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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

Public Reviews:

Reviewer #1 (Public review):

Weakness#1: The authors claim to have identified drivers that label single DANs in Figure 1, but their confocal images in Figure S1 suggest that many of those drivers label additional neurons in the larval brain. It is also not clear why only some of the 57 drivers are displayed in Figure S1.

As described in the Results section, we screened 57 GAL4 driver lines based on previous reports. These included drivers that had been shown to label a single dopaminergic neuron (DAN) or a small subset of DANs in the larval or adult brain hemisphere, suggesting potential for specific DAN labeling in larvae.

In Figure 1, TH-GAL4 was used to cover all neurons in the DL1 cluster, while R58E02 and R30G08 were well known drivers for pPAM. Fly strains in Figure 1h, k, l, and m were reported as single DAN strains in larvae[1], while strains in Figure 1e, f, g were reported identifying only several DANs in adult brains[2,3]. We examined these strains and only some of them labeled single DANs in 3rd instar larval brain hemisphere (Figure 1f, g, h, l and m). Among them, only strains in Figure 1f and h labeled single DAN in the brain hemisphere, without labeling other non-DANs. Other strains labeled non-DANs in addition to single DANs (Figure 1g, l and m). Taking ventral nerve cord (VNC) into consideration, strain in Figure 1h also labeled neurons in VNC (Figure S1e), while strain in Figure 1f did not (Figure S1c).

In summary, the driver shown in Figure 1f (R76F02AD;R55C10DBD, labeling DAN-c1) is the only line we identified that labels a single DAN in the 3rd instar larval brain hemisphere without additional labeling. The other lines shown in Figure 1 (g, h, l, m) label a single DAN but also include some non-DANs. Figure 1 focuses on strains that label a single or a pair of DANs.

Labeling patterns for all 57 driver lines are summarized in Table 1. Figure S1 includes representative examples; full confocal images for all screened strains are available upon request, as stated in the figure legend.

Weakness #2: Critically, R76F02-AD; R55C10-DBD labels more than one neuron per hemisphere in Figure S1c, and the authors cite Xie et al. (2018) to note that this driver labels two DANs in adult brains. Therefore, the authors cannot argue that the experiments throughout their paper using this driver exclusively target DAN-c1.

Figure S1c shows a single dopaminergic (DA) neuron in each brain hemisphere. While additional GFP-positive signals were occasionally observed, they did not originate from the cell bodies of DA neurons, as these were not labeled by the tyrosine hydroxylase (TH) antibody. These additional GFP signals primarily appeared to be neurites, including axonal terminals, although we cannot rule out the possibility that some represent false-positive signals or weakly stained non-neuronal cell bodies. This interpretation is based on the analysis of 22 third-instar larval brains.

To clarify this point in the manuscript, we added the following sentence to the Results section: “Based on the analysis of 22 brain samples, we observed this driver strain labels one neuron per hemisphere in the third-instar larval brain (Figure 2a–d, Figure S1c, Table S3).” Additionally, Table S3 was included to summarize the DAN-c1 labeling pattern across all 22 samples. An enlarged inset highlighting GFP-positive signals was also added to Figure S1c.

Weakness #3: Missing from the screen of 57 drivers is the driver MB320C, which typically labels only PPL1-γ1pedc in the adult and should label DAN-c1 in the larva. If MB320C labels DAN-c1 exclusively in the larva, then the authors should repeat their key experiments with MB320C to provide more evidence for DAN-c1 involvement specifically.

We thank the reviewer for this insightful suggestion. The MB320C driver primarily labels the PPL1-γ1pedc neuron in the adult brain, along with one or two additional weakly labeled cells. It would indeed be interesting to examine the expression pattern of this driver in third-instar larval brains. If it is found to label only DAN-c1 at this stage, we could consider using it to knock down D2R and assess whether this recapitulates our current findings.

While we agree that this is a promising direction for future studies, we believe it is not essential for the current manuscript, given the specificity of the DAN-c1 driver (please see our response to Reviewer #3 for details). Nonetheless, we appreciate the reviewer’s suggestion, and we recognize that MB320C could be a valuable tool for future experiments.

Weakness #4: The authors claim that the SS02160 driver used by Eschbach et al. (2020) labels other neurons in addition to DAN-c1. Could the authors use confocal imaging to show how many other neurons SS02160 labels? Given that both Eschbach et al. and Weber et al. (2023) found no evidence that DAN-c1 plays a role in larval aversive learning, it would be informative to see how SS02160 expression compares with the driver the authors use to label DAN-c1.

We did not have our own images showing DANs in brains of SS02160 driver cross line. However, Extended Data Figure 1 in the paper of Eschbach et al. shows strongly labeled four neurons on each brain hemisphere[4], indicating that this driver is not a strain only labeling one neuron, DAN-c1.

Weakness #5: The claim that DAN-c1 is both necessary and sufficient in larval aversive learning should be reworded. Such a claim would logically exclude any other neuron or even the training stimuli from being involved in aversive learning (see Yoshihara and Yoshihara (2018) for a detailed discussion of the logic), which is presumably not what the authors intended because they describe the possible roles of other DANs during aversive learning in the discussion.

We agree with the reviewer that the terms “necessary” and “sufficient” may be too exclusive and could unintentionally exclude contributions from other neurons. As noted in the Discussion section, we acknowledge that additional dopaminergic neurons may also play roles in larval aversive learning. To reflect this, we have revised our wording to use “important” and “mediates” instead of the more definitive terms “necessary” and “sufficient,” making our conclusions more accurate and appropriately measured.

Weakness #6: Moreover, if DAN-c1 artificial activation conveyed an aversive teaching signal irrespective of the gustatory stimulus, then it should not impair aversive learning after quinine training (Figure 2k). While the authors interpret Figure 2k (and Figure 5) to indicate that artificial activation causes excessive DAN-c1 dopamine release, an alternative explanation is that artificial activation compromises aversive learning by overriding DAN-c1 activity that could be evoked by quinine.

This is an excellent point, and we agree that we cannot rule out the possibility that artificial activation interferes with aversive learning by overriding the natural activity of DAN-c1 that would normally be evoked by quinine. The observed results with TRPA1 could potentially be attributed to dopamine depletion, inactivation due to prolonged depolarization, or neural adaptation. However, we believe that our hypothesis - that over-excitation of DAN-c1 impairs learning - is more consistent with our experimental findings and with previously published data. Our rationale is as follows: (1) Associative learning in larvae occurs only when the conditioned stimulus (CS, e.g., an odor such as pentyl acetate) and unconditioned stimulus (US, e.g., quinine) are paired. In wild-type larvae, the CS depolarizes a subset of Kenyon cells in the mushroom body (MB), while the US induces dopamine (DA) release from DAN-c1 into the lower peduncle (LP) compartment (Figure 7a). When both stimuli coincide, calcium influx from CS activation and Gαs signaling via D1-type dopamine receptors activate the MB-specific adenylyl cyclase, rutabaga, which functions as a coincidence detector (Figure 7d). (2) Rutabaga converts ATP to cAMP, activating the PKA signaling pathway and modifying synaptic strength between Kenyon cells and mushroom body output neurons (MBONs) (Figure 7d). These changes in synaptic strength underlie learned behavioral responses to future presentations of the same odor. (3) Our results show that D2R is expressed in DAN-c1, and that D2R knockdown impairs aversive learning. Since D2Rs typically inhibit neuronal excitability and reduce cAMP levels[5], we hypothesize that D2R acts as an autoreceptor in DAN-c1 to restrict DA release. When D2R is knocked down, this inhibition is lifted, leading to increased DA release in response to the US (quinine). The resulting excess DA, in combination with CS-induced calcium influx, would elevate cAMP levels in Kenyon cells excessively - disrupting normal learning processes (Figure 7b). This is supported by studies showing that dunce mutants, which have elevated cAMP levels, also exhibit aversive learning deficits[6]. (4) The TRPA1 activation results are consistent with our over-excitation model. When DAN-c1 was artificially activated at 34°C in the distilled water group, this mimicked the natural activation by quinine, producing an aversive learning response toward the odor (Figure 2k or new Figure 2i, DW group). Similarly, in the sucrose group, artificial activation mimicked quinine, producing a learning response that reflected both appetitive and aversive conditioning (Figure 2k, SUC group). (5) Over-excitation impairs learning in the quinine group. When DAN-c1 was activated during quinine exposure, both artificial and natural activation combined to produce excessive DA release. This over-excitation likely disrupted the cAMP balance in Kenyon cells, impairing learning and resulting in failure of aversive memory formation (Figure 2k, QUI group). This phenotype closely mirrors the effect of D2R knockdown in DAN-c1. (6) Optogenetic activation of DAN-c1 during aversive training similarly produced elevated DA levels due to both natural and artificial stimulation. This again would result in MBN over-excitation and a corresponding learning deficit. When optogenetic activation occurred during non-training phases (resting or testing), no additional DA was released during training, and aversive learning remained intact (Figure 5b). (7) Notably, when optogenetic activation was applied during training, we observed no aversive learning in the distilled water group and no reduction in the sucrose group (Figure 5c, 5d). We interpret this as evidence that the optogenetic stimulation was strong enough to cause elevated DA release in both groups, impairing learning in a manner similar to D2R knockdown or TRPA1 overactivation. (8) We extended this over-excitation framework to directly activate Kenyon cells (MBNs). Since MBNs are involved in both appetitive and aversive learning, their over-excitation disrupted both types of learning (Figure 6), further supporting our hypothesis. In summary, we propose that DAN-c1 activity is tightly regulated by D2R autoreceptors to ensure appropriate levels of dopamine release during aversive learning. Disruption of this regulation - either through D2R knockdown or artificial overactivation of DAN-c1 - results in excessive DA release, over-excitation of Kenyon cells, and impaired learning. This over-excitation model is consistent with both our experimental results and prior literature.

Weakness #7: The authors should not necessarily expect that D2R enhancer driver strains would reflect D2R endogenous expression, since it is known that TH-GAL4 does not label p(PAM) dopaminergic neurons.

Just like the example of TH-GAL4, it is possible that the D2R driver strains may partially reflect the expression pattern of endogenous D2R in larval brains. When we crossed the D2R driver strains with the GFP-tagged D2R strain, however, we observed co-localization in DM1 and DL2b dopaminergic neurons, as well as in mushroom body neurons (Figure S3c to h). In addition, D2R knockdown with D2R-miR directly supported that the GFP-tagged D2R strain reflected the expression pattern of endogenous D2R (Figure 4b to d, signals were reduced in DM1). In summary, we think the D2R driver strains supported the expression pattern we observed from the GFP-tagged D2R strain, especially in DM1 DANs.

Weakness #8: Their observations of GFP-tagged D2R expression could be strengthened with an anti-D2R antibody such as that used by Lam et al., (1999) or Love et al., (2023).

Love et al. (2023) used the antibody originally described by Draper et al.[6]. We attempted to use the same antibody in our experiments; however, we were unable to detect clear signals following staining. This may be due to a lack of specificity for neurons in the Drosophila larval brain or incompatibility with our staining protocol. Unfortunately, we were unable to locate a copy of the Lam (1999) paper for further reference.

Weakness #9: Finally, the authors could consider the possibility other DANs may also mediate aversive learning via D2R. Knockdown of D2R in DAN-g1 appears to cause a defect in aversive quinine learning compared with its genetic control (Figure S4e). It is unclear why the same genetic control has unexpectedly poor aversive quinine learning after training with propionic acid (Figure S5a). The authors could comment on why RNAi knockdown of D2R in DAN-g1 does not similarly impair aversive quinine learning (Figure S5b).

We re-analyzed the data related to DAN-g1. Interestingly, knockdown of D2R in DAN-g1 larvae trained with quinine (QUI) showed a significant difference in response index (R.I.) compared to the distilled water (DW) control group. However, it also differed significantly from the DAN-g1 genetic control group trained with QUI (two-way ANOVA with Tukey’s multiple comparisons, p = 0.0002), while it was not significantly different from the UAS-D2R-miR genetic control group (p = 0.2724). Furthermore, knockdown of D2R in DAN-g1 did not lead to aversive learning deficits when larvae were trained with a different odorant, propionic acid (ProA; Figure S5a). Similarly, using an RNAi line to knock down D2R in DAN-g1 did not result in learning impairment when larvae were trained with pentyl acetate (PA; Figure S5b). These inconsistencies may stem from differences in stimulus intensity across odorants, as well as the variable efficiency of the knockdown strategies (microRNA vs. RNAi). Based on these results, we propose that D2Rs in DAN-g1 may modulate larval aversive learning in a quantitative manner but do not play as critical a role as those in DAN-c1, where knockdown produces a clear qualitative effect. We have added this paragraph to the Discussion section of the manuscript.

Reviewer #2 (Public review):

Weakness#1: Is not completely clear how the system DAN-c1, MB neurons and Behavioral performance work. We can be quite sure that DAN-c1;Shits1 were reducing dopamine release and impairing aversive memory (Figure 2h). Similarly, DAN-c1;ChR2 were increasing dopamine release and also impaired aversive memory (Figure 5b). However, is not clear what is happening with DAN-c1;TrpA1 (Figure 2K). In this case the thermos-induction appears to impair the behavioral performance of all three conditions (QUI, DW and SUC) and the behavior is quite distinct from the increase and decrease of dopamine tone (Figure 2h and 5b).

The study successfully examined the role of D2R in DAN-c1 and MB neurons in olfactory conditioning. The conclusions are well supported by the data, with the exception of the claim that dopamine release from DAN-c1 is sufficient for aversive learning in the absence of unconditional stimulus (Figure 2K). Alternatively, the authors need to provide a better explanation of this point.

Please refer to our response to Weakness #6 of Reviewer #1 above.

Reviewer #3 (Public review):

Weakness #1: It is a strength of the paper that it analyses the function of dopamine neurons (DANs) at the level of single, identified neurons, and uses tools to address specific dopamine receptors (DopRs), exploiting the unique experimental possibilities available in larval Drosophila as a model system. Indeed, the result of their screening for transgenic drivers covering single or small groups of DANs and their histological characterization provides the community with a very valuable resource. In particular the transgenic driver to cover the DANc1 neuron might turn out useful. However, I wonder in which fraction of the preparations an expression pattern as in Figure 1f/ S1c is observed, and how many preparations the authors have analyzed. Also, given the function of DANs throughout the body, in addition to the expression pattern in the mushroom body region (Figure 1f) and in the central nervous system (Figure S1c) maybe attempts can be made to assess expression from this driver throughout the larval body (same for Dop2R distribution).

We thank the reviewer for the positive comments and thoughtful suggestions.

Regarding the R76F02AD; R55C10DBD strain, we examined 22 third instar larval brains expressing GFP, Syt-GFP, or Den-mCherry. All brains clearly labeled DAN-c1. In approximately half of the samples, only DAN-c1 was labeled. In the remaining samples, 1 to 5 additional weakly labeled soma were observed, typically without associated neurites. Only 1 or 2 strongly labeled non-DAN-c1 cells were occasionally detected. These additional labeled neurons were rarely dopaminergic. In the ventral nerve cord (VNC), 8 out of 12 samples showed no labeled cells. The remaining 4 samples had 2–4 strongly labeled cells. These results support our conclusion that the R76F02AD; R55C10DBD combination predominantly and specifically labels DAN-c1 in the third instar larval brain. As for the reviewer’s question about the expression pattern of R76F02AD; R55C10DBD and D2R in the larval body, we agree that this is a very interesting avenue for further investigation. However, our current study is focused on the central nervous system and larval learning behaviors. We hope to explore this question more fully in future work.

We added the following sentence to the Results section: “Based on analysis of 22 brain samples, we believe this driver strain consistently labels one neuron per hemisphere in the third-instar larval brain (Figure 2a - d, Figure S1c, Table S3).” In addition, we included Table S3 to summarize the DAN-c1 labeling patterns observed across these samples.

Weakness #2: A first major weakness is that the main conclusion of the paper, which pertains to associative memory (last sentence of the abstract, and throughout the manuscript), is not justified by their evidence. Why so? Consider the paradigm in Figure 2g, and the data in Figure 2h (22 degrees, the control condition), where the assay and the experimental rationale used throughout the manuscript are introduced. Different groups of larvae are exposed, for 30min, to an odour paired with either i) quinine solution (red bar), ii) distilled water (yellow bar), or iii) sucrose solution (blue bar); in all cases this is followed by a choice test for the odour on one side and a distilled-water blank on the other side of a testing Petri dish. The authors observe that odour preference is low after odour-quinine pairing, intermediate after odour-water pairing and high after odour-sucrose pairing. The differences in odour preference relative to the odour-water case are interpreted as reflecting odour-quinine aversive associations and odour-sucrose appetitive associations, respectively. However, these differences could just as well reflect non-associative effects of the 30-min quinine or sucrose exposure per se (for a classical discussion of such types of issues see Rescorla 1988, Annu Rev Neurosci, or regarding Drosophila Tully 1988, Behav Genetics, or with some reference to the original paper by Honjo & Furukubo-Tokunaga 2005, J Neurosci that the authors reference, also Gerber & Stocker 2007, Chem Sens).

As it stands, therefore, the current 3-group type of comparison does not allow conclusions about associative learning.

We adopted the single-odor larval learning paradigm from Honjo et al., who first developed and validated this method for studying larval olfactory associative learning7,8. To address the reviewer’s concern regarding potential non-associative effects from 30-minute exposure to quinine or sucrose, we refer to multiple lines of evidence provided in Honjo’s studies: (1) Honjo et al. demonstrated that only larvae receiving paired presentations of odor and unconditioned stimulus (quinine or sucrose) exhibited learned responses. Exposure to either stimulus alone, or temporally dissociated presentations, failed to induce any learning response. (2) When tested with a second, non-trained odorant, larvae only responded to the odorant previously paired with the unconditioned stimulus. This rules out generalized olfactory suppression and confirms odor-specific associative learning. (3) Well-characterized learning mutants (e.g., rutabaga, dunce) that show deficits in adult reciprocal odor learning also failed to exhibit learned responses in this single-odor paradigm, further supporting its validity. (4) In our study, we used two distinct odorants (pentyl acetate and propionic acid) and two independent D2R knockdown approaches (UAS-miR and UAS-RNAi). We consistently observed that D2R knockdown in DAN-c1 impaired aversive learning. Importantly, naïve olfactory, gustatory, and locomotor assays ruled out general sensory or motor defects. Comparisons with control groups (odor paired with distilled water) also ruled out non-associative effects such as habituation. Taken together, these results strongly support that the single-odor paradigm is a robust and reliable assay for assessing larval olfactory associative learning in Drosophila. We have added a section in the Discussion to clarify and defend the use of this paradigm in our study.

Weakness #3: A second major weakness is apparent when considering the sketch in Figure 2g and the equation defining the response index (R.I.) (line 480). The point is that the larvae that are located in the middle zone are not included in the denominator. This can inflate scores and is not appropriate. That is, suppose from a group of 30 animals (line 471) only 1 chooses the odor side and 29, bedazzled after 30-min quinine or sucrose exposure or otherwise confused by a given opto- or thermogenetic treatment, stay in the middle zone... a P.I. of 1.0 would result.

We gave 5 min during the testing stage to allow the larvae to wander on the testing plate. Under most conditions, more than half of larvae (>50%) will explore around, and the rest may stay in the middle zone (will not be calculated). We used 25-50 larvae in each learning assay, so finally around 10-30 larvae will locate in two semicircular areas. Indeed, based on our raw data, a R.I. of 1 seldom appears. Most of the R.I.s fall into a region from -0.2 to 0.8. We should admit that the calculation equation of R. I. is not linear, so it would be sharper (change steeply) when it approaches -1 and 1. However, as most of the values fall into the region from -0.2 to 0.8, we think ‘border effects’ can be neglected if we have enough numbers of larvae in the calculation (10-30).

Weakness #4: Unless experimentally demonstrated, claims that the thermogenetic effector shibire/ts reduces dopamine release from DANs are questionable. This is because firstly, there might be shibire/ts-insensitive ways of dopamine release, and secondly because shibire/ts may affect co-transmitter release from DANs.

Shibire^ts1 gene encodes a thermosensitive mutant of dynamin, expressing this mutant version in target neurons will block neurotransmitter release at the ambient temperature higher than 30C, as it represses vesicle recycling[7]. It is a widely used tool to examine whether the target neuron is involved in a specific physiological function. We cannot rule out that there might be Shibire^ts1 insensitive ways of dopamine release exist. However, blocking dopamine release from DAN-c1 with Shibire^ts1 has already led to learning responses changing (Figure 2h). This result indicated that the dopamine release from DAN-c1 during training is important for larval aversive learning, which has already supported our hypothesis.

For the second question about the potential co-transmitter release, we think it is a great question. Recently Yamazaki et al. reported co-neurotransmitters in dopaminergic system modulate adult olfactory memories in Drosophila[9], and we cannot rule out the roles of co-released neurotransmitters/neuropeptides in larval learning. Ideally, if we could observe the real time changes of dopamine release from DAN-c1 in wild type and TH knockdown larvae would answer this question. However, live imaging of dopamine release from one dopaminergic neuron is not practical for us at this time. On the other hand, the roles of dopamine receptors in olfactory associative learning support that dopamine is important for Drosophila learning. D1 receptor, dDA1, has been proven to be involved in both adult and larval appetitive and aversive learning[10,11]. In our work, D2R in the mushroom body showed important roles in both larval appetitive and aversive learning (Figure 6a). All this evidence reveals the importance of dopamine in Drosophila olfactory associative learning. In addition, there is too much unknow information about the co-release neurotransmitter/neuropeptides, as well as their potential complex ‘interaction/crosstalk’ relations. We believe that investigation of co-released neurotransmitter/neuropeptides is beyond the scope of this study at this time.

Weakness #5: It is not clear whether the genetic controls when using the Gal4/ UAS system are the homozygous, parental strains (XY-Gal4/ XY-Gal4 and UAS-effector/ UAS-effector), or as is standard in the field the heterozygous driver (XY-Gal4/ wildtype) and effector controls (UAS-effector/ wildtype) (in some cases effector controls appear to be missing, e.g. Figure 4d, Figure S4e, Figure S5c).

Almost all controls we used were homozygous parental strains. They did not show abnormal behaviors in either learnings or naïve sensory or locomotion assays. The only exception is the control for DAN-c1, the larvae from homozygous R76F02AD; R55C10DBD strain showed much reduced locomotion speed (Figure S6). To prevent this reduced locomotion speed affecting the learning ability, we used heterozygous R76F02AD; R55C10DBD/wildtype as control, which showed normal learning, naïve sensory and locomotion abilities (Figure 4e to i).

For Figure 4d, it is a column graph to quantify the efficiency of D2R knockdown with miR. Because we need to induce and quantify the knockdown effect in specific DANs (DM1), only TH-GAL4 can be used as the control group, rather than UAS-D2R-miR. For the missing control groups in Figure S4e and S5c, we have shown them in other Figures (Figure 4e).

We described this in the Materials and Methods part, “All control strains used in learning assays were homozygous (except DAN-c1×WT), while all experimental groups (D2R knockdown and thermogenetics) used were heterozygous by crossing the corresponding control strains”.

We also re-organized the Figure S4e and S5c along with the control groups to make it easier to understand.

Weakness #6: As recently suggested by Yamada et al 2024, bioRxiv, high cAMP can lead to synaptic depression (sic). That would call into question the interpretation of low-Dop2R leading to high-cAMP, leading to high-dopamine release, and thus the authors interpretation of the matching effects of low-Dop2R and driving DANs.

We appreciate the reviewer’s suggestion. We read through this literature, which also addresses the question we mentioned in the Discussion section, about the discrepancy between the cAMP elevation in the mushroom body neurons and the reduced MBN-MBON synaptic plasticity after olfactory associative learning in Drosophila. The author gave an explanation to the existing D1R-cAMP elevation-MBN-MBON LTD axis, which is really helpful to our understanding about the learning mechanism. However, unfortunately, we do not think this offers a possible explanation for our D2R-related mechanisms. We added this literature into our citation.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Throughout the behavioral experiments, a defect in aversive learning is defined as a relative increase in the response index (RI) after olfactory training with quinine (red) and a defect in appetitive learning as a relative decrease in RI after training with sucrose (blue). Training with distilled water (yellow) is intended to be a control for comparisons within genotypes/treatment groups but causes interpretation issues if it is also affected by experimental manipulations.

The authors typically make comparisons between quinine, water, and sucrose within each group, but this often forces readers to infer the key comparisons of interest. For example, the key comparison in Figure 2h is the statistically significant difference between the red groups, which differ only in the temperature used during training. Many other figure panels in the paper would also benefit from more direct statistical comparisons, particularly Figure 2k.

While I recognize the value of the water control, I strongly recommend that the authors make statistical comparisons directly between genotypes/treatment groups where possible and to interpret results with more caution when the water RI score differs substantially between groups. Also, since the authors are conducting two-way ANOVAs before Dunnett's multiple comparisons tests, they ideally should report the p-value for the main effect of each factor, plus the interaction p-value between the two factors before making multiple comparisons.

We appreciate the reviewer’s suggestion. In response, we re-analyzed all learning assay data in Figures 2 and 4 using two-way ANOVA followed by Tukey’s multiple comparisons test. Unlike our previous analysis, which only compared each experimental group to its corresponding DW control, we now compared all groups against one another. First, we found that most R.I. values from different temperature conditions (Figure 2) or genotypes (Figure 4) trained with DW were not significantly different, with the exception of the data in Figure 2i (formerly Figure 2k; discussed further below). The R.I. from DAN-c1 × D2R-miR larvae trained with QUI was significantly different from both genotype control groups (DAN-c1 × WT and UAS-D2R-miR), while no significant difference was observed between the two controls trained with QUI. Thus, this more comprehensive statistical approach supports the conclusions we previously reported. Second, as the reviewer noted, the new analysis allows for a more direct interpretation of our findings. For example, in the thermogenetic experiments using the Shibire^ts1 strain, the R.I. of DAN-c1 × UAS-Shibire^ts1 larvae trained with QUI at 34°C was not significantly different from the DW group at 34°C, but was significantly different from the QUI group at 22°C. Both findings support our conclusion that blocking dopamine release from DAN-c1 impairs larval aversive learning (Figure 2f).

In the dTRPA1 activation experiments, the R.I. of DAN-c1 × UAS-dTRPA1 larvae trained with DW at 34°C was significantly lower than that of the DW group at 22°C and the QUI group at 34°C, but not significantly different from the QUI group at 22°C (Figure 2i). These results indicate that activating DAN-c1 during training is sufficient to drive aversive learning even in the absence of QUI. Interestingly, when DAN-c1 × UAS-dTRPA1 larvae were trained with QUI at 34°C, their R.I. was significantly higher than that of the DW group at 34°C and significantly different from the QUI group at 22°C, but not significantly different from the DW group at 22°C (Figure 2i). We interpret this as evidence that simultaneous activation of DAN-c1 by both QUI and dTRPA1 leads to over-excitation, which in turn impairs aversive learning.

We have revised the figures (Figures 2, 4, 5, and 6) and updated the corresponding Results sections to reflect this new statistical analysis. Additionally, we now report the p-values for interaction, row factor, and column factor - either in Table S4 (for Figure 2) or in the figure captions for Figures 4, 5, 6, S4, S5, and S7.

