental biology to tumorigenesis. Overall, the data are convincing and the authors cover potential caveats from their model that might impact its utility for future work.

Strengths:

The authors do an excellent job of characterizing several gene deletions that show the specificity and applicability of the genetic mitfa-Cas9 zebrafish to studying melanocytes.

Weaknesses:

Variability across animals not fully analyzed.

To more clearly show variability across animals, we calculated the percentage of mitfa+ cells that express Cas9 across n=7 mitfaCas9 embryos. We also expanded Supplemental Figure 2 to show loss of pigmentation across n=7 individual adult MG-albino F2 fish instead of one representative image.

Reviewer #3 (Public review):

Summary:

Perlee et al. present a method for generating cell-type restricted knockouts in zebrafish, focusing on melanocytes. For this method, the authors knock-in a Cas9 encoding sequence into the mitfa locus. This mitfaCas9 line has restricted Cas9 expression, allowing the authors to generate melanocyte-specific knockouts rapidly by follow-up injection of sgRNA expressing transposon vectors.

The paper presents some interesting vignettes to illustrate the utility of their approach. These include 1) a derivation of albino mutant fish as a demonstration of the method's efficiency, 2) an interrogation and novel description of tuba1a as a potential non-autonomous contributor to melanocyte dispersion, and 3) the generation of sox10 deficient melanoma tumors that show "escape" of sox10 loss through upregulation of sox9. The latter two examples highlight the usefulness of cell-type targeted knockouts (Body-wide sox10 and tuba1a loss elicit developmental defects). Additionally, the tumor models involve highly multiplexed sgRNAs for tumor initiation which is nicely facilitated by the stable Cas9.

Strengths:

The approach is clever and could prove very useful for studying melanocytes and other cell types. As the authors hint at in their discussion, this approach would become even more powerful with the generation of other Cas9-restricted lineages so a single sgRNA construct can be screened across many lineages rapidly (or many sgRNA and fish lines screened combinatorially).

The biological findings used to demonstrate the power of the approach are interesting in their own right. If it proves true, tuba1a's non-autonomous effects on melanosome dispersion are striking, and this example demonstrates very nicely how one could use Perlee et al.'s approach to search for other non-autonomous mechanisms systematically. Similarly, the observation of the sox9 escape mechanism with sox10 loss is a beautiful demonstration of the relevance of SOX10/SOX9's reciprocal regulation in vivo. This system would be a very nice model for further interrogating mechanisms/interventions surrounding Sox10 in melanoma.

Finally, the figure presentation is very nice. This work involves complex genetic approaches including multiple fish generations and multiplexed construct injections. The vector diagrams and breeding schemes in the paper make everything very clear/"grok-able," and the paper was enjoyable to read.

Weaknesses:

The mitfa-driven GFP on their sgRNA-expressing cassette is elegant, but it makes one wonder why the endogenous knock-in is necessary. It would strengthen the motivation of the work if the authors could detail the potential advantages and disadvantages of their system compared to expressing Cas9 with a lineage-specific promoter from a transposon in their introduction or discussion.

We agree this needed a better and more clear explanation. There are many excellent examples of promoter driven Cas9 approaches. Within melanocytes, Ablain and others have developed the MAZERATI system (https://pubmed.ncbi.nlm.nih.gov/30385465/) which is very powerful, especially for melanoma development. In our minds, the major advantage of endogenous knockin is that we retain all of the natural regulatory elements (many of which are not known) and so small promoter fragments always run the risk of missing certain types of regulation. While these regulatory elements may not matter under homeostatic conditions, they may become very important under perturbation, stress or disease states. This is why it is common, for example, in the mouse field, to knock in things like Cre into endogenous loci. We have now added a clarification of this to the manuscript.

Related to the above - is mitfa haplosufficient? If the mitfaCas9/+ fish have any notable phenotypes, it would be worth noting for others interested in using this approach to study melanoma and pigmentation.

In normal melanocytes, mitfa is haplosufficient. There are no visible differences between mitfaCas9/+ and wild-type fish at any stages of development (Figure S1C). Although we did not directly compare tumor growth in mitfa-/+ and mitfa+/+ fish in this study, it is possible that the disruption of mitfa in mitfaCas9/+ fish affects melanoma development. Most zebrafish melanoma models involve the overexpression of mitfa with MiniCoopR vectors and it would be interesting in future studies to determine how mitfa heterozygosity affects melanoma initiation or progression. 

A core weakness (and also potential strength) of the system is that introduced edits will always be non-clonal (Fig 2H/I). The activity of individual sgRNAs should always be validated in the absence of any noticeable phenotype to interpret a negative result. Additionally, caution should be taken when interpreting results from rare events involving positive outgrowth (like tumorogenesis) to account for the fact many cells in the population might not have biallelic null alleles (i.e., 100% of the gene product removed).

Along those lines: in my opinion, the tuba1a results are the most provocative finding in the paper, but they lack key validation. With respect to cutting activity, the Alt-R and transgenic sgRNA expression approaches are not directly comparable. Since there is no phenotype in the melanocyte specific tuba1a knockouts, the authors must confirm high knockout efficiency with this set of reagents before making the claim there is a non-autonomous phenotype. This can be achieved with GFP+ sorting and NGS like they performed with their albino melanocytes.

The whole-body tuba1a knockout phenotype is expected to be pleiotropic, and this expectation might mask off-target effects. Controls for knockout specificity should be included. For instance, confidence in the claims would greatly increase if the dispersed melanosome phenotype could be recovered with guide-resistant tuba1a re-expression and if melanocyte-restricted tuba1a reexpression failed to rescue. As a less definitive but adequate alternative, the authors could also test if another guide or a morpholino against tuba1a phenocopies the described Alt-R edited fish.

Thank you for your thoughtful suggestions, which led us to an important discovery. While validating the original tuba1a guide RNA, we found that tuba1a sg1 also targets tuba1c, a gene that shares 99.78% homology with tuba1a in zebrafish. To determine which gene was responsible for the melanocyte phenotype, we designed multiple new guide RNAs specifically targeting either tuba1a or tuba1c and used Alt-R to globally knock them out in zebrafish embryos. However, none of these guides successfully replicated the phenotype (Sanger sequencing validation for the most efficient tuba1a and tuba1c guides is provided below).

Ultimately, we identified a new guide RNA (5’-GGTCTACAAAGACAGCCCTA-3’) that successfully phenocopied the original tuba1a sg1 melanocyte phenotype. Tuba1c—but not tuba1a—was predicted to have a mismatch at the 3’ end of the guide sequence, which is typically expected to inhibit target cleavage. Surprisingly, despite this mismatch, we observed robust cleavage in both tuba1a and tuba1c. Since the melanocyte phenotype was only reproducible when both tuba1a and tuba1c were targeted, this suggests potential compensatory interactions between these highly similar genes. We have updated the text and figures to reflect this finding and have included validation of this second guide RNA (tuba1a/c sg2) in Supplemental Figure 3.

As you suggested, we also conducted GFP+ sorting and NGS to confirm knockout of both tuba1a and tuba1c in melanocytes of mitfaCas9 fish (Figure S3G). The knockout percentages were comparable to those observed in our previous experiment with MG_-albino_ fish. This also confirms that this method can be used to sort and sequence GFP+ cells even when pigmentation is retained, which was not the case for albino fish. 

I have similar questions about the sox10 escapers, but these suggestions are less critical for supporting the authors claims (especially given the nice staining). Are the sox10 tumors relatively clonal with respect to sox10 mutations? And are the sox10 tumor mutations mostly biallelic frameshifts or potential missense mutations/single mutations that might not completely remove activity? I am particularly curious as SOX10 doesn't seem to be completely absent (and is still very high in some nuclei) in the immunohistochemistry.

We attempted to address this question by performing DNA sequencing on the FFPE blocks that we had retained from the original study. While our sequencing facility said this should be possible, we could not consistently generate high enough quality DNA to make a definitive statement either way. While we are very curious to know what the nature of the mutations are in these “escapers”, the student who performed these studies has now graduated, and it would take us several additional months to a year to fully address it. Given this, we would prefer to leave this open question to a future paper, but have addressed this limitation in the Discussion.

Recommendations for the authors:

Reviewing Editor:

Overall, the reviewers felt and eLife concurs that your manuscript is insightful and appropriate for publication. Reviewers were impressed by your generating a zebrafish line where CRISPRbased gene editing is exclusively limited to the melanocyte lineage, allowing assessment of celltype restricted gene knockouts. Your use of multiple candidate genes to demonstrate that your system induces lineage-restricted gene editing is compelling and will be of interest to the broad readership of eLife. This method will allow researchers to bypass embryonic lethal and non-cell autonomous phenotypes emerging from whole body knockout, drive directed phenotypes, such as depigmentation, and induce lineage-specific tumors, such as melanomas. This said, the argued increase in efficiency of this model compared to current tools was untested, and therefore it remains difficult for a reader to assess the extent to which your new model represents a major advance over prior ones. Of additional concern are the mechanistic explanations proposed to underlie the phenotypes, as these are largely unfounded. Thus, in preparing your final publication version of the paper, eLife strongly encourages you to fully address the reviewers' thoughtful comments. In particular, the boldness of the claims made in the manuscript should be reduced. Terms like "highly efficient" and "rapid" are unsupported due to the lack of comparison with other well-established methods, like MAZERATI.

As discussed above in each of the reviewer points above, we agree with both of these points. We have reduced the boldness of the claims, with a better discussion of the different approaches. We also address the potential mechanisms of our observations, and where and why we still lack an understanding of what gives rise to those phenotypes. 

There are also some minor discrepancies that should be edited in the manuscript: Fig.2A plasmid description is written oppositely in text; Fig.3 labels G-H are swapped in the legend description; Fig.5A MTdT is unexplained. This is a non-exhaustive list, and the authors are encouraged to carefully read through their manuscript to revise other minor mistakes and formatting errors.

Figure 2A was revised to show the correct orientation of mitfa:GFP and the guide RNA cassette as described in the text. Figure 3 legend was fixed. We have gone through the manuscript again to make sure we have not made any other errors, to the best of our knowledge.

The biggest concern is the expression of cas9 and the weak histological support shown in Fig.1 and Fig.S1. It would be a benefit to all readers and potential future users to know how robust cas9 expression is in the melanocyte lineage. It would be helpful if there is a way to analyze the percentage of cells that are mutated in each animal to understand the variability that can exist across animals with the method.

We have revised Figure 1C to show additional melanocytes and added a new quantification of Cas9 RNA expression in melanocytes (S1D). 

The analysis of the scRNA sequencing could also be described more fully.

More details have been added to the scRNA sequencing analysis including the functions that were used. 

The final major concern is whether this model is genuinely more valuable than MAZERATI. A more elaborate discussion would benefit potential future users to guide their decisions regarding which tool best suits their experimental goals.

As noted above, we agree with this statement. The reviewers are correct in that we did not directly compare our system to MAZERATI, and therefore cannot make any claims about efficiency in a comparative regard. Therefore, in our revised Discussion, we talk about the relative strengths and weaknesses of each approach, and emphasize that our approach mainly has the advantage of retaining endogenous regulatory elements for mitfa, but that each user should decide which is the best approach for their problem.

There are also some minor concerns that should be addressed.

Are the mitfaCas9 fish used as homozygotes before the first cross? If so, might be nice to include their nacre-like phenotype in diagrams like Fig 2A.

For these studies, heterozygous mitfaCas9 fish were used for all breedings and progeny were sorted for BFP+ eyes. This enabled the comparison to sibling controls without Cas9 expression. 

BFP+ eye screening for mitfaCas9 is elegant and included nicely in the diagrams. Are germline sgRNA integrants identified in F1 with melanocyte GFP? Or present at a high enough efficiency that this is not relevant? This would be good to include in the diagrams.

Germline sgRNA integrants are identified with melanocyte GFP in embryos. Figure 2A has been edited to show GFP expression. 

Most cells are GFP positive in S3C (the F0 "mosaic"). It might be nice to show a single GFP stripe like in the other panels for direct comparison of edited/non-edited in the same fish.

This figure (now S3E) has been edited to show a clear comparison between GFP+ and GFP- cells in the same fish. 

177 - CRISPR-Seq is basically amplicon sequencing. This would measure efficiency but not "specificity" as described. Off-target activity would have to be measured at other loci etc. Not necessary to do, but I don't think measured.

In this case, “specificity” refers to cell type specificity, not genomic specificity. We are measuring cell type specificity by comparing on-target cutting in GFP+ cells (melanocytes) versus GFP- cells (non-mitfa expressing cells). We did not look at off-target activity of Cas9 in this study and have edited the text to make this clearer. 

219 -"several gaps were visible"

Fixed

286 - TUBA1A should be italicized

Fixed

399 - SOX9's most enriched dependency in DepMap is cutaneous melanoma and its top coessential gene is SOX10. I'm not sure the SOX9/SOX10 interaction couldn't be parsed from DepMap alone.

This is true, and the DepMap was actually somewhat of an inspiration for our own studies. We have modified the line to acknowledge this and explain the main advantage of our system is in vivo confirmation of what the DepMap had alluded to.

433 - "fewer animals since all F1 animals (even those for recessive alleles) are informative."

The fact that this is approach is faster and more efficient per animal is important to highlight (and very believable), but is this technically true given not all F1 fish will have Cas9 or a germline sgRNA integration?

In considering this statement, we agree with you and decided to remove it from the text.

We hope the comments in both the public and private reviews will help improve the manuscript.

Reviewer #1 (Recommendations for the authors):

Overall, the boldness of the claims made in the manuscript should be reduced. Terms like "highly efficient" and "rapid" are unsupported due to the lack of comparison with other wellestablished methods, like MAZERATI.

As discussed above, we agree with this and have now modified the manuscript to better reflect what our system achieves in comparison to the well developed systems such as MAZERATI. Because we have not done a direct comparison, we are not able to make any claims about comparative efficiency, and instead focus on the potential benefits of a knockin approach, which is the maintenance of endogenous regulatory elements.

There are some minor discrepancies that should be edited in the manuscript: Fig.2A plasmid description is written oppositely in text; Fig.3 labels G-H are swapped in the legend description; Fig.5A MTdT is unexplained. This is a non-exhaustive list, and the authors are encouraged to carefully read through their manuscript to revise other minor mistakes and formatting errors.

Figure 2A was revised to show the correct orientation of mitfa:GFP and the guide RNA cassette as described in the text. Figure 3 legend was fixed. We have gone through the manuscript again to make sure we have not made any other errors, to the best of our knowledge.

The biggest concern is the expression of cas9 and the weak histological support shown in Fig.1 and Fig.S1. It would be a benefit to all readers and potential future users to know how robust cas9 expression is in the melanocyte lineage.

We have revised Figure 1C to show additional melanocytes and added a new quantification of Cas9 RNA expression in melanocytes (S1D). 

The second major concern is whether this model is genuinely more valuable than MAZERATI. A more elaborate discussion would benefit potential future users to guide their decision regarding which tool best suits their experimental goals.

As noted above, we agree with this statement. The reviewers are correct in that we did not directly compare our system to MAZERATI, and therefore cannot make any claims about efficiency in a comparative regard. Therefore, in our revised Discussion, we talk about the relative strengths and weaknesses of each approach, and emphasize that our approach mainly has the advantage of retaining endogenous regulatory elements for mitfa, but that each user should decide which is the best approach for their problem.

We hope the comments in both the public and private reviews will help improve the manuscript.

Reviewer #2 (Recommendations for the authors):

While that authors show the indel charts for the Crispr mutations generated in the supplement. However, I wonder if there is a way to analyze the percentage of cells that are mutated in each animal to understand the variability that can exist across animals with the method.

We have revised Figure 1C to show additional melanocytes and added a new quantification of Cas9 RNA expression in melanocytes (S1D). 

The analysis of the scRNA sequencing could be described more fully.

More details have been added to the scRNA sequencing analysis including the functions that were used. 

Reviewer #3 (Recommendations for the authors):

This was an excellent read, and I'm very interested in seeing it in its final form. Congratulations! My larger critiques are outlined in the public reviews. A few smaller points:

Are the mitfaCas9 fish used as homozygotes before the first cross? If so, might be nice to include their nacre-like phenotype in diagrams like Fig 2A.

For these studies, heterozygous mitfaCas9 fish were used for all breedings and progeny were sorted for BFP+ eyes. This enabled the comparison to sibling controls without Cas9 expression. 

BFP+ eye screening for mitfaCas9 is elegant and included nicely in the diagrams. Are germline sgRNA integrants identified in F1 with melanocyte GFP? Or present at a high enough efficiency that this is not relevant? This would be good to include in the diagrams.

Germline sgRNA integrants are identified with melanocyte GFP in embryos. Figure 2A has been edited to show GFP expression. 

Most cells are GFP positive in S3C (the F0 "mosaic"). It might be nice to show a single GFP stripe like in the other panels for direct comparison of edited/non-edited in the same fish.

This figure (now S3E) has been edited to show a clear comparison between GFP+ and GFP- cells in the same fish. 

177 - My understanding is that CRISPR-Seq is basically amplicon sequencing. This would measure efficiency but not "specificity" as described. Off-target activity would have to be measured at other loci etc. Not necessary to do in my opinion, but I don't think measured.

In this case, “specificity” refers to cell type specificity, not genomic specificity. We are measuring cell type specificity by comparing on-target cutting in GFP+ cells (melanocytes) versus GFP- cells (non-mitfa expressing cells). We did not look at off-target activity of Cas9 in this study and have edited the text to make this clearer. 

219 -"several gaps were visible"

Fixed

286 - TUBA1A should be italicized

Fixed

399 - I think I understand the logic of the DepMap argument, and the importance of studying tumor initiation in vivo stands for itself. But here is maybe not the best example (or might need clarification)? - SOX9's most enriched dependency in DepMap is cutaneous melanoma and its top co-essential gene is SOX10. I'm not sure the SOX9/SOX10 interaction couldn't be parsed from DepMap alone.

This is true, and the DepMap was actually somewhat of an inspiration for our own studies. We have modified the line to acknowledge this and explain the main advantage of our system is in vivo confirmation of what the DepMap had alluded to.

433 - "fewer animals since all F1 animals (even those for recessive alleles) are informative."

The fact that this is approach is faster and more efficient per animal is important to highlight (and very believable), but is this technically true given not all F1 fish will have Cas9 or a germline sgRNA integration?

In considering this statement, we agree with you and decided to remove it from the text.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Summary:

The authors present a new protocol to assess social dominance in pairs and triads of C57BL/6j mice, based on a competition to access a hidden food pellet. Using this new protocol, the authors have been able to identify stable ranking among male and female pairs, while reporting more fluctuant hierarchies among triads of males. Ranking readouts identified with this new apparatus were compared to the outcomes obtained with the same animals competing in the tube and in the warm spot tests, which have been both commonly used during the last decade to identify social ranks in rodents under laboratory conditions.

Strengths:

FPCT allows for easy and fast identification of a winner and a loser in the context of food competition. The apparatus and the protocol are relatively easy and quick to implement in the lab and free from any complex post-processing/analysis, which qualifies it for wide distribution, particularly within laboratories that do not have the resources to implement more sophisticated protocols. Hierarchical readouts identified through the FPCT correlate with social ranks identified with the tube and the warm spot tests, which have been widely adopted during the last decade and allow for study comparison.

Weaknesses:

While the FPCT is validated by the tube and the warm spot test, this paper would have gained strength by providing a more ethologically based validation. Tube and warm spot tests have been shown to provide conflicting results and might not been a sufficient measurement for social ranking (see Varholik et al, Scientific reports, 2019; Battivelli et al, Biological psychiatry, 2024). Instead, a general consensus pushing toward more ethological approaches for neuroscience studies is emerging.

We appreciate all the reviewers for recognizing the strength of the FPCT setup and the data. We also appreciate the reviewers for pointing out weakness and giving us valuable suggestions that help us to improve the quality of our manuscript through revision.

In this manuscript, we found the ranking results of the FPCT were largely consistent with the tube and the warm spot tests. Such a finding was unexpected by us as we considered that different competitive targets of different paradigms should provide the mice with distinct appeals and enable them to exert their specific advantages. However, the consistency between the FPCT and tube test was observed in the pairs of female mice, pairs of male mice and triads of male mice. The consistency between the FPCT, tube test and warm spot test was observed in pairs of male mice and triads of male mice. Thus, we concluded that there is a social rank-order stability of mice. 

We acknowledge that it’d better if this conclusion could be validated by more ethological approaches like urine-marking analysis and water competition test. Whereas, we did not rule out inconsistency of ranking results between two or more paradigms. Actually, there were inconsistent cases in our experiments. The inconsistency of ranking results between paradigms, even between FPCT and tube test, could be amplified if the tests were operated with other details of experimental protocols and conditions. This is in that too many factors and aspects can affect the readouts, such as formation of colony, tasks, test protocols, habituation and training. Using tube test itself, both stable 1,2 and unstable 3 ranking results have been reported.

Other papers already successfully identified social ranks dyadic food competition, using relatively simple scoring protocol (see for example Merlot et al., 2006), within a more naturalistic set-up, allowing the 2 opponents to directly interact while competing for the food. A potential issue with the FPCT, is that the opponents being isolated from each other, the normal inhibition expected to appear in subordinates in the presence of a dominant to access food, could be diminished, and usually avoiding subordinates could be more motivated to push for the access to the food pellet.

The hierarchical structure of mice colony could be established on the basis of physical aspects—such as muscular strength, vigorousness of fighting—and psychological aspects— such as boldness, focused motivation, active self-awareness of status. In the contexts of currently available food contest paradigms where the mice compete with bodily interaction, the physical and psychological aspects are intermingled in the interpretation of the mice’s winning/losing. In the FPCT, the opponents are isolated from each other so that the importance of direct bodily interaction in a competition is minimized, facilitating the exposure of psychological factors contributing to the establishment and/or expression of social status of the mice. In this study, the overall stable ranking results across the FPCT, tube test and warm spot test indicate that the status sense of animals is part of a comprehensive identify of self-recognition of individuals in an established mice social colony.

There are issues with use of the English language throughout the text. Some sentences are difficult to understand and should be clarified and/or synthesized.

We thank the reviewer for pointing out language issues. We have carefully corrected the grammar errors.

Open question:

Is food restriction mandatory? Palatable food pellet is not sufficient to trigger competition? Food restriction has numerous behavioral and physiological consequences that would be better to prevent to be able to clearly interpret behavioral outcomes in FPCT (see for example Tucci et al., 2006).

We thank the reviewer for raising this question. In the preliminary experiments, we noticed that food restriction was mandatory and palatable food pellet was not sufficient to trigger competition. In order to limit the potential influence of food restriction on competitive behavior, the mice underwent only a 24-hour food deprivation period at the beginning of training, followed by mild restriction of food supply to meet basic energy requirement.

Conclusive remarks:

Although this protocol attempts to provide a novel approach to evaluate social ranks in mice, it is not clear how it really brings a significant advance in neuroscience research. The FPCT dynamic is very similar to the one observed in the tube test, where mice compete to navigate forward in a narrow space, constraining the opponent to go backward. The main difference between the FPCT and the tube test is the presence of food between the opponents. In the tube test, a food reward was initially used to increase motivation to cross the tube and push the opponent upon the testing day. This component has been progressively abandoned, precisely because it was not necessary for the mice to compete in the tube.

This paper would really bring a significant contribution to the field by providing a neuronal imaging or manipulation correlate to the behavioral outcome obtained by the application of the FPCT.

Thank the reviewer for this comment on the significance of the FPCT paradigm. In this manuscript, we think it is interesting to report that the ranking results were consistent across the FPCT, tube test and warm spot test. This finding indicates that the status sense of animals might be a part of a comprehensive identify of self-recognition of individuals in an established social colony. 

Moreover, we are conducting researches on biological consequences and mechanisms of social competition. Hopefully, the results of the on-going project will be published in the near future.

Reviewer #2 (Public review):

Summary:

In this study, the authors have devised a novel assay to measure relative social rank in mice that is aimed at incorporating multiple aspects of social competition while minimizing direct contact between animals. Forming a hierarchy often involves complex social dynamics related to competitive drives for different fundamental resources including access to food, water, territory, and sexual mates. This makes the study of social dominance and its neural underpinnings hard, warranting the development of new tools and methods that can help understand both social functions as well as dysfunction.

Strengths:

This study showcases an assay called the Food Pellet Competition Test where cagemate mice compete for food, without direct contact, by pushing a block in a tube from opposite directions. The authors have attempted to quantify motivation to obtain the food independent of other factors such as age, weight, sex, etc. by running the assay under two conditions: one where the food is accessible and one where it isn't. This assay results in an impressive outcome consistency across days for females and males paired housed and for male groups of three. Further, the determined social ranks correlate strongly with two common assays: the tube test and the warm spot test.

Weaknesses:

This new assay has limited ethological validity since mice do not compete for food without touching each other with a block in the middle. In addition, the assay may only be valid for a single trial per day making its utility for recording neural recordings and manipulations limited to a single sample per mouse. Although the authors attempt to measure motivation as a factor driving who wins the social competition, the data is limited. This novel assay requires training across days with some mice reaching criteria before others. From the data reported, it is unclear what effects training can have on the outcome of social competition. Beyond the data shown, the language used throughout the manuscript and the rationale for the design of this novel assay is difficult to understand.

We appreciate the reviewers for the valuable comments on the strength and weakness of our manuscript. 

The design mentality of the FPCT was to (1) provide researchers with a choice of new food competition paradigm and (2) expose psychological factors influencing the establishment and/or expression social status in mice by avoiding direct physical competition between contenders (see revised Abstract and the last paragraph in the Introduction).

As a result, the consistent ranking across the FPCT, tube test and warm spot test might indicate that the status sense of animals is part of a comprehensive identify of self-recognition of individuals in an established social colony. 

We suggest to perform the FPCT test one trial per day per mouse as the mice might lose interest in the food pellet if it is tested frequently in a day, but it is practical to perform the FPCT assay for several days. 

Regarding the training, we suggest 4-5 days for training as we did. In this revision, we add training data which show the progressing latency of food-getting of mice (Figure 1). At the last day of training, the mice would go directly to push the block and eat the food after they entered the arena.

We thank the reviewer for pointing out language issues. We have carefully corrected the errors.

Reviewer #3 (Public review):

Summary:

The laboratory mouse is an ideal animal to study the neural and psychological underpinnings of social dominance behavior because of its economic cost and the animals' readiness to display dominant and subordinate behaviors in simple and testable environments. Here, a new and novel method for measuring dominance and the individual social status of mice is presented using a food competition assay. Historically, food competition assays have been avoided because they occur in an open arena or the home cage, and it can be difficult to assess who gets priority access to the resource and to avoid aggressive interactions such as bite wounding. Now, the authors have designed a narrow rectangular arena separated in half by a sliding floor-to-ceiling obstacle, where the mice placed at opposite sides of the obstacle compete by pushing the obstacle to gain priority access to a food pellet resting on the arena floor under the obstacle. One can also place the food pellet within the obstacle to restrict priority access to the food and measure the time or effort spent pushing the obstacle back and forth. As hypothesized, the outcomes in the food competition test were significantly consistent with those of the more common tube test (space competition) and warm spot competition test. This suggests that these animals have a stereotypic dominance organization that exists across multiple resource domains (i.e., food, space, and temperature). Only male and female C57 mice in same-sex pairs or triads were tested.

Strengths:

The design of the apparatus and the inclusion of females are significant strengths within the study.

Weaknesses:

There are at least two major weaknesses of the study: neglecting the value of test inconsistency and not providing the mice time to recognize who they are competing with.

Several studies have demonstrated that although inbred mice in laboratory housing share similar genetics and environment, they can form diverse types of hierarchical organizations (e.g., loose, stable, despotic, linear, etc.) and there are multiple resource domains in the home cage that mice compete over (e.g., space, food, water, temperature, etc.). The advantage of using multiple dominance assays is to understand the nuances of hierarchical organizations better. For example, some groups may have clear dominant and subordinate individuals when competing for food, but the individuals may "change or switch" social status when competing for space. Indeed, social relationships are dynamic, not static. Here, the authors have provided another test to measure another dimension of dominance: food competition. Rather than highlight this advantage, the authors highlight that the test is in agreement with the standard tube test and warm spot test and that C57 mice have stereotypic dominance across multiple domains. While some may find this great, it will leave many to continue using the tube test only (which measures the dimension of space competition) and avoid measuring food competition. If the reader looks at Figures 6E, F, and G they will see examples of inconsistency across the food competition test, tube test, and warm spot test in triads of mice. These groups are quite interesting and demonstrate the diversity of social dynamics in groups of inbred mice in highly standardized environmental conditions. Scientists interested in dominance should study groups that are consistent and inconsistent across multiple dimensions of dominance (e.g., space, food, mates, etc.).

Unlike the tube test and warm spot test, the food competition test presented here provides no opportunity for the animals to identify their opponent. That is, they cannot sniff their opponent's fur or anogenital region, which would allow them an opportunity to identify them individually. Thus, as the authors state, the test only measures psychological motivation to get a food reward. Notably, the outcome in the direct and indirect testing of food competition is in agreement, leaving many to wonder whether they are measuring the social relationship or the effort an individual puts forth in attaining a food reward regardless of the social opponent. Specifically, in the direct test, an individual can retrieve the food reward by pushing the obstacle out of the way first. In the indirect test, the animals cannot retrieve the reward and can only push the obstacle back and forth, which contains the reward inside. In Figure 4E, you can see that winners spent more time pushing the block in the indirect test. Thus, whether the test measures a social relationship or just the likelihood of gaining priority access to food is unclear. To rectify this issue, the authors could provide an opportunity for the animals to interact before lowering the obstacle and raising(?) a food reward. They may also create a very long one-sided apparatus to measure the amount of effort an individual mouse puts forth in the indirect test with only one individual - or any situation with just one mouse where the moving obstacle is not pushed back, and the animal can just keep pushing until they stop. This would require another experiment. It also may not tell us much more since it remains unclear whether inbred mice can individually identify one another

(see https://doi.org/10.1098/rspb.2000.1057 for more details).

A minor issue is that the write-up of the history of food competition assays and female dominance research is inaccurate. Food competition assays have a long history since at least the 1950s and many people study female dominance now.

Food competition: https://doi.org/10.1080/00223980.1950.9712776, https://psycnet.apa.org/fullte xt/1953-03267-

001.pdf, https://doi.org/10.1016/j.bbi.2003.11.007, https://doi.org/10.1038/s41586-02204507-5

Female dominance: history  https://doi.org/10.1016/j.cub.2023.03.020,  https://doi.org/10.1016/S0 031-9384(01)00494-2,  https://doi.org/10.1037/0735-7036.99.4.411

We thank the reviewers very much for so many helpful comments and suggestions.

In this manuscript, we want to address the overall and averagely consistency of ranking results between FPCT, tube test and warm spot test) as an unexpected finding. We agree that the inconsistency of social ranking occurred between trials and between paradigms should not be ignored. In the revision, we added description and discussion of inconsistent part of the different test paradigms (paragraph 2 in the section 3 of the Result, last 2 sentences of paragraph 4 in the Discussion)

Although the two opponents were separated each other, they were able to see and sniff each other because the block is transparency, there are holes in the lower portion of the block, and there is the gap between the block and chamber (Supplementary figures 1 and 2). In the female but not male groups, the presence of a cagemate opponent during the test 1 could significantly disturb the female mice and increase the its latency to get the food, comparing with last day of training when there was no opponent (Figure 3A). This indicates that one mouse, at least female mouse, could identify the existence of the opponent in the opposite side of the chamber. To further see whether social relation was influential to readouts of the FPCT, we performed additional experiments using two groups of non-cagemate mice to perform the competition. We did not detect obviously different ranks between the two groups (Figure 1H-1J), suggesting that establishment of social colony is necessary for FPCT to distinguish social ranks of mice.

Thank the reviewer for reminding us to recognize the history of food competition assays. We have added the citations and discussions of related literatures, both for male (paragraph 2 in the Introduction; paragraph 3 in the Discussion) and female (paragraph 1 of section 3 in the Results; paragraph 4 in the Discussion) mice. 

Reviewer #1 (Recommendations for the authors):

There are issues with use of the English language throughout the text. Some sentences are difficult to understand and should be clarified and/or synthesized.

We appreciate the reviewer for constructive comments and helpful corrections.

“Despite that 6 in 9 groups of mice display some extent of flipped ranking (Figures 6B-6G) and only 3 in 9 groups displayed continuously unaltered ranking (Figure 6H) during a total of 9 trials consisting of 3 trials of FPCT, 3 trials of tube test and 1 trial of WST, an obvious stable linear intragroup hierarchy was observed throughout all the trials and tasks"

The above sentence has been re-written as: The ranking result showed that 6 in 9 groups of mice displayed some extent of flipped ranking (Figures 4B-4G), and only 3 in 9 groups displayed continuously unaltered ranking (Figure 4H). Averagely, in the totally 27 trials consisting of 12 trials of FPCT, 12 trials of tube test and 3 trials of WST, an obvious stable linear intragroup hierarchy was observed across all the trials and tasks (paragraph 1 of section 4 in the Results).

"it is hard to attribute winning a competition in a shared space to stronger motivation rather than muscular superiority".

The above sentence has been deleted and re-written in paragraph 1 of section 4 in the Results and paragraph 3 in the Discussion.

"Unexpectedly, in most of the trials the mice preserved the winner or loser identity acquired in FPCT into tube test and WST (Figures 5L-5O)".

Why this is unexpected? Instead, it looks like this result is expected (tube test has been successfully applied to identify ranks in females, see Leclair et al, eLife, 2021).

We thank the reviewer for raising this point. FPCT is different from tube test and warm spot test at least in two aspects: competition for food vs space; presence vs absence of direct bodily interaction during competition. Some mice might be active in food competition, but not in space competition, while others might be on the contrary. Some mice might be good at physical contest, while others might be good at play tricks. Therefore, these factors made us expect task-specific outcomes of ranking results.

Vocabulary issues:

"Stereotypic", to talk about rank stability in a different context does not look appropriate. In behavioral neuroscience, stereotypy is more excepted to intend abnormal repetitive behaviors. The stability that the authors seem to indicate with the word "stereotype" refers rather to the concept of "consistency" or "stability".

We thank the reviewer for this detailed explanation. We have chosen to use "stability" to describe the data.

"Society", to talk about groups or colonies of animals sounds a bit odd. Society evokes more abstract concepts more likely to fit with human organization. I suggest the use of "group" or "colony".

"Hide" to qualify the block preventing access to the food pellet. It is said that the block is transparent. We suggest the use of "inaccessible" instead of hidden.

We strongly encourage the authors to further edit the entire script to improve language.

Thank the reviewer for kind correction. We have corrected the above vocabulary misuse. 

Technical issues / typos:

Figure 1. The picture does not seem optimal to visualize the apparatus.

Missing unit legend in Figure 4E.

Supplementary videos 2 and 4 are missing.

We have added a frontal view of the apparatus in the figure (Supplementary Figure 1), added a unit to the Figure 2F (previous Figure 4E), and we will make sure to upload the missing videos.

Reviewer #2 (Recommendations for the authors):

While the assay shows promise as a tool for studying social dominance, the study suffers from some limitations such as lack of ethological relevance. In addition, there is a lack of rationale and methodological clarity in the manuscript that can impact the ability of other scientists to be able to perform this novel assay.

(1) Related to lack of scientific rigor:

a. In the first paragraph of the introduction, the authors mention that "disability in social recognition and unsatisfied social status are associated with brain diseases such as autism, depression and schizophrenia". Both papers that they cited refer to mouse models, not humans (which is the species that is attributed these diagnoses clinically). In addition, neither citation discusses schizophrenia. While social dysfunctions can indeed be related to these diseases, to my knowledge this is not caused by a change in "social status" and there is no human data with patient populations and social status. Therefore, this sentence is inaccurate and there is no research that demonstrates that.

We thank the reviewer for raising this point. To express the opinion and cite literatures more accurately, we improved the sentence in the 1st paragraph of Introduction as follows: “Impaired awareness of social competition has been documented in individuals with autism spectrum disorder (ASD)4,5, and reduced social interaction has been characterized in corresponding animal models6. Similarly, maladaptive responses to social status loss has been associated with patient depressive disorders7,8 and animal models of depression1,9”. The reviewer is right that no patient disease is causally related with social status, and only depression has been proposedly associated with change of social status7,8.

b. In the second paragraph of the introduction, the authors mention a scarcity of research papers with designs for food competition-based social hierarchy assays for mice. At least two such papers have been published in the past few years (DOIs https://doi.org/10.1038/s41586-

021-04000-5 and https://doi.org/10.1038/s41586-022-04507-5). The authors should acknowledge the existence of these and other assays and discuss how their work would be related. In the same paragraph, they also mention that existing assays suffer from "hierarchy instability" and "complex calculations" without showing any citations or details for these claims.

We thank the reviewer for raising this point. We acknowledged that there are some available food competitions to measure social hierarchy for mice. But relative to space competition, food competition tests have not been used so commonly and widely. No food competition paradigm has been accepted as generally as some space competition paradigms like tube test and warm spot test. To improve the language and scientific expression, we revised the sentences as follows: “Relative to space competition, food competition tests for mice have been designated and applied less commonly in animal studies despite its long history 28-30. Several issues could be thought to be the underlying limitations for the application of food competition paradigms. First, there are methodological issues in some of these approaches, such as long video recording duration and difficulty in analyzing animal’s behaviors during competitive physical interaction in videos, hindering their application by laboratories that cannot afford sophisticated equipment and analysis”. Corresponding citations have been updated (see paragraph 3 in the Introduction).

c. The authors say that their study is the first to demonstrate that female mice follow social ranks. This is not the first study to do so and the authors should acknowledge existing publications that have done the same (eg DOI https://doi.org/10.7554/eLife.71401).

We have followed the reviewer’s suggestion to increase citations regarding social ranking of female mice tested by competition paradigms, especially food competition paradigms (see paragraph 1 of section 3 in the Results; paragraph 4 in the Discussion).

(2) Related to problems with interpretation of data:

a. The authors showed the assay works for females and males in pairwise housing, but two mice don't make a hierarchy, as hierarchies require a minimum of three individuals. Therefore, whether the assay works for females caged in three is an important question that is unaddressed in this study and is a caveat. extended the competition assay to male mice that are housed in cages of three. It would be important to show whether the assay generalizes well for female mice with this three-animal housing as well as discuss the effect of using even bigger groups of mice on the results of the assay.

We thank the reviewer for raising questions related to the interpretation of data and giving us the insightful the suggestions. We agree that it is interesting and important to probe if FPCT works for a group of three female mice. Although social rankings of pairs of male and female mice were not significantly different (new Figure 2D-2F and 3F-3H), that of triads of male and female mice could be different. We have tested trads of male mice and found that the mice displayed an overall linear hierarchical ranking. We would like to use FPCT to investigate the rankings of trads of female mice and even bigger group of mice in the future. In the present manuscript we’d like to address the feasible application of the FPCT in smaller groups. In the Discussion, we add contents commenting group size effect on social competition tests (see paragraph 4 in the Discussion).

b. The authors claim that "test 2" of their assay helps assert the motivation of mice for social competition as in Figure 4E. This could simply be a readout of how strong the mice are (muscle mass). To claim that this is indeed related to motivation during the FPCT assay, the authors should show the correlation of this readout with the latency to push the block during the social competition task.

We appreciate the reviewer for raising this question. The dimensions establishing the social structures include physical and psychological factors. In the FPCT paradigm, the two contenders are separated so that physical factors are minimized in this context and psychological factors should play more important role in competition in comparison with previous reported food competition paradigms. Therefore, in the revised manuscript we consider to attribute the ranking results mainly to psychological factors, rather than only motivation which is just one of the numerous psychological factors (paragraph 3 of Discussion). Moreover, in the Discussion we point out that we could not exclude physical factors still participate in the determination of competitive outcomes since some of mice pairs pushed the block simultaneously (paragraph 3 of Discussion).

c.The authors mention that they are interested to understand which factors lead to the outcome of the competition such as age, sex, physical strength, training level, and intensity of psychological motivation. However, in all their runs of the assay, they always matched these variables between the competitors. They should clarify that they were instead controlling for these variables. Another thing to note here is that while they controlled the body mass of the animals, that isn't the same as physical strength, as a lighter mouse can have more muscle mass than a heavier mouse. They should either specify this limitation or quantify the additional metric of "muscle mass" which is a much better proxy for physical strength. Thus, the claim that the outcome of the competition is solely affected by motivation is not convincing since they didn't rule out the others such as quantifying the rate of learning during training and strength.

We thank the reviewer for addressing this question. As our response to the question in (c), we acknowledge that it is not accurate to ascribe the outcomes of FPCT to psychological motivation. In the revised manuscript, the dimensions of contributing factors to the outcomes of FPCT have been simplified to physical and psychological factors. We consider that the psychological factor could be the main driver of mice participating in FPCT (see paragraph 3 of Discussion).

d. In the discussion, the authors mention that their task only requires a single day of food deprivation (the day before the first trial) while other assays suffer from a continued food deprivation protocol. However, the authors also use 10g per cage as the amount of food instead of giving them ad libitum access. Limited food is a food deprivation method. Thus, this is an inaccurate claim.

We thank the reviewer for raising this point. We have clarified the requirement of food restriction for FPCT in the revision. The mice were deprived of food for 24 hours while water consumption remained normally to enhance the appeal of the food pellet to the mice. Then, after 24 hours of food deprivation, each cage of mice was given 10 g of food every morning to meet their daily food requirements until the end of the test (see FPCT procedure section in Methods and materials).

e.In the second section of the results, the authors run their assay with female mice that are housed in cages of two. This section suffers from the same limitations as the first and can be improved by showing the training data, correlations of competition outcome with "motivation" and ruling out the other factors that could contribute to the outcome. Further, the authors saying that their FPCT assay is enough to show that female mice follow a social hierarchy by itself is a weak claim. They should instead include their cross-validation with the others to strengthen it.

We appreciate the reviewer for raising this question. We have taken the reviewer’s suggestion to show the training data (Figures 1E, 2A and 3A). As the factors contributing to the outcomes of FPCT are diverse, we’d like not to control and determine the exact factor in the current manuscript. We agree with the reviewer that cross-validation with different paradigms is suggested for the studies to rank social hierarchy as the ranking results could be variable with tasks, procedures and operations.

f.  In the last paragraph of the introduction, the authors mention how their assay involves "peaceful competition" since the mice are not in direct contact and hence cannot exhibit aggression. The authors do not address the limitation that a lack of physical contact actually makes the assay less ethological. Further, since the mice are housed in groups of two and three, it is not guaranteed that the mice will not be aggressive during their time in the home cage, which could affect their behavior during the competition assay. Whether the assay causes more aggression in the cage due to the lack of physical contact during the competition is not addressed in this study.

We thank the reviewer for raising this point. Diverse factors affect the outcomes of a food competition test, some of which belong to psychological factors and others belong to physical factors. We agree that a lack of physical contact makes the assay less naturally ethological. However, when the social statuses have been established during habituation housing a group of mice for enough time, the win/lose outcomes in the FPCT could be a readout of the expression of social statuses since the mice cannot exhibit aggression in the test. We have revised the Introduction and Discussion (paragraph 3 of Discussion). Thank you.

(3) Related to lack of methodological rigor and rationale clarity:

a. In the first section of the results, the authors run their assay with male mice that are housed in cages of two. While the data that they display is promising, we do not see how mice change behavior across days of training and how that relates to the outcome of the competition. It would be valuable to also show the training data for the mice, answering questions related to competency and any inter-animal variabilities prior to rank assessment. Plotting the training data across all days would be helpful for the other parts of the results as well. This is especially important because the methods mention that mice are trained until they get to the criterium, so this means that different individuals get different amounts of training.

We appreciate the reviewer for addressing the importance of showing training data. We have taken the reviewer’s suggestion and shown the training data (Figures 1E, 2A and 3A).

b.  It is unclear why the assay was run only once per mouse pair per day since most protocols for the tube test involve multiple repetitions each day while alternating the side from which the mice enter. The authors should address whether a single trial per day is enough to show consistent results and that it wouldn't vary with more.

We suggest to run the FPCT once or twice per mouse per day under conditions of mild food restriction, training and test procedures in this manuscript. Frequent tests might make the mice’s interest in the food pellet gradually diminished because the food supply was not fully deprived. According to our data, the outcomes of FPCT in 4 consecutive days were overall stable.

c.  In the results the authors say that they "raised 3 male mice" which may be incorrect because they report in the methods buying the mice buy mice and they housed all their mice for only three days before running the assay which might be too little for the hierarchy to stabilize. The authors should comment on what was the range of the cohabitation across different cages and whether it had an impact on the results.

According to our experiments, housing the mice for 3 days is enough to establish a mice social colony with relative stable status structure. Prolonged housing may produce either similar, stabler or more dynamic social colony.

d. There are also some formatting and/or convention issues in the results. The first figure callout in the results is for Figure 4 instead of Figure 1 (which is the standard). This is because the authors do not explain how the mice are trained for the task in the results section and show limited data about the training of the task. Not showing comprehensive training data would make replication of this study very difficult.

We appreciate the reviewer for raising this question. We have re-arranged the figures. The new arrangement of figures started with schematic drawing of FPCT procedure and training data (Figure 1).

e. The authors don't report the exact p-values in the figures

We reported the difference level in the figures in the revised manuscript. Thank you.

4. The writing of the manuscript suffers from a lack of clarity in most sections of the manuscript.

Here are several examples that are critical:

a. In the title and abstract, it isn't clear what the authors mean by "stereotype". It could be a behavior during the competition, or that the social ranks across assays are correlated or that the rank for the new assay is consistent across days.

b. There are several instances where the authors anthropomorphize mice using human features such as "urbanization" and "society" which are not established factors affecting mouse hierarchy. This further extends to anthropomorphizing mice in ways that are not standard such as an animal being "timid" or "bold" which would be hard to measure in mice, if not impossible.

c. Across the social dominance literature, relative social rank is described using more general "dominant" and "subordinate" titles instead of "superior" and "inferior" that are sometimes used in the manuscript. The authors should follow the standard language so that readers understand.

d.  In the third paragraph of the introduction, the authors say "Thus, it is more likely expected that different paradigms to weigh the social competency and status may lead to diverse readouts, given that competitive factors are included in competition paradigms." This sentence suffers from multiple syntax errors thereby reducing clarity

e. There are several typos in the manuscript such as using "dominate" instead of "dominant", "grades" instead of "outcomes" and "forth" instead of "fourth", to give a few examples.

We thank the reviewer for careful reading of the manuscript and very helpful comments. We have taken the above suggestions and improved the writing of the manuscript. For examples, "stereotype" was replaced by “stability”, mice "society" was expressed by "colony", the sentence “Thus, it is more.... in competition paradigms” has been deleted.

Reviewer #3 (Recommendations for the authors):

(1) The justification for the design of this new test paradigm is unclear. In the abstract, you state that the field needs a reliable, valid, and easily executable test. Your test provides this, as you state, but how is it better than the tube test? Does the tube test suffer from taskspecific win-or-lose outcomes? Can you provide evidence for this? The nature methods protocol for the tube test (https://doi.org/10.1038/s41596-018-0116-4) "strongly suggest using more than two dominance measures, for example, by also carrying out the warm spot test, or territory urine marking or ultrasonic courtship vocalization assays." This would suggest that results from the tube test can be task-specific, but I am not convinced that you have demonstrated that results from your food competition test are not task-specific. Indeed, by your title, one must run multiple tests.

This same problem is apparent in the introduction. In the second paragraph, there is a discussion of the tube test, warm spot test, and food competition tests. What is the problem with these tests?

I believe that social dominance relationships are complex and dynamic social relationships indicating who has priority access to a resource between multiple animals that live together. In these living situations, several resources can often be capitalized competed over-for example, space, food, mates, temperature, etc. Currently, we have tests to measure space via the tube test or urine marking, mates via ultrasonic vocalization, temperature via warm spot test, and food via food competition assays. The tube test, urine marking assay, and ultrasonic vocalization test have been demonstrated to be reliable, valid, and easily executable. However, the food competition assays are often difficult to execute because it is difficult to interpret the dominant behaviors and aggressive behaviors like bite wounding can occur during the test. Here, you present a new food competition assay to address these issues and show that it can be used in conjunction with other assays to measure social dominance across multiple resources easily. In doing so, you revealed that many same-sex groups of C57 mice have a stereotypic pattern of dominance behavior when competing across multiple types of resources: space, temperature, and food.

I ask that you please rebut if you disagree with me, and adjust your abstract, introduction, and discussion accordingly.

We thank the reviewer for all the constructive comments. We have adjusted the Abstract, Introduction and Discussion of the manuscript.

We recognize and appreciate the valuable tube test, warm spot test and many other competition tests, including food competitions. Tube test and warm spot test are space competition tasks. Relative to space competition, food competition tests for mice have been designated and applied less commonly in animal studies. Several issues (such as methodological issue, aggressive behaviors occurring in competition, and prolonged food deprivation) could be thought to be the underlying limitations of the application of food competition paradigms (paragraph 3 in the Introduction). Therefore, we clarify that the justification for the design of FPCT was “to have a new choice of food competition paradigm for mice, and to facilitate the exposure of psychological aspects contributing to the winning/losing outcomes in competitions” (last paragraph in the Introduction).

FPCT is different from tube test and warm spot test at least in two ways. FPCT is food completion task where the mice need no physical contact during competition, while tube test and WST are space competition tasks where the mice need direct physical contact during competition. Therefore, we expected inconsistent evaluation results of competitiveness and rankings if we compared FPCT with typically available competition paradigms—tube test and WST (last paragraph in the Introduction).

(2)  The design of the test needs to be described before the results. You can either move the methods section before the results or add a paragraph in the introduction to better describe the test. Here, you can also reference Figures 1 through 3 so that the figures are presented in the order of which they are mentioned in the paper. (It is very confusing that the first reference to a figure is Figure 4, when it should be Figure 1).

We appreciate the reviewer for raising this point and giving us suggestions. We have added a new section (section 1) in the Results. In the revised manuscript, the figures in the Results start with Figure 1 which shows schematic drawing of FPCT procedure, training data and some test results (Figure 1).

(3)  The sentence describing Figure 4H. You argue that this shows that the mice are well and equally trained. It also shows that they have the same motivation or preference for the food.

We appreciate the reviewer for this helpful comment. Data in previous Figures 4H and 5I have been presented as new Figures 2A and 3A, respectively, of revised manuscript. These retrospect analysis of training data displayed similar training level of food-getting and craving state for food (Sections 2 and 3 in the Results).

(4)  "Social ranking of multiple cagemate mice using FPCT, tube test and WST"

Here, you claim that "comparison of inter-task consistency revealed that the ranks evaluated by FPCT, tube test and WST did not differ from each other...Figure 6K." Okay, however, it is important to discuss the three cases when there wasn't consistency between the tests! Figure 6E-G.

We appreciate the reviewer for raising this point. In the revised manuscript, we add description and discussion of inconsistent part of the different test paradigms (paragraph 2 in the section 3 of the Result, last 2 sentences of paragraph 4 in the Discussion)

(5)  Replace all instances of "gender" with "sex". Animals do not have a gender.

(6)  Adjust the strain of the mice to C57BL/6JNifdc.

We have replaced "gender" with "sex" and “C57BL/6J” with “C57BL/6JNifdc”. Thank you for your careful correction.

(7)  What is the justification for running the warm spot test for one day and the other tests for four days?

From the consecutive FPCT and tube test, we already knew that the ranking results were overall stable. This stability was still observed in the day of warm spot test. A bad point for frequent warm spot test is that mice get much stress due to exposure in ice-cold environment. Therefore, we terminated the competition test after only one trial of warm spot test.

(8)  Grammar

The second sentence of the abstract: ...recognized as a valuable...

Results, sentence after "...was observed (Figure 4G)." it should be "Fourth"

We have corrected these and other grammar errors. We appreciate the reviewers for very careful review and all helpful comments.

Author Response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review): 

The authors survey the ultrastructural organization of glutamatergic synapses by cryo-ET and image processing tools using two complementary experimental approaches. The first approach employs so-called "ultra-fresh" preparations of brain homogenates from a knock-in mouse expressing a GFP-tagged version of PSD-95, allowing Peukes and colleagues to specifically target excitatory glutamatergic synapses. In the second approach, direct in-tissue (using cortical and hippocampal regions) targeting of the glutamatergic synapses employing the same mouse model is presented. In order to ascertain whether the isolation procedure causes any significant changes in the ultrastructural organization (and possibly synaptic macromolecular organization) the authors compare their findings using both of these approaches. The quantitation of the synaptic cleft height reveals an unexpected variability, while the STA analysis of the ionotropic receptors provides insights into their distribution with respect to the synaptic cleft.

The main novelty of this study lies in the continuous claims by the authors that the sample preservation methods developed here are superior to any others previously used. This leads them as well to systematically downplay or directly ignore a substantial body of previous cryo-ET studies of synaptic structure. Without comparisons with the cryo-ET literature, it is very hard to judge the impact of this work in the field. Furthermore, the data does not show any better preservation in the so-called "ultra-fresh" preparation than in the literature, perhaps to the contrary as synapses with strangely elongated vesicles are often seen. Such synapses have been regularly discarded for further analysis in previous synaptosome studies (e.g. Martinez-Sanchez 2021). Whilst the targeting approach using a fluorescent PSD95 marker is novel and seems sufficiently precise, the authors use a somewhat outdated approach (cryo-sectioning) to generate in-tissue tomograms of poor quality. To what extent such tomograms can be interpreted in molecular terms is highly questionable. The authors also don't discuss the physiological influence of 20% dextran used for high-pressure freezing of these "very native" specimens.

Lastly, a large part of the paper is devoted to image analysis of the PSD which is not convincing (including a somewhat forced comparison with the fixed and heavy-metal staining room temperature approach). Despite being a technically challenging study, the results fall short of expectations. 

Our manuscript contains a discussion of both conventional EM and cryoET of synapses. We apologise if we have omitted referencing or discussing any earlier cryoET work. This was certainly not our intention, and we include a more complete discussion of published cryoET work on synapses in our revised manuscript.

The reviewer is concerned that the synaptic vesicles in some synapse tomograms are “stretched” and that this may reflect poor preservation.  We would like to point out that such non-spherical synaptic vesicles have also been previously reported in cryoET of primary neurons grown on EM grids (Tao et al., J. Neuro, 2018). Indeed, there is no reason per se to suppose synaptic vesicles are always spherical and there are many diverse families of proteins expressed at the synapse that shape membrane curvature (BAR domain proteins, synaptotagmin, epsins, endophilins and others). We will add further discussion of this issue in the revised manuscript.

The reviewer regards ‘cryo-sectioning’ as outdated and cryoET data from these preparations as “poor quality”. We respectfully disagree. Preparing brain tissues for cryoET is generally considered to be challenging. The first successful demonstration of preparing such samples was before the advent of the cryoEM resolution revolution (with electron counting detectors) by Zuber et al (Proc. Natl. Acad. Sci.,2005) preparing cryo-sections/CEMOVIS of in vitro brain cultures. We followed this technique to prepare tissue cryo-sections for cryoET in our manuscript. Recently, cryoFIB-SEM liftout has been developed as an alternative method to prepare tissue samples for cryoET (Mahamid et al., J. Struct. Biol., 2015) and only more recently this method became available to more laboratories. Both techniques introduce damage as has been described (Han et al., J. Microsc., 2008; Lucas et al., Proc. Natl. Acad. Sci., 2023). Importantly no like-for-like, quantitative comparison of these two methodologies has yet been performed. We have recently demonstrated that the molecular structure of amyloid fibrils within human brain is preserved down to the protein fold level in samples prepared by cryo-sectioning (Gilbert et al., Nature, 2024). We will add further detail on the process by which we excluded poor quality tomograms from our analysis, which we described in detail in our methods section.

The reviewer asks what the physiological effect is of adding 20% w/v ~40,000 Da dextran? This is a reasonable concern since this could in principle exert osmotic pressure on the tissue sample. While we did not investigate this ourselves, earlier studies have (Zuber et al, 2005) showing cell membranes were not damaged by and did not have any detectable effect on cell structure in the presence of this concentration of dextran.

The reviewer is not convinced by our analysis of the apparent molecular density of macromolecules in the postsynaptic compartment that in conventional EM is called the postsynaptic density. However, the reviewer provides no reasoning for this assessment nor alternative approaches that could be attempted. We would like to add that we have tested multiple different approaches to objectively measure molecular crowding in cryoET data, that give comparable results. We believe that our conclusion – that we do not observe an increased molecular density conserved at the postsynaptic membrane, and that the PSD that we and others observed by conventional EM does not correspond to a region of increased molecular density - is well supported by our data.  We and the other reviewers consider this an important and novel observation.

Reviewer #2 (Public review): 

Summary: 

The authors set out to visualize the molecular architecture of the adult forebrain glutamatergic synapses in a near-native state. To this end, they use a rapid workflow to extract and plunge-freeze mouse synapses for cryo-electron tomography. In addition, the authors use knockin mice expression PSD95-GFP in order to perform correlated light and electron microscopy to clearly identify pre- and synaptic membranes. By thorough quantification of tomograms from plunge- and high-pressure frozen samples, the authors show that the previously reported 'post-synaptic density' does not occur at high frequency and therefore not a defining feature of a glutamatergic synapse.

Subsequently, the authors are able to reproduce the frequency of post-synaptic density when preparing conventional electron microscopy samples, thus indicating that density prevalence is an artifact of sample preparation. The authors go on to describe the arrangement of cytoskeletal components, membraneous compartments, and ionotropic receptor clusters across synapses.

Demonstrating that the frequency of the post-synaptic density in prior work is likely an artifact and not a defining feature of glutamatergic synapses is significant. The descriptions of distributions and morphologies of proteins and membranes in this work may serve as a basis for the future of investigation for readers interested in these features.

Strengths: 

The authors perform a rigorous quantification of the molecular density profiles across synapses to determine the frequency of the post-synaptic density. They prepare samples using two cryogenic electron microscopy sample preparation methods, as well as one set of samples using conventional electron microscopy methods. The authors can reproduce previous reports of the frequency of the post-synaptic density by conventional sample preparation, but not by either of the cryogenic methods, thus strongly supporting their claim. 

We thank the reviewer for their generous assessment of our manuscript.

Reviewer #3 (Public review): 

Summary: 

The authors use cryo-electron tomography to thoroughly investigate the complexity of purified, excitatory synapses. They make several major interesting discoveries: polyhedral vesicles that have not been observed before in neurons; analysis of the intermembrane distance, and a link to potentiation, essentially updating distances reported from plastic-embedded specimen; and find that the postsynaptic density does not appear as a dense accumulation of proteins in all vitrified samples (less than half), a feature which served as a hallmark feature to identify excitatory plastic-embedded synapses. 

Strengths: 

(1)The presented work is thorough: the authors compare purified, endogenously labeled synapses to wild-type synapses to exclude artifacts that could arise through the homogenation step, and, in addition, analyse plastic embedded, stained synapses prepared using the same quick workflow, to ensure their findings have not been caused by way of purification of the synapses. Interestingly, the 'thick lines of PSD' are evident in most of their stained synapses.

(2)I commend the authors on the exceptional technical achievement of preparing frozen specimens from a mouse within two minutes.

(3)The approaches highlighted here can be used in other fields studying cell-cell junctions.

(4)The tomograms will be deposited upon publication which will enable neurobiologists and researchers from other fields to carry on data evaluation in their field of expertise since tomography is still a specialized skill and they collected and reconstructed over 100 excellent tomograms of synapses, which generates a wealth of information to be also used in future studies.

(5) The authors have identified ionotropic receptor positions and that they are linked to actin filaments, and appear to be associated with membrane and other cytosolic scaffolds, which is highly exciting.

(6) The authors achieved their aims to study neuronal excitatory synapses in great detail, were thorough in their experiments, and made multiple fascinating discoveries. They challenge dogmas that have been in place for decades and highlight the benefit of implementing and developing new methods to carefully understand the underlying molecular machines of synapses.

Weaknesses: 

The authors show informative segmentations in their figures but none have been overlayed with any of the tomograms in the submitted videos. It would be helpful for data evaluation to a broad audience to be able to view these together as videos to study these tomograms and extract more information. Deposition of segmentations associated with the tomgrams would be tremendously helpful to Neurobiologists, cryo-ET method developers, and others to push the boundaries.

Impact on community: 

The findings presented by Peukes et al. pertaining to synapse biology change dogmas about the fundamental understanding of synaptic ultrastructure. The work presented by the authors, particularly the associated change of intermembrane distance with potentiation and the distinct appearance of the PSD as an irregular amorphous 'cloud' will provide food for thought and an incentive for more analysis and additional studies, as will the discovery of large membranous and cytosolic protein complexes linked to ionotropic receptors within and outside of the synaptic cleft, which are ripe for investigation. The findings and tomograms available will carry far in the synapse fields and the approach and methods will move other fields outside of neurobiology forward. The method and impactful results of preparing cryogenic, unlabelled, unstained, near-native synapses may enable the study of how synapses function at high resolution in the future.

We thank the reviewer for their supportive assessment of our manuscript.  We thank the reviewer for suggesting overlaying segmentations with videos of the raw tomographic volumes. We will include this in our revised manuscript.

Reviewer #1 (Recommendations for the authors): 

Major comments: 

(1) The previous literature on synaptic cryo-ET studies is systematically ignored. The results presented here (and their novelty) must be compared directly with this body of work, rather than with classical EM.

Our submitted manuscript included a 3-paragraph discussion of earlier synaptic cryoET studies, albeit we apologize that a seminal citation was missing, which we have corrected in our revised manuscript. We have now also included an additional brief discussion related to several more recent cryoET studies (see citations below) that were published after our pre-print was first deposited in 2021.

(1) Held, R.G., Liang, J., and Brunger, A.T. (2024). Nanoscale architecture of synaptic vesicles and scaffolding complexes revealed by cryo-electron tomography. Proc. Natl. Acad. Sci. 121, e2403136121. https://doi.org/10.1073/pnas.2403136121.

(2) Held, R.G., Liang, J., Esquivies, L., Khan, Y.A., Wang, C., Azubel, M., and Brunger, A.T. (2024). In-Situ Structure and Topography of AMPA Receptor Scaffolding Complexes Visualized by CryoET. bioRxiv, 2024.10.19.619226. https://doi.org/10.1101/2024.10.19.619226.

(3)Matsui, A., Spangler, C., Elferich, J., Shiozaki, M., Jean, N., Zhao, X., Qin, M., Zhong, H., Yu, Z., and Gouaux, E. (2024). Cryo-electron tomographic investigation of native hippocampal glutamatergic synapses. eLife 13, RP98458. https://doi.org/10.7554/elife.98458.

(4)Glynn, C., Smith, J.L.R., Case, M., Csöndör, R., Katsini, A., Sanita, M.E., Glen, T.S., Pennington, A., and Grange, M. (2024). Charting the molecular landscape of neuronal organisation within the hippocampus using cryo electron tomography. bioRxiv, 2024.10.14.617844. https://doi.org/10.1101/2024.10.14.617844.

We discuss the above papers in our revised manuscript with the following:

“Since submission of our manuscript, several reports of synapse cryoET from within cultured primary neurons (Held et al., 2024a, 2024b)  and mouse brain(Glynn et al., 2024; Matsui et al., 2024) were prepared by cryoFIB-milling. These new datasets are largely consistent with the data reported here. CryoFIB-SEM has the advantage of overcoming the local knife damage caused by cryo-sectioning but introduces amorphization across the whole sample that diminishes the information content (Al-Amoudi et al., 2005; Lovatt et al., 2022; Lucas and Grigorieff, 2023). We have recently shown cryoET data is capable of revealing subnanometer resolution in-tissue protein structure from vitreous cryo-sections (Gilbert et al., 2024) and near-atomic structures within cryo-sections has recently been demonstrated (Elferich et al., 2025).”

Although there is variation between individual synapses, PSDs are clearly visible in several previous cryo-ET studies (even if it's not as striking as in heavy-metal stained samples). In fact, although the contrast of the images is generally poor, PSDs are also visible in several examples shown in Figure 1 - Supplement 3. Not being able to detect them seems more of a problem of the workflow used here than of missing features. The authors should also discuss why heavy-metal stains would accumulate on a non-existing structure (PSD) in conventional EM.

We agree that apparent higher molecular density can be observed in example tomographic data of earlier cryoET studies. We also report individual examples of similar synapses in our dataset. A key strength of our approach is that we have assessed the molecular architecture of large numbers of adult brain synapses acquired by an unbiased approach (solely guided by PSD95 cryoCLEM), which indicate that a higher molecular density proximal to the postsynaptic membrane is not a conserved feature of glutamatergic synapses in the adult brain. There is no rationale for our cryoCLEM approach being a ‘problem of the workflow’.

The reviewer misunderstands the weaknesses of conventional/room temperature EM workflows (including resin-embedding and freeze substitution). It is unavoidable that most proteins are damaged by denaturation and/or washed away by washing samples in organic solvents (methanol/acetone that directly denature most proteins) during tissue preparation for conventional EM. It is therefore conceivable that in such preparations a relative increase in contrast proximal to the postsynaptic membrane (‘PSD’) would appear if cytoplasmic proteins were washed away during these harsh organic solved washing steps, leaving only those denatured proteins that are tethered to the postsynaptic membrane. It is not that the PSD is absent in cryoEM, rather that this difference in molecular crowding is not evident when tissues are imaged directly by cryoEM and have not undergone the harsh sample preparation required for conventional/room temperature EM.

(2) Whether the synapses examined here are in a more physiological state than those analyzed in other papers remains absolutely unclear. For example, the quality of the tomographic slice shown in Figure 1C is poor, with the majority of synaptic vesicles looking suspiciously elongated. 

We addressed this in our public reviews.

(3) How were actin filaments segmented and quantified (e.g. for Fig 1E)? Apart from actin, can the authors show some examples of other macromolecular complexes (e.g. ribosomes) that they are able to identify in synapses (based on the info in supplementary tables)? Also, the mapping of glutamatergic receptors is not convincing, as the molecules were picked manually. To analyze their distribution, they should be mapped as comprehensively as possible by e.g. template matching.

Actin filaments identified by ~7 nm diameter with ~70° branch points were manually segmented in IMOD. The number of filaments was counted per postsynaptic compartment. We have amended the methods section to include this description.

“In the PoSM, F-actin formed a network with ~70° branch points (Figure 1–figure supplement 1C) likely formed by Arp2/3, as expected(Pizarro-Cerdá 2017,Fäßler 2020) . Putative filament copy number in the PoSM was estimated by manual segmentation in IMOD.” Manual picking was validated by the quality of the subtomogram average, which although only reached modest resolution (25 Å) is consistent with the identification of ionotropic glutamate receptors.

(4) In the section "Synaptic organelles" the authors should provide some general information on the average number and size of synaptic vesicles (for the in-tissue tomograms).

We have provided this information in the methods section:

“The average diameter of synaptic vesicles was 40.2 nm and the minimum and maximum dimensions ranged from 20 to 57.8 nm, measured from the outside of the vesicle that included ellipsoidal synaptic vesicles similar to those previously reported (Tao et al., 2018).” A detailed survey of the presynaptic compartment, including the number of presynaptic vesicles was not the focus of our manuscript. We have deposited all tomograms from our dataset for any further data mining.

Can the "flat tubular membranes compartments" be attributed to ER? The angular vesicles certainly have a typical ER appearance, as such morphology has been seen in several cryo-ET studies of neuronal and non-neuronal cells.

In neuronal cells we regard it as unsafe to describe an intracellular organelle as being endoplasmic reticulum on the basis of morphology alone (eg. Smooth ER described widely in conventional EM) because of the apparent diversity of distinct organelles. As described in our methods section, we could have confidence that a membrane compartment is ER when we observe ribosomes tethered to the membrane. In instances where flat/tubular membranes did not have associated ribosomes, we take the cautious view that there is not sufficient evidence to define these as ER.

Importantly, polyhedral vesicles were distinct from the flat/tubular membranes that resembled ER and are at present organelles of unknown identity. It will be important in future experiments to determine what are the protein constituents of these distinct organelle types to understand both their functions and how these distinct membrane architectures are assembled.

Therefore, the sentences in lines 198-199 are simply wrong. Additionally, features of even higher membrane curvature are common in the ER (e.g. Collado et al., Dev Cell 2019). 

We thank the reviewer for bringing our attention to this excellent paper (Collado et al.). We agree that the sentence describing the curvature being higher than all other membranes except mitochondrial cristae is wrong. We have removed this sentence in the revised manuscript.

(5)The quality of the tomographic data for the in-tissue sample is low, likely due to cryo-sectioning-induced artifacts, as extensively documented in the literature. Additionally, the authors used 20% dextran as cryo-protectant for high-pressure freezing, which contrasts with statements like those in lines 342-344. Given that several publications describing the in-tissue targeting of synapses (e.g. from Eric Gouaux's lab) are available, the quality of the tomographic data presented in this work is underwhelming and limits the conclusions that can be drawn, not providing a solid basis for future studies of in-tissue synapse targeting. However, the complete workflow (excluding the sectioning part) can be adapted for a cryo-FIB approach. The authors should discuss the limitations of their approach. 

Our manuscript preprint was deposited in the Biorxiv several years before Matsui/Gouaux’s recent ELife paper that reported a novel work-flow for in-tissue cryoET. It is difficult to directly compare data from our and Matsui/Gouaux’s approach because the latter reported a dataset of only 3 tomograms. Note also that Matsui/Gouaux followed our approach of using 20% dextran 40,000 as a cryo-preservative. The use of 20% dextran 40,000 as a cryo-protectant was first established by Zuber et al., 2005 (PMID: 16354833) and shown avoid hyper-osmotic pressure and cell membrane rupture. However, Matsui/Gouaux additionally included 5% sucrose in their cryoprotectant. We did not include sucrose as cryo-preservative because this exerts osmotic pressure and was not necessary to achieve vitreous tissues in our workflow.