(2) The authors' motivation to find tools that label DANs other than DAN-c1 was unclear until much later in the paper when I saw the screening experiments in Figures S4 and S5. The authors could provide a clearer justification for why they focus on DAN-c1 in Figure 2 rather than another DAN for which they found a specific driver in Figure 1. The motivation for looking at individual pPAM neurons was also unclear.

We sincerely appreciate the reviewer’s thoughtful suggestion. Our study was initially motivated by the goal of characterizing the expression pattern of D2R in the larval brain. From there, we aimed to identify DAN drivers that label specific pairs of dopaminergic neurons, enabling us to assess the functional role of D2R in distinct DAN subtypes through targeted knockdown experiments. This approach ultimately led us to focus on DAN-c1, as it was the only neuronal population for which D2R knockdown resulted in a learning deficit. We then returned to examine the functional significance of DAN-c1 in aversive learning. While we recognize that a more comprehensive narrative might be desirable, the current structure of our manuscript reflects the most logical progression of our work based on our research priorities and experimental outcomes. We did explore alternative manuscript structures - such as beginning with the D2R expression pattern - but found that the current format best conveys our findings and rtionale.

Regarding our motivation to study individual PAM neurons: we aimed to identify whether D2R plays a role in a specific pair of pPAM neurons involved in larval appetitive learning. However, we were unable to find a driver that exclusively labels DAN-j1, which we believe to be the key neuron in this context (see Figure 1). As a result, our investigation into appetitive learning did not progress beyond the observation of D2R expression in pPAM neurons (Figure 3d), and we did not proceed with learning assays in this context. While we acknowledge the limitations of our study, we believe that our focus on DAN-c1 is well-justified based on both our findings and the tools currently available. We respectfully note that a major restructuring of the manuscript would not necessarily clarify the rationale for focusing on DAN-c1, and therefore we have maintained the current organization.

(3) The authors should also double-check and update the expression patterns of the drivers in Table 1 using references such as the FlyLight online resource. For example, MB438B labels PPL1-α'2α2, PPL1-α3, PPL1-γ1pedc according to FlyLight, not just PPL1-γ1pedc as initially reported by Aso and Hattori et al. (2014).

We appreciate the reviewer’s suggestion. We have double-checked and updated the driver expression patterns in Table 1, using FlyLight data as a reference.

(4) Interpreting overlaid green-and-red fluorescence confocal images would be difficult for any colorblind readers; I suggest that the authors consider using a more friendly color set.

We thank the reviewer for the suggestion. In our study, we need three distinct colors to represent different channels. We also tested an alternative color scheme using and cyan , magenta, and yellow (CMY) instead of the standard red, green, and blue (RGB). As a comparison (see below), we used a R76F02AD;R55C10DBD (DAN-c1) GFP-labeled brain as an example. In our evaluation, the RGB combination provided clearer visualization and appeared more natural, while the CMY scheme looked somewhat artificial. Therefore, we decided to retain the original RGB color scheme and did not modify the colors in the figures.

Author response image 1.

(5) For Figure 4d, counting each DAN as an individual N would violate the assumption of independence made by the unpaired t test, since multiple DANs are found in each brain and therefore are not independent. Instead, it would be better to count each individual N as the average intensity of the four DANs measured in each brain.

We revised the analysis of microRNA efficiency by averaging the fluorescence intensity of DANs within each brain, treating each brain as a single sample. Based on this approach, we re-plotted Figure 4d.

(6) Finally, the authors ought to make it clearer throughout the paper that they have implicated a pair of DAN-c1 neurons in aversive learning, not just a single DAN as currently stated in the title.

We thank the reviewer for the suggestion about the phrase we are using under this scenario. We have changed all “single neuron” to “a pair of neurons”.

Reviewer #2 (Recommendations for the authors):

(1) The results section presents: "Activation of DAN-c1 with dTRPA1 at 34°C during training induced repulsion to PA in the distilled water group (Figure 2k). These data suggested that DAN-c1 excitation and presumably increased dopamine release is sufficient for larval aversive learning in the absence of gustatory pairing."<br /> An alternative interpretation is that 30 min of TrpA activation depletes synaptic vesicle pool, or inactivates neurons because of prolonged depolarization, or DAN shows firing rate adaptation (e.g. see Pulver et al. 2009; doi:10.1152/jn.00071.2009). In such a case DA release would be reduced and not increased. Therefore, the interpretation that DAN-c1 activation is both necessary and sufficient in larval aversive learning is difficult to be sustained.

In this regard it is important to know how the sensory motor abilities are during a thermos-induction at 34°C during 30 min.

We thank the reviewer for the thoughtful suggestion. Regarding the concern about potential dopamine depletion or neuronal inactivation, we believe a comparison with the Shibire^ts1 experiments helps clarify the interpretation. Activation of Shibire^ts1 during training with distilled water did not result in aversive learning (Figure 2f), which is a distinct phenotype from that observed with dTRPA1 activation (Figure 2i). This suggests that the phenotypes seen with dTRPA1 activation are not due to reduced dopamine release. Additionally, as the reviewer suggested, we have revised our conclusion to state that “DAN-c1 is important for larval aversive learning,” rather than claiming it is both necessary and sufficient.

(2) The GRASP system can label the contact of a cell in close proximity like synaptic contacts, but also other situations like no synaptic contact. It would be useful to use a more specific synaptic labelling tool, like the trans-synaptic tracing system (Talay et al., 2017 https://doi.org/10.1016/j.neuron.2017.10.011), which provides a better label of synaptic contact.

We really appreciate the reviewer’s suggestion. First, we acknowledge that there are four general methods to reveal synaptic connections between neurons: immunohistochemistry (IHC), neuron labeling, viral tracing, GRASP, and electron microscopy (EM). Among these, IHC is not sufficiently convincing, viral tracing is challenging and rarely used in Drosophila, and EM, while the most accurate, is prohibitively expensive for our current goals. For these reasons, we chose the GRASP system to demonstrate the synaptic connections from dopaminergic neurons to the mushroom body. Second, we utilized an activity-dependent version of the GRASP system, linking split-GFP1-10 with synaptic proteins (e.g., synaptobrevin)[12] rather than with cell surface proteins like CD4 or CD8. This version significantly reduces false positive signals compared to the previous version, which was tagged with cell surface proteins. While we admit that this method does not provide as solid evidence of synaptic connections as EM, it is the most efficient method available to us for showing the synaptic connections from dopaminergic neurons to the mushroom body. Finally, we thank the reviewer for suggesting the literature on trans-synaptic tracing methods. Unfortunately, this method is not suitable for our goal, as it labels the entire postsynaptic neuron. In our study, we use GRASP to identify the specific dopaminergic neurons based on the synaptic locations and compartments within the mushroom body lobe. We require a labeling system at the subcellular level because, as noted, DAN-c1 forms synapses specifically in the lower peduncle (LP) of the mushroom body lobe, which is part of the axonal bundles from mushroom body neurons. Using the trans-synaptic tracing method would label the entire mushroom body, making it impossible to distinguish DAN-c1 from other DL1 dopaminergic neurons.

(3) Previously, Honjo et al (2009) used a petri dish of 8.5 cm and a filter paper for reinforcement of 5.5 cm. In this study the petri dish was 10 cm and the size of the filter paper was not informed. That is important information because it will determine the probability of conditioning.

A piece of filter paper (0.25cm² square) was used to hold odorants in this study. We have added this information to the Materials and Methods.

(4) Statistic analysis of Behavioral performance of Fig 2H-I was made by ANOVA followed by Dunnett multiple comparisons test. Which was the control group? In each graph 2 independent Dunnett tests were performed against the DW control group?

We have re-analyzed the data using a two-way ANOVA followed by Tukey’s multiple comparison test, as suggested by Reviewer #1. In Figure 2f-j (previously Figure 2h-l), the DW groups serve as the control groups. In our new analysis, we compared data across all groups using Tukey’s multiple comparison test, with particular focus on comparisons to the corresponding DW control groups.

(5) The sample size in staining experiments of figures 1-4 were not informed.

We have added Table S2 in the supplementary materials to provide the N numbers for brain samples used in the figures.

(6) Color code in Fig 5 is missing, I assumed that is the same as in figure 4e

We added color code in the figure legend of Figure 5.

(7) Line 506 "0.1% QH solutions" should be 0.1% QUI solutions

Changed.

(8) There is no information on the availability of data

We added Data Availability Statement: Data will be made available on request.

Reviewer #3 (Recommendations for the authors):

(1) Axes of behavioural experiments should better show the full span of possible values (-1;1) to allow a fair assessment.

We have adjusted the axes in all learning assay graphs to a range from -1 to 1 for consistency and clarity.

(2) Ns should better be given within the figures.

We have added Table S2 in the supplementary materials to provide the N numbers for brain samples used in the figures. Additionally, Tables S4 to S6 include the N numbers for the learning assays. While we initially considered including the N numbers within the figure captions, we found it challenging to present this information clearly and efficiently. Therefore, we decided to summarize the N numbers in the tables instead.

(3) Dot- or box-plots would be better for visualizing the data than means and SEMs.

We agree with the reviewer’s suggestion. In the behavioral assay graphs, both dot plots and mean ± SEM have been included for better visualization of the data.

(4) The paper reads as if Dop2R would reduce neuronal activity, rather than "just" cAMP levels. Such a misunderstanding should be avoided.

We appreciate the reviewer’s comment. Under most conditions, dopamine binding to D2Rs activates the Gαi/o pathway, which inhibits adenylyl cyclase (AC) and reduces cAMP levels. This reduction in cAMP ultimately leads to decreased neuronal activity. In other words, D2R activation typically has an inhibitory effect on neurons. Additionally, D2R can exert inhibitory effects through other signaling pathways, such as the inhibition of voltage-gated associative learning, we continue to emphasize the importance of the D2R-mediated AC-cAMP-PKA signaling pathway. However, we do not rule out the potential involvement of additional signaling pathways, such as inhibition of voltage-gated calcium channels via Gβγ subunits[5]. As noted in the Introduction, dopamine receptors are also involved in other signaling cascades, including PKC, MAPK, and CaMKII pathways. In the context of our study, based on current understanding of molecular signaling in Drosophila olfactory, we still think D2R mediated AC-cAMP-PKA signaling pathway would be the most important one. However, we cannot rule out the involvement of other signaling pathways.

(5) It would be better if citations were more clearly separated into ones that refer to adult flies versus work on larvae.

We separated the citations related to adult flies from those working on larvae.

(6) Line 81-83. DopECR is not found in mammals, is it?

You are correct. DopECR is not found in mammals. This non-canonical receptor shares structural homology with vertebrate β-adrenergic-like receptors. It can be activated rapidly by dopamine as well as insect ecdysteroids[13,14].

(7) Line 99: Better "a" learning center (some forms of learning work without mushroom bodies).

We have revised the text from "the learning center" to "a learning center," as suggested by the reviewer.

(8) Supplemental figures should be numbered according to the sequence in which they are mentioned in the text.

We have rearranged the sequence of supplemental figures to match the order in which they are referenced in the text.

(9) It is striking that dTRPA1-driving DANc1 is punishing in the water condition but that this effect does not summate with quinine punishment (but rather seems to impair it). Maybe you can back this up by ChR- or Chrimson-driving DANc1? Or by silencing DANc1 by GtACR1?

We appreciate the reviewer’s suggestion. Indeed, we observed similar but not identical results when we used ChR2 to activate DAN-c1 during the training stage (Figure 5b and c). We found that activating DAN-c1 with quinine (QUI) impaired aversive learning (Figure 5b), consistent with our findings using dTRPA1 activation of DAN-c1 when trained in QUI at 34°C (Figure 2i). We propose that the over-excitation of DAN-c1, whether induced by QUI or artificial manipulation (optogenetics and thermogenetics), impairs aversive learning, which aligns with our findings for D2R knockdown (Figure 4e). However, there are some differences between dTRPA1 and ChR2 activation. While dTRPA1 activation induced aversive learning when trained with distilled water (DW) at 34°C (Figure 2i), ChR2 did not induce aversive learning under the same conditions (Figure 5c). We believe this difference is due to the varying activation levels between the two manipulations. Our optogenetic stimulus may have been stronger than the thermogenetic one, potentially leading to over-excitation in the DW group, preventing aversive learning. In the QUI group, the more severe over-excitation impaired aversive learning, producing a phenotype similar to that observed with other over-excitation methods (e.g., thermogenetics or D2R knockdown), where the phenotype reached a maximum level. We have also addressed these points in the Discussion section.

(10) Unless I got the experimental procedure wrong, isn't it surprising that Figure S7b does not uncover a punishing effect of driving TH-Gals neurons?

This optogenetic experiment with ChR2 expression in TH-GAL4 neurons was a pioneering attempt to activate DAN-c1 using ChR2. As explained in response to question (9), the failure to observe a punishing effect in the DW group when TH-GAL4 neurons were activated during training may be due to our optogenetic stimulus being too strong. This likely resulted in over-excitation of DAN-c1 (among the neurons labeled by TH-GAL4), impairing aversive learning and preventing the appearance of typical aversive behaviors.

(11) It seems that Figure1f´ is repeated, in a mirrored manner, in Figure 2e.

We have removed Figure 2e, as it was deemed redundant and not necessary for this section.

Reference

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(3) Xie, T. et al. A Genetic Toolkit for Dissecting Dopamine Circuit Function in Drosophila. Cell Rep 23, 652-665 (2018). https://doi.org/10.1016/j.celrep.2018.03.068

(4) Eschbach, C. et al. Recurrent architecture for adaptive regulation of learning in the insect brain. Nat Neurosci 23, 544-555 (2020). https://doi.org/10.1038/s41593-020-0607-9

(5) Neve, K. A., Seamans, J. K. & Trantham-Davidson, H. Dopamine receptor signaling. J Recept Signal Transduct Res 24, 165-205 (2004). https://doi.org/10.1081/rrs-200029981

(6) Draper, I., Kurshan, P. T., McBride, E., Jackson, F. R. & Kopin, A. S. Locomotor activity is regulated by D2-like receptors in Drosophila: an anatomic and functional analysis. Dev Neurobiol 67, 378-393 (2007). https://doi.org/10.1002/dneu.20355

(7) Honjo, K. & Furukubo-Tokunaga, K. Induction of cAMP response element-binding protein-dependent medium-term memory by appetitive gustatory reinforcement in Drosophila larvae. J Neurosci 25, 7905-7913 (2005). https://doi.org/10.1523/JNEUROSCI.2135-05.2005

(8) Honjo, K. & Furukubo-Tokunaga, K. Distinctive neuronal networks and biochemical pathways for appetitive and aversive memory in Drosophila larvae. J Neurosci 29, 852-862 (2009). https://doi.org/10.1523/JNEUROSCI.1315-08.2009

(9) Yamazaki, D., Maeyama, Y. & Tabata, T. Combinatory Actions of Co-transmitters in Dopaminergic Systems Modulate Drosophila Olfactory Memories. J Neurosci 43, 8294-8305 (2023). https://doi.org/10.1523/jneurosci.2152-22.2023

(10) Selcho, M., Pauls, D., Han, K. A., Stocker, R. F. & Thum, A. S. The role of dopamine in Drosophila larval classical olfactory conditioning. PLoS One 4, e5897 (2009). https://doi.org/10.1371/journal.pone.0005897

(11) Kim, Y. C., Lee, H. G. & Han, K. A. D1 dopamine receptor dDA1 is required in the mushroom body neurons for aversive and appetitive learning in Drosophila. J Neurosci 27, 7640-7647 (2007). https://doi.org/10.1523/JNEUROSCI.1167-07.2007

(12) Macpherson, L. J. et al. Dynamic labelling of neural connections in multiple colours by trans-synaptic fluorescence complementation. Nat Commun 6, 10024 (2015). https://doi.org/10.1038/ncomms10024

(13) Abrieux, A., Duportets, L., Debernard, S., Gadenne, C. & Anton, S. The GPCR membrane receptor, DopEcR, mediates the actions of both dopamine and ecdysone to control sex pheromone perception in an insect. Front Behav Neurosci 8, 312 (2014). https://doi.org/10.3389/fnbeh.2014.00312

(14) Lark, A., Kitamoto, T. & Martin, J. R. Modulation of neuronal activity in the Drosophila mushroom body by DopEcR, a unique dual receptor for ecdysone and dopamine. Biochim Biophys Acta Mol Cell Res 1864, 1578-1588 (2017). https://doi.org/10.1016/j.bbamcr.2017.05.015

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:

This valuable study by Wu and Zhou combined neurophysiological recordings and computational modelling to investigate the neural mechanisms that underpin the interaction between sensory evaluation and action selection. The neurophysiological results suggest non-linear modulation of decision-related LIP activity by action selection, but some further analysis would be helpful in order to understand whether these results can be generalised to LIP circuitry or might be dependent on specific spatial task configurations. The authors present solid computational evidence that this might be due to projections from choice target representations. These results are of interest for neuroscientists investigating decision-making.

Strengths:

Wu and Zhou combine awake behaving neurophysiology for a sophisticated, flexible visual-motion discrimination task and a recurrent network model to disentangle the contribution of sensory evaluation and action selection to LIP firing patterns. The correct saccade response direction for preferred motion direction choices is randomly interleaved between contralateral and ipsilateral response targets, which allows the dissociation of perceptual choice from saccade direction.

The neurophysiological recordings from area LIP indicate non-linear interaction between motion categorisation decisions and saccade choice direction.

The careful investigation of a recurrent network model suggests that feedback from choice target representations to an earlier sensory evaluation stage might be the source for this non-linear modulation and that it is an important circuit component for behavioural performance.

The paper presents a possible solution to a central controversy about the role of LIP in perceptual decision-making, but see below.

Weaknesses:

The paper presents a possible solution to a central controversy about the role of LIP in perceptual decision-making. However, the authors could be more clear and upfront about their interpretational framework and potential alternative interpretations.

Centrally, the authors' model and experimental data appears to test only that LIP carries out sensory evaluation in its RFs. The model explicitly parks the representation of choice targets outside the "LIP" module receiving sensory input. The feedback from this separate target representation provides then the non-linear modulation that matches the neurophysiology. However, they ignore the neurophysiological results that LIP neurons can also represent motor planning to a saccade target.

The neurophysiological results with a modulation of the direction tuning by choice direction (contralateral vs ipsilateral) are intriguing. However, the evaluation of the neurophysiological results are difficult, because some of the necessary information is missing to exclude alternative explanations. It would be good to see the actual distributions and sizes of the RF, which were determined based on visual responses not with a delayed saccade task. There might be for example a simple spatial configuration, for example, RF and preferred choice target in the same (contralateral) hemifield, for which there is an increase in firing. It is a shame that we do not see what these neurons would do if only a choice target would be put in the RF, as has been done in so many previous LIP experiments. The authors exclude also some spatial task configurations (vertical direction decisions), which makes it difficult to judge whether these data and models can be generalised. The whole section is difficult to follow, partly also because it appears to mix reporting results with interpretation (e.g. "feedback").

The model and its investigation is very interesting and thorough, but given the neurophysiological literature on LIP, it is not clear that the target module would need to be in a separate brain area, but could be local circuitry within LIP between different neuron types.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors recorded activity in the posterior parietal cortex (PPC) of monkeys performing a perceptual decision-making task. The monkeys were first shown two choice dots of two different colors. Then, they saw a random dot motion stimulus. They had to learn to categorize the direction of motion as referring to either the right or left dot. However, the rule was based on the color of the dot and not its location. So, the red dot could either be to the right or left, but the rule itself remained the same. It is known from past work that PPC neurons would code the learned categorization. Here, the authors showed that the categorization signal depended on whether the executed saccade was in the same hemifield as the recorded PPC neuron or in the opposite one. That is, if a neuron categorized the two motion directions such that it responded stronger for one than the other, then this differential motion direction coding effect was amplified if the subsequent choice saccade was in the same hemifield. The authors then built a computational RNN to replicate the results and make further tests by simulated "lesions".

Strengths:

Linking the results to RNN simulations and simulated lesions.

Weaknesses:

Potential interpretational issues due to a lack of evidence on what happens at the time of the saccades.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The neurophysiological results with a modulation of the direction tuning by choice direction are intriguing. However, the evaluation of the neurophysiological results are difficult because some of the necessary information is missing to exclude alternative explanations.

We thank the reviewer for the helpful comments. We have addressed this point in detail in the following response.

(a) Clearly state in the results how the response field "RF", where the stimulus was placed, was mapped. The methods give as "MGS"" (i.e., spatial selectivity during stimulus presentation and delay)" task rather than the standard delayed saccade. And also "while for those neurons which did not show a clear RF during the MGS task, we presented motion stimuli in the positions (always in the visual field contralateral to the recorded hemisphere) in which neurons exhibited the strongest response to the motion stimuli." All this sounds more like a sensory receptive field not an eye movement response filed". What was the exact task and criterion?

We agree with the reviewer that the original description of how we mapped the response fields (RFs) of LIP neurons lacked sufficient detail. In this study, we used the memory-guided saccade (MGS) task to map the RFs of all isolated LIP neurons. Both MGS and delayed saccade tasks are commonly used to map a neuron's response field in previous decision-making studies.

In the MGS task, monkeys initially fixate on the center of the screen. Subsequently, a dot randomly flashes at one of the eight possible locations surrounding the fixation dot with an eccentricity of 8 degree, requiring the monkeys to memorize the location of the flashed dot. After a delay of 1000 ms, the monkeys are instructed to saccade to the remembered location once the fixation dot disappears. The MGS task is a standard behavior task for mapping visual, memory, and motor RFs, particularly in brain regions involved in eye movement planning and control, such as LIP, FEF, and the superior colliculus.

We believe the reviewer's confusion may stem from whether we mapped the visual, memory, or motor RFs of LIP neurons in the current study, as these "RFs" are not always consistent across individual neurons. In our study, we primarily mapped the visual and memory RFs of each LIP neuron by analyzing their activity during both the target presentation and delay periods. To focus on sensory evaluation-related activity, we presented the visual motion stimulus within the visual-memory RF of each neuron. For neurons that did not show a significant visual-memory RF, we used a different approach: we tested the neurons with the main task by altering the spatial configuration of the task stimuli to identify the visual field that elicited the strongest response when the motion stimulus was presented within it. This approach was used to guide the placement of the stimulus during the recording sessions.

Following the reviewer’s suggestion, we have added the following clarification to the results section to better describe how we mapped the RF of LIP neurons:

‘We used the memory-guided saccade (MGS) task, which is commonly employed in LIP studies, to map the receptive fields (RFs) of all isolated LIP neurons. Specifically, we mapped both the visual and memory RFs of each neuron by analyzing their activity during the target presentation and delay periods of the MGS task (see Methods).’.

(b) l.85 / l126: What do you mean by "orthogonal to the axis of the neural RF" - was the RF shape asymmetric, if so how did you determine this? OR do you mean the motion direction axis? Please explain.

We realized that the original description of this point may have been unclear and could lead to confusion. The axis of the neural RF refers to the line connecting the center of the RF (which coincides with the center of the motion stimulus) to the fixation dot. We have revised this sentence in the revised manuscript as follows:

‘To examine the neural activity related to the evaluation of stimulus motion, we presented the motion stimuli within the RF of each neuron, while positioning the saccade targets at locations orthogonal to the line connecting the center of the RF (which also marks the center of the motion stimulus) and the fixation dot.’

(c) Behavioural task. Figure 1 - are these example session? Please state this clearly. Can you show the examples (psychometric function and reaction times) separated for trials where correct choice direction aligning with the motion preference (within 90 degrees) and those that did not?

Figure 1 shows the averaged behavioral results from all recording sessions. We have added this detail in the revised legend of Figure 1.

We are uncertain about the reviewer’s reference to the “correct choice direction aligning with the motion preference,” as the term “motion preference” is specific to the neuron response, which are different for different neurons recorded simultaneously using multichannel recording probe.

Nonetheless, following the reviewer’s suggestion, we grouped the trials in each recording session into two groups based on the relationship between the saccade direction and the preferred motion direction of the identified LIP neuron during one example single-channel recording. Both the RT and the performance accuracy during one example session were shown in the following figure.

Author response image 1.

Give also the performance averaged across all sites included in this study and range.<br /> If performance does differ for different configuration, please, show that the main modulatory effect does not align with this distinction.

To clarify this point, we have plotted performance accuracy and RTs for horizontal, oblique, and vertical target position configurations separately, which are shown for both monkeys in the following figures. We did not observe any systematic influences of task configurations on the monkeys' performance accuracy. While the RTs did differ across different configurations, we believe these differences are likely attributable to several factors, such as varying levels of familiarity introduced by our training process and the intrinsic RT difference between different saccade directions.

Author response image 2.

(d) Show the distribution of RF positions and the direction preferences for the recording sites included in the quantitative analysis of this study. (And if available, separately those excluded).

Following the reviewer’s suggestion, we have plotted the centers of the RFs for all neurons with identifiable RFs, categorizing them by their preferred motion directions. To determine each neuron’s RF, we analyzed the average firing rates from both the target presentation and delay periods during each trial of the memory-guided saccade (MGS) task. The RF centers of neurons with significant RFs were determined through a two-step process. First, we selected neurons that exhibited significant RFs in the MGS based on the following criteria: 1) there must be a significant activity difference between the eight target locations, and 2) the mean activity during the selected periods should be significantly greater than the baseline activity during the fixation period. Second, we fitted the activity data from the eight conditions to a Gaussian distribution, using the center of the fitted distribution as the RF center. A significant proportion of neurons from both monkeys that exhibited significant response to motion stimuli did not exhibited notable RFs based our current method. The following figures show the distributions of RFs and motion direction preference for all LIP neurons with identifiable RFs separately for each monkey. Since this is not the focus of the current study, we are not planning to include this result in the revised manuscript.

Author response image 3.

(e) Following on from d), was there a systematic relationship between RF position or direction preference and modulation by choice direction? For instance could the responses be simply explained by an increase in modulation for choices into the same (contralateral) hemifield as where the stimulus was placed?

The reviewer raised a good point. To address whether there was a systematic relationship between RF position or direction preference and modulation by choice direction, we calculated a modulation index for each neuron to quantify the influence of saccade direction on neuronal responses to motion stimuli. We then plotted the modulation index against the RF position for each LIP neuron, shown as following:

Author response image 4.

As shown in the figures above, neurons with RFs farther from the horizontal meridian were more likely to exhibit stronger modulation by the saccade direction, while neurons with RFs closer to the horizontal meridian showed inconsistent and weaker modulation. This is because when the RFs was on the horizontal meridian, saccade directions were aligned with the vertical axis (with no contralateral or ipsilateral directions). This is consistent with the finding in Figure S3—no significant differences in direction selectivity between the CT and IT conditions in the data sessions where the saccade targets were aligned close to the vertical direction. Since fewer than half of the identified neurons showed clear receptive fields using our method, the figure above did not include all the neurons used in the analysis in the manuscript. Therefore, we chose not to include this figure in the revised manuscript.

Additionally, we quantified the relationship between the modulation index and direction preference for neurons in sessions where the monkeys’ saccades were aligned to either horizontal or oblique directions. As shown in the following figure, no systematic relationship was found between direction preference and modulation by the choice direction for LIP neurons at the population level.

Author response image 5.

We have added this result as Figure S 2 in the revised manuscript.

Notably, the observed modulation of saccade direction on LIP neurons’ response to motion stimuli cannot be simply explained by saccade direction selectivity. We presented two more evidence to rule out such possibility in the original manuscript. First, the modulation effect we observed was nonlinear; specifically, the firing rate of neurons increased for the preferred motion direction but decreased for the non-preferred motion direction (Figure 2i and Figure S1A-D). This phenomenon is unlikely to be attributed to a linear gain modulation driven by saccade directions. Second, we plotted the averaged neural activity for contralateral and ipsilateral saccade directions separately, and found that LIP neurons showed similar levels of activity between two saccade directions (revised Figure 2L).

Additionally, we added a paragraph in the Methods section to describe the way we calculated modulation index as follows:

“We have calculated a modulation index for each neuron to reflect the influence of saccade direction on neuron’s response to visual stimuli. The modulation index is calculated as:

where represents the average firing rate from 50ms to 250ms after sample onset for all contralateral saccade trails with a neuron’s preferred moving direction of visual stimuli. The naming conventions are the same for , , and . An MI value between 0 and 1 indicate higher modulation in contralateral saccade trials, and an MI value between -1 and 0 indicates higher modulation in ipsilateral saccade trials.”

Please split Figures 2G,H,I J,K, by whether the RF was located contralaterally or ipsilaterally. If there are only a small number of ipsilateral RFs, please show these examples, perhaps in an appendix.

This is a reasonable suggestion; however, it is not applicable to our study. Among all the neurons included in our analysis, only one neuron from each monkey exhibited ipsilateral receptive fields (RFs). Therefore, we believe it may not be necessary to plot the result for this outlier.

(f) Were the choice targets always equi-distant from the stimulus and at what distance was this? Please give quantitative details in methods.

The review was correct that the choice targets were always equidistant form the stimulus. The distance between the motion stimulus and the target was typically 12-15 degree. We have added the details in the revised Methods section as follows:

‘Therefore, the two saccade targets were equidistant from the stimulus, with the distance typically ranging from 12 to 15 degrees.

(2) For Figure 3E, how do you explain that there is an up regulation of for contralateral choices before the stimulus onset, i.e. before the animal can make a decision? Is this difference larger for error trials?

This is a good question, which we have attempted to clarify in the revised manuscript. We believe that the observed upregulation in neural activity for contralateral choices may reflect the monkeys’ internal choice bias or expectation (choice between two motion directions) prior to stimulus presentation, which could influence their subsequent decisions. In Figure 3E, we calculated the r-choice to assess the correlation between the neuron’s direction selectivity and the monkeys’ decisions on motion stimuli, separately for contralateral and ipsilateral choice conditions. The increased r-decision during the pre-stimulus period indicates stronger neural activity for trials in which the monkeys later reported that the upcoming stimulus was in the preferred direction, and weaker activity for trials where the stimulus was judged to be in the non-preferred direction. This correlation was more pronounced for contralateral choices than for ipsilateral ones. It is important to note that while the monkeys cannot predict the upcoming stimulus direction with greater-than-chance accuracy, these results suggest that pre-stimulus neural activity in LIP is correlated with the monkeys’ eventual decision for that trial. Furthermore, LIP neural activity was more strongly correlated with the monkeys’ decisions in the contralateral choice condition compared to the ipsilateral one.

Additionally, we clarify that the r-decision was calculated using both correct and error trials. When comparing Figure 2J with Figure 2K, the correlation between neural activity and the monkeys’ upcoming decision during the pre-stimulus period was most prominent in low- and zero-coherence trials, where the monkeys either made more errors or based decisions on guesswork. We infer that the monkeys' confidence in these decisions was likely lower compared to high-coherence trials. Thus, the decision process appears to be influenced by pre-stimulus neural activity, particularly in low-coherence and zero-coherence trials.

Although it is unclear precisely what covert process this pre-stimulus activity reflects, similar patterns of choice-predictive pre-stimulus activity have been observed in LIP and other brain areas (Shadlen, M.N. and Newsome,T.W., 2001; Coe, B., at al. 2002; Baso, M.A. and Wurtz, R.H., 1998; Z. M. Williams at al. 2003). We have clarified this point in the revised manuscript, including a revision of the relevant sentence in the Results section for clarity, shown as follows:

“Furthermore, we used partial correlation analysis to examine decision- and stimulus-related components of DS (i.e., r-decision and r-stimulus, Figure 3E and 3F) using all four coherence levels. The decision-related component of LIP DS was significantly greater in the CT condition than in the IT condition (Figure 3E; nested ANOVA: P = 1.07e-6, F= 25.72), and this difference emerged even before motion stimulus onset. This suggests that the LIP DS was more closely correlated with monkeys’ decisions in the CT condition than in the IT condition. The upregulation in r-decision for contralateral choices may reflect the monkeys’ internal choice bias or expectation (choice between two motion directions) prior to stimulus presentation, which could influence their subsequent decisions more in the CT condition”

(3) Figure 2K: what is the very large condition-independent contribution? It almost seems as most of what these neurons code for is neither saccade or motion related.

The condition-independent contribution is the time-dependent component that is unrelated to saccade, motion, or their interaction. Our findings are consistent with previous methodological studies, where this time-dependent component was shown to account for a significant portion of the variance in population activity (Kobak, D. et al., 2016)

(4) Abstract:

a) "We found that the PPC activity related to monkeys' abstract decisions about visual stimuli was nonlinearly modulated by monkeys' following saccade choices directing outside each neuron's response field."

This sentence is not clear/precise in two regards:

Should "directing" be "directed"?

Also, it is not just saccades directed outside the RF, but towards the contralateral hemifield.

We thank the reviewer for the suggestion. We agree that ‘directing’ should be ‘directed’ and revised it accordingly. However, we do not believe that ‘directed outside each neuron's response field’ should be replaced with “towards the contralateral hemifield”. There are two major reasons. First, the modulation effect was identified as the difference between contralateral and ipsilateral saccade directions. We cannot conclude that the modulation mainly happened in the contralateral saccade direction. Second, we used ‘directed outside each neuron's response field’ to emphasize that this modulation cannot be simply explained by saccade direction selectivity, whereas ‘towards the contralateral hemifield’ cannot fulfill this purpose.

(b) " Recurrent neural network modeling indicated that the feedback connections, matching the learned stimuli-response associations during the task, mediated such feedback modulation."

- should be "that feedback connection .... might mediate". A model can only ever give a possible explanation.

Thanks for the help on the writing again! We have revised this sentence as following: “Recurrent neural network modeling indicated that the feedback connections, matching the learned stimuli-response associations during the task, might mediate such feedback modulation.”

(c) "thereby increasing the consistency of flexible decisions." I am not sure what is really meant by increasing the consistency of flexible decisions? More correct or more the same?

We apologize for the confusion. In the manuscript, "decision consistency" refers to the degree of agreement in the model's decisions under specific conditions. A higher decision consistency indicates that the model is more likely to produce the same choice when encountering encounters a stimulus in that condition. We have incorporated your suggestion and revise this sentence as “thereby increasing the reliability of flexible decisions”. We also clarified the definition of consistency in the main text as follows:

“These disrupted patterns of saccade DS observed in the target module following projection-specific inactivation aligned with the decreased decision consistency of RNNs, where decision consistency reflects the degree of agreement in the model's choices under specific task conditions. This suggests a diminished reliance on sensory input and an increased dependence on internal noise in the decision-making process.”.

(5) Results: headers should be changed to reflect the actual results, not the interpretation:

"Nonlinear feedback modulation of saccade choice on visual motion selectivity in LIP"

"Feedback modulation specifically impacted the decision-correlated activity in LIP"

These first parts of the results describe neurophysiological modulations of LIP activity, the source cannot be known from the presented data alone. I thought that this feedback is suggested by the modelling results in the last part of the results. It is confusing to the reader that the titles already refer to the source of the modulation as "feedback". The titles should more accurelty describe what is found, not pre-judge the interpretation.

We thank the reviewer for those valuable suggestions. We have updated the subtitles to: “Nonlinear modulation of saccade choice on visual motion selectivity in LIP” and “Decision-correlated but not stimulus-correlated activity was modulated in LIP.”

(6) page 8, l366-380. Can you link the statements more directly to panels in Figure 6. For Figure 6H-K, it needs to be clarified that the headers for 6D-G also apply to H-K.

­We have added headers for Figure 6H-K in the revised version, and revised the corresponding results section as follows.

‘We further examined how the energy landscape in the 1-D subspace changed in relation to task difficulty (motion coherence). Consistent with prior findings, trials with lower decision consistency (trials using lower motion coherence) exhibited shallower attractor basins at the time of decision for all types of RNNs (Fig. 6H-K). However, both the depth and the positional separation of attractor basins in the network dynamics significantly decreased for all non-zero motion coherence levels after the ablation of all feedback connections (comparing Figure 6I with Figure 6H; P(depth) = 5.20e-25, F = 122.80; P(position) = 1.82e-27, F = 137.75; two-way ANOVA). Notably, this reduction in basin depth and separation was more pronounced in the specific group compared to the nonspecific groups after ablating the feedback connections (comparing Figure 6J with Figure 6K; P(depth) = 2.65e-13, F =57.35; P(position) = 3.73e-14, F = 61.79; two-way ANOVA). These results might underlie the computational mechanisms that explain the observed reduction in the decision consistency of RNNs following projection-specific inactivation: the shallower and closer attractor basins after ablating feedback connections resulted in less consistent decisions. This happened because the variability in neural activity made it more likely for population activity to stochastically shift out of the shallower basins and into nearby alternative ones.’

(7) line 556-557: Please provide a reference or data for the assertion that nearby recording sites in LIP (100 microns apart) have similar RFs.

The reviewer raised an interesting question that we are unable to address in depth with the current data, as we lack information on the specific cortical location for each recording session. In the original manuscript, we suggested that nearby recording sites in LIP have similar receptive fields (RFs), based on both our own experience with LIP recordings and previous studies. Specifically, we observed that neurons recorded within a single penetration using a single-channel electrode typically exhibited similar RFs. Similarly, the majority of neurons recorded from the same multichannel linear probe within a single session also showed comparable RFs. Additionally, several studies (both electrophysiological and fMRI) have reported topographic organization of RFs in LIP (Gaurav H. Patel et al., 2010; S. Ben Hamed et al., 2001; Gene J. Blatt et al., 1990).

(8) Line 568, Methods: a response criterion of a maximum firing rate of 2 spikes/s seems very low, especially for LIP. How do the results change if this lifted to something more realistic like 5 spikes/s or 10 spikes/s?

We chose this criterion to ensure we included as many neurons as possible in our analysis. To further clarify, we have plotted the distribution of maximum firing rates across all neurons. Based on our findings, relaxing this criterion is unlikely to affect the results, as the majority of neurons exhibit maximum firing rates well above 5 spikes/s, and many exceed 10 spikes/s. We hope this explanation addresses the concern.

Author response image 6.

Reviewer #2 (Recommendations For The Authors):

In this manuscript, the authors recorded activity in the posterior parietal cortex (PPC) of monkeys performing a perceptual decision-making task. The monkeys were first shown two choice dots of two different colors. Then, they saw a random dot motion stimulus. They had to learn to categorize the direction of motion as referring to either the right or left dot. However, the rule was based on the color of the dot and not its location. So, the red dot could either be to the right or left, but the rule itself remained the same. It is known from past work that PPC neurons would code the learned categorization. Here, the authors showed that the categorization signal depended on whether the executed saccade was in the same hemifield as the recorded PPC neuron or in the opposite one. That is, if a neuron categorized the two motion directions such that it responded stronger for one than the other, then this differential motion direction coding effect was amplified if the subsequent choice saccade was in the same hemifield. The authors then built a computational RNN to replicate the results and make further tests by simulated "lesions".

The data are generally interesting, and the manuscript is generally well written (but see some specific comments below on where I was confused). However, I'm still not sure about the conclusions. The way the experiment is setup, the "contra" saccade target is essentially in the same hemifield as the motion patch stimulus. Given that the RF's can be quite large, isn't it important to try to check whether the saccade itself contributed to the effects? i.e. if the RF is on the left side, and the "contra" saccade is to the left, then even if it is orthogonal to the location of the stimulus motion patch itself, couldn't the saccade still be part of a residual edge of the RF? This could potentially contribute to elevating the firing rate on the preferred motion direction trials. I think it would help to align the data on saccade onset to see what happens. It would also help to have fully mapped the neurons' movement fields by asking the monkeys to generate saccades to all screen locations in the monitor. The authors mention briefly that they used a memory-guided saccade task to map RF's, but it is also important to map with a visual target. And, in any case, it would be important to show the mapping results aligned on saccade onset.

Another comment is that the authors might want to mention this other recent related paper by the Pack group: https://www.biorxiv.org/content/10.1101/2023.08.03.551852v2.full.pdf

We thank the reviewer for the comments and realized that we did not explain our results clearly in the original manuscript. We agree with the reviewer that saccade direction selectivity might be a confounding factor for the modulation of the saccade choice direction onto LIP neurons’ activity responded to visual motion stimuli. Because the RFs of LIP neurons might be large and the saccade target might be presented within the edge of the RFs. However, we believe that the observed modulation of saccade direction on LIP neurons’ response to motion stimuli cannot be simply explained by saccade direction selectivity. We presented several pieces of evidence to rule out such possibility. First, the modulation effect we observed was not linear; specifically, the firing rate of neurons increased for the preferred motion direction but decreased for the non-preferred motion direction (Figure 2i and Figure S1A-D). This phenomenon is unlikely to be attributed to a linear gain modulation driven by saccade directions. Second, we plotted the averaged neural activity for contralateral and ipsilateral saccade directions separately, aligned the activity to either motion stimulus onset or saccade onset, and found that LIP neurons showed similar levels of activity between the contralateral and ipsilateral directions (revised Figure 2L), which is not consistent with obvious saccade direction selectivity.

To better control for this confound, we have added figures plotting the mean neural activity aligned to saccade onset for both contralateral and ipsilateral saccades, which are now included in the revised main Figure 2. These figures are presented in the detailed response below. Additionally, we have revised the corresponding results section to clarify our points, as outlined below:

“Figure 2A-2F shows three example LIP neurons that exhibited significant motion coherence correlated DS. Surprisingly, LIP neurons showed greater DS in the CT condition than in the IT condition, even though the same motion stimuli were used in the same spatial location for both conditions. The averaged population activity showed this DS difference between CT and IT conditions for all four coherence levels (Figure 2G, 2H). During presentation of their preferred motion direction, LIP neurons showed significantly elevated activity in the CT relative to the IT at all coherence levels (Figure S1A, S1B, nested ANOVA: P(high) = 0.0326, F = 4.65; P(medium) = 0.0088, 142 F = 7.03; P(low) = 0.0076, F = 7.32; P(zero) = 0.0124, F = 6.4), and a trend toward lower activity to the nonpreferred direction for CT vs. IT (Figure S1C, S1D, nested ANOVA: P(high) = 0.0994, F = 2.75; P(medium) = 0.0649, F = 3.12; P(low) = 0.0311, F = 4.73; P(zero) = 0.0273, F = 4.96). Most of the LIP neurons (48 of 83) showed such opposing trends in activity modulation between the preferred and nonpreferred directions (Figure 2I). These results indicated a nonlinear modulation of saccade choice on motion DS in LIP, aligned precisely with the response property of each neuron. This is unlikely to be driven by a linear gain modulation of saccade direction selectivity. Receiver operating characteristic (ROC) analysis further confirmed significantly greater motion DS in the CT condition than in the IT condition (Figure 2J 148 and 2K; nested ANOVA: P(high) = 5.0e-4, F= 12.44; P(medium) = 9.53e-6, F = 20.91; P(low) = 9.33e-7, F 149 = 26.03; P(zero) = 2.56e-8, F= 34.3). Such DS differences were observed even before stimulus onset. Moreover, LIP neurons exhibited similar levels of mean activity between different saccade directions (CT vs. IT) before monkeys’ saccade choice (Figure 2L), further supporting that saccade direction selectivity did not significantly contribute to the observed modulation of LIP neurons’ responses to motion stimuli.

We also thank the reviewer for pointing out the missing of this relevant study, we have added the suggested refence in the revised discussion section as follows:

‘A recent study demonstrated that neurons in the middle temporal area responded more strongly to motion stimuli when monkeys saccaded toward their RFs in a standard decision task with a fixed mapping between motion stimuli and saccade directions. This modulation emerged through the training process and contributed causally to the monkeys' following saccade choices. Consistently, we found that the response of LIP neurons to motion stimuli was more strongly correlated with the monkeys' decisions in the CT condition (saccades toward RFs) than in the IT condition, in a more flexible decision task. Together, these results suggest that the modulation of action selection on sensory processing may be a general process in perceptual decision-making. However, the observed modulation of saccade direction on LIP neurons' responses to motion stimuli cannot be simply explained by saccade direction selectivity. Several lines of evidence argue against this possibility. First, the modulation effect was nonlinear; specifically, neuronal firing rates increased for preferred motion directions but decreased for non-preferred directions (Figure 2I and Figure S1). This pattern is unlikely to be driven by a linear gain modulation based on saccade directions. Second, we found that LIP neurons exhibited similar levels of activity in both the CT and IT conditions (Figure 2L), which is inconsistent with the presence of clear saccade direction selectivity.

Some more specific comments are below:

- I had a bit of a hard time with the abstract. It does not appear to be crystal clear to me, and it is the first thing that I am reading after the title. For example, if there is a claim about both perceptual decision-making and later target selection, then I feel that the task should be explained a bit more clearly than saying "flexible decision" task. Also, "..modulated by monkeys' following saccade choices directing outside each neuron's response field" was hard to read. It needs to be rewritten. Maybe just say "...modulated by the subsequent eye movement choices, even when these eye movement choices always directed the eyes away from the recorded neuron's response field". Also, I don't fully understand what "selectivity-specific feedback" means. Then, the concept of "consistency" in flexible decisions is brought up, again without much context. The above are examples of why I had a hard time with the abstract.

We realize that our original statement may have been unclear and potentially caused confusion for the readers. Following the reviewer’s suggestions, we have revised the abstract as follows:

‘Neural activity in the primate brain correlates with both sensory evaluation and action selection aspects of decision-making. However, the intricate interaction between these distinct neural processes and their impact on decision behaviors remains unexplored. Here, we examined the interplay of these decision processes in posterior parietal cortex (PPC) when monkeys performed a flexible decision task, in which they chose between two color targets based on a visual motion stimulus. We found that the PPC activity related to monkeys’ abstract decisions about visual stimuli was nonlinearly modulated by their subsequent saccade choices, which were directed outside each neuron’s response field. Recurrent neural network modeling indicated that the feedback connections, matching the learned stimuli-response associations during the task, might mediate such feedback modulation. Further analysis on network dynamics revealed that selectivity-specific feedback connectivity intensified the attractor basins of population activity underlying saccade choices, thereby increasing the reliability of flexible decisions. These results highlight an iterative computation between different decision processes, mediated primarily by precise feedback connectivity, contributing to the optimization of flexible decision-making.’

Specifically, selectivity-specific feedback refers to the feedback connections with positive or negative weights between selectivity-matched and selectivity-nonmatched unit pairs, respectively.

Regarding "decision consistency," we define it as the degree to which the model’s decisions remain congruent under specific conditions. A higher level of decision consistency indicates that the model is more likely to produce the same choice each time it is presented with a stimulus under those conditions, in another words, decision reliability. We have revised the corresponding results section to make these concepts clearer.

- Line 69: I'm not fully sure, but I think that some people might suggest that superior colliculus is also involved in the sensory aspect of the evaluation. But, I guess the sentence itself is correct as you write it. So, I don't think anyone should argue with it. However, if someone does argue with it, then they would flag the next sentence, since if the colliculus does both, then do the sensory and motor parts really employ distinct neural processes? Anyway, I think this is very minor.

This is an interesting point. We have also noticed a recent study that demonstrates that the superior colliculus is causally involved in the sensory aspect of decision-making, specifically in visual categorization. However, the study also distinguishes between neural activity related to categorical decisions and that related to saccade planning. This suggests that the sensory and motor aspects of decision-making likely involve distinct neural processing, even within the same brain region—potentially reflecting separate populations of neurons. Therefore, we stand by our statement in the ‘next sentence’.

- Line 79-80: you might want to look at this work because I feel that it is relevant to cite here: https://www.biorxiv.org/content/10.1101/2023.08.03.551852v2

We have discussed this reference in the revised discussion section of the manuscript, please refer to the above response.

- For a result like that shown in Fig. 2, I feel that it is important to show RF mapping with a saccade task alone. i.e. for the same neurons, have a monkey make a delayed visually guided saccade task to all possible locations on the display, and demonstrate that there is no modulation by saccades to the targets. Otherwise, the result in Fig. 2 could reflect first an onset response by a motion, and then the saccade-related response that would happen anyway, even without the decision task. So, I feel that now, it is not entirely clear whether the result reflects this so-called feedback modulation, or whether simply planning the saccade to the target itself activates the neurons. With large RF's, this is a distinct possibility in my opinion.

- Line 174: this would also be predicted if the neuron's were responding based on the saccade target plan independent of the motion stimulus

- On a related note, I would recommend plotting all data also aligned on saccade onset. This can help establish what the cause of the effects described is

We understand the reviewer’s concern that the modulation might be related to saccade planning, and we acknowledge that the original manuscript might not adequately address this potential confound. Unfortunately, we did not map the LIP neurons' receptive fields (RFs) using a saccade-only task. However, as mentioned earlier, we believe that the modulation of LIP neurons' responses to motion stimuli based on saccade choice direction cannot be simply attributed to saccade direction selectivity. Several lines of evidence support this conclusion. First, the modulation we observed was nonlinear: the firing rate of neurons increased for the preferred motion direction but decreased for the non-preferred motion direction (Figure 2i and Figure S1A-D). This pattern is inconsistent with a simple linear gain modulation driven by saccade direction selectivity. Second, we directly compared LIP neuronal activity for contralateral and ipsilateral target conditions, and found no significant differences between the two. This suggests that saccade direction selectivity is unlikely to be the primary contributor to the observed modulation. In the revised figure, we added a plot (Figure 2L) that aligns neural activity to saccade onset, in addition to the original alignment to motion stimulus onset (Figure S1E). This new analysis further supports our interpretation.

Author response image 7.

- Even when reading the simulation results, I'm still not 100% sure I understand what is meant by this idea of "consistency" of flexible decision-making

We have addressed this issue in a previous comment and please refer to the response above.

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):

The authors of this study use electron microscopy and 3D reconstruction techniques to study the morphology of distinct classes of Drosophila sensory neurons *across many neurons of the same class.* This is a comprehensive study attempting to look at nearly all the sensory neurons across multiple sensilla to determine a) how much morphological variability exists between and within neurons of different and similar sensory classes, and 2) identify dendritic features that may have evolved to support particular sensory functions. This study builds upon the authors' previous work, which allowed them to identify and distinguish sensory neuron subtypes in the EM volumes without additional staining so that reconstructed neurons could reliably be placed in the appropriate class. This work is unique in looking at a large number of individual neurons of the same class to determine what is consistent and what is variable about their class-specific morphologies.

This means that in addition to providing specific structural information about these particular cells, the authors explore broader questions of how much morphological diversity exists between sensory neurons of the same class and how different dendritic morphologies might affect sensory and physiological properties of neurons.

The authors found that CO2-sensing neurons have an unusual, sheet-like morphology in contrast to the thin branches of odor-sensing neurons. They show that this morphology greatly increases the surface area to volume ratio above what could be achieved by modest branching of thin dendrites, and posit that this might be important for their sensory function, though this was not directly tested in their study. The study is mainly descriptive in nature, but thorough, and provides a nice jumping-off point for future functional studies. One interesting future analysis could be to examine all four cell types within a single sensilla together to see if there are any general correlations that could reveal insights about how morphology is determined and the relative contributions of intrinsic mechanisms vs interactions with neighboring cells. For example, if higher than average branching in one cell type correlated with higher than average branching in another type, if in the same sensilla. This might suggest higher extracellular growth or branching cues within a sensilla. Conversely, if higher branching in one cell type consistently leads to reduced length or branching in another, this might point to dendrite-dendrite interactions between cells undergoing competitive or repulsive interactions to define territories within each sensilla as a major determinant of the variability.

We thank the reviewer for the insightful comments and appreciation for our study.

Reviewer #2 (Public Review):

The manuscript employs serial block‐face electron microscopy (SBEM) and cryofixation to obtain high‐resolution, three‐dimensional reconstructions of Drosophila antennal sensilla containing olfactory receptor neurons (ORNs) that detectCO2. This method has been used previously by the same lab in Gonzales et. al, 2021. (https://elifesciences.org/articles/69896), which had provided an exemplary model by integrating high-resolution EM with electrophysiology and cell-type-specific labeling.

We thank the reviewer for expressing appreciation for our published study.

The previous study ended up correlating morphology with activity for multiple olfactory sensillar types. Compared to the 2021 study, this current manuscript appears somewhat incomplete and lacks integration with activity.

We thank the reviewer for their feedback. However, we would like to clarify that our previous study did not correlate morphology with activity to a greater extent than the current study. Both employed the same cryofixation, SBEM-based approach without recording odor-induced activity, but the focus of the current work is fundamentally different. While the previous study examined multiple sensillum types, the current study concentrates on a single sensillum type to address a distinct biological question regarding morphological heterogeneity. We appreciate the opportunity to clarify this distinction, and we hope that the revised manuscript more clearly conveys the unique scope and contributions of this study.

In fact older studies have also reported two-dimensional TEM images of the putative CO2 neuron in Drosophila (Shanbhag et al., 1999) and in mosquitoes (McIver and Siemicki, 1975; Lu et al, 2007), and in these instances reported that the dendritic architecture of the CO2 neuron was somewhat different (circular and flattened, lamellated) from other olfactory neurons.

We thank the reviewer for pointing this out. As noted in both the Introduction and Discussion sections, previous studies—including those cited by the reviewer—suggested that CO2-sensing neurons may have a distinct dendritic morphology. However, those earlier studies lacked the means to definitively link the observed morphology to CO2 neuron identity.

In contrast, our study assigns neuronal identity based on quantitative morphometric measurements, allowing us to confidently associate the unique dendritic architecture with CO2 neurons. Furthermore, we extend previous observations by providing full 3D reconstructions and nanoscale morphometric analyses, offering a much more comprehensive and definitive characterization of these neurons. We believe this represents a significant advancement over earlier work.

The authors claim that this approach offers an artifact‐minimized ultrastructural dataset compared to earlier. In this study, not only do they confirm this different morphology but also classify it into distinct subtypes (loosely curled, fully curled, split, and mixed). This detailed morphological categorization was not provided in prior studies (e.g., Shanbhag et al., 1999).

We thank the reviewer for acknowledging the significance of our study.

The authors would benefit from providing quantitative thresholds or objective metrics to improve reproducibility and to clarify whether these structural distinctions correlate with distinct functional roles.

We thank the reviewer for raising this point. However, we would like to clarify that assigning neurons to strict morphological subtypes was not the primary aim of our study. In practice, dendritic architectures can be highly complex, with individual neurons often displaying features characteristic of multiple subtypes. This is precisely why we included a “mixed” subtype category—to acknowledge and capture this morphological heterogeneity rather than impose rigid classification boundaries.