Before high-pressure freezing, Matsui/Gouaux also incubated tissue slices in a HEPES-buffered artificial cerebrospinal fluid (that included 2 mM CaCl2 but did not include glucose as an energy source) for 1 h at room temperature to label AMPA receptors with Fab fragment-Au conjugates. Under these conditions, neurons can elicit both physiological and excitotoxic action potentials (even though AMPARs were themselves antagonised with ZK-200775). The absence of glucose is a concern, and it is unclear to what extent tissue viability is affected by this incubation step. In contrast, we chose to use an NMDG-based artificial cerebrospinal fluid for slice preparation and high-pressure freezing that is a well-established method for preserving neuronal viability (Ting et al., 2018).

We addressed the supposed limitations of cryo-sectioning versus cryoFIB-SEM in our public response. In particular, we have recently shown that cryo-sectioning produced a  subnanometer resolution in-tissue structure of a protein, that has so far only been achieved for ribosome within cryoFIB-SEM sample preparations. A discussion of cryo-sectioning versus cryoFIB-SEM must be informed by new data that directly compares these methods, which is not the subject of our eLife paper. We also cite a recent preprint directly comparing cryoFIB-milled lamellae with cryo-sections and showing that near atomic resolution structures can also be obtained from the latter sample preparations (Elferich et al., 2025).

(6) The authors show (in Supplementary) putative tethers connecting SV and the plasma membrane. Is it possible to improve the image quality (e.g. some sort of filtering or denoising) so that the tethers appear more obvious? Can the authors observe connectors linking synaptic vesicles? 

We have tested multiple iterative reconstruction and denoising approaches, including SIRT and noise2noise filtering in Isonet. We observed instances of macromolecular complexes linking one synaptic vesicle with another. However, there was no question we sought to answer by performing a quantitative analysis of these linkers.

(7) Figure 4F is missing. 

Thank you for spotting this omission. We have corrected this in the revised manuscript.

(8) Most quantifications lack statistical analyses. These need to be included, and only statistically significant findings should be discussed. Terms like "significantly" (e.g. Line 144) should only be used in these cases.

We used the term ‘significantly’ in the results section (line 143 and line 166 in revised text, we cite figure 1H and 2F showing analyses in which we have in fact performed statistical tests (t-tests with Bonferroni correction) comparing the voxel intensities in regions of the cytoplasm that are proximal versus distal to the postsynaptic membrane. We have amended the main text to include the details of the statistical test that we performed. Also, we neglected to include a description of the statistical test in line 241, which cites Figure 3G. We have corrected this in the revised text.

Minor comments: 

(1) Can the authors comment on why only 1-2 grids are prepared per mouse brain (in M&M -section)?

We prepared only two grids in order to have prepared samples within 2 minutes, to limit deterioration of the sample.

(2) Figure 1 Supplement 2 and its legend are confusing (averaging of non-aligned versus aligned post-synaptic membrane). Can the authors describe more clearly their molecular density profile analysis?

We apologise that this figure legend was insufficient. We have included a detailed description of our molecular density profile analysis in the methods section entitled ‘Molecular density profile analysis’. In the revised manuscript we have now also included a citation to this methods section in Figure – figure 1 supplement 2 legend.

(3) Please clarify with higher precision the areas were recorded in relation to the fluorescent spots (e.g. Figures 3A-C).

We have included a white rectangular annotation in the cryoCLEM inset panels of Figures 3A-C to indicate the field of view of each corresponding tomographic slice. This shows that PSD95-GFP puncta localise to the postsynaptic compartments in each tomogram.

(4) Figure 4 Supplement 2D is not clear: the connection between receptors and actin should be shown in a segmentation.

We agree with the reviewer. A ‘connection’ is not clear, which is expected because the cytoplasmic domain of ionotropic glutamate receptor subunits is composed of a non-globular/intrinsically disordered sequence. We have amended our description of the proximity of actin cytoskeleton to ionotropic glutamate receptor clusters in the main text replacing “associated with” to “adjacent to”.

(5) Line 341: the reference is referred to by a number (56) at the end of the sentence, rather than by name.

Good spot. We have corrected this in the revised manuscript.

(6) Line 968: tomograms is misspelled. 

Good spot. We have corrected this error (line 1018 in our revised manuscript).

Reviewer #2 (Recommendations for the authors): 

(1) On page 11: "The position of (i)onotropic receptor...". 

Good spot. We have corrected this.

(2) On page 13: "Slightly higher relative molecular density..." this line ends with a citation to reference '56', but the works cited are not numbered.

Good spot. We have corrected this in the revised manuscript.

(3) On page 46: "as described in (69)..." the works cited are not numbered. 

Good spot. We have corrected this in the revised manuscript.

Reviewer #3 (Recommendations for the authors): <br /> (1) The title does not do the work justice. The authors make many exciting discoveries, e.g. PSD appearance, new polyhedral vesicles, ionotropic receptor positions, and intermembrane distance changes even within the synaptic cleft, but title their manuscript "The molecular infrastructure of glutamatergic synapses in the mammalian forebrain". It is also a bit misleading, since one would have expected more molecular detail and molecular maps as part of the work, so the authors may think about updating the title to reflect their exciting work. 

We thank the reviewer for recognising the exciting discoveries in our manuscript. Summarising all these in a title is challenging. We intend ‘molecular infrastructure’ to mean a structure composed of many molecules including proteins (by analogy ‘transport infrastructure’ is composed of many roads, ports and train lines).

(2) It would be in the spirit of eLife and open science if the authors could submit their segmentations alongside the tomographic data to either EMPIAR or pdb-dev (if they accept it) or the new CZII cryoET data portal for neurobiologists, method developers, and others to use. 

We agree with the reviewer. We have deposited in subtomogram averaged map of AMPA receptor in EMDB, and all tilt series and 4x binned tomographic reconstructions described in our manuscript (figure 1- table1 and figure 2 -table 2), together with segmentations in EMPIAR.  

(3) Methods: the authors establish an exciting new workflow to get from living mice to frozen specimens within 2 minutes and perform many unique analyses that would be useful to different fields. Their methods section overall is well described and contains criteria and details that should allow others to apply experiments to their scientific problems. However, it would be very helpful to expand on the methods in the 'annotation and analysis [...]' and "Subtomogram averaging" sections, to at least in short describe the steps without having to embark on a reference journey for each method and generally provide more detail. For the annotation section, the software used for annotation is not listed. Table 1 only contains the list of the counts of organelles etc. identified in each tomogram, no processing details. 

We have revised the methods section ‘annotation and analysis’ including software used (IMOD). We have also included a slightly more detailed description of subtomogram averaging. We did not include ‘processing details’ because there are none - identification of constituents in each tomogram was carried out manually, as described in the methods section.

(4) Some of the tomograms submitted as videos may have slipped through as an early version since they appear to be originating from not perfectly aligned tiltseries; vesicles and membranes can be observed 'rubberbanding'. The authors should go through and check their videos. 

We thank the referee for suggesting we double check our tomogram videos. All movies are representative tomographic reconstructions from ultra-fresh synapse preparations (Figure 1 – videos 1-7) and synapses in tissue cryo-sections (Figure 2 – videos 1-2). We have double checked that the videos correspond to tomograms that were aligned as good as possible. In general, tissue cryo-section tomograms reconstructed less well than ultra-fresh synapse tomograms, which limits the information content of these data, as expected. Consequently, the reconstructions shown in these videos were all reconstructed as best we could (testing multiple approaches in IMOD, and more recent software packages, eg. AreTomo). While we think it is important to share all tomograms, regardless of quality, we were careful to exclude tomograms for analysis that did not contain sufficient information for analysis (as described in the methods section).

Minor suggestions: 

(1) Page 13, line 341, reference 56, but references are not numbered. Please update.

Good spot. We have corrected this in the revised manuscript.

(2) Page 33, line 746, the figure legend is not referencing the correct figure panels G-K should be I-K;

We have amended the Figure 3 legend to “(G-K) Snapshots and quantification of membrane remodeling within glutamatergic synapses”.

(3) Page 33, line 750; reads 'same as E', but should be 'same as G'. 

Good spot. We have corrected this in the revised manuscript.

(4) Page 35, Figure 4: Please use more labels: Figure 4B: it would be helpful to use different colors for each view and match to the tomogram - then non-experts could easily relate the projections and real data; Figure 4C: please label domains; Figure 4F: the figure panel got lost. 

This is an interesting idea. While our subtomgram average of 2522 subvolumes provided decent evidence that these are ionotropic receptors, we are reluctant to label specific putative domains of individual subvolumes in the raw tomographic slice because the resolution of the raw tomogram (particularly in the Z-direction) is worse and may not be sufficient to resolve definitely each domain layer. We hope the reviewer appreciates our cautious approach.

(5) Page 42, line 933: incomplete sentence. 

Good spot. We have corrected this in the revised manuscript.

(6) Page 46, line 1038; Reference 69 is in brackets, but references are not numbered. Please update.

Good spot. We have corrected this in the revised manuscript.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

Note : The original preprint version of our manuscript has been reviewed by 3 subject experts for Review Commons. All the three reviewers’ comments on the original version of our manuscript have been fully addressed. Their input was extremely valuable in helping us clarify and refine the presentation of our results and conclusions. Their feedback contributed to making the study both more thoroughly developed and more accessible to a broad readership, while preserving its mechanistic depth. We believe that this revised version more effectively highlights the conceptual advances brought by our findings.

Reviewer #1

Evidence, reproducibility and clarity

The manuscript "Key roles of the zona pellucida and perivitelline space in promoting gamete fusion and fast block to polyspermy inferred from the choreography of spermatozoa in mice oocytes" by Dr. Gourier and colleagues explores the poorly understood process of gamete fusion and the subsequent block to polyspermy by live-cell imaging of mouse oocytes with intact zona pellucida in vitro. The new component in this study is the presence of the ZP, which in prior studies of live-cell imaging had been removed before. This allowed the authos to examine contributions of the ZP to the block in polyspermy in relation to the timing of sperm penetrating the ZP and sperm fusing with the oocyte. By carefully analysing the timing of the cascade of events, the authors find that the first sperm that reaches the membrane of the mouse oocyte is not necessarily the one that fertilizes the oocytes, revealing that other mechanisms post-ZP-penetration influence the success of individual sperm. While the rate of ZP penetration remains constant in unfertilized oocytes, it decreases upon fertilization for subsequent sperm, providing direct evidence for the known 'slow block to polyspermy' provided by changes to the ZP adhesion/ability to be penetrated. Careful statistical analyses allow the authors to revisit the role of the ZP in preventing polyspermy: They show that the ZP block resulting from the cortical reaction is too slow (in the range of an hour) to contribute to the immediate prevention of polyspermy in mice. The presented analyses reveal that the ZP does contribute to the block to polyspermy in two other ways, namely by effectively limiting the number of sperm that reach the oocyte surface in a fertilization-independent manner, and by retaining components like JUNO and CD9, that are shed from the oocyte plasma membrane after fertilization, in the perivitelline space, which may help neutralize surplus spermatozoa that are already present in the PVS. Lastly, the authors report that the ZP may also contribute to channeling the flagellar oscillations of spermatozoa in the PVS to promote their fusion competence.

Major comments:

• Are the key conclusions convincing?

The authors provide a careful analysis of the dynamics of events, though the analyses are correlative, and can only be suggestive of causation. While this is a limitation of the study, it provides important analysis for future research. Moreover, by analysing also control oocytes without fertilization and the timing of events, the authors have in some instances clear 'negative controls' for comparison.

Some claims would benefit from rewording or rephrasing to put the findings better in the context of what is already known and what is novel:

• the phrasing 'challenging prior dogma' might be too strong since it had been observed before that it is not necessarily the first sperm that gets through the ZP that fertilizes the egg (though I am afraid that I do not have any citations or references for this). However, given that in the field people generally think it is not necessarily and always the first sperm, the authors may want to consider weakening this claim.

Only real-time imaging of in vitro fertilization of zona pellucida-intact oocytes, as performed in our study, is capable of determining which spermatozoon crossing the zona pellucida fuses with the oocyte. However, such studies are rare, and most do not specifically address this question. As Reviewers 1 & 3, we have not found any citation or reference telling or showing that it is not necessarily the first spermatozoon to penetrate the zona pellucida that fertilizes the egg. In contrast, at least one reference (Sato et al., 1979) explicitly reports the opposite. If, as suggested by Reviewer 1 and 3, it has indeed been observed before that the first sperm to pass the ZP is not always the one that fertilizes, and if this idea is generally accepted in the field, then it is all the more important that a study demonstrates and publishes this point. This is precisely what our study makes possible. However, in case we may have overlooked a previous reference making the same observation as ours, we have removed the phrasing ‘challenging prior dogma’. That being said, the key issue is not so much that it is not necessarily the first spermatozoon penetrating the perivitelline space that fertilizes, but rather why spermatozoa that successfully reach the PVS of an unfertilized oocyte may fail to achieve fertilization. This is one of the central questions our study sought to address.

• I do think the cortical granule release could still contribute to the block to polyspermy though - as the authors here nicely show - at a later time-point only, and thus not the major and not the immediate block as previously thought. The wording in the abstract should therefore be adjusted (since it could still contribute...)

We are concerned that we may disagree on this point. The penetration block resulting from cortical granule release progressively reduces the permeability of the zona pellucida to spermatozoa, relative to its baseline permeability prior to sperm–oocyte fusion. Any decrease in this baseline permeability occurring before the fusion block becomes fully effective can contribute to the prevention of polyspermy by limiting the number of sperm that can access the oolemma at a time when fusion is still possible. In contrast, once the fusion block is fully established, limiting the number of spermatozoa traversing the ZP becomes irrelevant regarding the block to polyspermy, as the fusion block alone is sufficient to prevent additional fertilizations, rendering the penetration block obsolete. The only scenario that could challenge this obsolescence is if the fusion block were transient. In that case, as Reviewer 1 suggests, the penetration block could indeed play a role at a later time-point. However, taken together, our study and that of Nozawa et al. (2018) support the conclusion that this is not the case in mice:

• Our in vitro study using kinetic tracking shows that the time constant for completion of the fusion block is typically 6.2 ± 1.3 minutes. During this time window, we observe that the permeability of the zona pellucida to spermatozoa does not yet decrease significantly from the baseline level it exhibited prior to sperm–oocyte fusion (see Figures 5B and S1B in the revised manuscript, and Figures 5A and 5B in the initial version). Consequently, before the fusion block is fully established, the penetration block can contribute only marginally—if at all—to the prevention of polyspermy. In contrast, the naturally low baseline permeability of the ZP—independent of any fertilization-triggered penetration block—as well as the relatively long timing of fusion ( minutes on average) after sperm penetration in the perivitelline space, are factors that contribute to the preservation of monospermic while the fusion block is still being established.
• Our in vitro study using kinetic tracking shows that once the fusion block is completed following the first fusion event, no additional spermatozoa are able to fuse with the oocyte until the end of the experiment, 4 hours post-insemination (see blue points and fitting curve in Figure 5C). Meanwhile, one or more additional spermatozoa—most of them motile and therefore viable—are present in the perivitelline space in 50% of the oocytes analyzed (purple point in Figure 5C). This demonstrates that, once established, the fusion block remains effective for at least the entire duration of the experiment, supporting the idea of a fully functional and long-lasting fusion block.
• Nozawa et al. (2018) found that female mice lacking ovastacin—the protease released during the cortical reaction that renders the zona pellucida impenetrable—are normally fertile. They additionally reported that the oocytes recovered from these females after mating are monospermic despite the systematic presence of additional spermatozoa in the perivitelline space. These findings further support the conclusion that in mice the fusion block is both permanent and sufficient to prevent polyspermy. For all these reasons, we believe that even at a later time-point, the penetration block does not contribute to the prevention of polyspermy in mice.

To clarify the fact that the penetration block does not necessarily contribute to prevent polyspermy, which indeed challenges the commonly accepted view, we have substantially revised the discussion. Furthermore, Figure 9 from the initial version of the manuscript has been replaced by Figure 8 in the revised version. This new figure provides a more didactic illustration of the inefficacy of the penetration block in preventing polyspermy in mice, by showing the respective impact of the fusion block, the penetration block, as well as fusion timing and the natural baseline permeability of the zona pellucida, on the occurrence of polyspermy.

As for the abstract, it has also been thoroughly revised. The content related to this section is now expressed in a way that emphasizes the factors that actively contribute to the prevention of polyspermy in mice, rather than those with no or marginal contribution (such as the penetration block in this case).

• release of OPM components - in the abstract it's unclear what the authors mean by this - in the results part it becomes clear. Please already make it clear in the abstract that it is the fertility factors JUNO/CD9 that could bind to sperm heads upon their release and thus 'neutralize' them? I would also recommend not referring to it as 'outer' plasma membrane (there is no 'inner plasma membrane'). Moreover, in the abstract please clarify that this release is happening only after fusion of the first sperm and not all the time. In the abstract it sounds as if this was a completely new idea, but there is good prior evidence that this is in fact happening (as also then cited in the results part) - maybe frame it more as the retention inside the PVS as new finding.

We thank reviewer 1 for pointing out the lack of precision in the abstract regarding the “components” released from the oolemma, and the fact that our phrasing may have given the impression that the post-fertilization release of CD9 and JUNO is a novel observation. The new observation is that CD9 and JUNO, which are known to be massively released from the oolemma after fertilization, bind to spermatozoa in the perivitelline space. However, we cannot rule out the possibility that other oocyte-derived molecules not investigated here may undergo a similar process. This is why we employed the broader term “components”, which encompasses both CD9 and JUNO as well as potential additional molecules. That said, we acknowledge the lack of precision introduced by this terminology. To address this, we have revised the corresponding sentence in the abstract to better reflect our new findings relative to previous ones, and to eliminate the ambiguity introduced by the word “component”.

The revised sentence of the abstract reads as follows:

“Our observation that non-fertilizing spermatozoa in the perivitelline space are coated with CD9 and JUNO oocyte’s proteins, which are known to be massively released from the oolemma after gamete fusion, supports the hypothesis that the fusion block involves an effective perivitelline space-block contribution consisting in the neutralization of supernumerary spermatozoa in the perivitelline space by these and potentially other oocyte-derived factors.”

Moreover, we cannot state in the abstract that the release of CD9 and JUNO occurs only after the fusion of the first spermatozoon and not before, since some CD9 and JUNO are already detectable in the perivitelline space (PVS) prior to fusion. What our study shows is that, before fertilization, CD9 and JUNO are predominantly localized at the oocyte membrane. In contrast, after fusion (four hours post-insemination), oocyte CD9 is distributed between the membrane and the PVS, and the only JUNO signal detectable in the oocyte is found in the PVS. This is what we describe in the Results section on page 15.

Regarding the acronym “OPM” in the initial version of the manuscript, although it was defined in the introduction as referring to the oocyte plasma membrane and not the outer plasma membrane (which, indeed, would not be meaningful), we acknowledge that it may have caused confusion to people in the field due to its resemblance to the commonly used meaningful acronym “OAM” for outer acrosomal membrane. To avoid any ambiguity, we have replaced the acronym “OPM” throughout the revised manuscript with the term “oolemma”, which unambiguously refers to the plasma membrane of the oocyte.

It is unclear to me what the relevance of dividing the post-fusion/post-engulfment into different phases as done in Fig 2 (phase 1, and phase 2) - also for the conclusions of this paper this seems rather irrelevant and overly complicated, since the authors never get back to it and don't need it (it's not related to the polyspermy block analyses). I would remove it from the main figures and not divide into those phases since it is distracting from the main focus.

Sperm engulfment and PB2 extrusion are two processes that follow sperm–oocyte fusion. As such, they are clear indicators that fusion has occurred and that meiosis has resumed. Their progression over time is readily identifiable in bright-field imaging: sperm engulfment is characterized by the gradual disappearance of the spermatozoon head from the oolemma, whereas PB2 extrusion is observed as the progressive emergence of a rounded protrusion from the oocyte membrane (Figure 2 in the initial manuscript and Figure S2 A&B in the revised version). The kinetics of these events, measured from the arrest of “push-up–like” movement of the sperm head against the oolemma —assumed to coincide with sperm-oocyte fusion, as further justified in a later response to Reviewer 1—provide reliable temporal landmarks for estimating the timing of fusion when the fusion event itself is not directly observed in real time (Figure S2 C&D).

The four landmarks used in this estimation are:

(i) the disappearance of the sperm head from the oolemma due to internalization (28 ± 2 minutes post-arrest, mean ± SD);

(ii) the onset of PB2 protrusion from the oolemma (28 ± 2 minutes post-arrest);

(iii) the moment when the contact angle between the PB2 protrusion and the oolemma shifts from greater than to less than 90° (49 ± 6 minutes post-arrest);

(iv) the completion of PB2 extrusion (73 ± 10 minutes post-arrest).

The approach used to determine the fusion time window of a fertilizing spermatozoon from these landmarks is detailed in the “Determination of the Fertilization Time Windows” section of the Materials and Methods. Compared to the initial version of the manuscript, we have added a paragraph explaining the rationale for using the arrest of the push-up–like movement as a reliable indicator for sperm–oocyte fusion and have clarified the description of the approach used to determine fertilization timing.

The timed characterization of sperm engulfment and PB2 extrusion kinetics is highly relevant to the analysis of the penetration and fusion blocks, however we agree that its place is more appropriate in the Supplementary Information than in the main text. In accordance with the reviewer’s recommendation, this section has therefore been moved to the Supplementary Information SI2.

For the statistical analysis, I am not sure whether the assumption "assumption that the probability distribution of penetration or fertilization is uniform within a given time window" is in fact true since the probability of fertilizing decreases after the first fertilization event.... Maybe I misunderstood this, but this needs to be explained (or clarified) better, or the limitation of this assumption needs to be highlighted.

During in vitro fertilization experiments with kinetic tracking, each oocyte is observed sequentially in turn. As a result, sperm penetration into the perivitelline space or fusion with the oolemma may occur either during an observation round or in the interval between two rounds. In the former case, penetration or fusion is directly observed in real time, allowing for high temporal precision in determining the moment of the event. In contrast, when penetration or fusion occurs between two observation rounds, the precise timing cannot be directly determined. We can only ascertain that the event took place within the time window we have determined. Because, within a given penetration or fusion time window, we do not know the exact moment at which the event occurred, there is no reason to favor one time over another. This justifies the assumption that all time points within the window are equally probable. This explanation has been added in the section Statistical treatment of penetration and fertilization chronograms to study the kinetics of fertilization, penetration block and fusion block of the main text and in the section Statistical treatment of penetrations and fertilizations chronograms to study penetration and fusion blocks of the material and methods.

-Suggestion for additional experiments:

If I understood correctly, the onset of fusion in Fig 2C is defined by stopping of sperm beating? If it is by the sudden stop of the beating flagellum, this should be confirmed in this situation (with the ZP intact) that it correctly defines the time-point of fusion since this has not been measured in this set-up before as far as I understand. In order to measure this accurately, the authors will need to measure this accurate to be able to acquire those numbers (of time from fusion to end of engulfment), e.g. by pre-loading the oocyte with Hoechst to transfer Hoechst to the fusing sperm upon membrane fusion.

The nuclear dye Hoechst is widely used as a marker of gamete fusion, as it transfers from the ooplasm—when preloaded with the dye—into the sperm nucleus upon membrane fusion, thereby signaling the happening of the fusion event. This technique is applicable in the context of in vitro fertilization using ZP-free oocytes. However, it is not suitable when cumulus–oocyte complexes are inseminated, as is the case in both in vitro experimental conditions of the present study (standard IVF and IVF with kinetic tracking). Indeed, when cumulus–oocyte complexes are incubated with Hoechst to preload the oocytes, the numerous surrounding cumulus cells also take up the dye. Consequently, upon insemination, spermatozoa acquire fluorescence while traversing and dispersing the cumulus mass—before reaching the ZP—thus rendering Hoechst labeling ineffective as a specific marker of membrane fusion. This remains true even under optimized conditions involving brief Hoechst incubation of cumulus–oocyte complexes ( Nonetheless, we have strong evidence supporting the use of the arrest of sperm movement as a surrogate marker for the moment of fusion. In our previous study (Ravaux et al., 2016; ref. 4 in the revised manuscript), we investigated the temporal relationship between the abrupt cessation of sperm head movement on the oolemma—resulting from strong flagellar beating arrest—and the fusion event, using ZP-free oocytes preloaded with Hoechst. That study revealed a temporal delay of less than one minute between the cessation of sperm oscillations and the actual membrane fusion, thereby supporting the conclusion that in ZP-free oocytes, the arrest of vigorous sperm movement at the oolemma is a reliable indicator of the moment at which fusion occurs. In the same study, the kinetics of sperm head internalization into the ooplasm were also characterized, typically concluding within 20–30 minutes after movement cessation. These findings are fully consistent with our current observations in ZP-intact oocytes, where sperm head engulfment was completed approximately 24 ± 3 minutes after the arrest of sperm oscillations. Taken together, these results strongly support the conclusion that, in both ZP-free and ZP-intact oocytes, the arrest of sperm movement is a reliable indicator of the fusion event. This assumption formed the basis for our determination of fertilization time points in the present study.

These justifications were not fully detailed in the original version of the manuscript. We have addressed this in the revised version by explicitly presenting this rationale in the Materials and Methods section under Determination of the Fertilization Time Windows.

Fig 8: 2 comments

• To better show JUNO/CD9 pre-fusion attachment to the oocyte surface and post-fusion loss from the oocyte surface (but persistence in the PVS), an image after removal of the ZP (both for pre-fertilization and post-fertilization) would be helpful - the combination of those images with the ones you have (ZP intact) would make your point more visible.

We have followed this recommendation. Figure 8 of the initial manuscript has been replaced by Figure 6 in the revised manuscript, which illustrates the four situations encountered in this study: fertilized and unfertilized oocytes, each with and without unfused spermatozoa in their PVS. To better show JUNO/CD9 pre-fusion presence to the oocyte plasma membrane, as well as their post-fusion partial (for CD9) and near-complete (for JUNO) loss from the oocyte membrane (but persistence in the PVS), paired images of the same oocyte before and after of ZP removal are now provided, both for unfertilized (Figure 6A) and fertilized oocytes (Figure 6C).

• You show that the heads of spermatozoa post fusion are covered in CD9 and JUNO, yet I was missing an image of sperm in the PVS pre-fertilization (which should then not yet be covered).

As staining and confocal imaging of the oocytes were performed 4 hours after insemination, images of sperm in the PVS of an oocyte “pre-fertilization” cannot be strictly obtained. However, we can have images of spermatozoa present in the PVS of oocytes that remained unfertilized. This situation, now illustrated in Figure 6B of the revised manuscript, shows that these spermatozoa are also covered in JUNO and CD9, which they may have progressively acquired over time from the baseline presence of these proteins in the PVS of unfertilized oocytes. This also may provide a mechanistic explanation for their inability to fuse with the oolemma, and, consequently, for the failure of fertilization in these oocytes.

Minor comments:

• The videos were remarkable to look at, and great to view in full. However, for the sake of time, the authors might want to consider cropping them for the individual phases to have a shorter video (with clear crop indicators) with the most important different stages visible in a for example 1 min video (e.g. video.

We have followed this recommendation. The videos have been cropped and annotated in order to highlight the key events that support the points made in the result section from page 9 to 11 in the revised manuscript.

• In general, given that the ZP, PVS and oocyte membrane are important components, a general scheme at the very beginning outlining the relative positioning of each before and during fertilization (and then possibly also including the second polar body release) would be extremely helpful for the reader to orient themselves.

A general scheme addressing Reviewer 1 request, summarizing the key components and concepts discussed in the article and intended to help guide the reader, has been added to the introduction of the revised manuscript as Figure 1.

• first header results "Multi-penetration and polyspermy under in vivo conditions and standard and kinetics in vitro fertilization conditions" is hard to understand - simplify/make clearer (comparison of in vivo and in vitro conditions? Establishing the in vitro condition as assay?)

The title of the first Results section has been revised in accordance with Reviewer 1 suggestion. It now reads: Comparative study of penetration and fertilization rates under in vivo and two distinct in vitro fertilization conditions.

• Large parts of the statistical analysis (the more technical parts) could be moved to the methods part since it disrupts the flow of the text.

In the revised version of our manuscript, we have restructured this part of the analysis to ensure that more technical or secondary elements do not disrupt the flow of the main text. Accordingly, the equations have been reduced to only what is strictly necessary to understand our approach, their notation has been greatly simplified, and the statistical analysis of unfertilized oocytes whose zona pellucida was traversed by one or more spermatozoa has been moved to the Supplementary Information (SI1).

• To me, one of the main conclusions was given in the text of the results part, namely that "This suggests that first fertilization contributes effectively to the fertilization-block, but less so to the penetration block". I would suggest that the authors use this conclusion to strengthen their rationale and storyline in the abstract.

We agree with Reviewer 1 suggestion. Accordingly, we have not only thoroughly revised our abstract, but also the introduction and discussion, in order to better highlight the rationale of our study, its storyline, and the new findings which not only challenge certain established views but also open new research directions in the mechanisms of gamete fusion and polyspermy prevention.

• Wording: To characterize the kinetics with which penetration of spermatozoa in the PVS falls down after a first fertilization," falls down should be replaced with decreases (page 10 and page 12)

Falls down has been removed from the new version and replaced with decreases

Significance

Overall, this manuscript provides very interesting and carefully obtained data which provides important new insights particularly for reproductive biology. I applaud the authors on first establishing the in vivo conditions (how often do multiple sperm even penetrate the ZP in vivo) since studies have usually just started with in vitro condition where sperm at much higher concentration is added to isolated oocyte complexes. Thank you for providing an in vivo benchmark for the frequency of multiple sperm being in the PVS. While this frequency is rather low (somewhat expectedly, with 16% showing 2-3 sperm in the PVS), this condition clearly exists, providing a clear rationale for the investigation of mechanisms that can prevent additional sperm from entering.

My own expertise is experimentally - thus I don't have sufficient expertise to evaluate the statistical methods employed here.

__ __

Reviewer #2

Evidence, reproducibility and clarity

Overall, this is a very interesting and relevant work for the field of fertilization. In general, the experimental strategies are adequate and well carried out. I have some questions and suggestions that should be considered before the work is published.

1) Why are the cumulus cells not mentioned when the AR is triggered before or while the sperms cross it? It seems the paper assumes from previous work that all sperm that reach ZP and the OPM have carried out the acrosome reaction. This, though probably correct, is still a matter of controversy and should be discussed. It is in a way strange that the authors do not make some controls using sperm from mice expressing GFP in the acrosome, as they have used in their previous work.

We do not mention the cumulus cells or whether the acrosome reaction is triggered before, during, or after their traversal (i.e., upon sperm binding to the ZP), as this question, while scientifically relevant, pertains to a distinct line of investigation that lies beyond the scope of the present study. Even with the use of spermatozoa expressing GFP in the acrosome, addressing this question would require a complete redesign of our kinetic tracking protocol, which was specifically conceived to monitor in bright field the dynamic behavior of spermatozoa from the moment they begin to penetrate the perivitelline space of an oocyte. Accordingly, we imaged oocytes that were isolated 15 minutes after insemination of the cumulus–oocyte complexes, by which time most (if not all) cumulus cells had detached from the oocytes, as explained in the fourth paragraph of the material and methods of both the initial and revised versions of the manuscript. The spermatozoa we had access to were therefore already bound to the zona pellucida at the time of removal from the insemination medium, and had thus necessarily passed through the cumulus layer. It is unclear for us why Reviewer 2 believes that we “assume from previous work that all sperm that reach ZP has carried out the acrosome reaction”. We could not find any statement in our manuscript suggesting, let alone asserting, such an assumption, which we know to be incorrect. Based on both published work from Hirohashi’s group in 2011 (Jin et al., 2011, DOI: 10.1073/pnas.1018202108) and our own unpublished observation (both involving cumulus-oocyte masses inseminated with spermatozoa expressing GFP in the acrosome), it is established that only a subset of spermatozoa reaching the ZP after crossing the cumulus layer has undergone acrosome reaction. Moreover, from the same sources—as well as from a recent publication by Buffone’s group (Jabloñsky et al., 2023 DOI: 10.7554/eLife.93792 ) which is the one to which reviewer 2 refers in her/his 3rd comment, it is also well established that spermatozoa have all undergone acrosome reaction when they enter the PVS. To the best of our knowledge, this latter point has long been widely accepted and is not questioned. Therefore, stating this in the first paragraph of the Discussion in the revised manuscript, while referencing the two aforementioned published studies, should be appropriate. What remains a matter of ongoing debate, however, is the timing and the physiological trigger(s) of the acrosome reaction in fertilizing spermatozoa. The 2011 study by Hirohashi’s group challenged the previously accepted view that ZP binding induces the acrosome reaction, showing instead that most spermatozoa capable of crossing the ZP and fertilizing the oocyte had already undergone the acrosome reaction prior to ZP binding. However, as this issue lies beyond the scope of our study, we do not consider it appropriate to include a discussion of it in the manuscript.

2) In the penetration block equations, it is not clear to me why (𝑡𝑃𝐹1) refers to both PIPF1 and 𝜎𝜎𝑃I𝑃𝐹1. Is it as function off?

That is correct: (tPF1) means function of the time post-first fertilization. Both the post-first fertilization penetration index (i.e. PIPF1) and its incertainty (i.e. 𝜎𝑃I𝑃𝐹1 ) vary as a function of this time. However, as mentioned in a previous response to Reviewer 1, this section has been rewritten to improve clarity and readability. The equations have been limited to those strictly necessary for understanding our approach, and their notation has been significantly simplified.

3) Why do the authors think that the flagella stops. The submission date was 2024-10-01 07:27:26 and there has been a paper in biorxiv for a while that merits mention and discussion in this work (bioRxiv [Preprint]. 2024 Jul 2:2023.06.22.546073. doi: 10.1101/2023.06.22.546073.PMID: 37904966).

Our experimental approach allows us to determine when the spermatozoon stops moving, but not why it stops. We thank Reviewer 3 for pointing out this very relevant paper from Buffone’s group (doi: 10.7554/eLife.93792) which shows the existence of two distinct populations of live, acrosome-reacted spermatozoa. These correspond to two successive stages, which occur either immediately upon acrosome reaction in a subset of spermatozoa, or after a variable delay in others, during which the sperm transitions from a motile to an immotile state. The transition from the first to the second stage was shown to follow a defined sequence: an increase in the sperm calcium concentration, followed by midpiece contraction associated with a local reorganization of the helical actin cortex, and ultimately the arrest of sperm motility. For fertilizing spermatozoa in the PVS, this transition was shown to occur upon fusion. However, it was also reported in some non-fertilizing spermatozoa that this transition took place within the PVS. These findings are consistent with the requirement for sperm motility in order to achieve fusion with the oolemma. Moreover, the fact that some spermatozoa may prematurely transition to the immotile state within the PVS can therefore be added to the list of possible reasons why a spermatozoon that penetrates the PVS of an oocyte might fail to fuse.

This discussion has been added to the first paragraph of the Discussion section of our revised manuscript.

4) Please correct at the beginning of Materials and Methos: Sperm was obtained from WT male mice, it should say were.

Thank you, the correction has been done.

5) This is also the case in the fourth paragraph of this section: oocyte were not was.

The sentence in question has been modified as followed: “In the in vitro fertilization experiments with kinetic tracking, a subset of oocytes—together with their associated ZP-bound spermatozoa—was isolated 15 minutes post-insemination and transferred individually into microdrops of fertilization medium to enable identification.”

Significance

Understanding mammalian gamete fusion and polyspermy inhibition has not been fully achieved. The authors examined real time brightfield and confocal images of inseminated ZP-intact mouse oocytes and used statistical analyses to accurately determine the dynamics of the events that lead to fusion and involve polyspermy prevention under conditions as physiological as possible. Their kinetic observations in mice gamete interactions challenge present paradigms, as they document that the first sperm is not necessarily the one that fertilizes, suggesting the existence of other post-penetration fertilization factors. The authors find that the zona pellucida (ZP) block triggered by the cortical reaction is too slow to prevent polyspermy in this species. In contrast, their findings indicate that ZP directly contributes to the polyspermy block operating as a naturally effective entry barrier inhibiting the exit from the perivitelline space (PVS) of components released from the oocyte plasma membrane (OPM), neutralizing unwanted sperm fusion, aside from any block caused by fertilization. Furthermore, the authors unveil a new important ZP role regulating flagellar beat in fertilization by promoting sperm fusion in the PVS.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

SUMMARY: This study by Dubois et al. utilizes live-cell imaging studies of mouse oocytes undergoing fertilization. A strength of this study is their use of three different conditions for analyses of events of fertilization: (1) eggs undergoing fertilization retrieved from females at 15 hr after mating (n = 211 oocytes); (2) cumulus-oocyte complexes inseminated in vitro (n = 220 oocytes), and (3) zona pellucida (ZP)-intact eggs inseminated in vitro, transferred from insemination culture once sperm were observed bound to the ZP for subsequent live-cell imaging (93 oocytes). This dataset and these analyses are valuable for the field of fertilization biology. Limitations of this manuscript are challenges arise with some conclusions, and the presentation of the manuscript. There are some factual errors, and also some places where clearer explanations should to be provided, in the text and potentially augmented with illustrations to provide more clarity on the models that the authors interpret from their data.

MAJOR COMMENTS:

The authors are congratulated on their impressive collection of data from live-cell imaging. However, the writing in several sections is challenging to understand or seems to be of questionable accuracy. The lack of accuracy is suspected to be more an effect of overly ambitious attempts with writing style, rather than to mislead readers. Nevertheless, these aspects of the writing should be corrected. There also are multiple places where the manuscript contradicts itself. These contradictions should be corrected. Finally, there are factual points from previous studies that need correction.

Second, certain claims and the conclusions as presented are not always clearly supported by the data. This may be connected to the issues with writing style, word and phrasing choices, etc. The conclusions could be expressed more clearly, and thus may not require additional experiments or analyses to support them. The authors might also consider illustrations as ways to highlight the points they wish to make. (Figure 7 is a strong example of how they use illustrations to complement the text).

In response to Reviewer 3's concern about the writing style, which made several sections difficult to understand, we have thoroughly revised the entire manuscript to improve clarity, and precision. To further enhance comprehension, we have added illustrations in the revised version of the manuscript:

• Figure 1A presents the gamete components; Figure 1B depicts the main steps of fertilization considered in the present study; and Figure 1C illustrates the penetration and fusion blocks, along with the respective contributing mechanisms: the ZP-block for the penetration block, and the membrane-block and PVS-block for the fusion block

• Figure 2A provides a description of the three experimental protocols used in this study: Condition 1, in vivo fertilization after mating; Condition 2, standard in vitro fertilization following insemination of cumulus-oocyte complexes; and Condition 3, in vitro fertilization with kinetic tracking of oocytes isolated from the insemination medium 15 min after insemination of the cumulus-oocyte complexes.

• Figure 4 (formerly Figure 7 in the initial version) now highlights all fusing and non-fusing situations documented in videos 1-6 and associated paragraphs of the Results section.

• In the Discussion, Figure 9 from the original version has been replaced by Figure 8, which now provides a more pedagogical illustration of the inefficacy of the penetration block in preventing polyspermy in mice. This figure illustrates the respective contributions of the fusion block, the penetration block, fusion timing, and the intrinsic permeability of the zona pellucida to the occurrence of polyspermy.

We hope that this revised version of the article will guide the reader smoothly throughout, without causing confusion.

Regarding the various points that Reviewer 3 perceives as contradictions or factual errors, or the claims and the conclusions which, as presented, should not always supported by the data, we will provide our perspective on each of them as they are raised in the review.

SPECIFIC COMMENTS:

(1) The authors should use greater care in describing the blocks to polyspermy, particularly because they appear to be wishing to reframe views about prevention of polyspermic fertilization. The title mentions of "the fast block to polyspermy;" this problematic for a couple of different reasons. There is no strong evidence for block to polyspermy in mammals that occurs quickly, particularly not in the same time scale as the first-characterized fast block to polyspermy. To many biologists, the term "fast block to polyspermy" refers to the block that has been described in species like sea urchins and frogs, meaning a rapid depolarization of the egg plasma membrane. However, such depolarization events of the egg membrane have not been detected in multiple mammalian species. Moreover, the change in the egg membrane after fertilization does not occur in as fast a time scale as the membrane block in sea urchins and frogs (i.e., is not "fast" per se), and instead occurs in a comparable time frame as the conversation of the ZP associated with the cleavage of ZP2. Thus, it is misleading to use the terms "fast block" and "slow block" when talking about mammalian fertilization. This also is an instance of where the authors contradict themselves in the manuscript, stating, "the membrane block and the ZP block are established in approximatively the same time frame" (third paragraph of Introduction). This statement is indeed accurate, unlike the reference to a fast block to polyspermy in mammals.

We fully agree with Reviewer 3 on the importance of clearly defining the two blocks examined in the present study—the penetration block and the fusion block (as referred to in the revised version) —and of situating them in relation to the three blocks described in the literature: the ZP-block, membrane-block, and PVS-block. We acknowledge that this distinction was not sufficiently clear in the original version of the manuscript. In the revised version, these two blocks and their relationship to the ZP-, membrane-, and PVS-blocks are now clearly introduced in the second paragraph of the Introduction section and illustrated in the first figure of the manuscript (Fig. 1C). They are then discussed in detail in two dedicated paragraphs of the Discussion, entitled Relation between the penetration block and the ZP-block and Relation between the fusion block and the membrane- and PVS-blocks.

The penetration block refers to the time-dependent decrease in the number of spermatozoa penetrating the perivitelline space (PVS) following fertilization, whereas the fusion block refers to the time-dependent decrease in sperm-oolemma fusion events after fertilization. It is precisely to the characterization of these two blocks that our in vitro fertilization experiments with kinetic tracking allow us to access.

In this study, as in the literature, fusion-triggered modifications of the ZP that hinder sperm traversal of the ZP are referred to as the ZP-block (also known as ZP hardening). The ZP-block thus contributes to the post-fertilization reduction in sperm penetration into the PVS and thereby underlies the penetration block. Similarly, fusion-triggered alterations of the PVS and the oolemma that reduce the likelihood of spermatozoa that have reached the PVS successfully to fuse with the oolemma are referred to as the PVS-block and membrane-block, respectively. These two blocks act together to reduce the probability of sperm-oolemma fusion after fertilization, and thus contribute to the fusion block.

The time constant of the penetration block was found to be 48.3 ± 9.7 minutes, which is consistent with the typical timeframe of ZP-block completion—approximately one hour post-fertilization in mice—as reported in the literature. By contrast, the time constant of the fusion block was determined to be 6.2 ± 1.3 minutes, which is markedly faster than the time typically reported in the literature for the completion of the fusion-block (more than one hour in mice). This strongly suggests that the kinetics of the fusion block are not primarily governed by its membrane-block component, but rather by its PVS-block component—about which little to nothing was previously known.

Contrary to what Reviewer 3 appears to have understood from our initial formulation, there is therefore no contradiction or error in stating that "the membrane block and the ZP block are established within approximately the same timeframe", while the fusion block, which proceeds much more rapidly, is likely to rely predominantly on the PVS-block. We have thoroughly revised the manuscript to clarify this key message of the study.

However, we understand Reviewer 3’s objection to referring to the fusion block (or the PVS-block) as a fast block, given that this term is conventionally reserved for the immediate fertilization-triggered membrane depolarization occurring in sea urchins and frogs. Although the kinetics we report for the fusion block are considerably faster than those of the penetration block, they occur on the scale of minutes, and not seconds. In line with the reviewer's recommendation, we have therefore modified both the title and the relevant passages in the text to remove all references to the term fast block in the revised version.

(2) The authors aim to make the case that events occurring in the perivitelline space (PVS) prevent polyspermic fertilization, but the data that they present is not strong enough to make this conclusion. Additional experiments would optional for this study, but data from such additional experiments are needed to support the authors' claims regarding these functions in fertilization. Without additional data, the authors need to be much more conservative in interpretations of their data. The authors have indeed observed phenomena (the presence of CD9 and JUNO in the PVS) that could be consistent with a molecular basis of a means to prevent fertilization by a second sperm. However, the authors would need additional data from additional experimental studies, such as interfering with the release of CD9 and JUNO and showing that this experimental manipulation leads to increased polyspermy, or creating an experimental situation that mimics the presence of CD9 and JUNO (in essence, what the authors call "sperm inhibiting medium" on page 20) and showing that this prevents fertilization.

A major section of the Results section here (starting with "The consequence is that ... ") is speculation. Rather than be in the Results section, this should be in the Discussion. The language should be also softened regarding the roles of these proteins in the perivitelline space in other portions of the manuscript, such as the abstract and the introduction.

Finally, the authors should do more to discuss their results with the results of Miyado et al. (2008), which interestingly, posited that CD9 is released from the oocytes and that this facilitates fertilization by rendering sperm more fusion-competent. There admittedly are two reports that present data that suggest lack of detection of CD9-containing exosomes from eggs (as proposed by Miyado et al.), but nevertheless, the authors should put their results in context with previous findings.

We generally agree with all the remarks and suggestions made here. In the revised version of the manuscript, we have retained in the Results section (pp. 14–15) only the factual data concerning the localization of CD9 and JUNO in unfertilized and fertilized oocytes, as well as in the spermatozoa present in the PVS of these oocytes. We have taken care not to include any interpretive elements in this section, which are now presented exclusively in a dedicated paragraph of the Discussion, entitled “Possible molecular bases of the membrane-block and ZP-block contributing to the fusion block” (p. 21). There, we develop our hypothesis and discuss it in light of both the findings from the present study and previous work by other groups. In doing so, we also address the data reported by Miyado et al. (2008, https://doi.org/10.1073/pnas.0710608105), as well as subsequent studies by two other groups—Gupta et al. (2009, https://doi.org/10.1002/mrd.21040) and Barraud-Lange et al. (2012, https://doi.org/10.1530/REP-12-0040)—that have challenged Miyado’s findings.

We are fully aware that our interpretation of the coverage of unfused sperm heads in the perivitelline space (PVS) by CD9 and JUNO, released from the oolemma—as a potential mechanism of sperm neutralization contributing to the PVS block—remains, at this stage, a plausible hypothesis or working model that, as such, warrants further experimental investigation. It is precisely in this spirit that we present it—first in the abstract (p.1), then in the Discussion section (p. 21), and subsequently in the perspective part of the Conclusion section (p. 22).

(3) Many of the authors' conclusions focus on their prior analyses of sperm interaction - beautifully illustrated in Figure 7. However, the authors need to be cautious in their interpretations of these data and generalizing them to mammalian fertilization as a whole, because mouse and other rodent sperm have sperm head morphology that is quite different from most other mammalian species.

In a similar vein, the authors should be cautious in their interpretations regarding the extension of these results to mammalian species other than mouse, given data on numbers of perivitelline sperm (ranging from 100s in some species to virtually none in other species), suggesting that different species rely on different egg-based blocks to polyspermy to varying extents. While these observations of embryos from natural matings are subject to numerous nuances, they nevertheless suggest that conclusions from mouse might not be able to be extended to all mammalian species.

It is not clear to us whether Reviewer 3’s comment implies that we have, at some point in the manuscript, generalized conclusions obtained in mice to other mammalian species—which we have not—or whether it is simply a general, common-sense remark with which we fully agree: that findings established in one species cannot, by default, be assumed to apply to another.

We would like to emphasize that throughout the manuscript, we have taken care to restrict our interpretations and conclusions to the mouse model, and we have avoided any unwarranted extrapolation to other species.

To definitively close this matter—if there is indeed a matter—we have added the following clarifying statements in the revised version of the manuscript:

In the introduction, second paragraph (pp. 2–3):"The variability across mammalian species in both the rate of fertilized oocytes with additional spermatozoa in their PVS (from 0 to more than 80%) after natural mating and the number of spermatozoa present in the PVS of these oocytes (from 0 to more than a hundred) suggests that the time for completion of the penetration block and thus its efficiency to prevent polyspermy can vary significantly between species."

At the end of the preamble to the Results section (p. 4):"This experimental study was conducted in mice, which are the most widely used model for studying fertilization and polyspermy blocks in mammals. While there are many interspecies similarities, the findings presented here should not be directly extrapolated to humans or other mammalian species without species-specific validation."

In the Conclusion, the first sentence is (p.22) : “This study sheds new light on the complex mechanisms that enable fertilization and ensure monospermy in mouse model.”

Within the Conclusion section, among the perspectives of this work (p. 22):"In parallel, comparative studies in other mammalian species will be needed to assess the generality of the PVS-block and its contribution relative to the membrane-block and ZP-blocks, as well as the generality of the mechanical role played by flagellar beating and ZP mechanical constraint in membrane fusion."

(4) Results, page 4 - It is very valuable that the authors clearly define what they mean by a penetrating spermatozoon and a fertilizing spermatozoon. However, they sometimes appear not to adhere to these definitions in other parts of the manuscript. An example of this is on page 10; the description of penetration of spermatozoon seems to be referring to membrane fusion with the oocyte plasma membrane, which the authors have alternatively called "fertilizing" or fertilization - although this is not entirely clear. The authors should go through all parts of the manuscript very carefully and ensure consistent use of their intended terminology.

Overall, while these definitions on page 4 are valuable, it is still recommended that the authors explicitly state when they are addressing penetration of the ZP and fertilization via fusion of the sperm with the oocyte plasma membrane. This help significantly in comprehension by readers. An example is the section header in the middle of page 9 - this could be "Spermatozoa can penetrate the ZP after the fertilization, but have very low chances to fertilize."

We chose to define our use of the term penetration at the beginning of the Results section because, as readers of fertilization studies, we have encountered on multiple occasions ambiguity as to whether this term was referring to sperm entry into the perivitelline space following zona pellucida traversal, or to the fusion of the sperm with the oolemma. To avoid such ambiguity, we were particularly careful throughout the writing of our original manuscript to use the term penetration exclusively to describe sperm entry into the PVS. The terms fertilizing and fusion were reserved specifically for membrane fusion between the gametes. However, as occasional lapses are always possible, we followed Reviewer 3’s recommendation and carefully re-examined the entire manuscript to ensure consistent use of our intended terminology. We did not identify any inconsistencies, including on page 10, which was cited as an example by Reviewer 3. We therefore confirm that, in accordance with our predefined terminology, all uses of the term penetration, on that page and anywhere else in our original manuscript, refer exclusively to sperm entry into the PVS and do not pertain to fusion with the oolemma.

That said, it is important that all readers— including those who may only consult selected parts of the article—are able to understand it clearly. Therefore, despite the potential risk of slightly overloading the text, Reviewer 3’s suggestion to systematically associate the term penetration with ZP seems to us a sound one. However, we have opted instead to associate penetration with PVS, as our study focuses on the timing of sperm penetration into the perivitelline space, rather than on the traversal of the zona pellucida itself. Accordingly, except in a few rare instances where ambiguity seemed impossible, we have systematically used the phrasing “penetration into the PVS” throughout the revised version of the manuscript.

Another variation of this is in the middle of page 9, where the authors use the terms "fertilization block" and "penetration block." These are not conventional terms, and venture into being jargon, which could leave some readers confused. The authors could clearly define what they mean, particularly with respect to "penetration block,"

This point has already been addressed in our response to Comment 1 from Reviewer 3. We invite Reviewer 3 to refer to that response.

This extends to other portions of the manuscript as well, such as Figure 2C, with the label on the y-axis being "Time after fertilization." It seems that what the authors actually observed here was the cessation of sperm tail motility. (It is not evident they they did an assessment of sperm-oocyte fusion here.)

Regarding Figure 2C (original version), it has been merged with Figure 2B (original version) to form a single figure (Figure S2D), now included in Supplementary Information SI2. This new figure retains all the information originally presented in Figure 2C and indicates the time axis origin as the time when oscillatory movements of the sperm cease.

That said, for the reasons detailed in our response to Reviewer 1 and in the Materials and Methods, we explain why it is legitimate to use the cessation of sperm head oscillations on the oolemma as a marker for the timing of the fusion event. We invite the reviewers to refer to that response for a full explanation of our rationale.

(5) Several points that the authors try to make with several pieces of data do not come across clearly in the text, including Figure 2 on page 6, Figure 4 on page 9, and the various states utilized for the statistical treatment, "post-first penetration, post-first fertilization, no fertilization, penetration block and polyspermy block" on page 10. Either re-writing and clearer definitions'explanations are needed, and/or schematic illustrations could be considered to augment re-written text. Illustrations could be a valuable way present the intended concepts to readers more clearly and accurately. For example, Figure 4 and the associated text on page 9 get particularly confusing - although this sounds like a quite impressive dataset with observations of 138 sperm. Illustrations could be helpful, in the spirit of "a picture is worth 1000 words," to show what seem to be three different situations of sequences of events with the sperm they observed. Finally, the text in the Results about the 138 sperm is quite difficult to follow. It also might help comprehension to augment the percentages with the actual numbers of sperm - e.g., is 48.6% referring 67 of the total 138 sperm analyzed? Does the 85.1% refer to 57 of these 67 sperm?

Figure 2 in the original version of our manuscript concerns sperm engulfment and PB2 extrusion. As already mentioned in our response to Reviewer 1, the characterization of sperm engulfment and PB2 extrusion kinetics is highly relevant to the analysis of the penetration and fusion blocks. However, we agree that its presence in the main text may distract the reader from the main focus of the study. Therefore, this figure and the associated text have been moved to the Supplementary Information in the revised manuscript (SI 2, pages 26–27).

Regarding Figure 4 (original version), in response to Reviewer 3’s concern about the difficulty in grasping the message conveyed in its three graphs and associated text we have completely rethought the way these data are presented. Since the three graphs of Figure 4 were directly derived from the experimental timing data of sperm entry in the PVS and fusion with the oolemma in fertilized oocytes (originally shown in Figure 3A), we have combined them into a single figure in the revised manuscript: Figure 3 (page 8). This new Figure 3 now comprises three components:

• Figure 3A remains unchanged from the original version and shows the timing of sperm penetration and fusion in fertilized oocytes. Each sperm category (fused or non-fused , penetrated in the PVS before fusion or after fusion) is represented using a color code clearly explained in the main text (last paragraph of page 7).
• Figure 3B focuses specifically on the first spermatozoon to penetrate the PVS of each oocyte. It reports how many of these first-penetrating spermatozoa succeeded in fusing versus how many failed to do so, highlighting that being the first to arrive is not sufficient for fusion—other factors are involved. This is explained simply in the first paragraph of page 9.
• Figure 3C considers all spermatozoa that entered the PVS of fertilized oocytes, classifying them into three categories: those that penetrated the PVS before fertilization, those that did so after fertilization, and those for which the timing could not be precisely determined. Such classification makes it apparent that the number of spermatozoa penetrating before and after fertilization is of the same order of magnitude, indicating that fertilization is not very effective at preventing further sperm entry into the PVS for the duration of our observations (~4 hours). To facilitate the identification of these three categories, the same color code used in Figure 3A is applied. In addition, within each category, the number of spermatozoa that successfully fused are indicated in black. This allows the reader to quickly assess the fertilization probability for each category—high for sperm entering before fertilization, very low or null for those entering after fertilization. This analysis shows that fertilization is far more effective at blocking sperm fusion than at blocking sperm penetration. This is clearly explained in the second paragraph of page 9. Regarding__ statistical analysis__, as already mentioned in our responses to Reviewers 1 and 2, this section has been rewritten to improve clarity and readability. The notation has also been significantly simplified. To improve the overall fluidity of the text related to the statistical analysis, Figure 3B (original version), which presented the timing of penetration into the perivitelline space of oocytes that remained unfertilized, along with its associated statistical analysis previously in Figure 5B), have been revised and transferred together in a single Figure S1 of the Supplementary Information (SI1, pages 26; now Figures S1A and S1B).

(6) Introduction, page 2 - it is inaccurate to state that only diploid zygotes can develop into a "new being." Triploid zygotes typically fail early in develop, but can survive and, for example, contribute to molar pregnancies. Additionally, it would be beneficial to be more scientifically precise term than saying "development into a new being." This is recommended not only for scientific accuracy, but also due to current debates, including in lay public circles, about what defines "life" or human life.

In response to Reviewer 3’s comment, we no longer state in the revised version of the manuscript that only diploid zygotes can develop into a new being. We have modified our wording as follows, on page 2, second paragraph: “In mammals, oocytes fertilized by more than one spermatozoon cannot develop into viable offspring.”

(7) Introduction, page 2 - The mammalian sperm must pass through three layers, not just two as stated in the first paragraph of the Introduction. The authors should include the cumulus layer in this list of events of fertilization.

The sentence from the introduction from the original manuscript mentioned by Reviewer 3 was: “To fertilize, a spermatozoon must successively pass two oocyte’s barriers.” This statement is accurate in the sense that the cumulus cell layer is not part of the oocyte itself, unlike the two oocyte’s barriers: the zona pellucida and the oolemma. Moreover, the traversal of the cumulus layer is not within the scope of our study, unlike the traversal of the zona pellucida and fusion with the oolemma. However, it is also correct that in our study the spermatozoa have passed through the cumulus layer before reaching the oocyte. Therefore, in response to Reviewer 3’s comment, we have revised the sentence to clarify this point as follows:

“Once a spermatozoon has passed through the cumulus cell layer surrounding the oocyte, it still must overcome two oocyte’s barriers to complete fertilization.”

(8) Introduction, page 2 - While there is evidence that zinc is released from mouse egg upon fertilization, the evidence is not convincing or conclusive that zinc is released from cortical granules or via cortical granule exocytosis.

To better highlight the rationale, storyline, and scope of our study, the introduction has been thoroughly streamlined. In this context, the section discussing the cortical reaction and zinc release seemed more appropriate in the Discussion, specifically within the paragraph titled “Relationship between the penetration block and the ZP-block.”

To address the uncertainty raised by Reviewer 3 regarding the origin of the zinc spark release, we have rephrased this part as follows:

“The fertilization-triggered processes responsible for the changes in ZP properties are generally attributed to the cortical reaction—a calcium-induced exocytosis of secretory granules (cortical granules) present in the cortex of unfertilized mammalian oocytes—and to zinc sparks. As a result, proteases, glycosidases, lectins, and zinc are released into the perivitelline space (PVS), where they act on the components of the zona pellucida. This leads to a series of modifications collectively referred to as ZP hardening or the ZP-block”.

(9) The authors inaccurately state, "only if monospermic multi-penetrated oocytes are able to develop normally, which to our knowledge has never been proven in mice" (page 4) - This was demonstrated with the Astl knockout, assuming that the authors use of "multi-penetrated oocytes" here refers to the definition of penetration that they use, namely penetrating the ZP. This also is one of the instances where the authors contradict themselves, as they note the results with this knockout on page 18.

Thank you for bringing this point to our attention. Nozawa et al. (2018) found that female mice lacking ovastacin (Astl)—the protease released during the cortical reaction that plays a key role in rendering the zona pellucida impenetrable—are normally fertile. They also reported that oocytes recovered from these females after mating were monospermic, despite the consistent presence of additional spermatozoa in the perivitelline space. We can indeed consider that taken together these findings demonstrate that the presence of multiple spermatozoa in the PVS does not impair normal development, as long as the oocyte remains monospermic. In our study, we re-demonstrated this in a different way (by reimplantation of monospermic oocytes with additional spermatozoa in their PVS) in a more physiological context of WT oocytes, but we agree that we cannot state: “which to our knowledge has never been proven in mice.” This part of the sentence has therefore been removed. In the revised version of the manuscript, the sentence is now formulated in the first paragraph of page 5 as follows: “However, the contribution of the fusion block to prevent polyspermy has physiological significance only if monospermic oocytes with additional spermatozoa in their PVS can develop into viable pups.”

Minor comments:

There are numerous places where this reader marked places of confusion in the text. A sample of some of these:

We will indicate hereinafter how we have modified the text in the specific examples provided by Reviewer 3. Beyond these, however, we would like to emphasize that we have thoroughly revised the entire manuscript to improve clarity and precision.

Page 4 - "continuously relayed by other if they detach" - don't know what this means

Replaced now p 5 by “can be replaced by others if they detach”

Page 6 - "hernia" - do the authors mean "protrusion" on the oocyte surface?

The paragraph from the Results section in question has now been moved to the Supplementary Information, on pages 26 and 27. The term hernia has been systematically replaced with protrusion, including in the Materials and Methods section on page 24.

Page 10 - "penetration of spermatozoa in the PVS falls down" - don't know what this means

Falls down has been removed from the new version and replaced with decreases

Page 12 - "spermatozoa linked to the oocyte ZP" - not clear what "linked" means here

Replaced now page 16 by “spermatozoa bound to the oocyte ZP”

Page 14 - "by dint of oscillations" - don't know what this means

Replaced now page 10 by “the persistent flagellum movements”

Specifics for Materials and Methods:

Exact timing of females receiving hCG and then being put with males for mating - assume this was immediate but this is an important detail regarding the timing for the creation of embryos in vivo.

That is correct: females were placed with males for mating immediately after receiving hCG. This clarification has been added in the revised version of the manuscript.

Please provide the volumes in which inseminations occurred, and how many eggs were placed in this volume with the 10^6 sperm/ml.

The number of eggs may vary from one cumulus–oocyte complex to another. It is therefore not possible to specify exactly how many eggs were inseminated. However, we now indicate on page 23 the number of cumulus–oocyte complexes inseminated (4 per experiment), the volume in which insemination was performed (200 mL), and the sperm concentration used 106 sperm/mL.

**Referees cross-commenting**

I concur with Reviewer 1's comment, that the 'challenging prior dogma' about the first sperm not always being the one to fertilize the egg is too strong. As Reviewer 1 notes, "it had been observed before that it is not necessarily the first sperm that gets through the ZP that fertilizes the egg." I even thought about adding this comment to my review, although held off (I was hoping to find references, but that was taking too long).

Please refer to our response to Reviewer 1 regarding this point.

Author response:

The following is the authors’ response to the original reviews

Reviewing Editor Comments:

Focus and Scope:

The paper attempts to address too many topics simultaneously, resulting in a lack of focus and insufficient depth in the treatment of individual components.

We have moved this selective clinical review section that was previously Part I in the paper now to Part II, given the importance of leading off with the meta-analysis and resource before doing a selective review, which are now Part I. In the lead in to Part II, we now indicate that the review is not intended to be comprehensive, because there are other recent comprehensive reviews, which we cite. This part of the paper merely aims to generate hypotheses on the directionality of effects ripe for testing on how TUS could be used to excite or suppress function, illustrated with specific clinical examples. The importance of this section, even though not comprehensive, is that it should provide the reader with examples on how the directionality of TUS could be used specifically in a range of clinical applications. The reader will find that the same hypotheses do not apply to different clinical disorder. Therefore, patient specific hypotheses need to be motivated and then subsequently tested with empirical application of TUS, which Part II provides.

Part II. Selective TUS clinical applications review and TUS directionality hypotheses starts at line 458. Part I, the meta-analysis and resource section starts at line 199, after the Introduction on TUS and the importance on understanding how the directionality of TUS effects could be better understood.

Strengthening the Meta-Analysis:

The meta-analysis is the strongest aspect of the paper and should be expanded to include the relevant statistics. However, it currently omits several key concepts, studies, and discussion points, particularly related to replication and the dominance of results from specific groups. These omissions should be addressed even with a focus on meta-analysis.

We thank the reviewer for their enthusiasm about the meta-analysis, which we have now promoted to Part I in the revised paper. We have substantially updated the latest database (inTUS_DATABASE_1-2025.csv) and ensured that the R markdown script can re-generate all of the results and statistical values. We have inserted additional statistical values in the main manuscript, as requested. The inTUS Resource is located here (https://osf.io/arqp8/ under Cafferatti_et_al_inTUS_Resource), and we have aimed to make it as user friendly to use and contribute to as possible. For instance, the reader can find them all in the HTML link summarizing the R markdown output with all statistical values here: https://rpubs.com/BenSlaterNeuro/1268823, a part of the inTUS resource.

Since the last submission, there has been a tremendous increase in the number of TUS studies in healthy participants. We have curated and included all of the relevant studies we could find in the 1-2025 database, as the next large expansion of the database (now including 52 experiments in healthy participants). We then reran and report the results of the statistical tests via the R markdown script (starting at line 336). Finally, the online database (inTUS_DATABASE_1-2025.csv) has additional columns, suggested by the reviewers, including one to identify the same groups that conducted the TUS study, based on a social network analysis. The manuscript figures (Table 1 and Table 2) did not have the space to expand the data tables, but these additional columns are available in the database online. Finally, we have ensured that the resource is as easy to use as possible (line 862 has the Introduction to the inTUS Resource – which is also the online READ ME file), and we have been in contact with the iTRUSST consortium leads who are interested in discussing hosting the resource and helping it to become self-sustaining.

Conceptual Development:

The more conceptual part of the paper is underdeveloped. It lacks sufficient supporting data, a well-articulated argument, and a clear derivation or development of a concrete model.

To ensure that the conceptual sections are well developed, we have revised the introduction, including the background on TUS and bases for the interest in the directionality of effects. We have also revised the TUS mechanisms background as suggested by the reviewers. For Part I, the meta-analysis basis and hypotheses we have ensured the rationale is clearer. The hypotheses are based on several lines of research in the animal model and human literature as cited (starting with line 211). For Part II, the selective clinical review, we have revised this section as well to have each section on lowintensity TUS and end in a hypothesis on the directionality of TUS effects. Starting at line 199 we have clarified the scope of the review and ensured that all the relevant experiments in healthy participants (n = 52 experiments) have now been included in the next key update of the resource and meta-analysis in this key paper update.

Database Curation:

The authors should provide more detailed information about how the database will be curated and made accessible. They may consider collaborating with ITRUSST.

We have expanded the information on the Resource documents (starting at line 862) to make the resource as user friendly as possible. At the beginning of the resource development stage we had contacted but not heard from the ITRUSST consortium. Encouraged by this comment we again reached out and are now in contact with the ITRUSST consortium leads who are interested in discussing sustaining the resource. It would be wonderful to have the resource linked to other ITTRUST tools, since it was inspired by the organization. Practically what this means is that the resource rather than being hosted on Open Science Framework, would potentially be hosted on the ITRUSST web site (https://itrusst.com/). These discussions are in progress, but the next key update to the database (1-2025) is already available and reported in this key update to our original paper.

Reviewer #1: (Public Review)

Summary:

This paper is a relevant overview of the currently published literature on lowintensity focussed ultrasound stimulation (TUS) in humans, with a meta-analysis of this literature that explores which stimulation parameters might predict the directionality of the physiological stimulation effects.

The pool of papers to draw from is small, which is not surprising given the nascent technology. It seems nevertheless relevant to summarize the current field in the way done here, not least to mitigate and prevent some of the mistakes that other non-invasive brain stimulation techniques have suffered from, most notably the theory- and data-free permutation of the parameter space.

The meta-analysis concludes that there are, at best, weak trends toward specific parameters predicting the direction of the stimulation effects. The data have been incorporated into an open database, that will ideally continue to be populated by the community and thereby become a helpful resource as the field moves forward.

Strengths:

The current state of human TUS is concisely and well summarized. The methods of the meta-analysis are appropriate. The database is a valuable resource.

Weaknesses:

These are not so much weaknesses but rather comments and suggestions that the authors may want to consider.

We thank the reviewer for their support of the resource and meta-analysis. We have implemented the suggestions next as follows.

I may have missed this, but how will the database be curated going forward? The resource will only be as useful as the quality of data entry, which, given the complexity of TUS can easily be done incorrectly.

We have added a paragraph on how authors could use the Qualtrics form to submit their data and the curation process involved (from line 891). Currently, this process cannot be automated because we continue to find that reported papers do not report the TUS parameters that ITRUSST has encouraged the community to report (Martin et al., 2024). We can dedicate for a TUS expert to ensure that every 6 or 12 months the data base is curated and expanded. The current version is the latest 1-2025 update to the data base. Longer term we are in discussion with ITRUSST on whether the resource could become self sustaining when TUS papers regularly reporting all the relevant parameters such that the database expansion becomes trivial, and then the Resource R markdown script and other tools can be used to re-evaluate the statistical tests and the user can conduct secondary hypothesis testing on the data.

It would be helpful to report the full statistics and effect sizes for all analyses. At times, only p-values are given. The meta-analysis only provides weak evidence (judged by the p-values) for two parameters having a predictive effect on the direction of neuromodulation. This reviewer thinks a stronger statement is warranted that there is currently no good evidence for duty cycle or sonication direction predicting outcome (though I caveat this given the full stats aren't reported). The concern here is that some readers may gallop away with the impression that the evidence is compelling because the p-value is on the correct side of 0.05.

We have ensured that the R script can generate the full statistics from the tests and the effect sizes for all the analyses, and now also report more of the key statistical values in the revised paper (starting at line 336). As suggested, we have also ensured that the interpretation is sufficiently nuanced given the small sample sizes and the p-values below 0.1 but above 0.05 are interpreted as a statistical trend.

This reviewer thinks the issue of (independent) replication should be more forcefully discussed and highlighted. The overall motivation for the present paper is clearly and thoughtfully articulated, but perhaps the authors agree that the role that replication has to play in a nascent field such as TUS is worth considering.

We completely agree and have added additional columns to the online database to identify unique groups, using a social network analysis, and independent replications. These expanded tables did not fit in the manuscript versions of Tables 1 and 2 but are fully available in the Resource data tables ready for further analysis by interested resource users.

A related point is that many of the results come from the same groups (the so-called theta-TUS protocol being a clear example). The analysis could factor this in, but it may be helpful to either signpost independent replications, which studies come from the same groups, or both.

In the expanded database tables (inTUS_DATABASE_1-2025.csv: https://osf.io/arqp8/ under Cafferatti_et_al_inTUS_Resource) we have added a column to identify independent replication.

The recent study by Bao et al 2024 J Phys might be worth including, not least because it fails to replicate the results on theta TUS that had been limited to the same group so far (by reporting, in essence, the opposite result).

Thank you. We have added this study and over a dozen recent TUS studies in healthy participants to the database and redone the analyses.