Our intent in defining subtypes was not to imply discrete functional classes, but rather to highlight the range of morphological variation observed across ab1C neurons. While we agree that exploring potential correlations between structure and function is an important future direction, the current study focuses on characterizing this diversity using 3D reconstruction and morphometric analysis. We hope this clarifies the purpose and scope of our morphological categorization.

Strengths:

The study makes a convincing case that ab1C neurons exhibit a unique, flattened dendritic morphology unlike the cylindrical dendrites found in ab1D neurons. This observation extends previous qualitative TEM findings by not only confirming the presence of flattened lamellae in CO₂ neurons but also quantifying key morphometrics such as dendritic length, surface area, and volume, and calculating surface area-to-volume ratios. The enhanced ratios observed in the flattened segments are speculated to be linked to potential advantages in receptor distribution (e.g., Gr21a/Gr63a) and efficient signal propagation.

We thank the reviewer for appreciating the significance our current study.

Weaknesses:

While the manuscript offers valuable ultrastructural insights and reveals previously unappreciated heterogeneity among CO₂-sensing neurons, several issues warrant further investigation in addition to the points made above.

(1) Although this quantitative approach is robust compared to earlier descriptive reports, its impact is somewhat limited by the absence of direct electrophysiological data to confirm that ultrastructural differences translate into altered neuronal function. A direct comparison or discussion of how the present findings align with the functional data obtained from electrophysiology would strengthen the overall argument.

We thank the reviewer for this comment. We would like to clarify, however, that our study does not claim that the observed morphological heterogeneity necessarily leads to functional diversity. Rather, we consider this as a possible implication and discuss it as a potential question for future research. This idea is raised only in the Discussion section, and we are carefully not to present functional diversity as a conclusion of our study. Nonetheless, we have reviewed the relevant paragraph to ensure the language remains cautious and does not overstate our interpretation.

We also acknowledge the significance of directly linking ultrastructural features to neuronal function through electrophysiological recordings. However, at present, it is technically challenging to correlate the nanoscale morphology of individual ORNs with their functional activity, as this would require volume EM imaging of the very same neurons that were recorded via electrophysiology. Currently, there is no dye-labeling method compatible with single-sensillum recording and SBEM sample preparation that allows for unambiguous identification and segmentation of recorded ORNs at the necessary ultrastructural resolution.

To acknowledge this important limitation, we have added a paragraph in the Discussion section, as suggested, to clarify the current technical barriers and to highlight this as a promising direction for future methodological advances.

(2) Clarifying the criteria for dendritic subtype classification with quantitative parameters would enhance reproducibility and interpretability. Moreover, incorporating electrophysiological recordings from ab1C neurons would provide compelling evidence linking structure and function, and mapping key receptor proteins through immunolabeling could directly correlate receptor distribution with the observed morphological diversity.

Please see our response to the comment regarding the technical limitations of directly correlating ultrastructure with electrophysiological data.

In addition, we would like to address the suggestion of using immunolabeling to map receptor distribution in relation to the 3D EM models. Currently, antibodies against Gr21a or Gr63a (the receptors expressed in ab1C neurons) are not available. Even if such antibodies were available, immunogold labeling for electron microscopy requires harsh detergent treatment to increase antibody permeability, damaging morphological integrity. These treatments would compromise the very morphological detail that our study aims to capture and quantify.

(3) Even though Cryofixation is claimed to be superior to chemical fixation for generating fewer artifacts, authors need to confirm independently the variation observed in the CO2 neuron morphologies across populations. All types of fixation in TEMs cause some artifacts, as does serial sectioning. Without understanding the error rates or without independent validation with another method, it is hard to have confidence in the conclusions drawn by the authors of the paper.

We thank the reviewer for raising concerns regarding potential artifacts in morphological analyses. However, we would like to clarify that cryofixation is widely regarded as a gold standard for ultrastructural preservation and minimizing fixation-induced artifacts, as supported by extensive literature. This is why we adopted high-pressure freezing and freeze substitution in our study.

We have also published a separate methods paper (Tsang et al., eLife, 2018) directly comparing our cryofixation-based protocol with conventional chemical fixation, demonstrating substantial improvements in morphological preservation. This provides strong empirical support for the reliability of our approach.

Regarding the suggestion to validate observed morphological variation across populations: we note that determining the presence of artifacts requires a known ground truth, which is inherently unavailable as we could not measure the morphometrics of fly olfactory receptor neurons in their native state. In the absence of such a benchmark, we have instead prioritized using the best-available preparation methods and high-resolution imaging to ensure structural integrity.

Addressing these concerns and integrating additional experiments would significantly bolster the manuscript's completeness and advancement.

We appreciate the reviewer’s feedback. As discussed in our responses to the specific comments above, certain suggested experiments are currently limited by technical constraints, particularly in the context of high-resolution volume EM for insect tissues enclosed in cuticles.

Nevertheless, we have carefully addressed the reviewer’s concerns to the fullest extent possible within the scope of this study. We have revised the manuscript to clarify methodological limitations, added new explanatory content where appropriate, and ensured that our interpretations remain well grounded in the data. We hope these revisions strengthen the clarity and completeness of the manuscript.

Reviewer #3 (Public Review):

In the current manuscript entitled "Population-level morphological analysis of paired CO2- and odor-sensing olfactory neurons in D. melanogaster via volume electron microscopy", Choy, Charara et al. use volume electron microscopy and sensillum. They aim to investigate the degree of dendritic heterogeneity within a functional class of neurons using ab1Cand ab1D, which they can identify due to the unique feature of ab1 sensilla to house four neurons and the stereotypic location on the third antennal segment. This is a great use of volumetric electron imaging and neuron reconstruction to sample a population of neurons of the same type. Their data convincingly shows that there is dendritic heterogeneity in both investigated populations, and their sample size is sufficient to strongly support this observation. This data proposes that the phenomenon of dendritic heterogeneity is common in the Drosophila olfactory system and will stimulate future investigations into the developmental origin, functional implications, and potential adaptive advantage of this feature.

Moreover, the authors discovered that there is a difference between CO2- and odour-sensing neurons of which the first show a characteristic flattened and sheet-like structure not observed in other sensory neurons sampled in this and previous studies. They hypothesize that this unique dendritic organization, which increases the surface area to volume ratio, might allow more efficient CO2 sensing by housing higher numbers of CO2 receptors. This is supported by previous attempts to express CO2 sensors in olfactory sensory neurons, which lack this dendritic morphology, resulting in lower CO2 sensitivity compared to endogenous neurons.

Overall, this detailed morphological description of olfactory sensory neurons' dendrites convincingly shows heterogeneity in two neuron classes with potential functional impacts for odour sensing.

Strength:

The volumetric EM imaging and reconstruction approach offers unprecedented details in single cell morphology and compares dendrite heterogeneity across a great fraction of ab1 sensilla. The authors identify specific shapes for ab1C sensilla potentially linked to their unique function in CO2 sensing.

We thank the reviewer for the insightful comments and appreciation for our study.

Weaknesses:

While the morphological description is highly detailed, no attempts are made to link this to odour sensitivity or other properties of the neurons. It would have been exciting to see how altered morphology impacts physiology in these olfactory sensory cells.

We agree that linking morphological variation to physiological properties, such as odor sensitivity, would be a highly valuable direction for future research. However, the aim of the current study is to provide an in-depth nanoscale characterization based on a substantial proportion of ab1 sensilla, highlighting morphological heterogeneity among homotypic ORNs.

At present, it is technically challenging to correlate the nanoscale morphology of individual ORNs with their physiological responses, as this would require volume EM imaging of the exact neurons recorded via single-sensillum electrophysiology. Currently, no dye-labeling method exists that is compatible with both single-sensillum recording and the stringent requirements of SBEM sample preparation to allow for unambiguous identification and segmentation of recorded ORNs.

To acknowledge this important limitation, we have added a paragraph in the Discussion section clarifying the current technical barriers and highlighting this as a promising area for future methodological development. Please also see our responses to the reviewer’s 4th comment below, where we present preliminary experiments examining whether odor sensitivity varies among homotypic ORNs.

(Please see the following pages for additional responses to the reviewers’ specific comments. These responses are not intended for publication.)

Reviewer #1 (Recommendations for the authors):

As this is mainly a descriptive paper I have no suggestions for additional experiments. Minor Text Suggestions:

(1) The authors might want to include a better description/definition of the fly antennae, olfactory sensilla and their basic structure/makeup, position of the sensory neurons and dendrites within, etc, in the introduction perhaps in cartoon form to help readers that are not familiar (i.e. non-Drosophila readers) with the terminology and basic organization can follow the paper more easily from the start.

We thank the reviewer for the helpful suggestion to broaden the appeal of our study to a wider readership. In response, we added a new introductory paragraph at the beginning of the Results section, along with illustrations in a new supplementary figure (Figure 1—figure supplement 1). The new paragraph reads as follows.

“The primary olfactory organ in Drosophila is the antenna, which contains hundreds olfactory sensilla on the surface of its third segment (Figure 1—figure supplement 1A) . Each sensillum typically encapsulates the outer dendrites of two to four ORNs. The outer dendrites are the sites where odorant receptors are expressed, enabling the detection of volatile chemicals. A small portion of the outer dendrites lies beneath the base of the sensillum cuticle. At the ciliary constriction, the outer dendrites connect to the inner dendritic segment, which then links to the soma of each ORN (Figure 1—figure supplement 1B).”

(2) In Figure 4D, the letter annotations above the graphs are not clearly defined anywhere that I could easily find. Please clarify with different symbols and/or in the figure legend so readers can easily comprehend the stats that are presented.

We thank the reviewer for raising this point. As suggested, in the revised Figure 4D legend, following the original sentence “Statistical significance is determined by Kruskal-Wallis one-way ANOVA on ranks and denoted by different letters”, we added “For example, labels “a” and “b” indicate a significant difference between groups (P < 0.05), whereas labels with identical or shared letters (e.g., “a” and “a”, “a,b” and “a”, or “a,b” and “b”) indicate no significant difference.”

Reviewer #3 (Recommendations for the authors):

There are several aspects that I would like the authors to consider to improve the current manuscript:

(1) Line 331: "Our analysis highlights how structural scaling in ab1D neurons achieves enhanced sensory capacity while maintaining the biophysical properties of dendrites". This is a strong statement, and not shown by the authors. They speculate about this in the discussion, but I would like them to soften the language here.

We thank the reviewer for raising this point. As suggested, we have softened the language in the sentence in question. The revised version is as follows.

“Our analysis suggests that structural scaling in ab1D neurons may enhance sensory capacity while preserving the biophysical properties of dendrites.”

(2) The Supplementary material is not well presented and is not cited in the manuscript. It is not clear what the individual data files show, where they refer to, etc. Please provide clear labels of all data, cite them at the appropriate location in the manuscript, and make them more accessible to the reader. Also, there are two Videos mentioned in the manuscript that are not included in the submission.

We thank the reviewer for bringing this to our attention and apologize for the oversight. We appreciate the reviewer’s careful attention to the supplementary materials. We have addressed these issues accordingly: 1) all source data have been consolidated in to a single, clearly labeled Excel file to improve accessibility for readers; this file is now cited at the appropriate locations in the manuscript. 2) The supplementary videos mentioned in the manuscript have also been included in the re-submission.

(3) In Figure 1B, it is hard to recapitulate the increase in dendritic density in the presented pictures. Could the authors please highlight dendrites in the raw imaging files (e.g. by colour coding as done later in the manuscript). Also, it might be helpful to indicate the measured parameters visually in this Figure (e.g. volume, length, etc.).

We thank the reviewer for the helpful suggestion. As suggested, we have pseudocolored the dendrites in Figure 1B to enhance visual clarity.

As noted, the original legend stated that “the sensilla were arranged from left to right in order of increasing dendritic branch counts”. To improve clarity, we have now added the number of dendritic branches above each sensillum to make this information more explicit.

We hope these changes make the figure more accessible and informative for readers.

(4) Given the strength of the authors in in vivo physiology and single sensilla recordings, I would be very curious about how the described morphological heterogeneity is reflected in the response properties of ab1Cs and ab1Ds. Can the authors provide data (already existing from their lab) of these two neurons on response heterogeneity? I acknowledge that spike sorting can be very challenging in ab1s, but maybe it is possible to show the range of response sensitivities upon CO2 stimulation in ab1Cs? The authors speculate in the discussion and presented data will only be correlative - however I think it would strengthen the manuscript to have some link to physiology included.

We thank the reviewer for this insightful comment. We share the same curiosity about response variability among homotypic ORNs, including ab1C and ab1D. Ideally, this question could be addressed by recording from a large proportion of neurons of a given ORN type to assess the response variability within a single antenna. However, due to technical limitations, we are only able to reliably record from 3–4 ab1 sensilla per antennal preparation, representing approximately 8% of the total ab1 population.

Moreover, our recordings are typically limited to ab1 sensilla located on the posterior-medial side of the antenna, as this region provides the best accessibility for our recording electrode. This spatial constraint may limit our ability to sample the full morphological diversity of ab1C and ab1D neurons.

Given these limitations, it is technically challenging to rigorously assess physiological variability in ab1C and ab1D responses across the entire ab1 population. Nonetheless, we attempted to address this question using a different sensillum type where a larger proportion of the population is accessible to single-sensillum recording per antennal preparation. Specifically, we focused on ab2 sensilla in the following analysis because we can reliably record from 6 sensilla per antenna, representing approximately 25% of the total ab2 population.

In the preliminary data presented below, we recorded from 6 ab2A ORNs per antenna across a total of 6 flies. Spike analysis revealed that odor-evoked responses were consistent across individual ab2A neurons (Author response image 1A). When analyzing the dose-response curve for each ORN, we found no statistically significant differences in odor sensitivity, either among ORNs within the same antenna or across different flies (Author response image 1B; two-way ANOVA: P > 0.99 within antennae, P > 0.99 across flies). This is further supported by the closely clustered EC50 values (Author response image 1C). This result suggests that odor sensitivity is largely uniform among homotypic ab2A ORNs.

Author response image 1.

Homotypic ab2A ORNs display similar odorant sensitivity. (A) Single-sensillum recording. Raster plots of ab2A/Or59b ORN spike responses. Six ab2A ORNs from the same antenna were recorded per fly. Odor stimulus: methyl acetate (10-6). (B) Dose-response relationships of peak spike responses, normalized to the maximum response of the ORN to facilitate comparison of odor sensitivity. Each curve represents responses from a single ab2A ORN fitted with the Hill equation (n=36 ab2 sensilla from 6 flies). Responses recorded from the same antenna are indicated by the same color. Statistical comparisons between different ab2A ORNs from the same antenna (P > 0.99) or across flies (P > 0.99) were performed by two-way ANOVA. (C) Quantification of individual pEC50 values from (B), defined as -logEC50.

However, we are hesitant to include this result in the main manuscript for several reasons. First, it does not directly relate to the morphometric analysis of ab1C and ab1D neurons, which is the primary focus of our study. Second, while we were able to record from approximately 25% of the ab2 population, this level of coverage is still limited and potentially subject to sampling bias due to the spatial constraints of the antennal region accessible to the recording electrode.

At best, our data suggest limited variability in odor sensitivity among the recorded ab2A ORNs. However, we are cautious about generalizing this finding to the entire ab2 population. In light of these considerations, we hope the reviewer can appreciate the technical challenges inherent in addressing what may appear to be a straightforward question.

For these reasons, we have chosen to include this preliminary result in the response only, rather than in the main manuscript.

Author response: 

We thank the reviewers for their feedback on our paper. We have taken all their comments into account in revising the manuscript. We provide a point-by-point response to their comments, below.

Reviewer #1:

Major comments:

The manuscript is clearly written with a level of detail that allows others to reproduce the imaging and cell-tracking pipeline. Of the 22 movies recorded one was used for cell tracking. One movie seems sufficient for the second part of the manuscript, as this manuscript presents a proof-of-principle pipeline for an imaging experiment followed by cell tracking and molecular characterisation of the cells by HCR. In addition, cell tracking in a 5-10 day time-lapse movie is an enormous time commitment.

My only major comment is regarding "Suppl_data_5_spineless_tracking". The image file does not load.

It looks like the wrong file is linked to the mastodon dataset. The "Current BDV dataset path" is set to "Beryl_data_files/BLB mosaic cut movie-02.xml", but this file does not exist in the folder. Please link it to the correct file.

We have corrected the file path in the updated version of Suppl. Data 5.

Minor comments:

The authors state that their imaging settings aim to reduce photo damage. Do they see cell death in the regenerating legs? Is the cell death induced by the light exposure or can they tell if the same cells die between the movies? That is, do they observe cell death in the same phases of regeneration and/or in the same regions of the regenerating legs?

Yes, we observe cell death during Parhyale leg regeneration. We have added the following sentence to explain this in the revised manuscript: "During the course of regeneration some cells undergo apoptosis (reported in Alwes et al., 2016). Using the H2B-mRFPruby marker, apoptotic cells appear as bright pyknotic nuclei that break up and become engulfed by circulating phagocytes (see bright specks in Figure 2F)."

We now also document apoptosis in regenerated legs that have not been subjected to live imaging in a new supplementary figure (Suppl. Figure 3),  and we refer to these observations as follows: "While some cell death might be caused by photodamage, apoptosis can also be observed in similar numbers in regenerating legs that have not been subjected to live imaging (Suppl. Figure 3)."

Based on 22 movies, the authors divide the regeneration process into three phases and they describe that the timing of leg regeneration varies between individuals. Are the phases proportionally the same length between regenerating legs or do the authors find differences between fast/slow regenerating legs? If there is a difference in the proportions, why might this be?

Both early and late phases contribute to variation in the speed of regeneration, but there is no clear relationship between the relative duration of each phase and the speed of regeneration. We now present graphs supporting these points in a new supplementary figure (Suppl. Figure 2).  

To clarify this point, we have added the following sentence in the manuscript: "We find that the overall speed of leg regeneration is determined largely by variation in the speed of the early (wound closure) phase of regeneration, and to a lesser extent by variation in later phases when leg morphogenesis takes place (Suppl. Figure 2 A,B). There is no clear relationship between the relative duration of each phase and the speed of regeneration (Suppl. Figure 2 A',B')."

Based on their initial cell tracing experiment, could the authors elaborate more on what kind of biological information can be extracted from the cell lineages, apart from determining which is the progenitor of a cell? What does it tell us about the cell population in the tissue? Is there indication of multi- or pluripotent stem cells? What does it say about the type of regeneration that is taking place in terms of epimorphosis and morphallaxis, the old concepts of regeneration?

In the first paragraph of Future Directions we describe briefly the kind of biological information that could be gained by applying our live imaging approach with appropriate cell-type markers (see below). We do not comment further, as we do not currently have this information at hand. Regarding the concepts of epimorphosis and morphallaxis, as we explain in Alwes et al. 2016, these terms describe two extreme conditions that do not capture what we observe during Parhyale leg regeneration. Our current work does not bring new insights on this topic.

Page 5. The authors mention the possibility of identifying the cell ID based on transcriptomic profiling data. Can they suggest how many and which cell types they expect to find in the last stage based on their transcriptomic data?

We have added this sentence: "Using single-nucleus transcriptional profiling, we have identified approximately 15 transcriptionally-distinct cell types in adult Parhyale legs (Almazán et al., 2022), including epidermis, muscle, neurons, hemocytes, and a number of still unidentified cell types."

Page 6. Correction: "..molecular and other makers.." should be "..molecular and other markers.."

Corrected

Page 8. The HCR in situ protocol probably has another important advantage over the conventional in situ protocol, which is not mentioned in this study. The hybridisation step in HCR is performed at a lower temperature (37˚C) than in conventional in situ hybridisation (65˚C, Rehm et al., 2009). In other organisms, a high hybridisation temperature affects the overall tissue morphology and cell location (tissue shrinkage). A lower hybridisation temperature has less impact on the tissue and makes manual cell alignment between the live imaging movie and the fixed HCR in situ stained specimen easier and more reliable. If this is also the case in Parhyale, the authors must mention it.

This may be correct, but all our specimens were treated at 37˚C, so we cannot assess whether hybridisation temperature affects morphological preservation in our specimens.

Page 9. The authors should include more information on the spineless study. What been is spineless? What do the cell lineages tell about the spineless progenitors, apart from them being spread in the tissue at the time of amputation? Do spineless progenitors proliferate during regeneration? Do any spineless expressing cells share a common progenitor cell?

We now point out that spineless encodes a transcription factor. We provide a summary of the lineages generating spineless-expressing cells in Suppl. Figure 6, and we explain that "These epidermal progenitors undergo 0, 1 or 2 cell divisions, and generate mostly spineless-expressing cells (Suppl. Figure 5)."

Page 10. Regarding the imaging temperature, the Materials and Methods state "... a temperature control chamber set to 26 or 27˚C..."; however, in Suppl. Data 1, 26˚C and 29˚C are indicated as imaging temperatures. Which is correct?

We corrected the Methods by adding "with the exception of dataset li51, imaged at 29°C"

Page 10. Regarding the imaging step size, the Materials and Methods state "...step size of 1-2.46 µm..."; however, Suppl. Data 1 indicate a step size between 1.24 - 2.48 µm. Which is correct?

We corrected the Methods.

Page 11. Correct "...as the highest resolution data..." to "...at the highest resolution data..."

The original text is correct ("standardised to the same dimensions as the highest resolution data").

Page 11. Indicate which supplementary data set is referred to: "Using Mastodon, we generated ground truth annotations on the original image dataset, consisting of 278 cell tracks, including 13,888 spots and 13,610 links across 55 time points (see Supplementary Data)."

Corrected

p. 15. Indicate which supplementary data set is referred to: "In this study we used HCR probes for the Parhyale orthologues of futsch (MSTRG.441), nompA (MSTRG.6903) and spineless (MSTRG.197), ordered from Molecular Instruments (20 oligonucleotides per probe set). The transcript sequences targeted by each probe set are given in the Supplementary Data."

Corrected

Figure 3. Suggestion to the overview schematics: The authors might consider adding "molting" as the end point of the red bar (representing differentiation).

The time of molting is not known in the majority of these datasets, because the specimens were fixed and stained prior to molting. We added the relevant information in the figure legend: "Datasets li-13 and li-16 were recorded until the molt; the other recordings were stopped before molting."

Figure 4B': Please indicate that the nuclei signal is DAPI.

Corrected

Supplementary figure 1A. Word is missing in the figure legend: ...the image also shows weak…

Corrected

Supplementary Figure 2: Please indicate the autofluorescence in the granular cells. Does it correspond to the yellow cells?

Corrected

Video legend for video 1 and 2. Please correct "H2B-mREFruby" to "H2B-mRFPruby".

Corrected

Reviewer #2:

Major comments:

MC 1. Given that most of the technical advances necessary to achieve the work described in this manuscript have been published previously, it would be helpful for the authors to more clearly identify the primary novelty of this manuscript. The abstract and introduction to the manuscript focus heavily on the technical details of imaging and analysis optimization and some additional summary of the implications of these advances should be included here to aid the reader.

This paper describes a technical advance. While previous work (Alwes et al. 2016) established some key elements of our live imaging approach, we were not at that time able to record the entire time course of leg regeneration (the longest recordings were 3.5 days long). Here we present a method for imaging the entire course of leg regeneration (up to 10 days of imaging), optimised to reduce photodamage and to improve cell tracking. We also develop a method of in situ staining in cuticularised adult legs (an important technical breakthrough in this experimental system), which we combine with live imaging to determine the fate of tracked cells. We have revised the abstract and introduction of the paper to point out these novelties, in relation to our previous publications.

In the abstract we explain: "Building on previous work that allowed us to image different parts of the process of leg regeneration in the crustacean Parhyale hawaiensis, we present here a method for live imaging that captures the entire process of leg regeneration, spanning up to 10 days, at cellular resolution. Our method includes (1) mounting and long-term live imaging of regenerating legs under conditions that yield high spatial and temporal resolution but minimise photodamage, (2) fixing and in situ staining of the regenerated legs that were imaged, to identify cell fates, and (3) computer-assisted cell tracking to determine the cell lineages and progenitors of identified cells. The method is optimised to limit light exposure while maximising tracking efficiency."

The introduction includes the following text: "Our first systematic study using this approach presented continuous live imaging over periods of 2-3 days, capturing key events of leg regeneration such as wound closure, cell proliferation and morphogenesis of regenerating legs with single-cell resolution (Alwes et al., 2016). Here, we extend this work by developing a method for imaging the entire course of leg regeneration, optimised to reduce photodamage and to improve cell tracking. We also develop a method of in situ staining of gene expression in cuticularised adult legs, which we combine with live imaging to determine the fate of tracked cells."

MC 2. The description of the regeneration time course is nicely detailed but also very qualitative. A major advantage of continuous recording and automated cell tracking in the manner presented in this manuscript would be to enable deeper quantitative characterization of cellular and tissue dynamics during regeneration. Rather than providing movies and manually annotated timelines, some characterization of the dynamics of the regeneration process (the heterogeneity in this is very very interesting, but not analyzed at all) and correlating them against cellular behaviors would dramatically increase the impact of the work and leverage the advances presented here. For example, do migration rates differ between replicates? Division rates? Division synchrony? Migration orientation? This seems to be an incredibly rich dataset that would be fascinating to explore in greater detail, which seems to me to be the primary advance presented in this manuscript. I can appreciate that the authors may want to segregate some biological findings from the method, but I believe some nominal effort highlighting the quantitative nature of what this method enables would strengthen the impact of the paper and be useful for the reader. Selecting a small number of simple metrics (eg. Division frequency, average cell migration speed) and plotting them alongside the qualitative phases of the regeneration timeline that have already been generated would be a fairly modest investment of effort using tools that already exist in the Mastodon interface, I would roughly estimate on the order of an hour or two per dataset. I believe that this effort would be well worth it and better highlight a major strength of the approach.

The primary goal of this work was to establish a robust method for continuous long-term live imaging of regeneration, but we do appreciate that a more quantitative analysis would add value to the data we are presenting. We tried to address this request in three steps:

First, we examined whether clear temporal patterns in cell division, cell movements or other cellular features can be observed in an accurately tracked dataset (li13-t4, tracked in Sugawara et al. 2022). To test this we used the feature extraction functions now available on the Mastodon platform (see link). We could discern a meaningful temporal pattern for cell divisions (see below); the other features showed no interpretable pattern of variation.

Second, we asked whether we could use automated cell tracking to analyse the patterns of cell division in all our datasets. Using an Elephant deep learning model trained on the tracks of the li13-t4 dataset, we performed automated cell tracking in the same dataset, and compared the pattern of cell divisions from the automated cell track predictions with those coming from manually validated cell tracks. We observed that the automated tracks gave very imprecise results, with a high background of false positives obscuring the real temporal pattern (see images below, with validated data on the left, automated tracking on the right). These results show that the automated cell tracking is not accurate enough to provide a meaningful picture on the pattern of cell divisions.

Third, we tried to improve the accuracy of detection of dividing cells by additional training of Elephant models on each dataset (to lower the rate of false positives), followed by manual proofreading. Given how labour intensive this is, we could only apply this approach to 4 additional datasets. The results of this analysis are presented in Figure 4.

Author response image 1.

MC 3. The authors describe the challenges faced by their described approach:

Using this mode of semi-automated and manual cell tracking, we find that most cells in the upper slices of our image stacks (top 30 microns) can be tracked with a high degree of confidence. A smaller proportion of cell lineages are trackable in the deeper layers.