The summary of TUS effects is useful and concise. Two aspects may warrant highlighting, if anything to safeguard against overly simplistic heuristics for the application of TUS from less experienced users. First, could the effects of sonication (enhancing vs suppressing) depend on the targeted structure? Across the cortex, this may be similar, but for subcortical structures such as the basal ganglia, thalamus, etc, the idiosyncratic anatomy, connectivity, and composition of neurons may well lead to different net outcomes. Do the models mentioned in this paper account for that or allow for exploring this? And is it worth highlighting that simple heuristics that assume the effects of a given TUS protocol are uniform across the entire brain risk oversimplification or could be plain wrong? Second, and related, there seems to be the implicit assumption (not necessarily made by the authors) that the effects of a given protocol in a healthy population transfer like for like to a patient population (if TUS protocol X is enhancing in healthy subjects, I can use it for enhancement in patient group Y). This reviewer does not know to which degree this is valid or not, but it seems simplistic or risky. Many neurological and psychiatric disorders alter neurotransmission, and/or lead to morphological and structural changes that would seem capable of influencing the impact of TUS. If the authors agree, this issue might be worth highlighting.

We agree that given the divergence in circuits and cellular constituents between cortical and subcortical areas, it is important to distinguish studies that have focused on cortical or subcortical brain areas. The online data tables identify the target region. The analyses can be used to focus on the cortical or subcortical sites for analysis, although for the current version of the database there are too few subcortical sites with which to conduct analyses on subcortical sites. On the second point, that pathology may have affected the results, we completely agree and have clarified that the current database only includes healthy participant experiments for this reason. We are considering future updates to the resource may include clinical patient results (Line 247).

Reviewer #1 (Recommendations for the authors):

Minor edits (I wouldn't call them "corrections").

We sincerely appreciate the constructive comments and have aimed to address them all as suggested.

Perhaps the most relevant edit pertains to the statistics.

We now report the more complete statistical results (line 336) and the R markdown script can re-generate all the statistical values for the tests.

The issue of replication also seems relevant and ought to be raised. This reviewer does not want to prescribe what to do or impose the view the authors ought to adopt.

In the online version of the data tables for the latest dataset, we have added a column in the data table as suggested that identifies independent groups and replications.

The other points are left to the authors' discretion.

We have aimed to address all of the reviewer’s points. Thank you for the constructive input which has helped to improve the expanded database and resource.

Reviewer #2: (Public Review)

Summary:

This paper describes a number of aspects of transcranial ultrasound stimulation (TUS) including a generic review of what TUS might be used for; a meta-analysis of human studies to identify ultrasound parameters that affect directionality; a comparison between one postulated mechanistic model and results in humans; and a description of a database for collecting information on studies.

Strengths:

The main strength was a meta-analysis of human studies to identify which ultrasonic parameters might result in enhancement or suppression of modulation effects. The meta-analysis suggests that none of the US parameters correlate significantly with effects. This is a useful result for researchers in the field in trying to determine how the parameter space should be further investigated to identify whether it is possible to indeed enhance or suppress brain activity with ultrasound.

The database is a good idea in principle but would be best done in collaboration with ITRUSST, an international consortium, and perhaps should be its own paper.

Weaknesses:

The paper tries to cover too many topics and some of the technical descriptions are a bit loose. The review section does not add to the current literature. The comparison with a mechanistic model is limited to comparing data with a single model at a time when there is no general agreement in the field as to how ultrasound might produce a neuromodulation effect. The comparison is therefore of limited value.

We appreciate the reviewer’s assessment and interest in the meta-analysis and database to guide the development of TUS for more systematic control of the directionality of neuromodulation. With this next key expansion of the database (inTUS_DATABASE_1-2025.csv) we have added over a dozen new studies that have been published since our original submission (n = 52 experiments). We have also moved the ‘review’ part of the paper below the meta-analysis and resource description. We have clarified that the clinical review section (now Part II in the revised manuscript) is not intended as a comprehensive review but as a selective review showing how hypotheses on the directionality of TUS effects need to be carefully developed for specific patient groups that require different effects to be induced at specific brain areas. Finally, we have gotten in contact with the ITRUSST consortium leads, as suggested, and are in discussion on whether the inTUS resource could be hosted by ITRUSST. Since these discussions are ongoing practically what this might mean is moving the resource from the Open Science Framework to ITRUSST webpages, which would be a trivial update of the link to the resource in OSF.

We also sincerely appreciate the time and care the reviewer has given to provide us with the below guidance, all of which we have aimed to take on board in the revised paper.

Reviewer #2 (Recommendations for the authors):

Line 24/25 - I suggest avoiding using the term "deep brain stimulation" in reference to TUS as the term is normally used to describe electrically implanted electrodes.

We have removed the term “deep” brain stimulation in reference to TUS to avoid confusion with electrical DBS for patient treatment [Line 24].

Line 25 - I don't think "computational modelling" has changed how TUS can be done. There is still much to be understood about mechanisms. I think the modelling aspects of the paper should be toned down. Indeed the NICE data that is presented later appears to have a weak, if any, correlation to the outcomes.

We have revised the manuscript text throughout to ensure that the computational modeling contributions are not overstated, as noted, given the lack of strong correlation to the NICE model outcomes by the meta-analysis including in the latest results with the more extensive database (n = 52).

Line 32 - "exponentially increasing" is a well-defined technical term and the increase in studies should be quantified to ensure it is indeed exponential. I agree that TUS studies in humans are increasing but a quick tally of the data by year in the meta-analysis reported here doesn't suggest that it follows an "exponential" growth.

We have changed “exponential” to “to increase”. [Line 32]

Line 50 - I would suggest using the term sub-MHz rather than 100-1,000 kHz as it is challenging to deliver ultrasound at 1 MHz through the skull. The highest frequency in the meta-analysis is 850 kHz; but the majority are in the 200-500 kHz range.

We have made this correction to sub-MHz. [Line 54]

Line 58/59 - Is the FDA publication on diagnostic imaging relevant for saying that 50 W/cm2 is a lowintensity TUS? I think it's perhaps reasonable to say that intensities below diagnostic thresholds are "low intensities" but that is not clear in the text. I would refer to ITRUSST on what is appropriate for defining what is low, medium, or high.

We have cut the reference to the FDA here since it is, as noted, not as relevant as pointing to the ITRUSST definition.

Line 65/66 - I agree that ultrasound for neuromodulation is gaining traction and there is an increase in activity, but it also has a long history with the work of the Fry brothers published in the 1950s; and extensive work of Gavrilov in humans starting in the 1970s.

We have added citations to the Fry brothers and Gavrilov to the text in this section. [Line 69/70]

Line 75 - I think the intermembrane cavitation mechanism is unlikely to be due to "microbubbles" in a lipid membrane. The predicted displacements are on the order of nanometres, so they are unlikely to generate microbubbles. The work on comparing with NICE is limited. Note there are a number of experimental papers that have reported an absence of intra-membrane cavitation, including the Yoo et al 2022 which is referenced later in the paragraph. Also, there are other models, such as Liao et al 2021 (https://www.nature.com/articles/s41598020-78553-2).

As suggested, we have removed this phrase on microbubble formation as a likely mechanism. We have also added the Liao paper to this paragraph as it is relevant.

Line 83 - "At the lower intensities..." it is not clear whether this means all TUS intensities or the lower end of intensities used in TUS.

We now use the following wording here: “low intensities”. [Line 86]  

Line 85/86 - "more continuous stimulation" the modulation paradigms haven't been described yet and so pulse vs continuous hasn't been made clear to the reader. Also "more continuous" is very loose terminology. Something is either continuous or it isn't.

We agree and have removed “more” to be clear that the stimulation is continuous. [Line 88]

Line 87/88 - "TUS does not .. cavitation ..when ..ISPTA...<14 W/cm2". You can't use ISPTA to determine cavitation. It is the peak negative pressure which is the key driver for cavitation and the MI which is the generally accepted (although grudgingly by some) metric for assessing cavitation risk. You can link the negative pressure to ISPPA but not really to ISPTA. In histotripsy for example the ISPTA is low due to the low duty cycles to avoid heating but the cavitation is a huge effect. Technical terminology is loose.

We have corrected this to “TUS does not appear to cause significant heating or cavitation of brain tissue when the intensity remains low, based on Mechanical and Thermal Index values and recommendations of use”. [Line 90/91]

Line 89 - What is meant by "low intensity TUS"? I think all TUS used in the literature counts as low intensity - in that it is below the level allowed for diagnostic imaging.

We have ensured that the text is focused on TUS being low-intensity and only in the introduction do we distinguish low intensity TUS from moderate and high intensity TUS, such as used for thermal ablation [Lines 62-66].

Line 88/89 - Most temperature rises in brain tissue in TUS are well below 1 C - will this really change membrane capacitance significantly? If so it would have been good to consider a model for it.

We have revised this statement as “thermal effects could at least minimally alter cell membrane capacitance…”. [Line 93]

Line 111 - The text refers to "recent studies" but then the next two references are from 1990 and 2005 which I would argue don't count as "recent".

We have corrected this wording to “previous studies”. [Line 114]

Lines 122/129 - This paragraph on TMS pulsing should be linked to the TUS paragraph on pulsing (lines 109/116). The intervening paragraph on anaesthesia is relevant but breaks the flow.

We have merged the paragraph on anesthesia to the prior one on TUS so that the TMS paragraph is linked more closely to it [starting on line 112].

Line 130/131 - It is not clear to me that current studies are being guided by computational models. I think there is still no generally accepted theory for mechanisms. If the authors want to do a mechanisms paper then they should compare a few.

We have revised this as suggested to not overstate the contribution of the limited computational modeling studies throughout the manuscript.

Line 132 on - There are a number of studies that suggest that NICE is likely not the mechanism by which TUS produces neuromodulation.

We have revised this sentence as follows: “Although it remains questionable whether intramembrane cavitation is a key mechanism for TUS, the NICE model simulations explored a broad set of TUS parameters, including TUS intensity and the continuity of stimulation (duty cycle) on modelled neuronal responses.” [Lines 139/142]

Lines 137-140 - Terms are defined after their use. Things like ISPPTA, PRF, TI, and MI have been discussed already and so the terms should have been defined earlier. The authors should think carefully about how the material is presented to make it more logical for the reader.

We have ensured that the definitions precede the use of abbreviations and have added abbreviations to the tables.

Part I Line 180-437 - The review of potential applications for TUS reads like an introductory chapter of a thesis. It is entirely proper for a thesis to have a chapter like this, but it is not really relevant for a peer-reviewed research article. There are also numerous applications, e.g. mapping areas associated with decisions, or treating patients with addiction, which are not included, so it is not exhaustive. I would suggest this part be removed.

We have moved the ‘review’ part of the paper to Part II, given the metaanalysis and resource should be more prominent as Part I. In the review now Part II of the paper we also now make it clear that there are recent comprehensive reviews of the clinical literature ( line 465/467). Namely, the purpose of our selective review is to demonstrate how directionality of TUS effects need to be specific for the clinical application intended, given the great variability in clinical effects that might be desired, brain areas targeted and pathology being treated. We have also aimed to ensure that each section summary is scholarly and academically written to a high level. All the co-authors contributed to these sections so we have also edited to have some consistency across sections, with sections ending with directionality of TUS hypotheses that could be developed for empirical testing.

Line 453 - It is stated that "ISPTA, which mathematically integrates ISSPA by the sonication DC" It sounds rather grand to mathematically integrate but you can't integrate with respect to DC, you can integrate with respect to time. If you integrate intensity with respect to time over pulse and over the sonication time then one finds that ISPTA = DC x ISPPA, multiplication is also an important mathematical function and should be given its due. Lastly, I think there is a typo and ISSPA should read ISPPA

We have corrected the typo and the statement to “mathematically multiplies ISPPA by the continuity of sonication”. [Line 221/222]

Line 454 - I don't think ISPTA is a good measure of "dose." In radiation physics dose is well defined in terms of absorbed energy. The equivalent has yet to be defined for TUS so I would avoid using dose. The ISPTA does relate to TI - although it depends not just on the spatial peak but also on the spatial distribution and the frequency-dependent absorption coefficient of the tissue. I would just avoid the use of "dose" until the field has a better idea of what is going on.

We have cut this phrase on dose as suggested.

Page 16 Box 1 - TI is defined as diagnostic ultrasound imaging it is based on. Also, I think TI is dimensionless; it is referenced to a 1-degree temperature rise and so it can be interpreted in terms of celsius or kelvin; but to be technically accurate it is dimensionless.

We have made TI dimensionless in Box 1

Page 17 Box 2 - Here you have no units for TI - which is correct but inconsistent with Box 1. But the legend suggests a 2 K temperature rise where as your Box allows for 6 K. The value of 6 is consistent with FDA but my understanding of the BMUS guidelines is the TI must be less than or equal to 0.7 for unlimited time or less than 3 if the duration is less than 1 minute. I accept that the table is labelled FDA limits, but the bold table caption is "Recommendations for TUS parameters" I think you should give the ITRUSST values rather than FDA.

We have revised this Box legend to better distinguish the FDA and ITRUSST recommendation where they differ (e.g., the importance of ISPTA and the TI values). See revised legend for Box 2.

Page 18 Box 3 - Not sure what this is trying to show? Also, what is "higher intensity" and "lower intensity"?

Why not just give a range of values in each box?

We agree that the higher and lower intensities likely to lead to enhancement or suppression are poorly defined and have noted this in the legend: “Note that the threshold for ISPPA qualifying as ‘higher’ or ‘lower’ intensity is currently poorly understood, or may non-linearly interact with other factors” [Line 751/754, Box 3].

Line 444 - The hypotheses should be stated more clearly. Maybe I am just dense, but it is not obvious to me from box 3.

We provide the basis for the hypotheses in the manuscript text on the paragraph [Lines 106-179].

Line 481/482 - The intensity of a diagnostic ultrasound system is very well characterised. It just might be that the authors didn't report it. It is not clear what is meant by the "continuity." I guess it's to do with pulsing - which is also well defined but perhaps also not reported.

We agree and have revised this as follows “For the meta-analysis, we only included studies that either reported a basic set of TUS stimulation parameters or those sufficient for estimating the required parameters or those sufficient for estimating the required parameters necessary for the meta-analysis” [Lines 256/258]

Figure 2 - What is the purpose of this figure? Did you carry out simulations for all the studies? It doesn't seem to be relevant to the data here.

This figure illustrates the TUS targeting approach and simulations, in this case conducted in k-plan. These were conducted to evaluate approximations to ISPPA in brain values from the studies that did not report these values [Lines 264/268]).  

Figure 4 - The data in these figures is nice (and therefore doesn't need to have a NICE curve) To me it clearly shows that the data in the literature does not obviously segment into enhancement vs suppression with DC. I suspect it is the same with PRF. I think it would have been better if C and D had PRF on the horizontal axis for on-line and off-line so that effect could be seen more clearly.

We have kept the NICE curve only for a reference that some readers familiar with the NICE model might want to see overlaid in the figure, but have ensured that the text throughout makes clear that the NICE model predictions are not as statistically robust as initially anecdotally thought. PRF results are not significant but we do show a panel with the PRF measures on one axis (Fig. 4D). Figure 5 also shows box plot results with PRF as well as the other key TUS parameters. Moreover, in the inTUS resource we have provided an app for users to explore the data (https://benslaterneuro.shinyapps.io/Caffaratti_inTUS_Resource/).

Figure 5 - The text on the axes is too small to read. Was the DC significant for both on-line and offline? What about ISPPA for off-line. At least by eye, it looks as different as DC. Figure 5C doesn't add anything.

We have boosted the font for Figure 5 and have cut panel 5C since it was not adding much. We have also checked whether DC parameter was significant separately for on-line and off-line effects, but the sample sizes were too small for significance, and the statistical test was not significantly different for Online and Offline effects even in the 12025 database. Therefore they might look stronger for Offline effects in some of the plots in Figure 5, but are currently statistically indistinguishable [Lines 347/348].

Table 1 - There is a typo in the 3rd column. FF should have units of kHz, not KHz. In addition, SD should have units of s as that is the SI symbol for seconds. I would swap columns 9 and 10 so that ISPPA in water and ISPPA in the brain are next to each other.

We have corrected the typo in the 3rd column and ensured that units are kHz. SD in the tables has units of ‘s’ for seconds and have put ISPPA in water and in brain next to each other in the data tables.

Line 767 - "M.K. was supported..." There are TWO MKs in the author list.

We have changed this to M.Ka. for Marcus Kaiser.

Author response:

The following is the authors’ response to the original reviews

We thank the reviewers and editors for their careful consideration of our work and pointing out areas where the current version lacked clarity or necessary experiments. Based on the reviews we have made the following significant changes to the revised version:

(1) Revised the text to focus on the distinct pathogen responses to indole in isolation versus fecal material.

We believe the key takeaway from this work is that the native context of a given effector, in this case indole, can elicit markedly different bacterial responses compared to the pure compound in isolation. This is because natural environments contain multiple, often conflicting, stimuli that complicate predictions of overall chemotactic behavior. For example, while indole has been proposed to mediate chemorepulsion and contribute to colonization resistance against enteric pathogens, our findings challenge this model. We provide evidence that feces, the intestinal source of indole, actually induces attraction, and that indole taxis may in fact benefit the pathogen through prioritizing niches with low microbial competition. Put another way, the biological reservoir of indole, fecal material, generates an attraction response but indole regulated the degree of attraction.

Most current understanding of chemotaxis is based on responses to individual, purified effectors. Our study highlights the need to investigate chemotactic responses in the presence of native mixtures, which better reflect the complexity of natural environments and may reveal new functional insights relevant for disease.

Reviewer comments indicated that these core points above were not clearly conveyed in the previous version, and that the manuscript's logical flow needed improvement. In this revised version, we have substantially rewritten the text and removed extraneous content to sharpen the focus on these central findings. We have also aligned our discussion more closely with the experimental data. While we appreciated the reviewers’ thoughtful suggestions, we chose not to expand on topics that fall outside the scope of our current experiments.

(2) Provide new chemotaxis data with mixtures of fecal effectors (Fig. 5).

Related to the above, the reviewers and editors brought up concerns that our discovery of pathogen fecal attraction was underexplored. Although we showed Tsr to be important for mediating fecal attraction, even the tsr mutant showed attraction to a lesser degree, and the reviewers noted that we did not identify what other fecal attractants could be involved.

Fecal material is a complex biological material (as noted by Reviewer 3) and contains effectors already characterized as chemoattractants and chemorepellents. It would be ideal to be able to perform some experiment where individual effectors are removed from fecal material and then quantify chemotaxis. We considered methods to do this but ultimately found this approach unfeasible. Instead, we employed a reductionist approach and developed a synthetic approximate of fecal material containing a mixture of known chemoeffectors at fecal-relevant concentrations (Fig. 5). We used this defined system as a way to test the specific roles of the Tsr effectors L-Ser (attractant) and indole (repellent) in relation to glucose, galactose, and ribose (sensed through the chemoreceptor Trg), and L-Asp (sensed through the chemoreceptor Tar). We chose these effectors as they have reasonable structure-function relationships established in prior work, and had information available about their concentrations in fecal material. We present these data as a new Figure 5, and also provide videos clearly showing the responses to each treatment (Movies 7-10).

This defined system provided several new insights that help understand and model indole taxis amidst other fecal effectors. First, the complete effector mixture, like fecal treatment, elicits attraction. Second, L-Ser is able to negate indole chemorepulsion in cotreatments of the two effectors, and also other chemoattractants in the absence of L-Ser also negate this repulsion, albeit to a lesser degree, helping to explain why the tsr mutant still shows attraction to fecal material. Lastly, we also show that the degree of attraction in this system is controlled by indole, with mixtures containing greater indole showing less attraction. We feel this is an important addition to the study because it provides a new view on how indole-taxis functions in pathogen colonization; rather than causing the pathogen to swim away (like pure indole does) indole helps the pathogen rank and prioritize its attraction to fecal effector mixtures, biasing navigation toward lower indolecontaining niches.

We also acknowledge that this defined system does not capture all possible interactions. Indeed, there are even a few chemoreceptors in Salmonella for which the sensing functions remain poorly understood. Nonetheless, we believe the data offer mechanistic context for understanding fecal attraction and suggest that factors beyond Tsr, L-Ser, and indole also contribute to the observed behaviors, aligning with other data we present.

(3) Provide new data that show that E. coli MG1655, and disease-causing clinical isolate strains of the Enterobacteriaceae Tsr-possessing species E. coli, Citrobacter koseri, and Enterobacter cloacae exhibit fecal attraction (Fig. 4).

An important new finding from this study is our direct test of whether indole-rich fecal material elicits repulsion. Contrary to expectations, given that for E. coli indole is a wellcharacterized strong chemorepellent, we show that fecal material instead elicits attraction in non-typhoidal Salmonella.

Reviewers raised the question of whether our observations regarding indole taxis and attraction to indole-rich feces in Salmonella are similar or relevant to E. coli. While a full dissection of indole taxis in E. coli is beyond the scope of this study and has been the focus of extensive prior research, we sought to address this point by examining whether other enteric pathogens respond similarly to the native indole reservoir, fecal material. To this end, we present new data demonstrating that, like S. Typhimurium, E. coli and other representative enteric pathogens and pathobionts possessing Tsr are also attracted to indole-rich feces (Fig. 4, Movies 4–6, Fig. S4).

Notably, these new results represent some of the first characterizations of chemotactic behavior in the clinical isolates we examined, including E. coli NTC 9001 (a urinary tract infection isolate), Citrobacter koseri, and Enterobacter cloacae, adding another element of novelty to this work.

(4) Repeated all of the explant Salmonella Typhimurium infection studies and added a new experimental control competition between WT and an invasion-deficient mutant (invA).

Although our new colonic explant system was noted as a novelty and strength of this work, it was also seen as a weakness in that some of the results were surprising and difficult to link to chemotactic behavior. Reviewer 3 also brought up the need to be clear about our usage of the term ‘invasion’ in reference to S. Typhimurium entering nonphagocytic host cells, and requested we test an invasion-inhibited mutant (which we do in new experiments, now Fig. S1). We also note that some of the interpretations of these data were made challenging by result variability.

To help address these issues we performed additional replicates for all of our explant experiments (contained within Figure 1, Fig. S1-S2, and Data S1), to provide greater power for our analyses. These new data provide a clearer view of this system that revise our interpretations from the prior version of this study. While treatment with indole alone does suppress the WT advantage over chemotactic mutants for both total colonization and cellular invasion, essentially all other treatments have a similar result with a timedependent increase in both colonization and invasion, dependent on chemotaxis and Tsr. A remaining unique feature of fecal treatment is an increase in the cellular invaded population of the cells at 3 h post-infection. As requested by Reviewer 3, we provide new experimental data showing that in competitions between WT and an invasion-deficient mutant (invA), with fecal material pretreatment, we see the WT has an advantage only for the gentamicin-treated qualifications, providing some support that our model selects for the invaded sub-population. Although we note that the invA still can invade through alternative mechanisms (as discussed in earlier work such as here: https://doi.org/10.1111/1574-6968.12614), so the relative amount of presumed cellular invasion is less than WT, and not zero, in our experiments (Fig. S1).

One point of confusion in the previous version of the text was the assay design for the explant experiments, which is important to understand in order to interpret the results. During the explant infection bacteria are not immersed in the effector treatment solution, rather the tissue is soaked in the effector solution beforehand and then exposed to a 300 µl buffer solution containing the bacteria. This means that the bacteria experience only the residue of that treatment at concentrations far lower. We have added clarity about this through revising Fig. 1 to include a conceptual diagram of the assay (Fig. 1C), and added a new supplementary Fig. S5 that summarizes the explant data in this same conceptual model. We provide detail on the method in the text in lines 115-137. In describing the results, and synthesizing them in the discussion, we now state:

Line 112: “This establishes a chemical gradient which we can use to quantify the degree to which different effector treatments are permissive of pathogen association with, and cellular invasion of, the intestinal mucosa (Fig. 1C).”

And, a new section in the discussion devoted to describing the explant infections:

Line: 366: “Our explant experiments can be thought of as testing whether a layer of effector solution is permissive to pathogen entry to the intestinal mucosa, and whether chemotaxis provides an advantage in transiting this chemical gradient to associate with, and invade, the tissue (Fig. 1C, Fig. S5).”

As mentioned above, we have honed the text to focus on the disparity between the effects of indole alone versus treatments with indole-rich feces to help clarify how these data advance our understanding of the indole taxis in directing pathogenesis. While our explant studies still confirm the role of factors other than L-Ser, indole, and Tsr in directing Salmonella infection and cellular invasion, we now include further analyses of other fecal effectors (described above) that provide some insights into how fecal effectors have some redundancy in their impact.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study shows, perhaps surprisingly, that human fecal homogenates enhance the invasiveness of Salmonella typhimurium into cells of a swine colonic explant. This effect is only seen with chemotactic cells that express the chemoreceptor Tsr. However, two molecules sensed by Tsr that are present at significant concentrations in the fecal homogenates, the repellent indole and the attractant serine, do not, either by themselves or together at the concentrations in which they are present in the fecal homogenates, show this same effect. The authors then go on to study the conflicting repellent response to indole and attractant response to serine in a number of different in vitro assays.

Strengths:

The demonstration that homogenates of human feces enhance the invasiveness of chemotactic Salmonella Typhimurium in a colonic explant is unexpected and interesting. The authors then go on to document the conflicting responses to the repellent indole and the attractant serine, both sensed by the Tsr chemoreceptor, as a function of their relative concentration and the spatial distribution of gradients.

Thank you for your summary and acknowledgement of the strengths of this work. We hope the revised text and additional data we provide further improve your view of the study.

Weaknesses:

The authors do not identify what is the critical compound or combination of compounds in the fecal homogenate that gives the reported response of increased invasiveness. They show it is not indole alone, serine alone, or both in combination that have this effect, although both are sensed by Tsr and both are present in the fecal homogenates. Some of the responses to conflicting stimuli by indole and serine in the in vitro experiments yield interesting results, but they do little to explain the initial interesting observation that fecal homogenates enhance invasiveness.

Thank you for noting these weaknesses. We have provided new data using a defined mixture of fecal effectors to further investigate the roles of L-Ser, indole, and other effectors present in feces that we did not initially study. We have refined our discussion of these results to hopefully improve the clarity of our conclusions. We show now both in explant studies (Fig. 1I) and chemotaxis responses to a defined fecal effector system (Fig. 5) that L-Ser is able to abolish both the suppression of indole-mediated WT advantage and also indole chemorepulsion, respectively. We also show the latter can be accomplished by other fecal chemoattractants (Fig. 5). This is in line with our earlier finding that Tsr, the sensor of indole and L-Ser, is an important mediator of fecal attraction but not the sole mediator.

As this reviewer points out, there are indeed other factors mediating invasion that we do not elucidate here, but we do note these possibilities in the text (lines: 125-127):

“This benefit may arise from a combination of factors, including sensing of host-emitted effectors, redox or energy taxis, and/or swimming behaviors that enhance infection [5,30,31,35].”

Reviewer #2 (Public review):

Summary:

The manuscript presents experiments using an ex vivo colonic tissue assay, clearly showing that fecal material promotes Salmonella cell invasion into the tissue. It also shows that serine and indole can modulate the invasion, although their effects are much smaller. In addition, the authors characterized the direct chemotactic responses of these cells to serine and indole using a capillary assay, demonstrating repellent and attractant responses elicited by indole and serine, respectively, and that serine can dominate when both are present. These behaviors are generally consistent with those observed in E. coli, as well as with the observed effects on cell invasion.

Strengths:

The most compelling finding reported here is the strong influence of fecal material on cell invasion. Also, the local and time-resolved capillary assay provides a new perspective on the cell's responses.

Thank you for acknowledging these aspects of the study.

Weaknesses:

The weakness is that indole and serine chemotaxis does not seem to control the fecal-mediated cell invasion and thus the underlying cause of this effect remains unclear.

In addition, the fact that serine alone, which clearly acts as a strong attractant, did not affect cell invasion (compared to buffer) is somewhat puzzling. Additionally, wild-type cells showed nearly a tenfold advantage even without any ligand (in buffer), suggesting that factors other than chemotaxis might control cell invasion in this assay, particularly in the serine and indole conditions. These observations should probably be discussed.

Addressed above.

Final comment. As shown in reference 12, Tar mediates attractant responses to indole, which appear to be absent here (Figure 3J). Is it clear why? Could it be related to receptor expression?

Thank you for noting this. We now mention this in the discussion. In the course of this work, we encountered a number of apparent inconsistencies, or differences, between what we were observing with S. Typhimurium and what had been reported previously in studies of Tsr function in E. coli. We indeed noted that some studies had investigated a role of Tar for indole taxis (in E. coli), hence why we determined whether, and confirmed, that Tsr is required for indole taxis for S. Typhimurium (Fig. 6).

We do not know the reason for this apparent difference between the two bacteria, but we have previously shown with our same strain of S. Typhimurium IR715, under the same growth assay, and preparation protocol, that L-Asp is a strong chemoattractant for both WT and the tsr mutant (see Glenn et al. 2024, eLife, Fig. 5G: https://iiif.elifesciences.org/lax:93178%2Felife-93178-fig5-v1.tif/full/1500,/0/default.jpg).

This supports that this strain of Salmonella indeed has a functional Tar present and is expressed at a level sufficient for sensing L-Asp. So, if Tar generally mediates indole sensing we do not know why we would not see that in Salmonella. Hence, we do not see any role for Tar in indole chemorepulsion in our strain of study, which is different than reported for E. coli, but we cannot confirm the reason.

Reviewer #3 (Public review):

Summary:

In this manuscript, Franco and colleagues describe careful analyses of Salmonella chemotactic behavior in the presence of conflicting environmental stimuli. By doing so, the authors describe that this human pathogen integrates signals from a chemoattractant and a chemorepellent into an intermediate "chemohalation" phenotype.

Strengths:

The study was clearly well-designed and well-executed. The methods used are appropriate and powerful. The manuscript is very well written and the analyses are sound. This is an interesting area of research and this work is a positive contribution to the field.

Thank you for your comments.

Weaknesses:

Although the authors do a great job in discussing their data and the observed bacterial behavior through the lens of chemoattraction and chemorepulsion to serine and indole specifically, the manuscript lacks, to some extent, a deeper discussion on how other effectors may play a role in this phenomenon. Specifically, many other compounds in the mammalian gut are known to exhibit bioactivity against Salmonella. This includes compounds with antibacterial activity, chemoattractants, chemorepellers, and chemical cues that control the expression of invasion genes. Therefore, authors should be careful when making conclusions regarding the effect of these 2 compounds on invasive behavior.

Thank you for this comment, and we agree with your point. We hope we have revised the text and provided new data to address your concern. We have also chosen for clarity to keep our text close to our experimental data and so have refrained from speculating about some topics, even though you are absolutely correct about the immense complexity of these systems.

It is important that the word invasion is used in the manuscript only in its strictest sense, the ability displayed by Salmonella to enter non-phagocytic host cells. With that in mind, authors should discuss how other signals that feed into the control of Salmonella invasion can be at play here.

Thank you for your recommendation. We have revised the text to hopefully be clearer on our meaning of invasion in regard to Salmonella entering non-phagocytic host cells, essentially changing our usage to ‘cellular invasion’ throughout.

It is also a commonly-used phrase in reference to enteric infections and the colonization resistance conferred by the microbiome to refer to ‘invading pathogens’ (i.e. invasion in the sense of a new microbe colonizing the intestines), For instance, this recent review on Salmonella makes use of the term invading pathogen (https://www.nature.com/articles/s41579-021-00561-4). We acknowledge the confusion by this dual use of the term. We have mostly removed our statements using invasion in this context. We hope our language is clearer in this revised version.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

It was difficult to understand the true intent or importance of the study described in this manuscript. The first figure in the paper showed that a Salmonella Typhimurium strain lacking either CheY, and thus incapable of any chemotaxis, or the Tsr chemoreceptor, and thus incapable of sensing serine or indole, was modestly inferior to the wild-type version of that strain in invading the cells of a swine colonic explant. It then showed that, in the presence of a human fecal homogenate, the wild-type strain had a much greater advantage in invading the colonic cells. Thus, the presence of the fecal homogenate significantly increased invasiveness in a way that depends on chemotaxis and the Tsr chemoreceptor.

As human feces were determined to contain 882 micromolar indole and 338 micromolar serine, the effects of those concentrations of either indole or serine alone or in combination were tested. The somewhat surprising finding was that neither indole nor serine alone nor in combination changed the result from the experiment done with just buffer in the colonic explant.

The clear conclusion of this initial study is that both chemotaxis in general and chemotaxis mediated by Tsr improve the invasiveness of S. Typhimurium. They provide a much bigger advantage in the presence of human feces. However, two molecules present in the feces that are sensed by Tsr, serine, and indole, seem to have no effect on invasiveness either alone or in combination.

At this point, the parsimonious interpretation is that there is something else in human feces that is responsible for the increased invasiveness, and the authors acknowledge this possibility. However, they do not take what appears to be the obvious approach: to look for additional factors in human feces that might be responsible, either by themselves or in combination with indole and/or serine, for the increased invasiveness. Instead, they carry out a detailed examination of the counteracting effects of indole as a repellent and of serine as an attractant as a function of their relative concentrations and their spatial distributions.

Thank you for your comments. In our revised version, we have undertaken some additional studies of other fecal effectors that help better understand the relationship between L-Ser and indole, but also the roles of other chemoattractants (glucose, galactose, ribose, L-Asp) in mediating fecal attraction (Fig. 5). We agree with the reviewer and conclude that fecal attraction and the cell invasion phenotype mediated by fecal treatment are influenced by factors other than only Tsr, indole, and L-Ser. Our new data do show that L-Ser is sufficient to block both the invasion suppression effects of indole (negating the WT advantage) and also indole chemorepulsion, therefore making our detailed examination of the counteracting effects more relevant for understanding this system.

What they find is what other studies have shown, primarily with S. Typhimurium's relative, the gamma-proteobacterium Escherichia coli.

At high indole and low serine concentrations, the repulsion by indole wins out. At low indole and high serine concentrations, attraction by serine wins out. What is perhaps novel is what happens at an intermediate ratio of concentrations. Repulsion by indole dominates at short distances from the source, so there is a zone of clearing. At longer distances, attraction by serine dominates, so there is an accumulation of cells in a "halo" around the zone of clearing. Thus, assuming that serine and indole diffuse equally, the repulsive effect of indole dominates until its concentration falls below some critical level at which the concentration of serine is still high enough to exert an attractive effect.

They go on to show, using ITC, that serine binds to the periplasmic ligand-binding domain (LBD) of Tsr, something that has been studied extensively with very similar E. coli Tsr.

They also show that indole does not bind to the Tsr LBD, which also is known for E. coli Tsr.

This would be newsworthy only if the results were different for S. Typhimurium than for E. coli. As it is, it is merely confirmatory of something that was already known about Tsr of enteric bacteria.

An idea that the authors introduce, if I understand it correctly, is that a repellent response to something in feces, perhaps indole, drives S. Typhimurium chemotactically competent cells out of the colonic lumen and promotes invasion of the bacteria into the cells of the colonic lining. If the feces contain both an attractant and a repellent, bacteria might be attracted by the feces to the lining of the intestine and then enter the colonic cells to escape a repellent, perhaps indole. That is an interesting proposition.

In summary, I think that the initial experimental approach is fine. I do not understand the failure to follow up on the effect of the fecal homogenates in promoting invasion by chemotactic bacteria possessing Tsr. It seems there must be something else in the homogenates that is sensed by Tsr. Other amino acids and related compounds are also sensed by Tsr. Perhaps it is energy or oxygen taxis, which is partially mediated by Tsr, as the authors acknowledge.

Much of the work reported here is quasi-repetitive with work done with E. coli Tsr. Minimally, previous work on E. coli Tsr should be explained more thoroughly rather than dealt with only as a citation.

Thank you for your comments.

We would like to confirm our agreement that E. coli and S. enterica indeed possess similarities. They are Gammaproteobacteria and inhabit/infect the gut. But also we note they diverged evolutionarily during the Jurassic period (ca. 140 million years ago, see: PMC94677). In the context of colonizing humans, the former is a pathobiont, indoleproducer, and a native member of the microbiome, whereas the latter is a frank pathogen and does not produce indole. Hence, there are many reasons to believe one is not an approximate of the other, especially when it comes to causing disease.

We agree that much of what is known about indole taxis has come from excellent studies in well-behaved laboratory strains of E. coli, a powerful model. We believe that expanding this work to include clinically relevant pathogens is important for understanding its role in human disease. In this study, we contribute to that broader understanding by providing new mechanistic insights into Tsr-mediated indole taxis in S. Typhimurium, along with data demonstrating fecal attraction in other enteric pathogens and pathobionts. These findings help define a more general role for Tsr in enteric colonization and disease. While some of our results indeed confirm and extend prior findings, we respectfully believe that such confirmation in relevant pathogenic strains adds value to the field.

Regarding our ITC studies, to our knowledge no other study has investigated, using ITC whether indole does or does not bind the LBD (which we show it does not), nor investigated whether it interferes with L-Ser sensing (which we show it does not). Hence, these are not duplicate findings, although we do acknowledge this leaves the mechanism of indolesensing undiscovered. If we are incorrect in this regard, please provide us a citation and we will be happy to include it and revise our comments.

We now clarify in the text on lines 378-381: “While these leave the molecular mechanism of indole-sensing unresolved, it does eliminate two possibilities that have not, to our knowledge, been tested previously. Overall, our data add support to the hypothesis that a non-canonical sensing mechanism is employed by Tsr to respond to indole [8,18,69].”

Lastly, as noted by the reviewer, and which we mention in the text, essentially all prior studies on indole taxis were conducted in E. coli, and this is not what is new and novel about the work we present, which is focused on S. Typhimurium and testing the prediction that fecal indole protects against pathogen invasion. We have added in a few additional points of comparisons between our results and prior studies. While we appreciate that much understanding has come from E. coli as a model for indole taxis, we feel discussing prior work in extensive detail would be more suitable for a review and would occlude our new findings about Salmonella, and other enterics.

In an earlier version of the manuscript, we included more background on E. coli indole taxis. However, we found that the historical literature in this area was somewhat inconsistent, with different assays using varying time points and indole concentrations, often leading to results that were difficult to reconcile. Providing sufficient context to explain these discrepancies required considerable space and, ultimately, detracted from the focus of our current study. Hence, we have only brought in comparisons with E. coli where most relevant to the present work. Also, we provide new data that E. coli also exhibits fecal attraction, and so there is reason to believe the mechanisms we study here are also relevant to that system.

Some minor points

(1) Hyphens are not needed with constructs like "naturally occurring" or "commonly used".

Thank you. Revisions made throughout.

(2) The word "frank" as in "frank pathogen" seems odd. It seems "potent" would be better.

Thank you for this comment. Per your recommendation, we have removed this term.

The term ‘frank pathogen’ is standard usage in the field of bacterial pathogenesis in reference to a microbe that always causes disease in its host (in this case humans) and causes disease in otherwise healthy hosts (example: https://www.sciencedirect.com/science/article/pii/S1369527420300345). We actually used this specific term to distinguish an aspect of novelty of our study because E. coli can, sometimes, be a pathogen (i.e. a pathobiont) and of course E. coli indole taxis has been previously studied. Ours is the first study of indole taxis in a frank pathogen.

(3) It is unnecessary to coin a new word, chemohalation, to describe a phenomenon that is a simple consequence of repulsion by higher concentrations of a repellent and attraction by lower concentrations of attractant to generate a halo pattern of cell distribution.

Thank you for your opinion on this. We have softened our statements on this point, and in the newly revised version of the text less space is devoted to this idea. We now state in line 304-307:

“There exists no consensus descriptor for taxis of this nature, and so we suggest expanding the lexicon with the term “chemohalation,” in reference to the halo formed by the cell population, and which is congruent with the commonly-used terms chemoattraction and chemorepulsion.”

We appreciate the reviewer’s perspective and agree that the behavior we describe can be viewed as the result of competing attractant and repellent cues. However, we find that the traditional framework of “chemoattraction” and “chemorepulsion” is often insufficient to describe the spatial positioning behaviors we observe in our system. In our experience presenting and discussing this work, especially with audiences outside the chemotaxis field, it has been challenging to convey these dynamics clearly using only those two terms.

For this reason, we introduced the term chemohalation to describe this more nuanced behavior, which appears to reflect a balance of signals rather than a simple unidirectional response. More bacteria enter the field of view, but they are clearly positioned differently than regular ‘chemoattraction.’ We also note that Reviewers 2 and 3 did not raise concerns about the term, and after careful consideration, we have opted to retain it in the revised manuscript.

Reviewer #2 (Recommendations for the authors):

Lines 143-156 seem somewhat overcomplicated and may be confusing. For example: in line 143: "However, when colonic tissue was treated with purified indole at the same concentration, the competitive advantage of WT over the chemotactic mutants was abolished compared to fecaltreated tissue...". But indole was tested alone, so it did not abolish the response; rather the absence of fecal material did.

We appreciate your point. We have made revisions throughout to help improve the clarity of how we discuss the explant infection data and provide new visuals to help explain the experiment and data (Fig. 1C, Fig. S5).

Reviewer #3 (Recommendations for the authors):

(1) Line 46 - Are references 9-11 really about topography?

Thank you. You are correct. Revised and eliminated this statement.

(2) Lines 87-89 - It seems to me that a bit more information on this would be helpful to the reader.

In our revision of the text, to make it more centered on our primary findings of the differences between indole taxis when indole is the sole effector versus amidst other effectors, we have removed this section.

(3) Line 112 - When mentioning the infection of the cecum and colon, authors should specify that this is in mice.

Thank you for this comment. In our revised version we provide references both for animal model infections and work in human patients (ex: https://www.sciencedirect.com/science/article/abs/pii/S0140673676921000)

We have revised our statement to be (Line 99-100: “Salmonella Typhimurium preferentially invades tissue of the distal ileum but also infects the cecum and colon in humans and animal models [42–46].”

(4) Lines 122-123 - Authors state that "This experimental setup simulates a biological gradient in which the effector concentration is initially highest near the tissue and diffuses outward into the buffer solution.". Was this experimentally demonstrated? If not, authors should tone this down.

We have removed this comment and instead present a conceptual diagram illustrating this idea (Fig. 1C). Also, addressed by above.

(5) When looking at the results in Figure 1, I wonder what the results of this experiment would be if the authors tested an invasion mutant of Salmonella. In a strain that is able to perform chemotaxis (attraction and repulsion) but unable to actively invade, would there be a phenotype here? Is it possible that the fecal material affects cellular uptake of Salmonella, independently of active invasion? I don't think the authors necessarily need to perform this experiment, but I think it could be informative and this possibility should at least be discussed.

Thank you for your comments and suggestions. We have included new data of an explant co-infection experiment with WT and an invasion-deficient mutant invA (Fig. S1). Under these conditions, WT exhibits an advantage in the gentamicin-treated homogenate, but not the untreated homogenate, suggestive of an advantage in cellular invasion.

However, we did not repeat all experiments with this genetic background. We felt that would be outside the scope of this work, and would probably require dual chemotaxis/invA deletions to assess the impact of each, which also could be difficult to interpret. The hypothesis mentioned by the Reviewer is possible, but we were not able to devise a way to test this idea, as it seems we would need to deactivate all other mechanisms of Salmonella invasion.

(6) Lines 137-140 - Because this is a competition experiment and results are plotted as CI, the reader can't readily assess the impact of human feces on invasion by WT Salmonella.

Thank you for pointing this out. We want to mention that the data are plotted as CI in the main text, but the supplemental contains the disaggregated CFU data (Fig. S1-2) and the numerical values (Data S1).

Please include the magnitude of induction in this sentence, compared to the buffer control.

The text of this section has been changed to account for new data.

Additionally, although unlikely, the presence of the chemotaxis mutants in the same infection may be a confounding factor. In order to irrefutably ascertain that feces induces invasion, I suggest authors perform this experiment with the wildtype strain (and mutant) alone in different conditions.

Thank you for this suggestion, although after careful consideration we have decided not to repeat these explant studies with monoinfections. Coinfections are a common tool in Salmonella pathogenesis studies, including prior chemotaxis studies which our work builds upon (ex: https://pmc.ncbi.nlm.nih.gov/articles/PMC3630101/). The explant experiments, even controlling as many aspects as we did, still show lots of variability and one way to mitigate this is through competition experiments so that each strain experiences the same environment.

We agree that a cost of this approach is that one strain may affect the other, or may alter the environment in a way that impacts the other. Thus, the resulting data must also be understood through this lens. We have revised the text to stay closer to the competitive advantage phenotype.

(7) Line 150 - Authors state that bacterial loads are similar. However, authors should perform and report statistical analyses of these comparisons, at least in the supplementary data.

We have removed this statement as requested. We do note, however, that the mean CFU values across treatments at identical time points appear qualitatively similar, which is an observation that does not require statistical testing.

(8) Lines 154-154 - This seems incorrect, as the effect observed with the mixture of indole and serine is very similar to the addition of serine alone. Therefore, there was no "neutralization" of their individual effects.

We have revised this statement.

(9) Line 159-161 - I strongly suggest authors reword this sentence. I don't think this is the best way to describe these results. The stronger phenotype observed was with the fecal material. Therefore, it is the indole (alone) condition that does not "elicit a response". Focusing on indole too much here ignores everything else that is present in feces and also the fact that there was a drastic phenotype when feces were used.

Thank you for your opinion on this. We believe this is one of the ways in which our earlier draft was unclear. It was actually a primary motivation of this work to test whether there were differences in pathogen infection, mediated by chemotaxis, in the presence of indole as a singular effector or in its near-native context in fecal material, and our revised text centers our study around this question. We believe this distinction is important for the reasons mentioned earlier.

Relative to buffer treatment, indole changes the behavior of the system, eliminating the WT advantage, and this is the effect we refer to. We have made many revisions to the text of these sections and hope it better conveys this idea. We expect we may still have differences regarding the interpretation of these results, but regardless, thank you for your suggestions and we have tried to implement them to improve the clarity of the text.

(10) Line 162 - Again, I disagree with this. Indole does not have an effect to be cancelled out by serine.

Addressed above, and this text has been changed. Also, we provide new chemotaxis data that at fecal-relevant concentrations of indole and L-Ser, indole chemorepulsion is overridden (Fig. 5).

(11) Lines 166-168 - Again, this is a skewed analysis. Indole and serine could not possibly provide an "additive effect" since they do not provide an effect alone. There is nothing to be added.

This text has been deleted.

(12) Lines 168-170 - Most of the citations provided to this sentence are inadequate. Our group has previously shown that the mammalian gut harbors thousands of small molecules (Antunes LC et al. Antimicrob Agents Chemother 2011). You obviously do not have to cite our work, but there is significant literature out there about the complexity of the gut metabolome.

Thank you for this comment. We have revised this particular text, but do make mention of potential other effectors driving these effects, which was also requested by the other reviewers.

Your work and others indeed support there being thousands of molecules in the gut, but our work centers on chemotaxis, and bacteria have a small number of chemoreceptors and only sense a very tiny fraction of these molecules as effectors. Since the impacts of infection of the explants depends on chemotaxis, we keep our comments restricted to those, but agree that there are likely many interactions involved, such as those impacting gene expression.

Please note our more detailed description of the explant infection assay (and shown in Fig. 1C) that may change your view on the significance of non-chemotaxis effects. The bacteria only experience the effectors at low concentration, not the high concentration that is used to soak and prepare the tissue prior to infection.

(13) Figure 2 - The letter 'B' from panel B is missing.

Thank you very much for bringing this oversite to our attention. We have fixed this.

(14) Legend of Figure 3 - Panel J is missing a proper description. Figure legends need improvement in general, to increase clarity.

Thank you for noting this. This is now Fig. 6E. We have provided an additional description of what this panel shows. We have edited the legend text to read: “E. Shows a quantification of the relative number of cells in the field of view over time following treatment with 5 mM indole for a competition experiment with WT and tsr (representative image shown in F).”

We also have made other edits to figure legends to improve their clarity and add additional experimental details and context. By breaking up larger figures into smaller figures, we also hope to have improved the clarity of our data presentation.

(15) Lines 264-265 - Maybe I am missing something, but I do not see the ITC data for serine alone.

We have clarified in the text that this was measured in our previous study https://elifesciences.org/articles/93178). The present study is a ‘Research Advance’ article format, and so builds on our prior observation.

We have revised the text to read: “To address these possibilities, we performed ITC of 50 μM Tsr LBD with L-Ser in the presence of 500 μM indole and observed a robust exothermic binding curve and KD of 5 µM, identical to the binding of L-Ser alone, which we reported previously (Fig. 6H) [36].”

(16) Lines 296-297 - What is the effect of these combinations of treatments on bacterial cells? I commend the authors for performing the careful growth assays, but I wonder if bacterial lysis could be a factor here. I am not doubting the effect of chemotaxis, but I am wondering if toxic effects could be a confounding factor. For instance, could it be that the "avoidance" close to the compound source and subsequent formation of a halo suggest bacterial death and lysis? I suggest the authors perform a very simple experiment, where bacteria are exposed to the compounds at various concentrations and combinations, and cells are observed over time to ensure that no bacterial lysis occurs.

Thank you for mentioning this possibility. If we understand correctly, the Reviewer is asking if the chemohalation effect we report could be from the bacteria lysing near the source. Our data actually argue against this possibility through a few lines of evidence.

First, if this were the case in experiments with the cheY mutant, we would also see an effect near the source. But actually, in experiments with either the cheY mutant or the tsr mutant, neither of which can sense indole, the bacteria just ignore the stimulus and show an even distribution (see current Fig. 6F).

Second, our calculations suggest that in the chemotaxis assay (CIRA), the bacteria only experience rather low local concentration of indole, mostly I the nM concentration range, because as soon as the effector treatment is injected into the greater volume, it is immediately diluted. This means the local concentration is far below what we see inhibits growth of the cells in the long run and may not be toxic (Fig. 7, Fig. S3).

Lastly, in the representative video presented we can observe individual cells approach and exit the treatment (Movie 11). Due to the above we have not performed additional experiments to test for lysis.

(17) Lines 310-311 - Isn't this the opposite of the model you propose in Figure 5? The higher the concentration of indole in the lumen the more likely Salmonella is to swim away from it and towards the epithelium, favoring invasion, no?

We appreciate the opportunity to clarify this point and apologize for any confusion caused. In response, we have revised the text to place less emphasis on chemohalation, and the specific statement and model in question have now been removed. Instead, we provide a summary of our explant data in light of the other analyses in the study (Fig. S5).

What we meant here was in relation to the microscopic level, not whether or not a host/intestine is colonized. To put it another way, we think our data supports that the pathogen colonizes and infects the host regardless of indole presence, but it uses indole as a means to prioritize which tissues are optimal for colonization at the microscopic level. The prediction made by others was that bacteria swim away from indole source and therefor this could prevent or inhibit pathogen colonization of the intestines, which our data does not support.

(18) Lines 325-326 - Maybe, but feces also contain several compounds with antibacterial activity, as well as other compounds that could elicit chemorepulsion. This should be stated and discussed.

We have removed this statement since we did not explicitly test the growth of the bacteria with fecal treatments. We have refrained from speculating further in the text since we do not have direct knowledge of how that relationship with differing effectors could play out.

We agree with the reviewer that the growth assays are reductionist and give insight only into the two effectors studied. We provide evidence from several different types of enterics that they all exhibit fecal attraction, and it seems unlikely the bacteria would be attracted to something deleterious, but we have not confirmed.

(19) Lines 371-374 - How preserved (or not) is the mucus layer in this model? The presence of an inhibitory molecule in the lumen does not necessarily mean that it will protect against invasion. It is possible that by sensing indole in the lumen Salmonella preferentially swims towards the epithelium, thus resulting in enhanced evasion.

The text in question has been removed. However, we acknowledge the reviewer’s point, and that these explant tissues do not fully model an in vivo intestinal environment. Other than a gentle washing with PBS to remove debris prior to the experiment the tissue is not otherwise manipulated, and feasibly the mucus layer is similar to its in vivo state.

In mentioning this hypothesis about indole, which our data do not support, we were echoing a prediction from the field, proposed in the studies we cite. We agree with the reviewer that there were other potential outcomes of indole impacting chemotaxis and invasion, and indeed our data supports that.

(20) Lines 394-395 - The authors need to remember that the ability to invade the intestinal epithelium is not only a product of chemoattraction and repulsion forces. Several compounds in the gut are used by Salmonella as cues to alter invasion gene expression. See PMID: 25073640, 28754707, 31847278, and many others.

Thank for you for this point, and we now include these citations. We have revised the text in question, stating:

“In addition to the factors we have investigated, it is already well-established in the literature that the vast metabolome in the gut contains a complex repertoire of chemicals that modulate Salmonella cellular invasion, virulence, growth, and pathogenicity [79–81].”

Our intent is not to diminish the role of other intestinal chemicals but rather to put our new findings into the context of bacterial pathogenesis. We do provide evidence that specific chemoeffectors present in fecal material alter where bacteria localize through chemotaxis, which is one method of control over colonization.

(21) Line 408 - I think it could be hard to observe this using your experimental approach.

Because you need to observe individual cells, the number of cells you observe is relatively small. If, in a bet-hedging strategy, the proportion of cells that were chemoattracted to indole was relatively low you likely would not be able to distinguish it from an occasional distribution close to the repellent source. You may or may not want to discuss this.

Thank you for this observation. It is indeed challenging to both observe large scale population behaviors and also the behaviors of individual cells in the same experiment. Our ability to make this distinction is similar to the approach used in the study we cite, so that is our comparison.

But, if there was a subpopulation that was attracted we would predict a ‘bull’s-eye’ population structure, with some cells attracted and other avoiding the source, which we do not see - we see the halo. So, we find no evidence of the bet-hedging response seen in a different study using E. coli and using different time scales than we have.

(22) Lines 410-411 - What could the other attractants be? Would it be possible/desirable to speculate on this?

We have changed the text here, but we present new data that examines some of these other attractants (Fig. 5).

(23) Line 431 - What exactly do you mean by "running phenotype"? Please, provide a brief explanation.

We have removed this text, but a running phenotype means the swimming bacteria rarely make direction changes (i.e. tumbles), which has been associated with promoting contact with the epithelium, described in the references we cite. Hence, this type of swimming behavior could contribute to the effects we observe in the explant studies, potentially explaining some of the Tsr-mediated advantage that was not dependent on L-Ser/indole.

(24) Line 441 - Other work has shown that feces contain inhibitors of invasion gene expression. The authors should integrate this knowledge into their model. In fact, indole has been shown to repress host cell invasion by Salmonella, so it is important that authors understand and discuss the fact that the impact of indole is multifaceted and not only a reflection of its action as a chemorepellent. PMID: 29342189, 22632036.

We agree with the reviewer about this point, and mention this in the text (lines 55-57): “Indole is amphipathic and can transit bacterial membranes to regulate biofilm formation and motility, suppress virulence programs, and exert bacteriostatic and bactericidal effects at high concentrations [16–18,20–22].”

We have added in the references suggested.

What we test here is the specific hypothesis made by others in the field about indole chemorepulsion serving to dissuade pathogens from colonizing.

For instance, the statement from: https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0190613

“Since indole is also a chemorepellent for EHEC [23], it is intriguing to speculate that in addition to attenuating Salmonella virulence, indole also attenuates the recruitment and directed migration of Salmonella to its infection niche in the GI tract.”

And from: https://doi.org/10.1073/pnas.1916974117

“We propose that indole spatially segregates cells based on their state of adaptation to repel invaders while recruiting beneficial resident bacteria to growing microbial communities within the GI tract.”

And

“Thus, foreign ingested bacteria, including invading pathogens such as E. coli O157:H7 and S. enterica, are likely to be prevented by indole from gaining a foothold in the mucosa.”

As shown by others, indole certainly does have many roles in controlling pathogenesis, and there are other chemicals we do not investigate that control invasion and bacterial growth, but we keep our statements here restricted to chemotaxis since that is what are experiments and data show.

(25) Line 472 - "until fully motile". How long did this take, how variable was it, and how was it determined?

Thank you for asking for this clarification. We have added that the time was between 1-2 h, and confirmed visually. Our methods are similar to those described in earlier chemotaxis studies (ex: 10.1128/jb.182.15.4337-4342.2000).

(26) Line 487 - I worry that the fact fecal samples were obtained commercially means that compound stability/degradation may be a factor to consider here. How long had the sample been in storage? Is this information available?

Thank you for this question. We agree that the fecal sample we used serves as a model system and we cannot rule out that handling by the supplier could potentially alter its contents in some way that would impact bacterial chemosensing. However, we note that the measurements of L-Ser and indole we obtained are in the appropriate range for what other studies have shown.

The fecal sample used for all work in the study were from a single healthy human donor, obtained from Lee Biosolutions (https://www.leebio.com/product/395/fecal-stool-samplehuman-donor-991-18). The supplier did not state the explicit date of collection, nor indicated any specific handline or storage methods that would obviously degrade its native metabolites, but we cannot rule that out. In our hands, the fecal sample was collected and kept frozen at -20 C. For research purposes, portions were extracted and thawed as needed, maintaining the frozen state of the original sample to limit degradation from freeze-thaws.

Author response:

The following is the authors’ response to the previous reviews

Recommendations for the authors:

Reviewing Editor Comments:

The resubmitted version of the manuscript adequately addressed several initial comments made by reviewing editors, including a more detailed analysis of the results (such as those of bilayer thickness). This version was seen by 2 reviewers. Both reviewers recognize this work as being an important contribution to the field of BK and voltage-dependent ion channels in general. The long trajectories and the rigorous/novel analyses have revealed important insights into the mechanisms of voltage-sensing and electromechanical coupling in the context of a truncated variant of the BK channel. Many of these observations are consistent with structural and functional measurements of the channel, available thus far. The authors also identify a novel partially expanded state of the channel pore that is accessed after gating-charge displacement, which informs the sequence of structural events accompanying voltage-dependent opening of BK.

However, there are key concerns regarding the use of the truncated channel in the simulations. While many gating features of BK are preserved in the truncated variant, studies have suggested that opening of the channel pore to voltage-sensing domain rearrangement is impaired upon gating-ring deletion. So the inferences made here might only represent a partial view of the mechanism of electromechanical coupling.

It is also not entirely clear whether the partially expanded pore represents a functionally open, sub-conductance, or another closed state. Although the authors provide evidence that the inner pore is hydrated in this partially open state, in the absence of additional structural/functional restraints, a confident assignment of a functional state to this structure state is difficult. Functional measurements of the truncated channel seem to suggest that not only is their single channel conductance lower than full-length channels, but they also appear to have a voltage-independent step that causes the gates to open. It is unclear whether it is this voltage-independent step that remains to be captured in these MD trajectories. A clean cut resolution of this conundrum might not be feasible at this time, but it could help present the various possibilities to the readers.

We appreciate the positive comments and agree that there will likely be important differences between the mechanistic details of voltage activation between the Core-MT and full-length constructs of BK channels. We also agree that the dilated pore observed in the simulation may not be the fully open state of Core-MT.

Nonetheless, the notion that the simulation may not have captured the full pore opening transition or the contribution of the CTD should not render the current work “incomplete”, because a complete understanding of BK activation would be an unrealistic goal beyond the scope of this work. We respectfully emphasize that the main insights of the current simulations are the mechanisms of voltage sensing (e.g., the nature of VSD movements, contributions of various charged residues, how small charge movements allow voltage sensing, etc.) as well as the role of the S4-S5-S6 interface in VSD-pore coupling. As noted by the Editor and reviewers, these insights represent important steps towards establishing a more complete understanding of BK activation.

Below are the specific comments of the two experts who have assessed the work and made specific suggestions to improve the manuscript.

Reviewer #1 (Recommendations for the authors):

(1) Although the successful simulation of V-dependent K+ conduction through the BK channel pore and analysis of associated state dependent VSD/pore interactions and coupling analysis is significant, there are two related questions that are relevant to the conclusions and of interest to the BK channel community which I think should be addressed or discussed.

One key feature of BK channels is their extraordinarily large conductance compared to other K+ selective channels. Do the simulations of K+ conductance provide any insight into this difference? Is the predicted conductance of BK larger than that of other K+ channels studied by similar methods? Is there any difference in the conductance mechanism (e.g., the hard and soft knock-on effects mentioned for BK)?

The molecular basis of the large conductance of BK channels is indeed an interesting and fundamental question. Unfortunately, this is beyond the scope of this work and the current simulation does not appear to provide any insight into the basis of large conductance. It is interesting to note, though, the conductance is apparently related to the level of pore dilation and the pore hydration level, as increasing hydration level from ~30 to ~40 waters in the pore increases the simulated conductance from ~1.5 to 6 pS (page 8). This is consistent with previous atomistic simulations (Gu and de Groot, Nature Communications 2023; ref. 33) showing that the pore hydration level is strongly correlated with observed conductance. As noted in the manuscript, the conductance mechanism through the filter appears highly similar to previous simulations of other K+ channels (Page 8). Given the limit conductance events observed in the current simulations, we will refrain from discussing possible basis of the large conductance in BK channels except commenting on the role of pore hydration (page 8; also see below in response to #5).

The pore in the MD simulations does not open as wide as the Ca-bound open structure, which (as the authors note) may mean that full opening requires longer than 10 us. I think that is highly likely given that the two 750 mV simulations yielded different degrees of opening and that in BK channels opening is generally much slower than charge movement. Therefore, a question is - do any of the conclusions illustrated in Figures 6, S5, S6 differ if the Ca-bound structure is used as the open state? For example, I expect the interactions between S5 and S6 might at least change to some extent as S6 moves to its final position. In this case, would conclusions about which residues interact, and get stronger or weaker, be the same as in Figures S6 b,c? Providing a comparison may help indicate to what extent the conclusions are dependent on achieving a fully open conformation.

We appreciate the reviewer’s suggestion and have further analyzed the information flow and coupling pathways using the simulation trajectory initiated from the Ca²⁺-bound cryo-EM structure (sim 7, Table S1). The new results are shown in two new SI Figures S7 and S8, and new discussion has been added to pages 14-15. Comparing Figures 5 and S7, we find that dynamic community, coupling pathways, and information flow are highly similar between simulation of the open and closed states, even though there are significant differences in S5 contacts in the simulated open state vs Ca²⁺-bound open state (Figure S8). Interestingly, there are significant differences in S4-S5 packing in the simulated and Ca²⁺-bound open states (Figure S8 top panel), which likely reflect important difference in VSD/pore interactions during voltage vs Ca²⁺ activation.

(2) P4 Significance -"first, successful direct simulation of voltage-activation"

This statement may need rewording. As noted above Carrasquel-Ursulaez et al.,2022 (reference 39) simulated voltage sensor activation under comparable conditions to the current manuscript (3.9 us simulation at +400 mV), and made some similar conclusions regarding R210, R213 movement, and electric field focusing within the VSD. However, they did not report what happens to the pore or simulate K+ movement. So do the authors here mean something like "first, successful direct simulation of voltage-dependent channel opening"?

We agree with the reviewer and have revised the statement to “ … the first successful direct simulation of voltage-dependent activation of the big potassium (BK) channel, ..”

(3) P5 "We compare the membrane thickness at 300 and 750 mV and the results reveal no significant difference in the membrane thickness (Figure S2)"

The figure also shows membrane thickness at 0 mV and indicates it is 1.4 Angstroms less than that at 300 or 750 mV. Whether or not this difference is significant should be stated, as the question being addressed is whether the structure is perturbed owing to the use of non-physiological voltages (which would include both 300 and 750 mV).

We have revised the Figure S2 caption to clarify that one-way ANOVA suggest the difference is not significant.

(4) P7 "It should be noted that the full-length BK channel in the Ca2+ bound state has an even larger intracellular opening (Figure 2f, green trace), suggesting that additional dilation of the pore may

occur at longer timescales."

As noted above, I agree it is likely that additional pore dilation may occur at longer timescales. However, for completeness, I suppose an alternative hypothesis should be noted, e.g. "...suggesting that additional dilation of the pore may occur at longer timescales, or in response to Ca-binding to the full length channel."

This is a great suggestion. Revised as suggested.

(5) Since the authors raise the possibility that they are simulating a subconductance state, some more discussion on this point would be helpful, especially in relation to the hydrophobic gate concept. Although the Magleby group concluded that the cytoplasmic mouth of the (fully open) pore has little impact on single channel conductance, that doesn't rule out that it becomes limiting in a partially open conformation. The simulation in Figure 3A shows an initial hydration of the pore with ~15 waters with little conductance events, suggesting that hydration per se may not suffice to define a fully open state. Indeed, the authors indicate that the simulated open state (w/ ~30-40 waters) has 1/4th the simulated conductance of the open structure (w/ ~60 waters). So is it the degree of hydration that limits conductance? Or is there a threshold of hydration that permits conductance and then other factors that limit conductance until the pore widens further? Addressing these issues might also be relevant to understanding the extraordinarily large conductance of fully open BK compared to other K channels.

We agree with the reviewer’s proposal that pore hydration seems to be a major factor that can affect conductance. This is also well in-line with the previous computational study by Gu and de Groot (2023). We have now added a brief discussion on page 8, stating “Besides the limitation of the current fixed charge force fields in quantitively predicting channel conductance, we note that the molecular basis for the large conductance of BK channels is actually poorly understood (78). It is noteworthy that the pore hydration level appears to be an important factor in determining the apparent conductance in the simulation, which has also been proposed in a previous atomistic simulation study of the Aplysia BK channel (33).”

Minor points

(1) P5 "the fully relaxed pore profile (red trace in Figure S1d, top row) shows substantial differences compared to that of the Ca2+-free Cryo-EM structure of the full-length channel."

For clarity, I suggest indicating which is the Ca-free profile - "... Ca2+-free Cryo-EM structure of the full-length channel (black trace)."

We greatly appreciate the thoughtful suggestion. Revised as suggested.

(2) P8 "Consistent with previous simulations (78-80), the conductance follows a multi-ion mechanism, where there are at least two K+ ions inside the filter"

For clarity, I suggest indicating these are not previous simulations of BK channels (e.g., "previous simulations of other K+ channels ...").

Author response: Revised as suggested. Thank you.

(3) Figure 2, S1 - grey traces representing individual subunits are very difficult to see (especially if printed). I wonder if they should be made slightly darker. Similar traces in Figure 3 are easier to see.

The traces in Figure S1 are actually the same thickness in Figure 3 and they appear lighter due to the size of the figure. Figure 2 panels a-c have been updated to improve the resolution.

(4) Figure 2 - suggest labeling S6 as "S6 313-324" (similar to S4 notation) to indicate it is not the entire segment.

Figure 2 panel d) has been updated as suggested.

(5) Figure 2 legend - "Voltage activation of Core-MT BK channels. a-d)..."

It would be easier to find details corresponding to individual panels if they were referenced individually. For example:

"a-d) results from a 10-μs simulation under 750 mV (sim2b in Table S1). Each data point represents the average of four subunits for a given snapshot (thin grey lines), and the colored thick lines plot the running average. a) z-displacement of key side chain charged groups from initial positions. The locations of charged groups were taken as those of guanidinium CZ atoms (for Arg) and sidechain carboxyl carbons (for Asp/Glu) b) z-displacement of centers-of-mass of VSD helices from initial positions, c) backbone RMSD of the pore-lining S6 (F307-L325) to the open state, and d) tilt angles of all TM helices. Only residues 313-324 of S6 were included inthe tilt angle calculation, and the values in the open and closed Cryo-EM structures are marked using purple dashed lines. "

We appreciate the thoughtful suggestion and have revised the caption as suggested.

(6) Figure S1 - column labels a,b,c, and d should be referenced in the legend.

The references to column labels have been added to Figure S1 caption.

(7) References need to be double-checked for duplicates and formatting.

a) I noticed several duplicate references, but did not do a complete search: Budelli et al 2013 (#68, 100), Horrigan Aldrich 2002 (#22,97), Sun Horrigan 2022 (#40, 86), Jensen et al 2012 (#56,81).

b) Reference #38 is incorrectly cited with the first name spelled out and the last name abbreviated.

We appreciate the careful proofreading of the reviewer. The duplicated references were introduced by mistake due to the use of multiple reference libraries. We have gone through the manuscript and removed a total of 5 duplicated references.

Response to additional reviewer comments

My only new comment is that the numbering of residues in Fig. S8 does not match the standard convention for hSlo and needs to be doublechecked. For the residues I checked, the numbers appear to be shifted 3 compared hSlo (e.g. Y315, P317, E318, G324 should be Y318, P320, E321, G327).

We greatly appreciate the reviewer for catching the errors in residue labels. Figure S8 has now been updated to include correct residue labels. Thanks!

Reviewer #2 (Recommendations for the authors):

This manuscript has been through a previous level of review. The authors have provided their responses to the previous reviewers, which appear to be satisfactory, and I have no additional comments, beyond the caveats concerning interpretations based on the truncated channel, which are noted above.

We greatly appreciate the constructive comments and insightful advice. Please see above response to the Reviewing Editor’s comments for response and changes regarding the caveats concerning interpretations of the current simulations.

This work has been peer reviewed in GigaScience (https://doi.org/10.1093/gigascience/giaf054), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer: Victor Quesada

This work offers a in improved version of the reference genome for the loggerhead sea turtle. The authors have also analyzed the methylation patterns of blood obtained from different individuals and with two methods. The resulting data set includes gene annotations, methylation levels and the specific analysis of methylation levels of genes involved in temperature-dependent sex determination (TSD). While the improvements offered by this work seem modest, I think that the data sets may provide important resources for future works.-In my opinion, the use of a previous version of the same genome in the assembly process should be noted in the abstract. It would be enough to write "... followed by homolgy-guided scaffolding to GSC_CCare_1.0...".-If possible, the authors should clarify the taxonomic relationship between the reference individual in this work and the reference individual for the previous version of the genome (ref. 26). Is it the same NCBI taxid?-There is a mention to "lateral terminal repeats" at the "Genome annotation" section (page 7). I think it is a typo and it should read "long terminal repeats".-In the same section, at page 9, reference 73 refers to StringTie, not gffread. In addition, it is not clear how "in-frame stop codons were removed". A simple way to unambiguously explain this would be to provide the options that were used, as with other programs.-I would revise the use of "coverage" versus "depth". For instance, the expression "...a coverage of 9.2(...)X" would be more precise as "...a sequencing depth of 9.2(...)X". Coverage should be a fraction or a percentage. However, this is only a piece of advice, as there is no strong consensus at the moment.-The interpretation of methylation patterns is always difficult. In my opinion, the manuscript should discuss several limitations about the results:First, using blood as the starting tissue is convenient but not ideal, as many methylation patterns are tissue-specific. The authors may want to add a reference to preliminary evidence that some methylation changes in blood cells are related to TSD (Bock et al., Mol Ecol. 2022; 31:5487-5505).Second, the work examines broad patterns of methylation (all promoters, all coding sequences,...). While this may be interesting for descriptive purposes, it may also drown significant signals. The manuscript should mention this limitation.*Figure 2B shows methylation per gene. If the aim is to compare both kinds of sequencing, there should be at least one comparison of methylation per CpG, which might even be cathegorial or downsampled.-The origin of the duplication of EP300 seems outside the scope of the manuscript. Nevertheless, given that the question is posed, the authors may want to perform a simple phylogenetic analysis of the sequences. Even the basic analysis of the annotated copies plus an outgroup is likely to give a robust answer to this question.-For the benefit of non-specialists, the manuscript might include a brief mention of how microchromosomes allow a larger number of combinations of variants without chromosome recombination.-Some expressions may be edited for clarity and precission. Examples are "which should be verified whether they are true" (page 17) and "microchromosomes have greater methylation potential and realised levels...".

This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giaf049), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer: Nezar Abdennur

The authors present VCF Zarr, a specification that translates the variant call format (VCF) data model into an array-based representation for the Zarr storage format. They also present the vcf2zarr utility to convert large VCFs to Zarr. They provide data compression and analysis benchmarks comparing VCF Zarr to existing variant storage technologies using simulated genotype data. They also present a case study on real world Genomics England aggV2 data.The authors' benchmarks overall show that VCF Zarr has superior compression and computational analysis performance at scale relative to data stored as roworiented VCF and that VCF Zarr is competitive with specialized storage solutions that require similarly specialized tools and access libraries for querying. An attractive feature is that VCF Zarr allows for variant annotation workflows that do not require full dataset copy and conversion. Another key point is that Zarr is a high-level spec and data model for the chunked storage of n-d arrays, rather than a bytelevel encoding designed specifically around the genomic variant data type. I personally have used Zarr productively for several applications unrelated to statistical genetics. While Zarr VCF mildly underperforms some of the specialized formats (Savvy in compute, Genozip in compression) in a few instances, I believe the accessibility, interoperability, and reusability gains of Zarr make the small tradeoff well worthwhile.Because Zarr has seen heavy adoption in other scientific communities like the geospatial and Earth sciences, and is well integrated in the scientific Python stack, I think it holds potential for greater reusability across the ecosystem. As such, I think the VCF Zarr spec is a highly valuable if not overdue contribution to an entrenched field that has recently been confronted by a scalability wall.Overall, the paper is clear, comprehensive, and well written. Some high-level comments: The benefits for large scientific datasets to be analysis-ready cloud-optimized (ARCO) have been well articulated by Abernathey et al., 2021. However, I do think that the "local"/HPC single-file use case is still important and won't disappear any time soon, and for some file system use cases, expansive and deep hierarchies can be performance limiting (this was hinted at in one of the benchmarks). In this scenario would a large Zarr VCF perform reasonably well (or even better on some file systems) via a single local zip store? The description of the intermediate columnar format (ICF) used by vcf2zarr is missing some detail. At first I got the impression it might be based on something like Parquet, but running the provided code showed that it consists of a similar file-based chunk layout to Zarr. This should be clarified in the manuscript. The authors discuss the possibility of storing an index mapping genomic coordinates to chunk indexes. Have Zarr-based formats in other fields like geospatial introduced their own indexing approaches to take inspiration from? Since VCF Zarr is still a draft proposal, it could be useful to indicate where community discussions are happening and how potential new contributors can get involved, if possible. This doesn't need to be in the paper per se, but perhaps documented in the spec repo.Minor comments: In the background: "For the representation to be FAIR, it must also be accessible," -- A is for "accessible", so "also" doesn't make sense. "There is currently no efficient, FAIR representation...". Just a nit and feel free to ignore, but the solution you present is technically "current".* In Figure 2, the zarr line is occluded by the sav line and hard to see.

Author response:

Reviewer #1 (Public review):

The usefulness of the proposed new metric of "variant consistency" and how it can guide users in selecting demultiplexing methods seems a little unclear. It correlates with the level of ambient RNA/DNA contamination, which makes it look like a metric on data quality. However, it does depend on the exact demultiplexing method, yet it's not clear how it directly connects to the "accuracy" of each demultiplexing method, which is the most important property that users of these methods care about. Since the simulated data has ground truth of donor identities available, I would suggest using the simulated data to show whether "variant consistency" directly indicates the accuracy of each method, especially the accuracy within those "C2" reads.

I also think the tool and analyses presented in this paper need some further clarification and documentation on the details, such as how the cell-type gene and peak probabilities are determined in the simulation, and how doublets from different cell types are handled in the simulation and analysis. A few analyses and figures also need a more detailed description of the exact methods used. 

We thank the reviewer for their suggestions. We plan on revising the manuscript to reflect their suggestions, which will include clarification of the variant consistency metric and its relationship with demultiplexing accuracy based on the simulations and additional detail regarding ambisim’s generation of multiplexed snRNA/snATAC.

Reviewer #2 (Public review):

(1) Throughout the manuscript, the figure legends are difficult to understand, and this makes it difficult to interpret the graphs.

(2) Since this is both a new tool and a benchmark, it would be worthwhile in the Discussion to comment on which demultiplexing tools one may want to choose for their dataset, especially given the warning against ensemble methods. From this extensive benchmarking, one may want to choose a tool based on the number of donors one has pooled, the modalities present, and perhaps even the ambient RNA (if it has been estimated previously).

(3) What are the minimal computational requirements for running ambisim? What is the time cost? 

We thank the reviewer for their suggestions. We plan on updating the manuscript to better clarify figure legends. We will also outline a set of concrete recommendations in our discussion section based on different multiplexed experimental designs. Finally, we will also include extra computational benchmarks for ambisim.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #2:

Minor reviews:

The caveats are (1) the particular point will perhaps only be interesting to a small slice of the eQTL research community; (2) the authors provide no statistical controls/error estimate or independent validation of the variance partitioning analysis in Figure 3, and (3) the authors don't seem to use the single-cell growth/fitness estimates for anything else, as Figure 4 uses loci mapped to growth from a previously published, standard culture-by-culture approach. It would be appropriate for the manuscript to mention these caveats.

We have added two small mention of these caveats – mainly that the study may not generalize, and that the study does not attempt to try the variance partitioning on other traits or other system where the values of the partitions are better established.

I also think it is not appropriate for the manuscript to avoid a comparison between the current work and Boocock et al., which reports single-cell eQTL mapping in the same yeast system. I recommend a citation and statement of the similarities and differences between the papers.

We have added this reference and a clear statement of similarities between the two studies. It was not our intention to avoid this; we had simply not seen that study in the initial submission.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

Reviewer #1 (Evidence, Reproducibility, and Clarity)

Reviewer comment: This is a very well conceived study of responses to plasma membrane stresses in yeast that signal through the conserved TORC2 complex. Physical stress through small molecular intercalators in the plasma membrane is shown to be independent of their biochemistry and then studies for its effect on plasma membrane morphology and the distribution of free ergosterol (the yeast equivalent of cholesterol), with free being the pool of cholesterol that is available to probes and/or sterol transfer proteins. Experiments nicely demonstrate a negative feedback loop consisting of: stress -> increased free sterol and TORC2 inhibition -> activation of LAM proteins (as demonstrated by Relents and co-workers previously) -> removal of free sterol -> return to unstressed state of PM and TORC2.

Author response: We thank the reviewer for their positive and encouraging feedback. We are pleased to submit our revised manuscript and have addressed all points raised below.

Comment: Fig 2A: Is detection of PIP/PIP2/PS linear for target, or possibly just showing availability that is increased due to local positive curvature?

Response: This is an excellent and fundamental question. While FLARE signal likely reflects lipid availability, its detection is indeed influenced by factors such as membrane curvature and lipid composition, due to varying insertion depths of the lipid-binding domains. For example, studies using NMR suggest that the PLCδ PH domain partially inserts into membranes, potentially conferring curvature sensitivity (Flesch et al., 2005; Uekama et al., 2009). Similarly, curvature influences lactadherin binding, though it's unclear if this extends to its isolated C2 domain (Otzen et al., 2012; Shao et al., 2008; Shi et al., 2004). We could not find direct evidence for curvature sensitivity of P4C(SidC), but assume some influence exists.

To avoid overinterpreting these limitations, we now describe our data based solely on the FLAREs used, rather than inferring enrichment of specific lipid species. We refer to these PM structures as "PI(4,5)P₂-containing", consistent with prior literature (Riggi et al., 2018) and have revised our manuscript accordingly.

Comment: Can any marker be identified for the D4H spots at 2 minutes? In particular, are they early endosomes (shown by brief pre-incubation with FM4-64)?

Response: We appreciate the reviewer's suggestion and have now added new data (Fig. S2E-H). We tested colocalization of D4H spots with FM4-64 (early endosomes), GFP-VPS21 (early endosome marker), and LipidSpot{trade mark, serif} 488 (lipid droplets), but found no overlap. This later observation was not unexpected given that D4H does not recognize Sterol esters. D4H foci also did not overlap with ER (dsRED-HDEL), though they were frequently adjacent to it. While their exact identity remains unknown, we agree this is an intriguing direction for future investigation.

Comment: Is there any functional (& direct) link between Arp inhibition (as in the Pombe study of LAMs by the lab of Sophie Martin) and PM disturbance by amphipathic molecules?

Response: We have explored this connection and now present new data (see final paragraph of Results). Briefly, we show that CK-666 induces internalization of PM sterols in a Lam2/4-dependent manner, and that TORC2 activity is more strongly reduced in lam2Δ lam4Δ cells compared to WT. These findings support the idea that, like PalmC, Arp2/3 inhibition triggers a PM stress that is counteracted by sterol internalization.

Minor Comment: Fig 2A: Labels not clear. Say for each part what FP is used for pip2.

Response: As noted above, we revised image labels to clarify which FLAREs were used, and refer to data accordingly throughout.

Minor Comment: Move fig s2d to main ms. The 1 min and 2 min data are integral to the story.

Response: We agree and have incorporated the 1-min and 2-min data into the main figures. Vehicle-treated controls were moved to Fig. S2.

Minor Comment: The role of Lam2 and Lam4 in retrograde sterol transport has in vivo only been linked to one of their two StART domains not both, as mentioned in the text.

Response: Thank you for pointing this out. We have corrected the text to:

"[...]Lam2 and Lam4[...] contain two START domains, of which at least one has been demonstrated to facilitate sterol transport between membranes (Gatta et al., 2015; Jentsch et al., 2018; Tong et al., 2018)."

Minor Comment: Throughout, images of tagged D4H should be labelled as such, not as "Ergosterol".

Response: We have updated all relevant figure labels and text to refer to "D4H" rather than "Ergosterol", in line with this recommendation.

Reviewer #1 (Significance):

These results in budding yeast are likely to be directly applicable to a wide range of eukaryotic cells, if not all of them. I expect this paper to be a significant guide of research in this area. The paper specifically points out that the current experiments do not distinguish the precise causation among the two outcomes of stress: increased free sterol and TORC2 inhibition. Of these two outcomes which causes which is not yet known. If data were added that shed light on this causation that would make this work much more signifiant, but I can understand 100% that this extra step lies beyond - for a later study for which the current one forms the bedrock.

Response:

We thank the reviewer for their generous assessment. We agree that understanding the causality between increased free sterol and TORC2 inhibition is a critical next step.

Based on our current data, we believe the increase in free ergosterol precedes TORC2 inhibition. For example, TORC2 inhibition alone (e.g., via pharmacological means) does not initially increase free sterol, while it does enhance Lam2/4 activity, promoting sterol internalization (Fig. 3A). Baseline TORC2 activity also inversely correlates with free PM sterol levels in lam2Δ lam4Δ versus LAM2T518A LAM4S401A cells (Figs. 2D, S2C).

Additionally, during sterol depletion, we observe an initial increase in TORC2 activity before growth inhibition occurs, after which activity declines-likely due to compromised PM integrity (Fig. S2M). We now also show that adaptation to several other stresses (e.g., osmotic shock, heat shock, CK-666) partially depends on sterol internalization, which correlates with TORC2 activation (Fig. 4, S4B).

While these findings strengthen the model that PM stress perturbs sterol availability and secondarily impacts TORC2, we cannot yet definitively demonstrate causality. As suggested by Reviewer 3, we tested cholesterol-producing yeast (Souza et al., 2011), but found their response to PalmC indistinguishable from WT, making it difficult to draw mechanistic conclusions (Rebuttal Fig. 2).

Taken together, we favour a model where sterols affect PM properties sensed by TORC2, probably lipid-packing, rather than acting as direct effectors. We hope our revised manuscript more clearly conveys this model and serves as a strong foundation for future mechanistic studies.

Reviewer #2 (Evidence, Reproducibility, and Clarity)

Reviewer comment: This manuscript describes multiple effects of positively-charged membrane-intercalating amphipaths (palmitoylcarnitine, PalmC, in particular) on TORC2 in yeast plasma membranes. It is a "next step" in the Loewith laboratory's characterization of the effect of this agent on this system. The study confirms the findings of Riggi et al.(2018) that PalmC inhibits TORC2 and drives the formation of membrane invaginations that contain phosphatidylinositol-bis-phosphate (PIP2) and other anionic phospholipids. It also demonstrates that PalmC intercalates into the membrane, acts directly (rather than through secondary metabolism) and is representative of a class of cationic amphipaths. The interesting finding here is that PalmC causes a rapid initial increase in the plasma membrane ergosterol accessible to the DH4 sterol probe followed by a decrease caused by its transfer to the cytoplasm through its transporter, LAM2/4. TORC2 is implicated in these processes. Loewith et al. have pioneered in this area and this study clearly shows their expertise. Several of the findings reported here are novel. However, I am concerned that PalmC may not be revealing the physiology of the system but rather adding tangential complexity. (This concern applies to the precursor studies using PalmC to probe the TORC2 system.) In particular, I am not confident that the data justify the authors' conclusions "...that TORC2 acts in a feedback loop to control active sterol levels at the PM and [the results] introduce sterols as possible TORC2 signalling modulators."

Author response:

We thank Reviewer #2 for the constructive and critical evaluation of our work. We appreciate the acknowledgment of the novelty and technical strength of several of our findings, and we understand the concern that PalmC could be eliciting non-physiological effects. Our study was designed precisely to use PalmC and similar membrane-active amphipaths as tools to strongly perturb the plasma membrane (PM) in a controlled and tractable way. We now state this intention explicitly in both the Introduction and Discussion sections. To address concerns about the specificity and physiological relevance of PalmC, we have expanded our dataset to include additional PM stressors (hyperosmotic shock, Arp2/3 inhibition, and heat shock), all of which reproduce key features observed with PalmC-namely, TORC2 inhibition, PM invaginations, and retrograde sterol transport (Fig. 4, S4).

We hope this more comprehensive dataset, along with revised discussion and clarified claims, addresses the reviewer's concerns regarding physiological interpretation and artifact.

Major issues 1 and 2: 1. The invaginations induced by PalmC may not be physiologic but simply the result of the well-known "bilayer couple" bending of the bilayer due to the accumulation of cationic amphipaths in the inner leaflet of the plasma membrane bilayer which is rich in anionic phospholipids. Such unphysiological effects make the observed correlation of invagination with TORC2 inhibition etc. hard to interpret.

Electrostatic/hydrophobic association of PIP2 with PalmC could sequester the anionic phospholipid(s). Such associations could also drive the accumulation of PIP2 in the invaginations. This could explain PalmC inhibition of TORC2 through a simple physical rather than biological process. So, it is difficult to draw any physiological conclusion about PIP2 from these experiments.

Response to major issues 1 and 2:

We agree that amphipath-induced bilayer stress, including via the bilayer-couple mechanism, may contribute to PM curvature changes. However, the reviewer's assumption that PalmC inserts preferentially into the inner leaflet appears inconsistent with both literature and our observations. PalmC is zwitterionic, not cationic, and is unlikely to electrostatically sequester anionic lipids such as PIP2. For clarification, we included a short summary of our proposed mechanism of PalmC in the context of the current literature in our Discussion:

"[...] study it was also demonstrated that addition of phospholipids to the outer PM leaflet causes an excess of free sterol at the inner PM leaflet, and its subsequent retrograde transport to lipid droplets (Doktorova et al., 2025). Although we cannot exclude that it is the substrate of a flippase or scramblase, PalmC is not a metabolite found in yeast, nor, given its charged headgroup, is it likely to spontaneously flip to the inner leaflet (Goñi, Requero and Alonso, 1996). Thus, we propose that PalmC accumulates in the outer leaflet, disrupts the lipid balance with the inner leaflet which is, similarly to the mammalian cell model (Doktorova et al., 2025), rectified by sterol mobilization, flipping and internalization (Fig. 5B)."

While we agree that PM invaginations per se are not the central focus of this study, they are indeed a reproducible and biologically intriguing phenomenon. We emphasize that similar invaginations occur not only during PalmC treatment but also in response to other physiological stresses, such as hyperosmotic shock and Arp2/3 inhibition (Fig. 4), and have been reported independently by others (Phan et al., 2025). Furthermore, related structures have been documented in yeast mutants with altered PIP2 metabolism or TORC2 hyperactivity (Rodríguez-Escudero et al., 2018; Sakata et al., 2022; Stefan et al., 2002), and even in mammalian neurons with SJ1 phosphatase mutations (Stefan et al., 2002). These observations support our interpretation that the observed invaginations represent an exaggerated manifestation of a physiologically relevant stress-adaptive process. In our previous study we indeed proposed that PI(4,5)P2 enrichment in PM invaginations was important for PalmC-induced TORC2 inactivation, using the heat sensitive PI(4,5)P2 kinase allele mss4ts - a rather blunt tool (Riggi et al., 2018). We have now come to the conclusion that different mechanisms other than, or in addition to, PIP2 changes drive TORC2 inhibition in our system. In this study, we use the 2xPH(PLC) FLARE exclusively as a generic PM marker, not as a readout of PIP2 biology. Rather, we propose that sterol redistribution and/or the biophysical impact that this has on the PM are central drivers, with TORC2 acting as a signaling node that senses and adjusts PM composition accordingly.

We now clarify these arguments in the revised Discussion and have reframed our use of PalmC as a probe to explore the capacity of the PM to adapt to acute stress via dynamic lipid rearrangements.

Major issue 3:

As the authors point out, a large number of intercalated amphipaths displace sterols from their association with bilayer phospholipids. This unphysiologic mechanism can explain how PalmC causes the transient increase in the availability of plasma membrane ergosterol to the D4H probe and its subsequent removal from the plasma membrane via LAM2/4. TORC2 regulation may not be involved. In fact, the authors say that "TORC2 inhibition, and thereby Lam2/4 activation, cannot be the only trigger for PalmC induced sterol removal." Furthermore, the subsequent recovery of plasma membrane ergosterol could simply reflect homeostatic responses independent of the components studied here.

Response:

We agree that increased free sterols in the inner leaflet likely initiate retrograde transport. Our results suggest that TORC2 inhibition facilitates this process by disinhibiting Lam2/4, allowing more efficient clearance of ergosterol from the PM (Fig. 3A, S2C). However, the process is not exclusively dependent on TORC2, and we state this explicitly.

We do not observe recovery of PM ergosterol on the timescales measured, while TORC2 activity recovers, suggesting that restoration likely occurs later via biosynthetic or anterograde trafficking pathways, which are outside the scope of this study. These points are clarified in the revised Discussion.

Major issue 3a:

The data suggest that LAM2/4 mediates the return of cytoplasmic ergosterol to the plasma membrane. To my knowledge, this is a nice finding that not been reported previously and is worth confirming more directly.

Response:

We thank the reviewer for this observation but would like to clarify a misunderstanding: our data do not suggest that Lam2/4 mediates anterograde sterol transport. Our results and prior work (Gatta et al., 2015; Roelants et al., 2018) show that Lam2/4 mediate retrograde transport from the PM to the ER, and TORC2 inhibits this process. We now clarify this point in the revised manuscript, stating:

"In vivo, Lam2/4 seem to predominantly transport sterols from the PM to the ER, following the concentration gradient (Gatta et al., 2015; Jentsch et al., 2018; Tong et al., 2018)."

Major issue 4:

I agree with the authors that "It is unclear if the excess of free sterols itself is part of the inhibitory signal to TORC2..." Instead, the inhibition of TORC2 by PalmC may simply result from its artifactual aggregation of the anionic phospholipids (especially, PIP2) needed for TORC2 activity. This would not be biologically meaningful. If the authors wish to show that accessible ergosterol inhibits TORC2 activity or vice versa, they should use more direct methods. For example, neutral amphipaths that do not cause the aforementioned PalmC perturbations should still increase plasma membrane ergosterol and send it through LAM2/4 to the ER.

Response:

We now provide evidence that three orthologous treatments (hyperosmotic shock, heat shock and Arp2/3 inhibition) similarly cause sterol mobilization and, in the absence of sterol clearance from the PM, prolonged TORC2 inhibition. These results do not support the reviewer's contention that the inhibition of TORC2 by PalmC is simply resulting from its artifactual aggregation of the anionic phospholipids. Furthermore, PalmC is zwitterionic, and its interaction with anionic lipids should be somewhat limited.

In our experimental setup, neutral amphipaths did not trigger TORC2 inhibition or D4H redistribution While this differs from prior in vitro work (Lange et al., 2009), we attribute this in part to a discrepancy to experimental setup differences, including flow chamber artifacts that we discuss in the methods section.

Importantly, only amphipaths with a charged headgroup, including zwitterionic (PalmC) and positively charged analogs, produced robust effects. A negatively charged derivative also seemed to have a minor effect on TORC2 activity and PM sterol internalization (Palmitoylglycine (Fig. 1D, Rebuttal Fig. 1). This suggests that in vivo, charge-based membrane perturbation is required to alter PM sterol distribution and TORC2 activity.

Major issue 5.:

The mechanistic relationship between TORC2 activity and ergosterol suggested in the title, abstract, and discussion is not secure. I agree with the concluding section of the manuscript called "Limitations of the study". It highlights the need for a better approach to the interplay between TORC2 and ergosterol.

Response:

This may have been true of the previous submission, but we now demonstrate that provoking PM stress in four orthogonal ways triggers mobilization of sterols, which left uncleared, prevents normal (re)activation of TORC2 activity. We thus conclude that free sterols, directly or more likely indirectly, inhibit TORC2. The role that TORC2 plays in sterol retrotranslocation has been demonstrated previously (Roelants et al., 2018). We believe our expanded data and clarified framework make a compelling case for a stress-adaptive role of sterol retrograde transport that is supervised and modulated-but not fully driven-by TORC2 activity.

Thus, we feel in the present version of this manuscript that the title is now justified.

Minor issue: Based on earlier work using the reporter fliptR, the authors claim that PalmC reduces membrane tension. They should consider that this intercalated dye senses many variables including membrane tension but also lipid packing. I suspect that, by intercalating into and thereby altering the bilayer, PalmC is affecting the latter rather than the former.

Response:

We thank the reviewer for this important point regarding the multifactorial sensitivity of intercalating dyes such as Flipper-TR®, including to membrane tension and lipid packing.

We respectfully note, however, that our current study does not include any new data generated using Flipper-TR®. We referred to earlier work (Riggi et al., 2018) for context, where Flipper-TR® was used as a membrane tension reporter.

We fully agree that the response of such "smart" membrane probes integrates multiple biophysical parameters-including tension, packing, and hydration-which are themselves interrelated as consequences of membrane composition (Colom et al., 2018; Ragaller et al., 2024; Torra et al., 2024). Indeed, this interconnectedness is central to our interpretation of PalmC's pleiotropic effects on the plasma membrane (PM). In our previous study, we observed that PalmC treatment not only reduced apparent PM tension (as measured by Flipper-TR®) but also increased membrane order ((Riggi et al., 2018); see laurdan GP, Fig. 6C), and here we show that it promotes the redistribution of free sterol away from the PM.

Furthermore, PalmC's effect on membrane tension was supported by orthogonal in vitro data: its addition to giant unilamellar vesicles (GUVs) led to a measurable increase in membrane surface area and decreased tension, as shown by pipette aspiration ((Riggi et al., 2018), Fig. 3F). This provides complementary evidence that the membrane tension reduction is not merely an artifact of Flipper-TR® reporting.

That said, we agree with the reviewer that in the case of TORC2 inhibition or hyperactivation, the observed changes in PM tension are based solely on Flipper-TR® data, without additional orthogonal validation. To address this concern, we have revised the relevant text in the manuscript to more cautiously reflect this complexity. The revised sentence now reads:

"Consistent with this role, data generated with the lipid packing reporter dye Flipper-TR® suggest that acute chemical inhibition of TORC2 increases PM tension, while Ypk1 hyperactivation decreases it."

This revised phrasing acknowledges both the utility and the limitations of Flipper-TR® as a probe of membrane biophysics.

Reviewer #2 Significance:

This is an interesting topic. However, use of the exogenous probe, palmitoylcarnitine, could be causing multiple changes that complicate the interpretation of the data.

Reviewers #1 and #3 were much more impressed by this study than I was. I am not a yeast expert and so I may have missed or confused something. I would therefore welcome their expert feedback regarding my comments (#2). Ted Steck

Response:

Thank you for your constructive feedback.

We believe that the manuscript is now much improved, and we hope to have convinced you that the mechanisms that we've elucidated using PalmC represent a general adaptation response to physiological PM stressors.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Reviewer comment: The authors describe the effects of surfactant-like molecules on the plasma membrane (PM) and its associated TORC2 complex. Addition of the surfactants with a positively-charged headgroup and a hydro-carbon tail of at least 16 caused the rapid clustering of PI-4,5P2 together with PI-4P and phosphatidylserine in large membrane invaginations. The authors convincingly demonstrate that this effect of the surfactants on the PM is likely caused by a direct disturbance of the PM organization and/or lipid composition. Interestingly, upon PalmC treatment, free ergosterol of the PM was found to first concentrate in the clusters, but within The kinetics of the changes in free ergosterol levels and the changes in TORC2 activity do not match. Ergosterol is rapidly depleted after PalmC treatment (The Lam2/4 data support the idea that ergosterol transport plays a role in the TORC2 recovery, but what role this is, is not clear to me. I think the data fit better with a model in which PalmC causes low tension of the PM which in turn disrupts normal lipid organization and thus causes TORC2 to shut down, maybe not by changes in free ergosterol but by changes, for instance, in lipid raft formation (which is in part effected by ergosterol levels). The transport of ergosterol is only one mechanism that is involved in restoring PM tension and TORC2 activity. However, sensing free ergosterol alone is most likely not the mechanism explaining how TORC2 senses PM tension.

Therefore, I recommend that the model is revised (or supported by more data), reflecting the fact that free ergosterol levels do not directly correlate with the TORC2 activity, but instead might be only one of the PM parameters that regulate TORC2.

Author response:

We thank the reviewer for their thoughtful assessment and constructive suggestions. As described in more detail above, we have included in our revised version of this manuscript a variety of new data, including the sterol-internalization dependent adaptation of the PM and regulation of TORC2 during additional stresses. We think that these data vastly improve on our previous manuscript version. We have addressed each point risen by the reviewer below and revised the manuscript accordingly, including a rewritten discussion and updated model to better reflect the limitations of our current understanding of how TORC2 senses changes in the plasma membrane (PM). It is true that the appearance of PM invaginations tracks well with TORC2 inhibition, but it is not clear to us if they are upstream of this inhibition or merely another symptom of the preceding PM perturbation (PalmC-induced free sterol increase can be observed after 10s (Fig. S2A), but PM invaginations become visible only after ~1 min - meanwhile we can observe near complete TORC2 inhibition after 30s). In this study, we are mostly interested in the role of PM sterol redistribution in stress response. Indeed we think that the role of free sterol clearance during stresses is to adapt the PM to these stresses - thus restoring PM parameters which in turn reactivates TORC2. This can be seen for hyperosmotic stress and the newly introduced PM stressors, Arp2/3 inhibition and heat shock response (Fig. 4). We have therefore softened our model and updated discussion and final figure (Fig. 5) to reflect that TORC2 likely responds to broader changes in PM organization or tension, with sterol redistribution representing one of several contributing factors rather than the sole signal.

Comment: - If TORC2 is indeed inhibited by free ergosterol, the addition of ergosterol to the growth medium should be able to trigger similar effects as PalmC. If this detection of free ergosterol is very specific (e.g. if TORC2 has a binding pocket for ergosterol) we would expect that addition of other sterols such a cholesterol or ergosterol precursors should not inhibit TORC2.

Response:

We appreciate this suggestion and agree that testing whether exogenous ergosterol can mimic PalmC effects would help assess specificity. However, yeast do not readily take up sterols under aerobic conditions, which renders artificial sterol enrichment at the yeast PM rather difficult. We have now included additional data characterizing our Lam2/4 mutants (see below), and pharmacological sterol synthesis inhibition, showing that a depletion of free sterols from the PM correlates with lower TORC2 activity (Fig. 2D, S2C). Additionally, as suggested, we tried to probe if ergosterol directly interacts with TORC2 through a specific binding pocket, by treating a yeast strain expressing cholesterol rather than ergosterol (Souza et al., 2011) with PalmC. However, the response of TORC2 activity in these cells was very similar to that of WT cells (Rebuttal Fig. 2). In conclusion, we agree that at present we do not know mechanistically how sterols affect TORC2 activity, although it does indeed seem more likely to be through an indirect mechanism linked to changes in PM parameters. The nature of such a mechanism will be subject to further studies. We hope that the introduced changes to the manuscript adequately reflect these considerations.

Rebuttal Fig. 2: WT yeast cells which produce ergosterol as main sterol, and mutant cells which produce cholesterol instead were treated with 5 µM PalmC, and TORC2 activity was assessed by relative phosphorylation of Ypk1 on WB. One representative experiment out of two replicates.

Comment: - The experiment in Figure 1C is not controlled for differences in membrane intercalation of the different compounds. For instance, does C16 choline and C16 glycine accumulate at the same rate in the PM (measure similar to experiment in Figure 1B). Maybe the positive charge at the headgroup of the surfactants increases the local concentration at the PM and therefore can explain the difference in effect on the PM.

Response:

We agree with the reviewer that the effects of the various PalmC derivatives are not directly controlled for differences in membrane intercalation. Our structure-activity screen was intended to demonstrate the general biophysical mode of action of PalmC-like compounds and to define minimal structural requirements for activity.

We now note in the manuscript that differential membrane insertion could contribute to the observed variation in efficacy, particularly in relation to tail length. While we considered this additional suggested experiment, it was ultimately judged to be outside the scope of this study due to its complexity and limited impact on the central conclusions.

A clarifying sentence has been added to the relevant results section to explicitly acknowledge this limitation:

"We did not control for differences in PM intercalation efficiency."

We also include a discussion here to further clarify our interpretation. Prior in vitro studies have shown that while intercalation is necessary, it is not sufficient for PM perturbation. For example, palmitoyl-CoA intercalates into membranes but does not induce the same biophysical effects as PalmC (Goñi et al., 1996; Ho et al., 2002). Thus, we believe that intercalation is only part of the story, and that the intrinsic propensity of different headgroups to perturb the PM plays a key role in the disruption of PM lipid organization.

Comment: - Are the intracellular ergosterol structures associated (or in close proximity) with lipid droplets (ergosterol being modified and delivered into a lipid droplet)?

Response:

We thank the reviewer for raising this point. We now include additional data (Fig. S2H) showing that intracellular D4H-positive structures do not reside near or colocalize with lipid droplets. The latter is not entirely unexpected as D4H does not recognize esterified sterols. However, we do observe an increase in overall LD volume following PalmC treatment, consistent with the idea that internalized PM sterols may be stored in LDs as sterol esters over time - although we did not test if this increase in LD volume is Lam2/4 dependent. This increase is mentioned in the revised results text. An increase in cellular LDs has also been recently reported during hyperosmotic shock (Phan et al., 2025).

For more attempts to identify a marker for intracellular D4H foci, see reply to reviewer 1.

Comment:

• How does the AA and DD mutations in Lam2/4 change the localization of the ergosterol sensor (before and after PalmC treatment).

Response:

We thank the reviewer for this question, as in the course of generating these data we realized that our "inhibited" DD mutant was in fact not phosphomimetic but displayed the same D4H distribution as the "hyperactive" AA mutant, i.e. a marked inwards shift of D4H signal away from the PM to internal structures due to increased PM-ER retrograde transport of sterols (Fig. S2C). This led us to critically re-evaluate and ultimately repeat our TORC2 activity WB experiments for PalmC treatment in LAM2/4 mutants. In this new set of experiments, the faster TORC2 recovery after PalmC treatment in the LAM2T518A LAM4S401A mutant did unfortunately not repeat robustly. It is possible that such differences can be observed under specific conditions. Nevertheless, the improved overall quality of the Western blot data allowed us to make the observation that baseline activity was already slightly different in these strains. The Lam2/4 centered part of the results section has subsequently been updated in the manuscript:

"Using a phosphospecific antibody, we did not observe an increase in baseline TORC2 activity in lam2Δ lam4Δ cells, which had been previously reported by electrophoretic mobility shift (Murley et al., 2017). Instead, baseline TORC2 activity was consistently slightly decreased in these cells (Fig. 2D). Ypk1, activated directly by TORC2, inhibits Lam2 and Lam4 through phosphorylation on Thr518 and Ser401, respectively (Roelants et al., 2018; Topolska et al., 2020). We substituted these residues with alanine, generating a strain in which Lam2/4 were no longer inhibited by phosphorylation (Roelants et al., 2018). In these cells, yeGFP-D4H showed that free sterols were constitutively shifted away from the PM to intracellular structures (Fig. S2C, bottom panel). Intriguingly, in opposition to lam2Δ lam4Δ cells, basal TORC2 activity was increased in LAM2T518A LAM4S401A cells (Fig. 2D). This suggests that a decrease in free PM sterols stimulates TORC2 activity [...]"

"In LAM2T518A LAM4S401A cells, TORC2 activity recovers with similar kinetics as the WT (Fig. 2D, bottom blot), suggesting that Lam2/4 release from TORC2 dependent inhibition during PalmC treatment is a fast and efficient process in WT cells, not further expedited by these constitutively active Lams."

As suggested, we also observed D4H localization in LAM2T518A LAM4S401A after PalmC treatment, and implemented these data to further demonstrate that PalmC causes an increase in the fraction of free ergosterol at the PM, which is subsequently removed:

"PalmC addition to LAM2T518A LAM4S401A cells likewise resulted first in a transient increase and then a further decrease in PM yeGFP-D4H signal (Fig. 3C, S3D)."

Comment: - Does Lam2/4 localize to ER-PM contact sites near the large PM invaginations, which could allow for efficient transport of the free ergosterol that accumulates in these structures.

Response:

We were curious about this too, and have now added the requested data in our supplementary material and added a sentence in our results:

"Indeed, in cells expressing GFP-Lam2 we observed that PalmC induced PM invaginations often formed at sites with preexisting GFP-Lam2 foci (Fig. S2K, cyan arrow), although GFP-Lam2 foci did not always colocalize with invaginations (Fig. S2K, yellow arrow) and vice versa. "

Additionally, in the effort to characterize intracellular D4H foci during PalmC as requested by reviewer 1, we also looked at the localization of these foci relative to ER, and found that

"During early timepoints, intracellular foci are usually in close vicinity to ER (Fig. S2E)"

Reviewer #3 (Significance (Required)): The manuscript describes the effects of small molecule surfactants on the PM organization and on TORC2 activity. This is an important set of observation that helps understanding the response of cells to environmental stressors that affect the PM. This field of study is very challenging because of the limited tools available to directly observe lipids and their movements. I consider the data and most of its interpretations of high importance, but I am not convinced of the larger model that tries to link the ergosterol data with TORC2 activity. With adjustments of the model or additional experimental support, this manuscript will be of general interest for cell biologists, especially for researchers studying membrane stress response pathways.

Response:

We thank the reviewer for highlighting the importance of studying PM stress responses and acknowledging the technical challenges involved. We hope the applied changes and additional data succeed in softening our claims about TORC2 regulation while convincing the reviewer that free sterol levels at the PM are one of several contributing factors that correlate with changes in TORC2 activity.

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Reply to the reviewers

We thank all the reviewers for their helpful and constructive comments and for their time.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):*

Summary: Dady et al have developed fluorescent reporters to enable live imaging of cell behaviour and morphology in human pluripotent stem cell lines (PSCs). These reporters target 3 main features, the plasma membrane, nucleus and cytoskeleton. Reporter PSCs have been generated using a piggyBac transposon-mediated stable integration strategy, using a hyperactive piggyBac transposase (HyPBase). The same constructs were also used for mosaic labelling of cells within 2D cultures using lipofectamine transfection.

The reporters used are tagged with either eGFP or mKate2 (far red) and tag the plasma membrane (pm) via the addition of a 20 amino-acid sequence from rat GAP-43 to the N-terminus of the fluorescent protein, the nucleus via Histone 2B with a laser-mediated photo-conversion option (H2B-mEos3.2), and the cytoskeleton via F-Tractin. In total, the authors produced lines with the following:

• pm-mKate2 (far red) • pm-eGFP (green) • H2B-mEos3.2 (green to red) • F-tractin-mKate2 (far red) • H2B-mEos3.2 and pm-mKate2 (green to red, plus far red)

The cell lines used to generate these were the human embryonic stem cell line H9 and human induced pluripotent cell line ChiPS4. The constructs were also used to label cells in a mosaic fashion, using lipofectamine transfection of the original cell lines once they had formed neural rosettes.

Using these cells, Dady et al then performed live imaging in vitro of human spinal cord rosettes and assessed cell behaviour. In particular they analysed mitotic cleavage planes and apical positioning of neural progenitor cells (NPCs), and assessed actin dynamics within these cells. They showed a slowing of the cell cycle length after the initial expansion phase, an increase in the rate of asymmetric division of these NPCs, and abscission of the apical membrane during these divisions. The F-tractin reporter showed enrichment at the basal nuclear membrane during these cell divisions, suggested to help prevent basal chromosome displacement during mitosis.

Major comments: The data presented are convincing and could be strengthened by the following additions and clarifications:*

2. How long do the fluorescent reports take to be visible when transfected via lipofectamine? How efficiently are they expressed? And what concentrations were tested to enable the mosaic expression presented? * We followed the manufacturer’s instructions for Lipofectamine 3000 transfection, using the protocol recommended for set up for a 6 wells plate. We detected fluorescence the following morning ~16h. We did not assess earlier time points or optimise efficiency as we observed the mosaic pattern of expression we set out to achieve, with small groups of labelled cells and single cells as shown in Figure 3 and movies 2 and 3. This information and the detailed protocol provided below are now included in the Methods section “Labelling individual cells in human spinal cord rosettes by lipofection”.

Manufacturer’s instructions for Lipofectamine 3000 transfection (6 well plate):

• 1 tube containing 125 ul of Opti-MEM and 7.5 ul of Lipofectamine 3000
• 1 tube containing 250 ul of Opti-MEM with 5 ug of DNA (total mix DNAs of 2 ug/ul) and P3000 Reagent
• Add diluted DNA to diluted Lipofectamine 3000 (Ratio 1:1) and incubate for 10 to 15 min at Room Temperature.
• 20 ul of DNA-Lipid complex was added to neural rosettes growing in 8 well IBIDI dishes (20 ul/well).
• The ratio of DNA (PiggyBac plasmid) and HypBase transposase was kept at 5:1 (for a final concentration of 2ug/ul).

• Cells in IBIDI dishes were left to develop in a sterile incubator overnight and mosaic fluorescence was observed the following morning (~16h post-lipofection).

• Will these cell lines and constructs be made publicly available after publication?*

The cell lines can be made available: for those reporters made in the H9 WiCell line an MTA will first have to be signed between the requesting PI and WiCell and permission for us to share the line(s) confirmed by WiCell; similarly, for reporters in ChiPS4 line an MTA will first need to be signed between the requesting PI and Cellartis/TakaraBio Europe. We will need to make a charge to cover costs. Constructs will be deposited with Addgene.

• Were the H9 and ChiPS4 lines characterised after the reporters were added to show they still proliferate/differentiate as they did prior to the reporter integration*?

In the Results we make clear that all lines created are polyclonal, with exception of a pm-eGFP ChiPS4 line, which is a monoclonal line (lines 145-150). We do not have direct data measuring cell proliferation but collected cell passaging data for all the reporter lines. This showed that they grow to similar densities at each passage compared to the parental line (this metadata is now provided as Supplementary data 1 and is cited in the Methods, line 348).

As a proof of principle for this approach, we created one monoclonal line from a polyclonal line ChIPS4-pm-eGFP. The latter was made by selecting an individual clone and this was then expanded and characterised for expression of pluripotency markers (immunocytochemistry data Figure S4), and the ability to differentiate into 3 germ layers (qPCR Supplementary data 1). This information is already cited in the Methods (Lines 358-362).

• Can the novel actin dynamics described be quantified? How many cells imaged show these novel dynamics?* Some of this quantification data was already reported in the paper (in figure 4 legend and in the Methods); we have now updated this and provide the detailed metadata in an Excel spread sheet, Supplementary data 4 (cited in the Methods, line 489)

Minor comments: 1. Some images in the figures and supplemental movies are low in resolution, for example the DAPI in Fig 4B, making it hard to distinguish individual cells. Please increase this.

We consider the DAPI labelling in Figure 4b to be clear, however, we wonder whether the reviewer was expecting to also see this combined with the other markers. We have therefore now provided these merged additional images in a revised Figure 4.

• Please show a merge of Phalloidin and F-Tractin in Fig4, this will help the colocalization to be fully appreciated.*

This has now been provided in revised Figure 4B.

• Some additional annotation on the supplemental movies would be useful to indicate to the **reader exactly what cell to follow. *

We have added indicative arrows to the movies, and note that more detailed labelling of the series of still images from these movies are provided in the main figures (Figures 3D and 4E & F).

*Reviewer #1 (Significance (Required)):

Human neurogenesis is currently poorly understood compared to many model systems used, yet key differences have already been identified between the human and the mouse, prompting the need for further investigation of human neural development. A major reason that human neurogenesis has been difficult to study is a lack of tools to enable cell morphology and behaviours to be analysed in real time.

The reporters and reporter PSC lines generated by Dady et al will allow many of these cell characteristics to be observed using live imaging. For example, the morphology of neural progenitors during and after cell divisions, how the apical and basal processes and membranes are divided, and how the actin cytoskeleton helps to regulate these processes.

*Importantly, PSC lines can be very heterogeneous, making generating reporter lines costly and time intensive. The use of these reporters with lipofectamine transfection, for a mosaic labelling, allows the visualisation of the plasma membrane, nucleus and cytoskeleton in any human PSC/NPC line, or even in human tissue cultures, without the need to generate each specific reporter line, making it a valuable tool for many labs in the field.

We strongly agree with this final point; this is a major reason for our study.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):*

The manuscript describes the generation of novel lines of human pluripotent stem cells bearing fluorescent reporters, engineered through piggyBac transposon-mediated integration. The cells are differentiated into neuronal organoids, allowing to capture cellular behaviors associated to cell division. A replating protocol allows the observation of aging neurons by reducing the thickness of the tissue thereby facilitating live imaging. The authors also leverage the transposon technology to create mosaically-labelled organoids which allows visualizing aspects of neuronal delamination, notably cytoskeleton dynamics. They discover an undescribed pattern of F-actin enrichment at the basal nuclear membrane prior to nuclear envelope breakdown.

L104-109: "Moreover, the transposon system obviates drawbacks of directly engineering endogenous proteins...". Despite the risk of endogenous protein dysfunction, directly tagging allows the full regulation of gene expression (including the promoter, the enhancers and other regulatory regions rather than a strong constitutive promoter such as CAG). In addition, the number of copies integrated and the genomic regions are variable with PB, which does not reflect the endogenous expression. This could be rephrased by nuancing the advantages and drawbacks of each approach. The PiggyBac method is easier and faster, but it results in overexpression of a tagged protein that will be expressed since the hESC state and might not reflect the expression dynamics of the endogenous protein.* We agree and have now revised this in the Introduction L109-118.

*L124-126: "To monitor cell shape and dynamics we used a plasma membrane (pm) localized protein tagged with eGFP or mKate2 (pm-eGFP or pm-mKate2)." Could the authors provide more details and a reference on the palmitoylated rat peptide use to force membrane expression? *

This information, including the peptide sequence, is provided in the Methods (L330-331), we have now added a reference addressing its role in membrane localisation PMID: 2918027.

L132-133: " Finally, to observe actin cytoskeletal dynamics we selected F-tractin, for its minimal impact on cytoskeletal homeostasis".

A recent JCB paper (https://doi.org/10.1083/jcb.202409192) suggests that "F-tractin alters actin organization and impairs cell migration when expressed at high levels". Whether the overexpression of F-tractin in hESC using a CAG promoter reflects the physiological F-actin dynamics and/or if the high levels could lead to an alteration of cell behavior should be addressed or at least discussed. The paper we cite in this sentence (Belin et al 2014) evaluates F-tractin expression against other approaches to labelling and monitoring the actin cytoskeleton and concludes that in comparison F-tractin has minimal impact.

We do appreciate that expression above the endogenous level has the potential to alter cell behaviour and have revised the paper to more explicitly acknowledge this: in the Introduction (L109-112), and in the Discussion/conclusion (L289-293) where we now note the recent advances reported in Shatskiy et al. 2025 PMID: 39928047.

“A further potential limitation of this approach is that over-expression driven by the CAG promoter might not reflect physiological protein dynamics and/or alter cell behaviour; for example, high levels of F-Tractin can impair cell migration and induce actin bundling, interestingly, this can now be minimised by removing the N-terminal region (Shatskiy et al 2025)”.

L146-147: "...to generate polyclonal cell lines selected for expression of easily detectable (medium level) fluorescence for live imaging studies". What are the criteria used to define medium level? Number of copies integrated into the genome? Or levels by FACS during clone selection?

To clarify, all the lines presented here are polyclonal, except for one clonal line, pm-eGFP in ChiPS4. The numbers of copies integrated may vary from cell to cell in polyclonal lines. In this study, we selected cells for all lines with a FACS gate and this data is presented in Figure S1 (see line 147).

L260-263: "Efficient stable integration and moderate expression levels were achieved by optimising, i) the quantity and ratio of piggyBac plasmids and transposase and ii) subsequent FACS to exclude high expressing cells, as well as iii) transfection methods, including temporally defined lipofection in hiPSC-derived tissues." The ration 5:1 is classically used for PB Transposase delivery, however there is still high variability in the number of copies integration. Lipofection in derived tissues has been shown to be challenging. Could the authors should provide quantitative data regarding the efficiency of their approaches, notably the level of mosaicism one could expect?

We provide quantitative data for the efficiency of transfection using nucleoporation assays (FACS data presented in Supplementary figure S1), which shows more than 80-90% efficiency for eGFP in 82.82% of cells, mKate2 in 92.74% of cells, and H2B-mEos3 22.75% of cells, while 13.79% of cells co-expressed pm-Kate and H2B-mEos3.2. No comparative data regarding the efficiency of the tissue Lipofection assay was collected: our goal was to label single/small numbers of cells in order to monitor individual cell behaviours, and this “inefficient labelling” was readily achieved following the manufacturer’s instructions (please see response to Review 1 point 1), further details are now provided in the Methods.

L191-194: "We further wished to monitor sub-cellular behaviour within the developing neuroepithelium. To achieve this, we devised a strategy to target a mosaic of cells in established neural rosettes using lipofection. PiggyBac constructs and HyPBase transposase were transfected into D8/D9 human spinal cord neural progenitors using lipofectamine (Felgner, et al., 1987)(Fig. 3A)." The mosaicism is not an all or nothing in this method but also leads to variations in expression levels among the positive cells. The protocol for lipofection could be better detailed to allow easy reproduction by other teams, and its expected efficiency should be discussed. It would be interesting to explore the relationship between individual cells phenotype and expression levels. Please see response to Reviewer 1 point 1 above for more detailed lipofection protocol which generated mosaic expression, this is now also included in the Methods. We agree that investigating the relationship between individual cell phenotypes and expression levels would be interesting, but we think this is beyond the scope of this paper.

Additional comments: -Did the authors perform karyotyping of the hPSCs prior to use in the differentiation protocol?

As these are polyclonal lines, we did not undertake karyotyping. This could be done for the one monoclonal line described here (pm-eGFP ChiPS4 line): we lack funds for commercial options, but we are exploring other possibilities.

-Were pluripotency assays performed after reporter lines generation?

These were carried out for the clonal pm-eGFP ChiPS4 line (lines 145-150). The latter was made by selecting an individual clone and this was then expanded and characterised for expression of pluripotency markers by IF (Figure S4), and the ability to differentiate into 3 germ layers by qPCR (Supplementary data 2). This information is provided in the Methods (Lines 358-362).

*-Did the authors measure the cell proliferation rate in H2B-overexpressing cells and controls? Since H2B plays an important role in cytokinesis, it could interfere in cell division when H2B is overexpressed (see doi: 10.3390/cells8111391). *

We did not directly measure cell division when H2B is over-expressed. However, we assessed cell -passaging time of all the transfected cell lines. This showed that they grow to similar densities at each passage compared to the parental line (this is now provided as Supplementary data 1 and is cited in the Methods, line 348). We also found no difference between apical visiting time of progenitors in spinal cord rosettes expressing pm-eGFP or H2B-mEoS3.2, further supporting the conclusion that levels of H2B-mEoS3.2 expression achieved in this line did not interfere with cell division (metadata provided in Supplementary data 3).

The authors should provide data concerning the efficiency of expression of the distinct markers after electroporation. This is provided in Supplementary Figure S1 (FACS data) and detailed above for this reviewer.

*At Fig 1C, the schematic representation describes clone selection, however in the methods it is stated (L348-349): "Sorted cells expressing medium levels of fluorescence were expanded and frozen then representative lots of each polyclonal cell line...". There is some confusion regarding which experiments were performed using polyclonal medium-level mixed populations or monoclonal populations. *

We apologise for any confusion and have revised the Figure 1C schematic to indicate that cells can be selected to either make polyclonal lines or clonal lines.

*Reviewer #2 (Significance (Required)):

The study provides novel tools, as well as elements regarding neuroepithelium biology. It is well conducted and written, and the quality of images is excellent. It reads more as a resource paper in its current version, since the observation regarding neural cell division and delamination are interesting but not deeply explored, so this review will focus on those technical aspects rather than the novelty of the biological findings.

This study would be of interests for researchers in stem cells and organoids, developmental biology, and neurosciences.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

In the manuscript, "Engineering fluorescent reporters in human pluripotent cells and strategies for live imaging human neurogenesis" the authors Dady et al. describe the adaptation of a recent advancement in transposase technology (HyPBase) as a method to integrate live reporters in human pluripotent stem cells. They show that these florescent reporters paired with new imaging strategies can be used to confirm the existence cellular behaviour described in other species such as the interkinetic nuclear migration (IKNM) of dividing progenitors in neural tube development. Finally, they demonstrate that this live imaging system is also able to discover novel biology by identifying previously undescribed actin polymerization at the basal nuclear surface of cortical progenitors undergoing cell division. Overall, the study presents two examples in which this adapted tool will aid in live-imaging studies of cellular biology.

Major Concerns: 1. This work needs more controls to properly demonstrate claims that their engineering strategy provides an advancement to current Piggyback methods. Their HyPBase strategy needs to be compared and quantified in terms of efficiency with other methods to support their claims (increased detection and reduced phototoxicity).*

We do not make specific claims for our experiments with respect to the superiority of HyPBase strategy. Our comments on this approach referred to by the reviewer here are in the Introduction (L 94-103), are supported by the literature (e.g. more stable gene expression than native piggyBac or the Tc1/mariner transposase Sleeping Beauty (Doherty, et al., 2012, Yusa, et al., 2011) and serve to explain our selection of HyPBase for our experiments. We make a case for using HyPBase as opposed to another transposase and although it would be interesting to compare efficiencies, this comment does not specify what “other methods” might be informative.

2.Throughout the manuscript more quantification is needed of the results. How many rosettes were examined? Were all the reported cells within one rosette? Were there differences between rosettes? This should be done for both the spinal and cortical differentiations.

The reviewer appears to have missed this information – we placed detailed quantifications in the figure legends (numbers of independent experiments and rosettes) and in the Methods in a specific section on Quantification of cell behaviour (L465-486), rather than in the main text. These has since been further updated and we now also provide additional metadata in the form of Excel spreadsheets for quantifications and analyses made for both spinal cord and cortical rosettes (Supplementary data 3 and 4 respectively).

Minor Comments: 1. Line 246 needs quantification shown in figures of the statements made. Specifically, how many cells were measured to get this number?

This information was provided in the figure 4 legend and we have since added numbers to these data; we were able to monitor 169 divisions in 21 rosettes; 154/166 divisions had vertical cleavage planes (symmetric) and 12/166 had horizontal cleavage planes (asymmetric).

These detailed observations were made in two independent experiments, along with observations of basal nuclear membrane F-Tractin localisation. This is noted in figure 4 legend, Methods and detailed metadata is provided in Supplementary data 4.

2.How many cells in the cortical rosettes had the enriched actin at the basal nuclear surface?

We confidently observed basal nuclear membrane F-Tractin enrichment in 141/146 divisions, for the remaining 20 cases (166-146), we could not tell whether F-Tractin is enriched or not at the basal nuclear membrane either because of low expression levels or because the basal nuclear membrane was out of focus at NEB. In 5 cases, we did not see the basal nuclear enrichment despite sufficient F-Tractin expression levels and the nucleus being in focus. We have updated the Fig4 legend excluding the non-analysable cases and see detailed metadata is provided in Supplementary data 4.

*Reviewer #3 (Significance (Required)):

General Assessment: This manuscript makes a very minor advancement in the field of stem cell engineering and developmental biology, but one that is worthy of publication with a few edits.

Advance: While PiggyBac reporters are widely used in stem cell engineering, Dady et al. demonstrate a new workflow using HyPBase which would be beneficial to the field. However, to increase this benefit, much more description and quantification of the methods would be needed. The biological advances of this manuscript are also very minor, but interesting as most of them confirm that human neural rosettes mimic many of the observed cell behaviours seen in animal models. Along these lines is the actin dynamics observation in cortical rosettes is interesting, but a preliminary observation and in need of follow up experiments.

Audience: Regardless, this technique would be of interest to the wider field of stem cell engineering.

My Expertise: Human Stem Cell Engineering, Neural Tube Development*

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors have assembled a cohort of 10 SiNET, 1 SiAdeno, and 1 lung MiNEN samples to explore the biology of neuroendocrine neoplasms. They employ single-cell RNA sequencing to profile 5 samples (siAdeno, SiNETs 1-3, MiNEN) and single-nuclei RNA sequencing to profile seven frozen samples (SiNET 4-10).

They identify two subtypes of siNETs, characterized by either epithelial or neuronal NE cells, through a series of DE analyses. They also report findings of higher proliferation in non-malignant cell types across both subtypes. Additionally, they identify a potential progenitor cell population in a single-lung MiNEN sample.

Strengths:

Overall, this study adds interesting insights into this set of rare cancers that could be very informative for the cancer research community. The team probes an understudied cancer type and provides thoughtful investigations and observations that may have translational relevance.

Weaknesses:

The study could be improved by clarifying some of the technical approaches and aspects as currently presented, toward enhancing the support of the conclusions:

(1) Methods: As currently presented, it is possible that the separation of samples by program may be impacted by tissue source (fresh vs. frozen) and/or the associated sequencing modality (single cell vs. single nuclei). For instance, two (SiNET1 and SiNET2) of the three fresh tissues are categorized into the same subtype, while the third (SiNET9) has very few neuroendocrine cells. Additionally, samples from patient 1 (SiNET1 and SiNET6) are separated into different subtypes based on fresh and frozen tissue. The current text alludes to investigations (i.e.: "Technical effects (e.g., fresh vs. frozen samples) could also impact the capture of distinct cell types, although we did not observe a clear pattern of such bias."), but the study would be strengthened with more detail.

We thank the reviewer for the thoughtful and constructive review. Due to the difficulty in obtaining enough SiNET samples, we used two platforms to generate data - single cell analysis of fresh samples, and single nuclei analysis of frozen samples. We opted to combine both sample types in our analysis while being fully aware of the potential for batch effects. We therefore agree that this is a limitation of our work, and that differences between samples should be interpreted with caution.

Nevertheless, we argue that the two SiNET subtypes that we have identified are very unlikely to be due to such batch effect. First, the epithelial SiNET subtype was not only detected in two fresh samples but also in one frozen sample (albeit with relatively few cells, as the reviewer correctly noted). Second, and more importantly, the epithelial SiNET subtype was also identified in analysis of an external and much larger cohort of bulk RNA-seq SiNET samples that does not share the issue of two platforms (as seen in Fig. 2f). Moreover, the proportion of samples assigned to the two subtypes is similar between our data and the external data. We therefore argue that the identification of two SiNET subtypes cannot be explained by the use of two data platforms. However, we agree that the results should be further investigated and validated by future studies.

The reviewer also commented that two samples from the same patient which were profiled by different platforms (SiNET1 and SiNET6) were separated into different subtypes. We would like to clarify that this is not the case, since SiNET6 was not included in the subtype analysis due to too few detected Neuroendocrine cells, and was not assigned to any subtype, as noted in the text and as can be seen by its exclusion from Figure 2 where subtypes are defined. We apologize that our manuscript may have given the wrong impression about SiNET6 classification (it was labeled in Fig. 4a in a misleading manner). In the revised manuscript, we corrected the labeling in Fig. 4a and clarified that SiNET6 is not assigned to any subtype. We also further acknowledge the limitation of the two platforms and the arguments in favor of the existence of two SiNET subtypes.     

(Additional specific recommendations for the authors are provided below)

(2) Results:

Heterogeneity in the SiNET tumor microenvironment: It is unclear if the current analysis of intratumor heterogeneity distinguishes the subtypes. It may be informative if patterns of tumor microenvironment (TME) heterogeneity were identified between samples of the same subtype. The team could also evaluate this in an extension cohort of published SiNET tumors (i.e. revisiting additional analyses using the SiNET bulk RNAseq from Alvarez et al 2018, a subset of single-cell data from Hoffman et al 2023, or additional bulk RNAseq validation cohorts for this cancer type if they exist [if they do not, then this could be mentioned as a need in Discussion])

We agree that analysis of an independent cohort will assist in defining the association between TME and the SiNET subtype. However, the sample size required for that is significantly larger than the data available. In the revised manuscript we note that as a direction for future studies.

(3) Proliferation of NE and immune cells in SiNETs: The observed proliferation of NE and immune cells in SiNETs may also be influenced by technical factors (including those noted above). For instance, prior studies have shown that scRNA-seq tends to capture a higher proportion of immune cells compared to snRNA-seq, which should be considered in the interpretation of these results. Could the team clarify this element?

We agree that different platforms could affect the observed proportions of immune cells, and more generally the proportions of specific cell types. However, the low proliferation of Neuroendocrine cells and the higher proliferation of immune cells (especially B cells, but also T cells and macrophages) is consistently observed in both platforms, as shown in Fig. 4a, and therefore appears to be reliable despite the limitations of our work. We clarify this consistency in the revised manuscript. 

(4) Putative progenitors in mixed tumors: As written, the identification of putative progenitors in a single lung MiNEN sample feels somewhat disconnected from the rest of the study. These findings are interesting - are similar progenitor cell populations identified in SiNET samples? Recognizing that ideally additional validation is needed to confidently label and characterize these cells beyond gene expression data in this rare tumor, this limitation could be addressed in a revised Discussion.

We do not find evidence for similar progenitors in the SiNET samples, but they also do not contain two co-existing lineages of cancer cells within the same tumor, so this is harder to define. We agree about the need for additional validation for this specific finding and have noted that in the revised Discussion.

Reviewer #2 (Public review):

Summary:

The research identifies two main SiNET subtypes (epithelial-like and neuronal-like) and reveals heterogeneity in non-neuroendocrine cells within the tumor microenvironment. The study validates findings using external datasets and explores unexpected proliferation patterns. While it contributes to understanding SiNET oncogenic processes, the limited sample size and depth of analysis present challenges to the robustness of the conclusions.

Strengths:

The studies effectively identified two subtypes of SiNET based on epithelial and neuronal markers. Key findings include the low proliferation rates of neuroendocrine (NE) cells and the role of the tumor microenvironment (TME), such as the impact of Macrophage Migration Inhibitory Factor (MIF).

Weaknesses:

However, the analysis faces challenges such as a small sample size, lack of clear biological interpretation in some analyses, and concerns about batch effects and statistical significance.

Reviewer #3 (Public review):

Summary:

In this study, the authors set out to profile small intestine neuroendocrine tumors (siNETs) using single-cell/nucleus RNA sequencing, an established method to characterize the diversity of cell types and states in a tumor. Leveraging this dataset, they identified distinct malignant subtypes (epithelial-like versus neuronal-like) and characterized the proliferative index of malignant neuroendocrine cells versus non-malignant microenvironment cells. They found that malignant neuroendocrine cells were far less proliferative than some of their non-malignant counterparts (e.g., B cells, plasma cells, epithelial cells) and there was a strong subtype association such that epithelial-like siNETs were linked to high B/plasma cell proliferation, potentially mediated by MIF signaling, whereas neuronal-like siNETs were correlated with low B/plasma cell proliferation. The authors also examined a single case of a mixed lung tumor (neuroendocrine and squamous) and found evidence of intermediate/mixed and stem-like progenitor states that suggest the two differentiated tumor types may arise from the same progenitor.

Strengths:

The strengths of the paper include the unique dataset, which is the largest to date for siNETs, and the potentially clinically relevant hypotheses generated by their analysis of the data.

Weaknesses:

The weaknesses of the paper include the relatively small number of independent patients (n = 8 for siNETs), lack of direct comparison to other published single-cell NET datasets, mixing of two distinct methods (single-cell and single-nucleus RNA-seq), lack of direct cell-cell interaction analyses and spatially-resolved data, and lack of in vitro or in vivo functional validation of their findings.

The analytical methods applied in this study appear to be appropriate, but the methods used are fairly standard to the field of single-cell omics without significant methodological innovation. As the authors bring forth in the Discussion, the results of the study do raise several compelling questions related to the possibility of distinct biology underlying the epithelial-like and neuronal-like subtypes, the origin of mixed tumors, drivers of proliferation, and microenvironmental heterogeneity. However, this study was not able to further explore these questions through spatially-resolved data or functional experiments.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Methods:

a) Could the team clarify the discrepancy in subtype assignment between two samples from the same patient? i.e. are these samples from the same tumor? If so, what does the team think is the explanation for the difference in subtype assignment?

As noted above in response to the public review of reviewer #1, SiNET6 was in fact not assigned to any subtype (due to insufficient NE cells) and hence there was no discrepancy. We apologize for the misleading labeling of SiNET6 in the previous version and have corrected this In the revised version of Figure 4.

b) What is the rationale for scoring tumor-derived programs on samples with no tumor cells? For instance, SiNET3 does not contain NE cells, and SiNET9 has a very low fraction of NE cells. Please clarify how the scoring was performed on these samples, as the program assignments may be driven by other cell types in samples with little to no NE cells.

Scoring for tumor-derived programs was done only for the NE cells. Accordingly, SiNET3 was not scored or assigned to any of the programs. SINET9 was included in this analysis - although it had a relatively small fraction of NE cells, the absolute number of profiled cells was particularly high in this sample and therefore the number of NE cells was 130, higher than our cutoff of 100 cells.

c) Given the heterogeneity of cell types within each sample, would there be a way to provide a refined sense of confidence for certain cell type annotations? This would be helpful given the heterogeneity in marker gene expression and the absence of gold-standard markers for fibroblasts and endothelial cells in this cancer type. Additionally, there seems to be an unusually large proportion of NK and T cells - was there selection for this (given that these tumors are largely not immune infiltrated)?

Author Response: Except for the Neuroendocrine cells, there are six TME cell types that we consistently find in multiple SiNET samples: macrophages, T cells, B/plasma cells, fibroblasts, endothelial and epithelial cells. Each of these cell types are identified as discrete clusters in analysis of the respective tumors (as shown in Fig. 1a,b and Fig. S1), and these are exactly the six most common non-malignant cell types that we and others found in single cell analysis across various other tumor types (e.g. see Gavish et al. 2023, ref. #15). The signatures used to annotate these cell types are shown in Table S2, and they primarily consist of classical markers that are traditionally used to define those cell types. We therefore believe that the annotation of these typical tumor-associated cell types is robust and does not include major uncertainties. In addition to these five common cell types, there are three cell types that we find only in 1-2 of the samples – epithelial cells, plasma cells and NK cells. Again, we believe that their annotation is robust, and these cell types are primarily not used for further analysis.

There was no selection for any specific cell types in this study. Nevertheless, single cell (or single nuclei) analysis may lead to biases towards specific cell types, that we cannot evaluate directly from the data. NK cells were detected only in one tumor. T cells were detected in eight of the ten samples; but in four of those samples the frequency of T cells was lower than 5% and only in one sample the frequency was above 20%. Therefore, while we cannot exclude a technical bias towards high frequency of T/NK cells, we do not consider these frequencies as high enough to suggest this specific type of bias. In the revised manuscript, we clarify that the commonly observed cell types in SiNETs are the same as those commonly observed in other tumors and we acknowledge the possibility of a technical bias in cell type capture.  

d) Evaluating the expression of one gene at a time may not effectively demonstrate subtype-specific patterns, particularly when comparing NE cells from one tumor to non-NE cells from another, which may not be an appropriate approach for identifying differentially expressed genes. DE analysis coupled with concordance analysis, for example, could strengthen the results.

We apologize, but we do not fully understand this comment. We note that the initial normalization by non-NE cells was done in order to decrease batch effects when combining the data of the two platforms. We also note that the two subtypes were identified by two distinct approaches, as shown in Fig. 2c and in Fig. 2f.

(2) Results:

See the above public review.

(3) Minor Comments:

a) Results: Single cell and single nuclei RNA-seq profiling of SiNETs

The results say ten primary tumor samples from eight patients. Later in the paragraph it says, "After initial quality controls, we retained 29,198 cells from the ten patients." Please clarify to either ten samples or eight patients.

Indeed these are ten samples rather than ten patients. We corrected that in the revised version and thank the reviewer for noticing our error.

b) Methods:

- Please specify which computational tools were used to perform quality control, signature scoring, etc.

The approaches for quality control, scoring etc. are described in the methods. We implemented these approaches with R code and did not use other computational tools.

- Minor point but be consistent with naming convention (ie, siAdeno vs SiAdeno) throughout the paper. For example, under "Sample Normalization, Filtering and annotations" change "siAdeno" to "SiAdeno."

Thank you for noting this, we corrected that.

- Add processing and analysis of MiNEN sample to the methods section. It is not mentioned in the methods at all.

As noted in the revised manuscript, the MiNEN sample was analyzed in the same way as the SiNET fresh samples.

c) Supplementary Figures:

Figure S1: Change (A-H) to (A-I) to account for all panels in the figure.

Figure S4: Add (C) after "the siAdeno sample" in the legend.

Thank you for noting this, we corrected that.

(4) Font size is quite small in the main figures.

We enlarged the font in selected figure panels.

Reviewer #2 (Recommendations for the authors):

(1) The small number of samples used in some analyses affects the robustness of the findings. Increasing the sample size or including more validation data could improve the statistical reliability and make the results more convincing. The authors should consider expanding the cohort size or integrating additional external datasets to increase statistical power.

We agree with the reviewer that adding more samples would improve the reliability of the results. However, the external data that we found was not comparable enough to enable integration with our data, and we are unable to profile additional SiNET samples in our lab. We hope that future studies would support our results and extend them further.

(2) The biological significance of differentially expressed genes needs more depth, limiting the insights into SiNET biology. The authors should perform a comprehensive pathway enrichment analysis and integrate findings with existing literature. Tools like Gene Set Enrichment Analysis (GSEA) or Overrepresentation Analysis (ORA) could provide a more holistic view of altered biological processes.

We thank the reviewer for this suggestion. We did examine the functional enrichment of differentially expressed genes and did not find additional enrichments that we felt were important to highlight beyond what we described. We report the genes in supplementary tables, enabling other researchers to examine these lists further. 

(3) The unexpected finding of higher proliferation in non-malignant cells requires further investigation and plausible biological explanation. The authors should perform additional analyses to explore potential mechanisms, such as investigating cell cycle regulators or performing in vitro validation experiments. The authors should consider single-cell trajectory analysis to explore these highly proliferative non-malignant cells' potential differentiation or activation states.

We agree that our results are descriptive and that we do not fully explain the mechanism for the high level of non-malignant cell proliferation. We did attempt to perform follow up computational analysis. These analyses raised the hypothesis that high levels of MIF are causing the proliferation of immune cells. Additional analyses that we performed were not sufficient to conclusively identify a mechanism, and we felt that they were not informative enough to be included in the manuscript. Further in vitro (or in vivo) studies are beyond the scope of the current work.

(3) More details are required on methods used for p-value adjustment, and criteria for statistical significance should be clearly defined. Additionally, integrating scRNA-seq and snRNA-seq data needs a more thorough explanation, including batch effect mitigation and more explicit cell clustering representation. The authors should clearly describe p-value adjustments (e.g., FDR) and batch correction methods (e.g., Harmony, FastMNN integration) and include additional figures showing corrected UMAP plots or heatmaps post-batch correction to enhance the confidence in results.

We now clarify in the Methods our use of FDR for p-value adjustments. As for batch correction, we have avoided the use of integration methods as we believe that they tend to distort the data and decrease tumor-specific signals. Instead, we primarily analyzed one tumor at a time and never directly compared cell profiles across distinct tumors but only compared the differences between subpopulations; specifically, we normalized the expression of NE cells by subtracting the expression of reference non-NE cells from the same tumor as a method to decrease batch effects. We now clarify this point in the Methods section.