Given that the authors quantify this in Table 1, it would aid the reader to provide metrics in the manuscript text at this point. Furthermore, the metrics provided in Table 1 appear to be for overall performance, but the text describes that performance appears to be heavily depth dependent. Segregating the performance metrics further, for example providing DET, TRA, precision and recall for superficial layers only and for the overall dataset, would help support these arguments and better highlight performance a potential adopter of the method might expect.

In the revised manuscript we have added data on the tracking performance of Elephant in relation to imaging depth in Suppl. Figure 3. These data confirm our original statement (which was based on manual tracking) that nuclei are more challenging to track in deeper layers.

We point to these new results in two parts of the paper, as follows: "A smaller proportion of cells are trackable in the deeper layers (see Suppl. Figure 3)", and "Our results, summarised in Table 1A, show that the detection of nuclei can be enhanced by doubling the z resolution at the expense of xy resolution and image quality. This improvement is particularly evident in the deeper layers of the imaging stacks, which are usually the most challenging to track (Suppl. Figure 3)."

MC 4. Performance characterization in Table 1 appears to derive from a single dataset that is then subsampled and processed in different ways to assess the impact of these changes on cell tracking and detection performance. While this is a suitable strategy for this type of optimization it leaves open the question of performance consistency across datasets. I fully recognize that this type of quantification can be onerous and time consuming, but some attempt to assess performance variability across datasets would be valuable. Manual curation over a short time window over a random sampling of the acquired data would be sufficient to assess this.

We think that similar trade-offs will apply to all our datasets because tracking performance is constrained by the same features, which are intrinsic to our system; e.g. by the crowding of nuclei in relation to axial resolution, or the speed of mitosis in relation to the temporal resolution of imaging. We therefore do not see a clear rationale for repeating this analysis. On a practical level, our existing image datasets could not be subsampled to generate the various conditions tested in Table 1, so proving this point experimentally would require generating new recordings, and tracking these to generate ground truth data. This would require months of additional work.

A second, related question is whether Elephant would perform equally well in detecting and tracking nuclei across different datasets. This point has been addressed in the Sugawara et al. 2022 paper, where the performance of Elephant was tested on diverse fluorescence datasets.

Reviewer #3:

Major comments:

• The authors should clearly specify what are the key technical improvements compared to their previous studies (Alwes et al. 2016, Elife; Konstantinides & Averof 2014, Science). There, the approaches for mounting, imaging, and cell tracking are already introduced, and the imaging is reported to run for up to 7 days in some cases.

In Konstantinides and Averof (2014) we did not present any live imaging at cellular resolution. In Alwes et al. (2016) we described key elements of our live imaging approach, but we were never able to record the entire time course of leg regeneration. The longest recordings in that work were 3.5 days long.

We have revised the abstract and introduction to clarify the novelty of this work, in relation to our previous publications. Please see our response to comment MC1 of reviewer 2.

• While the authors mention testing the effect of imaging parameters (such as scanning speed and line averaging) on the imaging/tracking outcome, very little or no information is provided on how this was done beyond the parameters that they finally arrived to.

Scan speed and averaging parameters were determined by measuring contrast and signal-to-noise ratios in images captured over a range of settings. We have now added these data in Supplementary Figure 1.

• The authors claim that, using the acquired live imaging data across entire regeneration time course, they are now able to confirm and extend their description of leg regeneration. However, many claims about the order and timing of various cellular events during regeneration are supported only by references to individual snapshots in figures or supplementary movies. Presenting a more quantitative description of cellular processes during regeneration from the acquired data would significantly enhance the manuscript and showcase the usefulness of the improved workflow.

The events we describe can be easily observed in the maximum projections, available in Suppl. Data 2. Regarding the quantitative analysis, please see our response to comment MC2 of reviewer 2.  

• Table 1 summarizes the performance of cell tracking using simulated datasets of different quality. However only averages and/or maxima are given for the different metrics, which makes it difficult to evaluate the associated conclusions. In some cases, only 1 or 2 test runs were performed.

The metrics extracted from each of the three replicates, per dataset, are now included in Suppl. Data 4.

We consistently used 3 replicates to measure tracking performance with each of the datasets. The "replicates" column label in Table 1 referred to the number of scans that were averaged to generate the image, not to the replicates used for estimating the tracking performance. To avoid confusion, we changed that label to "averaging".

• OPTIONAL: An imaging approach that allows using the current mounting strategy but could help with some of the tradeoffs is using a spinning-disk confocal microscope instead of a laser scanning one. If the authors have such a system available, it could be interesting to compare it with their current scanning confocal setup.

Preliminary experiments that we carried out several years ago on a spinning disk confocal (with a 20x objective and the CSU-W1 spinning disk) were not very encouraging, and we therefore did not pursue this approach further. The main problem was bad image quality in deeper tissue layers.

Minor comments:

• The presented imaging protocol was optimized for one laser wavelength only (561 nm) - this should be mentioned when discussing the technical limitations since animals tend to react differently to different wavelengths. Same settings might thus not be applicable for imaging a different fluorescent protein.

In the second paragraph of the Results section, we explain that we perform the imaging at long wavelengths in order to minimise photodamage. It should be clear to the readers that changing the excitation wavelength will have an impact for long-term live imaging.

• For transferability, it would be useful if the intensity of laser illumination was measured and given in the Methods, instead of just a relative intensity setting from the imaging software. Similarly,more details of the imaging system should be provided where appropriate (e.g., detector specifications).

We have now measured the intensity of the laser illumination and added this information in the

Methods: "Laser power was typically set to 0.3% to 0.8%, which yields 0.51 to 1.37 µW at 561 nm (measured with a ThorLabs Microscope Slide Power Sensor, #S170C)."

Regarding the imaging system and the detector, we provide all the information that is available to us on the microscope's technical sheets.

• The versions of analysis scripts associated with the manuscript should be uploaded to an online repository that permanently preserves the respective version.

The scripts are now available on gitbub and online repositories. The relevant links are included in the revised manuscript.

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:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The image analysis pipeline is tested in analysing microscopy imaging data of gastruloids of varying sizes, for which an optimised protocol for in toto image acquisition is established based on whole mount sample preparation using an optimal refractive index matched mounting media, opposing dual side imaging with two-photon microscopy for enhanced laser penetration, dual view registration, and weighted fusion for improved in toto sample data representation. For enhanced imaging speed in a two-photon microscope, parallel imaging was used, and the authors performed spectral unmixing analysis to avoid issues of signal cross-talk.

In the image analysis pipeline, different pre-treatments are done depending on the analysis to be performed (for nuclear segmentation - contrast enhancement and normalisation; for quantitative analysis of gene expression - corrections for optical artifacts inducing signal intensity variations). Stardist3D was used for the nuclear segmentation. The study analyses into properties of gastruloid nuclear density, patterns of cell division, morphology, deformation, and gene expression.

Strengths:

The methods developed are sound, well described, and well-validated, using a sample challenging for microscopy, gastruloids. Many of the established methods are very useful (e.g. registration, corrections, signal normalisation, lazy loading bioimage visualisation, spectral decomposition analysis), facilitate the development of quantitative research, and would be of interest to the wider scientific community.

We thank the reviewer for this positive feedback.

Weaknesses:

A recommendation should be added on when or under which conditions to use this pipeline.

We thank the reviewer for this valuable feedback, which will be addressed in the revision. In general, the pipeline is applicable to any tissue, but it is particularly useful for large and dense 3D samples—such as organoids, embryos, explants, spheroids, or tumors—that are typically composed of multiple cell layers and have a thickness greater than 50 µm.

The processing and analysis pipeline are compatible with any type of 3D imaging data (e.g. confocal, 2 photon, light-sheet, live or fixed).

- Spectral unmixing to remove signal cross-talk of multiple fluorescent targets is typically more relevant in two-photon imaging due to the broader excitation spectra of fluorophores compared to single-photon imaging. In confocal or light-sheet microscopy, alternating excitation wavelengths often circumvents the need for unmixing. Spectral decomposition performs even better with true spectral detectors; however, these are usually not non-descanned detectors, which are more appropriate for deep tissue imaging. Our approach demonstrates that simultaneous cross-talk-free four-color two-photon imaging can be achieved in dense 3D specimen with four non-descanned detectors and co-excitation by just two laser lines. Depending on the dispersion in optically dense samples, depth-dependent apparent emission spectra need to be considered.

- Nuclei segmentation using our trained StarDist3D model is applicable to any system under two conditions: (1) the nuclei exhibit a star-convex shape, as required by the StarDist architecture, and (2) the image resolution is sufficient in XYZ to allow resampling. The exact sampling required is object- and system-dependent, but the goal is to achieve nearly isotropic objects with diameters of approximately 15 pixels while maintaining image quality. In practice, images containing objects that are natively close to or larger than 15 pixels in diameter should segment well after resampling. Conversely, images with objects that are significantly smaller along one or more dimensions will require careful inspection of the segmentation results.

- Normalization is broadly applicable to multicolor data when at least one channel is expected to be ubiquitously expressed within its domain. Wavelength-dependent correction requires experimental calibration using either an ubiquitous signal at each wavelength. Importantly, this calibration only needs to be performed once for a given set of experimental conditions (e.g., fluorophores, tissue type, mounting medium).

- Multi-scale analysis of gene expression and morphometrics is applicable to any 3D multicolor image. This includes both the 3D visualization tools (Napari plugins) and the various analytical plots (e.g., correlation plots, radial analysis). Multi-scale analysis can be performed even with imperfect segmentation, as long as segmentation errors tend to cancel out when averaged locally at the relevant spatial scale. However, systematic errors—such as segmentation uncertainty along the Z-axis due to strong anisotropy—may accumulate and introduce bias in downstream analyses. Caution is advised when analyzing hollow structures (e.g., curved epithelial monolayers with large cavities), as the pipeline was developed primarily for 3D bulk tissues, and appropriate masking of cavities would be needed.

Reviewer #2 (Public review):

Summary:

This study presents an integrated experimental and computational pipeline for high-resolution, quantitative imaging and analysis of gastruloids. The experimental module employs dual-view two-photon spectral imaging combined with optimized clearing and mounting techniques to image whole-mount immunostained gastruloids. This approach enables the acquisition of comprehensive 3D images that capture both tissue-scale and single-cell level information.

The computational module encompasses both pre-processing of acquired images and downstream analysis, providing quantitative insights into the structural and molecular characteristics of gastruloids. The pre-processing pipeline, tailored for dual-view two-photon microscopy, includes spectral unmixing of fluorescence signals using depth-dependent spectral profiles, as well as image fusion via rigid 3D transformation based on content-based block-matching algorithms. Nuclei segmentation was performed using a custom-trained StarDist3D model, validated against 2D manual annotations, and achieving an F1 score of 85+/-3% at a 50% intersection-over-union (IoU) threshold. Another custom-trained StarDist3D model enabled accurate detection of proliferating cells and the generation of 3D spatial maps of nuclear density and proliferation probability. Moreover, the pipeline facilitates detailed morphometric analysis of cell density and nuclear deformation, revealing pronounced spatial heterogeneities during early gastruloid morphogenesis.

All computational tools developed in this study are released as open-source, Python-based software.

Strengths:

The authors applied two-photon microscopy to whole-mount deep imaging of gastruloids, achieving in toto visualization at single-cell resolution. By combining spectral imaging with an unmixing algorithm, they successfully separated four fluorescent signals, enabling spatial analysis of gene expression patterns.

The entire computational workflow, from image pre-processing to segmentation with a custom-trained StarDist3D model and subsequent quantitative analysis, is made available as open-source software. In addition, user-friendly interfaces are provided through the open-source, community-driven Napari platform, facilitating interactive exploration and analysis.

We thank the reviewer for this positive feedback.

Weaknesses:

The computational module appears promising. However, the analysis pipeline has not been validated on datasets beyond those generated by the authors, making it difficult to assess its general applicability.

We agree that applying our analysis pipeline to published datasets—particularly those acquired with different imaging systems—would be valuable. However, only a few high-resolution datasets of large organoid samples are publicly available, and most of these either lack multiple fluorescence channels or represent 3D hollow structures. Our computational pipeline consists of several independent modules: spectral filtering, dual-view registration, local contrast enhancement, 3D nuclei segmentation, image normalization based on a ubiquitous marker, and multiscale analysis of gene expression and morphometrics.

Spectral filtering has already been applied in other systems (e.g. [7] and [8]), but is here extended to account for imaging depth-dependent apparent emission spectra of the different fluorophores. In our pipeline, we provide code to run spectral filtering on multichannel images, integrated in Python. In order to apply the spectral filtering algorithm utilized here, spectral patterns of each fluorophore need to be calibrated as a function of imaging depth, which depend on the specific emission windows and detector settings of the microscope.

Image normalization using a wavelength-dependent correction also requires calibration on a given imaging setup to measure the difference in signal decay among the different fluorophores species. To our knowledge, the calibration procedures for spectral-filtering and our image-normalization approach have not been performed previously in 3D samples, which is why validation on published datasets is not readily possible. Nevertheless, they are described in detail in the Methods section, and the code used—from the calibration measurements to the corrected images—is available open-source at the Zenodo link in the manuscript.

Dual-view registration, local contrast enhancement, and multiscale analysis of gene expression and morphometrics are not limited to organoid data or our specific imaging modalities. If we identify suitable datasets to validate these modules, we will include them in the revised manuscript.

To evaluate our 3D nuclei segmentation model, we plan to test it on diverse systems, including gastruloids stained with the nuclear marker Draq5 from Moos et al. [1]; breast cancer spheroids; primary ductal adenocarcinoma organoids; human colon organoids and HCT116 monolayers from Ong et al. [2]; and zebrafish tissues imaged by confocal microscopy from Li et al [3]. These datasets were acquired using either light-sheet or confocal microscopy, with varying imaging parameters (e.g., objective lens, pixel size, staining method).

Preliminary results are promising (see Author response image 1). We will provide quantitative comparisons of our model’s performance on these datasets, using annotations or reference predictions provided by the original authors where available.

Author response image 1.

Qualitative comparison of our custom Stardist3D segmentation strategy on diverse published 3D nuclei datasets. We show one slice from the XY plane for simplicity. (a) Gastruloid stained with the nuclear marker DRAQ5 imaged with an open-top dual-view and dual-illumination LSM [1]. (b) Breast cancer spheroid [2]. (c) Primary pancreatic ductal adenocarcinoma organoids imaged with confocal microscopy[2]. (d) Human colon organoid imaged with LSM laser scanning confocal microscope [2]. (e) Monolayer HCT116 cells imaged with LSM laser scanning confocal microscope [2]. (f) Fixed zebrafish embryo stained for nuclei and imaged with a Zeiss LSM 880 confocal microscopy [3].

Besides, the nuclei segmentation component lacks benchmarking against existing methods.

We agree with the reviewer that a benchmark against existing segmentation methods would be very useful. We tried different pre-trained models:

- CellPose, which we tested in a previous paper ([4]) and which showed poor performances compared to our trained StarDist3D model.

- DeepStar3D ([2]) is only available in the software 3DCellScope. We could not benchmark the model on our data, because the free and accessible version of the software is limited to small datasets. An image of a single whole-mount gastruloid with one channel, having dimensions (347,467,477) was too large to be processed, see screenshot below. The segmentation model could not be extracted from the source code and tested externally because the trained DeepStar3D weights are encrypted.

Author response image 2.

Screenshot of the 3DCellScore software. We could not perform 3D nuclei segmentation of a whole-mount gastruloids because the image size was too large to be processed.

- AnyStar ([5]), which is a model trained from the StarDist3D architecture, was not performing well on our data because of the heterogeneous stainings. Basic pre-processing such as median and gaussian filtering did not improve the results and led to wrong segmentation of touching nuclei. AnyStar was demonstrated to segment well colon organoids in Ong et al, 2025 ([2]), but the nuclei were more homogeneously stained. Our Hoechst staining displays bright chromatin spots that are incorrectly labeled as individual nuclei.

- Cellos ([6]), another model trained from StarDist3D, was also not performing well. The objects used for training and to validate the results are sparse and not touching, so the predicted segmentation has a lot of false negatives even when lowering the probability threshold to detect more objects. Additionally, the network was trained with an anisotropy of (9,1,1), based on images with low z resolution, so it performed poorly on almost isotropic images. Adapting our images to the network’s anisotropy results in an imprecise segmentation that can not be used to measure 3D nuclei deformations.

We tried both Cellos and AnyStar predictions on a gastruloid image from Fig. S2 of our main manuscript. Author response image 3 displays the results qualitatively compared to our trained model Stardist-tapenade. For the revision of the paper, we will perform a comprehensive benchmark of these state-of-the-art routines, including quantitative assessment of the performance.

Author response image 3.

Qualitative comparison of two published segmentation models versus our model. We show one slice from the XY plane for simplicity. Segmentations are displayed with their contours only. (Top left) Gastruloid stained with Hoechst, image extracted from Fig S2 of our manuscript. (Top right) Same image overlayed with the prediction from the Cellos model, showing many false negatives. (Bottom left) Same image overlayed with the prediction from our Stardist-tapenade model. (Bottom right) Same image overlayed with the prediction from the AnyStar model, false positives are indicated with a red arrow.

Appraisal:

The authors set out to establish a quantitative imaging and analysis pipeline for gastruloids using dual-view two-photon microscopy, spectral unmixing, and a custom computational framework for 3D segmentation and gene expression analysis. This aim is largely achieved. The integration of experimental and computational modules enables high-resolution in toto imaging and robust quantitative analysis at the single-cell level. The data presented support the authors' conclusions regarding the ability to capture spatial patterns of gene expression and cellular morphology across developmental stages.

Impact and utility:

This work presents a compelling and broadly applicable methodological advance. The approach is particularly impactful for the developmental biology community, as it allows researchers to extract quantitative information from high-resolution images to better understand morphogenetic processes. The data are publicly available on Zenodo, and the software is released on GitHub, making them highly valuable resources for the community.

We thank the reviewer for these positive feedbacks.

Reviewer #3 (Public review):

Summary

The paper presents an imaging and analysis pipeline for whole-mount gastruloid imaging with two-photon microscopy. The presented pipeline includes spectral unmixing, registration, segmentation, and a wavelength-dependent intensity normalization step, followed by quantitative analysis of spatial gene expression patterns and nuclear morphometry on a tissue level. The utility of the approach is demonstrated by several experimental findings, such as establishing spatial correlations between local nuclear deformation and tissue density changes, as well as the radial distribution pattern of mesoderm markers. The pipeline is distributed as a Python package, notebooks, and multiple napari plugins.

Strengths

The paper is well-written with detailed methodological descriptions, which I think would make it a valuable reference for researchers performing similar volumetric tissue imaging experiments (gastruloids/organoids). The pipeline itself addresses many practical challenges, including resolution loss within tissue, registration of large volumes, nuclear segmentation, and intensity normalization. Especially the intensity decay measurements and wavelength-dependent intensity normalization approach using nuclear (Hoechst) signal as reference are very interesting and should be applicable to other imaging contexts. The morphometric analysis is equally well done, with the correlation between nuclear shape deformation and tissue density changes being an interesting finding. The paper is quite thorough in its technical description of the methods (which are a lot), and their experimental validation is appropriate. Finally, the provided code and napari plugins seem to be well done (I installed a selected list of the plugins and they ran without issues) and should be very helpful for the community.

We thank the reviewer for his positive feedback and appreciation of our work.

Weaknesses

I don't see any major weaknesses, and I would only have two issues that I think should be addressed in a revision:

(1) The demonstration notebooks lack accompanying sample datasets, preventing users from running them immediately and limiting the pipeline's accessibility. I would suggest to include (selective) demo data set that can be used to run the notebooks (e.g. for spectral unmixing) and or provide easily accessible demo input sample data for the napari plugins (I saw that there is some sample data for the processing plugin, so this maybe could already be used for the notebooks?).

We thank the reviewer for this relevant suggestion. The 7 notebooks were updated to automatically download sample tests. The different parts of the pipeline can now be run immediately: https://github.com/GuignardLab/tapenade/tree/chekcs_on_notebooks/src/tapenade/notebooks

(2) The results for the morphometric analysis (Figure 4) seem to be only shown in lateral (xy) views without the corresponding axial (z) views. I would suggest adding this to the figure and showing the density/strain/angle distributions for those axial views as well.

We agree with the reviewer that a morphometric analysis based on the axial views would be informative and plan to perform this analysis for the revision.

(1) Moos, F., Suppinger, S., de Medeiros, G., Oost, K.C., Boni, A., Rémy, C., Weevers, S.L., Tsiairis, C., Strnad, P. and Liberali, P., 2024. Open-top multisample dual-view light-sheet microscope for live imaging of large multicellular systems. Nature Methods, 21(5), pp.798-803.

(2) Ong, H.T., Karatas, E., Poquillon, T., Grenci, G., Furlan, A., Dilasser, F., Mohamad Raffi, S.B., Blanc, D., Drimaracci, E., Mikec, D. and Galisot, G., 2025. Digitalized organoids: integrated pipeline for high-speed 3D analysis of organoid structures using multilevel segmentation and cellular topology. Nature Methods, 22(6), pp.1343-1354.

(3) Li, L., Wu, L., Chen, A., Delp, E.J. and Umulis, D.M., 2023. 3D nuclei segmentation for multi-cellular quantification of zebrafish embryos using NISNet3D. Electronic Imaging, 35, pp.1-9.

(4) Vanaret, J., Dupuis, V., Lenne, P. F., Richard, F., Tlili, S., & Roudot, P. (2023). A detector-independent quality score for cell segmentation without ground truth in 3D live fluorescence microscopy. IEEE Journal of Selected Topics in Quantum Electronics, 29(4: Biophotonics), 1-12.

(5) Dey, N., Abulnaga, M., Billot, B., Turk, E. A., Grant, E., Dalca, A. V., & Golland, P. (2024). AnyStar: Domain randomized universal star-convex 3D instance segmentation. In Proceedings of the IEEE/CVF Winter Conference on Applications of Computer Vision (pp. 7593-7603).

(6) Mukashyaka, P., Kumar, P., Mellert, D. J., Nicholas, S., Noorbakhsh, J., Brugiolo, M., ... & Chuang, J. H. (2023). High-throughput deconvolution of 3D organoid dynamics at cellular resolution for cancer pharmacology with Cellos. Nature Communications, 14(1), 8406.

(7) Rakhymzhan, A., Leben, R., Zimmermann, H., Günther, R., Mex, P., Reismann, D., ... & Niesner, R. A. (2017). Synergistic strategy for multicolor two-photon microscopy: application to the analysis of germinal center reactions in vivo. Scientific reports, 7(1), 7101.

(8) Dunsing, V., Petrich, A., & Chiantia, S. (2021). Multicolor fluorescence fluctuation spectroscopy in living cells via spectral detection. Elife, 10, e69687.

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.

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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.

This manuscript examines preprint review services and their role in the scholarly communications ecosystem.  It seems quite thorough to me. In Table 1 they list many peer-review services that I was unaware of e.g. SciRate and Sinai Immunology Review Project.

To help elicit critical & confirmatory responses for this peer review report I am trialling Elsevier’s suggested “structured peer review” core questions, and treating this manuscript as a research article.

Introduction

1. Is the background and literature section up to date and appropriate for the topic?

   Yes.

2. Are the primary (and secondary) objectives clearly stated at the end of the introduction?

   No. Instead the authors have chosen to put the two research questions on page 6 in the methods section. I wonder if they ought to be moved into the introduction – the research questions are not methods in themselves. Might it be better to state the research questions first and then detail the methods one uses to address those questions afterwards? [as Elsevier’s structured template seems implicitly to prefer.

Methods

1. Are the study methods (including theory/applicability/modelling) reported in sufficient detail to allow for their replicability or reproducibility?

   I note with approval that the version number of the software they used (ATLAS.ti) was given.

   I note with approval that the underlying data is publicly archived under CC BY at figshare.

   The Atlas.ti report data spreadsheet could do with some small improvement – the column headers are little cryptic e.g. “Nº  ST “ and “ST” which I eventually deduced was Number of Schools of Thought and Schools of Thought (?)   

   Is there a rawer form of the data that could be deposited with which to evidence the work done? The Atlas.ti report spreadsheet seemed like it was downstream output data from Atlas.ti. What was the rawer input data entered into Atlas.ti? Can this be archived somewhere in case researchers want to reanalyse it using other tools and methods.

   I note with disapproval that Atlas.ti is proprietary software which may hinder the reproducibility of this work. Nonetheless I acknowledge that Atlas.ti usage is somewhat ‘accepted’ in social sciences despite this issue.

   I think the qualitative text analysis is a little vague and/or under-described: “Using ATLAS.ti Windows (version 23.0.8.0), we carried out a qualitative analysis of text from the relevant sites, assigning codes covering what they do and why they have chosen to do it that way.” That’s not enough detail. Perhaps an example or two could be given? Was inter-rater reliability performed when ‘assigning codes’ ? How do we know the ‘codes’ were assigned accurately?

2. Are statistical analyses, controls, sampling mechanism, and statistical reporting (e.g., P-values, CIs, effect sizes) appropriate and well described?

   This is a descriptive study (and that’s fine) so there aren’t really any statistics on show here other than simple ‘counts’ (of Schools of Thought) in this manuscript. There are probably some statistical processes going on within the proprietary qualitative analysis of text done in ATLAS.ti but it is under described and so hard for me to evaluate. 

Results

1. Is the results presentation, including the number of tables and figures, appropriate to best present the study findings?

   Yes. However, I think a canonical URL to each service should be given.  A URL is very useful for disambiguation, to confirm e.g. that the authors mean this Hypothesis (www.hypothes.is) and NOT this Hypothesis (www.hyp.io). I know exactly which Hypothesis is the one the authors are referring to but we cannot assume all readers are experts 😊

   Optional suggestion: I wonder if the authors couldn’t present the table data in a slightly more visual and/or compact way? It’s not very visually appealing in its current state. Purely as an optional suggestion, to make the table more compact one could recode the answers given in one or more of the columns 2, 3 and 4 in the table e.g. "all disciplines = ⬤ , biomedical and life sciences = ▲, social sciences =  ‡  , engineering and technology = † ". I note this would give more space in the table to print the URLs for each service that both reviewers have requested.

   ———————————————————————————————

   | Service name | Developed by | Scientific disciplines | Types of outputs |

   | Episciences | Other | ⬤ | blah blah blah. |

   | Faculty Opinions | Individual researcher | ▲ | blah blah blah. |

   | Red Team Market | Individual researcher | ‡ | blah blah blah. |

   ———————————————————————————————

   The "Types of outputs" column might even lend themselves to mini-colour-pictograms (?) which could be more concise and more visually appealing? A table just of text, might be scientifically 'correct' but it is incredibly dull for readers, in my opinion.

2. Are additional sub-analyses or statistical measures needed (e.g., reporting of CIs, effect sizes, sensitivity analyses)?

   No / Not applicable. 

Discussion

1. Is the interpretation of results and study conclusions supported by the data and the study design?

   Yes.

2. Have the authors clearly emphasized the limitations of their study/theory/methods/argument?

   No. Perhaps a discussion of the linguistic/comprehension bias of the authors might be appropriate for this manuscript. What if there are ‘local’ or regional Chinese, Japanese, Indonesian or Arabic language preprint review services out there? Would this authorship team really be able to find them?