(4) The lack of analysis of interactions between different cell types limits understanding of tumor microenvironment dynamics. The authors should employ cell-cell interaction analysis tools (e.g., CellPhoneDB, NicheNet) to explore potential communication networks within the tumor microenvironment. This could provide valuable insights into how different cell types influence tumor progression and maintenance.

We thank the reviewer for this suggestion. We have tried to use such methods but found the results difficult to interpret since these approaches generated very long lists of potential cell-cell interactions that are largely not unique to the SiNET context and their relevance remains unclear without follow up experiments, which are beyond the scope of this work. We therefore focused only on ligand/receptors that came up robustly through specific analyses such as the differences between SiNET subtypes. In particular, MIF is highly expressed in the epithelial subtype, and remarkably, MIF upregulation is shared across multiple cell types. Thus, the cell-cell interactions that are suggested by the SiNET data as somewhat unique to this context are those involving MIF and its receptor (CD74 on immune cell types), while other interactions detected by the proposed methods primarily reflect the generic ligand/receptors expressed by corresponding TME cell types.   

Reviewer #3 (Recommendations for the authors):

(1) For a relatively small dataset, the mixing of single-cell versus single-nucleus RNA-seq should be discussed more. It would be nice to have 1-2 tumors that are analyzed by both methods to compare and increase our understanding of how these different approaches may affect the results. This could be accomplished by splitting a fresh tumor into two parts, processing it fresh for single-cell RNA-seq, and freezing the other part for single-nucleus RNA-seq.

We agree with the reviewer that the different techniques may bias our results and we refer to this limitation in the Results and Discussion sections. However, it is important to note that we do not directly integrate the primary data across these modalities, but rather analyze each tumor separately and only combine the results across tumors. For example, we first compare the NE cells from each tumor to control non-NE cells from the same tumor and then only compare the sets of NE-specific genes across tumors. Moreover, the subtypes that we detect cannot be explained by these modalities, as the first subtype contains samples from both methods and these subtypes are further demonstrated in external bulk data. Similarly, the results regarding low proliferation of NE cells and high proliferation of B/plasma cells are observed across both modalities. We therefore argue that while the combination of methods is a limitation of this work it does not account for the main results.  

(2) The authors state that they defined the siNET transcriptomic signature by comparing their siNET single-cell/nucleus data to other NETs profiled by bulk RNA-seq. Some of the genes in the signature, such as CHGA, are widely used as markers for NETs (and not specific for siNET). The authors should address this in more detail.

To define the SiNET transcriptomic signature we first analyzed each tumor separately and compared the expression of Neuroendocrine (NE) cells to that of non-NE cells to detect NE-specific genes. Next, we compared the lists of NE-specific genes across the 8 SiNET patients and found a subset of 26 genes which were shared across most of the analyzed SiNET samples (Fig. 2a). Thus, the signature was defined only from analysis of SiNETs and not based on comparison to other types of NETs and hence it is expected that the signature could contain both SiNET-specific genes and more generic NET genes such as CHGA.

Only after defining this signature, we went on to compare it between SiNETs and other types of NETs (pancreatic and rectal) based on external bulk RNA-seq data. In this comparison, we observed that the signature was clearly higher in SiNETs than in the other NETs (Fig. 2b). This result supports the accuracy of the signature and further suggests that it contains a fraction of SiNET-specific genes and not only generic NET genes such as CHGA. Thus, we would expect this signature to perform well also for distinguishing between SiNET and types of NETs, but it does contain a subset of genes that would be high in the other NETs. Finally, we note that even though CHGA is a generic NET marker, the bulk RNA-seq data would suggest that, at least at the mRNA level, this gene is still higher expressed in SiNETs than in other NETs. To avoid confusion regarding the definition and specificity of the SiNET transcriptomic signature we have extended the description of this section in the revised manuscript.

(3) The authors only compare their data to bulk transcriptomic data on NETs. While in some instances this makes sense given the bulk dataset has >80 tumors, they should at least cite and do some comparison to other published single-cell RNA-seq datasets of NETs (e.g., PMID: 37756410, 34671197). The former study listed has 3 siNETs, 4 pNETs, and 1 gNET. Do the epithelial-like and neuronal-like signatures show up in this dataset too?

We examined these studies but concluded that their data was inadequate to identify the two SiNET subtypes. The latter study was of pNETs, while the former study had 3 SiNET samples but only from 2 patients, and furthermore it was enriching for immune cells with only very low amounts of NE cells. Therefore, we now cite this work in the discussion but cannot use it to extend the results from our work.

(4) How did the authors statistically handle patients with more than one tumor sample (true for n = 2)? These tumor samples would not be truly independent.

In both cases where we had two distinct samples of the same patient, only one sample had sufficient NE cells to be included in NE-related analysis and therefore the other samples (SiNET3 and SiNET6) were excluded from all analysis of NE differential expression and subtypes. These samples were only included in the initial analysis (Fig. 1) and in TME-related analysis (Fig. 3-4) in which there was no statistical analysis of differences between patients and hence no problem with the inclusion of 2 samples for the same patient. We clarified this issue in the revised version.

(5) The association between siNET subtype and B/plasma cell proliferation is very interesting, as is the hypothesis regarding MIF signaling. It would be illuminating for the authors to perform cell-cell interaction analyses with methods such as CellChat in this context rather than just relying on DE. Spatial mapping would be helpful too and while this may be outside the scope of this study, it should at least be expounded upon in the Discussion section.

Indeed, spatial transcriptomic analysis would add interesting insight to our data and to SiNET biology. Unfortunately, this is not within the scope of the current project but we note this interesting possibility in the Discussion. Regarding additional methods for cell-cell interactions, we have performed such analysis but found it not informative as it highlighted a large number of interactions that are not unique SiNETs and are difficult to interpret, and therefore we do not include this in the revised version. 

(6) The authors note that in the mixed lung tumor, the NE component was more proliferative than that observed with siNETs. How does the proliferation compare to pNETs, gNETs, in other published studies? How about assessing the clonality of the SCC and LNET malignant cells with various genomic or combined genomic/transcriptomic methods?

The percentage of proliferating NE cells in the mixed lung tumor was higher than 60%. This is extremely high, approximately four-fold higher than the average that we found in a pan-cancer analysis and higher than the average of any of the >20 cancer types that we analyzed (Gavish et al. 2023, ref. #15). This remarkably high proliferation serves as a control for the low proliferation that we found in SiNET NE cells.

(7) In the Discussion on page 13, the authors write "Second, proliferation of NE cells may be inhibited by prior treatments with somatostatin analogues." How many patients were treated in this manner? This information should be made more explicit in the manuscript.

Details on pretreatment with somatostatin analogues are provided in Table S1. All patients were pre-pretreated with somatostatin analogues, with the possible exception of one patient (P8, SiNET10) for which we could not confidently obtain this information.

(8) On page 5, "bone-fide" is misspelled.

(9) On page 8, "exact identify" is misspelled.

We thank the reviewer and have corrected the typos.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors provide a study among healthy individuals, general medical patients and patients receiving haematopoietic cell transplants (HCT) to study the gut microbiome through shotgun metagenomic sequencing of stool samples. The first two groups were sampled once, while the patients receiving HCT were sampled longitudinally. A range of metadata (including current and previous (up to 1 year before sampling) antibiotic use) was recorded for all sampled individuals. The authors then performed shotgun metagenomic sequencing (using the Illumina platform) and performed bioinformatic analyses on these data to determine the composition and diversity of the gut microbiota and the antibiotic resistance genes therein. The authors conclude, on the basis of these analyses, that some antibiotics had a large impact on gut microbiota diversity, and could select opportunistic pathogens and/or antibiotic resistance genes in the gut microbiota.

Strengths:

The major strength of this study is the considerable achievement of performing this observational study in a large cohort of individuals. Studies into the impact of antibiotic therapy on the gut microbiota are difficult to organise, perform and interpret, and this work follows state-of-the-art methodologies to achieve its goals. The authors have achieved their objectives and the conclusion they draw on the impact of different antibiotics and their impact on the gut microbiota and its antibiotic resistance genes (the 'resistome', in short), are supported by the data presented in this work.

Weaknesses:

The weaknesses are the lack of information on the different resistance genes that have been identified and which could have been supplied as Supplementary Data.

We have now supplied a list of individual resistance genes as supplementary data.

In addition, no attempt is made to assess whether the identified resistance genes are associated with mobile genetic elements and/or (opportunistic) pathogens in the gut. While this is challenging with short-read data, alternative approaches like long-read metagenomics, Hi-C and/or culture-based profiling of bacterial communities could have been employed to further strengthen this work.

We agree this is a limitation, and we now refer to this in the discussion. Unfortunately we did not have funding to perform additional profiling of the samples that would have provided more information about the genetic context of the AMR genes identified.

Unfortunately, the authors have not attempted to perform corrections for multiple testing because many antibiotic exposures were correlated.

The reviewer is correct that we did not perform formal correction for multiple testing. This was because correlation between antimicrobial exposures meant we could not determine what correction would be appropriate and not overly conservative. We now describe this more clearly in the statistical analysis section.

Impact:

The work may impact policies on the use of antibiotics, as those drugs that have major impacts on the diversity of the gut microbiota and select for antibiotic resistance genes in the gut are better avoided. However, the primary rationale for antibiotic therapy will remain the clinical effectiveness of antimicrobial drugs, and the impact on the gut microbiota and resistome will be secondary to these considerations.

We agree that the primary consideration guiding antimicrobial therapy will usually be clinical effectiveness. However antimicrobial stewardship to minimise microbiome disruption and AMR selection is an increasingly important consideration, particularly as choices can often be made between different antibiotics that are likely to be equally clinically effective.

Reviewer #2 (Public Review):

Summary:

In this manuscript by Peto et al., the authors describe the impact of different antimicrobials on gut microbiota in a prospective observational study of 225 participants (healthy volunteers, inpatients and outpatients). Both cross-sectional data (all participants) and longitudinal data (a subset of 79 haematopoietic cell transplant patients) were used. Using metagenomic sequencing, they estimated the impact of antibiotic exposure on gut microbiota composition and resistance genes. In their models, the authors aim to correct for potential confounders (e.g. demographics, non-antimicrobial exposures and physiological abnormalities), and for differences in the recency and total duration of antibiotic exposure. I consider these comprehensive models an important strength of this observational study. Yet, the underlying assumptions of such models may have impacted the study findings (detailed below). Other strengths include the presence of both cross-sectional and longitudinal exposure data and the presence of both healthy volunteers and patients. Together, these observational findings expand on previous studies (both observational and RCTs) describing the impact of antimicrobials on gut microbiota.

Weaknesses:

(1) The main weaknesses result from the observational design. This hampers causal interpretation and corrects for potential confounding necessary. The authors have used comprehensive models to correct for potential confounders and for differences between participants in duration of antibiotic exposure and time between exposure and sample collection. I wonder if some of the choices made by the authors did affect these findings. For example, the authors did not include travel in the final model, but travel (most importantly, south Asia) may result in the acquisition of AMR genes [Worby et al., Lancet Microbe 2023; PMID 37716364). Moreover, non-antimicrobial drugs (such as proton pump inhibitors) were not included but these have a well-known impact on gut microbiota and might be linked with exposure to antimicrobial drugs. Residual confounding may underlie some of the unexplained discrepancies between the cross-sectional and longitudinal data (e.g. for vancomycin).

We agree that the observational design means there is the potential for confounding, which, as the reviewer notes, we attempt to account for as far as possible in the multivariable models presented. We cannot exclude the possibility of residual confounding, and we highlight this as a limitation in the  discussion. We have expanded on this limitation, and mention it as a possible explanation for inconsistencies between longitudinal and cross sectional models. Conducting randomised trials to assess the impacts of multiple antimicrobials in sick, hospitalised patients would be exceptionally difficult, and so it is hard to avoid reliance on observational data in these settings.

We did record participants’ foreign travel and diet, but these exposures were not included in our models as they were not independently associated with an impact on the microbiome and their inclusion did not materially affect other estimates. However, because most participants were recruited from a healthcare setting, few had recent foreign travel and so this study was not well powered to assess the effects of travel on AMR carriage. We have added this as a limitation.

In addition, the authors found a disruption half-life of 6 days to be the best fit based on Shannon diversity. If I'm understanding correctly, this results in a near-zero modelled exposure of a 14-day-course after 70 days (purple line; Supplementary Figure 2). However, it has been described that microbiota composition and resistome (not Shannon diversity!) remain altered for longer periods of time after (certain) antibiotic exposures (e.g. Anthony et al., Cell Reports 2022; PMID 35417701). The authors did not assess whether extending the disruption half-life would alter their conclusions.

The reviewer is correct that the best fit disruption half-life of 6 days means the model assumes near-zero exposure by 70 days. We appreciate that antimicrobials can cause longer-term disruption than is represented in our model, and we refer to this in the discussion (we had cited two papers supporting this, and we are grateful for the additional reference above, which we have added). We agree that it is useful to clarify that the longer term effects may be seen in individual components of the microbiome or AMR genes, but not in overall measures of diversity, so have added this to the discussion.

(2) Another consequence of the observational design of this study is the relatively small number of participants available for some comparisons (e.g. oral clindamycin was only used by 6 participants). Care should be taken when drawing any conclusions from such small numbers.

We agree. Although our participants received a large number of different antimicrobial exposures, these were dependent on routine clinical practice at our centre and we lack data on many potentially important exposures. We had mentioned this in relation to antimicrobials not used at our centre, and have now clarified in the discussion that this also limits reliability of estimates for antimicrobials that were rarely used in study participants.

(3) The authors assessed log-transformed relative abundances of specific bacteria after subsampling to 3.5 million reads. While I agree that some kind of data transformation is probably preferable, these methods do not address the compositional data of microbiome data and using a pseudocount (10-6) is necessary for absent (i.e. undetected) taxa [Gloor et al., Front Microbiol 2017; PMID 29187837]. Given the centrality of these relative abundances to their conclusions, a sensitivity analysis using compositionally-aware methods (such as a centred log-ratio (clr) transformation) would have added robustness to their findings.

We agree that using a pseudocount is necessary for undetected taxa, which we have done assuming undetected taxa had an abundance of 10^-6 (based on the lower limit of detection at the depth we sequenced). We refer to this as truncation in the methods section, but for clarity we have now also described this as a pseudocount.  Because our analysis focusses on major taxa that are almost ubiquitous in the human gut microbiome, a pseudocount was only used for 3 samples that had no detectable Enterobacteriaciae.

We are aware that compositionally-aware methods are often used with microbiome data, and for some analyses these are necessary to avoid introducing spurious correlations. However the flaws in non-compositional analyses outlined in Gloor et al do not affect the analyses in this paper:

(1) The problems related to differing sequence depths or inadequate normalisation do not apply to our dataset, as we took a random subset of 3.5 million reads from all samples (Gloor et al correctly point out that this method has the drawback of losing some information, but it avoids problems related to variable sequencing depth)

(2) The remainder Gloor et al critiques multivariate analyses that assess correlations between multiple microbiome measurements made on the same sample, starting with a dissimilarity matrix. With compositional data these can lead to spurious correlations, as measurements on an individual sample are not independent of other measurements made on the same sample. In contrast, our analyses do not use a dissimilarity matrix, but evaluate the association of multiple non-microbiome covariates (e.g. antibiotic exposures, age) with single microbiome measures. We use a separate model for each of 11 specified microbiome components, and display these results side-by side. This does not lead to the same problem of spurious correlation as analyses of dissimilarity matrices. However, it does mean that estimates of effects on each taxa outcome have to be interpreted in the context of estimates on the other taxa. Specifically, in our models, the associations of antimicrobial exposure with different taxa/AMR genes are not necessarily independent of each other (e.g. if an antimicrobial eradicated only one taxon then it would be associated with an increase in others). This is not a spurious correlation, and makes intuitive sense when using relative abundance as outcome. However, we agree this should be made more explicit.

For these reasons, at this stage we would prefer not to increase the complexity of the manuscript by adding a sensitivity analysis.

(4) An overall description of gut microbiota composition and resistome of the included participants is missing. This makes it difficult to compare the current study population to other studies. In addition, for correct interpretation of the findings, it would have been helpful if the reasons for hospital visits of the general medical patients were provided.

We have added a summary of microbiome and resistome composition in the results section and new supplementary table 2), and we also now include microbiome and resistome profiles of all samples in the supplementary data. We also provide some more detail about the types of general medical patients included. We are not able to provide a breakdown of the initial reason for admission as this was not collected.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Provide a supplementary table with information on the abundance of individual genes in the samples.

This supplementary data is now included.

(2) Engage with an expert in statistics to discuss how statistical analyses can be improved.

A experienced biostatistician has been involved in this study since its conception, and was involved in planning the analysis and in the responses to these comments.

(3) Typos and other minor corrections:

Methods: it is my understanding that litre should be abbreviated with a lowercase l.

Different journals have different house styles: we are happy to follow Editorial guidance.

p. 9: abuindance should be corrected to abundance.

Corrected

p. 9: relative species should be relevant species?  

Yes, corrected. Thank you.

p. 9 - 10: can the apparent lack of effect of beta-lactams on beta-lactamase gene abundance be explained by the focus on a small number of beta-lactamase resistance genes that are found in Enterobacteriaceae and which are not particularly prevalent, while other classes of resistance genes (e.g. Bacteroidal beta-lactamases) were excluded?

It is possible that including other beta-lactamases would have led to different results, but as a small number of beta-lactamases in Enterobacteriaceae are of major clinical importance we decided to focus on these (already justified in the Methods). A full list of AMR genes identified is now provided in the supplementary data.

p. 10: beta-lactamse should be beta-lactamase

Corrected

Figure 3A: could the data shown for tetracycline resistance genes be skewed by tetQ, which is probably one of the most abundant resistance genes in the human gut and acts through ribosome protection?

TetQ was included, but only accounted for 23% of reads assigned to tetracycline resistance genes so is unlikely to have skewed the overall result. We limited the analysis to a few major categories of AMR genes and, other than VanA, have avoided presenting results for single genes to limit the degree of multiple testing. We now include the resistome profile for each sample in the supplementary data so that readers can explore the data if desired.

Reviewer #2 (Recommendations For The Authors):

(1) Given the importance of obligate anaerobic gut microbiota for human health, it might be interesting to divide antibiotics into categories based on their anti-anaerobic activity and assess whether these antibiotics differ in their effects on gut microbiota.

The large majority of antibiotics used in clinical practice have activity against aerobic bacteria and anaerobic bacteria, so it is not possible to easily categorise them this way. There are two main exceptions (metronidazole and aminoglycosides) but there was insufficient use of these drugs to clearly detect or rule out a difference between them, even when categorising antimicrobials by class, so we prefer not to frame the results in these terms. Also see our comments on this categorisation below.

(2) For estimating the abundance of anaerobic bacteria, three major groups were assessed: Bacteroidetes, Actinobacteria and Clostridia. To me, this seems a bit aspecific. For example, the phylum Bacteroidetes contains some aerobic bacteria (e.g. Flavobacteriia). Would it be possible to provide a more accurate estimation of anaerobic bacteria?

We think that an emphasis on a binary aerobic/anaerobic classification is less biologically meaningful that the more granular genetic classification we use, and its use largely reflects the previous reliance on culture-based methods for bacterial identification. Although some important opportunistic human pathogens are aerobic, it is not clear that the benefit or harm of most gut commensals relates to their oxygen tolerance, and all luminal bacteria exist in an anaerobic environment. As such we prefer not to perform an additional analysis using this category. We are also not sure that this could be done reliably, as many of the taxa are characterised poorly, or not at all.

We appreciate that Bacteroidetes, Actinobacteria and Clostridia are diverse taxa that include many different species, so may seem non-specific, but these were chosen because:

i) they are non-overlapping with Enterobacteriaceae and Enterococcus, the major opportunistic pathogens of clinical relevance, so could be used in parallel, and

ii) they make up the large majority of the gut microbiome in most people and most species are of low pathogenicity, so it is plausible that their disruption might drive colonisation with more pathogenic organisms (or those carrying important AMR genes).

We have more clearly stated this rationale.

(3) A statement on the availability of data and code for analysis is missing. I would highly recommend public sharing of raw sequence data and R code for analysis. If possible, it would be very valuable if processed microbiome data and patient metadata could be shared.

We agree, and these have been submitted as supplementary data. We have added the following statement “The data and code used to produce this manuscript are available in the supplementary material, including processed microbiome data, and pseudonymised patient metadata. The sequence data for this study have been deposited in the European Nucleotide Archive (ENA) at EMBL-EBI under accession number PRJEB86785.”

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Cao et al. provides a compelling investigation into the role of mutational input in the rapid evolution of pesticide resistance, focusing on the two-spotted spider mite's response to the recent introduction of the acaricide cyetpyrafen. This well-documented introduction of the pesticide - and thus a clearly defined history of selection - offers a powerful framework for studying the temporal dynamics of rapid adaptation. The authors combine resistance phenotyping across multiple populations, extensive resequencing to track the frequency of resistance alleles, and genomic analyses of selection in both contemporary and historical samples. These approaches are further complemented by laboratory-based experimental evolution, which serves as a baseline for understanding the genetic architecture of resistance across mite populations in China. Their analyses identify two key resistance-associated genes, sdhB and sdhD, within which they detect 15 mutations in wild-collected samples. Protein modeling reveals that these mutations cluster around the pesticide's binding site, suggesting a direct functional role in resistance. The authors further examine signatures of selective sweeps and their distribution across populations to infer the mechanisms - such as de novo mutation or gene flow-driving the spread of resistance, a crucial consideration for predicting evolutionary responses to extreme selection pressure. Overall, this is a well-rounded, thoughtfully designed, and well-written manuscript. It shows significant novelty, as it is relatively rare to integrate broad-scale evolutionary inference from natural populations with experimentally informed bioassays, however, some aspects of the methods and discussion have an opportunity to be clarified and strengthened.

Strengths:

One of the most compelling aspects of this study is its integration of genomic time-series data in natural populations with controlled experimental evolution. By coupling genome sequencing of resistant field populations with laboratory selection experiments, the authors tease apart the individual effects of resistance alleles along with regions of the genome where selection is expected to occur, and compare that to the observed frequency in the wild populations over space and time. Their temporal data clearly demonstrates the pace at which evolution can occur in response to extreme selection. This type of approach is a powerful roadmap for the rest of the field of rapid adaptation.

The study effectively links specific genetic changes to resistance phenotypes. The identification of sdhB and sdhD mutations as major drivers of cyetpyrafen resistance is well-supported by allele frequency shifts in both field and experimental populations. The scope of their sampling clearly facilitated the remarkable number of observed mutations within these target genes, and the authors provide a careful discussion of the likelihood of these mutations from de novo or standing variation. Furthermore, the discovered cross-resistance that these mutations confer to other mitochondrial complex II inhibitors highlights the potential for broader resistance management and evolution.

Weaknesses:

(1) Experimental Evolution:

- Additional information about the lab experimental evolution would be useful in the main text. Specifically, the dose of cyetpyrafen used should be clarified, especially with respect to the LD50 values. How does it compare to recommended field doses? This is expected to influence the architecture of resistance evolution. What was the sample size? This will help readers contextualize how the experimental design could influence the role of standing variation.

The experimental design involved sampling approximately 6,000 individuals from the wild population ZJSX1, which were subsequently divided into two parallel cohorts under controlled laboratory conditions. The selection group (LabR) was subjected to continuous selection pressure using cyetpyrafen, while the control group (LabS) was maintained under identical laboratory conditions without exposure to acyetpyrafen. A dynamic selection regime was implemented wherein the acaricide dosage was systematically adjusted every two generations to maintain a consistent selection intensity, achieving a mortality rate of 60% ± 10% in the LabR population. This adaptive dosage strategy ensured sustained evolutionary pressure while preventing population collapse. The LC₅₀ values were tested at F1, F32, F54, F60, F62, and F66 generations using standardized bioassay protocols to quantify resistance development trajectories and optimize dosage for subsequent selection cycles. We provided the additional information in subsection 4.1 of the materials and methods section.

- The finding that lab-evolved strains show cross-resistance is interesting, but potentially complicates the story. It would help to know more about the other mitochondrial complex II inhibitors used across China and their impact on adaptive dynamics at these loci, particularly regarding pre-existing resistance alleles. For example, a comparison of usage data from 2013, 2017, and 2019 could help explain whether cyetpyrafen was the main driver of resistance or if previous pesticides played a role. What happened in 2020 that caused such rapid evolution 3 years after launch?

Although the introduction of the other two SDHI acaricides complicates the story, we would like to provide a complete background on the usage of acaricides with this mode of action in China. Although cyflumetofen was released in 2013 before cyetpyrafen, and cyenopyrafen was released in 2019 after cyetpyrafen, their market share is minor (about 3.2%) compared to cyetpyrafen (about 96.8%, personal communication). Since cross-resistance is reported among SDHIs, we could not exclude the contribution of cyflumetofen to the initial accumulation of resistance alleles, but the effect should be minor, both because of their minimal market share and because of the independent evolution of resistance in the field as found in our study. Although the contribution of cyflumetofen and cyenopyrafen cannot be entirely excluded, the rapid evolution of resistance seems likely to be mainly explained by the intensive application of cyetpyrafen. To clarify this issue, we added relevant information in the first paragraph of the discussion section.

(2) Evolutionary history of resistance alleles:

- It would be beneficial to examine the population structure of the sampled populations, especially regarding the role of migration. Though resistance evolution appears to have had minimal impact on genome-wide diversity (as shown in Supplementary Figure 2), could admixture be influencing the results? An explicit multivariate regression framework could help to understand factors influencing diversity across populations, as right now much is left to the readers' visual acuity.

The genetic structure of the populations was examined by Treemix analysis. We detected only one migration event from JXNC to SHPD (no resistance data available for these two populations), suggesting a limited role for migration to resistance evolution. The multiple regression analysis revealed that overall genetic diversity and Tajima’s D across the genome were not significantly associated with resistance levels, genetic structure or geographic coordinates (P > 0.05), which all support a limited role of migration in resistance development.

- It is unclear why lab populations were included in the migration/treemix analysis. We might suggest redoing the analysis without including the laboratory populations to reveal biologically plausible patterns of resistance evolution.

Thank you for the constructive suggestion. The Treemix analysis was redone by removing laboratory populations and is now reported.

- Can the authors explore isolation by distance (IBD) in the frequency of resistance alleles?

Thank you for the constructive suggestion. No significant isolation-by-distance pattern was detected for resistance allele frequencies across all surveyed years (2020: P=0.73; 2021: P=0.52; 2023: P=0.16; Mantel test). We added these results to the text.

- Given the claim regarding the novelty of the number of pesticide resistance mutations, it is important to acknowledge the evolution of resistance to all pesticides (antibiotics, herbicides, etc.). ALS-inhibiting herbicides have driven remarkable repeatability across species based on numerous SNPs within the target gene.

We appreciate this comment, which highlights the need to place our findings within the broader evolutionary context of pesticide resistance. We have investigated references relevant to the evolution of resistance to diverse pesticides. As far as we can tell, the 15 target mutations in eight amino acid residues are among the highest number of pesticide resistance mutations detected, especially within the context of animal studies. We have added relevant text to the second paragraph of the discussion.

- Figure 5 A-B. Why not run a multivariate regression with status at each resistance mutation encoded as a separate predictor? It is interesting that focusing on the predominant mutation gives the strongest r2, but it is somewhat unintuitive and masks some interesting variation among populations.

We conducted a multiple regression analysis to explore the influence of multiple mutations on resistance levels of field populations. However of 15 putative resistant mutations, only five were detected in more than three populations where bioassay data are available, i.e. I260T, I260V, D116G, R119C, R119L. The frequency of three of these mutations, I260T (P = 0.00128), I260V (P = 0.00423) and D116G (P = 0.00058), are significantly correlated with the resistance level of field populations. This has been added.

(3) Haplotype Reconstruction (Line 271-):

- We are a bit sceptical of the methods taken to reconstruct these haplotypes. It seems as though the authors did so with Sanger sequencing (this should be mentioned in the text), focusing only on homozygous SNPs. How many such SNPs were used to reconstruct haplotypes, along what length of sequence? For how many individuals were haplotypes reconstructed? Nonetheless, I appreciated that the authors looked into the extent to which the reconstructed haplotypes could be driven by recombination. Can the authors elaborate on the calculations in line 296? Is that the census population size estimate or effective?

Because haplotypes could not be determined when more than two loci were heterozygous, we detected haplotypes from sequencing data with at most one heterozygous locus. In total 844 individuals and 696 individuals were used to detect haplotypes of sdhB and sdhD. We detected 11 haplotypes (with 8 SNPs) and 24 haplotypes (with 11 SNPs) along 216 bp of the sdhB and 155 bp of the sdhD genes, respectively. Please see the fifth paragraph of subsection 2.4. We used ρ = 4 × Ne × d (genetic distance) (Li and Stephens, 2003) to calculate the number of effective individuals for one recombination event.

(4) Single Mutations and Their Effect (line 312-):

- It's not entirely clear how the breeding scheme resulted in near-isogenic lines. Could the authors provide a clearer explanation of the process and its biological implications?

To investigate the effect of single mutations or their combination on resistance levels, we isolated the females and males with the same homozygous/ hemizygous genotypes for creating homozygous lines. Females from these lines were not near-isogenic, but homozygous for the critical mutations. We revised the description in the methods section to clearly define these lines.

- If they are indeed isogenic, it's interesting that individual resistance mutations have effects on resistance that vary considerably among lines. Could the authors run a multivariate analysis including all potential resistance SNPs to account for interactions between them? Given the variable effects of the D116G substitution (ranging from 4-25%), could polygenic or epistatic factors be influencing the evolution of resistance?

We couldn’t conduct multivariate analysis because most lines have only one resistant SNP. The four lines homozygous for 116G were from the same population. The variable mortality may reflect other unknown mechanisms but these are beyond the scope of this study.

- Why are there some populations that segregate for resistance mutations but have no survival to pesticides (i.e., the green points in Figure 5)? Some discussion of this heterogeneity seems required in the absence of validation of the effects of these particular mutations. Could it be dominance playing a role, or do the authors have some other explanation?

We didn’t investigate the degree of dominance of each mutation. The mutation I260V shows incompletely dominant inheritance (Sun, et al. 2022). To investigate survival rate of different populations, the two-spotted spider mite T. urticae was exposed to 1000 mg/L of cyetpyrafen, higher than the recommended field dose of 100 mg/L. Such a high concentration may lead to death of an individual heterozygous for certain mutations, such as I260V.

- The authors mention that all resistance mutations co-localized to the Q-site. Is this where the pesticide binds? This seems like an important point to follow their argument for these being resistance-related.

Yes. We revised Fig. 3c to show the Q-site.

(5) Statistical Considerations for Allele Frequency Changes (Figure 3):

- It might be helpful to use a logistic regression model to assess the rate of allele frequency changes and determine the strength of selection acting on these alleles (e.g., Kreiner et al. 2022; Patel et al. 2024). This approach could refine the interpretation of selection dynamics over time.

Thank you for this suggestion. A logistic regression model was used to track allele frequencies trajectories. The selection coefficient of each allele and their joint effects were estimated.

Reviewer #2 (Public review):

Summary:

This paper investigates the evolution of pesticide resistance in the two-spotted spider mite following the introduction of an SDHI acaricide, cyatpyrafen, in China. The authors make use of cyatpyrafen-naive populations collected before that pesticide was first used, as well as more recent populations (both sensitive and resistant) to conduct comparative population genomics. They report 15 different mutations in the insecticide target site from resistant populations, many reported here for the first time, and look at the mutation and selection processes underlying the evolution of resistance, through GWAS, haplotype mapping, and testing for loss of diversity indicating selective sweeps. None of the target site mutations found in resistant populations was found in pre-exposure populations, suggesting that the mutations may have arisen de novo rather than being present as standing variation, unless initially present at very low frequencies; a de novo origin is also supported by evidence of selective sweeps in some resistant populations. Furthermore, there is no significant evidence of migration of resistant genotypes between the sampled field populations, indicating multiple origins of common mutations. Overall, this indicates a very high mutation rate and a wide range of mutational pathways to resistance for this target site in this pest species. The series of population genomic analyses carried out here, in addition to the evolutionary processes that appear to underlie resistance development in this case, could have implications for the study of resistance evolution more widely.

Strengths:

This paper combines phenotypic characterisation with extensive comparative population genomics, made possible by the availability of multiple population samples (each with hundreds of individuals) collected before as well as after the introduction of the pesticide cyatpyrafen, as well as lab-evolved lines. This results in findings of mutation and selection processes that can be related back to the pesticide resistance trait of concern. Large numbers of mites were tested phenotypically to show the levels of resistance present, and the authors also made near-isogenic lines to confirm the phenotypic effects of key mutations. The population genomic analyses consider a range of alternative hypotheses, including mutations arising by de novo mutation or selection from standing genetic variation, and mutations in different populations arising independently or arriving by migration. The claim that mutations most likley arose by multiple repeated de novo mutations is therefore supported by multiple lines of evidence: the direct evidence of none of the mutations being found in over 2000 individuals from naive populations, and the indirect evidence from population genomics showing evidence of selective sweeps but not of significant migration between the sampled populations.

Weaknesses:

As acknowledged within the discussion, whilst evidence supports a de novo origin of the resistance-associated mutations, this cannot be proven definitively as mutations may have been present at a very low frequency and therefore not found within the tested pesticide-naive population samples.

We agree that we could not definitively exclude the presence of a very low incidence of favoured mutations before the introduction of this novel acaricide.

Near-isofemale lines were made to confirm the resistance levels associated with five of the 15 mutations, but otherwise, the genotype-phenotype associations are correlative, as confirmation by functional genetics was beyond the scope of this study.

We hope that future functional studies will validate the effects of these mutations on resistance in both the two-spotted spider mite T. urticae and other spider mite species. This could be done by creating near-isogenic female lines or using CRISPR-Cas9 technology, as gene knockouts have recently been established for T. urticae.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Could the authors elaborate on the environmental context (e.g., climate, geography) of the sampled populations to give more nuance to the analysis of genetic differentiation and resistance evolution?

We have explored the influence of geographic isolation on the frequency of resistance alleles by Mantel tests (isolation by distance). We didn’t investigate the influence of climate, because most of the samples were from greenhouses, where the climate to which the pest is exposed is unclear.

(2) Line 161: is this supposed to be one R and one S?

Yes, we added this information (LabR and LabS).

(3) Line 207: variation is not saturated at the first two sites because the different combinations are not seen. This is a bit misleading.

What we wanted to indicate was that the two codon positions are saturated, rather than their combinations. We revised this sentence by adding “of each codon position”.

(4) Line 376: continuous selection did not "result in a new mutation arising". Rather, the mutation arose and was subsequently selected on.

We revised the expression of this de novo mutation and selection process.

(5) Line 402: can the authors explore what Ne would be necessary to drive the number of mutational origins they observe, as in (Karasov et al. 2010)?

It is challenged to estimate Ne, especially when mutation rate data from the two-spotted spider mite T. urticae is unavailable. We observed 2.7 resistant mutations per population in samples collected in 2024, seven years after the release of cyetpyrafen. The estimated mutation rate (Θ) is  0.0193, given 20 generations per year for T. urticae. An effective population size (Ne) of 2.29*10⁶ would be necessary to reach the number of de novo mutations observed in this study, given Θ  =  3Neμ (haplodiploid sex determination of T. urticae) and a mutation rate of μ  =  2.8*10^-9 per base pair per generation as estimated for Drosophila melanogaster (Keightley et al., 2014). The high reproductive capacity of T. urticae (> 100 eggs per female) and short generation time makes it easier to reach such a population size in the field as we now note.

(6) Line 482: how did the authors precisely kill 60% of samples with their selection? What was the applied rate? In general, listing the rates of insecticide used in dose response would be useful to decipher if LD50s are projected outside of the doses used (seems like they are). In this case, authors should limit their estimates to those > the highest rate used in the dose response.

It is difficult to control mortality precisely. We applied cyetpyrafen every two generations but did not determine the LC₅₀ every two generations. When mortality was lower than 60%, another round of spraying was applied by increasing the dosage of the pesticide. The LC₅₀ values were tested at F₁, F₃₂, F₅₄, F₆₀, F₆₂, and F₆₆ generations to establish the trajectories around resistance.

(7) The light pink genomic region in Figure 2 was distracting. Why is it included if there is no discussion of genomic regions outside the sdh genes? Generally, there was a lot going on in this figure, and some guiding categories (i.e., lab selected vs wild population) on the figure itself could help orient the reader.

We included chromosome 2 colored in light pink/ red to show the selection signal across a wider genomic region. In the figure legend, we added a description of the lab selected, field resistant and field susceptible populations. Very little common selection signal was detected among resistant populations on chromosome 2, indicating this region was less likely to be involved in resistance evolution of T. urticae to cyetpyrafen. We also described the result briefly in the figure legend.

Reviewer #2 (Recommendations for the authors):

(1) The most significant aspect of this study is the use of multiple pest population samples taken before as well as after the introduction of a class of pesticides, allowing a thorough comparative population genomics study in a species where a range of resistance mutations have appeared within a few years. I would prefer to see a title conveying this significance, rather than the current study, which focuses on the total number of mutations and claimed notoriety of the (at that point unnamed) study species. Similarly, I would prefer an abstract that relies less on superlative claims and includes more details: the scientific name of the study species; the number of years in which resistance evolved; the number of historical specimens; how the resistance levels for single mutations were shown.

(1) The title was changed by adding “the two-spotted spider mite Tetranychus urticae” and removing the “unprecedented number” to emphasize that “recurrent mutations drive rapid evolution”, i.e., “Recurrent Mutations Drive the Rapid Evolution of Pesticide Resistance in the Two-spotted Spider Mite Tetranychus urticae.”

(2) The scientific name of the study species was added.

(3) The number of years in which resistance evolved was added.

(4) The number of historical specimens was added (2666).

(5) Because we used homozygous lines but not iso-genic lines or gene-edited lines, our bioassay data could not provide direct evidence on the level of resistance conferred by each mutation. We revised our description of the results and removed this content from the abstract.

Line 29: if you want to claim the number is unprecedented, please specify the context: unprecedented for a pesticide target in an arthropod pest? (more resistance mutations may have been found in bacteria/fungi...).

We revised the sentence by adding “in an arthropod pest”.

Line 30: rather than a claim of notoriety, it may be better to specify what damage this pest causes.

Revised by describing it as an arthropod pest.

Line 34: please clarify, was this all in different haplotypes, or were some mutations found in combination?

Done: We identified 15 target mutations, including six mutations on five amino acid residues of subunit sdhB, and nine mutations on three amino acid residues of subunit sdhD, with as many as five substitutions on one residue.

(2) The introduction begins by framing the context as resistance evolution in invertebrate pests. However, the evolutionary processes examined in the study are applicable to resistance in other systems, and potentially to other cases of rapid contemporary evolution. The authors could show wider significance for their work beyond the subfield of invertebrate pests by including more of this wider context in their introduction and discussion: even if this means they can no longer claim novelty based on the number of mutations alone, the study is a strong example of the use of population genomics combined with functional and phenotypic characterisation to investigate the evolutionary processes underlying the emergence of resistance, so could have wider importance than within its current framing.

The background was revised as mentioned above to take this into account.

For example, in lines 48-50, please clarify what is meant by pesticides here (insects/arthropods? weeds and pathogens too?) In lines 69-73, the opposite is sometimes seen in fungal pathogens, with large numbers of mutations generated in lab-evolved strains.

We extended pesticides to those targeting arthropods, weeds and pathogens. We still emphasize the situation mainly with respect to arthropod pests.

(3) Lines 91-93: how many modes of action? How recently were SDHI acaricides introduced?

Added: at least 11 groups of acaricides based on their modes of action. SDHI was launched in 2007.

(4) Line 98-102: Use in China is a useful background for the study populations, but the global context should be included too.

Yes, four SDHI acaricides developed around the globe were introduced.

(5) Line 113: They show diverse mutations, but all within the mechanism of target-site point mutations.

We agree to your suggestion. This sentence has been removed as it repeats information stated above it.

(6) Line 115-116: Yes, agreed; I think this is the main strength of the current study and should be emphasised sooner.

Thanks.

(7) Line 158: Selective sweep signals were clear in half of the resistant populations but not in the others. The suggestion that the others had undergine soft sweeps, with multiple mutations increasing in frequency simultaneously but no one reaching fixation, seems reasonable; but the authors could compare the populations that did show a sweep with those that did not (for example, was there greater diversity or evenness of genotypes in those that did not?).

Five resistant populations with selection signals identified by PBE analysis (Figure 2b) showed corresponding decreases in π and Tajima’s D near the two SDH genes but not across the genome (Figure S1).

(8) Line 313: please clarify "in combination with other mutations" within a mixed population or combined in one individual/haplotype? Also, the phrase "characterised the function" may be a little misleading, as this is a correlative analysis, not functional confirmation.

None of the combinations of different resistant mutations was observed in a single haplotype. Here, we examine resistance levels associated with a single mutation or two mutations on sdhB and sdhD in one individual, i.e. sdhB_I260V and sdhD_R119C. We revised the sentences to avoid any implication of functional confirmation.

(9) Line 358: again, please clarify the context: among arthropod pests?

Done.

(10) Line 360-363: please give some background on when and where these related compounds were introduced.

Added.

(11) Line 410: yes fitness costs may be a factor, but you could also give an example of a cost expressed in the absence of any pesticides, as well as the given example of negative cross-resistance.

We added the example of the H258Y mutation which causes both fitness costs and negative cross-resistance.

(12) Lines 419-438: this is one aspect where the situation for insecticides is in contrast with some other resistance areas.

Yes, we restricted these statements to arthropod pests.

(13) Line 466: some more detail could be given here: for example, SNP-specific monitoring would be less effective, but amplicon sequencing would be more suitable.

Yes, revised.

(14) Lines 472-475: Please list the numbers of field/lab, pre/post exposure, and sensitive/resistant populations within the main text.

Done. The number of sensitive/resistant populations was reported in the result section.

(15) Line 483: randomly selected individuals?

Yes, added randomly selected individuals.

(16) Line 556: Sanger sequencing to characterise populations? Or a number of individuals from each population?

Revised.

(17) References: there are some duplicate entries, please check this.

Checked.

(18) Figure 1e: consider a log(10) scale to better show large fold changes and avoid multiple axis breaks.

Thanks for your suggestions. However we didn’t scale the LC₅₀ value, because we wanted to show the specific impact of 1,000 mg/L. The breaks in the Y axis around 30 mg/L -1,000 mg/L reveal that the LC50s of the resistant populations were all greater than 1000 mg/L, while those of the susceptible populations were all below 30 mg/L. This justified the use 1000 mg/L as a discriminating dose to investigate resistance status and level in subsequent work.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Azlan et al. identified a novel maternal factor called Sakura that is required for proper oogenesis in Drosophila. They showed that Sakura is specifically expressed in the female germline cells. Consistent with its expression pattern, Sakura functioned autonomously in germline cells to ensure proper oogenesis. In sakura KO flies, germline cells were lost during early oogenesis and often became tumorous before degenerating by apoptosis. In these tumorous germ cells, piRNA production was defective and many transposons were derepressed. Interestingly, Smad signaling, a critical signaling pathway for the GSC maintenance, was abolished in sakura KO germline stem cells, resulting in ectopic expression of Bam in whole germline cells in the tumorous germline. A recent study reported that Bam acts together with the deubiquitinase Otu to stabilize Cyc A. In the absence of sakura, Cyc A was upregulated in tumorous germline cells in the germarium. Furthermore, the authors showed that Sakura co-immunoprecipitated Otu in ovarian extracts. A series of in vitro assays suggested that the Otu (1-339 aa) and Sakura (1-49 aa) are sufficient for their direct interaction. Finally, the authors demonstrated that the loss of otu phenocopies the loss of sakura, supporting their idea that Sakura plays a role in germ cell maintenance and differentiation through interaction with Otu during oogenesis.

Strengths:

To my knowledge, this is the first characterization of the role of CG14545 genes. Each experiment seems to be well-designed and adequately controlled

Weaknesses:

However, the conclusions from each experiment are somewhat separate, and the functional relationships between Sakura's functions are not well established. In other words, although the loss of Sakura in the germline causes pleiotropic effects, the cause-and-effect relationships between the individual defects remain unclear.

Comments on latest version:

The authors have attempted to address my initial concerns with additional experiments and refutations. Unfortunately, my concerns, especially my specific comments 1-3, remain unaddressed. The present manuscript is descriptive and fails to describe the molecular mechanism by which Sakura exerts its function in the germline. Nevertheless, this reviewer acknowledges that the observed defects in sakura mutant ovaries and the possible physiological significance of the Sakura-Out interaction are worth sharing with the research community, as they may lay the groundwork for future research in functional analysis.

We thank the reviewer for valuable comments. We would like to investigate the molecular mechanism by which Sakura exerts its function in the germline in near future studies. 

Reviewer #2 (Public review):

In this study, the authors identified CG14545 (named it sakura), as a key gene essential for Drosophila oogenesis. Genetic analyses revealed that Sakura is vital for both oogenesis progression and ultimate female fertility, playing a central role in the renewal and differentiation of germ stem cells (GSC).

The absence of Sakura disrupts the Dpp/BMP signaling pathway, resulting in abnormal bam gene expression, which impairs GSC differentiation and leads to GSC loss. Additionally, Sakura is critical for maintaining normal levels of piRNAs. Also, the authors convincingly demonstrate that Sakura physically interacts with Otu, identifying the specific domains necessary for this interaction, suggesting a cooperative role in germline regulation. Importantly, the loss of otu produces similar defects to those observed in sakura mutants, highlighting their functional collaboration.

The authors provide compelling evidence that Sakura is a critical regulator of germ cell fate, maintenance, and differentiation in Drosophila. This regulatory role is mediated through modulation of pMad and Bam expression. However, the phenotypes observed in the germarium appear to stem from reduced pMad levels, which subsequently trigger premature and ectopic expression of Bam. This aberrant Bam expression could lead to increased CycA levels and altered transcriptional regulation, impacting piRNA expression. In this revised manuscript, the authors further investigated whether Sakura affects the function of Orb, a binding partner they identified, in deubiquitinase activity when Orb interacts with Bam.

We appreciate the authors' efforts to address all our comments. While these revisions have greatly improved the clarity of certain sections, some of the concerns remain unclear, while details mentioned in the responses about these studies should be incorporated in the manuscript. Specifically, the manuscript still lacks the demonstration that Sakura co-localizes with Orb/Bam despite having the means for staining and visualization. This would bring insight into the selective binding of Orb with Bam vs. Sakura perhaps at different stages of oogenesis. Such analyses would allow for more specific conclusions, further alluding to the underlying mechanism, rather than the general observations currently presented.

This elaborate study will be embraced by both germline-focused scientists and the developmental biology community.

We thank the reviewer for valuable comments. We believe that the author meant Otu, not Orb, for the binding partner of Sakura that we identified. We would like to investigate the colocalization of Sakura with other proteins including Otu and the molecular mechanism by which Sakura exerts its function in the germline in near future studies. 

Reviewer #3 (Public review):

In this very thorough study, the authors characterize the function of a novel Drosophila gene, which they name Sakura. They start with the observation that sakura expression is predicted to be highly enriched in the ovary and they generate an anti-sakura antibody, a line with a GFP-tagged sakura transgene, and a sakura null allele to investigate sakura localization and function directly. They confirm the prediction that it is primarily expressed in the ovary and, specifically, that it is expressed in germ cells, and find that about 2/3 of the mutants lack germ cells completely and the remaining have tumorous ovaries. Further investigation reveals that Sakura is required for piRNA-mediated repression of transposons in germ cells. They also find evidence that sakura is important for germ cell specification during development and germline stem cell maintenance during adulthood. However, despite the role of sakura in maintaining germline stem cells, they find that sakura mutant germ cells also fail to differentiate properly such that mutant germline stem cell clones have an increased number of "GSC-like" cells. They attribute this phenotype to a failure in the repression of Bam by dpp signaling. Lastly, they demonstrate that sakura physically interacts with otu and that sakura and otu mutants have similar germ cell phenotypes. Overall, this study helps to advance the field by providing a characterization of a novel gene that is required for oogenesis. The data are generally high-quality and the new lines and reagents they generated will be useful for the field.

Comments on latest version:

With these revisions, the authors have addressed my main concerns.

We thank the reviewer for valuable comments.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

The manuscript is much improved based on the changes made upon recommendations from the reviewers.

Though most of our comments have been addressed, we have a few more we wish to recommend. For previous points we made, we replied with further clarification for the authors.

Figure 1

(1) B should be the supplemental figure.

We moved the former Fig 1B to Supplemental Figure 1.

• Previous Fig1B (sakura mRNA expression level) is now Fig S2, not S1. Please make this data as Fig S1.

We moved Fig S1 to main Fig7A and renumbered Fig S2-S16 to Fig S1-S15.

(2) C - How were the different egg chamber stages selected in the WB? Naming them 'oocytes' is deceiving. Recommend labeling them as 'egg chambers', since an oocyte is claimed to be just the one-cell of that cyst.

We changed the labeling to egg chambers.

• The labels on lanes for Stages 12-13 and Stage 14, still only say "chambers", not "egg chambers". Also there is no Stage 1-3 egg chamber. More accurately, the label should be "Germarium - Stage 11 egg chambers".

We updated the lables on lanes as suggested by the reviewer.

(3) Is the antibody not detecting Sakura in IF? There is no mention of this anywhere in the manuscript.

While our Sakura antibody detects Sakura in IF, it seems to detect some other proteins as well. Since we have Sakura-EGFP fly strain (which fully rescues sakuranull phenotypes) to examine Sakura expression and localization without such non-specific signal issues, we relied on Sakura-EGFP rather than anti-Sakura antibodies for IF.

• Please put this info into the Methods section.

We added this info into the Methods section.

(4) Expand on the reliance of the sakura-EGFP fly line. Does this overexpression cause any phenotypes?

sakura-EGFP does not cause any phenotypes in the background of sakura[+/+] and sakura[+/-].

• Please add this detail into the manuscript.

We added this info into the Methods section.

Figure 5

(1) D - It might make more sense if this graph showed % instead of the numbers.

We did not understand the reviewer's point. We think using numbers, not %, makes more sense.

• Having a different 'n' number for each experiment does not allow one to compare anything except numbers of the egg chambers. This must be normalized.

We still don’t agree with the reviewer. In Fig 5D, we are showing the numbers of stage 14 oocytes per fly (= per a pair of ovaries). ‘n’ is the number of flies (= number of a pair of ovaries) examined. We now clarified this in the figure legend. Different ‘n’ number does not prevent us from comparing the numbers of stage 14 oocytes per fly. Therefore, we would like to show as it is now.

(2) Line 213 - explain why RNAi 2 was chosen when RNAi 1 looks stronger.

Fly stock of RNAi line 2 is much healthier than RNAi line 1 (without being driven Gal4) for some reasons. We had a concern that the RNAi line 1 might contain an unwanted genetic background. We chose to use the RNAi 2 line to avoid such an issue.

• Please add this information to the manuscript.

We added this info into the Methods section.

Figure 7/8 - can go to Supplemental.

We moved Fig 8 to supplemental. However, we think Fig 7 data is important and therefore we would like to present them as a main figure.

• Current Fig S1 should go to Fig 7, to better understand the relationship between pMad and Bam expression.

We moved Fig S1 to main Fig7A and renumbered Fig S2-S16 to Fig S1-S15.

Figure 9C - Why the switch to S2 cells? Not able to use the Otu antibody in the IP of ovaries?

We can use the Otu antibody in the IP of ovaries. However, in anti-Sakura Western after anti Otu IP, antibody light chain bands of the Otu antibodies overlap with the Sakura band. Therefore, we switched to S2 cells to avoid this issue by using an epitope tag.

• Please add this info to the Methods section.

We added this info into the Methods section.

Figure 10- Some images would be nice here to show that the truncations no longer colocalize.

We did not understand the reviewer's points. In our study, even for the full-length proteins. We have not shown any colocalization of Sakura and Otu in S2 cells or in ovaries, except that they both are enriched in developing oocytes in egg chambers.

• Based on your binding studies, we would expect them to colocalize in the egg chamber, and since there are antibodies and a GFP-line available, it would be important to demonstrate that via visualization.

As we wrote in the response and now in the manuscript, our antibodies are not best for immunostaining. We will try to optimize the experimental conditions in the future studies.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment 

The authors utilize a valuable computational approach to exploring the mechanisms of memorydependent klinotaxis, with a hypothesis that is both plausible and testable. Although they provide a solid hypothesis of circuit function based on an established model, the model's lack of integration of newer experimental findings, its reliance on predefined synaptic states, and oversimplified sensory dynamics, make the investigation incomplete for both memory and internal-state modulation of taxis.  

We would like to express our gratitude to the editor for the assessment of our work. However, we respectfully disagree with the assessment that our investigation is incomplete, if the negative assessment is primarily due to the impact of AIY interneuron ablation on the chemotaxis index (CI) which was reported in Reference [1]. It is crucial to acknowledge that the CI determined through experimental means incorporates contributions from both klinokinesis and klinotaxis [1]. It is plausible that the impact of AIY ablation was not adequately reflected in the CI value. Consequently, the experimental observation does not necessarily diminish the role of AIY in klinotaxis. Anatomical evidence provided by the database (http://ims.dse.ibaraki.ac.jp/ccep-tool/) substantiates that ASE sensory neurons and AIZ interneurons, which have been demonstrated to play a crucial role in klinotaxis [Matsumoto et al., PNAS 121 (5) e2310735121], have the much higher number of synaptic connections with AIY interneurons. These findings provide substantial evidence supporting the validity of the presented minimal neural network responsible for salt klinotaxis.

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

This research focuses on C. elegans klinotaxis, a chemotactic behavior characterized by gradual turning, aiming to uncover the neural circuit mechanism responsible for the context-dependent reversal of salt concentration preference. The phenomenon observed is that the preferred salt concentration depends on the difference between the pre-assay cultivation conditions and the current environmental salt levels. 

We would like to express our gratitude for the time and consideration you have dedicated to reviewing our manuscript.

The authors propose that a synaptic-reversal plasticity mechanism at the primary sensory neuron, ASER, is critical for this memory- and context-dependent switching of preference. They build on prior findings regarding synaptic reversal between ASER and AIB, as well as the receptor composition of AIY neurons, to hypothesize that similar "plasticity" between ASER and AIY underpins salt preference behavior in klinotaxis. This plasticity differs conceptually from the classical one as it does not rely on any structural changes but rather synaptic transmission is modulated by the basal level of glutamate, and can switch from inhibitory to excitatory. 

To test this hypothesis, the study employs a previously established neuroanatomically grounded model [4] and demonstrates that reversing the ASER-AIY synapse sign in the model agent reproduces the observed reversal in salt preference. The model is parameterized using a computational search technique (evolutionary algorithm) to optimize unknown electrophysiological parameters for chemotaxis performance. Experimental validity is ensured by incorporating constraints derived from published findings, confirming the plausibility of the proposed mechanism. 

Finally. the circuit mechanism allowing C. elegans to switch behaviour to an exploration run when starved is also investigated. This extension highlights how internal states, such as hunger, can dynamically reshape sensory-motor programs to drive context-appropriate behaviors.  

We would like to thank the reviewer for the appropriate summary of our work. 

Strengths and weaknesses: 

The authors' approach of integrating prior knowledge of receptor composition and synaptic reversal with the repurposing of a published neuroanatomical model [4] is a significant strength. This methodology not only ensures biological plausibility but also leverages a solid, reproducible modeling foundation to explore and test novel hypotheses effectively.

The evidence produced that the original model has been successfully reproduced is convincing.

The writing of the manuscript needs revision as it makes comprehension difficult.  

We would like to thank the reviewer for recognizing the usefulness of our approach. In the revised version, we improved the explanation according to your suggestions.  

One major weakness is that the model does not incorporate key findings that have emerged since the original model's publication in 2013, limiting the support for the proposed mechanism. In particular, ablation studies indicate that AIY is not critical for chemotaxis, and other interneurons may play partially overlapping roles in positive versus negative chemotaxis. These findings challenge the centrality of AIY and suggest the model oversimplifies the circuit involved in klinotaxis.

We would like to express our gratitude for the constructive feedback we have received. We concur with some of your assertions. In fact, our model is the minimal network for salt klinotaxis, which includes solely the interneurons that are connected to each other via the highest number of synaptic connections. It is important to note that our model does not consider redundant interneurons that exhibit overlapping roles. Consequently, the model is not applicable to the study of the impact of interneuron ablation. In the reference [1], the influence of interneuron ablations on the chemotaxis index (CI) has been investigated. The experimentally determined CI value incorporates the contributions from both klinokinesis and klinotaxis. Consequently, it is plausible that the impact of AIY ablation was not significantly reflected in the CI value. The experimental observation does not necessarily diminish the role of AIY in klinotaxis. 

Reference [1] also shows that ASER neurons exhibit complex, memory- and context-dependent responses, which are not accounted for in the model and may have a significant impact on chemotactic model behaviour. 

As the reviewer has noted, our model does not incorporate the context-dependent response of the ASER. Instead, the impact of the salt concentration-dependent glutamate release from the ASER [S. Hiroki et al. Nat Commun 13, 2928 (2022)] as the result of the ASER responses was in detail examined in the present study.

The hypothesis of synaptic reversal between ASER and AIY is not explicitly modeled in terms of receptor-specific dynamics or glutamate basal levels. Instead, the ASER-to-AIY connection is predefined as inhibitory or excitatory in separate models. This approach limits the model's ability to test the full range of mechanisms hypothesized to drive behavioral switching.  

We would like to express our gratitude to the reviewer for their constructive feedback. As you correctly noted, the hypothesized synaptic reversal between ASER and AIY is not explicitly modeled in terms of the sensitivity of the receptors in the AIY and the glutamate basal levels by the ASER. On the other hand, in the present study, under considering a substantial difference in the sensitivity of the two glutamate receptors on the AIY, we sought to endeavored to elucidate the impact of salt-concentration-dependent glutamate basal levels on klinotaxis. To this end, we conducted a comprehensive examination of the full range gradual change in the ASER-to-AIY connection from inhibitory to excitatory, as illustrated in Figures S4 and S5.

While the main results - such as response dependence on step inputs at different phases of the oscillator - are consistent with those observed in chemotaxis models with explicit neural dynamics (e.g., Reference [2]), the lack of richer neural dynamics could overlook critical effects. For example, the authors highlight the influence of gap junctions on turning sensitivity but do not sufficiently analyze the underlying mechanisms driving these effects. The role of gap junctions in the model may be oversimplified because, as in the original model [4], the oscillator dynamics are not intrinsically generated by an oscillator circuit but are instead externally imposed via $z_¥text{osc}$. This simplification should be carefully considered when interpreting the contributions of specific connections to network dynamics. Lastly, the complex and contextdependent responses of ASER [1] might interact with circuit dynamics in ways that are not captured by the current simplified implementation. These simplifications could limit the model's ability to account for the interplay between sensory encoding and motor responses in C. elegans chemotaxis. 

We might not understand the substance of your assertions. However, we understand that the oscillator dynamics were not intrinsically generated by the oscillator neural circuit that is explicitly incorporated into our modeling. On the other hand, the present study focuses on how the sensory input and resulting interneuron dynamics regulate the oscillatory behavior of SMB motor neurons to generate klinotaxis. The neuron dynamics via gap junctions results from the equilibration of the membrane potential yi of two neurons connected by gap junctions rather than the zi. We added this explanation in the revised manuscript as follows.

“The hyperpolarization signals in the AIZL are transmitted to the AIZR via the gap junction (Figs. S1d and S1f and Fig. 3d). This is because the neuron dynamics via gap junctions results from the equilibration of the membrane potential y_i of two neurons connected by gap junctions rather than the z_i.”

In the limitation, we added the following sentence:

“In the present study, the oscillator components of the SMB are not intrinsically generated by an oscillator circuit but are instead externally imposed via 𝑧_i^OSC. Furthermore, the complex and context-dependent responses of ASER {Luo:2014et} were not taken into consideration. It should be acknowledged as a limitation of this study that these omitted factors may interact with circuit dynamics in ways that are not captured by the current simplified implementation.”

Appraisal: 

The authors show that their model can reproduce memory-dependent reversal of preference in klinotaxis, demonstrating that the ASER-to-AIY synapse plays a key role in switching chemotactic preferences. By switching the ASER-AIY connection from excitatory to inhibitory they indeed show that salt preference reverses. They also show that the curving/turn rate underlying the preference change is gradual and depends on the weight between ASER-AIY. They further support their claim by showing that curving rates also depend on cultivated (set-point).  

We would like to thank the reviewer for assessing our work.

Thus within the constraints of the hypothesis and the framework, the model operates as expected and aligns with some experimental findings. However, significant omissions of key experimental evidence raise questions on whether the proposed neural mechanisms are sufficient for reversal in salt-preference chemotaxis.  

We agree with your opinion. The present hypothesis should be verified by experiments.

Previous work [1] has shown that individually ablating the AIZ or AIY interneurons has essentially no effect on the Chemotactic Index (CI) toward the set point ([1] Figure 6). Furthermore, in [1] the authors report that different postsynaptic neurons are required for movement above or below the set point. The manuscript should address how this evidence fits with their model by attempting similar ablations. It is possible that the CI is rescued by klinokinesis but this needs to be tested on an extension of this model to provide a more compelling argument.  

We would like to express our gratitude for the constructive feedback we have received. In the reference [1], the influence of interneuron ablations on the chemotaxis index (CI) has been investigated. It is important to acknowledge that the experimentally determined CI value encompasses the contributions of both klinokinesis and klinotaxis. It is plausible that the impact of AIY ablation was not reflected in the CI value. Consequently, these experimental observations do not necessarily diminish the role of AIY in klinotaxis. The neural circuit model employed in the present study constitutes a minimal network for salt klinotaxis, encompassing solely interneurons that are connected to each other via the highest number of synaptic connections. Anatomical evidence provided by the database (http://ims.dse.ibaraki.ac.jp/cceptool/) substantiates that ASE sensory neurons and AIZ interneurons, which have been demonstrated to play a crucial role in klinotaxis [Matsumoto et al., PNAS 121 (5) e2310735121], have the much higher number of synaptic connections with AIY interneurons. Our model does not take into account redundant interneurons with overlapping roles, thus rendering it not applicable to the study of the effects of interneuron ablation.

The investigation of dispersal behaviour in starved individuals is rather limited to testing by imposing inhibition of the SMB neurons. Although a circuit is proposed for how hunger states modulate taxis in the absence of food, this circuit hypothesis is not explicitly modelled to test the theory or provide novel insights.  

As the reviewer noted, the experimentally identified neural circuit that inhibits the SMB motor neurons in starved individuals is not incorporated in our model. Instead of incorporating this circuit explicitly, we examined whether our minimal network model could reproduce dispersal behavior under starvation conditions solely due to the experimentally demonstrated inhibitory effect of SMB motor neurons.

Impact: 

This research underscores the value of an embodied approach to understanding chemotaxis, addressing an important memory mechanism that enables adaptive behavior in the sensorimotor circuits supporting C. elegans chemotaxis. The principle of operation - the dependence of motor responses to sensory inputs on the phase of oscillation - appears to be a convergent solution to taxis. Similar mechanisms have been proposed in Drosophila larvae chemotaxis [2], zebrafish phototaxis [3], and other systems. Consequently, the proposed mechanism has broader implications for understanding how adaptive behaviors are embedded within sensorimotor systems and how experience shapes these circuits across species.

We would like to express our gratitude for useful suggestion. We added this argument in Discussion of the revised manuscript as follows.    

“The principle of operation, in which the dependence of motor responses to sensory inputs on the phase of motor oscillation, appears to be a convergent solution for taxis and navigation across species. In fact, analogous mechanisms have been postulated in the context of chemotaxis in Drosophila larvae chemotaxis {Wystrach:2016bt} and phototaxis in zebrafish {Wolf:2017ei}. Consequently, the synaptic reversal mechanism highlighted in this study offers the framework for understanding how the behaviors that are adaptive to the environment are embedded within sensorimotor systems and how experience shapes these neural circuits across species.”

Although the reported reversal of synaptic connection from excitatory to inhibitory is an exciting phenomenon of broad interest, it is not entirely new, as the authors acknowledge similar reversals have been reported in ASER-to-AIB signaling for klinokinesis ( Hiroki et al., 2022). The proposed reversal of the ASER-to-AIY synaptic connection from inhibitory to excitatory is a novel contribution in the specific context of klinotaxis. While the ASER's role in gradient sensing and memory encoding has been previously identified, the current paper mechanistically models these processes, introducing a hypothesis for synaptic plasticity as the basis for bidirectional salt preference in klinotaxis.  

The research also highlights how internal states, such as hunger, can dynamically reshape sensory-motor programs to drive context-appropriate behaviors.  

The methodology of parameter search on a neural model of a connectome used here yielded the valuable insight that connectome information alone does not provide enough constraints to reproduce the neural circuits for behaviour. It demonstrates that additional neurophysiological constraints are required.  

We would like to acknowledge the appropriate recognition of our work.

Additional Context 

Oscillators with stimulus-driven perturbations appear to be a convergent solution for taxis and navigation across species. Similar mechanisms have been studied in zebrafish phototaxis [3], Drosophila larvae chemotaxis [2], and have even been proposed to underlie search runs in ants. The modulation of taxis by context and memory is a ubiquitous requirement, with parallels across species. For example, Drosophila larvae modulate taxis based on current food availability and predicted rewards associated with odors, though the underlying mechanism remains elusive. The synaptic reversal mechanism highlighted in this study offers a compelling framework for understanding how taxis circuits integrate context-related memory retrieval more broadly.  

We would like to express our gratitude for the insightful commentary. In the revised manuscript, we incorporated the argument that the similar oscillator mechanism with stimulus-driven perturbations has been observed for zebrafish phototaxis [3] and Drosophila larvae chemotaxis [2] into Discussion.

As a side note, an interesting difference emerges when comparing C. elegans and Drosophila larvae chemotaxis. In Drosophila larvae, oscillatory mechanisms are hypothesized to underlie all chemotactic reorientations, ranging from large turns to smaller directional biases (weathervaning). By contrast, in C. elegans, weathervaning and pirouettes are treated as distinct strategies, often attributed to separate neural mechanisms. This raises the possibility that their motor execution could share a common oscillator-based framework. Re-examining their overlap might reveal deeper insights into the neural principles underlying these maneuvers. 

We would like to acknowledge your thoughtfully articulated comment. As the reviewer pointed out, the anatomical database (http://ims.dse.ibaraki.ac.jp/ccep-tool/) shows that that the neural circuits underlying weathervaning and pirouettes in C. elegans are predominantly distinct but exhibit partial overlap. When we restrict our search to the neurons that are connected to each other with the highest number of synaptic connections, we identify the projections from the neural circuit of weathervaning to the circuit of pirouettes; however we observed no reversal projections. This finding suggests that the neural circuit of weathervaning, namely, our minimal neural network, is not likely to be affected by that of pirouettes, which consists of AIB interneurons and interneurons and motor neurons the downstream. 

(1) Luo, L., Wen, Q., Ren, J., Hendricks, M., Gershow, M., Qin, Y., Greenwood, J., Soucy, E.R., Klein, M., Smith-Parker, H.K., & Calvo, A.C. (2014). Dynamic encoding of perception, memory, and movement in a C. elegans chemotaxis circuit. Neuron, 82(5), 1115-1128. 

(2) Antoine Wystrach, Konstantinos Lagogiannis, Barbara Webb (2016) Continuous lateral oscillations as a core mechanism for taxis in Drosophila larvae eLife 5:e15504. 

(3) Wolf, S., Dubreuil, A.M., Bertoni, T. et al. Sensorimotor computation underlying phototaxis in zebrafish. Nat Commun 8, 651 (2017). 

(4) Izquierdo, E.J. and Beer, R.D., 2013. Connecting a connectome to behavior: an ensemble of neuroanatomical models of C. elegans klinotaxis. PLoS computational biology, 9(2), p.e1002890. 

Reviewer #2 (Public review): 

Summary: 

This study explores how a simple sensorimotor circuit in the nematode C. elegans enables it to navigate salt gradients based on past experiences. Using computational simulations and previously described neural connections, the study demonstrates how a single neuron, ASER, can change its signaling behavior in response to different salt conditions, with which the worm is able to "remember" prior environments and adjust its navigation toward "preferred" salinity accordingly.  

We would like to express our gratitude for the time and consideration the reviewer has dedicated to reviewing our manuscript.

Strengths: 

The key novelty and strength of this paper is the explicit demonstration of computational neurobehavioral modeling and evolutionary algorithms to elucidate the synaptic plasticity in a minimal neural circuit that is sufficient to replicate memory-based chemotaxis. In particular, with changes in ASER's glutamate release and sensitivity of downstream neurons, the ASER neuron adjusts its output to be either excitatory or inhibitory depending on ambient salt concentration, enabling the worm to navigate toward or away from salt gradients based on prior exposure to salt concentration.

We would like to thank the reviewer for appreciating our research. 

Weaknesses: 

While the model successfully replicates some behaviors observed in previous experiments, many key assumptions lack direct biological validation. As to the model output readouts, the model considers only endpoint behaviors (chemotaxis index) rather than the full dynamics of navigation, which limits its predictive power. Moreover, some results presented in the paper lack interpretation, and many descriptions in the main text are overly technical and require clearer definitions.  

We would like to thank the reviewer for the constructive feedback. As the reviewer noted, the fundamental assumptions posited in the study have yet to be substantiated by biological validation, and consequently, these assumptions must be directly assessed by biological experimentation. The model performance for salt klinotaxis has been evaluated by multiple factors, including not only a chemotaxis index but also the curving rate vs. bearing (Fig. 4a, the bearing is defined in Fig. A3) and the curving rate vs. normal gradient (Fig. 4c). These two parameters work to characterize the trajectory during salt klinotaxis. In the revised version, we meticulously revised the manuscript according to the reviewer’s suggestions. We would like to express our sincere gratitude for your insightful review of our work.

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors): 

An interesting and engaging methodology combining theoretical and computational approaches. Overall I found the manuscript up to discussion a difficult read, and I would suggest revising it. I would also recommend introducing the general operating principle of the oscillator with sensory perturbations before jumping into the implementation details of signal propagation specific to C.

elegans.  