Additional points:

• Perhaps the points made in this manuscript about financial sustainability (p24) are a little too pessimistic. I get it, there is merit to this argument, but there is also some significant investment going on there if you know where to look. Perhaps it might be worth citing some recent investments e.g. Gates -> PREreview (2024) https://content.prereview.org/prereview-welcomes-funding/  and Arcadia’s $4 million USD to COAR for the Notify Project which supports a range of preprint review communities including Peer Community In, Episciences, PREreview and Harvard Library.  (source: https://coar-repositories.org/news-updates/coar-welcomes-significant-funding-for-the-notify-project/ ) 

• Although I note they are mentioned, I think more needs to be written about the similarity and overlap between ‘overlay journals’ and preprint review services. Are these arguably not just two different terms for kinda the same thing? If you have Peer Community In which has it’s overlay component in the form of the Peer Community Journal, why not mention other overlay journals like Discrete Analysis and The Open Journal of Astrophysics.   I think Peer Community In (& it’s PCJ) is the go-to example of the thin-ness of the line the separates (or doesn’t!) overlay journals and preprint review services. Some more exposition on this would be useful.

Thank you very much for the opportunity to review the preprint titled “Preprint review services: Disrupting the scholarly communication landscape?” (https://doi.org/10.31235/osf.io/8c6xm) The authors review services that facilitate peer review of preprints, primarily in the STEM (science, technology, engineering, and math) disciplines. They examine how these services operate and their role within the scholarly publishing ecosystem. Additionally, the authors discuss the potential benefits of these preprint peer review services, placing them in the context of tensions in the broader peer review reform movement. The discussions are organized according to four “schools of thought” in peer review reform, as outlined by Waltman et al. (2023), which provides a useful framework for analyzing the services. In terms of methodology, I believe the authors were thorough in their search for preprint review services, especially given that a systematic search might be impractical.

As I see it, the adoption of preprints and reforming peer review are key components of the move towards improving scholarly communication and open research. This article is a useful step along that journey, taking stock of current progress, with a discussion that illuminates possible paths forward. It is also well-structured and easy for me to follow. I believe it is a valuable contribution to the metaresearch literature.

On a high level, I believe the authors have made a reasonable case that preprint review services might make peer review more transparent and rewarding for all involved. Looking forward, I would like to see metaresearch which gathers further evidence that these benefits are truly being realised.

In this review, I will present some general points which merit further discussion or clarification to aid an uninitiated reader. Additionally, I raise one issue regarding how the authors framed the article and categorised preprint review services and the disciplines they serve. In my view, this problem does not fundamentally undermine the robust search, analyses, and discussion in this paper, but it risks putting off some researchers and constrains how broadly one should derive conclusions.

General comments

Some metaresearchers may be aware of preprints, but not all readers will be familiar with them. I suggest briefly defining what they are, how they work, and which types of research have benefited from preprints, similar to how “preprint review service” is clearly defined in the introduction.

Regarding Waltman et al.’s (2023) “Equity & Inclusion” school of thought, does it specifically aim for “balanced” representation by different groups as stated in this article? There is an important difference between “balanced” versus “equitable” representation, and I would like to see it addressed in this text.

Another analysis I would like to see is whether any of the 23 services reviewed present any evidence that their approach has improved research quality. For instance, the discussion on peer review efficiency and incentives states that there is currently “no hard evidence” that journals want to utilise reviews by Rapid Reviews: COVID-19, and that “not all journals are receptive” to partnerships. Are journals skeptical of whether preprint review services could improve research quality? Or might another dynamic be at work?

The authors cite Nguyen et al. (2015) and Okuzaki et al. (2019), stating that peer review is often “overloaded”. I would like to see a clearer explanation by what “overloaded” means in this context so that a reader does not have to read the two cited papers.

To the best of my understanding, one of the major sticking points in peer review reform is whether to anonymise reviewers and/or authors. Consequently, I appreciate the comprehensive discussion about this issue by the authors.

However, I am only partially convinced by the statement that double anonymity is “essentially incompatible” with preprint review. For example, there may be, as yet not fully explored, ways to publish anonymous preprints with (a) a notice that it has been submitted to, or is undergoing, peer review; and (b) that the authors will be revealed once peer review has been performed (e.g. at least one review has been published). This would avoid the issue of publishing only after review is concluded as is the case for Hypothesis and Peer Community In.

Additionally, the authors describe 13 services which aim to “balance transparency and protect reviewers’ interests”. This is a laudable goal, but I am concerned that framing this as a “balance” implies a binary choice, and that to have more of one, we must lose an equal amount of the other. Thinking only in terms of “balance” prevents creative, win-win solutions. Could a case be made for non-anonymity to be complemented by a reputation system for authors and reviewers? For example, major misconduct (e.g. retribution against a critical review) would be recorded in that system and dissuade bad actors. Something similar can already be seen in the reviewer evaluation system of CrowdPeer, which could plausibly be extended or modified to highlight misconduct.

I also note that misconduct and abusive behaviour already occur even in fully or partially anonymised peer review, and they are not limited to the review or preprints. While I am not aware of existing literature on this topic, academics’ fears seem reasonable. For example, there is at least anecdotal testimonies that a reviewer would deliberately reject a paper to retard the progress of a rival research group, while taking the ideas of that paper and beating their competitors to winning a grant. Or, a junior researcher might refrain from giving a negative review out of fear that the senior researcher whose work they are reviewing might retaliate. These fears, real or not, seem to play a part in the debates about if and how peer review should (or should not) be anonymised. I would like to see an exploration of whether de-anonimisation will improve or worsen this behaviour and in what contexts. And if such studies exist, it would be good to discuss them in this paper.

I found it interesting that almost all preprint review services claim to be complementary to, and not compete with, traditional journal-based peer review. The methodology described in this article cannot definitely explain what is going on, but I suspect there may be a connection between this aversion to compete with traditional journals, and (a) the skepticism of journals towards partnering with preprint review services and (b) the dearth of publisher-run options. I hypothesise that there is a power dynamic at play, where traditional publishers have a vested interest in maintaining the power they hold over scholarly communication, and that preprint review services stress their complementarity (instead of competitiveness) as a survival mechanism. This may be an avenue for further metaresearch.

To understand preprints from which fields of research are actually present on the services categorised under “all disciplines,” I used the Random Integer Set Generator by the Random.org true random number service (https://www.random.org/integer-sets/) to select five services for closer examination: Hypothesis, Peeriodicals, PubPeer, Qeios, and Researchers One. Of those, I observed that Hypothesis is an open source web annotation service that allows commenting on and discussion of any web page on the Internet regardless of whether it is research or preprints. Hypothesis has a sub-project named TRiP (Transparent Review in Preprints), which is their preprint review service in collaboration with Cold Spring Harbor Laboratory. It is unclear to me why the authors listed Hypothesis as the service name in Table 1 (and elsewhere) instead of TRiP (or other similar sub-projects). In addition, Hypothesis seems to be framed as a generic web annotation service that is used by some as a preprint review tool. This seems fundamentally different from others who are explicitly set up as preprint review services. This difference seems noteworthy to me.

To aid readers, I also suggest including hyperlinks to the 23 services reviewed in this paper. My comments on disciplinary representation in these services are elaborated further below.

One minor point of curiosity is that several services use an “automated tool” to select reviewers. It would be helpful to describe in this paper exactly what those tools are and how they work, or report situations where services do not explain it.

Lastly, what did the authors mean by “software heritage” in section 6? Are they referring to the organisation named Software Heritage (https://www.softwareheritage.org/) or something else? It is not clear to me how preprint reviews would be deposited in this context.

Respecting disciplinary and epistemic diversity

In the abstract and elsewhere in the article, the authors acknowledge that preprints are gaining momentum “in some fields” as a way to share “scientific” findings. After reading this article, I agree that preprint review services may disrupt publishing for research communities where preprints are in the process of being adopted or already normalised. However, I am less convinced that such disruption is occurring, or could occur, for scholarly publishing more generally.

I am particularly concerned about the casual conflation of “research” and “scientific research” in this article. Right from the start, it mentions how preprints allow sharing “new scientific findings” in the abstract, stating they “make scientific work available rapidly.” It also notes that preprints enable “scientific work to be accessed in a timely way not only by scientists, but also…” This framing implies that all “scholarly communication,” as mentioned in the title, is synonymous with “scientific communication.” Such language excludes researchers who do not typically identify their work as “scientific” research. Another example of this conflation appears in the caption for Figure 1, which outlines potential benefits of preprint review services. Here, “users” are defined as “scientists, policymakers, journalists, and citizens in general.” But what about researchers and scholars who do not see themselves as “scientists”?

Similarly, the authors describe the 23 preprint review services using six categories, one of which is “scientific discipline”. One of those disciplines is called “humanities” in the text, and Table 1 lists it as a discipline for Science Open Reviewed. Do the authors consider “humanities” to be a “scientific” discipline? If so, I think that needs to be justified with very strong evidence.

Additionally, Waltman et al.’s four schools of thought for peer review reform works well with the 23 services analysed. However, at least three out of the four are explicitly described as improving “scientific” research.

Related to the above are how the five “scientific disciplines” are described as the “usual organisation” of the scholarly communication landscape. On what basis should they be considered “usual”? In this formulation, research in literature, history, music, philosophy, and many other subjects would all be lumped together into the “humanities”, which sit at the same hierarchical level as “biomedical and life sciences”, arguably a much more specific discipline. My point is not to argue for a specific organisation of research disciplines, but to highlight a key epistemic assumption underlying the whole paper that comes across as very STEM-centric (science, technology, engineering, and math).

How might this part of the methodology affect the categories presented in Table 1? “Biomedical and life sciences” appear to be overrepresented compared to other “disciplines”. I’d like to see a discussion that examines this pattern, and considers why preprint review services (or maybe even preprints more generally) appear to cover mostly the biomedical or physical sciences.

In addition, there are 12 services described as serving “all disciplines”. I believe this paper can be improved by at least a qualitative assessment of the diversity of disciplines actually represented on those services. Because it is reported that many of these service stress improving the “reproducibility” of research, I suspect most of them serve disciplines which rely on experimental science.

I randomly selected five services for closer examination, as mentioned above. Of those, only Qeios has demonstrated an attempt to at least split “arts and humanities” into subfields. The others either don’t have such categories altogether, or have a clear focus on a few disciplines (e.g. life sciences for Hypothesis/TRiP). In all cases I studied, there is a heavy focus on STEM subjects, especially biology or medical research. However, they are all categorised by the authors as serving “all disciplines”.

If preprint review services originate from, or mostly serve, a narrow range of STEM disciplines (especially experiment-based ones), it would be worth examining why that is the case, and whether preprints and reviews of them could (or could not) serve other disciplines and epistemologies.

It is postulated that preprint review services might “disrupt the scholarly communication landscape in a more radical way”. Considering the problematic language I observed, what about fields of research where peer-reviewed journal publications are not the primary form of communication? Would preprint review services disrupt their scholarly communications?

To be clear, my concern is not just the conflation of language in a linguistic sense but rather inequitable epistemic power. I worry that this conflation would (a) exclude, minoritise, and alienate researchers of diverse disciplines from engaging with metaresearch; and (b) blind us from a clear pattern in these 23 services, that is their strong focus on the life sciences and medical research and a discussion of why that might be the case. Critically, what message are we sending to, for example, a researcher of 18th century French poetry with the language and framing of this paper? I believe the way “disciplines” are currently presented here poses a real risk of devaluing and minoritising certain subject areas and ways of knowing. In its current form, I believe that while this paper is a very valuable contribution, one should not derive from it any conclusions which apply to scholarly publishing as a whole.

The authors have demonstrated inclusive language elsewhere. For example, they have consciously avoided “peer” when discussing preprint review services, clearly contrasting them to “journal-based peer review”. Therefore, I respectfully suggest that similar sensitivity be adopted to avoid treating “scientific research” and “research” as the same thing. A discussion, or reference to existing works, on the disciplinary skew of preprints (and reviews of them) would also add to the intellectual rigour of this already excellent piece.

Overall, I believe this paper is a valuable reflection on the state of preprints and services which review them. Addressing the points I raised, especially the use of more inclusive language with regards to disciplinary diversity, would further elevate its usefulness in the metaresearch discourse. Thank you again for the chance to review.

Signed:

Dr Pen-Yuan Hsing (ORCID ID: 0000-0002-5394-879X)

University of Bristol, United Kingdom

Data availability

I have checked the associated dataset, but still suggest including hyperlinks to the 23 services analysed in the main text of this paper.

In "Researchers Are Willing to Trade Their Results for Journal Prestige: Results from a Discrete Choice Experiment", the authors investigate researchers’ publication preferences using a discrete choice experiment in a cross-sectional survey of international health and medical researchers. The study investigates publishing decisions in relation to negotiation of trade-offs amongst various factors like journal impact factor, review helpfulness, formatting requirements, and usefulness for promotion in their decisions on where to publish. The research is timely; as the authors point out, reform of research assessment is currently a very active topic. The design and methods of the study are suitable and robust. The use of focus groups and interviews in developing the attributes for study shows care in the design. The survey instrument itself is generally very well-designed, with important tests of survey fatigue, understanding (dominant choice task) and respondent choice consistency (repeat choice task) included. Respondent performance was good or excellent across all these checks. Analysis methods (pMMNL and latent class analysis) are well-suited to the task. Pre-registration and sharing of data and code show commitment to transparency. Limitations are generally well-described.

In the below, I give suggestions for clarification/improvement. Except for some clarifications on limitations and one narrower point (reporting of qualitative data analysis methods), my suggestions are only that – the preprint could otherwise stand, as is, as a very robust and interesting piece of scientific work.

1. Respondents come from a broad range of countries (63), with 47 of those countries represented by fewer than 10 respondents. Institutional cultures of evaluation can differ greatly across nations. And we can expect variability in exposure to the messages of DORA (seen, for example, in level of permeation of DORA as measured by signatories in each country, https://sfdora.org/signers/)..%3B!!NVzLfOphnbDXSw!HdeyeHHei6yWQHFjhN3deSSfp82ur9i9JNOLEVOYZN0BvyslUO2S8DlvjBbautmafJEvlUsxQZbT0JLQX7lO8EcOYtZsJkA%24&data=05%7C02%7Ca.l.brasil.varandas.pinto%40cwts.leidenuniv.nl%7C9f47a111adec49d04bb608dd0614ae94%7Cca2a7f76dbd74ec091086b3d524fb7c8%7C0%7C0%7C638673408085242099%7CUnknown%7CTWFpbGZsb3d8eyJFbXB0eU1hcGkiOnRydWUsIlYiOiIwLjAuMDAwMCIsIlAiOiJXaW4zMiIsIkFOIjoiTWFpbCIsIldUIjoyfQ%3D%3D%7C0%7C%7C%7C&sdata=by5mhPfSM0MFFG9LE2iiYjdtSs5IhvpuukqVv%2FLak2s%3D&reserved=0 "https://eur03.safelinks.protection.outlook.com/?url=https%3A%2F%2Furldefense.com%2Fv3%2F__https%3A%2F%2Fsfdora.org%2Fsigners%2F).%3B!!NVzLfOphnbDXSw!HdeyeHHei6yWQHFjhN3deSSfp82ur9i9JNOLEVOYZN0BvyslUO2S8DlvjBbautmafJEvlUsxQZbT0JLQX7lO8EcOYtZsJkA%24&data=05%7C02%7Ca.l.brasil.varandas.pinto%40cwts.leidenuniv.nl%7C9f47a111adec49d04bb608dd0614ae94%7Cca2a7f76dbd74ec091086b3d524fb7c8%7C0%7C0%7C638673408085242099%7CUnknown%7CTWFpbGZsb3d8eyJFbXB0eU1hcGkiOnRydWUsIlYiOiIwLjAuMDAwMCIsIlAiOiJXaW4zMiIsIkFOIjoiTWFpbCIsIldUIjoyfQ%3D%3D%7C0%7C%7C%7C&sdata=by5mhPfSM0MFFG9LE2iiYjdtSs5IhvpuukqVv%2FLak2s%3D&reserved=0") In addition, some contexts may mandate or incentivise publication in some venues using measures including IF, but also requiring journals to be in certain databases like WoS or Scopus, or having preferred journal lists). I would suggest the authors should include in the Sampling section a rationale for taking this international approach, including any potentially confounding factors it may introduce, and then adding the latter also in the limitations.

2. Reporting of qualitative results: In the introduction and methods, the role of the focus groups and interviews seems to have been just to inform the design of the experiment. But then, results from that qualitative work then appear as direct quotes within the discussion to contextualise or explain results. In this sense though, the qualitative results are being used as new data. Given this, I feel that the methods section should include description of the methods and tools used for qualitative data analysis (currently it does not). But in addition, to my understanding (and this may be a question of disciplinary norms – I’m not a health/medicine researcher), generally new data should not be introduced in the discussion section of a research paper. Rather the discussion is meant to interpret, analyse, and provide context for the results that have already been presented. I personally hence feel that the paper would benefit from the qualitative results being reported separately within the results section.

3. Impact factors – Discussion section: While there is interesting new information on the relative trade-offs amongst other factors, the most emphasised finding, that impact factors still play a prominent role in publication venue decisions, is hardly surprising. More could perhaps be done to compare how the levels of importance reported here differ with previous results from other disciplines or over time (I know a like-for-like comparison is difficult but other studies have investigated these themes, e.g., https://doi.org/10.1177/01655515209585). In addition, beyond the question of whether impact factors are important, a more interesting question in my view is why they still persist. What are they used for and why are they still such important “driver[s] of researchers’ behaviour”? This was not the authors’ question, and they do provide some contextualisation by quoting their participants, but still I think they could do more to contextualise what is known from the literature on that to draw out the implications here. The attribute label in the methods for IF is “ranking”, but ranking according of what and for what? Not just average per-article citations in a journal over a given time frame. Rather, impact factors are used as a proxy indicators of less-tangible desirable qualities – certainly prestige (as the title of this article suggests), but also quality, trust (as reported by one quoted focus group member “I would never select a journal without an impact factor as I always publish in journals that I know and can trust that are not predatory”, p.6), journal visibility, importance to the field, or improved chances of downstream citations or uptake in news media/policy/industry etc. Picking apart the interactions of these various factors in researchers’ choices to make use of IFs (which is not in all cases bogus or unjustified) could add valuable context. I’d especially recommend engaging at least briefly with more work from Science and Technology Studies - especially Müller and de Rijcke’s excellent Thinking with Indicators study (doi: 10.1093/reseval/rvx023), but also those authors other work, as well as work from Ulrike Felt, Alex Rushforth (esp https://doi.org/10.1007/s11024-015-9274-5), Björn Hammerfelt and others.

4. Disciplinary coverage: (1) A lot of the STS work I talk about above emphasises epistemic diversity and the ways cultures of indicator use differ across disciplinary traditions. For this reason, I think it should be pointed out in the limitations that this is research in Health/Med only, with questions on generalisability to other fields. (2) Also, although the abstract and body of the article do make clear the disciplinary focus, the title does not. Hence, I believe the title should be slightly amended (e.g., “Health and Medical Researchers Are Willing to Trade …”)

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:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Chen et al. identified the role of endocardial id2b expression in cardiac contraction and valve formation through pharmaceutical, genetic, electrophysiology, calcium imaging, and echocardiography analyses. CRISPR/Cas9 generated id2b mutants demonstrated defective AV valve formation, excitation-contraction coupling, reduced endocardial cell proliferation in AV valve, retrograde blood flow, and lethal effects.

Strengths:

Their methods, data and analyses broadly support their claims.

Weaknesses:

The molecular mechanism is somewhat preliminary.

We thank the reviewer for the positive assessment of our work. A detailed point-by-point response has been incorporated in the response to “Recommendations for the authors” section.

Reviewer #2 (Public review):

Summary:

Biomechanical forces, such as blood flow, are crucial for organ formation, including heart development. This study by Shuo Chen et al. aims to understand how cardiac cells respond to these forces. They used zebrafish as a model organism due to its unique strengths, such as the ability to survive without heartbeats, and conducted transcriptomic analysis on hearts with impaired contractility. They thereby identified id2b as a gene regulated by blood flow and is crucial for proper heart development, in particular, for the regulation of myocardial contractility and valve formation. Using both in situ hybridization and transgenic fish they showed that id2b is specifically expressed in the endocardium, and its expression is affected by both pharmacological and genetic perturbations of contraction. They further generated a null mutant of id2b to show that loss of id2b results in heart malformation and early lethality in zebrafish. Atrioventricular (AV) and excitation-contraction coupling were also impaired in id2b mutants. Mechanistically, they demonstrate that Id2b interacts with the transcription factor Tcf3b to restrict its activity. When id2b is deleted, the repressor activity of Tcf3b is enhanced, leading to suppression of the expression of nrg1 (neuregulin 1), a key factor for heart development. Importantly, injecting tcf3b morpholino into id2b-/- embryos partially restores the reduced heart rate. Moreover, treatment of zebrafish embryos with the Erbb2 inhibitor AG1478 results in decreased heart rate, in line with a model in which Id2b modulates heart development via the Nrg1/Erbb2 axis. The research identifies id2b as a biomechanical signaling-sensitive gene in endocardial cells that mediates communication between the endocardium and myocardium, which is essential for heart morphogenesis and function.

Strengths:

The study provides novel insights into the molecular mechanisms by which biomechanical forces influence heart development and highlights the importance of id2b in this process.

Weaknesses:

The claims are in general well supported by experimental evidence, but the following aspects may benefit from further investigation:

(1) In Figure 1C, the heatmap demonstrates the up-regulated and down-regulated genes upon tricane-induced cardiac arrest. Aside from the down-regulation of id2b expression, it was also evident that id2a expression was up-regulated. As a predicted paralog of id2b, it would be interesting to see whether the up-regulation of id2a in response to tricane treatment was a compensatory response to the down-regulation of id2b expression.

We thank the reviewer for the comment. As suggested, we performed qRT-PCR analysis to assess id2a expression in tricaine-treated heart. Our results demonstrate a significant upregulation of id2a following the inhibition of cardiac contraction, suggesting a potential compensatory response to the decreased id2b. These new results have been incorporated into the revised manuscript (Figure 1D).

(2) The study mentioned that id2b is tightly regulated by the flow-sensitive primary cilia-klf2 signaling axis; however aside from showing the reduced expression of id2b in klf2a and klf2b mutants, there was no further evidence to solidify the functional link between id2b and klf2. It would therefore be ideal, in the present study, to demonstrate how Klf2, which is a transcriptional regulator, transduces biomechanical stimuli to Id2b.

We have examined the expression levels of id2b in both klf2a and klf2b mutants. The whole mount in situ results clearly demonstrate a decrease in id2b signal in both mutants (Figure 3E). As noted by the reviewer, klf2 is a transcriptional regulator, suggesting that the regulation of id2b may occur at the transcriptional level. However, dissecting the molecular mechanisms underlying the crosstalk between klf2 and id2b is beyond the scope of the present study.

(3) The authors showed the physical interaction between ectopically expressed FLAG-Id2b and HA-Tcf3b in HEK293T cells. Although the constructs being expressed are of zebrafish origin, it would be nice to show in vivo that the two proteins interact.

We thank the reviewer for this insightful comment. As suggested, we synthesized Flag-id2b and HA-tcf3b mRNA and co-injected them into 1-cell stage zebrafish embryos. We collected 100-300 embryos at 12, 24, and 48 hpf and performed western blot analysis using the same anti-HA and anti-Flag antibodies validated in HEK293 cell experiments. Despite multiple independent attempts, we were unable to detect clear bands of the tagged proteins in zebrafish embryos. We speculate that this could be due to mRNA instability, translational efficiency, or the low abundance of Id2b and Tcf3b proteins. We have acknowledged these technical limitations in the revised manuscript and clarified that the HEK293 cell data support a potential interaction between Id2b and Tcf3b, while confirming their endogenous interaction will require further investigations (Lines 295-296).

Reviewer #3 (Public review):

Summary:

How mechanical forces transmitted by blood flow contribute to normal cardiac development remains incompletely understood. Using the unique advantages of the zebrafish model system, Chen et al make the fundamental discovery that endocardial expression of id2b is induced by blood flow and required for normal atrioventricular canal (AVC) valve development and myocardial contractility by regulating calcium dynamics. Mechanistically, the authors suggest that Id2b binds to Tcf3b in endocardial cells, which relieves Tcf3b-mediated transcriptional repression of Neuregulin 1 (NRG1). Nrg1 then induces expression of the L-type calcium channel component LRRC1. This study significantly advances our understanding of flow-mediated valve formation and myocardial function.

Strengths:

Strengths of the study are the significance of the question being addressed, use of the zebrafish model, and data quality (mostly very nice imaging). The text is also well-written and easy to understand.

Weaknesses:

Weaknesses include a lack of rigor for key experimental approaches, which led to skepticism surrounding the main findings. Specific issues were the use of morpholinos instead of genetic mutants for the bmp ligands, cilia gene ift88, and tcf3b, lack of an explicit model surrounding BMP versus blood flow induced endocardial id2b expression, use of bar graphs without dots, the artificial nature of assessing the physical interaction of Tcf3b and Id2b in transfected HEK293 cells, and artificial nature of examining the function of the tcf3b binding sites upstream of nrg1.

We thank the reviewer for the positive assessment and the constructive suggestions. We have performed additional experiments and data analysis to address these issues. A detailed point-by-point response has been incorporated in the response to “Recommendations for the authors” section.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Questions/Concerns:

(1) In the introduction, it would be beneficial to include background information on the id2b gene, what is currently known about its function in heart development/regeneration and in other animal models than just the zebrafish.

We thank the reviewer for the constructive suggestion. In the revised manuscript, we have added a paragraph in the Introduction to provide background on id2b and its role in heart development. Specifically, we discuss its function as a member of the ID (inhibitor of DNA binding) family of helix-loop-helix (HLH) transcriptional regulators and highlight its involvement in cardiogenesis in both zebrafish and mouse models. These additions help place our findings in a broader developmental and evolutionary context (Lines 91-100).

(2) Of the 6 differentially expressed genes identified in Figure 1C, why did the authors choose to focus on id2b and not the other 5 downregulated genes?

We thank the reviewer for the comments. As suggested, we have added a sentence in the revised manuscript to clarify the rationale for selecting id2b as the focus of the present study (Lines 117-121).

(3) As the authors showed representative in situ images for id2b expression with blebbistatin treatment in Figure 1E, and tnn2a MO in Figure 1F, it would also be beneficial to show relative mRNA expression levels for id2b in conditions of blebbistatin treatment and tnn2a MO knockdown. In Fig. 1C: id2b is downregulated with tricaine, but id2a is upregulated with tricaine. Do these genes perform similar or different functions, results of gene duplication events?

We thank the reviewer for the thoughtful suggestion. Our in situ hybridization results demonstrate reduced id2b expression following tricaine, blebbistatin, and tnn2 morpholino treatment. To further validate these observations and enhance cellular resolution, we generated an id2b:eGFP knockin line. Analysis of this reporter line confirmed a significant reduction in id2b expression in the endocardium upon inhibition of cardiac contraction and blood flow (Figure 3A-D), supporting our in situ results. The divergent expression patterns of id2a and id2b in response to tricaine treatment likely reflect functional specification following gene duplication in zebrafish. While our current study focuses on characterizing the role of id2b in zebrafish heart development, the specific function of id2a remains to be determined. 