In order to elucidate the relation between the general operating principle of the oscillator with sensory perturbations and the results shown by the two graphs from the bottom in Fig. 3d, the following statement was added on page 12.

“It is remarkable that this regulatory mechanism derived via the optimization of the CI has been observed in the context of chemotaxis in Drosophila larvae chemotaxis {Wystrach:2016bt} and phototaxis in zebrafish {Wolf:2017ei}. The principle of operation, in which the dependence of motor responses to sensory inputs on the phase of motor oscillation, therefore, may serve as a convergent solution for taxis and navigation across species.”

The abstract could benefit from a clarification of terms to benefit a broader audience:  The term "salt klinotaxis" is used without prior introduction or definition. It would be beneficial to briefly explain this term, as it may not be familiar to all readers. 

Due to the limitation of the word number in the abstract, the explanation of salt klinotaxis could not be included.

Although ASER is introduced as a right-side head sensory neuron, AIY neurons are not similarly introduced. It may also benefit to introduce here that ASER integrates memory with current salt gradients, tuning its output to produce context-appropriate behaviour.  

Due to the limitation of the word number in the abstract, we could add no more the explanations. 

"it can be anticipated that the ASER-AIY synaptic transmission will undergo a reversal due to alterations in the basal glutamate Release": Where is this expectation drawn from? Is it derived from biophysical or is it a functional expectation to explain the network's output constraints?  

As delineated before this sentence, it is derived from a comprehensive consideration of the sensitivity of excitatory/inhibitory glutamate receptors expressed on the postsynaptic AIY interneurons, in conjunction with varying the basal level of glutamate transmission from ASER.

The statement that the model "revealed the modular neural circuit function downstream of ASE" could be more explicit. What specific insights about the downstream circuit were uncovered?

Highlighting one or two key findings would strengthen the impact.  

Due to the limitation of the word number in the abstract, no more details could be added here, while the sentence was revised as “revealed that the circuit downstream of ASE functions as a module that is responsible for salt klinotaxis.” This is because the salt-concentration dependent behaviors in klinitaxis can be reproduced through the modulation of the ASRE-AIY synaptic connections alone, despite the absence of alterations in the neural circuit downstream of AIY.

I believe the authors should cite Luo et al. 2014, which also studies how chemotactic behaviours arise from neural circuit dynamics, including the dynamic encoding of salt concentration by ASER, and the crucial downstream interaction with AIY for chemotactic actions. 

We would like to express our gratitude for useful suggestion. We cited Luo et al. 2014 in the discussion on the limitation of our work. 

The introduction could also be improved for clarity. Specifically in the last paragraph authors should clarify how the observed synchrony of ASER excitation to the AIZ (Matsumoto et al., 2024), validates the resulting network.  

We would like to express our gratitude for useful suggestion. We added the following explanation in the last paragraph of the introduction.

“Specifically, the synchrony of the excitation of the ASER and AIZ {Matsumoto:2024ig} taken together with the experimentally identified inhibitory synaptic transmission between the AIY and AIZ revealed that the ASER-AIY synaptic connections should be inhibitory, which was consistent with the network obtained from the most evolved model.”

In addition, we added the following explanation after “It was then hypothesized that the ASER-AIY inhibitory synaptic connections are altered to become excitatory due to a decrease in the baseline release of glutamate from the ASER when individuals are cultured under C_cult < C_test.”

This is due to the substantial difference in the sensitivity of excitatory/inhibitory glutamate receptors expressed on the postsynaptic AIY interneurons.

I would also strongly recommend replacing the term "evolved model", with "Optimized Model" or "Best-Performing Model" to clarify this is a computational optimization process with limitations - optimization through GAs does not guarantee finding global optima.  

We revised "evolved model" as "optimized model" in the main and SI text.

The text overall would benefit from editing for clarity and expression.  

According to the revisions mentioned above, we revised “best optimized model” as “most optimized model” in the main and SI text.

The font size on the plot axis in Figures 3 c&d should be increased for readability on the printed page. Label the left/right panel to indicate unconstrained / constrained evolution.  

As you noted, the font size of the subscript on the vertical axis in Figs 3c and 3d was too small. We have revised the font size of the subscript in Figs. 3c and 3d and also in Fig. 5e. At your suggestion, “unconstrained” and “constrained” have been added as labels to the left and right panels in Fig. 3.

There is no input/transmission to AIYR to step input in either model shown in Figure 3? 

As shown in Fig. S1e and S1f, there are the transmissions to the AIYR from the ASEL and ASER. 

Supplementary Figure 1 attempts to explain the interactions. There are inconsistent symbols used for inhibition and excitation between network schema (colours) and the z response plots (arrows vs circles), combined with different meanings for red/blue making it very confusing. 

We could not address the inconsistency in the color of arrows and lines with an ending between Figs. S1c and S1d and Figs. S1a and S1b. On the other hand, Figs. S1e and S1f were revised so that the consistent symbols were used for inhibition, excitation, and electrical gap connections in Figs. S1c-S1f. The same revisions were made for Fig. S7c-S7f.

Model parameters are given to 15 decimal precision, which seems excessive. Is model performance sensitive to that order? We would expect robustness around those values. The authors should identify relevant orders and truncate parameters accordingly. 

We examined the influence of the parameter truncation on the trajectory and decided that the parameters with four decimal places were appropriate. According to this, we revised Table A4.

Figure 3 caption typo "step changes I the salt concentration".  

The typo was revised in Fig. 3 caption. 

Reviewer #2 (Recommendations for the authors): 

(1) Overall, the language of the paper is not properly organized, making the paper's logic and purpose hard to follow. In the Results Section, many observations or findings lack explicit interpretation. To address this issue, the authors should consider (1) adopting the contextcontent-conclusion scheme, (2) optimizing the logic flow by clearly identifying the context and goals prior to discussing their results and findings, (3) more explicitly interpreting their results, especially in a biological context.  

We would like to express our gratitude for helpful suggestion. According to your suggestion listed below, we revised the main and SI texts.

(2) In Figure 2, trajectories from the model with AIY-AIZ constraints show a faster convergence than those from the constraint-free model. However, in the corresponding texts in the Results section, the authors claimed no significant difference. It seems that the authors made this argument only based on CI (Chemotaxis Index). Therefore, in order to address such inconsistency, the authors need more explanation on why only relying on CI, which is an endpoint metric, instead of the whole navigation.  

I would like to thank you for the helpful comment. In the present study, not only the CI but also the curving rate shown in Fig. 4 were applied to characterize the behavior in klinotaxis.

According to your comments, we revised the related description in the main text as follows:

“The difference between these CI values is slight, while the model optimized with the constraints exhibits a marginally accelerated attainment of the salt concentration peak, as shown by the trajectories. The slightly higher chemotaxis performance observed in the constrained model is not essentially attributed to the introduction of the AIY-AIZ synaptic constraints but rather depends on the specific individuals selected from the optimized individuals obtained from the evolutionary algorithm. In fact, even when the AIY-AIZ constraints are taken into consideration, the model retains a significant degree of freedom to reproduce salt klinotaxis due to the presence of a substantial parameter space. Consequently, the impact of the AIY-AIZ constraints on the optimization of the CI is expected to be negligible.”

(3) In Figures 3a and b, some inter-neuron connections are relatively weak (e.g., AIYR to AIZR in Figure 3a) - thus it is unclear whether the polarity of such synapses would significantly influence the behavioral outcome or not. The authors could consider plotting the change of the connection strengths between neurons over the course of model optimization to get a sense of confidence in each inter-neuron connection. 

In the evolutional algorithm, the parameters of individuals are subject to discontinuous variation due to the influence of selection, crossover, and mutations. Consequently, it is not straightforward to extract information regarding parameter optimization from parameter changes due to the non-systematic nature of parameter variation..

(4) In Figure 3, the order of individual figure panels is incorrect: in the main text, Figure 3 a and b were mentioned after c and d. Also, the caption of Figure 3c "negative step changes I the" should be "in".  

The main text underwent revision, with the description of Figures 3a and 3b being presented prior to that of Figures 3c and 3d. The typo was revised.

(5) In Figure 4, the order of individual figure panels is messed up: in the main text, Figure 4 a was mentioned after b.  

The main text underwent revision, with the description of Figure 4a being presented prior to that of Figure 4b.

(6) Also in Figure 4, the authors need to provide a definition/explanation of "Bearing" and "Translational Gradient". In Figure 4d, the definition of positive and negative components is not clear.  

Normal and Translational Salt Concentration Gradient in METHOD was referenced for the definition and explanation of the bearing and the translational gradient. We added the following explanation on the positive and negative components.

“The positive and negative components of the curving rate are respectively sampled from the trajectory during leftward turns (as illustrated in Fig. 4b) and rightward turns, respectively.”

(7) Figure 5: the authors need to explain why c has an error bar and how they were calculated, as this result is from a computational model. Figure 5d is experimental results - the authors need to add error bars to the data points and provide a sample size. 

As explained in Analysis of the Salt Preference Behavior in Klinotaxis in METHOD, the ensemble average of these quantities was determined by performing 100,000 sets of the simulation with randomized initial orientation for a simulation time of T_sim=200 sec. The error bars for the experimental data were added in Figs. 5c, 6a, and S9a.

(8) On Page 14, the authors said, "To this end, this end, we used the best evolved network with the constraints, in which we varied the synaptic connections between ASER and AIY from inhibitory to excitatory." How did the model change the ASER-AIY signaling specifically? The authors should provide more explanation or at least refer to the Methods Section.  

The caption of Fig. S4 was referred as the explanation on the detailed method. 

(9) Page 15: "a subset a subset exhibited a slight curve...". This observation from the model simulation is contradictory to experiments. However, their explanation of that is hard to understand.  

I would like to thank you for the helpful comment. To improve this, we added the following explanation:

“In the case of step increases in 𝑧OFF as illustrated in the second right panel from the bottom in Fig.3d, the turning angle φ is increased from its ideal oscillatory component to a value close to zero, causing the model worm to deviate from the ideal sinusoidal trajectory and gradually turn toward lower salt concentrations. On the other hand, in the case of step increases in 𝑧ON as illustrated in the second left panel from the bottom in Fig.3d, the turning angle φ is again increased from its ideal oscillatory component to a value close to zero, causing the model worm to deviate from the ideal sinusoidal trajectory and gradually turn toward higher salt concentrations. The behaviors that are consistent with these analyses are observed in the trajectory illustrated in Fig. S8b.”

(10) Last result session: inhibited SMB in starved worms is due to a mechanism unrelated to their neural network model upstream to SMB. Therefore, their results recapitulating the worms' dispersal behaviors cannot strengthen the validity of their model.  

We agree with your opinion. We think that the findings from the study of starved worms do not provide evidence to validate the neural network model upstream of SMB.   

(11) Discussion: "in contrast, the remaining neurons...". This argument lacks evidence or references.  

This argument is based on the results obtained from the present study. This sentence was revised as follows:

“This regulatory process enables the reproduction of salt concentration memory-dependent reversal of preference behavior in klinotaxis, despite the remaining neurons further downstream of the ASER not undergoing alterations and simply functioning as a modular circuit to transmit the received signals to the motor systems. Consequently, the sensorimotor circuit allows a simple and efficient bidirectional regulation of salt preference behavior in klinotaxis.”

(12) To increase the predictive power of their model, can the authors perform simulations on mutant worms, like those with altered glutamate basal level expression in ASER?  

We would like to express our gratitude for useful suggestion. The simulations, in which the weight of the ASER-AIY synaptic connection is increased from negative (inhibitory connection) to positive (excitatory connection), as illustrated in Figure S4, provide valuable insights into the relationship between varying glutamate basal levels from ASER and behavior in klinotaxis, such as the chemotaxis index.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Comments for the authors of Review Commons Manuscript RC-2024-02804:

The author of the Review Commons manuscript "Antigen flexibility supports the avidity of hemagglutinin-specific antibodies at low antigen densities", present their recent work evaluating hemagglutinin interactions with cellular receptors and antibodies. This manuscript focuses specifically on the avidity of the hemagglutinin using a fluorescence-based assay to measure dissociation kinetics and steady-state binding of antibodies to virions. Their findings confirm that bivalent interactions can offset weak monovalent affinity and that HA ectodomain flexibility is an additional determinant of antibody avidity. These findings are key for our understanding of neutralizing antibodies. Below are some comments that I would like the authors to address as they revise the manuscript.

Comments:

1. Can the authors provide justification for the two influenza viruses that they used.

We selected the lab-adapted IAV strains A/WSN/1933 (H1N1) and A/Hong Kong/1968 (H3N2) for this work because they are well-studied, including in the context of the antibodies used here, S139/1 and C05. While both antibodies bind to more contemporary H3N2 strains, they no not bind to HA from pandemic H1N1. Another feature of these strains is that their HAs have high enough affinity to both antibodies to enable strong signal in our imaging assays. This context for our strain selection has been added in lines 85-88.

1. The use of filamentous particles is a strength, but authors should detail the role of filamentous vs. spherical in nature and lab settings. This will help researchers that plan to repeat these assays.

We have revised the text (lines 336-339) to include more context on the biology of filamentous and spherical influenza viruses. In our experiments, HK68 naturally produces filaments in cell culture whereas WSN33 does not. To produce filaments artificially, we replace the M1 sequence from WSN33 with that of M1 from A/Udorn/1972, an H3N2 strain that is closely related to HK68.

1. Did the authors add the Udorn M1 to the HK68 as well?

Since HK68 naturally forms filaments, we did not introduce Udorn M1 into this strain. We note that the amino acid sequences of Udorn M1 and HK68 M1 differ only at position 167 (Alanine in Udorn, Threonine in HK68), and that this residue has previously been found to not correlate with virus morphology (10.1016/j.virol.2003.12.009).

Reviewer #1 (Significance (Required)):

This manuscript focuses specifically on the avidity of the hemagglutinin using a fluorescence-based assay to measure dissociation kinetics and steady-state binding of antibodies to virions. Thie findings confirm that bivalent interactions can offset weak monovalent affinity and that HA ectodomain flexibility is an additional determinant of antibody avidity. These findings are key for our understanding of neutralizing antibodies.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Summary

In this study, Benegal et al. investigate the binding kinetics of HA-head-specific antibodies (S139/1 and C05) to intact influenza virus particles using a fluorescence microscopy-based technique to measure the dissociation rate (koff) of the antibodies. By applying their proposed equilibrium model for bivalent antibody binding to HA, the authors calculated the crosslinking rate (kx), which represents the rate at which a single-bound antibody crosslinks to an additional HA molecule. Their experiments revealed that antigen crosslinking significantly slows koff, reducing it by up to two orders of magnitude. The authors further utilized streptavidin-coated beads conjugated with biotinylated HA or biotinylated BSA at varying concentrations to control HA surface density. Their results demonstrated that the two tested HA-head-specific antibodies retained the ability to crosslink HAs even at ~10-fold lower HA surface densities. In a complementary experiment, they employed an HA-anchor-specific antibody to restrict HA flexibility, which led to reduced binding of S139/1 and C05 IgGs but not their Fab fragments. This finding suggests that HA flexibility, rather than density, is the primary determinant of antibody crosslinking and avidity. Overall, the authors present an innovative approach to elucidating the dissociation and crosslinking kinetics of antibodies targeting intact virions or nanoparticles. The study is well-designed, with alternative interpretations of the results carefully considered and addressed throughout. I have only a few minor comments and suggestions for clarification.

Minor comments:

1. In Figure 1, does the grey color of each IgG in panel C indicate the Fc domain? If so, please add the description of the colors to the figure legend. In fact, it may be better to explain all the colors used here (for HA1, HA2, Fab heavy chain, light chain, etc.).

We have included this information in panel C and the caption for Figure 1.

1. Under the section," Bivalent binding of S139/1 and C05 persists after ~10-fold reductions in HA surface densities", the beginning of the second paragraph writes, "For both S139/1 and C05 Fab, binding increases linearly with HA density, as expected for a monovalent interaction dictated by absolute HA availability rather than density (Fig. 3D). Interestingly, the same relationship is observed for S139/1 IgG."

Visually, I think the same relationship also seems to hold for C05 IgG. Would it be better to perform some linear regression and report the R2 value for the fitting so that this assessment can be quantitative?

We agree with the reviewer's point. In Figure 3 of the revised manuscript, we include the results from a linear regression analysis to make this assessment more quantitative.

1. At the end of the same page, in the same paragraph, the authors mentioned, "In contrast to the IgG, Fab binding measured at twice the molar concentration of the IgG is nearly undetectable under these conditions, confirming the IgG binding is not occurring through monovalent interactions (Fig. S2E)." What are the conditions you are referring to? In Fig. S2E, there is only the Ab intensity for the Ab binding at 100% HA (and not the other percentages). For the Ab intensity of S139/1 Fab, what is the concentration of the Fab used in Figure 3D? Why could the intensity in this experiment for S139/1 Fab reach ~100,000, whereas that of the 8 nM in Fig. S2E can only reach ~20,000?

To clarify this point, we have updated Figure 3 to include the antibody concentration used for each experiment. The experiments in Fig 3 are conducted approximately around the respective KD of each IgG or Fab to ensure both consistency and strong signal-to-noise. For S139/1, we use 4nM of IgG, and 25nM of Fab. In Fig S2E, we use a concentration of Fab fragments double to that of the IgG, to reach an equivalent concentration of binding sites and confirm that the IgG binding we see is indeed due to bivalent binding. In this case, we use 4nM of IgG and 8nM of Fab.

1. Under the section, "Tilting of HA about its membrane anchor contributes to C05 and S139/1 avidity", in the second paragraph, the authors wrote, "If this is correct, we reasoned that avidity could be reduced by constraining tilting of the HA ectodomain. To test this hypothesis, we used FISW84, an antibody that binds to the HA anchor epitope and biases the ectodomain into a tilted conformation (Fig. 4B)."

Can you use some computational models (maybe the same one you used for Figure 4A) to show that when an HA trimer is bounded by FISW84 Fabs, the tilting of HA is constrained? I think this will help substantiate the assertion above.

This is an important point. The model that we employ in Figure 4A is suited to predicting the angles sampled by HAs when they are bound by an IgG antibody, but it does not take into consideration clashes with the viral membrane. It is these clashes that we predict based on published structures (reference 35 in the revised manuscript) will constrain HA tilting when FISW84 binds to the HA anchor. We have revised the text (Lines 247-249) to clarify these points.

1. It would be good if you could mention the strain of HA used in the experiments in Figure 4 in the actual Figure as well (as supposed to just in the figure legend).

We have added this information to Figure 4 in the revised manuscript.

1. I do not see a method section for the structure-based model you used in Figure 4. In the text, you cited your previous study (ref 28) for the model, but it would be good to write about this briefly (and how you specifically apply the model in this study) in this current manuscript.

We have updated the methods to include a subsection ("Geometric Model for Preferred Crosslinking Geometry") on how the structure-based model was set up, along with a corresponding visual in Fig S3 of the angles of freedom given.

1. In Figure S1 panel D, what is the unit of the antibody concentration? Could you please add it to the graph legend?

We have updated the figure (S1E in the revised manuscript) to include this information.

Reviewer #2 (Significance (Required)):

Previously, this group utilized the same fluorescence-based method to investigate the potency of anti-HA IgG1 antibodies in preventing viral entry versus egress, as well as the tendency of antibodies targeting different HA epitopes to crosslink two HA trimers in cis or in trans (He et al., J Virol, 2024). In this study, they extend their work by evaluating, in-depth, how the density and flexibility of hemagglutinin (HA) on the viral surface influence the binding avidity of anti-HA antibodies. Using two human IgG1 antibodies targeting the HA head, the authors demonstrate that these antibodies can crosslink two HA trimers in cis, even when the trimers are further apart than adjacent HAs. Notably, the study reveals that HA flexibility, rather than density, is the key determinant modulating antibody crosslinking. Even at a 10-fold reduced HA density compared to the original, the antibodies retained their ability to crosslink trimers.

This study provides critical insights into the relationship between HA density, flexibility, and antibody function, adding to the broader understanding of antibody crosslinking-a topic frequently discussed in the field of influenza research. These findings could have significant implications for vaccine design, particularly for strategies involving the display of the HA ectodomain on nanoparticles, potentially guiding the development of more effective influenza vaccines. Furthermore, the broader relevance of these findings may extend to other viruses with similar structural and immunological properties.

My expertise lies in the structural determination of antibody-antigen complexes in influenza and other pathogens. While I may not have sufficient expertise to evaluate specific technical details of the fluorescence-based methods employed, the authors have convincingly demonstrated the robustness of their experimental design and interpretation, supported by appropriate controls.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

SUMMARY In "Antigen flexibility supports the avidity of hemagglutinin-specific antibodies at low antigen densities", Benegal et al. develop a microscopy-based assay to measure dissociation of HA head-binding antibodies from intact virions. This assay allows the authors to explore the contribution of IgG bivalent avidity to antibody interaction with native virions, which is not accessible using other methods such as BLI. Using this assay, the authors further explore the effect of HA density on IgG avidity with engineered low-HA virions and then with artificial HA-coated microspheres. In addition to measuring antibody dissociation, the authors perform structural analyses to predict the conformational preferences of many HA IgGs from published structures. The authors conclude that low HA densities (down to ~10%) still support high avidity binding for the 2 IgGs tested, and thus there would be little evolutionary pressure for IAV to reduce the HA density as a strategy to evade immune recognition.

MAJOR COMMENTS

The data presented are generally convincing for the two antibodies tested, with some caveats listed below. I believe the microscopy technique is valuable and provides a significant contribution to the field, and I believe that the finding that avidity persists at low densities for IAV is compelling and worth communicating to other virologists. Overall, with the incorporation of the suggested major revisions, this manuscript represents a significant advancement in the field.

A major limitation of the current study is the small number of antibodies tested. Two antibodies are quite few, particularly since this work attempts to generalize these observations with structural predictions of dozens or hundreds of HA antibodies. While I believe that the resilience of IgG binding to lower epitope densities is likely common to many HA antibodies (or antibodies in general), this work alone does not support this. To this end, the authors should acknowledge their limited sample size in the text or discussion and that the generalization to other antibodies is speculative. Alternatively, the authors could demonstrate with additional antibodies (such as F045-092 which is pointed out in Fig S3A and perhaps group 'i' antibodies according to Fig S3A).

This is an important point, and we more explicitly acknowledge this limitation in lines 277-278.

It seems to me lateral diffusion of HA in the viral membrane is an important discussion point that was missed in this manuscript. The authors should comment on what is known about the lateral mobility of HA on virions, and how this could impact the ability of an IgG to crosslink. The authors should comment about whether long range diffusion and/or short range "shuffling" of glycoproteins could contribute to crosslinking preferences of antibodies in addition to the tilt, which is the only movement discussed. As appropriate, the authors should then comment on how this may affect their interpretation of experiments using beads. In experiments on beads, there is certainly no lateral mobility of the HA trimers; what are the consequences of this on the analysis?

We agree that this is an important consideration, and we have revised the manuscript (lines 296-298) to address these points. Briefly, we have previously performed fluorescence recovery after photobleaching of covalently labeled HA and NA on the surface of filamentous influenza particles (10.7554/eLife.43764; see Figure 1B of this reference for a representative example). This data indicates that long range diffusion does not seem to be occurring on the virion surface. Short range diffusion, or shuffling, has not been observed, but cannot be ruled out, and may increase conformations favorable to bivalent binding.

Should the authors qualify the limitations in the scope of their experimental results and the system of choice (beads vs. virions) as described in my previous comments, I suggest three experiments that I believe are essential to support the authors' claims. Alternative to qualifying the limitations, two optional experiments are also listed that could support the authors' claims as they are - those require a more extensive experimental undertaking and are thus labeled [OPTIONAL].

1) The photobleaching experiment shown in Figure S1A. I am concerned that measuring photobleaching in steady state conditions does not properly control for the experimental conditions. In steady state, bleached antibody could unbind and be replaced by fluorescent antibody that has diffused into the field of view. This should be more thoroughly controlled by irreversibly capturing antibody (such as with biotin) and imaging after excess antibody is washed away, or by some other method such as capturing and imaging virus that has been directly labeled with AF555. This should be possible using reagents and techniques already demonstrated by the authors.

We have updated the supplemental information with a more rigorous control for photobleaching; the revised figures are shown in Fig S1A. In this experiment, fluorescent S139/1 IgG was bound to HK68 virions. The antibody was washed away, and the loss of fluorescence signal was imaged separately under two conditions: 1) Dissociation only; an image was collected at 0s and one at 60s. 2) Dissociation and photobleaching; an image was collected at a rate of 1 frame per second for 60 seconds. The difference between the endpoint intensities from both conditions is not statistically significant. This supports our conclusion that, in the absence of antibodies in solution that can exchange with those bound to virions, photobleaching does not make a detectable contribution to the loss of signal we observe in our antibody dissociation experiments.

2) In imaging, the authors analyzed only filamentous virions because they exhibit the best signal to noise ratio, which is a reasonable technical simplification. However, this relies on the assumption that glycoprotein presentation is relatively constant between virions of different sizes. It would be helpful to perform some analysis of small virions in any movie where there is sufficient signal. This would support the assumption that rates for small virions are comparable to those of filaments in the same experiment. This should be possible by performing additional analysis on existing data, without requiring additional experiments.

Thank you for calling our attention to a point that needs clarification. The analysis that was restricted to filaments was for the SEP-HA binding experiments (shown in Fig 3A&B). This was done in order to select only those particles that were not diffraction-limited, so that we could control for any systematic differences in size between the two populations by measuring HA signal per unit particle length. For the dissociation experiments (Fig 2), data was taken from all virions in the fields of view. For this analysis, the normalized dissociation curves were averaged in two ways to account for the potential discrepancy that the reviewer points out. In the first method, the average was taken with each virion equally weighted, while in the second method, the entire field of view was masked and normalized together. Both curves look very similar, suggesting that any potential differences between smaller virions and filaments are not enough to make a quantifiable difference in dissociation rate. A representative dissociation curve with both analyses shown side-by-side has been added in Figure S1B.

3) In figure 3, C05 fab binding is used to assay HA content of the SEP HA virions. An additional method of confirming HA content that is more independent from the imaging assay would be beneficial, such as a Western blot to quantify HA relative to NP, NA, or M1 etc.

We have used western blotting to quantify the amount of HA contained relative to M1 in each population. This new data is discussed in lines 163-168 of the revised manuscript and shown in Figure S2C. As noted in the revised text, western blot analysis suggests that the density of native HA is decreased to ~31% its normal level in SEP-HA virions, lower than the ~75% value determined via fluorescence microscopy. One possible reason for this disparity is the presence of virus-like particles in the SEP-HA sample that completely lack wildtype HA. These would be excluded from our imaging analysis but captured by the western blot.

4) [OPTIONAL] In figure 4, it is depicted that FISW84 biases HA in a tilted conformation, and the authors reasonably propose the reduced flexibility discourages crosslinking by IgGs. From the modeling summarized in Figure S3A, are there any antibodies predicted to prefer crosslinking HA at the same angle FISW84 tilts the ectodomain? Would FISW84 enhance crosslinking by such an antibody?

This is an interesting suggestion, and we have revised the manuscript (lines 247-249) to clarify our thinking on this point. Based on the structure of the FISW84 Fab (PDB ID 6HJQ), we conclude that binding of a single Fab fragment does not necessarily actively tilt the HA ectodomain in a specific direction. Rather, it restricts tilting in the direction that would cause a steric clash between the Fab and the membrane. As a result, HA can still sample a range of angles, but this range is no longer symmetrical about the ectodomain axis. By reducing the likelihood that two HA ectodomains would tilt towards each other at a favorable angle, we would expect all antibodies to be disadvantaged to some degree. A possible exception could be if three FISW84 Fab fragments manage to bind to a single HA trimer. In this case, the HA ectodomain would be forced to remain perpendicular to the membrane to accommodate them all. This would favor antibodies that prefer binding to HAs where the ectodomains are parallel to each other. In our analysis in Figure S3A, this includes primarily antibodies that bind to the HA central stalk, such as 31.b.09. However, we note that these antibodies may encounter barriers to bivalent binding that we do not consider here, including proximity to the FISW84 epitope and the high density of HA in the membrane.

5) [OPTIONAL] In figure S3A, the authors display theoretical tilt and spacing preferences for many HA antibodies based on published structures. Interestingly, their group iii antibody is predicted to prefer greater spacing and tilt, and likewise the authors observe increased binding at lower densities (in figure 3E). It would be beneficial to the work to test group i antibodies (base binding) in the dissociation experiments. The behavior of a base binding antibody, particularly at low densities could reinforce the modeling performed for this work.

This is an excellent suggestion which we are not currently able to pursue for technical reasons. In particular, it would be difficult to distinguish between increased binding of these antibodies at low antigen densities that is due to bivalent attachment (and thus reduced dissociation) versus increased accessibility of the epitope, which may be occluded at higher HA densities.

The experiments are well explained and supported by methods that would enable reproducibility.

The authors state "The statistical tests and the number of replicates used in specific cases are described in the figure legends" yet in many cases this information is absent. For the k values in fig 2D, some indication of error or confidence interval would be helpful.

We have ensured that this information is included in each of the captions. Regarding the k values, formal error propagation is challenging due to the way the k values were derived. Specifically, these values were calculated by fitting the average of the three initial dissociation traces, rather than fitting each replicate individually and then averaging the rate constants. As a result, the usual methods for estimating confidence intervals or standard error of the mean are not directly applicable.

MINOR COMMENTS

o Some of the small details in fig 1A and fig S1 are lost due to small figure size - such as the sialic acid residues and lipid bilayer.

We have resized the figure components.

o Although described in the text, it could be helpful to incorporate into figure 2 why the BLI data is shown for S129 fab. Perhaps indicate in 2C that that curve is "too fast to accurately measure" and perhaps near the table in 2D indicate the blue data is from Lee et al. It may be fine to simply remove the BLI results from the figure and refer to them only in the discussion of the experiments. Even with the measured data, the difference between fab and IgG is striking enough to support the paper, and the BLI data may be more confusing in the figure than it adds.

We have updated the caption for Figure 2D to clarify that binding between the S139/1 Fab and A/WSN/1933 HA is approaching the limit of detection in our assay, and that the additional rates are from Lee et al. We have also updated the table to make the presentation of the kinetic parameters more clear.

o In figure 3A, better describe the fluorescent components in the fluorescent images in the legend.

We have updated the caption for Figure 3A to describe the fluorescent components shown in the image. Specifically, the panel labeled 'HA' shows signal from a fluorescent FI6v3 scFv, while the panel labeled 'decoy' shows signal from the SEP-HA construct.

o From personal experience, the flexibility of HA ectodomain can be significantly affected by how much of the membrane proximal linker region is retained or removed. Could the authors comment on how they chose the cutoff for their HA ectodomain used in the bead experiments and their rationale?

This is an important point, and while the precise impact of the linker on HA flexibility remains uncertain, we agree that it may increase the freedom of motion of the ectodomain relative to the HA membrane anchor. We mention this caveat in the revised text (lines 188-191) and we have added an AlphaFold2 prediction of how our recombinant HA might look to Figure S2D.

o In Figure S1B, if I understand correctly: black dashed line "IgG equivalent dissociation rate" is the experimental data, magenta "Crosslinking model fit" is the theoretically total antibody bound as described by the mathematical model. Then the gray lines "Double- /singly- bound antibodies plot the theoretical amount of antibody bound once and bound twice. If this is correct, I believe it would be clearer if the singly- and doubly- bound were plotted in separate colors, and that this is explained more clearly in the legend.

We have revised the figure to show doubly- and singly-bound curves using different line styles.

o Related to an earlier comment, if lateral diffusion may play a role, how might this differ between different types of antibodies?

As mentioned in our previous response, we do not anticipate that lateral diffusion makes a significant contribution to antibody binding to the surface of virions, although it may be important on the cell surface.

o Could the authors comment in the discussion on how their results on virions may translate to the surface of the infected cell, which is also decorated in viral glycoproteins? Early time points of infection could be an in vivo example of low-density HA. What extent may antibody binding and crosslinking affect viral proteins on the cell surface or the immune response?

This is a very interesting point. Antibody binding to the infected cell surface has been shown to alter viral release and morphology, presumably at lower HA densities than those observed the viral surface. We have added a brief discussion of this point (lines 291-295) to the revised manuscript.

o The github link in the methods is incorrect or not yet available.

Thank you for noting this. We have updated the link.

o Reference 1 has an incorrect or expired link.

These references have been updated.

Reviewer #3 (Significance (Required)):

• This work represents a conceptual advance in our understanding of antibody action on viral pathogens. The authors adapt existing microscopy methodologies to measure antibody avidity in a new way that is better representative of in vivo conditions.

• To my knowledge, this is the first instance of direct measurement of antibody off-rates from intact virus particles, instead of immobilized protein as in BLI, SPR, or interferometry.

• This work should be of interest to virologist and biophysicists interested in the cooperative binding of antibodies and the relation of virus structural organization to antibody recognition. Immunologist may also be influenced by this work. This work may be followed up by other researchers similarly measuring the association and dissociation rates of antibodies with single virions, or otherwise comparing fab to IgG binding to gain insight into when crosslinking is or is not occurring.

• Reviewer expertise: Single-virion imaging, protein complexes, biochemistry, influenza A.

• I do not have sufficient expertise to evaluate the mathematical models and differential equations for modeling the k-on and k-off rates.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this study, Benegal et al. investigate the binding kinetics of HA-head-specific antibodies (S139/1 and C05) to intact influenza virus particles using a fluorescence microscopy-based technique to measure the dissociation rate (koff) of the antibodies. By applying their proposed equilibrium model for bivalent antibody binding to HA, the authors calculated the crosslinking rate (kx), which represents the rate at which a single-bound antibody crosslinks to an additional HA molecule. Their experiments revealed that antigen crosslinking significantly slows koff, reducing it by up to two orders of magnitude.

The authors further utilized streptavidin-coated beads conjugated with biotinylated HA or biotinylated BSA at varying concentrations to control HA surface density. Their results demonstrated that the two tested HA-head-specific antibodies retained the ability to crosslink HAs even at ~10-fold lower HA surface densities. In a complementary experiment, they employed an HA-anchor-specific antibody to restrict HA flexibility, which led to reduced binding of S139/1 and C05 IgGs but not their Fab fragments. This finding suggests that HA flexibility, rather than density, is the primary determinant of antibody crosslinking and avidity.

Overall, the authors present an innovative approach to elucidating the dissociation and crosslinking kinetics of antibodies targeting intact virions or nanoparticles. The study is well-designed, with alternative interpretations of the results carefully considered and addressed throughout. I have only a few minor comments and suggestions for clarification.

Minor comments:

1. In Figure 1, does the grey color of each IgG in panel C indicate the Fc domain? If so, please add the description of the colors to the figure legend. In fact, it may be better to explain all the colors used here (for HA1, HA2, Fab heavy chain, light chain, etc.).
2. Under the section," Bivalent binding of S139/1 and C05 persists after ~10-fold reductions in HA surface densities", the beginning of the second paragraph writes, "For both S139/1 and C05 Fab, binding increases linearly with HA density, as expected for a monovalent interaction dictated by absolute HA availability rather than density (Fig. 3D). Interestingly, the same relationship is observed for S139/1 IgG."

Visually, I think the same relationship also seems to hold for C05 IgG. Would it be better to perform some linear regression and report the R2 value for the fitting so that this assessment can be quantitative? 3. At the end of the same page, in the same paragraph, the authors mentioned, "In contrast to the IgG, Fab binding measured at twice the molar concentration of the IgG is nearly undetectable under these conditions, confirming the IgG binding is not occurring through monovalent interactions (Fig. S2E)." What are the conditions you are referring to? In Fig. S2E, there is only the Ab intensity for the Ab binding at 100% HA (and not the other percentages). For the Ab intensity of S139/1 Fab, what is the concentration of the Fab used in Figure 3D? Why could the intensity in this experiment for S139/1 Fab reach ~100,000, whereas that of the 8 nM in Fig. S2E can only reach ~20,000? 4. Under the section, "Tilting of HA about its membrane anchor contributes to C05 and S139/1 avidity", in the second paragraph, the authors wrote, "If this is correct, we reasoned that avidity could be reduced by constraining tilting of the HA ectodomain. To test this hypothesis, we used FISW84, an antibody that binds to the HA anchor epitope and biases the ectodomain into a tilted conformation (Fig. 4B)."

Can you use some computational models (maybe the same one you used for Figure 4A) to show that when an HA trimer is bounded by FISW84 Fabs, the tilting of HA is constrained? I think this will help substantiate the assertion above. 5. It would be good if you could mention the strain of HA used in the experiments in Figure 4 in the actual Figure as well (as supposed to just in the figure legend). 6. I do not see a method section for the structure-based model you used in Figure 4. In the text, you cited your previous study (ref 28) for the model, but it would be good to write about this briefly (and how you specifically apply the model in this study) in this current manuscript. 7. In Figure S1 panel D, what is the unit of the antibody concentration? Could you please add it to the graph legend?

Significance

Previously, this group utilized the same fluorescence-based method to investigate the potency of anti-HA IgG1 antibodies in preventing viral entry versus egress, as well as the tendency of antibodies targeting different HA epitopes to crosslink two HA trimers in cis or in trans (He et al., J Virol, 2024). In this study, they extend their work by evaluating, in-depth, how the density and flexibility of hemagglutinin (HA) on the viral surface influence the binding avidity of anti-HA antibodies. Using two human IgG1 antibodies targeting the HA head, the authors demonstrate that these antibodies can crosslink two HA trimers in cis, even when the trimers are further apart than adjacent HAs. Notably, the study reveals that HA flexibility, rather than density, is the key determinant modulating antibody crosslinking. Even at a 10-fold reduced HA density compared to the original, the antibodies retained their ability to crosslink trimers.

This study provides critical insights into the relationship between HA density, flexibility, and antibody function, adding to the broader understanding of antibody crosslinking-a topic frequently discussed in the field of influenza research. These findings could have significant implications for vaccine design, particularly for strategies involving the display of the HA ectodomain on nanoparticles, potentially guiding the development of more effective influenza vaccines. Furthermore, the broader relevance of these findings may extend to other viruses with similar structural and immunological properties.

My expertise lies in the structural determination of antibody-antigen complexes in influenza and other pathogens. While I may not have sufficient expertise to evaluate specific technical details of the fluorescence-based methods employed, the authors have convincingly demonstrated the robustness of their experimental design and interpretation, supported by appropriate controls.

Author response:

The following is the authors’ response to the original reviews

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

Walton et al. set out to isolate new phages targeting the opportunistic pathogen Pseudomonas aeruginosa. Using a double ∆fliF ∆pilA mutant strain, they were able to isolate 4 new phages, CLEW-1. -3, -6, and -10, which were unable to infect the parental PAO1F Wt strain. Further experiments showed that the 4 phages were only able to infect a ∆fliF strain, indicating a role of the MS-protein in the flagellum complex. Through further mutational analysis of the flagellum apparatus, the authors were able to identify the involvement of c-di-GMP in phage infection. Depletion of c-di-GMP levels by an inducible phosphodiesterase renders the bacteria resistant to phage infection, while elevation of c-di-GMP through the Wsp system made the cells sensitive to infection by CLEW-1. Using TnSeq, the authors were able to not only reaffirm the involvement of c-di-GMP in phage infection but also able to identify the exopolysaccharide PSL as a downstream target for CLEW-1. C-di-GMP is a known regulator of PSL biosynthesis. The authors show that CLEW-1 binds directly to PSL on the cell surface and that deletion of the pslC gene resulted in complete phage resistance. The authors also provide evidence that the phage-PSL interaction happens during the biofilm mode of growth and that the addition of the CLEW-1 phage specifically resulted in a significant loss of biofilm biomass. Lastly, the authors set out to test if CLEW-1 could be used to resolve a biofilm infection using a mouse keratitis model. Unfortunately, while the authors noted a reduction in bacterial load assessed by GFP fluorescence, the keratitis did not resolve under the tested parameters. 

Strengths: 

The experiments carried out in this manuscript are thoughtful and rational and sufficient explanation is provided for why the authors chose each specific set of experiments. The data presented strongly supports their conclusions and they give present compelling explanations for any deviation. The authors have not only developed a new technique for screening for phages targeting P. aeruginosa, but also highlight the importance of looking for phages during the biofilm mode of growth, as opposed to the more standard techniques involving planktonic cultures. 

Weaknesses: 

While the paper is strong, I do feel that further discussions could have gone into the decision to focus on CLEW-1 for the majority of the paper. The paper also doesn't provide any detailed information on the genetic composition of the phages. It is unclear if the phages isolated are temperate or virulent. Many temperate phages enter the lytic cycle in response to QS signalling, and while the data as it is doesn't suggest that is the case, perhaps the paper would be strengthened by further elimination of this possibility. At the very least it might be worth mentioning in the discussion section. 

Thank you for your review. The genomes of all Clew phages and Ocp-2 have been uploaded [Genbank accession# PQ790658.1, PQ790659.1, PQ790660.1, PQ790661.1, and PQ790662.1]. It turns out that the Clew phage are highly related, which is highlighted by the genomic comparison in the supplementary figure S1. It therefore made sense to focus our in-depth analysis on one of the phage. We have included a supplementary figure (S1A), demonstrating that the other Clew phage also require an intact psl locus for infection, to make that logic clearer. The phage are virulent (there is apparently a bit of a debate about this with regard to Bruynogheviruses, but we have not been able to isolate lysogens). This is now mentioned in the discussion.  

Reviewer #2 (Public review): 

This manuscript by Walton et al. suggests that they have identified a new bacteriophage that uses the exopolysaccharide Psl from Pseudomonas aeruginosa (PA) as a receptor. As Psl is an important component in biofilms, the authors suggest that this phage (and others similarly isolated) may be able to specifically target biofilm-growing bacteria. While an interesting suggestion, the manner in which this paper is written makes it difficult to draw this conclusion. Also, some of the results do not directly follow from the data as presented and some relevant controls seem to be missing. 

Thank you for your review. We would argue that the combination of demonstrating Psl-dependent binding of Clew-1 to P. aeruginosa, as well as demonstration of direct binding of Clew-1 to affinity-purified Psl, indicates that the phage binds directly to Psl and uses it as a receptor. In looking at the recommendations, it appears that the remark about controls refers to not using the ∆pslC mutant alone (as opposed to the ∆fliF2 ∆pslC double mutant) as a control for some of the binding experiments. However, since the ∆fliF2 mutant is more permissive for phage infection, analyzing the effect of deleting pslC in the context of the ∆fliF2 mutant background is the more stringent test. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

First off, I would like to congratulate the authors on this study and manuscript. It is very well executed and the writing and flow of the paper are excellent. The findings are intriguing and I believe the paper will be very well received by both the phage, Pseudomonas, and biofilm communities. 

Thank you for your kind review of our work!

I have very little to critique about the paper but I have listed a few suggestions that I believe could strengthen the paper if corrected: 

Comments and suggestions: 

(1) The paper initially describes 4 isolated phages but no rationale is given for why they chose to continue with CLEW-1, as opposed to CLEW-3, -6, and -10. The paper would benefit from going into more detail with phage genomics and perhaps characterize the phage receptor binding to PSL. 

Clew-1, -3, -6, and -10 are actually quite similar to one another. The genomes are now uploaded to Genbank [accession# PQ790658.1, PQ790659.1, PQ790660.1, and PQ790661.1]. They all require an intact Psl locus for infection, we have updated Fig. S1 to show this for the remaining Clew phage. In the end, it made sense to focus on one of these related phage and characterize it in depth.

(2) PA14 was used in some experiments but not listed in the strain table. 

Thank you, this has been added in the resubmission.

(3) Would have been good to see more strains/isolates used.

We are currently characterizing the host range of Clew-1. It appears to be pretty limited, but this will likely be included in another paper that will focus on host range, not only of Clew-1, but other biofilm-tropic phage that we have isolated since then.

(4) Could purified PSL be added to make non-PSL strain (like PA14) susceptible? 

We have tried adding purified Psl to a psl mutant strain, but this does not result phage sensitivity. Further characterization of the Psl receptor, is something we are currently working on, but will likely be a much bigger story than can be easily accommodated in a revised manuscript.

(5) No data on resistance development. 

We have not done this as yet.

(6) Alternative biofilm models. Both in vitro and in vivo. 

We agree that exploring the interaction of Clew-1 with biofilms in greater detail is a logical next step. The revised manuscript does have data on the viability of P. aeruginosa biofilm bacteria after Clew-1 infection using either a bead biofilm model or LIVE/DEAD staining of static biofilms. However, expanding on this further (setting up flow-cell biofilms, developing reporters to monitor phage infection, etc.) is beyond the scope of this initial report and characterization of Clew-1.

(7) There is a mistake in at least one reference. An unknown author is listed in reference 48. DA Garsin is not part of the paper. Might be worth looking into further mistakes in the reference list as I suspect this might be an issue related to the citation software.

Thank you. Yes, odd how that extra author got snuck in. This has been corrected.

(8) I don't seem to be able to locate a Genbank file or accession number. If it wasn't performed how was evolutionary relatedness data generated?

The genomes of all Clew phages and Ocp-2 have been uploaded [Genbank accession# PQ790658.1, PQ790659.1, PQ790660.1, PQ790661.1, and PQ790662.1]

(9) No genomic information about the isolated phages. Are they temperate or virulent? This would be important information as only strictly lytic phages are currently deemed appropriate for phage therapy. 

These phage are virulent. We have only been able to isolate resistant bacteria from plaques, but they do not harbor the phage (as detected by PCR). This matches what other researchers have found for Bruynogheviruses.

Reviewer #2 (Recommendations for the authors): 

Others have used different PA mutants lacking known phage receptors to pan for new phages. However, it is not totally clear how the screen here was selected for the Psl-specific phage. The authors used flagella and pili mutants and found Clew-1, -3, -6, and -10. These were all Bruynogheviruses. They also isolated a phage that uses the O antigen as a receptor. The family of this latter phage and how it is known to use this as a receptor is not described. 

Phage Ocp-2 is a Pbunavirus. We added new supplementary figure S3, addressing the O-antigen receptor.

The authors focused on Clew-1, but the receptor for these other Clew phages is not presented. For Clew-1 the phage could plaque on the fliF deletion mutant but not the wild-type strain. The reason for this never appears to be addressed. The authors leap to consider the involvement of c-di-GMP, but how this relates to fliF appears to be lacking. 

We have included a supplementary figure demonstrating that all the Clew phage require Psl for infection (Fig. S1A). As noted above, we have uploaded the genomic data that underpins the comparison in our supplementary figure. The phage are all closely related. It therefore made sense to focus on one of the phage for the analysis.  

It is particularly unclear why this phage doesn't plaque on PAO1 as this strain does make Psl. Related to this, it actually looks like something is happening to PAO1 in Figure S4 (although what units are on the x-axis is not entirely clear).

We hypothesize that the fraction of susceptible cells in the population dictates whether the phage can make overt plaques. The supplementary figure S4 indicates that a subpopulation of the wild-type culture is susceptible and this is borne out by the fraction of wild type cells that the phage can bind to (~50%). The fliF mutation increases this frequency of susceptible cells to 80-90% (Fig. 3).

The Tnseq screen to identify receptors is clever and identifies additional phosphodiesterase genes, the deletion of which makes PAO1 susceptible. And the screen to find resistant fliF mutants identified genes involved in Psl. However, the link between the phosphodiesterase mutants and the amount of Psl produced never appears to be established. And the statement that Psl is required for infection (line 130) is never actually tested.

The link between c-di-GMP and Psl production is well-established in the literature. I think the requirement for Psl in infection is demonstrated multiple ways, including lack of plaque formation on psl mutant strains and lack of phage binding to strains that do not produce Psl, direct binding of the phage to affinity purified Psl.

Figure 2C describes using a ∆fliF2 strain but how this is different (or if it is different) from ∆fliF described in the text is never explained.

The difference in the deletions is explained in table S1, in the description for the deletion constructs used in their construction, pEXG2-∆fliF and pEXG2-∆fliF2 (∆fliF2 is smaller than ∆fliF and can be complemented completely with our complementing plasmid, pP37-fliF, which is the reason why we used the ∆fliF2 mutation going forward, rather than the ∆fliF mutation on which the phage was originally isolated).

Similarly, there is a sentence (line 138) that "Attachment of Clew-1 is Psl-dependent" but this would appear to have no context.

The relevant figure, Fig. 3, is cited in the next sentence and is the subject of the remaining paragraphs in this section of the manuscript.

For Figure 3B, why wasn't the single ∆pslC mutant visualized in this analysis? Similar questions relate to the data in Figure 4.

Analyzing the effect of the pslC deletion in the context of the ∆fliF2 mutant background, which is more permissive for phage infection, is the more stringent test.  

The efficacy of Clew-1 in the mouse keratitis model is intriguing but it is unclear why the CFU/eye are so variable. The description of how the experiment was actually carried out is not clear. Was only one eye scratched or both? Were controls included with a scratch and no bacteria ({plus minus} phage)?

One eye was infected. We did not conduct a no-bacteria control (just scratching the cornea is not sufficient to cause disease). The revised manuscript has an updated animal experiment in which we carried the infection forward to 72h with two phage treatments. Following this regiment, there is a significant decrease in CFU, as well as corneal opacity (disease). Variability of the data is a fairly common feature in animal experiments. There are a number of factors, such as does the mouse blink and remove some of the inoculum shortly after deposition of the bacteria or the phage after each treatment that could explain this variability.

Author response:

The following is the authors’ response to the current reviews.

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

The revised manuscript has gained much clarity and consistency. One previous criticism, however, has in my opinion not been properly addressed. I think the problem boils down to not clearly distinguishing between orthologs and paralogs/homologs. As this problem affects a main conclusion - the prevalence of deletions over insertions in the MTBC - it should be addressed, if not through additional analyses, then at least in the discussion.

Insertions and deletions are now distinguished in the following way: "Accessory regions were further classified as a deletion if present in over 50% of the 192 sub-lineages or an insertion/duplication if present in less than 50% of sub-lineages." The outcome of this classification is suspicious: not a single accessory region was classified as an insertion/duplication. As a check of sanity, I'd expect at least some insertions of IS6110 to show up, which has produced lineage- or sublineage-specific insertions (Roychowdhury et al. 2015, Shitikov et al. 2019). Why, for example, wouldn't IS6110 insertions in the single L8 strain show up here?

In a fully clonal organism, any insertion/duplication will be an insertion/duplication of an existing sequence, and thus produce a paralog. If I'm correctly understanding your methods section, paralogs are systematically excluded in the pangraph analysis. Genomic blocks are summarized at the sublineage levels as follows (l.184 ): "The DNA sequences from genomic blocks present in at least one sub-lineage but completely absent in others were extracted to look for long-term evolution patterns in the pangenome." I presume this is done using blastn, as in other steps of the analysis.

So a sublineage-specific copy of IS6110 would be excluded here, because IS6110 is present somewhere in the genome in all sublineages. However, the appropriate category of comparison, at least for the discussion of genome reduction, is orthology rather than homology: is the same, orthologous copy of IS6110, at the same position in the genome, present or absent in other sublineages? The same considerations apply to potential sublineage-specific duplicates of PE, PPE, and Esx genes. These gene families play important roles in host-pathogen interactions, so I'd argue that the neglect of paralogs is not a finicky detail, but could be of broader biological relevance.

Within the analysis we undertook we did look at paralogous blocks in pangraph, based on copy number per genome. However, this could have been clearer in the text and we will rectify this. We also focussed on duplicated/deleted blocks that were present in two of more sub-lineages. This is noted in figure 4 legend but we will make this clearer in other sections of the manuscript.

We agree that indeed the way paralogs are handled could still be optimised, and that gene duplicates of some genes could have biological importance. The reviewer is suggesting that a synteny analysis between genomes would be best for finding specific regions that are duplicated/deleted within a genome, and if those sections are duplicated/deleted in the same regions of the genome. Since Pangraph does not give such information readily, a larger amount of analysis would be required to confirm such genome position-specific duplications. While this is indeed important, we deem this to be out of scope for the current publication, but will note this as a limitation in the discussion. However, this does not fundamentally change the main conclusions of our analysis.

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this paper, Behruznia and colleagues use long-read sequencing data for 335 strains of the Mycobacterium tuberculosis complex to study genome evolution in this clonal bacterial pathogen. They use both a "classical" pangenome approach that looks at the presence and absence of genes, and a more general pangenome graph approach to investigate structural variants also in non-coding regions. The two main results of the study are that (1) the MTBC has a small pangenome with few accessory genes, and that (2) pangenome evolution is driven by deletions in sublineage-specific regions of difference. Combining the gene-based approach with a pangenome graph is innovative, and the former analysis is largely sound apart from a lack of information about the data set used. The graph part, however, requires more work and currently fails to support the second main result. Problems include the omission of important information and the confusing analysis of structural variants in terms of "regions of difference", which unnecessarily introduces reference bias. Overall, I very much like the direction taken in this article, but think that it needs more work: on the one hand by simply telling the reader what exactly was done, on the other by taking advantage of the information contained in the pangenome graph.

Strengths:

The authors put together a large data set of long-read assemblies representing most lineages of the Mycobacterium tuberculosis context, covering a large geographic area. State-of-the-art methods are used to analyze gene presence-absence polymorphisms (Panaroo) and to construct a pangenome graph (PanGraph). Additional analysis steps are performed to address known problems with misannotated or misassembled genes in pangenome analysis.

Weaknesses:

The study does not quite live up to the expectations raised in the introduction. Firstly, while the importance of using a curated data set is emphasized, little information is given about the data set apart from the geographic origin of the samples (Figure 1). A BUSCO analysis is conducted to filter for assembly quality, but no results are reported. It is also not clear whether the authors assembled genomes themselves in the cases where, according to Supplementary Table 1, only the reads were published but not the assemblies. In the end, we simply have to trust that single-contig assemblies based on long-reads are reliable.

We have now added a robust overview of the dataset to supplementary file 1. This is split into 3 sections: public genomes, which were assembled by others; sequenced genomes, which were created and assembled by us; the BUSCO information for all the genomes together. We did not assemble any public data ourselves but retrieved these from elsewhere. We have modified the text to be more specific on this (Line 114 onwards) and the supplementary file is updated to better outline the data.

One issue with long read assemblies could be that high rates of sequencing errors result in artificial indels when coverage is low, which in turn could affect gene annotation and pangenome inference (e.g. Watson & Warr 2019, https://doi.org/10.1038/s41587-018-0004-z). Some of the older long-read data used by the authors could well be problematic (PacBio RSII), but also their own Nanopore assemblies, six of which have a mean coverage below 50 (Wick et al. 2023 recommend 200x for ONT, https://doi.org/ 10.1371/journal.pcbi.1010905). Could the results be affected by such assembly errors? Are there lineages, for example, for which there is an increased proportion of RSII data? Given the large heterogeneity in data quality on the NCBI, I think more information about the reads and the assemblies should be provided.

We have now included an analysis where we looked to see if the sequencing platform influenced the resulting accessory genome size and the pseudogene count. The details of this are included in lines 207-219, and the results are outlined in lines 251-258. Essentially, we found no correlation between sequencing platform and genome characteristics, although less stringent cut-offs did suggest that PacBio SMRT-only assembled genomes may have larger accessory genomes. We do not believe this is enough to influence our larger inferences from this data. It should be noted that complete genomes, in general, give a better indication of pangenome size compared to draft genomes, as has been shown previously (e.g. Marin et al., 2024). Even with some small potential bias, this makes our analysis more robust than any previously published.

In relation to the sequencing depth of our own data, all genomes had coverage above 30x, which Sanderson et al. (2024) has shown to be sufficient for highly accurate sequence recovery. We fixed an issue with the L9 isolate from the previous submission, which resulted in a better BUSCO score and overall quality of that isolate and the overall dataset.

The part of the paper I struggled most with is the pangenome graph analysis and the interpretation of structural variants in terms of "regions of difference". To start with, the method section states that "multiple whole genomes were aligned into a graph using PanGraph" (l.159/160), without stating which genomes were for what reason. From Figure 5 I understand that you included all genomes, and that Figure 6 summarizes the information at the sublineage level. This should be stated clearly, at present the reader has to figure out what was done. It was also not clear to me why the authors focus on the sublineage level: a minority of accessory genes (107 of 506) are "specific to certain lineages or sublineages" (l. 240), so why conclude that the pangenome is "driven by sublineage-specific regions of difference", as the title states? What does "driven by" mean? Instead of cutting the phylogeny arbitrarily at the sublineage level, polymorphisms could be described more generally by their frequencies.

We apologise for the ambiguity in the methodology. All the isolates were inputted to Pangraph to create the pangenome using this method. This is now made clearer in lines 175-177. Standard pangenome statistics (size, genome fluidity, etc.) derived from this Pangraph output are now present in the results section as well (lines 301-320).

We then only looked at regions of difference at the sub-lineage level, meaning we grouped genomes by sub-lineage within the resulting graph and looked for blocks common between isolates of the same sub-lineage but absent from one or more other sub-lineages. We did this from both the Panaroo output and the Pangraph output and then retained only blocks found by both. The results of this are now outlined in lines 351-383.

We focussed on these sub-lineage-specific regions to focus on long-term evolution patterns and not be influenced by single-genome short-term changes. We do not have enough genomes of closely related isolates to truly look at very recent evolution, although the small accessory genome indicates this is not substantial in terms of gene presence/absence. We also did not want potential mis-annotations in a single genome to heavily influence our findings due to the potential issues pointed out by the reviewer above. We state this more clearly in the introduction (lines 106-108), methods (lines 184-186) and results (345-347), and we indicate the limitations in the Discussion, lines 452-457 and 471-473. We also changed the title to ‘shaped’ instead of ‘driven by’.

I fully agree that pangenome graphs are the way to go and that the non-coding part of the genome deserves as much attention as the coding part, as stated in the introduction. Here, however, the analysis of the pangenome graph consists of extracting variants from the graph and blasting them against the reference genome H37Rv in order to identify genes and "regions of difference" (RDs) that are variable. It is not clear what the authors do with structural variants that yield no blast hit against H37Rv. Are they ignored? Are they included as new "regions of difference"? How many of them are there? etc. The key advantage of pangenome graphs is that they allow a reference-free, full representation of genetic variation in a sample. Here reference bias is reintroduced in the first analysis step.

We apologise for the confusion here as indeed the RDs terminology is very MTBC-specific. Current RDs are always relevant to H37Rv, as that is how original discovery of these regions was done and that is how RDScan works. We clarify this in the introduction (lines 67-68). If we found a large sequence polymorphism (e.g. by Pangraph) and searched for known RDs using RDScan, we then assigned a current RD name to this LSP. This uses H37Rv as a reference. If we did not find a known RD, we then classified the LSP as a new RD if it is present in H37Rv, or left the designation as an LSP if not in H37Rv, thus expanding the analysis beyond the H37Rv-centric approaches used by others previously. This is hopefully now made clearer in the methods, lines 187-194.

Along similar lines, I find the interpretation of structural variants in terms of "regions of difference" confusing, and probably many people outside the TB field will do so. For one thing, it is not clear where these RDs and their names come from. Did the authors use an annotation of RDs in the reference genome H37Rv from previously published work (e.g. Bespiatykh et al. 2021)? This is important basic information, its lack makes it difficult to judge the validity of the results. The Bespiatykh et al. study uses a large short-read data (721 strains) set to characterize diversity in RDs and specifically focuses on the sublineage-specific variants. While the authors cite the paper, it would be relevant to compare the results of the two studies in more detail.

We have amended the introduction to explain this terminology better (lines 67-68). Naming of the RDs here came from using RDScan to assign current names to any accessory regions we found and if such a region was not a known RD, we gave it a lineage-related name, allowing for proper RD naming later (lines 187-194). Because the Bespiatyk paper is the basis for RDScan, our work implicitly compares to this throughout, as any RDs we find which were not picked up by RDScan are thus novel compared to that paper.

As far as I understand, "regions of difference" have been used in the tuberculosis field to describe structural variants relative to the reference genome H37Rv. Colloquially, regions present in H37Rv but absent in another strain have been called "deletions". Whether these polymorphisms have indeed originated through deletion or through insertion in H37Rv or its ancestors requires a comparison with additional strains. While the pangenome graph does contain this information, the authors do not attempt to categorize structural variants into insertions and deletions but simply seem to assume that "regions of difference" are deletions. This, as well as the neglect of paralogs in the "classical" pangenome analysis, puts a question mark behind their conclusion that deletion drives pangenome evolution in the MTBC.

We have now amended the analysis to specifically designate a structural variant as a deletion if present in the majority of strains and absent in a minority, or an insertion/duplication if present in a minority and absent in a majority (lines 191-192). We also ran Panaroo without merging paralogs to examine duplication in this output; Pangraph implicitly includes paralogs already.

From all these analyses we did not find any structural variants classed as insertions/duplications and did not find paralogs to be a major feature at the sub-lineage level (lines 377-383). While these features could be important on shorter timescales, we do not have enough closed genomes to confidently state this (limitation outlined in lines 452-457). Therefore, our assertion that deletions are a primary force shaping the long-term evolution in this group still holds.

Reviewer #2 (Public Review):

Summary:

The authors attempted to investigate the pangenome of MTBC by using a selection of state-of-the-art bioinformatic tools to analyse 324 complete and 11 new genomes representing all known lineages and sublineages. The aim of their work was to describe the total diversity of the MTBC and to investigate the driving evolutionary force. By using long read and hybrid approaches for genome assembly, an important attempt was made to understand why the MTBC pangenome size was reported to vary in size by previous reports.

Strengths:

A stand-out feature of this work is the inclusion of non-coding regions as opposed to only coding regions which was a focus of previous papers and analyses which investigated the MTBC pangenome. A unique feature of this work is that it highlights sublineage-specific regions of difference (RDs) that were previously unknown. Another major strength is the utilisation of long-read whole genomes sequences, in combination with short-read sequences when available. It is known that using only short reads for genome assembly has several pitfalls. The parallel approach of utilizing both Panaroo and Pangraph for pangenomic reconstruction illuminated the limitations of both tools while highlighting genomic features identified by both. This is important for any future work and perhaps alludes to the need for more MTBC-specific tools to be developed.

Weaknesses:

The only major weakness was the limited number of isolates from certain lineages and the over-representation others, which was also acknowledged by the authors. However, since the case is made that the MTBC has a closed pangenome, the inclusion of additional genomes would not result in the identification of any new genes. This is a strong statement without an illustration/statistical analysis to support this.

We have included a Heaps law and genome fluidity calculation for each pangenome estimation to demonstrate that the pangenome is closed. This is detailed in lines 225-228 with results shown in lines 274-278 and 316- 320 and Supplementary Figure 2. We agree that more closely related genomes would benefit a future version of this analysis and indicate we indicate the limitations in the Discussion, lines 452-457 and 471-473.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Abstract

l. 24, "with distinct genomic features". I'm not sure what you are referring to here.

We refer to the differences in accessory genome and related functional profiles but did not want to bloat the abstract with such additional details

Introduction

l. 40, "L1 to L9". A lineage 10 has been described recently: https://doi.org/10.3201/eid3003.231466.

We have updated the text and the reference. Unfortunately, no closed genome for this lineage exists so we have not included it in the analyses. We note this in the results, like 232

l.62/3, "caused by the absence of horizontal gene transfer, plasmids, and recombination". Recombination is not absent in the MTBC, only horizontal gene transfer seems to be, which is what the cited studies show. Indeed a few sentences later homologous recombination is mentioned as a cause of deletions.

This has now been removed from the introduction

l. 67, "within lineage diversity is thought to be mostly driven by SNPs". Again I'm not sure what is meant here with "driven by". Point mutations are probably the most common mutational events, but duplications, insertions, deletions, and gene conversion also occur and can affect large regions and possibly important genes, as shown in a recent preprint (https://doi.org/10.1101/2024.03.08.584093).

We have changed the text to say ‘mostly composed of’. While indeed other SNVs may be contributing, the prevailing thought at lineage level is that SNPs are the primary source of diversity. The linked pre-print is looking at within transmission clusters and this has not been described at the lineage level, which could be done in a future work.

l. 100/1. "that can account for variations in virulence, metabolism, and antibiotic resistance". I would phrase this conservatively since the functional inferences in this study are speculative.

This has now been tempered to be less specific.

Methods

l. 108. That an assembly has a single contig does not mean that it is "closed". Many single contig assemblies on NCBI are reference-guided short-read assemblies, that is, fragments patched together rather than closed assemblies. The same could be true for long-read assemblies.

We specifically chose those listed as closed on NCBI so rely on their checks to ensure this is true. We have stated this better in the paper, line 117.

l. 111. From Supplementary Table 1 understand that for many genomes only the reads were available (no ASM number). Did you assemble these genomes? If yes, how? The assembly method is not indicated in the supplement, contrary to what is written here.

All public genomes were downloaded in their assembled forms from the various sources. This is specified better in the text (line 118) and the supplementary table 1 now lists the accessions for all the assemblies.

l. 113. How many assemblies passed this threshold? And is BUSCO actually useful to assess assembly quality in the MTBC? I assume the dynamic, repetitive gene families that cause problems for assembly and mapping in TB (PE, PPE, ESX) do not figure in the BUSCO list of single-copy orthologs.

All assemblies passed the BUSCO thresholds for high-quality genomes as laid out in Supplementary Table 1. While indeed this does not include multi-copy genes such as PE/PPE we focussed on regions of difference at the sub-lineage level where two or more genomes represent that sub-lineage. This means any assembly issues in a single genome would need to be exactly the same in another of the same sub-lineage to be included in our results. Through this, we aimed to buffer out issues in individual assemblies.

l. 147: Why is Panaroo used with -merge-paralogs? I understand that near-identical genes may not be too interesting from a functional perspective, but if the aim of the analysis is to make broad claims about processes driving genome evolution, paralogs should be considered.

We chose to do so with merged paralogs to look for larger patterns of diversity beyond within-genome paralogs. Additionally, this was required to build the core phylogenetic tree. However, as the reviewer points out, this may bias our findings towards deletions and away from duplications as a primary evolutionary force.

We repeated this without the merged paralogs option and indeed found a larger pangenome, as outlined in Table 1. However, at the sub-lineage level, this did not result in any new presence/absence patterns (lines 381-383). This means the paralogs tended to be in single genomes only. This still indicates that deletions are the primary force in the longer-term evolution of the complex but indeed on shorter spans this may be different.

l. 153: remove the comment in brackets.

This has been fixed and the proper URL placed in instead.

l. 159: which genomes, and why those?

This is now clarified to state all genomes were used for this analysis.

l. 161, "gene blocks": since this analysis is introduced as capturing the non-coding part of the genome, maybe just call them "blocks"?

All references to gene blocks are now changed to genomic blocks to be more specific.

l. 162: what happens with blocks that yield no hits against RvD1, TbD1, and H37Rv?

We named these with lineage-specific names (supplementary table 4) but did not assign RD names specifically.

l. 164: where does the information about the regions of difference come from? How exactly were these regions determined?

Awe have expanded this section to be more specific on the use of RDScan and new naming, along with how we determine if something is an RD/LSP.

Results

l. 185ff: This paragraph gives many details about the geographic origin of the samples, but what I'd expect here is a short description of assembly qualities, for example, the results of the BUSCO analysis, a description of your own Nanopore assemblies, or a small analysis of the number of indels/pseudogenes relative to sequencing technology or coverage (see comment in the public review).

This section (lines 231-258) has been expanded considerably to give a better overview of the dataset and any potential biases. Supplementary table 1 has also been expanded to include more information on each strain.

l. 187, "324 genomes published previously": 322 according to the methods section.

The number has been fixed throughout to the proper total of public genomes (329).

l. 201: define the soft core, shell, and cloud genes.

This is now defined on line 262

l. 228, "defined primarily by RD105 and RD207 deletions": this claim seems to come from the analysis of variable importance (Factoextra), which should be made clear here.

This has been clarified on line 333.

l. 237, "L8, serving as the ancestor of the MTBC": this is incorrect, equivalent to saying that the Chimpanzee is the ancestor of Homo sapiens.

We have changed this to basal to align with how it is described in the original paper.

l. 239, "The accessory genome of the MTBC". It is a bit confusing that the same term, 'accessory genome', is used here for the graph-based analysis, which is presented as a way to look at the non-coding part of the genome.

We have clarified the terminology on line 347 and improved consistency throughout.

l. 240/1, "specific to certain lineages and sublineages". What exactly do you mean by "specific" to? Present only in members of a certain lineage/sublineage? In all members of a certain lineage/sublineage? Maybe an additional panel in Figure 5, showing examples of lineage- and sublineage-specific variants, would help the reader grasp this key concept.

We have clarified this on line 349 and the legend of what is now figure 4.

l. 241/2, "82 lineage and sublineage-specific genomic regions ranging from 270 bp to 9.8 kb". Were "gene blocks" filtered for a minimum size, or why are there no variants smaller than 270 bp? A short description of all the blocks identified in the graph could be informative (their sizes, frequencies ...).

Yes, a minimum of 250bp was set for the blocks to only look at larger polymorphisms. This is clarified on line 177 and 304.

A second point: It is not entirely clear to me what Figure 6 is showing. Are you showing here a single representative strain per sublineage? Or have you somehow summarized the regions of difference shown in Figure 5 at the sublineage level? What is the tree on the left? This should be made clear in the legend and maybe also in the methods/results.

In figure 4 (which was figure 6), because each RD is common to all members of the same sub-lineage, we have placed a single branch for each sub-lineage. This is has been clarified in the legend.

l. 254, "this gene was classified as being in the core genome": why should a partially deleted gene not be in the core genome?

You are correct, we have removed that statement.

l. 258/259, "The Pangraph alignment approach identified partial gene deletion and non-coding regions of the DNA that were impacted by genomic deletion". I do not understand how you classify a structural variant identified in the pangenome graph as a deletion or an insertion.

This has been clarified as relative to H37Rv, as this is standard practice for RDs and general evolutionary analyses in MTBC, as outlined above.

l. 262/263 , "the accessory genome of the MTBC is small and is acquired vertically from a common ancestor within the lineage". If deletion is the main process involved here, "acquired" seems a bit strange.