(4) In Fig. 2b, could the authors compare the id2b fluorescence with RNAscope ISH at 24, 48, and 72 hpf? RNAscope ISH allows for the visualization of single RNA molecules in individual cells. The authors should at least compare these in the heart to demonstrate that id2b accurately reflects the endogenous id2b expression. In Fig. 2E: Suggest showing the individual fluorescent images for id2b:eGFP and kdrl:mCherry in the same colors as top panel images instead of in black and white. In Fig. 2F: The GFP fluorescence from id2b:eGFP signals looks overexposed.

We thank the reviewer for the valuable comment. In response, we attempted RNAscope in situ hybridization on embryos carrying the id2b:eGFP reporter to directly compare fluorescent reporter expression with endogenous id2b transcripts. However, we encountered a significant reduction in id2b:eGFP fluorescence following the RNAscope procedure, and even subsequent immunostaining with anti-GFP antibodies yielded only weak signals. Despite this technical limitation, the RNAscope results independently confirmed id2b expression in endocardial cells (Figure 2E), supporting the specificity and cell-type localization observed with the reporter line. As suggested by the reviewer, we have updated Figure 2G to display id2b:eGFP and kdrl:mCherry images in the same color scheme as the top panel to improve consistency and clarity. Additionally, we have replaced the images in Figure 2F to avoid overexposure and better represent the spatial distribution of id2b:eGFP in adult heart.

(5) In Fig. 3A: are all the images in panel A taken with the same magnification? In Fig. 3e, could the authors show the localization of klf2 and id2b and confirm their expression in the same endocardial cells? In Fig. 3, the authors conclude that klf2-mediated biomechanical signaling is essential for activating id2b expression. This statement is somewhat overstated because they only demonstrated that knockout of klf2 reduced id2b expression.

We thank the reviewer for these constructive comments. All images presented in Figure 3A were captured using the same magnification, as now clarified in the revised figure legend. We appreciate the reviewer’s question regarding the localization of klf2 and id2b. While we were unable to directly visualize both markers in the same embryos due to the current unavailability of klf2 reporter lines, prior studies using klf2a:H2B-eGFP transgenic zebrafish have demonstrated that klf2a is broadly expressed in endocardial cells, with enhanced expression in the atrioventricular canal region (Heckel et al., Curr Bio 2015, PMID: 25959969; Gálvez-Santisteban et al., Elife 2019, PMID: 31237233). Our id2b:eGFP reporter analysis revealed a similarly broad endocardial expression pattern. These independent observations support the likelihood that klf2a and id2b are co-expressed in the same endocardial cell population.   

We also appreciate the reviewer’s comments regarding the connection between biomechanical signaling and id2b expression. Previous studies have already established that biomechanical cues directly regulate klf2 expression in zebrafish endocardial cells (Vermot et al., Plos Biol 2009, PMID: 19924233; Heckel et al., Curr Bio 2015, PMID: 25959969). In the present study, we observed a significant reduction in id2b expression in both klf2a and klf2b mutants, suggesting that id2b acts downstream of klf2. These observations together establish the role of biomechanical cues-klf2-id2b signaling axis in endocardial cells. Nevertheless, we agree with the reviewer that further investigation is required to elucidate the precise mechanism by which klf2 regulates id2b expression.

(6) In Fig. 4: What's the mRNA expression for id2b in WT and id2b mutant fish hearts?

We performed qRT-PCR analysis on purified zebrafish hearts and observed a significant reduction in id2b mRNA levels in id2b mutants compared to wild-type controls. These new results have been incorporated into the revised manuscript (Figure 4A).

(7) In Fig. 5E, the heart rate shows no difference between id2b+/+ and id2b-/- fish according to echocardiography analysis. However, Fig. 5B indicates a difference in heart rate. Could the authors explain this discrepancy?

We thank the reviewer for this insightful observation. In our study, we observed a reduction in heart rate in id2b mutants during embryonic stages (120 hpf), as shown in Figure 5B. However, this difference was not evident in adult fish based on echocardiography analysis (Figure 5E). While the exact reason for these changes during development remains unclear, it is possible that the reduction in cardiac output observed in id2b mutants during early development triggers compensatory mechanisms over time, ultimately restoring heart rate in adulthood. Given that heart rate is primarily regulated by pacemaker activity, further investigation will be required to determine whether such compensatory adaptations occur and to elucidate the underlying mechanisms.

(8) In Fig. 6A: it's a little hard to read the gene names in the left most image in the panel. In Fig. 6B, the authors conducted qRT-PCR analysis of 72 hpf embryonic hearts and validated decreased nrg1 levels in id2b-/- compared to control. Since nrg1 is not specifically expressed in endocardial cells in the developing heart, the authors should isolate endocardial cells and compare nrg1 expression in id2b-/- to control. This would ensure that the loss of id2b affects nrg1 expression derived from endocardial cells rather than other cell types. In Supp Figure S6: Suggest adding an image of the UMAP projection to show tcf3b expression in endocardial cells from sequencing analysis.

We thank the reviewer for these helpful suggestions. In response, we have increased the font size of gene names in the leftmost panel of Figure 6A to improve readability. Regarding nrg1 expression, we acknowledge the importance of assessing its cell-type specificity. Unfortunately, due to the lack of reliable transgenic or knock-in tools for nrg1, its precise expression pattern in embryonic hearts remains unclear. We attempted to isolate endocardial cells from embryonic hearts using FACS, but the limited number of cells obtained at this stage precluded reliable qRT-PCR analysis. Nonetheless, our data show that id2b is specifically expressed in endocardial cells, and publicly available single-cell RNA-seq datasets also support that nrg1 is predominantly expressed in endocardial, but not myocardial or epicardial cells during embryonic heart development (Figure 6-figure supplement 1). These findings suggest that id2b may regulate nrg1 expression in a cell-autonomous manner within the endocardium. As suggested, we have also added a UMAP image to Figure 7-figure supplement 1 to show tcf3b expression in endocardial cells, further supporting the cell identity in single-cell dataset.

(9) In Fig. 6, Nrg1 knockout shows no gross morphological defects and normal trabeculation in larvae. Could the authors explain why they propose that endocardial id2b promotes nrg1 synthesis, thereby enhancing cardiomyocyte contractile function? Did Nrg1 knockdown with Mo lead to compromised calcium signaling and cardiac contractile function? Nrg2a has been reported to be expressed in endocardial cells in larvae, and its loss leads to heart function defects. Perhaps Nrg2a plays a more important role than Nrg1.

We thank the reviewer for raising this important point. Although we did not directly test nrg1 knockout in our study, previous reports have shown that genetic deletion of nrg1 in zebrafish does not impair cardiac trabeculation during embryonic stages (Rasouli et al., Nat Commun 2017, PMID: 28485381; Brown et al., J Cell Mol Med 2018, PMID: 29265764). However, reduced trabecular area and signs of arrhythmia were observed in juvenile and adult fish (Brown et al., J Cell Mol Med 2018, PMID: 29265764), suggesting a potential role for nrg1 in maintaining cardiac structure and function later in development. Whether calcium signaling and cardiac contractility are affected at these stages remains to be determined. Given that morpholino-induced knockdown is limited to early embryonic stages, it is not suitable for assessing nrg1 function in juvenile or adult hearts.

As noted by the reviewer, nrg2a is expressed in endocardial cells, and its deletion has been associated with cardiac defects (Rasouli et al., Nat Commun 2017, PMID: 28485381). To assess its potential involvement in our model, we performed qRT-PCR analysis and observed increased nrg2a expression in id2b mutant hearts (Author response image 1). This upregulation may reflect a compensatory response to the loss of id2b. Therefore, nrg2a is unlikely to play an essential role in mediating the depressed cardiac function in this context.

Author response image 1.

Expression levels of nrg2a. qRT-PCR analysis of nrg2a mRNA in id2b^+/+ and id2b^-/- adult hearts. Data were normalized to the expression of actb1. N=5 biological replicates, with each sample containing two adult hearts.

(10) In Fig. 7A of the IP experiment, it is recommended that the authors establish a negative control using control IgG corresponding to the primary antibody source. This control helps to differentiate non-specific background signal from specific antibody signal.

As suggested, we have included an IgG control corresponding to the primary antibody species in the immunoprecipitation (IP) experiment to distinguish specific from non-specific binding. The updated data are presented in Figure 7A of the revised manuscript.

(11) In Pg. 5, line 115: there is no reference included for previous literature on blebbistatin.

We have added the corresponding reference (Line 126, Reference #5).

In Pg. 5, lines 118-119; pg. 6 line 144: It would be beneficial to include a short sentence describing why choosing a tnnt2a morpholino knockdown to help provide mechanistic context to readers.

We thank the reviewer for the constructive suggestion. In cardiomyocytes, tnnt2a encodes a sarcomeric protein essential for cardiac contraction, and its knockdown is a well-established method for abolishing heartbeat and blood flow in zebrafish embryos, thereby allowing investigation of flow-dependent gene regulation. In the revised manuscript, we have added a sentence and corresponding reference to clarify the rationale for using tnnt2a morpholino in our study (Lines 128-129, Reference #35).

In Pg. 6, line 140: Results title of "Cardiac contraction promotes endocardial id2b expression through primary cilia but not BMP" is misleading and contradicts the results presented in this section and corresponding figure. For example, the bmp Mo knockdown experiments led to decreased id2b fluorescence and the last statement of this results section contradicts the title that BMP does not promote endocardial id2b in lines 179-180: "Collectively, these results suggest that BMP signaling and blood flow modulate id2b expression in a developmental-stage-dependent manner." It would be helpful to clarify whether BMP signaling is involved in id2b expression or not.

We apologize for any confusion caused by the section title. Our results demonstrate that id2b expression is regulated by both BMP signaling and biomechanical forces in a developmental-stage-specific manner. Specifically, morpholino-mediated knockdown of bmp2b, bmp4, and bmp7a at the 1-cell stage significantly reduced id2b:eGFP fluorescence at 24 hpf (Figure 3-figure supplement 1A, B), suggesting that id2b is responsive to BMP signaling during early embryonic development. However, treatment with the BMP inhibitor Dorsomorphin during later stages (24-48 or 36-60 hpf) did not significantly alter id2b:eGFP fluorescence intensity in individual endocardial cells, although a modest reduction in total endocardial cell number was noted (Figure 3-figure supplement 1C, D). These results suggest that BMP signaling is required for id2b expression during early development but becomes dispensable at later stages, when biomechanical cues may play a more prominent role. To address this concern and better reflect the data, we have revised the Results section title to: "BMP signaling and cardiac contraction regulate id2b expression". This revised title more accurately reflects the dual regulation of id2b expression (Line 153).

In line 205: Any speculation on why the hemodynamics was preserved between id2b mutant and WT siblings at 96 hpf?

As suggested, we have included a sentence to address this observation. “Surprisingly, the pattern of hemodynamics was largely preserved in id2b^-/- embryos compared to id2b^+/+ siblings at 96 hpf (Figure 4-figure supplement 1E, Video 1, 2), suggesting that the reduced number of endocardial cells in the AVC region was not sufficient to induce functional defects.” (Lines 223-225)

In line 246: Fig. 6k and 6j are referenced, but should be figure 5k and 5j.

We have corrected this in the revised manuscript.

Reviewer #2 (Recommendations for the authors):

he manuscript was overall well explained, aside from a few minor points that would help facilitate reader comprehension:

(1) The last paragraph of the introduction could be a brief summary of the study.

We thank the reviewer for this constructive suggestion. As recommended, we have included a paragraph in the Introduction section summarizing our key findings to provide clearer context for the study (Lines 96-100).

(2) Lines 127-128: 'revealed a substantial recapitulation of the... of endogenous id2b expression' may need to be rephrased.

We thank the reviewer for the valuable suggestion. In the revised manuscript, we have changed the sentence to: “Comparison of id2b:eGFP fluorescence with in situ hybridization at 24, 48, and 72 hpf revealed that the reporter signal closely recapitulates the endogenous id2b expression pattern.” (Lines 137-139)

(3) Line 182: '... in a developmental-stage-dependent manner' sounds a bit ambiguous, may need to slightly elaborate/ clarify what this means.

We thank the reviewer for the helpful comment. To improve clarity, we have revised the statement to: “Collectively, these results suggest that id2b expression is regulated by both BMP and biomechanical signaling, with the relative contribution of each pathway varying across developmental stages.” (Lines 195-197)

Reviewer #3 (Recommendations for the authors):

(1) The conclusion that BMP signaling prior to 24 hpf is necessary for id2b expression is not fully supported by the data. How do the authors envision pre-linear heart tube BMP signaling impacting endocardial id2b expression during later chamber stages? Id2b reporter fluorescence can be clearly visualized in the linear heart tube in panel B from Figure 1. Does id2b expression initiate prior to contraction? Can the model be refined by showing when id2b endocardial reporter fluorescence is first observed, and whether this early/pre-contractile expression is dependent on BMP signaling?

We thank the reviewer for the important comment. As suggested, we performed morpholino-mediated knockdown of bmp2b, bmp4, and bmp7a at the 1-cell stage. Live imaging at 24 hpf showed significantly reduced id2b:eGFP fluorescence compared to controls (Figure 3-figure supplement 1A, B), suggesting that id2b is responsive to BMP signaling during early embryonic development. However, treatment with the BMP inhibitor Dorsomorphin during 24-48 or 36-60 hpf did not significantly impact id2b:eGFP fluorescence intensity in individual endocardial cells, although a reduction in endocardial cell number was observed (Figure 3-figure supplement 1C, D). These results suggest that BMP signaling is essential for id2b expression during early embryonic development, while it becomes dispensable at later stages, when biomechanical cues exert a more significant role.

(2) Overexpressing tagged versions of TCF3b and Id2b in HEK293 cells is a very artificial way to make the major claim that these two proteins interact in endogenous endocardial cells. Can this be done in zebrafish embryonic or adult hearts?

We thank the reviewer for this insightful comment. As suggested, we synthesized Flag-id2b and HA-tcf3b mRNA and co-injected them into 1-cell stage zebrafish embryos. We collected 100-300 embryos at 12, 24, and 48 hpf and performed western blot analysis using the same anti-HA and anti-Flag antibodies validated in HEK293 cell experiments. Despite multiple independent attempts, we were unable to detect clear bands of the tagged proteins in zebrafish embryos. We speculate that this could be due to mRNA instability, translational efficiency, or the low abundance of Id2b and Tcf3b proteins. We have acknowledged these technical limitations in the revised manuscript and clarified that the HEK293 cell data support a potential interaction between Id2b and Tcf3b, while confirming their endogenous interaction will require further investigations (Lines 295-296).

(3) The data presented are consistent with the claim that the tcf3b binding sites are functional upstream of nrg1 to repress its transcription. To fully support this idea, those two sites should be disrupted with gRNAs if possible.

We thank the reviewer for the valuable suggestion. In response, we attempted to disrupt the tcf3b binding sites using sgRNAs. However, we encountered technical difficulties in identifying sgRNAs that specifically and efficiently target these binding sites without affecting adjacent regions. Despite these challenges, our luciferase reporter assay, using tcf3b mRNA overexpression and morpholino knockdown, clearly demonstrated that tcf3b binds to and regulates nrg1 promoter region. Nevertheless, we acknowledge that future study using genome editing will be necessary to validate the direct binding of tcf3b to nrg1 promoter.

Minor Points:

(1) Must remove all of the "data not shown" statements and add the primary data to the Supplemental Figures.

As suggested, we have removed all of the “data not shown” statements and added the original data to the revised manuscript (Figure 4E, middle panels, and Figure 4-figure supplement 1F)

(2) Must present the order of the panels in the figure as they are presented in the text. One example is Figure 6 where 6E is discussed in the text before 6C and 6D.

We thank the reviewer for bring up this important point. In the revised manuscript, we have carefully revised the manuscript to ensure that the order of figure panels matches the sequence in which they are discussed in the text. Specifically, we have reorganized the presentation of Figure 6 panels to align with the text flow, discussing panels 6C and 6D before panel 6E. The updated figure and corresponding text have been corrected accordingly in the revised manuscript.

(3) Change the italicized gene names (e.g. tcf3b) to non-italicized names with the first letter capitalized (e.g. Tcf3b) when referencing the protein.

As suggested, we have revised the manuscript to use non-italicized names with the first letter capitalized when referring to proteins.

(4) All bar graphs should be replaced with dot bar graphs.

We have replaced all bar graphs with dot bar graphs throughout the manuscript.

(5) The new id2b mutant allele should be validated as a true null using quantitative RT-PCR to show that the message becomes destabilized through non-sense mediated decay or by immunostaining/western blot analysis if there is a zebrafish Id2b-specific antibody available.

We thank the reviewer for this important suggestion. We have performed qRT-PCR analysis and detected a significant reduction in id2b mRNA levels in id2b^-/- compared to id2b^+/+ controls. These new results are presented in Figure 4A of the revised manuscript.

(6) Was tricaine used to anesthetize embryos for capturing heart rate and percent fractional area change? This analysis should be performed with no or very limited tricaine as it affects heart rate and systolic function. These parameters were captured at 120 hpf, but the authors should also look earlier at 72 hpf at a time when valves are not present by calcium transients are necessary to support heart function.

We thank the reviewer for this important comment. When performing live imaging to assess cardiac contractile function, we used low-dose tricaine (0.16 mg/mL) to anesthetize the zebrafish embryos. We have included this important information in the Methods section (Line 503). As suggested, we have also included the heart function results at 72 hpf, which are now presented in Figure 5-figure supplement 2A-C of the revised manuscript.

(7) The alpha-actinin staining in Figure 5-supplement 2D is very pixelated and unconvincing. This should be repeated and imaged at a higher resolution.

As suggested, we have re-performed the α-actinin staining and acquired higher-resolution images. The updated results are now presented in Figure 5-figure supplement 2G of the revised manuscript.

(8) The authors claim that reductions in id2b mutant heart contractility are due to perturbed calcium transients instead of sarcomere integrity. Why do the authors think that regulation of calcium dynamics was not observed in the DEG enriched GO-terms? Was significant downregulation of cacna1 identified in the bulk RNAseq?

We thank the reviewer for raising this important point. In our bulk RNAseq dataset comparing id2b mutant and control hearts, GO term enrichment was primarily associated with pathways related to cardiac muscle contraction and heart contraction (Figure 5-figure supplement 1B). We speculate that the transcriptional changes related to calcium dynamics may be relatively subtle and thus were not captured as significantly enriched GO terms. In addition, our qRT-PCR analysis revealed a significant reduction in cacna1c expression in id2b mutant hearts compared to controls, suggesting that id2b deletion impairs calcium channel expression. However, this change was not detected by RNA-seq, likely due to limitations in sensitivity.

(9) In line 277, the authors say, "To determine whether this interaction occurs in zebrafish, Flag-id2b and HA-tcf3b were co-expressed in HEK293 cells...". This should be re-phrased to, "To determine if zebrafish Id2b and Tcf3b interact in vitro, Flag-id2b and HA-tcf3b were co-expressed in HEK293 cells for co-immunoprecipitation analysis." The sentence in line 275 should be changed to, "....heterodimer with Tcf3b to limit its function as a potent transcriptional repressor."

We thank the reviewer for these constructive comments and have revised the text accordingly (Lines 291-294).

(10) Small text corrections or ideas:

Line 63: emphasized

We have corrected this in the revised manuscript.

Line 71: studied signaling pathways

We have corrected this in the revised manuscript.

Line 106: the top 6 DEGS (I think that the authors mean top 6 GO-terms) and is Id2b in one of the enriched GO categories?

id2b is one of the top DEGs. This point has been clarified in the revised manuscript (Lines 116-117).

Line 125: a knockin id2b:eGFP reporter line

We have corrected this in the revised manuscript (Line 136).

Line 138: This paragraph could use a conclusion sentence.

We have added a conclusion sentence in the revised manuscript (Lines 150-151).

Line 190: id2b-/- zebrafish experienced early lethality

We have revised the statement as suggested (Line 206).

Line 193: The prominent enlargement of the atrium with a smaller ventricle has characterized as cardiomyopathy in zebrafish (Weeks et al. Cardiovasc Res, 2024, PMID: 38900908), which has also been associated with disruptions in calcium transients (Kamel et al J Cardiovasc Dev Dis, 2021, PMID: 33924051 and Kamel et al, Nat Commun 2021, PMID: 34887420). This information should be included in the text along with these references.

We thank the reviewer for this helpful suggestion. We have incorporated these important references into the revised manuscript and included the relevant information to acknowledge the established link between atrial enlargement, cardiomyopathy, and disrupted calcium transients in zebrafish models (Reference #41, 42, and 45; Lines 210 and 260).

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 original reviews

We thank the three reviewers for their insightful feedback. We look forward to addressing the raised concerns in a revised version of the manuscript. There were a few common themes among the reviews that we will briefly touch upon now, and we will provide more details in the revised manuscript. 

First, the reviewers asked for the reasoning behind the task ratios we implemented for the different attentional width conditions. The different ratios were selected to be as similar as possible given the size and spacing of our stimuli (aside from the narrowest cue width of one bin, the ratios for the others were 0.66, .6 and .66). As Figure 1b shows, while the ratios were similar, task difficulty is not constant across cue widths: spreading attention makes the task more difficult generally. But, while the modeled width of the spatial distribution of attention changes monotonically with cue width, task difficulty does not. Furthermore, prior work has indicated that there is a relationship between task difficulty and the overall magnitude of the BOLD response, however we don’t suspect that this will influence the width of the modulation. How task difficulty influences the BOLD response is an important topic, and we hope that future work will investigate this relationship more directly.   

Second, reviewers raised interest in the distribution of spatial attention in higher visual areas. In our study we focus only on early visual regions (V1-V3). This was primarily driven by pragmatic considerations, in that we only have retinotopic estimates for our participants in these early visual areas. Our modeling approach is dependent on having access to the population receptive field estimates for all voxels, and while the main experiment was scanned using whole brain coverage, retinotopy was measured in a separate session using a field of view only covering the occipital cortex.  

Lastly, we appreciate the opportunity to clarify the purpose of the temporal interval analysis. The reviewer is correct in assuming we set out to test how much data is needed to recover the cortical modulation and how dynamic a signal the method can capture. This analysis does show that more data provides more reliable estimates, though the model was still able to recover the location and width of the attentional cue at shorter timescales of as few as two TRs. This has implications for future studies that may involve more dynamic tracking of the attentional field.

Public Reviews

Reviewer #1 (Public review): 

The authors conducted an fMRI study to investigate the neural effects of sustaining attention to areas of different sizes. Participants were instructed to attend to alphanumeric characters arranged in a circular array. The size of attention field was manipulated in four levels, ranging from small (18 deg) to large (162 deg). They used a model-based method to visualize attentional modulation in early visual cortex V1 to V3, and found spatially congruent modulations of the BOLD response, i.e., as the attended area increased in size, the neural modulation also increased in size in the visual cortex. They suggest that this result is a neural manifestation of the zoomlens model of attention and that the model-based method can effectively reconstruct the neural modulation in the cortical space. 

The study is well-designed with sophisticated and comprehensive data analysis. The results are robust and show strong support for a well-known model of spatial attention, the zoom-lens model. Overall, I find the results interesting and useful for the field of visual attention research. I have questions about some aspects of the results and analysis as well as the bigger picture. 

(1) It appears that the modulation in V1 is weaker than V2 and V3 (Fig 2). In particular, the width modulation in V1 is not statistically significant (Fig 5). This result seems a bit unexpected. Given the known RF properties of neurons in these areas, in particular, smaller RF in V1, one might expect more spatially sensitive modulation in V1 than V2/V3. Some explanations and discussions would be helpful. Relatedly, one would also naturally wonder if this method can be applied to other extrastriate visual areas such as V4 and what the results look like. 

We agree with the reviewer. It’s very interesting how the spatial resolution within different visual regions contributes to the overall modulation of the attentional field, and how this in turn would influence perception. Our data showed that fits in V1 appeared to be less precise than in V2 and V3. This can be seen in the goodness of fit of the model as well as the gain and absolute angular error estimates. The goodness of fit and gain were lowest in V1 and the absolute angular error was largest in V1 (see Figure 5). We speculate that the finer spatial granularity of V1 RFs was countered by a lower amplitude and SNR of attention-related modulation in V1, resulting in overall lower sensitivity to variation in attentional field width. Prior findings concur that the magnitude of covert spatial attention increases when moving from striate to extrastriate cortex (Bressler & Silver (2010); Buracas & Boynton (2007)). Notably, in our perception condition, V1 showed more spatially sensitive modulation (see Figure 7), consistent with the known RF properties of V1 neurons.

Regarding the second point: unfortunately, our dataset did not allow us to explore higherorder cortical regions with the model-based approach. While the main experiment was scanned using a sequence with whole brain coverage, the pRF estimates came from a separate scanning session which only had limited occipital coverage. Our modeling approach is dependent on the polar angle estimates from this pRF session. We now explicitly state this limitation in the methods (lines 87-89):

“In this session, the field of view was restricted to the occipital cortex to maximize SNR, thereby limiting the brain regions for which we had pRF estimates to V1, V2, and V3.”

(2) I'm a bit confused about the angular error result. Fig 4 shows that the mean angular error is close to zero, but Fig 5 reports these values to be about 30-40 deg. Why the big discrepancy? Is it due to the latter reporting absolute errors? It seems reporting the overall bias is more useful than absolute value. 

The reviewer’s inference here is exactly right: Figure 4 shows signed error, whereas Figure 5 shows absolute error. We show the signed error for the example participant because, (1) by presenting the full distribution of model estimates for one participant, readers have access to a more direct representation of the data, and (2) at the individual level it is possible to examine potential directional biases in the location estimates (which do not appear to be present). As we don’t suspect a consistent directional bias across the group, we believe the absolute error in location estimates is more informative in depicting the precision in location estimates using the model-based approach. In the revised manuscript, we modified Figure 5 to make the example participant’s data visually distinct for easy comparison. We have clarified this reasoning in the text (results lines 59-64):

“The angular error distribution across blocks, separated by width condition, is shown in Figure 4 for one example participant to display block-to-block variation. The model reliably captured the location of the attentional field with low angular error and with no systematic directional bias. This result was observed across participants. We next examined the absolute angular error to assess the overall accuracy of our estimates.”

(3) A significant effect is reported for amplitude in V3 (line 78), but the graph in Fig 5 shows hardly any difference. Please confirm the finding and also explain the directionality of the effect if there is indeed one. 

We realize that the y-axis scale of Figure 5 was making it difficult to see that gain decreases with cue width in area V3. Instead of keeping the y-axis limits the same across visual regions, we now adapt the y-axis scale of each subplot to the range of data values:  

We now also add the direction of the effect in the text (results lines 83-86):

“We observed no significant relationship between gain and cue width in V1 and V2 (V1 t(7)=.54, p=.605; V2 t(7)=-2.19, p=.065), though we did find a significant effect in V3 illustrating that gain decreases with cue width (t(7)=-3.12, p=.017).”

(4) The purpose of the temporal interval analysis is rather unclear. I assume it has to do with how much data is needed to recover the cortical modulation and hence how dynamic a signal the method can capture. While the results make sense (i.e., more data is better), there is no obvious conclusion and/or interpretation of its meaning. 