We agree and changed the header to better reflect the discussion on mis-annotation issues

Figure 1: Good to know, but not directly relevant for the rest of the paper. Maybe move it to the supplement?

This has been moved to Supplementary figure 1

Figure 2: the y-axis is labeled 'Variable genome size', but from the text and the legend I figure it should be 'Number of accessory genes'?

This has been changed to ‘accessory genes’ in Figure 1 (which was figure 2 in previous version).

Figure 4: too small.

We will endeavour to ensure this is as large as possible in the final version.

Discussion

l. 271, "MTBC accessory genome is ... acquired vertically". See above.

Changed, as outlined above.

l. 292, "appeared to be fragmented genes caused by misassemblies". Is there a way to distinguish "true" pseudogenes from misassemblies? This could be a relevant issue for low-coverage long-read assemblies (see public review).

Not that we are currently aware of, but we do know other groups which are working on this issue.

l. 300/1, "the whole-genome approach could capture higher genetic variations". Do you mean the graph approach? I'm not sure that comparing the two approaches here makes sense, as they serve different purposes. A pangenome graph is a summary of all genetic variation, while the purpose of Panaroo is to study gene absence/presence. So by definition, the graph should capture more genetic variation.

This statement was specifically to state that much genetic variation in MTBC is outside the coding genes and so traditional “pangenome’ analyses are actually not looking at the full genomic variation.

l. 302/3, "this method identified non-coding regions of the genome that were affected by genomic deletions". See the comments above regarding deletions versus insertions. I'd say this method identifies coding and non-coding regions that were affected by genomic deletions and insertions.

We have undertaken additional analyses to be sure these are likely deletions, as outlined above.

l. 305: what are "lineage-independent deletions"?

We labelled these as convergent evolution, now clarified on line 443.

l. 329: How is RD105 "caused" by the insertion of IS6110? I did not find RD105 mentioned in the Alonso et al. paper. Similarly below, l. 331, how is RD207 "linked" to IS6110?

The RD105 connection was misattributed as IS6110 insertion is related to RD152, not RD105. This has now been removed.

RD207 is linked to IS6110 as its deletion is due to recombination between two such elements. This is now clarified on line 486.

l. 345, "the growth advantage gene group": not quite sure what this is.

We have fixed this on line 499 to state they are genes which confer growth advantages.

l. 373ff: The role of genetic drift in the evolution of the MTBC is an open question, other studies have come to different conclusions than Hershberg et al. (this has been recently reviewed: https://doi.org/10.24072/pcjournal.322).

We have outlined this debate better in lines 527-531

l. 375/6, "Gene loss, driven by genetic drift, is likely to be a key contributor to the observed genetic diversity within the MTBC." This sentence would need some elaboration to be intelligible. How does genetic drift drive gene loss?

We have removed this.

l. 395/6, "... predominantly driven by genome reduction. This observation underlines the importance of genomic deletions in the evolution of the MTBC." See comments above regarding deletions. I'm not convinced that your study really shows this, as it completely ignores paralogs and the processes counteracting reductive genome evolution: duplication and gene amplification.

As outlined above, we have undertaken additional analyses to more strongly support this statement.

l. 399, "the accessory genome of MTBC is a product of gene deletions, which can be classified into lineage-specific and independent deletions". Again, I'm not sure what is meant by lineage-independent deletions.

We have better defined this in the text, line 443, to be related to convergent evolution.

Reviewer #2 (Recommendations For The Authors):

Suggestions for improved or additional experiments, data, or analyses.

In lines 120-121, it is mentioned that TB-profiler v4.4.2 was used for lineage classification, but this version was released in February 2023. As I understand there have been some changes (inclusion/exclusion) of certain lineage markers. Would it not be appropriate to repeat lineage classification with a more recent version? This would of course require extensive re-analysis, so could the lineage marker database perhaps also be cited.

We have rerun all the genomes through TB-Profiler v6.5 and updated the text to state this; the exact database used is also now stated.

Could the authors perhaps include the sequencing summary or quality of the nanopore sequences? The L9 (Mtb8) sample had a relatively lower depth and resulted in two contigs. Yet one contig was the initial inclusion criteria. It is unclear whether these samples were excluded from some of the analyses. Mtb6 also has relatively low coverage. Was the sequencing quality adequate to accurately identify all the lineage markers, in particular those with a lower depth of coverage? Could a hybrid approach be an inexpensive way to polish these assemblies?

We reanalysed the L9 sample and, with some better cleaning, got it to a single contig with better depth and overall score. This is outlined in the Supplementary table 1 sheets. While depth is average, it is still above the recommended 30x, which is needed for good sequence recovery (Sanderson et al., 2024). We did indeed recover all lineage markers from these assemblies.

Recommendations for improving the writing and presentation.

The introduction is well-written and recent MTBC pangenomic studies have been incorporated, but I am curious as to why this paper was not referred to: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC6922483/ I believe this was the first attempt to study the pangenome, albeit with a different research question. Nearly all previous analyses largely focused on utilizing the pangenome to investigate transmission.

Indeed this study did look at a pangenome of sorts, but specifically SNPs and not genes or regions. Since the latter is the main basis for pangenome work these days, we chose not to include this paper.

Minor corrections to the text and figures.

In line 129, it is explained that DNA was extracted to be suitable for PacBio sequencing, but ONT sequencing was used for the 11 new sequences. Is this a minor oversight or do the authors feel that DNA extracted for PacBio would be suitable for ONT sequencing? It is a fair assumption.

We apologise, this is a long-read extraction approach and not specific to PacBio. We have amended the text to state this.

In line 153, this should be removed: (Conor, could you please add the script to your GitHub page?).

This has been fixed now.

Reviewer #2 (Public review):

Summary:

The study introduces new tools for measuring intracellular Ca2+ concentration gradients around retinal rod bipolar cell (rbc) synaptic ribbons. This is done by comparing the Ca2+ profiles measured with mobile Ca2+ indicator dyes versus ribbon-tethered (immobile) Ca2+ indicator dyes. The Ca2+ imaging results provide a straightforward demonstration of Ca2+ gradients around the ribbon and validate their experimental strategy. This experimental work is complemented by a coherent, open-source, computational model that successfully describes changes in Ca2+ domains as a function of Ca2+ buffering. In addition, the authors try to demonstrate that there is heterogeneity among synaptic ribbons within an individual rbc terminal.

Strengths:

The study introduces a new set of tools for estimating Ca2+ concentration gradients at ribbon AZs, and the experimental results are accompanied by an open-source, computational model that nicely describes Ca2+ buffering at the rbc synaptic ribbon. In addition, the dissociated retinal preparation remains a valuable approach for studying ribbon synapses. Lastly, excellent EM.

Comments on revisions:

Specific minor comments:

(1) Rewrite the final sentence of the Abstract. It is difficult to understand.

(2) Add a definition in the Introduction (and revisit in the Discussion) that delineates between micro- and nano-domain. A practical approach would be to round up and round down. If you round up from 0.6 um, then it is microdomain which means ~ 1 um or higher. Likewise, round down from 0.3 um to nanodomain? If you are using confocal, or even STED, the resolution for Ca imaging will be in the 100 to 300 nm range. The point of your study is that your new immobile Ca2-ribbon indicator may actually be operating on a tens of nm scale: nanophysiology. The Results are clearly written in a way that acknowledges this point but maybe make such a "definition" comment in the intro/discussion in order to: 1) demonstrate the power of the new Ca2+ indicator to resolve signals at the base of the ribbon (effectively nano), and 2) (Discussion) to acknowledge that some are achieving nanoscopic resolution (50 to 100nm?) with light microscopy (as you ref'd Neef et al., 2018 Nat Comm).

(3) Suggested reference: Grabner et al. 2022 (Sci Adv, Supp video 13, and Fig S5). Here rod Cav channels are shown to be expressed on both sides the ribbon, at its base, and they are within nanometers from other AZ proteins. This agrees with the conclusions from your imaging work.

(4) In the Discussion, add a little more context to what is known about synaptic transmission in the outer and inner retina.. First, state that the postsynaptic receptors (for example: mGluR6-OnBCs vs KARs-Off-BCs, vs. AMPAR-HCs), and possibly the synaptic cleft (ground squirrel), are known to have a significant impact on signaling in the outer retina. In the inner retina, there are many more unknowns. For example, when I think of the pioneering Palmer JPhysio study, which you sight, I think of NMDAR vs AMPAR, and uncertainty in what type postsynaptic cell was patched (GC or AC....). Once you have informed the reader that the postsynapse is known to have a significant impact on signaling, then promote your experimental work that addresses presynaptic processes: "...the new tool and results allow us to explore release heterogeneity, ribbon by ribbon in dissociated preps, which we eventually plan to use at ribbon synapses within slices......to better understand how the presynapse shapes signaling......".

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors, Dalal, et. al., determined cryo-EM structures of open, closed, and desensitized states of the pentameric ligand-gated ion channel ELIC reconstituted in liposomes, and compared them to structures determined in varying nanodisc diameters. They argue that the liposomal reconstitution method is more representative of functional ELIC channels, as they were able to test and recapitulate channel kinetics through stopped-flow thallium flux liposomal assay. The authors and others have described channel interactions with membrane scaffold proteins (MSP), initially thought to be in a size-dependent manner. However, the authors reported that their cryo-EM ELIC structure interacts with the large nanodisc spNW25, contrary to their original hypotheses. This suggests that the channel's interactions with MSPs might alter its structure, possibly not accurately representing/reflecting functional states of the channel.

Strengths:

Cryo-EM structural determination from proteoliposomes is a promising methodology within the ion channel field due to their large surface area and lack of MSP or other membrane mimetics that could alter channel structure. Comparing liposomal ELIC to structures in various-sized nanodiscs gives rise to important discussions for other membrane protein structural studies when deciding the best method for individual circumstances.

Weaknesses:

The overarching goal of the study was to determine structural differences of ELIC in detergent nanodiscs and liposomes. Including comparisons of the results to the native bacterial lipid environment would provide a more encompassing discussion of how the determined liposome structures might or might not relate to the native receptor in its native environment. The authors stated they determined open, closed, and desensitized states of ELIC reconstituted in liposomes and suggest the desensitization gate is at the 9' region of the pore. However, no functional studies were performed to validate this statement.

The goal of this study was to determine structures of ELIC in the same lipid environment in which its function is characterized. However, it is also worth noting that phosphatidylethanolamine and phosphatidylglyerol, two lipids used for the liposome formation, are necessary for ELIC function (PMID 36385237) and principal lipid components of gram-negative bacterial membranes in which ELIC is expressed.

The desensitized structure of ELIC in liposomes shows a pore diameter at the hydrophobic L240 (9’) residue of 3.3 Å, which is anticipated to pose a large energetic barrier to the passage of ions due to the hydrophobic effect. We have included a graphical representation of pore diameters from the HOLE analysis for all liposome structures in Supplementary Figure 6B. While we have not tested the role of L240 in desensitization with functional experiments, it was shown by Gonzalez-Gutierrez and colleagues (PMID 22474383) that the L240A mutation apparently eliminates desensitization in ELIC. This finding is consistent with L240 (9’) being the desensitization gate of ELIC. We have referenced this study when discussing the desensitization gate in the Results.

Reviewer #2 (Public review):

Summary

The report by Dalas and colleagues introduces a significant novelty in the field of pentameric ligand-gated ion channels (pLGICs). Within this family of receptors, numerous structures are available, but a widely recognised problem remains in assigning structures to functional states observed in biological membranes. Here, the authors obtain both structural and functional information of a pLGIC in a liposome environment. The model receptor ELIC is captured in the resting, desensitized, and open states. Structures in large nanodiscs, possibly biased by receptor-scaffold protein interactions, are also reported. Altogether, these results set the stage for the adoption of liposomes as a proxy for the biological membranes, for cryoEM studies of pLGICs and membrane proteins in general.

Strengths

The structural data is comprehensive, with structures in liposomes in the 3 main states (and for each, both inward-facing and outward-facing), and an agonist-bound structure in the large spNW25 nanodisc (and a retreatment of previous data obtained in a smaller disc). It adds up to a series of work from the same team that constitutes a much-needed exploration of various types of environment for the transmembrane domain of pLGICs. The structural analysis is thorough.

The tone of the report is particularly pleasant, in the sense that the authors' claims are not inflated. For instance, a sentence such as "By performing structural and functional characterization under the same reconstitution conditions, we increase our confidence in the functional annotation of these structures." is exemplary.

Weaknesses

Core parts of the method are not described and/or discussed in enough detail. While I do believe that liposomes will be, in most cases, better than, say, nanodiscs, the process that leads from the protein in its membrane down to the liposome will play a big role in preserving the native structure, and should be an integral part of the report. Therefore, I strongly felt that biochemistry should be better described and discussed. The results section starts with "Optimal reconstitution of ELIC in liposomes [...] was achieved by dialysis". There is no information on why dialysis is optimal, what it was compared to, the distribution of liposome sizes using different preparation techniques, etc... Reading the title, I would have expected a couple of paragraphs and figure panels on liposome reconstitution. Similarly, potential biochemical challenges are not discussed. The methods section mentions that the sample was "dialyzed [...] over 5-7 days". In such a time window, most of the members of this protein family would aggregate, and it is therefore a protocol that can not be directly generalised. This has to be mentioned explicitly, and a discussion on why this can't be done in two days, what else the authors tested (biobeads? ... ?) would strengthen the manuscript.

To a lesser extent, the relative lack of both technical details and of a broad discussion also pertains to the cryoEM and thallium flux results. Regarding the cryoEM part, the authors focus their analysis on reconstructions from outward-facing particles on the basis of their better resolutions, yet there was little discussion about it. Is it common for liposome-based structures? Are inward-facing reconstructions worse because of the increased background due to electrons going through two membranes? Are there often impurities inside the liposomes (we see some in the figures)? The influence of the membrane mimetics on conformation could be discussed by referring to other families of proteins where it has been explored (for instance, ABC transporters, but I'm sure there are many other examples). If there are studies in other families of channels in liposomes that were inspirational, those could be mentioned. Regarding thallium flux assays, one argument is that they give access to kinetics and set the stage for time-resolved cryoEM, but if I did not miss it, no comparison of kinetics with other techniques, such as electrophysiology, nor references to eventual pioneer time-resolved studies are provided.

Altogether, in my view, an updated version would benefit from insisting on every aspect of the methodological development. I may well be wrong, but I see this paper more like a milestone on sample prep for cryoEM imaging than being about the details of the ELIC conformations.

Additions have been made to the Results and Discussion sections elaborating on the following points: 1) reconstitution of ELIC in liposomes using dialysis, the advantage of this over other methods such as biobeads, and whether the dialysis protocol can be shortened for other less stable proteins; 2) the issue of separating outward- and inward-facing channels; 3) referencing the effect of nanodiscs on ABC transporters, structures of membrane proteins in liposomes, and pioneering time-resolved cryo-EM studies; and 4) comparison of the kinetics of ELIC gating kinetics with electrophysiology measurements. With regards to the first point, it should be noted that all necessary details are provided in the Methods to reproduce the experiments including the reconstitution and stopped-flow thallium flux assay. It is also important to note that the same preparation for making proteoliposomes was used for assessing function using the stopped-flow thallium flux assay and for determining the structure by cryo-EM. This is now stated in the Results.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major revisions:

(1) The authors suggest that the desensitization gate is located at the 9' region within the pore. However, as stated by the authors, the 2' residues function as the desensitization gate in related channels. In a few of their HOLE analyzed structures (e.g. Figure 2B and 4B), there seems to be a constriction also at 2', but this finding is not discussed in the context of desensitization. Further functional testing of mutated 9' and/or 2' gates would bolster the argument for the location of the desensitization gate.

As stated above, we have included HOLE plots of pore radius in Supplementary Fig. 6B and referenced the study showing that the L240A mutation (9’) in ELIC (PMID 22474383) appears to eliminate desensitization. This result along with the narrow pore diameter at 9’ in the desensitized structure suggests that 9’ is likely a desensitization gate in ELIC. In contrast, mutation of Q233 (2’) to a cysteine in a previous study produced a channel that still desensitizes (PMID 25960405). Since Q233 is a hydrophilic residue in contrast to L240, Q233 probably does not pose the same energetic barrier to ion translocation as L240 based on the structure.

(2) In discussing functional states of ELIC and ELIC5 in different reconstitution methods, the authors reference constriction sites determined by HOLE analysis software. These constriction sites were key evidence for the authors to determine functional state, however, it is difficult to discern pore sizes based on the figures. Pore diameters and clear color designation (ie, green vs orange) with the figures would greatly aid their discussions.

HOLE plots are displayed in Supplementary Fig. 6B and pore diameters are not provided in the text.

(3) The authors had an intriguing finding that ELIC dimers are found in spNW25 scaffolds. Is there any functional evidence to suggest they could be functioning as dimers?

There is no evidence that the function of ELIC or other pLGICs is altered by the formation of dimers of pentamers. Therefore, while this result is intriguing and likely facilitated by concentrating multiple ELIC pentamers within the nanodisc, it is not clear if these interactions have any functional importance. We have stated this in the Results.

(4) Thallium flux assay to validate channel function within proteoliposomes. Proteoliposomes are known to be generally very leaky membranes, would be good to have controls without ELIC added to determine baseline changes in fluorescence.

We have established from multiple previous studies that liposomes composed of 2:1:1 POPC:POPE:POPG (PMID 36385237 and 31724949) do not show significant thallium flux as measured by the stopped-flow assay (PMID 29058195) in the absence of ELIC activity. Furthermore, in the present study, the data in Fig. 1A of WT ELIC shows a low thallium flux rate 60 seconds after exposure to agonist when the ion channel has mostly desensitized. Therefore, this data serves also as a control indicating that the high thallium flux rates in response to agonist (at earlier delay times) are not due to leak, but rather due to ELIC channel activity.

Minor revisions:

(1) Abstract and introduction. 'Liganded' should be ligand

We removed this word and changed it to “agonist-bound” for consistency throughout the manuscript.

(2) Inconsistent formatting of FSC graphs in Supplemental Figure 4

The difference is a consequence of the different formatting between cryoSPARC and Relion FSC graphs.

Reviewer #2 (Recommendations for the authors):

Minor writing remarks:

The present report builds on previous work from the same team, and to my eye it would be a plus if this were conveyed more explicitly. I see it as a strength to explore various developments in several papers that complement each other. E.g in the introduction when citing reference 12 (Dalal 2024), later in introducing ref 15 (Petroff 2022), I wish I was reminded of the main findings and how they fit with the new results.

We have expanded on the Results and Discussion detailing key findings from these studies that are relevant to the current study.

Suggestions for analysis:

Data treatment. Maybe I missed it, but I wondered if C1 vs C5 treatment of the liposome data showed any interesting differences? When I think about the biological membrane, I picture it as a very crowded place with lots of neighbouring proteins. I would not be surprised if, similarly to what they do in discs, the receptor would tend to stick to, or bump into, anything present also in liposomes (a neighboring liposome, some undefined density inside the liposome).

We attempted to perform C1 heterogeneous refinement jobs in cryoSPARC and C1 3D classification in Relion5. For the WT datasets, these did not produce 3D reconstructions that were of sufficient quality for further refinement. For ELIC5 with agonist, the C1 reconstructions were not different than the C5 reconstructions. Furthermore, there was no evidence of dimers of pentamers from the 2D or 3D treatments, unlike what was observed in the spNW25 nanodiscs. This is likely because the density of ELIC pentamers in the liposomes was too low to capture these transient interactions. We have included this information in the Methods.

In data treatment, we sometimes find only what we're looking for. I wondered if the authors tried to find, for instance, the open and D conformations in the resting dataset during classifications.

This is an interesting question since some population of ELIC channels could visit a desensitized conformation in the absence of agonist and this would not be detected in our flux assay. After extensive heterogeneous refinement jobs in cryoSPARC and 3D classification jobs in Relion5, we did not detect any unexpected structures such as open/desensitized conformations in the apo dataset.

In the analysis of the M4 motions, is there info to be gained by looking at how it interacts with the rest of the TMD? For instance, I wondered if the buried surface area between M4 and the rest was changed. Also one could imagine to look at that M4 separately in outward-facing and inward-facing conformations (because the tension due to the bilayer will not be the same in the outer layer in both orientations - intuitively, I'd expect different levels of M4 motions)

We have expanded our analysis of the structures as recommended. We determined the buried surface area between M4 and the rest of the channel in the liganded WT and ELIC5 structures in liposomes and nanodiscs, as well as the area between the TMD interfaces for these structures. There appears to be a pattern where liposome structures show less buried surface area between M4 and the rest of the channel, and less area at the TMD interfaces. Overall, this suggests that the liposome structures of ELIC in the open-channel or desensitized conformations are more loosely packed in the TMD compared to the nanodisc structures.

We have also further discussed the issue of separating outward- and inward-facing conformations in the Results. The problem with classifying outward- and inward-facing orientations is that top/down or tilted views of the particles cannot be easily distinguished as coming from channels in one orientation or the other, unless there are conformational differences between outward- and inward-facing channels that would allow for their separation during 3D heterogeneous refinement or 3D classification. Furthermore, since the inward-facing reconstructions are of much lower resolution than the outward-facing reconstructions, we suspect that these particles are more heterogeneous possibly containing junk, multiple conformations, or particles that are both inward- and outward-facing. On the other hand, the outward-facing structures are of good quality, and therefore we are more confident that these come from a more homogeneous set of particles that are likely outward-facing (Note that most particles are outward facing based on side views of the 2D class averages). That said, when examining the conformation of M4 in outward- and inward-facing structures, we do not see any significant differences with the caveat that the inward-facing structures are of poor quality and that inward- and outward-facing particles may not have been well-separated.

Reviewer #3 (Public review):

A bias in how people infer the amount of control they have over their environment is widely believed to be a key component of several mental illnesses including depression, anxiety, and addiction. Accordingly, this bias has been a major focus in computational models of those disorders. However, all of these models treat control as a unidimensional property, roughly, how strongly outcomes depend on action. This paper proposes---correctly, I think---that the intuitive notion of "control" captures multiple dimensions in the relationship between action and outcome. In particular, the authors identify one key dimension: the degree to which outcome depends on how much *effort* we exert, calling this dimension the "elasticity of control". They additionally argue that this dimension (rather than the more holistic notion of controllability) may be specifically impaired in certain types of psychopathology. This idea has the potential to change how we think about several major mental disorders in a substantial way and can additionally help us better understand how healthy people navigate challenging decision-making problems. More concisely, it is a very good idea.

Unfortunately, my view is that neither the theoretical nor empirical aspects of the paper really deliver on that promise. In particular, most (perhaps all) of the interesting claims in the paper have weak empirical support.

Starting with theory, the authors do not provide a strong formal characterization of the proposed notion of elasticity. There are existing, highly general models of controllability (e.g., Huys & Dayan, 2009; Ligneul, 2021) and the elasticity idea could naturally be embedded within one of these frameworks. The authors gesture at this in the introduction; however, this formalization is not reflected in the implemented model, which is highly task-specific. Moreover, the authors present elasticity as if it is somehow "outside of" the more general notion of controllability. However, effort and investment are just specific dimensions of action; and resources like money, strength, and skill (the "highly trained birke") are just specific dimensions of state. Accordingly, the notion of elasticity is necessarily implicitly captured by the standard model. Personally, I am compelled by the idea that effort and resource (and therefore elasticity) are particularly important dimensions, ones that people are uniquely tuned to. However, by framing elasticity as a property that is different in kind from controllability (rather than just a dimension of controllability), the authors only make it more difficult to integrate this exciting idea into generalizable models.

Turning to experiment, the authors make two key claims: (1) people infer the elasticity of control, and (2) individual differences in how people make this inference are importantly related to psychopathology.

Starting with claim 1, there are three subclaims here; implicitly, the authors make all three. (1A) People's behavior is sensitive to differences in elasticity, (1B) people actually represent/track something like elasticity, and (1C) people do so naturally as they go about their daily lives. The results clearly support 1A. However, 1B and 1C are not strongly supported.

(1B) The experiment cannot support the claim that people represent or track elasticity because effort is the only dimension over which participants can engage in any meaningful decision-making. The other dimension, selecting which destination to visit, simply amounts to selecting the location where you were just told the treasure lies. Thus, any adaptive behavior will necessarily come out in a sensitivity to how outcomes depend on effort.

Notes on rebuttal: The argument that vehicle/destination choice is not trivial because people occasionally didn't choose the instructed location is not compelling to me-if anything, the exclusion rate is unusually low for online studies. The finding that people learn more from non-random outcomes is helpful, but this could easily be cast as standard model-based learning very much like what one measures with the Daw two-step task (nothing specific to control here). Their final argument is the strongest, that to explain behavior the model must assume "a priori that increased effort could enhance control." However, more literally, the necessary assumption is that each attempt increases the probability of success-e.g. you're more likely to get a heads in two flips than one. I suppose you can call that "elasticity inference", but I would call it basic probabilistic reasoning.

For 1C, the claim that people infer elasticity outside of the experimental task cannot be supported because the authors explicitly tell people about the two notions of control as part of the training phase: "To reinforce participants' understanding of how elasticity and controllability were manifested in each planet, [participants] were informed of the planet type they had visited after every 15 trips." (line 384).

Notes on rebuttal: The authors try to retreat, saying "our research question was whether people can distinguish between elastic and inelastic controllability." I struggle to reconcile this with the claim in the abstract "These findings establish the elasticity of control as a distinct cognitive construct guiding adaptive behavior". That claim is the interesting one, and the one I am evaluating the evidence in light of.

Finally, I turn to claim 2, that individual differences in how people infer elasticity are importantly related to psychopathology. There is much to say about the decision to treat psychopathology as a unidimensional construct (the authors claim otherwise, but see Fig 6C). However, I will keep it concrete and simply note that CCA (by design) obscures the relationship between any two variables. Thus, as suggestive as Figure 6B is, we cannot conclude that there is a strong relationship between Sense of Agency (SOA) and the elasticity bias---this result is consistent with any possible relationship (even a negative one). As it turns out, Figure S3 shows that there is effectively no relationship (r=0.03).

Notes on rebuttal: The authors argue for CCA by appeal to the need to "account for the substantial variance that is typically shared among different forms of psychopathology". I agree. A simple correlation would indeed be fairly weak evidence. Strong evidence would show a significant correlation after *controlling for* other factors (e.g. a regression predicting elasticity bias from all subscales simultaneously). CCA effectively does the opposite, asking whether-with the help of all the parameters and all the surveys-one can find any correlation between the two sets of variables. The results are certainly suggestive, but they provide very little statistical evidence that the elasticity parameter is meaningfully related to any particular dimension of psychopathology.

There is also a feature of the task that limits our ability to draw strong conclusions about individual differences about elasticity inference. In the original submission, the authors stated that the study was designed to be "especially sensitive to overestimation of elasticity". A straightforward consequence of this is that the resulting *empirical* estimate of estimation bias (i.e., the gamma_elasticity parameter) is itself biased. This immediately undermines any claim that references the directionality of the elasticity bias (e.g. in the abstract). Concretely, an undirected deficit such as slower learning of elasticity would appear as a directed overestimation bias.

When we further consider that elasticity inference is the only meaningful learning/decision-making problem in the task (argued above), the situation becomes much worse. Many general deficits in learning or decision-making would be captured by the elasticity bias parameter. Thus, a conservative interpretation of the results is simply that psychopathology is associated with impaired learning and decision-making.

Notes on rebuttal: I am very concerned to see that the authors removed the discussion of this limitation in response to my first review. I quote the original explanation here:

- In interpreting the present findings, it needs to be noted that we designed our task to be especially sensitive to overestimation of elasticity. We did so by giving participants free 3 tickets at their initial visits to each planet, which meant that upon success with 3 tickets, people who overestimate elasticity were more likely to continue purchasing extra tickets unnecessarily. Following the same logic, had we first had participants experience 1 ticket trips, this could have increased the sensitivity of our task to underestimation of elasticity in elastic environments. Such underestimation could potentially relate to a distinct psychopathological profile that more heavily loads on depressive symptoms. Thus, by altering the initial exposure, future studies could disambiguate the dissociable contributions of overestimating versus underestimating elasticity to different forms of psychopathology.

The logic of this paragraph makes perfect sense to me. If you assume low elasticity, you will infer that you could catch the train with just one ticket. However, when elasticity is in fact high, you would find that you don't catch the train, leading you to quickly infer high elasticity-eliminating the bias. In contrast, if you assume high elasticity, you will continue purchasing three tickets and will never have the opportunity to learn that you could be purchasing only one-the bias remains.

The authors attempt to argue that this isn't happening using parameter recovery. However, they only report the *correlation* in the parameter, whereas the critical measure is the *bias*. Furthermore, in parameter recovery, the data-generating and data-fitting models are identical-this will yield the best possible recovery results. Although finding no bias in this setting would support the claims, it cannot outweigh the logical argument for the bias that they originally laid out. Finally, parameter recovery should be performed across the full range of plausible parameter values; using fitted parameters (a detail I could only determine by reading the code) yields biased results because the fitted parameters are themselves subject to the bias (if present). That is, if true low elasticity is inferred as high elasticity, then you will not have any examples of low elasticity in the fitted parameters and will not detect the inability to recover them.

Minor comments:

Below are things to keep in mind.

The statistical structure of the task is inconsistent with the framing. In the framing, participants can make either one or two second boarding attempts (jumps) by purchasing extra tickets. The additional attempt(s) will thus succeed with probability p for one ticket and 2p - p^2 for two tickets; the p^2 captures the fact that you only take the second attempt if you fail on the first. A consequence of this is buying more tickets has diminishing returns. In contrast, in the task, participants always jumped twice after purchasing two tickets, and the probability of success with two tickets was exactly double that with one ticket. Thus, if participants are applying an intuitive causal model to the task, they will appear to "underestimate" the elasticity of control. I don't think this seriously jeopardizes the key results, but any follow-up work should ensure that the task's structure is consistent with the intuitive causal model.

The model is heuristically defined and does not reflect Bayesian updating. For example, it over-estimates maximum control by not using losses with less than 3 tickets (intuitively, the inference here depends on what your beliefs about elasticity). Including forced three-ticket trials at the beginning of each round makes this less of an issue; but if you want to remove those trials, you might need to adjust the model. The need to introduce the modified model with kappa is likely another symptom of the heuristic nature of the model updating equations.

Author response:

The following is the authors’ response to the original reviews

Summary of our revisions

(1) We have explained the reason why the untrained RNN with readout (value-weight) learning only could not well learn the simple task: it is because we trained the models continuously across trials with random inter-trial intervals rather than separately for each episodic trial and so it was not trivial for the models to recognize that cue presentation in different trials constitutes a same single state since the activities of untrained RNN upon cue presentation should differ from trial to trial (Line 177-185).

(2) We have shown that dimensionality was higher in the value-RNNs than in the untrained RNN (Fig. 2K,6H).

(3) We have shown that even when distractor cue was introduced, the value-RNNs could learn the task (Fig. 10).

(4) We have shown that extended value-RNNs incorporating excitatory and inhibitory units and conforming to the Dale's law could still learn the tasks (Fig. 9,10-right column).

(5) In the original manuscript, the non-negatively constrained value-RNN showed loose alignment of value-weight and random feedback from the beginning but did not show further alignment over trials. We have clarified its reason and found a way, introducing a slight decay (forgetting), to make further alignment occur (Fig. 8E,F).

(6) We have shown that the value-RNNs could learn the tasks with longer cue-reward delay (Fig. 2M,6J) or action selection (Fig. 11), and found cases where random feedback performed worse than symmetric feedback.

(7) We compared our value-RNNs with e-prop (Bellec et al., 2020, Nat Commun). While e-prop incorporates the effects of changes in RNN weights across distant times through "eligibility trace", our value-RNNs do not. The reason why our models can still learn the tasks with cue-reward delay is considered to be because our models use TD error and TD learning itself, even TD(0) without eligibility trace, is a solution for temporal credit assignment. In fact, TD error-based e-prop was also examined, but for that, result with symmetric feedback, but not with random feedback, was shown (their Fig. 4,5) while for another setup of reward-based e-prop without TD error, result with random feedback was shown (their SuppFig. 5). We have noted these in Line 695-711 (and also partly in Line 96-99).

(8) In the original manuscript, we emphasized only the spatial locality (random rather than symmetric feedback) of our learning rule. But we have now also emphasized the temporal locality (online learning) as it is also crucial for bio-plausibility and critically different from the original value-RNN with BPTT. We also changed the title.

(9) We have realized that our estimation of true state values was invalid (as detailed in page 34 of this document). Effects of this error on performance comparisons were small, but we apologize for this error.

Reviewer #1 (Public review):

Summary:

Can a plastic RNN serve as a basis function for learning to estimate value. In previous work this was shown to be the case, with a similar architecture to that proposed here. The learning rule in previous work was back-prop with an objective function that was the TD error function (delta) squared. Such a learning rule is non-local as the changes in weights within the RNN, and from inputs to the RNN depends on the weights from the RNN to the output, which estimates value. This is non-local, and in addition, these weights themselves change over learning. The main idea in this paper is to examine if replacing the values of these non-local changing weights, used for credit assignment, with random fixed weights can still produce similar results to those obtained with complete bp. This random feedback approach is motivated by a similar approach used for deep feed-forward neural networks.

This work shows that this random feedback in credit assignment performs well but is not as well as the precise gradient-based approach. When more constraints due to biological plausibility are imposed performance degrades. These results are not surprising given previous results on random feedback. This work is incomplete because the delay times used were only a few time steps, and it is not clear how well random feedback would operate with longer delays. Additionally, the examples simulated with a single cue and a single reward are overly simplistic and the field should move beyond these exceptionally simple examples.

Strengths:

• The authors show that random feedback can approximate well a model trained with detailed credit assignment.

• The authors simulate several experiments including some with probabilistic reward schedules and show results similar to those obtained with detailed credit assignments as well as in experiments.

• The paper examines the impact of more biologically realistic learning rules and the results are still quite similar to the detailed back-prop model.

Weaknesses:

*please note that we numbered your public review comments and recommendations for the authors as Pub1 and Rec1 etc so that we can refer to them in our replies to other comments.

Pub1. The authors also show that an untrained RNN does not perform as well as the trained RNN. However, they never explain what they mean by an untrained RNN. It should be clearly explained.

These results are actually surprising. An untrained RNN with enough units and sufficiently large variance of recurrent weights can have a high-dimensionality and generate a complete or nearly complete basis, though not orthonormal (e.g: Rajan&Abbott 2006). It should be possible to use such a basis to learn this simple classical conditioning paradigm. It would be useful to measure the dimensionality of network dynamics, in both trained and untrained RNN's.

We have added an explanation of untrained RNN in Line 144-147:

“As a negative control, we also conducted simulations in which these connections were not updated from initial values, referring to as the case with "untrained (fixed) RNN". Notably, the value weights w (i.e., connection weights from the RNN to the striatal value unit) were still trained in the models with untrained RNN.”

We have also analyzed the dimensionality of network dynamic by calculating the contribution ratios of each principal component of the trajectory of RNN activities. It was revealed that the contribution ratios of later principal components were smaller in the cases with untrained RNN than in the cases with trained value RNN. We have added these results in Fig. 2K and Line 210-220 (for our original models without non-negative constraint):

“In order to examine the dimensionality of RNN dynamics, we conducted principal component analysis (PCA) of the time series (for 1000 trials) of RNN activities and calculated the contribution ratios of PCs in the cases of oVRNNbp, oVRNNrf, and untrained RNN with 20 RNN units. Figure 2K shows a log of contribution ratios of 20 PCs in each case. Compared with the case of untrained RNN, in oVRNNbp and oVRNNrf, initial component(s) had smaller contributions (PC1 (t-test p = 0.00018 in oVRNNbp; p = 0.0058 in oVRNNrf) and PC2 (p = 0.080 in oVRNNbp; p = 0.0026 in oVRNNrf)) while later components had larger contributions (PC3~10,15~20 p < 0.041 in oVRNNbp; PC5~20 p < 0.0017 in oVRNNrf) on average, and this is considered to underlie their superior learning performance. We noticed that late components had larger contributions in oVRNNrf than in oVRNNbp, although these two models with 20 RNN units were comparable in terms of cue~reward state values (Fig. 2J-left).”

and Fig. 6H and Line 412-416 (for our extended models with non-negative constraint):

“Figure 6H shows contribution ratios of PCs of the time series of RNN activities in each model with 20 RNN units. Compared with the cases with naive/shuffled untrained RNN, in oVRNNbp-rev and oVRNNrf-bio, later components had relatively high contributions (PC5~20 p < 1.4×10,sup>−6</sup> (t-test vs naive) or < 0.014 (vs shuffled) in oVRNNbp-rev; PC6~20 p < 2.0×10⁻⁷ (vs naive) or PC7~20 p < 5.9×10⁻¹⁴ (vs shuffled) in oVRNNrf-bio), explaining their superior value-learning performance.”

Regarding the poor performance of the model with untrained RNN, we would like to add a note. It is sure that untrained RNN with sufficient dimensions should be able to well represent just <10 different states, and state values should be able to be well learned through TD learning regardless of whatever representation is used. However, a difficulty (nontriviality) lies in that because we modeled the tasks in a continuous way, rather than in an episodic way, the activity of untrained RNN upon cue presentation should generally differ from trial to trial. Therefore, it was not trivial for RNN to know that cue presentation in different trials, even after random lengths of inter-trial interval, should constitute a same single state. We have added this note in Line 177-185:

“This inferiority of untrained RNN may sound odd because there were only four states from cue to reward while random RNN with enough units is expected to be able to represent many different states (c.f., [49]) and the effectiveness of training of only the readout weights has been shown in reservoir computing studies [50-53]. However, there was a difficulty stemming from the continuous training across trials (rather than episodic training of separate trials): the activity of untrained RNN upon cue presentation generally differed from trial to trial, and so it is non-trivial that cue presentation in different trials should be regarded as the same single state, even if it could eventually be dealt with at the readout level if the number of units increases.”

The original value RNN study (Hennig et al., 2023, PLoS Comput Biol) also modeled tasks in a continuous way (though using backprop-through-time (BPTT) for training) and their model with untrained RNN also showed considerably larger RPE error than the value RNN even when the number of RNN units was 100 (the maximum number plotted in their Fig. 6A).

Pub2. The impact of the article is limited by using a network with discrete time-steps, and only a small number of time steps from stimulus to reward. What is the length of each time step? If it's on the order of the membrane time constant, then a few time steps are only tens of ms. In the classical conditioning experiments typical delays are of the order to hundreds of milliseconds to seconds. Authors should test if random feedback weights work as well for larger time spans. This can be done by simply using a much larger number of time steps.

In the revised manuscript, we examined the cases in which the cue-reward delay (originally 3 time steps) was elongated to 4, 5, or 6 time-steps. Our online value RNN models with random feedback could still achieve better performance (smaller squared value error) than the models with untrained RNN, although the performance degraded as the cue-reward delay increased. We have added these results in Fig. 2M and Line 223-228 (for our original models without non-negative constraint)

“We further examined the cases with longer cue-reward delays. As shown in Fig. 2M, as the delay increased, the mean squared error of state values (at 3000-th trial) increased, but the relative superiority of oVRNNbp and oVRNNrf over the model with untrained RNN remained to hold, except for cases with small number of RNN units (5) and long delay (5 or 6) (p < 0.0025 in Wilcoxon rank sum test for oVRNNbp or oVRNNrf vs untrained for each number of RNN units for each delay).”

and Fig. 6J and Line 422-429 (for our extended models with non-negative constraint):

“Figure 6J shows the cases with longer cue-reward delays, with default or halved learning rates. As the delay increased, the mean squared error of state values (at 3000-th trial) increased, but the relative superiority of oVRNNbp-rev and oVRNNrf-bio over the models with untrained RNN remained to hold, except for a few cases with 5 RNN units (5 delay oVRNNrf-bio vs shuffled with default learning rate, 6 delay oVRNNrf-bio vs naive or shuffled with halved learning rate) (p < 0.047 in Wilcoxon rank sum test for oVRNNbp-rev or oVRNNrf-bio vs naive or shuffled untrained for each number of RNN units for each delay).”

Also, we have added the note about our assumption and consideration on the time-step that we described in our provisional reply in Line 136-142:

“We assumed that a single RNN unit corresponds to a small population of neurons that intrinsically share inputs and outputs, for genetic or developmental reasons, and the activity of each unit represents the (relative) firing rate of the population. Cortical population activity is suggested to be sustained not only by fast synaptic transmission and spiking but also, even predominantly, by slower synaptic neurochemical dynamics [46] such as short-term facilitation, whose time constant can be around 500 milliseconds [47]. Therefore, we assumed that single time-step of our rate-based (rather than spike-based) model corresponds to 500 milliseconds.”

Pub3. In the section with more biologically constrained learning rules, while the output weights are restricted to only be positive (as well as the random feedback weights), the recurrent weights and weights from input to RNN are still bi-polar and can change signs during learning. Why is the constraint imposed only on the output weights? It seems reasonable that the whole setup will fail if the recurrent weights were only positive as in such a case most neurons will have very similar dynamics, and the network dimensionality would be very low. However, it is possible that only negative weights might work. It is unclear to me how to justify that bipolar weights that change sign are appropriate for the recurrent connections and inappropriate for the output connections. On the other hand, an RNN with excitatory and inhibitory neurons in which weight signs do not change could possibly work.

We examined extended models that incorporated inhibitory and excitatory units and followed Dale's law with certain assumptions, and found that these models could still learn the tasks. We have added these results in Fig. 9 and subsection “4.1 Models with excitatory and inhibitory units” and described the details of the extended models in Line 844-862:

Pub4. Like most papers in the field this work assumes a world composed of a single cue. In the real world there many more cues than rewards, some cues are not associated with any rewards, and some are associated with other rewards or even punishments. In the simplest case, it would be useful to show that this network could actually work if there are additional distractor cues that appear at random either before the CS, or between the CS and US. There are good reasons to believe such distractor cues will be fatal for an untrained RNN, but might work with a trained RNN, either using BPPT or random feedback. Although this assumption is a common flaw in most work in the field, we should no longer ignore these slightly more realistic scenarios.

We examined the performance of the models in a task in which distractor cue randomly appeared. As a result, our model with random feedback, as well as the model with backprop, could still learn the state values much better than the models with untrained RNN. We have added these results in Fig. 10 and subsection “4.2 Task with distractor cue”

Reviewer #1 (Recommendations for the authors):

Detailed comments to authors

Rec1. Are the untrained RNNs discussed in methods? It seems quite good in estimating value but has a strong dopamine response at time of reward. Is nothing trained in the untrained RNN or are the W values trained. Untrained RNN are not bad at estimating value, but not as good as the two other options. It would seem reasonable that an untrained RNN (if I understand what it is) will be sufficient for such simple Pavlovian conditioning paradigms. This is provided that the RNN generates a complete, or nearly complete basis. Random RNN's provided that the random weights are chosen properly can indeed generate a nearly complete basis. Once there is a nearly complete temporal basis, it seems that a powerful enough learning rule will be able to learn the very simple Pavlovian conditioning. Since there are only 3 time-steps from cue to reward, an RNN dimensionality of 3 would be sufficient. A failure to get a good approximation can also arise from the failure of the learning algorithm for the output weights (W).

As we mentioned in our reply to your public comment Pub1 (page 3-5), we have added an explanation of "untrained RNN" (in which the value weights were still learnt) (Line 144-147). We also analyzed the dimensionality of network dynamics by calculating the contribution ratios of principal components of the trajectory of RNN activities, showing that the contribution ratios of later principal components were smaller in the cases with untrained RNN than in the cases with trained value RNN (Fig. 2K/Line 210-220, Fig.6H/Line 412-416). Moreover, also as we mentioned in our reply to your public comment Pub1, we have added a note that even learning of a small number of states was not trivially easy because we considered continuous learning across trials rather than episodic learning of separate trials and thus it was not trivial for the model to know that cue presentation in different trials after random lengths of inter-trial interval should still be regarded as a same single state (Line 177-185).

Rec2. For all cases, it will be useful to estimate the dimensionality of the RNN. Is the dimensionality of the untrained RNN smaller than in the trained cases? If this is the case, this might depend on the choice of the initial random (I assume) recurrent connectivity matrix.

As mentioned above, we have analyzed the dimensionality of the network dynamics, and as you said, the dimensionality of the model with untrained RNN (which was indeed the initial random matrix as you said, as we mentioned above) was on average smaller than the trained value RNN models (Fig. 2K/Line 210-220, Fig.6H/Line 412-416).

Rec3. It is surprising that the error starts increasing for more RNN units above ~15. See discussion. This might indicate a failure to adjust the learning parameters of the network rather than a true and interesting finding.

Thank you very much for this insightful comment. In the original manuscript, we set the learning rate to a fixed value (0.1), without normalization by the squared norm of feature vector (as we mentioned in Line 656-7 of the original manuscript) because we thought such a normalization could not be locally (biologically) implemented. However, we have realized that the lack of normalization resulted in excessively large learning rate when the number of RNN units was large and it could cause instability and error increase as you suggested. Therefore, in the revised manuscript, we have implemented a normalization of learning rate (of value weights) that does not require non-local computations, specifically, division by the number of RNN units. As a result, the error now monotonically decreased, as the number of RNN units increased, in the non-negatively constrained models (Fig. 6E-left) and also largely in the unconstrained model with random feedback, although still not in the unconstrained model with backprop or untrained RNN (Fig. 2J-left)

Rec4. Not numbering equations is a problem. For example, the explanations of feedback alignment (lines 194-206) rely on equations in the methods section which are not numbered. This makes it hard to read these explanations. Indeed, it will also be better to include a detailed derivation of the explanation in these lines in a mathematical appendix. Key equations should be numbered.

We have added numbers to key equations in the Methods, and references to the numbers of corresponding equations in the main text. Detailed derivations are included in the Methods.

Rec5. What is shown in Figure 3C? - an equation will help.

We have added an explanation using equations in the main text (Line 256-259).

Rec6. The explanation of why alignment occurs is not satisfactory, but neither is it in previous work on feedforward networks. The least that should be done though

Regarding why alignment occurs, what remained mysterious (to us) was that in the case of nonnegatively constrained model, while the angle between value weight vector (w) and the random feedback vector (c) was relatively close (loosely aligned) from the beginning, it appeared (as mentioned in the manuscript) that there was no further alignment over trials, despite that the same mechanism for feedback alignment that we derived for the model without non-negative constraint was expected to operate also under the non-negative constraint. We have now clarified the reason for this, and found a way, introduction of slight decay (forgetting) of value weights, by which feedback alignment came to occur in the non-negatively constraint model. We have added these in the revised manuscript (Line 463-477):

“As mentioned above, while the angle between w and c was on average smaller than 90° from the beginning, there was no further alignment over trials. This seemed mysterious because the mechanism for feedback alignment that we derived for the models without non-negative constraint was expected to work also for the models with non-negative constraint. As a possible reason for the non-occurrence of feedback alignment, we guessed that one or a few element(s) of w grew prominently during learning, and so w became close to an edge or boundary of the non-negative quadrant and thereby angle between w and other vector became generally large (as illustrated in Fig. 8D). Figure 8Ea shows the mean±SEM of the elements of w ordered from the largest to smallest ones after 1500 trials. As conjectured above, a few elements indeed grew prominently.

We considered that if a slight decay (forgetting) of value weights (c.f., [59-61]) was assumed, such a prominent growth of a few elements of w may be mitigated and alignment of w to c, beyond the initial loose alignment because of the non-negative constraint, may occur. These conjectures were indeed confirmed by simulations (Fig. 8Eb,c and Fig. 8F). The mean squared value error slightly increased when the value-weightdecay was assumed (Fig. 8G), however, presumably reflecting a decrease in developed values and a deterioration of learning because of the decay.”

Rec7. I don't understand the qualitative difference between 4G and 4H. The difference seems to be smaller but there is still an apparent difference. Can this be quantified?

We have added pointers indicating which were compared and statistical significance on Fig. 4D-H, and also Fig. 7 and Fig. 9C.

Rec8. More biologically realistic constraints.

Are the weights allowed to become negative? - No.

Figure 6C - untrained RNN with non-negative x_i. Again - it was not explained what untrained RNN is. However, given my previous assumption, this is probably because the units developed in an untrained RNN is much further from representing a complete basis function. This cannot be done with only positive values. It would be useful to see network dynamics of units for untrained RNN. It might also be useful in all cases to estimate the dimensionality of the RNN. For 3 time-steps, it needs to be at least 3, and for more time steps as in Figure 4, larger.

As we mentioned in our reply to your public comment Pub3 (page 6-8), in the revised manuscript we examined models that incorporated inhibitory and excitatory units and followed Dale's law, which could still learn the tasks (Fig. 9, Line 479-520). We have also analyzed the dimensionality of network dynamics as we mentioned in our replies to your public comment Pub1 and recommendations Rec1 and Rec2.

Rec9. A new type of untrained RNN is introduced (Fig 6D) this is the first time an explanation of of the untrained RNN is given. Indeed, the dimensionality of the second type of untrained RNN should be similar to the bioVRNNrf. The results are still not good.

In the model with the new type of untrained RNN whose elements were shuffled from trained bioVRNNrf, contribution ratios of later principal components of the trajectory of RNN activities (Fig. 6H gray dotted line) were indeed larger than those in the model with native untrained RNN (gray solid line) but still much smaller than those in the trained value RNN models with backprop (red line) or random feedback (blue line). It is considered that in value RNN, RNN connections were trained to realize high-dimensional trajectory, and shuffling did not generally preserve such an ability.

Rec10. The discussion is too long and verbose. This is not a review paper.

We have made the original discussion much more compact (from 1686 words to 940 words). We have added new discussion, in response to the review comments, but the total length remains to be shorter than before (1589 words).

Reviewer #2 (Public review):

Summary:

Tsurumi et al. show that recurrent neural networks can learn state and value representations in simple reinforcement learning tasks when trained with random feedback weights. The traditional method of learning for recurrent network in such tasks (backpropagation through time) requires feedback weights which are a transposed copy of the feed-forward weights, a biologically implausible assumption. This manuscript builds on previous work regarding "random feedback alignment" and "value-RNNs", and extends them to a reinforcement learning context. The authors also demonstrate that certain nonnegative constraints can enforce a "loose alignment" of feedback weights. The author's results suggest that random feedback may be a powerful tool of learning in biological networks, even in reinforcement learning tasks.

Strengths:

The authors describe well the issues regarding biologically plausible learning in recurrent networks and in reinforcement learning tasks. They take care to propose networks which might be implemented in biological systems and compare their proposed learning rules to those already existing in literature. Further, they use small networks on relatively simple tasks, which allows for easier intuition into the learning dynamics.

Weaknesses:

The principles discovered by the authors in these smaller networks are not applied to deeper networks or more complicated tasks, so it remains unclear to what degree these methods can scale up, or can be used more generally.

We have examined extended models that incorporated inhibitory and excitatory units and followed Dale's law with certain assumptions, and found that these models could still learn the tasks. We have added these results in Fig. 9 and subsection “4.1 Models with excitatory and inhibitory units”.

We have also examined the performance of the models in a task in which distractor cue randomly appeared, finding that our models could still learn the state values much better than the models with untrained RNN. We have added these result in Fig. 10 and subsection “4.2 Task with distractor cue”.

Regarding the depth, we continue to think about it but have not yet come up with concrete ideas.

Reviewer #2 (Recommendations for the authors):

(1) I think the work would greatly benefit from more proofreading. There are language errors/oddities throughout the paper, I will list just a few examples from the introduction:

Thank you for pointing this out. We have made revisions throughout the paper.

line 63: "simultaneously learnt in the downstream of RNN". Simultaneously learnt in networks downstream of the RNN? Simulatenously learn in a downstream RNN? The meaning is not clear in the original sentence.

We have revised it to "simultaneously learnt in connections downstream of the RNN" (Line 67-68).

starting in line 65: " A major problem, among others.... value-encoding unit" is a run-on sentence and would more readable if split into multiple sentences.

We have extensively revised this part, which now consists of short sentences (Line 70-75).

line 77: "in supervised learning of feed-forward network" should be either "in supervised learning of a feed-forward network" or "in supervised learning of feed-forward networks".

We have changed "feed-forward network" to "feed-forward networks" (Line 83).

(2) Under what conditions can you use an online learning rule which only considers the influence of the previous timestep? It's not clear to me how your networks solve the temporal credit assignment problem when the cue-reward delay in your tasks is 3-5ish time steps. How far can you stretch this delay before your networks stop learning correctly because of this one-step assumption? Further, how much does feedback alignment constrain your ability to learn long timescales, such as in Murray, J.M. (2019)?

The reason why our models can solve the temporal credit assignment problem at least to a certain extent is considered to be because temporal-difference (TD) learning, which we adopted, itself has a power to resolve temporal credit assignment, as exemplified in that TD(0) algorithms without eligibility trance can still learn the value of distant rewards. We have added a discussion on this in Line 702-705:

“…our models do not have "eligibility trace" (nor memorable/gated unit, different from the original value-RNN [26]), but could still solve temporal credit assignment to a certain extent because TD learning is by itself a solution for it (notably, recent work showed that combination of TD(0) and model-based RL well explained rat's choice and DA patterns [132]).”

We have also examined the cases in which the cue-reward delay (originally 3 time steps) was elongated to 4, 5, or 6 time-steps, and our models with random feedback could still achieve better performance than the models with untrained RNN although the performance degraded as the cue-reward delay increased. We have added these results in Fig. 2M and Line 223-228 (for our original models without non-negative constraint)

“We further examined the cases with longer cue-reward delays. As shown in Fig. 2M, as the delay increased, the mean squared error of state values (at 3000-th trial) increased, but the relative superiority of oVRNNbp and oVRNNrf over the model with untrained RNN remained to hold, except for cases with small number of RNN units (5) and long delay (5 or 6) (p < 0.0025 in Wilcoxon rank sum test for oVRNNbp or oVRNNrf vs untrained for each number of RNN units for each delay).”

and Fig. 6J and Line 422-429 (for our extended models with non-negative constraint):

“Figure 6J shows the cases with longer cue-reward delays, with default or halved learning rates. As the delay increased, the mean squared error of state values (at 3000-th trial) increased, but the relative superiority of oVRNNbp-rev and oVRNNrf-bio over the models with untrained RNN remained to hold, except for a few cases with 5 RNN units (5 delay oVRNNrf-bio vs shuffled with default learning rate, 6 delay oVRNNrf-bio vs naive or shuffled with halved learning rate) (p < 0.047 in Wilcoxon rank sum test for oVRNNbp-rev or oVRNNrf-bio vs naive or shuffled untrained for each number of RNN units for each delay).”

As for the difficulty due to random feedback compared to backprop, there appeared to be little difference in the models without non-negative constraint (Fig. 2M), whereas in the models with nonnegative constraint, when the cue-reward delay was elongated to 6 time-steps, the model with random feedback performed worse than the model with backprop (Fig. 6J bottom-left panel).

(3) Line 150: Were the RNN methods trained with continuation between trials?

Yes, we have added

“The oVRNN models, and the model with untrained RNN, were continuously trained across trials in each task, because we considered that it was ecologically more plausible than episodic training of separate trials.” in Line 147-150. This is considered to make learning of even the simple cue-reward association task nontrivial, as we describe in our reply to your comment 9 below.

(4) Figure 2I, J: indicate the statistical significance of the difference between the three methods for each of these measures.

We have added statistical information for Fig. 2J (Line 198-203):

“As shown in the left panel of Fig. 2J, on average across simulations, oVRNNbp and oVRNNrf exhibited largely comparable performance and always outperformed the untrained RNN (p < 0.00022 in Wilcoxon rank sum test for oVRNNbp or oVRNNrf vs untrained for each number of RNN units), although oVRNNbp somewhat outperformed or underperformed oVRNNrf when the number of RNN units was small (≤10 (p < 0.049)) or large (≥25 (p < 0.045)), respectively.”

and also Fig. 6E (for non-negative models) (Line 385-390):

“As shown in the left panel of Fig. 6E, oVRNNbp-rev and oVRNNrf-bio exhibited largely comparable performance and always outperformed the models with untrained RNN (p < 2.5×10⁻¹² in Wilcoxon rank sum test for oVRNNbp-rev or oVRNNrf-bio vs naive or shuffled untrained for each number of RNN units), although oVRNNbp-rev somewhat outperformed or underperformed oVRNNrf-bio when the number of RNN units was small (≤10 (p < 0.00029)) or large (≥25 (p < 3.7×10⁻⁶)), respectively…”

Fig. 2I shows distributions, whose means are plotted in Fig. 2J, and we did not add statistics to Fig. 2I itself.

(5) Line 178: Has learning reached a steady state after 1000 trials for each of these networks? Can you show a plot of error vs. trial number?

We have added a plot of error vs trial number for original models (Fig. 2L, Line 221-223):

“We examined how learning proceeded across trials in the models with 20 RNN units. As shown in Fig. 2L, learning became largely converged by 1000-th trial, although slight improvement continued afterward.”

and non-negatively constrained models (Fig. 6I, Line 417-422):

“Figure 6I shows how learning proceeded across trials in the models with 20 RNN units. While oVRNNbp-rev and oVRNNrf-bio eventually reached a comparable level of errors, oVRNNrf-bio outperformed oVRNNbp-rev in early trials (at 200, 300, 400, or 500 trials; p < 0.049 in Wilcoxon rank sum test for each). This is presumably because the value weights did not develop well in early trials and so the backprop-type feedback, which was the same as the value weights, did not work well, while the non-negative fixed random feedback worked finely from the beginning.”

As shown in these figures, learning became largely steady at 1000 trials, but still slightly continued, and we have added simulations with 3000 trials (Fig. 2M and Fig. 6J).

(6) Line 191: Put these regression values in the figure caption, as well as on the plot in Figure 3B.

We have added the regression values in Fig. 3B and its caption.

(7) Line 199: This idea of being in the same quadrant is interesting, but I think the term "relatively close angle" is too vague. Is there another more quantatative way to describe this what you mean by this?

We have revised this (Line 252-254) to “a vector that is in a relatively close angle with c , or more specifically, is in the same quadrant as (and thus within at maximum 90° from) c (for example, [c₁  c₂  c₃]^T and [0.5c₁ 1.2c₂ 0.8c₃]T) “

(8) Line 275: I'd like to see this measure directly in a plot, along with the statistical significance.

We have added pointers indicating which were compared and statistical significance on Fig. 4D-H, and also Fig. 7 and Fig. 9C.

(9) Line 280: Surely the untrained RNN should be able to solve the task if the reservoir is big enough, no? Maybe much bigger than 50 units, but still.

We think this is not sure. A difficulty lies in that because we modeled the tasks in a continuous way rather than in an episodic way (as we mentioned in our reply to your comment 3), the activity of untrained RNN upon cue presentation should generally differ from trial to trial. Therefore, it was not trivial for RNN to know that cue presentation in different trials, even after random lengths of inter-trial interval, should constitute a same single state. We have added this note in Line 177-185:

“This inferiority of untrained RNN may sound odd because there were only four states from cue to reward while random RNN with enough units is expected to be able to represent many different states (c.f., [49]) and the effectiveness of training of only the readout weights has been shown in reservoir computing studies [50-53]. However, there was a difficulty stemming from the continuous training across trials (rather than episodic training of separate trials): the activity of untrained RNN upon cue presentation generally differed from trial to trial, and so it is non-trivial that cue presentation in different trials should be regarded as the same single state, even if it could eventually be dealt with at the readout level if the number of units increases.”

The original value RNN study (Hennig et al., 2023, PLoS Comput Biol) also modeled tasks in a continuous way (though using BPTT for training) and their model with untrained RNN also showed considerably larger RPE error than the value RNN even when the number of RNN units was 100 (the maximum number plotted in their Fig. 6A).

(10) It's a bit confusing to compare Figure 4C to Figure 4D-H because there are also many features of D-H which do not match those of C (response to cue, response to late reward in task 1). It would make sense to address this in some way. Is there another way to calculate the true values of the states (e.g., maybe you only start from the time of the cue) which better approximates what the networks are doing?

As we mentioned in our replies to your comments 3 and 9, our models with RNN were trained continuously across trials rather than separately for each episodic trial, and whether the models could still learn the state representation is a key issue. Therefore, starting learning from the time of cue would not be an appropriate way to compare the models, and instead we have made statistical comparison regarding key features, specifically, TD-RPEs at early and late rewards, as indicated in Fig. 4D-H.

(11) Line 309: Can you explain why this non-monotic feature exists? Why do you believe it would be more biologically plausible to assume monotonic dependence? It doesn't seem so straightforward to me, I can imagine that competing LTP/LTD mechanisms may produce plasticity which would have a non-monotic dependence on post-synaptic activity.

Thank you for this insightful comment. As you suggested, non-monotonic dependence on the postsynaptic activity (BCM rule) has been proposed for unsupervised learning (cortical self-organization) (Bienenstock et al., 1982 J Neurosci), and there were suggestions that triplet-based STDP could be reduced to a BCM-like rule and additional components (Gjorgjieva et al., 2011 PNAS; Shouval, 2011 PNAS). However, the non-monotonicity appeared in our model, derived from the backprop rule, is maximized at the middle and thus opposite from the BCM rule, which is minimized at the middle (i.e., initially decrease and thereafter increase). Therefore we consider that such an increase-then-decreasetype non-monotonicity would be less plausible than a monotonic increase, which could approximate an extreme case (with a minimum dip) of the BCM rule. We have added a note on this point in Line 355-358:

“…the dependence on the post-synaptic activity was non-monotonic, maximized at the middle of the range of activity. It would be more biologically plausible to assume a monotonic increase (while an opposite shape of nonmonotonicity, once decrease and thereafter increase, called the BCM (Bienenstock-Cooper-Munro) rule has actually been suggested [56-58]).”

(12) Line 363: This is the most exciting part of the paper (for me). I want to learn way more about this! Don't hide this in a few sentences. I want to know all about loose vs. feedback alignment. Show visualizations in 3D space of the idea of loose alignment (starting in the same quadrant), and compare it to how feedback alignment develops (ending in the same quadrant). Does this "loose" alignment idea give us an idea why the random feedback seems to settle at 45 degree angle? it just needs to get the signs right (same quadrant) for each element?

In reply to this encouraging comment, we have made further analyses of the loose alignment. By the term "loose alignment", we meant that the value weight vector w and the feedback vector c are in the same (non-negative) quadrant, as you said. But what remained mysterious (to us) was while the angle between w and c was relatively close (loosely aligned) from the beginning, it appeared (as mentioned in the manuscript) that there was no further alignment over trials (and the angle actually settled at somewhat larger than 45°), despite that the same mechanism for feedback alignment that we derived for the model without non-negative constraint was expected to operate also under the nonnegative constraint. We have now clarified the reason for this, and found a way, introduction of slight decay (forgetting) of value weights, by which feedback alignment came to occur in the non-negatively constraint model. We have added this in Line 463-477:

“As mentioned above, while the angle between w and c was on average smaller than 90° from the beginning, there was no further alignment over trials. This seemed mysterious because the mechanism for feedback alignment that we derived for the models without non-negative constraint was expected to work also for the models with non-negative constraint. As a possible reason for the non-occurrence of feedback alignment, we guessed that one or a few element(s) of w grew prominently during learning, and so w became close to an edge or boundary of the non-negative quadrant and thereby angle between w and other vector became generally large (as illustrated in Fig. 8D). Figure 8Ea shows the mean±SEM of the elements of w ordered from the largest to smallest ones after 1500 trials. As conjectured above, a few elements indeed grew prominently.

We considered that if a slight decay (forgetting) of value weights (c.f., [59-61]) was assumed, such a prominent growth of a few elements of w may be mitigated and alignment of w to c, beyond the initial loose alignment because of the non-negative constraint, may occur. These conjectures were indeed confirmed by simulations (Fig. 8Eb,c and Fig. 8F). The mean squared value error slightly increased when the value-weightdecay was assumed (Fig. 8G), however, presumably reflecting a decrease in developed values and a deterioration of learning because of the decay.”

As for visualization, because the model's dimension was high such as 12, we could not come up with better ways of visualization than the trial versus angle plot (Fig. 3A, 8A,F). Nevertheless, we would expect that the abovementioned additional analyses of loose alignment (with graphs) are useful to understand what are going on.

(13) Line 426: how does this compare to some of the reward modulated hebbian rules proposed in other RNNs? See Hoerzer, G. M., Legenstein, R., & Maass, W. (2014). Put another way, you arrived at this from a top-down approach (gradient descent->BP->approximated by RF->non-negativity constraint>leads to DA dependent modulation of Hebbian plasticity). How might this compare to a bottom up approach (i.e. starting from the principle of Hebbian learning, and adding in reward modulation)

The study of Hoerzer et al. 2014 used a stochastic perturbation, which we did not assume but can potentially be integrated. On the other hand, Hoerzer et al. trained the readout of untrained RNN, whereas we trained both RNN and its readout. We have added discussion to compare our model with Hoerzer et al. and other works that also used perturbation methods, as well as other top-down approximation method, in Line 685-711 (reference 128 is Hoerzer et al. 2014 Cereb Cortex):

“As an alternative to backprop in hierarchical network, aside from feedback alignment [36], Associative Reward-Penalty (A_R-P) algorithm has been proposed [124-126]. In A_R-P, the hidden units behave stochastically, allowing the gradient to be estimated via stochastic sampling. Recent work [127] has proposed Phaseless Alignment Learning (PAL), in which high-frequency noise-induced learning of feedback projections proceeds simultaneously with learning of forward projections using the feedback in a lower frequency. Noise-induced learning of the weights on readout neurons from untrained RNN by reward-modulated Hebbian plasticity has also been demonstrated [128]. Such noise- or perturbation-based [40] mechanisms are biologically plausible because neurons and neural networks can exhibit noisy or chaotic behavior [129-131], and might improve the performance of value-RNN if implemented.

Regarding learning of RNN, "e-prop" [35] was proposed as a locally learnable online approximation of BPTT [27], which was used in the original value RNN 26. In e-prop, neuron-specific learning signal is combined with weight-specific locally-updatable "eligibility trace". Reward-based e-prop was also shown to work [35], both in a setup not introducing TD-RPE with symmetric or random feedback (their Supplementary Figure 5) and in another setup introducing TD-RPE with symmetric feedback (their Figure 4 and 5). Compared to these, our models differ in multiple ways.

First, we have shown that alignment to random feedback occurs in the models driven by TD-RPE. Second, our models do not have "eligibility trace" (nor memorable/gated unit, different from the original valueRNN [26]), but could still solve temporal credit assignment to a certain extent because TD learning is by itself a solution for it (notably, recent work showed that combination of TD(0) and model-based RL well explained rat's choice and DA patterns [132]). However, as mentioned before, single time-step in our models was assumed to correspond to hundreds of milliseconds, incorporating slow synaptic dynamics, whereas e-prop is an algorithm for spiking neuron models with a much finer time scale. From this aspect, our models could be seen as a coarsetime-scale approximation of e-prop. On top of these, our results point to a potential computational benefit of biological non-negative constraint, which could effectively limit the parameter space and promote learning.”

Related to your latter point (and also replying to other reviewer's comment), we also examined the cases where the random feedback in our model was replaced with uniform feedback, which corresponds to a simple bottom-up reward-modulated triplet plasticity rule. As a result, the model with uniform feedback showed largely comparable, but somewhat worse, performance than the model with random feedback. We have added the results in Fig. 2J-right and Line 206-209 (for our original models without non-negative constraint):

“The green line in Fig. 2J-right shows the performance of a special case where the random feedback in oVRNNrf was fixed to the direction of (1, 1, ..., 1)^T (i.e., uniform feedback) with a random coefficient, which was largely comparable to, but somewhat worse than, that for the general oVRNNrf (blue line).”

and Fig. 6E-right and Line 402-407 (for our extended models with non-negative constraint):

“The green and light blue lines in the right panels of Figure 6E and Figure 6F show the results for special cases where the random feedback in oVRNNrf-bio was fixed to the direction of (1, 1, ..., 1) ^T (i.e., uniform feedback) with a random non-negative magnitude (green line) or a fixed magnitude of 0.5 (light blue line). The performance of these special cases, especially the former (with random magnitude) was somewhat worse than that of oVRNNrf-bio, but still better than that of the models with untrained RNN. and also added a biological implication of the results in Line 644-652:

We have shown that oVRNNrf and oVRNNrf-bio could work even when the random feedback was uniform, i.e., fixed to the direction of (1, 1, ..., 1) ^T, although the performance was somewhat worse. This is reasonable because uniform feedback can still encode scalar TD-RPE that drives our models, in contrast to a previous study [45], which considered DA's encoding of vector error and thus regarded uniform feedback as a negative control. If oVRNNrf/oVRNNrf-bio-like mechanism indeed operates in the brain and the feedback is near uniform, alignment of the value weights w to near (1, 1, ..., 1) is expected to occur. This means that states are (learned to be) represented in such a way that simple summation of cortical neuronal activity approximates value, thereby potentially explaining why value is often correlated with regional activation (fMRI BOLD signal) of cortical regions [113].”

Reviewer #3 (Public review):

Summary:

The paper studies learning rules in a simple sigmoidal recurrent neural network setting. The recurrent network has a single layer of 10 to 40 units. It is first confirmed that feedback alignment (FA) can learn a value function in this setting. Then so-called bio-plausible constraints are added: (1) when value weights (readout) is non-negative, (2) when the activity is non-negative (normal sigmoid rather than downscaled between -0.5 and 0.5), (3) when the feedback weights are non-negative, (4) when the learning rule is revised to be monotic: the weights are not downregulated. In the simple task considered all four biological features do not appear to impair totally the learning.

Strengths:

(1) The learning rules are implemented in a low-level fashion of the form: (pre-synaptic-activity) x (post-synaptic-activity) x feedback x RPE. Which is therefore interpretable in terms of measurable quantities in the wet-lab.

(2) I find that non-negative FA (FA with non negative c and w) is the most valuable theoretical insight of this paper: I understand why the alignment between w and c is automatically better at initialization.

(3) The task choice is relevant since it connects with experimental settings of reward conditioning with possible plasticity measurements.

Weaknesses:

(4) The task is rather easy, so it's not clear that it really captures the computational gap that exists with FA (gradient-like learning) and simpler learning rule like a delta rule: RPE x (pre-synpatic) x (postsynaptic). To control if the task is not too trivial, I suggest adding a control where the vector c is constant c_i=1.

We have examined the cases where the feedback was uniform, i.e., in the direction of (1, 1, ..., 1) in both models without and with non-negative constraint. In both models, the models with uniform feedback performed somewhat worse than the original models with random feedback, but still better than the models with untrained RNN. We have added the results in Fig. 2J-right and Line 206-209 (for our original models without non-negative constraint):

“The green line in Fig. 2J-right shows the performance of a special case where the random feedback in oVRNNrf was fixed to the direction of (1, 1, ..., 1) ^T (i.e., uniform feedback) with a random coefficient, which was largely comparable to, but somewhat worse than, that for the general oVRNNrf (blue line).”

and Fig. 6E-right and Line 402-407 (for our extended models with non-negative constraint):

“The green and light blue lines in the right panels of Figure 6E and Figure 6F show the results for special cases where the random feedback in oVRNNrf-bio was fixed to the direction of (1, 1, ..., 1) ^T (i.e., uniform feedback) with a random non-negative magnitude (green line) or a fixed magnitude of 0.5 (light blue line). The performance of these special cases, especially the former (with random magnitude) was somewhat worse than that of oVRNNrf-bio, but still better than that of the models with untrained RNN.”

We have also added a discussion on the biological implication of the model with uniform feedback mentioned in our provisional reply in Line 644-652:

“We have shown that oVRNNrf and oVRNNrf-bio could work even when the random feedback was uniform, i.e., fixed to the direction of (1, 1, ..., 1) ^T, although the performance was somewhat worse. This is reasonable because uniform feedback can still encode scalar TD-RPE that drives our models, in contrast to a previous study [45], which considered DA's encoding of vector error and thus regarded uniform feedback as a negative control. If oVRNNrf/oVRNNrf-bio-like mechanism indeed operates in the brain and the feedback is near uniform, alignment of the value weights w to near (1, 1, ..., 1) is expected to occur. This means that states are (learned to be) represented in such a way that simple summation of cortical neuronal activity approximates value, thereby potentially explaining why value is often correlated with regional activation (fMRI BOLD signal) of cortical regions [113].”

In addition, while preparing the revised manuscript, we found a recent simulation study, which showed that uniform feedback coupled with positive forward weights was effective in supervised learning of one-dimensional output in feed-forward network (Konishi et al., 2023, Front Neurosci).

We have briefly discussed this work in Line 653-655:

“Notably, uniform feedback coupled with positive forward weights was shown to be effective also in supervised learning of one-dimensional output in feed-forward network [114], and we guess that loose alignment may underlie it.”

(5) Related to point 3), the main strength of this paper is to draw potential connection with experimental data. It would be good to highlight more concretely the prediction of the theory for experimental findings. (Ideally, what should be observed with non-negative FA that is not expected with FA or a delta rule (constant global feedback) ?).

We have added a discussion on the prediction of our models, mentioned in our provisional reply, in Line 627-638:

“oVRNNrf predicts that the feedback vector c and the value-weight vector w become gradually aligned, while oVRNNrf-bio predicts that c and w are loosely aligned from the beginning. Element of c could be measured as the magnitude of pyramidal cell's response to DA stimulation. Element of w corresponding to a given pyramidal cell could be measured, if striatal neuron that receives input from that pyramidal cell can be identified (although technically demanding), as the magnitude of response of the striatal neuron to activation of the pyramidal cell. Then, the abovementioned predictions could be tested by (i) identify cortical, striatal, and VTA regions that are connected, (ii) identify pairs of cortical pyramidal cells and striatal neurons that are connected, (iii) measure the responses of identified pyramidal cells to DA stimulation, as well as the responses of identified striatal neurons to activation of the connected pyramidal cells, and (iv) test whether DA→pyramidal responses and pyramidal→striatal responses are associated across pyramidal cells, and whether such associations develop through learning.”

Moreover, we have considered another (technically more doable) prediction of our model, and described it in Line 639-643:

“Testing this prediction, however, would be technically quite demanding, as mentioned above. An alternative way of testing our model is to manipulate the cortical DA feedback and see if it will cause (re-)alignment of value weights (i.e., cortical striatal strengths). Specifically, our model predicts that if DA projection to a particular cortical locus is silenced, effect of the activity of that locus on the value-encoding striatal activity will become diminished.”

(6a) Random feedback with RNN in RL have been studied in the past, so it is maybe worth giving some insights how the results and the analyzes compare to this previous line of work (for instance in this paper [1]). For instance, I am not very surprised that FA also works for value prediction with TD error. It is also expected from the literature that the RL + RNN + FA setting would scale to tasks that are more complex than the conditioning problem proposed here, so is there a more specific take-home message about non-negative FA? or benefits from this simpler toy task? [1] https://www.nature.com/articles/s41467-020-17236-y

As for a specific feature of non-negative models, we did not describe (actually did not well recognize) an intriguing result that the non-negative random feedback model performed generally better than the models without non-negative constraint with either backprop or random feedback (Fig. 2J-left versus Fig. 6E-left (please mind the difference in the vertical scales)). This suggests that the non-negative constraint effectively limited the parameter space and thereby learning became efficient. We have added this result in Line 392-395:

“Remarkably, oVRNNrf-bio generally achieved better performance than both oVRNNbp and oVRNNrf, which did not have the non-negative constraint (Wilcoxon rank sum test, vs oVRNNbp : p < 7.8×10,sup>−6</sup> for 5 or ≥25 RNN units; vs oVRNNrf: p < 0.021 for ≤10 or ≥20 RNN units).”

Also, in the models with non-negative constraint, the model with random feedback learned more rapidly than the model with backprop although they eventually reached a comparable level of errors, at least in the case with 20 RNN units. This is presumably because the value weights did not develop well in early trials and so the backprop-based feedback, which was the same as the value weights, did not work well, while the non-negative fixed random feedback worked finely from the beginning. We have added this result in Fig. 6I and Line 417-422:

“Figure 6I shows how learning proceeded across trials in the models with 20 RNN units. While oVRNNbp-rev and oVRNNrf-bio eventually reached a comparable level of errors, oVRNNrf-bio outperformed oVRNNbp-rev in early trials (at 200, 300, 400, or 500 trials; p < 0.049 in Wilcoxon rank sum test for each). This is presumably because the value weights did not develop well in early trials and so the backprop-type feedback, which was the same as the value weights, did not work well, while the non-negative fixed random feedback worked finely from the beginning.”

We have also added a discussion on how our model can be positioned in relation to other models including the study you mentioned (e-prop by Bellec, ..., Maass, 2020) in subsection “Comparison to other algorithms” of the Discussion):

Regarding the slightly better performance of the non-negative model with random feedback than that of the non-negative model with backprop when the number of RNN units was large (mentioned in our provisional reply), state values in the backprop model appeared underdeveloped than those in the random feedback model. Slightly better performance of random feedback than backprop held also in our extended model incorporating excitatory and inhibitory units (Fig. 9B).

(6b) Related to task complexity, it is not clear to me if non-negative value and feedback weights would generally scale to harder tasks. If the task in so simple that a global RPE signal is sufficient to learn (see 4 and 5), then it could be good to extend the task to find a substantial gap between: global RPE, non-negative FA, FA, BP. For a well chosen task, I expect to see a performance gap between any pair of these four learning rules. In the context of the present paper, this would be particularly interesting to study the failure mode of non-negative FA and the cases where it does perform as well as FA.

In the cue-reward association task with 3 time-steps delay, the non-negative model with random feedback performed largely comparably to the non-negative model with backprop, and this remained to hold in a task where distractor cue, which was not associated with reward, appeared in random timings. We have added the results in Fig. 10 and subsection “4.2 Task with distractor cue”.

We have also examined the cases where the cue-reward delay was elongated. In the case of longer cue-reward delay (6 time-steps), in the models without non-negative constraint, the model with random feedback performed comparably to (and slightly better than when the number of RNN units was large) the model with backprop (Fig. 2M). In contrast, in the models with non-negative constraint, the model with random feedback underperformed the model with backprop (Fig. 6J, left-bottom). This indicates a difference between the effect of non-negative random feedback and the effect of positive+negative random feedback.

We have further examined the performance of the models in terms of action selection, by extending the models to incorporate an actor-critic algorithm. In a task with inter-temporal choice (i.e., immediate small reward vs delayed large reward), the non-negative model with random feedback performed worse than the non-negative model with backprop when the number of RNN units was small. When the number of RNN increased, these models performed more comparably. These results are described in Fig. 11 and subsection “4.3 Incorporation of action selection”.

(7) I find that the writing could be improved, it mostly feels more technical and difficult than it should. Here are some recommendations:

7a) for instance the technical description of the task (CSC) is not fully described and requires background knowledge from other paper which is not desirable.

7b) Also the rationale for the added difficulty with the stochastic reward and new state is not well explained.

7c) In the technical description of the results I find that the text dives into descriptive comments of the figures but high-level take home messages would be helpful to guide the reader. I got a bit lost, although I feel that there is probably a lot of depth in these paragraphs.

As for 7a), 'CSC (complete serial compound)' was actually not the name of the task but the name of the 'punctate' state representation, in which each state (timing from cue) is represented in a punctate manner, i.e., by a one-hot vector such as (1, 0, ..., 0), (0, 1, ..., 0), ..., and (0, 0, ..., 1). As you pointed out, using the name of 'CSC' would make the text appearing more technical than it actually is, and so we have moved the reference to the name of 'CSC' to the Methods (Line 903-907):

“For the agents with punctate state representation, which is also referred to as the complete serial compound (CSC) representation [1, 48, 133], each timing from a cue in the tasks was represented by a 10-dimensional one-hot vector, starting from (1 0 0 ... 0)^T for the cue state, with the next state (0 1 0 ... 0) ^T and so on.”

and in the Results we have instead added a clearer explanation (Line 163-165):

“First, for comparison, we examined traditional TD-RL agent with punctate state representation (without using the RNN), in which each state (time-step from a cue) was represented in a punctate manner, i.e., by a one-hot vector such as (1, 0, ..., 0), (0, 1, ..., 0), and so on.”

As for 7b), we have added the rationale for our examination of the tasks with probabilistic structures (Line 282-294):

“Previous work [54] examined the response of DA neurons in cue-reward association tasks in which reward timing was probabilistically determined (early in some trials but late in other trials). There were two tasks, which were largely similar but there was a key difference that reward was given in all the trials in one task whereas reward was omitted in some randomly determined trials in another task. Starkweather et al. [54] found that the DA response to later reward was smaller than the response to earlier reward in the former task, presumably reflecting the animal's belief that delayed reward will surely come, but the opposite was the case in the latter task, presumably because the animal suspected that reward was omitted in that trial. Starkweather et al.[54] then showed that such response patterns could be explained if DA encoded TD-RPE under particular state representations that incorporated the probabilistic structures of the task (called the 'belief state'). In that study, such state representations were 'handcrafted' by the authors, but the subsequent work [26] showed that the original value-RNN with backprop (BPTT) could develop similar representations and reproduce the experimentally observed DA patterns.”

As for 7c), we have extensively revised the text of the results, adding high-level explanations while trying to reduce the lengthy low-level descriptions (e.g., Line 172-177 for Fig2E-G).

(8) Related to the writing issue and 5), I wished that "bio-plausibility" was not the only reason to study positive feedback and value weights. Is it possible to develop a bit more specifically what and why this positivity is interesting? Is there an expected finding with non-negative FA both in the model capability? or maybe there is a simpler and crisp take-home message to communicate the experimental predictions to the community would be useful?

There is actually an unexpected finding with non-negative model: the non-negative random feedback model performed generally better than the models without non-negative constraint with either backprop or random feedback (Fig. 2J-left versus Fig. 6E-left), presumably because the nonnegative constraint effectively limited the parameter space and thereby learning became efficient, as we mentioned in our reply to your point 6a above (we did not well recognize this at the time of original submission).

Another potential merit of our present work is the simplicity of the model and the task. This simplicity enabled us to derive an intuitive explanation on why feedback alignment could occur. Such an intuitive explanation was lacking in previous studies while more precise mathematical explanations did exist. Related to the mechanism of feedback alignment, one thing remained mysterious to us at the time of original submission. Specifically, in the non-negatively constraint random feedback model, while the angle between the value weight (w) and the random feedback (c) was relatively close (loosely aligned) from the beginning, it appeared (as mentioned in the manuscript) that there was no further alignment over trials (and the angle actually settled at somewhat larger than 45°), despite that the same mechanism for feedback alignment that we derived for the model without non-negative constraint was expected to operate also under the non-negative constraint. We have now clarified the reason for this, and found a way, introduction of slight decay (forgetting) of value weights, by which feedback alignment came to occur in the non-negatively constraint model. We have added this in Line 463-477:

“As mentioned above, while the angle between w and c was on average smaller than 90° from the beginning, there was no further alignment over trials. This seemed mysterious because the mechanism for feedback alignment that we derived for the models without non-negative constraint was expected to work also for the models with non-negative constraint. As a possible reason for the non-occurrence of feedback alignment, we guessed that one or a few element(s) of w grew prominently during learning, and so w became close to an edge or boundary of the non-negative quadrant and thereby angle between w and other vector became generally large (as illustrated in Fig. 8D). Figure 8Ea shows the mean±SEM of the elements of w ordered from the largest to smallest ones after 1500 trials. As conjectured above, a few elements indeed grew prominently.

We considered that if a slight decay (forgetting) of value weights (c.f., [59-61]) was assumed, such a prominent growth of a few elements of w may be mitigated and alignment of w to c, beyond the initial loose alignment because of the non-negative constraint, may occur. These conjectures were indeed confirmed by simulations (Fig. 8Eb,c and Fig. 8F). The mean squared value error slightly increased when the value-weightdecay was assumed (Fig. 8G), however, presumably reflecting a decrease in developed values and a deterioration of learning because of the decay.”

Correction of an error in the original manuscript

In addition to revising the manuscript according to your comments, we have made a correction on the way of estimating the true state values. Specifically, in the original manuscript, we defined states by relative time-steps from a reward and estimated their values by calculating the sums of discounted future rewards starting from them through simulations. However, we assumed variable inter-trial intervals (ITIs) (4, 5, 6, or 7 time-steps with equal probabilities), and so until receiving cue information, agent should not know when the next reward will come. Therefore, states for the timings up to the cue timing cannot be defined by the upcoming reward, but previously we did so (e.g., state of "one timestep before cue") without taking into account the ITI variability.

We have now corrected this issue, having defined the states of timings with respect to the previous (rather than upcoming) reward. For example, when ITI was 4 time-steps and agent existed in its last time-step, agent will in fact receive a cue at the next time-step, but agent should not know it until actually receiving the cue information and instead should assume that s/he was at the last time-step of ITI (if ITI was 4), last − 1 (if ITI was 5), last − 2 (if ITI was 6), or last − 3 (if ITI was 7) with equal probabilities (in a similar fashion to what we considered when thinking about state definition for the probabilistic tasks). We estimated the true values of states defined in this way through simulations. As a result, the corrected true value of the cue-timing has become slightly smaller than the value described in the original manuscript (reflecting the uncertainty about ITI length), and consequently small positive TD-RPE has now appeared at the cue timing.

Because we measured the performance of the models by squared errors in state values, this correction affected the results reporting the performance. Fortunately, the effects were relatively minor and did not largely alter the results of performance comparisons. However, we sincerely apologize for this error. In the revised manuscript, we have used the corrected true values throughout the manuscript, and we have described the ways of estimating these values in Line 919-976.

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Reply to the reviewers

1. General Statements [optional]

We thank the three reviewers for the time and caution taken to assess our manuscript, and for their constructive feedback that will help improve the study. We herewith provide a revision plan, expecting that the additional experiments and corrections will address the key points raised by the reviewers.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

• *

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

Summary: The manuscript by Delgado et al. reports the role of the actin remodeling Arp2/3 complex in the biology of Langerhans cells, which are specialized innate immune cells of the epidermis. The study is based on a conditional KO mouse model (CD11cCre;Arpc4fl/fl), in which the deletion of the Arp2/3 subunit ArpC4 is under the control of the myeloid cell specific CD11c promoter.

In this model, the assembly of LC networks in the epidermis of ear and tail skin is preserved when examining animals immediately after birth (up to 1 week). Subsequently however LCs from ArpC4-deleted mice start displaying morphological aberrations (reduced elongation and number of branches at 4 weeks of age). Additionally, a profound decline in LC numbers is reported in the skin of both the ear and tail of young adult mice (8-10 weeks).

To explore the cause of such decline, the authors then opt for the complementary in vitro study of bone-marrow derived DCs, given the lack of a model to study LCs in vitro. They report that ArpC4 deletion is associated with aberrantly shaped nuclei, decreased expression of the nucleoskeleton proteins Lamin A/C and B1, nuclear envelop ruptures and increased DNA damage as shown by γH2Ax staining. Importantly, they provide evidence that the defects evoked by ArpC4 deletion also occur in the LCs in situ (immunofluorescence of the skin in 4-week old mice).

Increased DNA damage is further documented by staining differentiating DCs from ArpC4-deleted mice with the 53BP1 marker. In parallel, nuclear levels of DNA repair kinase ATR and recruitment of RPA70 (which recruits ATR to replicative forks) are reduced in the ArpC4-deleted condition. In vitro treatment of DCs with the topoisomerase II inhibitor etoposide and the Arp2/3 inhibitor CK666 induce comparable DNA damage, as well as multilobulated nuclei and DNA bridges. The authors conclude that the ArpC4-KO phenotype might stem, at least in part, from a defective ability to repair DNA damages occurring during cell division.

The study in enriched by an RNA-seq analysis that points to an increased expression of genes linked to IFN signaling, which the authors hypothetically relate to overt activation of innate nucleic acid sensing pathways.

The study ends by an examination of myeloid cell populations in ArpC4-KO mice beyond LCs. Skin cDC2 and cDC2 subsets display skin emigration defects (like LCs), but not numerical defects in the skin (unlike LCs). Myeloid cell subsets of the colon are also present in normal numbers. In the lungs, interstitial and alveolar macrophages are reduced, but not lung DC subsets. Collectively, these observations suggest that ArpC4 is essential for the maintenance of myeloid cell subsets that rely on cell division to colonize or to self-maintain within their tissue of residency (including LCs).

MAJOR COMMENTS

1. ArpC4 and Arp2/3 expression The authors argue that LCs from Arpc4KO mice should delete the Arpc4 gene in precursors that colonize the skin around birth. It would be important to show it to rule out the possibility that the lack of phenotype (initial seeding, initial proliferative burst) in young animals (first week) could be related to an incomplete deletion of ArpC4 expression. Also important would be to show what is happening to the Arp2/3 complex in LCs from Arpc4KO mice.

__Response: __We thank this reviewer for the careful assessment of our manuscript. Regarding this specific comment, we would like to clarify that we do not expect ArpC4 to be deleted in LC precursors, as CD11c is only expressed once the cells have entered the epidermis. Instead, we expect the deletion to take place after birth around day 2-4 (Chorro et al., 2009). For this reason, we performed a deletion PCR of epidermal cells at postnatal day 7 (P7), a time at which the proliferative burst occurs. This analysis revealed CD11c-Cre-driven recombination in the ArpC4 locus (Fig. S2C). This experiment indicates that ArpC4 deletion does not alter LC proliferation and postnatal network formation.

Revision plan: We will revise the manuscript text to more clearly explain when ArpC4 will be deleted during development when using the CD11c-Cre transgene, and better emphasize the rationale for the deletion PCR.

In the in vitro studies with DCs, the level of ArpC4 and Arp2/3 deletion at the protein level is also not documented.

__Response: __We have previously analyzed the expression of ArpC4 in BMDCs in a recent study, confirming its loss in CD11c-Cre;ArpC4fl/fl cells at the protein level: Rivera et al. Immunity 2022; doi: 10.1016/j.immuni.2021.11.008. PMID: 34910930 (Fig. S2D). Therefore, in the current manuscript we only refer to that paper (Results, first paragraph).

The authors explain that surface expression of the CD11c marker, which drives Arpc4 deletion, gradually increased during differentiation of DCs: from 50% to 90% of the cells. Does that mean that loss of ArpC4 expression is only effective in a fraction of the cells examined before day 10 of differentiation (e.g. in the RNA-seq analysis)?

__Response: __The reviewer is correct, there is heterogeneity in CD11c expression, which is inherent of these DC culture model, implying that Arpc4 gene deletion will be partial. However, despite this, we were able to detect significant differences between the transcriptomes of control and CD11c-Cre;ArpC4fl/fl DCs in early phases during differentiation, emphasizing that the phenotype of ArpC4 loss is robust.

Revision Plan: We will include a notion on this heterogeneity in the revised manuscript text.

Intra-nuclear versus extra-nuclear activities of Arp2/3

The authors favor a model whereby intra-nuclear ArpC4 helps maintaining nuclear integrity during proliferation of DCs (and possibly LCs). However, multiple pools of Arp2/3 have been described and accordingly, multiple mechanisms may account for the observed phenotype: i) cytoplasmic pool to drive the protrusions sustaining the assembly of the LC network and its connectivity with keratinocytes ; ii) peri-nuclear pool to protect the nucleus ; iii) Intra-nuclear pool to facilite DNA repair mechanisms e.g. by stabilizing replicative forks (the scenario favored by the authors).

__Response: __The referee is correct, and this is actually discussed in our manuscript (page 11, upper paragraph): we cannot exclude that several pools of branched actin are influencing the phenotype we here describe.

Unfortunately, we have previously tested several antibodies against ArpC4, but in our hands, and despite comprehensive optimization, they did not yield specific signals that would enable us to assess changes in subcellular localization in murine cells. Upon this reviewer's comment, we will now reassess the available tools and found an antibody against ArpC2 (Millipore, Anti-p34-Arc/ARPC2, 07-227-I-100UG) that may work based on published data. We have ordered this product to test it for IF staining of ArpC2, hoping to be able to delineate the subcellular localization of ArpC2 in DCs and potentially LCs.

Revision plan: Upon receipt, we will test the ArpC2 antibody (Millipore, #07-227-I-100UG) both in cultured DCs and in epidermal whole mounts, running various optimization protocols regarding fixation, permeabilization and blocking reagents, next to antibody dilution. That way we hope to be able to detect the subcellular localization of Arp2/3 complex components as requested by this reviewer.

It is recommended that the authors try to gather more supportive data to sustain the intra-nuclear role. Documenting ArpC4 presence in the nucleus would help support the claim. It could be combined with treatments aiming at blocking proliferation in order to reinforce the possibility that a main function of ArpC4 is to protect proliferating cells by favoring DNA repair inside the nucleus.

__Response: __We thank this reviewer for this very helpful comment. As outlined in the previous response, we will aim at obtaining subcellular localization data for Arp2/3 complex components, and along with that study a potential intranuclear localization. Beyond that, in comparison to commonly cultured cell types, however, we face two hurdles addressing the nuclear Arp2/3 role in full: 1) Due to poor transduction rates and epigenetic silencing, we cannot sufficiently express exogenous constructs such as ArpC4-NLS in DCs to assess the subcellular localization of Arp2/3 complex components. 2) We have performed preliminary tests to block proliferation in DCs, using the cyclin D kinase 1 inhibitor RO3306 at different concentrations and incubation times during DC differentiation. Unfortunately, most cells were found dead after treatment. Further lowering the inhibitor concentrations (below 3.5uM) will likely not block the cell cycle, rendering this approach unsuited.

Revision plan: We will test the suitability of additional antibodies directed against Arp2/3 complex components to assess their subcellular localization, with the aim to discriminate peripheral cytoplasmic vs. perinuclear vs. intranuclear localization. In addition, we will add a comment in the discussion, further addressing this point. In the case we remain unable to pinpoint that Arp2/3 resides in the nucleus, we will further tone down our current phrasing in the discussion, also emphasizing the possibility that cytoplasmic or perinuclear pools of the complex may indirectly help maintain the integrity of the genome in LCs.

Nuclear envelop ruptures

The nuclear envelop ruptures are not sufficiently documented (how many cells were imaged? quantification?). The authors employ STED microscopy to examine Lamin B1 distribution. The image shown in Figure 4A does not really highlight the nuclear envelop, but rather the entire content. Whether it is representative is questionable. We would expect Lamin B1 staining intensity to be drastically reduced given the quantification shown in Figure 3D. In addition, although the authors have stressed in the previous figure that Arpc4-KO is associated with nucleus shape aberrations, the example shown in Figure 4A is that of a nucleus with a normal ovoid shape.

It is recommended to quantify the ruptures with Lap2b antibodies (or another staining that would better delineate the envelop) in order to avoid the possible bias due to the reduced staining intensity of Lamin B1.

__Response: __NE ruptures were quantified by imaging NLS-GFP-expressing DCs in microchannels to visualize leakage of their nuclear content (Fig. 4B,C). The STED image mentioned by the referee (Fig. 4A,D) was only shown to further illustrate examples of NE ruptures, here using Lamin B as an immunofluorescence marker for the NE. We do agree with the reviewer that it was not chosen optimally to represent the ArpC4-KO phenotype regarding nuclear shape and Lamin B1.

Revision plan: We will provide representative examples of nuclear illustrations of the ArpC4-KO phenotype vs. control cells. In addition, we will perform STED microscopy of Lap2B immunostained DCs as suggested by the referee.

A missing analysis is that of nuclear envelop ruptures as a function of nucleus deformations.

__Response: __As stated in the manuscript (page 5, third paragraph), the morphology of DCs is quite heterogeneous. As mentioned above, nuclear rupture events were quantified by live-imaging of NLS-GFP expressing DCs, enabling the tracing of rupture events. Live imaging is the only robust manner to measure nuclear membrane rupture events as they are transient due to rapid membrane repair (Raab et al. Science 2016). The NLS-GFP label itself, however, is not accurate enough to also quantify nuclear deformations. The latter therefore was quantified after cell fixation, using DAPI and/or immunostaining for NE envelope markers (Figures 3 and S3).

Revision plan: We will quantify nuclear deformations using Lap2B staining of the nuclear envelope as suggested by the referee.

Fig 4B-C: same frequency of Arpc4-KO and WT cells displaying nuclear envelop ruptures in the 4-µm channels; however image show a rupture for the Arpc4-KO and no rupture for the WT cells (this is somehow misleading). Are ruptures similar in Arpc4-KO and WT cells in this condition?

__Response: __We apologize for choosing an image that better reflects our quantification, our mistake.

Revision plan: We will choose an image that better reflects our quantification.

Fig 4D-E: is their a direct link between nuclear envelop ruptures and ƴH2A.X?

__Response: __At present, we can only correlate the findings of increased gH2Ax and elevated events of nuclear envelope ruptures in ArpC4-KO DCs. Rescue experiments are very difficult to impossible in DCs (e.g. restoring Lamin A/C and B levels in the KOs and subsequently assessing the amount of DNA damage). While we are afraid that we cannot address a potential link between NE ruptures and DNA damage by experiments in a manner feasible within this manuscript's revision, we have discussed this interesting aspect based on observations in immortalized cell culture systems (page 10). However, we would like to note that this was indeed shown for different cell types in Nader et al. Cell 2021. This effect results from access of cytosolic nuclease Trex1 to nuclear DNA.

Revision plan: This point will be clarified in our revised manuscript.

Interesting (but optional) would be to understand what is happening to DNA, histones? Is their evidence for leakage in the cytoplasm?

__Response: __We have not investigated so far. We will attempt to do so.

Revision plan: To address this aspect, we plan to perform immunostainings for double-stranded DNA in the cytoplasm (along with an NE marker). This approach has been used in the field to mark cytoplasmic DNA.

RNA seq analysis

The RNA-seq analysis suffers from a lack of direct connection with the rest of the study. The extracted molecular information is not validated nor further explored. It remains very descriptive. The PCA analysis suggests a « more pronounced transcriptomic heterogeneity in differentiating Arpc4KO DCs ». However it seems difficult to make such a claim from the comparison of 3 mice per group. In addition, such heterogeneity is not seen in the more detailed analysis (Fig 5F). The authors claim that « day 10 control and Arpc4KO DCs showed no to very little differences in gene expression, in contrast to cells at days 7-9 of differentiation ». This is not obvious from the data displayed in the corresponding figure. In addition, it is not expected that cells that may take a divergent differentiation path at days 7-9 may would return to a similar transcriptional activity at day 10.

A point that is not discussed is that before day 10 of DC differentiation, Arpc4 KO is expected to only occur in about 50% of the cell population. This is expected to impact the RNA-seq analysis.

Not all clusters have been exploited (e.g. cluster 3 elevated, cluster 6 partly reduced). I suggest the authors reconsider their analysis and analysis of the RNA-seq analysis (or eventually invest in complementary analysis).

__Response: __Despite a comprehensive analysis of the different transcriptomes of control and ArpC4 mutant cells during DC differentiation, we decided to focus the presentation and discussion of our RNAseq results on the most notable findings. Of these, the elevated innate immune responses in ArpC4-KO DCs (Fig. 5E,H) caught our particular attention, as this seemed highly meaningful in light of DC and LC functions.

Revision plan: As suggested by the referee, in the revised manuscript, we will better connect the RNAseq data to the other cellular and molecular analyses shown, complementing these results by investigating the potential involvement of innate immune responses in the ArpC4-KO phenotype.

What causes the profound numerical drop of LC in the epidermis?

A major open question is what causes the massive drop of LCs. Although differentiating Arpc4KO DCs start accumulating DNA damage upon proliferation, they succeed in progressing through the cell cycle. There is even a slightly elevated expression of cell cycle genes at day 7 of differentiation in the DC model.

Only a trend for increased apoptosis is observed in ear and tail skin. It would be important to provide complementary data documenting increased death (or aberrant emigration?) of LCs in the 4-8 week time window.

__Response: __We agree with the reviewer that this is an important question. We exclude that elevated emigration causes the decline of LCs in ArpC4-KO epidermis, as ArpC4-mutant LCs are significantly reduced (and not increased) in skin-draining lymph nodes (Fig. 7E). To assess whether increased cell death contributed to LC loss, we have tried to identify LCs that are just about to die. As the reviewer noted, we could only observe a trend of apoptosis-positive LCs in mutant epidermis. We assume that this is because of a quick elimination of compromised LCs following DNA damage, with only a short time passing until LCs with impaired genome integrity will be cleared from the system, making it very difficult to detect gH2Ax-positive cells that are positive for markers of cell death.

Revision plan: Despite the abovementioned expected limitations to detect DNA-damage-positive but viable LCs in vivo, for the manuscript revision we will collect 6-week-old mice to analyze LC numbers and apoptosis (cleaved Caspase-3), complementing our data derived from 7-day and 4-week-old mice (Figures S2A,B, S2E,F). Suited mice have been born end of May; we are ready to analyze them at 6-weeks of age, accordingly.

Functional consequences

Although the study reports novel aspects of LC biology, the consequence of ArpC4 deletion for skin barrier function and immunosurveillance are not investigated. It would seem very relevant to test how this model copes with radiation, chemical and/or microorganism challenges.

__Response: __We fully agree with this reviewer that this is a very interesting point. Therefore, next to assessing the steady-state circulation of LCs and DCs, we also addressed the consequence of ArpC4 loss for LC function in chemically challenged skin: we performed skin painting experiments using the contact sensitizer fluorescein isothiocyanate (FITC), diluted in the sensitizing agent dibutyl phthalate (DBP), to detect cutaneous-derived phagocytes within draining lymph nodes. These experiments revealed that migration of Arpc4KO LCs (as well as of Arpc4KO DCs) to skin-draining lymph nodes was impaired (Fig. 7C-E), confirming an in vivo role of ArpC4 for immune cell migration to lymphatic organs following a chemical challenge. Considering the lengthy legal approval procedures for new animal experimentation procedures, additional in vivo challenges -beyond the provided FITC challenge study- would take at least 6 additional months, which would delay excessively the revision of our manuscript.

Revision Plan: We will better explain the FITC painting experiment to highlight its importance.

MINOR COMMENTS:

1- Figure 1D

Gating strategy: twice the same empty plots. The content seems to be missing... Does this need to be shown in the main figure?

__Response: __We apologize for this problem; there might be a problem due to file conversion of PDF reader software. In our PDF versions (including the published bioRxiv preprint) we do see the data points (see below); however, we have earlier experienced incomplete FACS plots during manuscript preparation.

Revision plan: We will take extra care and double-check the results after converting the figures into PDFs. In addition, we will provide JPG files when submitting the revised manuscript, to prevent such problems.

2- Figure 2

Best would be to keep same scale to compare P1 and P7 (tail skin, figure 2A)

Response and revision plan: We will replace the examples with micrographs of comparable scale (already solved, will be provided with manuscript revision).

Overlay of Ki67 and MHC-II does not allow to easily visualize the double-positive cells (Fig 2C)

Response and revision plan: We will provide single-channel image next to the merged view, and improve the visualization of double-positive cells (already solved, will be provided with manuscript revision)

Quality of Ki67 staining different for Arpc4-KO (less intense, less focused to the nuclei): a technical issue or could that reflect something?

Response and revision plan: We thank the reviewer for spotting this. We have re-assessed all Ki67 micrographs and noted that the originally chosen examples indeed are not fully representative. We have meantime selected more representative examples of Ki67-positive cells in control and mutant tissues, reflecting no difference in the principal nature of Ki67 staining (already taken care of, will be provided with manuscript revision).

Fig 2C: Panels mounted differently for ear and tail skin (different order to present the individual stainings, Dapi for tail skin only).

Response and revision plan: We will harmonize the sequence of panels in figure 2 with submission of the revised manuscript.

3- LC branch analysis (Fig 1 and 2)

While Fig 1 indicates that ear skin LCs form in average twice as few branches as tail skin LCs (3-4 versus 8-9 branches per cell), Fig 2 shows the opposite (10-12 versus 6-7 branches per cell).

Is this due to a very distinct pattern between the 2 considered ages (4 weeks versus 8-10 weeks)? Could the author double-check that there is no methodological bias in their analysis?

Response: We thank the reviewer for hinting us on this apparent inconsistency. Indeed, our initial analysis suffered from a bias in detecting LC dendrites, as the tissue cellularity and overall morphology significantly differs between 4-week-old and adult animals: In adult animals, the immunostainings show a higher baseline background signal for the skin epithelium compared to P28. We had noted this beforehand and had adjusted the imaging pipeline accordingly, with a more stringent thresholding to eliminate background signals in the case of adult tissues. While we were able to detect the described ArpC4 phenotype, this strategy resulted in a reduced ability to detect dendrites (both in control and mutant tissues), explaining the seemingly reduced number of dendrites in adult vs. 4-week-old tissues.

Revision plan: We have double-checked both the micrographs and the corresponding quantifications and did not identify errors. Instead, our assumption -that a too high stringency for background reduction in adults caused the discrepancy- turned out correct. At present, we are re-doing the detailled analyses of LC morphology at 4-week and adult stages by confocal microscopy using a 63x objective rather than a 40x objective as done previously. First results confirm that with this approach the number of LC dendrites across these ages are largely comparable, while the phenotypes of ArpC4 loss are retained. We will provide a completely new analysis with revision of the manuscript.

4- Fig 3 E-G

How many animals were examined (n=5)? Reproducible accros animals? Why was it done with 4-week animals (phenotype not complete? Event occurring before loss in numbers...)

Response and revision plan: As mentioned in the figure legend for Fig. 3F we have analysed N = 4 control and N= 5 KO mice (for clarity, we will add this information to Figure 3E and G in the revised document). We chose the 4-week time-point as this was the stage when the loss of LCs first became apparent (even though non-significant at this age). We aimed to learn whether changes in nuclear morphology and nuclear envelope markers represented early molecular and cellular events following ArpC4 loss. Compared to later stages, this strategy poses a reduced risk to detect indirect effects of ArpC4 loss. We will clarify this in the revised manuscript text.

Staining Lamin A/C globally more intense in the Arpc4-KO epidermis (also seems to apply to the masks corresponding to the LCs). Surprising to see that the quantification indicates a major drop of Lamin A/C intensity in the LCs.

Response and revision plan: We again thank the reviewer for this careful assessment. The originally chosen micrographs are indeed not fully representative. As with many tissue stainings, there is inter-sample variability. We have now revisited the micrographs and did not find a significant global reduction of Lamin A/C in the entire epidermis (including keratinocytes/KCs). The drop of Lamin A/C intensity is restricted to ArpC4 LCs -and not KCs- and in line with the reduced Lamin A/C expression data in DCs (Fig. 3C,D). We have selected more representative examples, which will be provided with the revised manuscript.

Legend Fig 4D replace confocal microscopy by STED microscopy

Revision plan: We will replace "confocal microscopy" by "STED microscopy" accordingly.

6- Figure 4F

Intensity/background of γH2Ax staining very distinct between the 2 micrographs shown for WT and Arpc4-KO epidermis.

Response and revision plan: We have revisited the micrographs and now selected more representative examples, which will be provided in the revised manuscript.

7- Figure 7C, F, H

Gating strategies: would be better to harmonize the style of the plots (dot plots and 2 types of contour plots have been used...)

Response and revision plan: We agree and will provide a harmonized plot illustration in the revised manuscript.

8- Figure 7H

Legend of lower gating strategy seems to be wrong (KO and not WT).

Response and revision plan: We thank the reviewer for pointing out this mistake. A corrected figure display will be provided with revision.

Reviewer #1 (Significance (Required)):

Strengths: the general quality of the manuscript is high. It is very clearly written and it contains a very detailed method section that would allow reproducing the reported experiments. This work entails a clear novelty in that it represents the first investigation of the role of ArpC4 in LCs. It opens an interesting perspective about specific mechanisms sustaining the maintenance of myeloid cell subsets in peripheral tissues. This work is therefore expected to be of interest for a large audience of cellular immunologists and beyond. Challenging skin function with an external trigger would lift the relevance for a even wider audience (see main point 6).

__Response: __see point 6.

Limitations: in its current version the manuscript suffers from a lack of solidity around a few analysis (see main points on ArpC4 and Arp2/3 protein expression, nuclear envelop rupture analysis,...). It also tends to formulate a narrative centered on the ArpC4 intra-nuclear function that is not definitely proven.

The field of expertise of this reviewer is: cellular immunology and actin remodeling.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

SUMMARY This is a study in experimental mice employing both in vitro and, importantly, in vivo approaches. EPIDERMAL LANGERHANS CELLS serve as a paradigm for the maintenance of homeostasis of myeloid cells in a tissue, epidermis in this case. In addition to well known functions of the ACTIN NETWORK in cell migration, chemotaxis, cell adherence and phagocytosis the authors reveal a critical function of actin networks in the survival of cells in their home tissue.

Actin-related proteins (Arp), specifically here the Arp2/3 complex, are necessary to form the filamentous actin networks. The authors use conditional knock-out mice where Arpc4 (an essential component of the Arp2/3 complex) is deleted under the control of CD11c, the most prominent dendritic cell marker which is also expressed on Langerhans cells. In normal mice, epidermal Langerhans cells reside in the epidermis virtually life-long. They initially settle the epidermis around and few days after birth an establish a dense network by a burst of proliferation and then they "linger on" by low level maintenance proliferation. In the epidermis of Arpc4 knock-out mice Langerhans cells also start off with this proliferative burst but, strikingly, they do not stay but are massively reduced by the age of 8-12 weeks.

The analyses of this decline revealed that

-- the shape (number of nuclear lobes) and integrity of cell nuclei was compromised; they were fragile and ruptured to some degree when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- DNA damage, as detected by staining for gamma-H2Ax or 53BP1 accumulated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- recruitment of DNA repair molecules was inhibited when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- gene signatures of interferon signaling and response were increased when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- in vivo migration of dendritic cells and Langerhans cells from the skin to the draining lymph nodes in an inflammatory setting (FITC painting of the skin) was impaired when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- the persistence of the typical dense network of Langerhans cells in the epidermis, created by proliferation shortly after birth, is abrogated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing. Importantly, this was not the case for myeloid cell populations that settle a tissue without needing that initial burst of proliferation. For instance, numbers of colonic macrophages were not affected when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing.

Thus, the authors conclude that the Arp2/3 complex is essential by its formation of actin networks to maintain the integrity of nuclei and ensure DNA repair thereby ascertaining the maintenance proliferation of Langerhans cells and, as the consequence, the persistence of the dense epidermal netowrk of Langerhans cells.

Up-to-date methodology from the fields of cell biology and cellular immunology (cell isolation from tissues, immunofluorescence, multiparameter flow cytometry, FISH, "good old" - but important - transmission electronmicroscopy, etc.) was used at high quality (e.g., immunofluorescence pictures!). Quantitative and qualitative analytical methods were timely and appropriate (e.g., Voronoi diagrams, cell shape profiling tools, Cre-lox gene-deletion technology, etc.). Importantly, the authors used a clever method, that they had developed several years ago, namely the analysis of dendritic cell migration in microchannels of defined widths. Molecular biology methods such as RNAseq were also employed and analysed by appropriate bioinformatic tools.

MAJOR COMMENTS:

• ARE THE KEY CONCLUSIONS CONVINCING? Yes, they are.

• SHOULD THE AUTHORS QUALIFY SOME OF THEIR CLAIMS AS PRELIMINARY OR SPECULATIVE, OR REMOVE THEM ALTOGETHER? No, I think it is ok as it stands. The authors are wording their claims and conclusions not apodictically but cautiously, as it should be. They point out explicitely which lines of investigations they did not follow up here.

• WOULD ADDITIONAL EXPERIMENTS BE ESSENTIAL TO SUPPORT THE CLAIMS OF THE PAPER? REQUEST ADDITIONAL EXPERIMENTS ONLY WHERE NECESSARY FOR THE PAPER AS IT IS, AND DO NOT ASK AUTHORS TO OPEN NEW LINES OF EXPERIMENTATION. I think that the here presented experimental evidence suffices to support the conclusions drawn. No additional experiments are necessary.

• ARE THE SUGGESTED EXPERIMENTS REALISTIC IN TERMS OF TIME AND RESOURCES? IT WOULD HELP IF YOU COULD ADD AN ESTIMATED COST AND TIME INVESTMENT FOR SUBSTANTIAL EXPERIMENTS. Not applicable.

• ARE THE DATA AND THE METHODS PRESENTED IN SUCH A WAY THAT THEY CAN BE REPRODUCED? Yes, they are.

• ARE THE EXPERIMENTS ADEQUATELY REPLICATED AND STATISTICAL ANALYSIS ADEQUATE? Yes.

__Response: __We thank the reviewer very much for assessing our work, for providing constructive suggestions, and for acknowledging the strength of the study.

MINOR COMMENTS:

• SPECIFIC EXPERIMENTAL ISSUES THAT ARE EASILY ADDRESSABLE. None

• ARE PRIOR STUDIES REFERENCED APPROPRIATELY? Essentially yes. Regarding the reduction / loss of the adult epidermal Langerhans cell network, it may be of some interest to also refer to / discuss to another one of the few examples of this phenomenon. There, the initial burst of proliferation is followed by reduced proliferation and increased apoptosis when a critical member of the mTOR signaling cascade is conditionally knocked out (Blood 123:217, 2014).

__Response and revision plan: __As suggested, we will include into the revised manuscript further examples with related phenotypes regarding the progressive decline of LCs.

• ARE THE TEXT AND FIGURES CLEAR AND ACCURATE? Yes they are. Figures are well arranged for easy comprehension.

• DO YOU HAVE SUGGESTIONS THAT WOULD HELP THE AUTHORS IMPROVE THE PRESENTATION OF THEIR DATA AND CONCLUSIONS?

1. Materials & Methods. The authors write, regarding flow cytometry of epidermal cells: "Briefly, 1cm2 of back skin from 8-14 weeks old female wild-type and knockout littermates was dissociated in 0.25 mg/mL Liberase (Sigma, cat. #5401020001) and 0.5 mg/mL DNase (Sigma, cat.#10104159001) in 1 mL of RPMI (Sigma) and mechanically disaggregated in Eppendorf tubes, FOLLOWED BY INCUBATED for 2 h at 37 {degree sign}C." Followed by what?

__Response and revision plan: __We apologize for this mistake. The text should read: "... followed by blocking and antibody labeling of cells in single cell suspension.". We will provide the correct text in the revised manuscript.

Materials & Methods. BMDC electronmicroscopy. What is "IF". Please specify.

__Response and revision plan: __We also regret this mistake in the method text. It should read: "... For electron microscopy analysis, after PDMS removal, cells were fixed using 2.5% glutaraldehyde ...". We will correct this in the revised manuscript.

RESULTS in gene expression analyses. The authors observe some increase in apoptosis (as detected by cleaved-Caspase-3 staining). Is this observation in immunofluorescence also evident in the RNAseq data (where the IFN changes were seen), i.e., in Figure 5.

__Response and revision plan: __We will check our RNAseq data regarding any changes in apoptosis-related genes and, if so, include these in the revised manuscript.

Figure 7 F and G. Perhaps the authors may want to swap upper and lower panels in F or G, so that macrophage FACS plots and bar graphs are in the same row - ob, obiously, DC plots and bars likewise.

__Response and revision plan: __We agree and will harmonize the panel sequence in the revised manuscript.

Figure 7H. "Gating strategy in ArpC4WT Lung (previously gated in Live CD45+ cells)" - The lower row is knock-out, not WT. This is indicated correctly in the legand, but in the figure both rows are labeled as WT.

__Response and revision plan: __Indeed, the legend information is correct, but the corresponding figure panel is incorrect. We will provide a corrected version with revision.

The reference by Park et al. 2021 is missing in the list.

__Response and revision plan: __We will add the reference to the revised bibliography.

Figure 1D. Sure, the bar graphs are meant to say "CD11c"? The FACS plots show "CD11b".

__Response and revision plan: __We will check the panels and correct where necessary.

As to cDC1. In Figure 1D the FACS plot shows an absence of CD103+ cDC1 cells. In contrast, In Figure 7A-left side panel, there is not difference in cDC1 cells between WT and KO mice. Is therefore the flow cytometry plot in Figure 1D not representative regarding cDC1 cells? Correct?

__Response and revision plan: __The reviewer is correct about this apparent discrepancy. We have not observed differences in the control vs. Aprc4-KO cDC1 population, hence Figure 7 represents our findings. For figure 1, we have by mistake chosen a non-representative plot, with the aim of illustrating the gating strategy. We apologize for this mistake and will provide a corrected an representative FACS plot figure in the revised manuscript.

Reviewer #2 (Significance (Required)):

• DESCRIBE THE NATURE AND SIGNIFICANCE OF THE ADVANCE (E.G. CONCEPTUAL, TECHNICAL, CLINICAL) FOR THE FIELD. This is a conceptual advance. It adds a big step to our understanding of how immune cells in tissues (which all come from the bone marrow or are seeded before birth from embryonal hematopoietic organs such as yolk sac and fetal liver) can remain resident in these tissues. For cell types such as Langerhans cells, which establish their final population density within their tissues of residence, the presented finding convincingly buttress the role of proliferation and thereby the role for the actin-related protein complex 2/3 (Arp2/3).

• PLACE THE WORK IN THE CONTEXT OF THE EXISTING LITERATURE (PROVIDE REFERENCES, WHERE APPROPRIATE). While we know much about actin-related proteins (Arp), as correctly cited by the authors, this knowledge is derived mostly from in vitro studies. The submitted study translates the findings to an in vivo setting for the first time.

• STATE WHAT AUDIENCE MIGHT BE INTERESTED IN AND INFLUENCED BY THE REPORTED FINDINGS. Skin immunologists foremost, but these findings are of interest to the entire community of immunologists, but also cell biologists.

• DEFINE YOUR FIELD OF EXPERTISE. My expertise is in skin immunology, in particular skin dendritic cells including Langerhans cells.

We acknowledge the referee for their positive assessment of our manuscript.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Summary:

The manuscript identifies a role of the Arp2/3 complex, the major regulator of actin branching in cells, for controlling the homeostasis of murine Langerhans cells (LCs), a specialized subset of dendritic cells in the skin epidermis. The findings of the study are based on the analysis of CD11c-Cre Arpc4-flox mice, a conditional knockout mouse model, which interferes with Arp2/3 function in Langerhans cells and other CD11c-expressing myeloid cells, e.g. dendritic cell or macrophage subsets. By using immunofluorescence and flow cytometry analysis of epidermis and skin tissues, the authors provide a detailed analysis of LC numbers at different developmental stages (postnatal day 1, 7, 28, and adult mice) and demonstrate that Arpc4-deficiency does not interfere with the establishment of LC networks until postnatal day 28. However, LCs in ear and tail skin are substantially reduced in Arpc4-deficient mice at 8-12 weeks of age. In parallel to their in vivo model, the authors analyze cultures of bone marrow-derived dendritic cells (BMDCs) from control and CD11c-Cre Arpc4-flox mice. Arpc4-deficiency in BMDCs, which develop over 8-10 days in culture, results in nuclear shape and lamina abnormalities, as well as signs of increased DNA damage. Aspects of this phenotype are also detected in Langerhans cells in epidermal preparations. Transcriptomic analysis of BMDCs highlights a gene signature of increased expression of the interferon response pathway and alterations in cell cycle regulation. Arpc4-deficient BMDCs show increased expression of DNA damage markers and reduced expression of certain DNA repair factors. Based on these correlative findings from the BMDC model, the authors conclude that the decline in LC numbers might develop from the accumulation of DNA damage over time, which the authors phrease "pre-mature aging of Langerhans cells". Lastly, the authors show a heterogenous picture how Arp2/3 depletion affects distinct DC populations in CD11c-Cre Arpc4-flox mice. While some tissue-resident DC subsets appear normal in numbers, others are declined in numbers in the tissue. This may be related to their proliferation potential in tissues.

Major comments:

• Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

1) The authors claim that Arpc4 deficiency selectively compromises myeloid cell populations that rely on proliferation for tissue colonization (Figure 7). The presented data might give hints for such a general hypothesis, but solid experimental proof to prove this is lacking. When comparing myeloid cell subsets from foru different irgans, the authors refer to published data that some dendritic cell subsets are more proliferative in tissues than others and that CD11cCre Arpc4-flox mice appear to have reduced cell numbers in these populations. However, the presented data are purely correlative and no functional connection to cell proliferation has been made to the phenotypes. While some dendritic cell subsets (Langerhans cells, alveolar DCs) show reduced cell numbers in CD11cCre Arpc4-flox mice, other myeloid cell cells subsets are unaffected (e.g. dermal cDC1 and 2, colon macrophages).There could be plenty of other reasons that might underly the observed discrepancies between these cell subsets, e.g. Arp2/3 knockout efficiency and myeloid cell turnover in the tissue are just two examples, which have not been taken into consideration. Direct measurement of cell proliferation, e.g. BrdU labeling, and the observed phenotype would be missing to make such claims. The data could either be removed. Experimentally addressing these points could take 3-6 months.

Response and planned revisions: We thank the referee for bringing this point. We agree that these results give hints that support our conclusion but that do not address this question directly. However, we would like to insist on the fact that our conclusion is based on studies from others showing that alveolar macrophages self-maintain themselves through proliferation (Bain et al. Mucosal Immunology 2022). In contrast, it has been reported that most colonic macrophages are derived from monocytes that are being recruited to the gut through life (Bain et al. Mucosal Immunity 2023)

We propose to better explain and discuss these points in our revised manuscripts. In addition, we will stress that we do not exclude that different intracellular Arpc4-dependent processes might contribute to the phenotypes observed (beyond maintenance of DNA integrity). These revisions will help mitigate our conclusions and leave open the potential implication of alternative mechanisms that will be discussed as suggested by the referee.

2) The authors claim that DC subsets (e.g. dermal cDCs), which develop from pre-DCs, are not affected by Arp2/3 depletion (Figure 7, although the FACS plot in Fig. 1D would suggest a different picture for cDC1). This is surprising in light of the data with bone marrow-derived DCs (BMDCs), the major in vitro model of this study, which develop from CDPs that again develop from pre-DCs. BMDCs did show aberrant nuclei and signs of DNA damage. How would the authors then explain the discrepancies of the BMDC model with DC subsets, where the authors feel that the pre-DC origin explains the phenotypic difference? This is a general concern of the data interpretation and conclusions.

__Response: __We thank the referee to bring this point that indeed requires clarification. Two non-exclusive hypotheses could explain this apparent discrepancy:

• The ontogeny of bone-marrow-derived DCs: Depending on the protocol used, there might be variations in the precursors DCs develop from. We use one of the first protocols, which was pioneered by Paola Ricciardi-Castagnoli lab (Winzler et al. J.Exp.Med. 1997). It relies on a supernatant from J558 cells transfected with GMCSF, which contains additional cytokines and mainly generate DC2-like DCs. Langerhans cells are closer to DC2s, which resemble more macrophages than DC1s. We thus chose this protocol rather than the protocols that use Flt3-L, which produce both DC1s and DC2s developed from common dendritic-cell precursors (CDPs). It is thus possible that our BM-derived DCs develop from other precursor cells that are possibly closer to monocyte precursors.
• As shown in Figure 5C, kinetics of acquisition of CD11c expression, and thus deletion of the Arpc4 gene, might be distinct in vivo and in vitro. In vivo, as stated in our manuscript, DCs acquire CD11c as preDCs and undergo few rounds of divisions after. In vitro, as shown by our cycling experiments, BM-derived DCs continuously cycle, so they will keep dividing after having acquire CD11c (around day 7) and deleting the Arpc4 gene. __Revision plan: __We propose to mention these hypotheses in the discussion of our manuscript to explain the apparent contradiction raised by the referee.

3) In line with point 2, the authors never show that BMDCs show reduced proliferation, reduced cell numbers or increased cell death in Arpc4-deficient cell cultures, as a consequence of the detected DNA damage and impaired DNA repair. In fact, Figure 5C even shows that cell growth rates between control and KO are equal. This is a major mismatch in the current study. Since the authors use the BMDC model to explain the declining cell numbers in Langerhans cells (which derive from fetal liver cells), this phenotype is not mirrored by the BMDC culture and it remains open whether the observed changes in nuclear DNA damage and repair are indeed directly linked to the observed phenotype of declining cell numbers in the tissue. These aspects require argumentation why cell growth is unchanged in KO cells. Additional experiments addressing these points with sufficient biological replicates (cultures from different mice) could take 2-3 months, including preparation time.

__Response____: __We thank the referee for bringing this point, which was probably not properly discussed in the first version of our manuscript. Indeed, Arpc4KO BM-derived DCs do not show the premature cell death phenotype observed in LCs in vivo, as stated by the referee. There are at least two putative non-exclusive explanations for this. First, unlike LCs, which are long-lived cells, BM-derived DCs can be kept in culture for only 10-12 days. As DNA damage-induced cell death takes time (LCs only start to die about 3-4 weeks after network establishment), the lifespan of BM-DCs could simply not be long enough to observe this phenotype. Second, in the epidermis, LCs are physically constrained and continuously exposed to diverse signals that might increase their sensitivity to DNA damage and thereby induction of subsequent cell death.

__Revision Plan: __We will clarify this point in our revised manuscript by providing putative explanations for the death phenotype of Arpc4-deficient LCs not being observed in BM-derived DCs. We will further explain that this does not invalidate this cellular model as it was used to raise hypotheses on the putative role played by Arpc4 in myeloid cells, i.e. maintenance of DNA integrity, which was then confirmed in vivo (Arpc4KO LCs do indeed display DNA damage in the epidermis). Without this "imperfect cellular model", we would have probably not been able to uncover this novel function of Arp2/3 in immune cells.

4) The authors refer to a "pre-mature aging" phenotype of Arpc4-deficient BMDCs and LCs, based on reductions in Lamin B, Lamin A and increases in gH2AX and 53BP1. I find this term and overstatement of the current data and suggest that other markers for cell senescence, such as p53, Rb, p21 and b-Galactosidase are then also used to make such strong claim on "aging" and cell senescence. Experimentally addressing this point with sufficient biological replicates could take 2-3 months, including preparation time.

__Revision Plan: __We will assess the expression of these genes and senescence signatures in our RNAseq analysis as well as in Arpc4WT and Arpc4KO-derived DCs, as suggested by the referee.

5) The study does not provide a mechanism how the Arp2/3 complex would mediate the observed effects on DNA damage and repairs has not been addressed in the cell model, and only potential scenarios from other non-myeloid cell lines are discussed. It remains unclear whether the observed phenotypes in Arpc4-depleted myleoid cells relate to the direct nuclear function of Arp2/3 or the cytosolic function of Arp2/3, including its roles in cytoskeletal regulation that may have secondary effects on the nuclear alterations. This is a general concern of the presented data, data on mechanism might require more than 6 months.

__Revision Plan: __The referee is correct: Our manuscript shows that Arp2/3 deficiency in specific myeloid cells impacts on their survival in vivo and proposes that this could result at least in part from impaired maintenance of DNA integrity in these cells. We do not know whether this also applies to non-myeloid cells, which, although very interesting, is beyond the scope of the present study. In addition, we do not have any experimental tool to distinguish whether the DNA damage phenotype of Arpc4KO cells involves the nuclear or cortical pool of F-actin, this is why we have left this question open in the discussion of our manuscript.

6) OPTIONAL: The authors make a strong case arguing that the increased interferon expression signature (based on the transcriptomics data) reflects the nuclear ruptures in Arpc4-deficient cells and adds to the observed phenotype. If this is so, what happens then in STING knockout cells in the presence of CK666 inhibitor?

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__Revision Plan____: __The referee is correct in that we do not show this point experimentally and should therefore temper this conclusion.

• Are the data and the methods presented in such a way that they can be reproduced?

1) The analyses include quite a number of intensity calculations of immunofluorescence signals (Fig. 3D, E; Fig. 4E, Fig. 5B and 6B)? The background stainings are often variable or very high. In some cases it is even unclear whether stainings are really detecting protein and go beyond background staining (Fig. 6A, Fig. 5F). How were immunofluorescence data acquired and dealt with different background staining intensities?

__Revision Plan: __We will carefully describe the microscopes used for image acquisition as well as the downstream analyses for each experiment, which indeed vary depending on the signals observed with distinct antibodies or construct.

2) It remained unclear to me on which basis the nuclear deformations in Fig. 3G, H were calculated?

__Revision Plan: __We will carefully describe the methods used to quantify nuclear deformations.

3) The detailed phenotype of control mice is a bit unclear. It appears as if these were Cre-negative animals. Did the authors have some proof-of-principle experiments showing that CD11cCre Arpc4 +/+ animals have comparable phenotypes to Cre-negative animals?

• Are the experiments adequately replicated and statistical analysis adequate?

__Revision Plan: __We have never observed any decline in LC numbers in other mouse lines/genotypes (for example in cPLA2flox/flox;CD11c-Cre mice shown in the manuscript, Fig. S6B), excluding a putative role for the Cre in LC death.

For most experiments, the number of biological replicates (mice, or BMDC cultures from different mice) and individual values (n, cells) are indicated. Statistical analysis appears adequate.

Minor comments:

• Prior published studies on Arp2/3 function in immune cells are referenced accordingly. A number of additional pre-print manuscripts on this topic have not been cited and could be considered referencing.

__Revision Plan: __We will fix this point and cite additional, relevant preprints.

• The text is very clearly and very well written. Figures are clear and accurate for most cases. There are some open questions:

• Fig. 1B: The number of dots betwenn graph and legend do not match. The dots are not n=12 for both genotypes. Additionally: What do the symbols in the circles in the graph stand for? This is also in another later figure unclear.

• Fig. 2C: The current IF presentation (overlay MHCII with Ki67) is not very helpful. An additional image that shows only the Ki67 signal in the MHCII mask would be very helpful.

• Fig. 4B: BMDCs of which culture day were used for these experiments?

• Fig. 4A and D shows the same representative cells for two biological messages, which is only moderately convincing regarding a "general" phenotype.

• Fig. 5, B: Scale bars are missing.

__Revision Plan: __We will fix all these points.

Reviewer #3 (Significance (Required)):

Strengths and Advance:

The study provides strong data and a very detailed analysis of how the Arp2/3 complex regulates stages of Langerhans cell development and homeostasis. The role of the Arp2/3 complex as regulator of actin branching, which is involved in many cellular functions, has previously not been reported for this cell type. Previous research in immune cells have already studied the Arp2/3 complex, but studies were focussed on its role in migration and the majority of published phenotypes related to cell migration. While there are already a number of in vitro studies showing that the Arp2/3 complex can regulate aspects of cell cycle control or cell death in non-immune cells, most of these studies were performed with immortalized, non-immune cell lines, which can be more easily manipulated to dissect mechanistic aspects of the cellular phenotype, but are limited in their physiological interpretation. Hence, it is a major strength of this study to investigate the effects of Arp2/3 in a primary immune cell type, directly in the native and physiological environment. This is important because in vitro data from other cell types cannot be easily extrapolated to any other cell type and it is critical for our understanding to collect physiological data from tissues, where the biology really happens. The finding that the Arp2/3 complex regulates the tissue-residency of Langerhans cell through processes that are unrelated to migration are partially unexpected, shifting the view of this protein complex's physiological role to other cell biological processes, e.g. regulation of cell proliferation.

Limitations: The limitations of the study are detailed in the five major points listed above. The study accumulates many experiments that characterize the phenotype of Arpc4-depleted cells, showing signs of DNA damage in Langerhans cells and cultures of BMDCs. How the Arp2/3 complex would mechanistically mediate the observed effects on DNA damage and repairs have not been addressed. It also remains open whether this is due to the effects of the Arp2/3 complex in the nucleus or the cytosol, which would be biologically extremely important to understand. Above that, there are some discrepancies regarding the phenotype of the BMDC model, which does neither entirely match the Langerhans cell phenotype in the tissue (reduced proliferation, LC derive from different progenitors), nor other endogenous DC populations, which should also derive from similar progenitors.

Audience and reviewer background:

In its current form, the manuscript will already be of interest for several research fields: Langerhans cell and dendritic cell homeostasis, immune cell trafficking, actin and cytoskeleton regulation in immune cells, physiological role of actin-regulating proteins. My own field of expertise is immune cell trafficking in mouse models, leukocyte migration and cytoskeletal regulation. I cannot judge the analysis and clustering of the bulk RNA sequencing data.

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Referee #2

Evidence, reproducibility and clarity

Summary:

• This is a study in experimental mice employing both in vitro and, importantly, in vivo approaches. EPIDERMAL LANGERHANS CELLS serve as a paradigm for the maintenance of homeostasis of myeloid cells in a tissue, epidermis in this case. In addition to well known functions of the ACTIN NETWORK in cell migration, chemotaxis, cell adherence and phagocytosis the authors reveal a critical function of actin networks in the survival of cells in their home tissue.

• Actin-related proteins (Arp), specifically here the Arp2/3 complex, are necessary to form the filamentous actin networks. The authors use conditional knock-out mice where Arpc4 (an essential component of the Arp2/3 complex) is deleted under the control of CD11c, the most prominent dendritic cell marker which is also expressed on Langerhans cells. In normal mice, epidermal Langerhans cells reside in the epidermis virtually life-long. They initially settle the epidermis around and few days after birth an establish a dense network by a burst of proliferation and then they "linger on" by low level maintenance proliferation. In the epidermis of Arpc4 knock-out mice Langerhans cells also start off with this proliferative burst but, strikingly, they do not stay but are massively reduced by the age of 8-12 weeks.

• The analyses of this decline revealed that

a) the shape (number of nuclear lobes) and integrity of cell nuclei was compromised; they were fragile and ruptured to some degree when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

b) DNA damage, as detected by staining for gamma-H2Ax or 53BP1 accumulated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

c) recruitment of DNA repair molecules was inhibited when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

d) gene signatures of interferon signaling and response were increased when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

e) in vivo migration of dendritic cells and Langerhans cells from the skin to the draining lymph nodes in an inflammatory setting (FITC painting of the skin) was impaired when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

f) the persistence of the typical dense network of Langerhans cells in the epidermis, created by proliferation shortly after birth, is abrogated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing. Importantly, this was not the case for myeloid cell populations that settle a tissue without needing that initial burst of proliferation. For instance, numbers of colonic macrophages were not affected when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing.

• Thus, the authors conclude that the Arp2/3 complex is essential by its formation of actin networks to maintain the integrity of nuclei and ensure DNA repair thereby ascertaining the maintenance proliferation of Langerhans cells and, as the consequence, the persistence of the dense epidermal netowrk of Langerhans cells.

• Up-to-date methodology from the fields of cell biology and cellular immunology (cell isolation from tissues, immunofluorescence, multiparameter flow cytometry, FISH, "good old" - but important - transmission electronmicroscopy, etc.) was used at high quality (e.g., immunofluorescence pictures!). Quantitative and qualitative analytical methods were timely and appropriate (e.g., Voronoi diagrams, cell shape profiling tools, Cre-lox gene-deletion technology, etc.). Importantly, the authors used a clever method, that they had developed several years ago, namely the analysis of dendritic cell migration in microchannels of defined widths. Molecular biology methods such as RNAseq were also employed and analysed by appropriate bioinformatic tools.

Major comments:

• ARE THE KEY CONCLUSIONS CONVINCING? Yes, they are.

• SHOULD THE AUTHORS QUALIFY SOME OF THEIR CLAIMS AS PRELIMINARY OR SPECULATIVE, OR REMOVE THEM ALTOGETHER? No, I think it is ok as it stands. The authors are wording their claims and conclusions not apodictically but cautiously, as it should be. They point out explicitely which lines of investigations they did not follow up here.

• WOULD ADDITIONAL EXPERIMENTS BE ESSENTIAL TO SUPPORT THE CLAIMS OF THE PAPER? REQUEST ADDITIONAL EXPERIMENTS ONLY WHERE NECESSARY FOR THE PAPER AS IT IS, AND DO NOT ASK AUTHORS TO OPEN NEW LINES OF EXPERIMENTATION. I think that the here presented experimental evidence suffices to support the conclusions drawn. No additional experiments are necessary.

• ARE THE SUGGESTED EXPERIMENTS REALISTIC IN TERMS OF TIME AND RESOURCES? IT WOULD HELP IF YOU COULD ADD AN ESTIMATED COST AND TIME INVESTMENT FOR SUBSTANTIAL EXPERIMENTS. Not applicable.

• ARE THE DATA AND THE METHODS PRESENTED IN SUCH A WAY THAT THEY CAN BE REPRODUCED? Yes, they are.

• ARE THE EXPERIMENTS ADEQUATELY REPLICATED AND STATISTICAL ANALYSIS ADEQUATE? Yes.

Minor comments:

• SPECIFIC EXPERIMENTAL ISSUES THAT ARE EASILY ADDRESSABLE. None

• ARE PRIOR STUDIES REFERENCED APPROPRIATELY? Essentially yes. Regarding the reduction / loss of the adult epidermal Langerhans cell network, it may be of some interest to also refer to / discuss to another one of the few examples of this phenomenon. There, the initial burst of proliferation is followed by reduced proliferation and increased apoptosis when a critical member of the mTOR signaling cascade is conditionally knocked out (Blood 123:217, 2014).

• ARE THE TEXT AND FIGURES CLEAR AND ACCURATE? Yes they are. Figures are well arranged for easy comprehension.

• DO YOU HAVE SUGGESTIONS THAT WOULD HELP THE AUTHORS IMPROVE THE PRESENTATION OF THEIR DATA AND CONCLUSIONS?

• Materials & Methods. The authors write, regarding flow cytometry of epidermal cells: "Briefly, 1cm2 of back skin from 8-14 weeks old female wild-type and knockout littermates was dissociated in 0.25 mg/mL Liberase (Sigma, cat. #5401020001) and 0.5 mg/mL DNase (Sigma, cat.#10104159001) in 1 mL of RPMI (Sigma) and mechanically disaggregated in Eppendorf tubes, FOLLOWED BY INCUBATED for 2 h at 37 {degree sign}C." Followed by what?

• Materials & Methods. BMDC electronmicroscopy. What is "IF". Please specify.

• RESULTS in gene expression analyses. The authors observe some increase in apoptosis (as detected by cleaved-Caspase-3 staining). Is this observation in immunofluorescence also evident in the RNAseq data (where the IFN changes were seen), i.e., in Figure 5.

• Figure 7 F and G. Perhaps the authors may want to swap upper and lower panels in F or G, so that macrophage FACS plots and bar graphs are in the same row - ob, obiously, DC plots and bars likewise.

• Figure 7H. "Gating strategy in ArpC4WT Lung (previously gated in Live CD45+ cells)" - The lower row is knock-out, not WT. This is indicated correctly in the legand, but in the figure both rows are labeled as WT.

• The reference by Park et al. 2021 is missing in the list.

• Figure 1D. Sure, the bar graphs are meant to say "CD11c"? The FACS plots show "CD11b".

• As to cDC1. In Figure 1D the FACS plot shows an absence of CD103+ cDC1 cells. In contrast, In Figure 7A-left side panel, there is not difference in cDC1 cells between WT and KO mice. Is therefore the flow cytometry plot in Figure 1D not representative regarding cDC1 cells? Correct?

Significance

• DESCRIBE THE NATURE AND SIGNIFICANCE OF THE ADVANCE (E.G. CONCEPTUAL, TECHNICAL, CLINICAL) FOR THE FIELD. This is a conceptual advance. It adds a big step to our understanding of how immune cells in tissues (which all come from the bone marrow or are seeded before birth from embryonal hematopoietic organs such as yolk sac and fetal liver) can remain resident in these tissues. For cell types such as Langerhans cells, which establish their final population density within their tissues of residence, the presented finding convincingly buttress the role of proliferation and thereby the role for the actin-related protein complex 2/3 (Arp2/3).

• PLACE THE WORK IN THE CONTEXT OF THE EXISTING LITERATURE (PROVIDE REFERENCES, WHERE APPROPRIATE). While we know much about actin-related proteins (Arp), as correctly cited by the authors, this knowledge is derived mostly from in vitro studies. The submitted study translates the findings to an in vivo setting for the first time.

• STATE WHAT AUDIENCE MIGHT BE INTERESTED IN AND INFLUENCED BY THE REPORTED FINDINGS. Skin immunologists foremost, but these findings are of interest to the entire community of immunologists, but also cell biologists.

• DEFINE YOUR FIELD OF EXPERTISE. My expertise is in skin immunology, in particular skin dendritic cells including Langerhans cells.