We apologize for not making our reasoning clear. We now emphasize our reasoning in the revised manuscript (results lines 110-112). Our objective was to quantify how much data was needed to recover the dynamic signal. As expected, we found that including more data reduces noise (averaging helps), but importantly, we found that we still obtained meaningful model fits even with limited data. We believe this has important implications for future paradigms that explore more dynamic deployment of spatial attention, where one would not want to average over multiple repetitions of a condition.

The first paragraph of the Temporal Interval Analysis section in the results now reads: 

“In the previous analyses, we leveraged the fact that the attentional cue remained constant for 5-trial blocks (spatial profiles were computed by averaging BOLD measurements across a block of 10 TRs). We next examined the degree to which we were able to recover the attentional field on a moment-by-moment (TR-by-TR) basis. To do this, we systematically adjusted the number of TRs that contributed to the averaged spatial response profile. To maintain a constant number of observations across the temporal interval conditions, we randomly sampled a subset of TRs from each block. This allowed us to determine the amount of data needed to recover the attentional field, with a goal of examining the usability of our modeling approach in future paradigms involving more dynamic deployment of spatial attention.”

(5) I think it would be useful for the authors to make a more explicit connection to previous studies in this literature. In particular, two studies seem particularly relevant. First, how do the present results relate to those in Muller et al (2003, reference 37), which also found a zoom-lens type of neural effects. Second, how does the present method compare with spatial encoding model in Sprague & Serences (2013, reference 56), which also reconstructs the neural modulation of spatial attention. More discussions of these studies will help put the current study in the larger context.

We now make a more explicit connection to prior work in the discussion section (lines 34-54). 

“We introduced a novel modeling approach that recovered the location and the size of the attentional field. Our data show that the estimated spatial spread of attentional modulation (as indicated by the recovered FWHM) consistently broadened with the cue width, replicating prior work (Müller et al., 2003; Herrmann et al., 2010). Our results go beyond prior work by linking the spatial profiles to pRF estimates, allowing us to quantify the spread of both attentional and perceptual modulation in degrees of polar angle. Interestingly, the FWHM estimates for the attentional and perceptual spatial profiles were highly similar. Additionally, for area V3 we replicate that the population response magnitude decreased with cue width (Müller et al., 2003; Feldmann-Wüstefeld and Awh, 2020). One innovation of our method is that it directly reconstructs attention-driven modulations of responses in visual cortex, setting it apart from other methods, such as inverted encoding models (e.g. Sprague & Serences, 2013). Finally, we demonstrated that our method has potential to be used in more dynamic settings, in which changes in the attentional field need to be tracked on a shorter timescale.”

(6) Fig 4b, referenced on line 123, does not exist. 

We have corrected the text to reference the appropriate figure (Figure 5, results line 136).

Reviewer #2 (Public review):

Summary: 

The study in question utilizes functional magnetic resonance imaging (fMRI) to dynamically estimate the locus and extent of covert spatial attention from visuocortical activity. The authors aim to address an important gap in our understanding of how the size of the attentional field is represented within the visual cortex. They present a novel paradigm that allows for the estimation of the spatial tuning of the attentional field and demonstrate the ability to reliably recover both the location and width of the attentional field based on BOLD responses. 

Strengths: 

(1) Innovative Paradigm: The development of a new approach to estimate the spatial tuning of the attentional field is a significant strength of this study. It provides a fresh perspective on how spatial attention modulates visual perception. 

(2) Refined fMRI Analysis: The use of fMRI to track the spatial tuning of the attentional field across different visual regions is methodologically rigorous and provides valuable insights into the neural mechanisms underlying attentional modulation. 

(3) Clear Presentation: The manuscript is well-organized, and the results are presented clearly, which aids in the reader's comprehension of the complex data and analyses involved. 

We thank the reviewer for summarizing the strengths in our work. 

Weaknesses: 

(1) Lack of Neutral Cue Condition: The study does not include a neutral cue condition where the cue width spans 360°, which could serve as a valuable baseline for assessing the BOLD response enhancements and diminishments in both attended and non-attended areas. 

We do not think that the lack of a neutral cue condition substantially limits our ability to address the core questions of interest in the present work. We set out to estimate the locus and the spread of covert spatial attention. By definition, a neutral cue does not have a focus of attention as the whole annulus becomes task relevant. We agree with the reviewer that how spatial attention influences the magnitude of the BOLD response is still not well defined; i.e., does attending a location multiplicatively enhance responses at an attended location or does it instead act to suppress responses outside the focus of attention? A neutral cue condition would be necessary to be able to explore these types of questions. However, our findings don’t rest on any assumptions about this. Instead, we quantify the attentional modulation with a model-based approach and show that we can reliably recover its locus, and reveal a broadening in the attentional modulation with wider cues. 

We realize that throughout the original manuscript we often used the term ‘attentional enhancement,’ which might inadvertently specify an increase with respect to a neutral condition. To be more agnostic to the directionality of the effect, we have changed this to ‘attentional modulation’ and ‘attentional gain’ throughout the manuscript. Additionally, we have added results and visualizations for the baseline parameter to all results figures (Figures 4-7) to help readers further interpret our findings.  

(2) Clarity on Task Difficulty Ratios: The explicit reasoning for the chosen letter-to-number ratios for various cue widths is not detailed. Ensuring clarity on these ratios is crucial, as it affects the task difficulty and the comparability of behavioral performance across different cue widths. It is essential that observed differences in behavior and BOLD signals are attributable solely to changes in cue width and not confounded by variations in task difficulty.  

The ratios were selected to be as similar as possible given the size and spacing of our stimuli (aside from the narrowest cue width of one bin, the proportions for the others were 0.67, 0.60, and 0.67). We have updated the methods section to state this explicitly (methods lines 36-38): 

“The ratios were selected to be as similar as possible given the size and spacing of our stimuli (aside from the one-bin cue, the proportions for the other cues were 0.67, 0.60, 0.67).”

As Figure 1b shows, task accuracy showed small and non-monotonic changes across the three larger cue widths, dissociable from the monotonic pattern seen for the modelestimated width of the attentional field. Furthermore, as prior work has indicated that there is a relationship between task difficulty and the overall magnitude of the BOLD response (e.g., Ress, Backus & Heeger, 2000), we would primarily expect effects of task difficulty on the gain or baseline rather than the width. How exactly task difficulty influences the BOLD response and whether this would, in fact, interact with the width of the attentional field is an important topic, and we hope that future work will investigate this relationship more directly.  

We have clarified these points within the text, and now explicitly motivate future work looking at these important interactions (discussion lines 57-67):

“The observed effects of attentional field width were unlikely to be directly attributable to variation in task difficulty. Participants' task in our study was to discriminate whether more numbers or more letters were presented within a cued region of an iso-eccentric annulus of white noise. For our different cue widths, the ratios of numbers and letters were selected to be as similar as possible given the size and spacing of our stimuli. Changes in accuracy across the three larger cue widths were small and non-monotonic, implying task difficulty was dissociable from width per se. This dissociation bolsters the interpretability of our model fits; nevertheless, future work should further investigate how task difficulty interacts with the spread of the attentional field and the amplitude of attention-related BOLD effects (cf. Ress, Backus & Heeger, 2000).”

Reviewer #3 (Public review):

Summary: 

In this report, the authors tested how manipulating the contiguous set of stimuli on the screen that should be used to guide behavior - that is, the scope of visual spatial attention - impacts the magnitude and profile of well-established attentional enhancements in visual retinotopic cortex. During fMRI scanning, participants attended to a cued section of the screen for blocks of trials and performed a letter vs digit discrimination task at each attended location (and judged whether the majority of characters were letters/digits). Importantly, the visual stimulus was identical across attention conditions, so any observed response modulations are due to topdown task demands rather than visual input. The authors employ population receptive field (pRF) models, which are used to sort voxel activation with respect to the location and scope of spatial attention and fit a Gaussian-like function to the profile of attentional enhancement from each region and condition. The authors find that attending to a broader region of space expands the profile of attentional enhancement across the cortex (with a larger effect in higher visual areas), but does not strongly impact the magnitude of this enhancement, such that each attended stimulus is enhanced to a similar degree. Interestingly, these modulations, overall, mimic changes in response properties caused by changes to the stimulus itself (increase in contrast matching the attended location in the primary experiment). The finding that attentional enhancement primarily broadens, but does not substantially weaken in most regions, is an important addition to our understanding of the impact of distributed attention on neural responses, and will provide meaningful constraints to neural models of attentional enhancement. 

Strengths: 

(1) Well-designed manipulations (changing location and scope of spatial attention), and careful retinotopic/pRF mapping, allow for a robust assay of the spatial profile of attentional enhancement, which has not been carefully measured in previous studies.

(2) Results are overall clear, especially concerning width of the spatial region of attentional enhancement, and lack of clear and consistent evidence for reduction in the amplitude of enhancement profile.

(3) Model-fitting to characterize spatial scope of enhancement improves interpretability of findings.

We thank the reviewer for highlighting the strengths of our study. 

Weaknesses: 

(1) Task difficulty seems to vary as a function of spatial scope of attention, with varying ratios of letters/digits across spatial scope conditions, which may complicate interpretations of neural modulation results  

The reviewer is correct in observing that task accuracy varied across cue widths. Though we selected the task ratios to be as similar as possible given the size and spacing of our stimuli (aside from the narrowest cue width of one bin, the proportions for the others were 0.67, 0.60, and 0.67), behavioral accuracy across the three larger cue widths was not identical. Prior research has shown that there is a relationship between task difficulty and the overall magnitude of the BOLD response (e.g., Ress, Backus & Heeger, 2000). Thus, we would primarily expect effects of task difficulty on gain rather than width. How task difficulty influences the BOLD response and whether this would, in fact, interact with the width of the attentional field is an important topic, and we hope that future work will investigate this relationship more directly.  

To clarify these points and highlight the potential for future work looking at these important interactions, we added the following text to the discussion section (discussion lines 57-67):

“The observed effects of attentional field width were unlikely to be directly attributable to variation in task difficulty. Participants' task in our study was to discriminate whether more numbers or more letters were presented within a cued region of an iso-eccentric annulus of white noise. For our different cue widths, the ratios of numbers and letters were selected to be as similar as possible given the size and spacing of our stimuli. Changes in accuracy across the three larger cue widths were small and non-monotonic, implying task difficulty was dissociable from width per se. This dissociation bolsters the interpretability of our model fits; nevertheless, future work should further investigate how task difficulty interacts with the spread of the attentional field and the amplitude of attention-related BOLD effects (cf. Ress, Backus and Heeger, 2000).”

(2) Some aspects of analysis/data sorting are unclear (e.g., how are voxels selected for analyses?) 

We apologize for not describing our voxel selection in sufficient detail. Some of the questions raised in the private comments are closely related to this point, we therefore aim to clarify all concerns below:

- Voxel selection: To select voxels that contribute to the 1D spatial profiles, we relied on the independent pRF dataset. We first defined some general requirements that needed to be met. Specifically, 1) the goodness of fit (R²) of the pRF fits needed to be greater than 10%; 2) the estimated eccentricity had to fall within [0.7 9.1] degree eccentricity (to exclude voxels in the fovea and voxels with estimated eccentricities larger than the pRF mapping stimulus); 3) the estimated size must be greater than 0.01 degree visual angle. 

Next, we included only voxels whose pRF overlapped with the white noise annulus. Estimated eccentricity was used to select all voxels whose eccentricity estimate fell within the annulus bounds. However, here it is also important to take the size of the pRF into account. Some voxels’ estimated eccentricity might fall just outside the annulus, but will still have substantial overlap due to the size of their pRF. Therefore, we further included all voxels whose estimated pRF size resulted in overlap with the annulus. 

This implies that some voxels with greater eccentricities and larger pRF sizes contribute to the 1D profile, which will influence the spatial specificity of the 1D profiles. However, we want to emphasize that in our view, the exact FWHM value is not so much of interest, as this will always be dependent on the voxel selection and many other data processing steps. Instead, we focus on the relative differences of the FWHM driven by the parametric attentional cue width manipulation. 

- Data sorting and binning. The reviewer raises an important point about how the FWHM value should be interpreted considering the data processing steps. To generate the 1D spatial profile, we binned voxels based on their estimated polar angle preference into 6degree bins and applied a moving average of 18 degrees to smooth the 1D profiles. Both of these processing steps will influence the spatial specificity of the profile. The binning step facilitates recentering based on cue center and combining across trials.

To explore the extent to which the moving average substantially impacted our results, we reran our analyses without that smoothing step. The vast majority of the results held. In V1, we found a significant effect of cue width on FWHM where the result was not significant previously (t(7)=2.52, p\=.040). Additionally, when looking at the minimum number of TRs needed to see a significant effect of cue width on FWHM, without the smoothing step in V1 it took 10 TRs (not significant at 10 TRs previously), in V2 it took 5 TRs (10 previously), and in V3 it took 3 TRs (2 previously). The other notable difference is that FWHM was generally a bit larger when the moving average smoothing was performed. We have visualized the group results for the FWHM estimates below to help with comparison. 

Author response image 1.

No moving average smoothing:

Voxel selection methods have been clarified in methods section lines 132-139:

“Within each ROI, pRF modeling results were used to constrain voxel selection used in the main experiment. We excluded voxels with a preferred eccentricity outside the bounds of the pRF stimulus (<0.7° and >9.1°), with a pRF size smaller than 0.01°, or with poor spatial selectivity as indicated by the pRF model fit (R2 < 10%). Following our 2D visualizations (see below), we further constrained voxel selection by only including voxels whose pRF overlapped with the white noise annulus. We included all voxels with an estimated eccentricity within the annulus bounds, as well as voxels with an estimated pRF size that would overlap the annulus.”

Data binning methods have been clarified in methods section lines 154-159: 

“Voxels with pRFs overlapping the white noise annulus were grouped into 60 bins according to their pRF polar angle estimate (6° polar angle bin width). We computed a median BOLD response within each bin. This facilitated the recentering of each profile to align all cue centers for subsequent combining across trials. To improve the signal-to-noise ratio, the resulting profile was smoothed with a moving average filter (width 18° polar angle; see Figure 2b).”

(3) While the focus of this report is on modulations of visual cortex responses due to attention, the lack of inclusion of results from other retinotopic areas (e.g. V3AB, hV4, IPS regions like IPS0/1) is a weakness 

We agree with the reviewer that using this approach in other retinotopic areas would be of significant interest. In this case, population receptive field mapping occurred in a separate session with a field of view only covering the occipital cortex (in contrast to the experimental session, which had whole-brain coverage). Because our modeling approach relies on these pRF estimates, we were unable to explore higher visual areas. However, we hope future work will follow up on this.

We have added the following text to the methods section describing the pRF mapping session (lines 87-89):

“In this session, the field of view was restricted to the occipital cortex to maximize SNR, thereby limiting the brain regions for which we had pRF estimates to V1, V2, and V3.”

(4) Additional analyses comparing model fits across amounts of data analyzed suggest the model fitting procedure is biased, with some parameters (e.g., FWHM, error, gain) scaling with noise. 

In this analysis, we sought to test how much data was needed to recover the attentional field, in view of the need for additional fMRI-based tools for use in tasks that involve more rapid dynamic adaptation of attention. Though we did find that more data reduced noise (and accordingly decreased absolute error and amplitude while increasing FWHM and R²), absolute angular error remained low across different temporal intervals (well below the chance level of 90°). With regard to FWHM, we believe that the more important finding is that the model-estimated FWHM was modulated by cue width at shorter timescales of as few as two TRs while maintaining relatively low angular error. We refrain from drawing conclusions here on the basis of the exact FWHM values, both because we don’t have a ground truth for the attentional field and because various processing pipeline steps can impact the values as well. Rather, we are looking at relative value and overall patterns in the estimates. The observed patterns imply that the model recovers meaningful modulation of the attentional field even at shorter time scales.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Additional data reporting and discussion of results are needed as outlined in the public review. 

Reviewer #2 (Recommendations for the authors):

(1) The current experimental design effectively captured the impact of varying cue widths on the BOLD response in the visual cortex. However, the inclusion of a neutral cue condition, where the cue width spans 360{degree sign} and all peripheral stimuli are attended, could serve as a valuable baseline. This would enable a quantitative assessment of how much the BOLD response is enhanced in specific spatial regions due to focused cues and, conversely, how much it is diminished in non-attended areas, along with the spatial extent of these effects. 

Please refer to our response in the public review. 

(2) While the study provides valuable insights into BOLD signal changes in visual areas corresponding to the focus of attention, it does not extend its analysis to the impact on regions outside the focus of attention. It would be beneficial to explore whether there is a corresponding decrease in BOLD signal in non-attended regions, and if identified, to describe the spatial extent and position of this effect relative to the attended area. Such an analysis could yield deeper insights into how attention influences activity across the visual cortex. 

We agree with the reviewer that it is very interesting to examine the spread of attention across the whole visual field. Our experiment was designed to focus on width modulations at a fixed eccentricity, but future work should explore how the attentional field changes with eccentricity and interacts with spatial variations across the visual field. This is highlighted in our discussion section (lines 76-81): 

“Future work can help provide a better understanding of the contribution of spatial attention by considering how the attentional field interacts with these well described spatial variations across the visual field. Measuring the full spatial distribution of the attentional field (across both eccentricity and polar angle) will shed light on how spatial attention guides perception by interacting with the non-uniformity of spatial representations.”

The addition of figure panels for the estimated baseline parameter in Figures 4-7 provides further information about BOLD effects in unattended regions of the annulus.  

(3) The rationale behind the selection of task difficulty ratios for different cue widths, specifically the letter-to-number ratios of 1:0, 1:2, 2:3, and 3:6 (or vice versa) for cue widths of 18{degree sign}, 54{degree sign}, 90{degree sign}, and 162{degree sign} respectively, was not explicitly discussed. It would be beneficial to clarify the basis for these ratios, as they may influence the perceived difficulty of the task and thus the comparability of behavioral performance across different cue widths. Ensuring that the task difficulty is consistent across conditions is crucial for attributing differences in behavior and BOLD signals solely to changes in cue width and not confounded by variations in task difficulty. 

Please refer to our response in the public review. We now clarify why we selected these ratios, and acknowledge more explicitly that behavioral performance differed across width conditions. See also our reply to private comment 1 from Reviewer 3 for some additional analyses examining task related influences.

Reviewer #3 (Recommendations for the authors):

(1) Task difficulty: the task seems exceptionally challenging. Stimuli are presented at a relativelyeccentric position for a very brief duration, and a large number of comparisons must be made across a broad region of space. This is reflected in the behavioral performance, which decreases rapidly as the scope of attention increases (Fig. 1). Because trials are blocked, does this change in task difficulty across conditions impact the degree to which neural responses are modulated? How should we consider differences in task difficulty in interpreting the conclusions (especially with respect to the amplitude parameter)? Also, note that the difficulty scales both with number of stimuli - as more need to be compared - but also with the ratio, which differs nonmonotonically across task conditions. One way to dissociate these might be RT: for 54/162, which both employ the same ratio of letter/digits and have similar accuracy, is RT longer for 162, which requires attending more stimuli? 

In addition to our comments in response to the public review, we emphasize that the reviewer makes an important point that there are differences in task difficulty, though the ratios are as close as they can be given the size and spacing of our stimuli. Behavioral performance varied non-monotonically with cue width, bolstering our confidence that our monotonically increasing model-estimated width is likely not entirely driven by task difficulty. There nevertheless remain open questions related to how task difficulty does impact BOLD attentional modulation, which we hope future work will more directly investigate.

The reviewer's comments identify two ways our data might preliminarily speak to questions about BOLD attentional modulation and task difficulty. First: how might the amplitude parameter reflect task difficulty? This is an apt question as we agree with the reviewer that it would be a likely candidate in which to observe effects of task difficulty. We do find a small effect of cue width on our amplitude estimates (amplitude decreases with width) in V3. Using the same analysis technique to look at the relationship between task difficulty and amplitude, we find no clear relationship in any of the visual areas (all p >= 0.165, testing whether the slopes differed from zero at the group level using a one-sample t-test). We believe future work using other experimental manipulations should look more systematically at the relationship between task difficulty and amplitude of the attentional BOLD enhancement.

Second: Does the same ratio at different widths elicit different behavioral responses (namely accuracy and RT)? We followed the reviewer’s suggestion to compare performance between cue widths of three and nine (identical ratios, different widths; see Author response image 2 and Figure 5). We found that, using a paired t-test, behavioral accuracy differed between the two cue widths (mean accuracy of 0.73 versus 0.69, p = 0.008), with better performance for cue width three. RT did not differ significantly between the two conditions (paired t-test, p = 0.729). This could be due to the fact that participants were not incentivized to respond as quickly as possible, they merely needed to respond before the end of the response window (1.25 s) following the stimulus presentation (0.5 s). The comparisons for accuracy and RT (calculated from time of stimulus appearance) are plotted below:

Author response image 2.

In summary, with matched stimulus ratios, the wider cue was associated with worse (though not slower) performance. This could be due to the fact that more elements are involved and/or that tasks become more difficult when attending to a broader swath of space. Given these results, we believe that future studies targeting difficulty effects should use direct and independent manipulations of task difficulty and attentional width. 

(2) Eye movements: while the authors do a good job addressing the average eccentricity of fixation, I'm not sure this fully addresses concerns with eye movements, especially for the character-discrimination task which surely benefits from foveation (and requires a great deal of control to minimize saccades!). Can the authors additionally provide data on, e.g., # of fixations within the attended stimulus annulus, or fixation heatmap, or # of saccades, or some other indicator of likelihood of fixating the letter stimuli for each condition? 

We agree with the reviewer that this task is surely much easier if one foveated the stimuli, and it did indeed require control to minimize saccades to the annulus. (We appreciate the effort and motivation of our participants!) We are happy to provide additional data to address these reasonable concerns about eye movements. Below, we have visualized the number of fixations to the annulus, separated by participant and width. Though there is variability across participants, there are at most 16 instances of fixations to the annulus for a given participant, combined across all width conditions. The median number of fixations to the annulus per width is zero (shown in red). Considering the amount of time participants engaged in the task (between 8 and 12 runs of the task, each run with 100 trials), this indicates participants were generally successful at maintaining central fixation while the stimuli were presented.

Author response image 3.

We added the results of this analysis to the methods section (lines 205-208):

“Additionally, we examined the number of fixations to the white noise annulus itself. No participant had more than 16 fixations (out of 800-1200 trials) to the annulus during the task, further suggesting that participants successfully maintained fixation.”

(3) pRF sorting and smoothing: Throughout, the authors are analyzing data binned based on pRF properties with respect to the attended location ("voxels with pRFs overlapping with the white noise annulus", line 243-244) First, what does this mean? Does the pRF center need to be within the annulus? Or is there a threshold based on the pRF size? If so, how is this implemented? Additionally, considering the methods text in lines 242-247, the authors mention that they bin across 6 deg-wide bins and smooth with a moving average (18 deg), which I think will lead to further expansion of the profile of attentional enhancement (see also below) 

We provide a detailed response in the public review. Furthermore, we have clarified the voxel selection procedure in the Methods (lines 132–139 & 154–159).

(4) FWHM values: The authors interpret the larger FWHMs estimated from their model-fitting than the actual size of the attended region as a meaningful result. However, depending on details of the sorting procedure above, this may just be due to the data processing itself. One way to identify how much expansion of FWHM occurs due to analysis is by simulating data given estimates of pRF properties for a 'known' shape of modulation (e.g., square wave exactly spanning the attended aperture) and compare the resulting FWHM to that observed for attention and perception conditions (e.g., Fig. 7c). 

We provide a detailed response in the public review. The essence of our response is to refrain from interpreting the precise recovered FWHM values, which will be influenced by multiple processing steps, and instead to focus on relative differences as a function of the attentional cue width. Accordingly, we did not add simulations to the revised manuscript, although we agree with the reviewer that such simulations could shed light on the underlying spatial resolution, and how binning and smoothing influences the estimated FWHM. We have clarified our interpretation of FWHM results in the manuscript as follows:

Results lines 137-141:

“One possibility is that the BOLD-derived FWHM might tend to overestimate the retinotopic extent of the modulation, perhaps driven by binning and smoothing processing steps to create the 1D spatial profiles. If this were the case, we would expect to obtain similar FWHM estimates when modeling the perceptual modulations as well.”

Results lines 169-175:

“Mirroring the results from the attentional manipulation, FWHM estimates systematically exceeded the nominal size of the perceptually modulated region of the visual field. Comparing the estimated FWHMs of the perceptual and attentional spatial profiles (Figure 7c) revealed that the estimated widths were highly comparable (Pearson correlation r=0.664 across width conditions and visual regions). Importantly, the relative differences in FWHM show meaningful effects of both cue and contrast width in a similar manner for both attentional and perceptual forms of modulation.”

Discussion lines 16-22:

“We also found that the estimated spatial spread of the attentional modulation (as indicated by the recovered FWHM) was consistently wider than the cued region itself. We therefore compared the spread of the attention field with the spatial profile of a perceptually induced width manipulation. The results were comparable in both the attentional and perceptual versions of the task, suggesting that cueing attention to a region results in a similar 1D spatial profile to when the stimulus contrast is simply increased in that region.”

(5) Baseline parameter: looking at the 'raw' response profiles shown in Fig. 2b, it looks, at first, like the wider attentional window shows substantially lower enhancement. However, this seems to be mitigated by the shift of the curve downwards. Can the authors analyze the baseline parameter in a similar manner as their amplitude analyses throughout? This is especially interesting in contrast to the perception results (Fig. 7), for which the baseline does not seem to scale in a similar way. 

We agree with the reviewer that the baseline parameter is worth examining, and have therefore added panels displaying the baseline parameter into all results figures (Figures 4-7). There was no significant association between cue width and baseline offset in any of the three visual regions.

(6) Outlier: Fig. 5, V2, Amplitude result seems to have a substantial outlier - is there any notable difference in e.g. retinotopy in this participant? 

One participant indeed has a notably larger median amplitude estimate in V2. Below, we plot the spatial coverage from the pRF data for this participant (022), as well as all other participants.

Author response image 4.

Each subplot represents a participant's 2D histogram of included voxels for the 1D spatial profiles; the colors indicate the proportion of voxels that fell within a specific x,y coordinate bin. Note that this visualization only shows x and y estimates and does not take into account size of the pRF. While there is variation across participants in the visual field coverage, the overall similarity of the maps indicates that retinotopy is unlikely to be the explanation. 

To further explore whether this participant might be an outlier, we additionally looked at behavioral performance, angular error and FWHM parameters as well as the goodness of fit of the model. On all these criteria this participant did not appear to be an outlier. We therefore see no reason to exclude this participant from the analyses.  

(7) Fig. 4 vs Fig. 5: I understand that Fig. 4 shows results from a single participant, showing variability across blocks, while Fig. 5 shows aggregate results across participants. However, the Angular Error figure shows complementary results - Fig. 4 shows the variability of best-fit angular error, while Fig. 5 shows the average deviation (approximately the width of the error distribution). This makes sense I think, but perhaps the abs(error) for the single participant shown in Fig. 4 should be included in the caption so we can easily compare between figures. 

That's right: the Figure 4 results show the signed error, whereas the Figure 5 results show the absolute error. We agree that reporting the absolute error values for the example participant would facilitate comparison. Rather than add the values to the text, we have made the example participant’s data visually distinct within Figure 5 for easy comparison.  

(8) Bias in model fits: the analysis shown in Fig. 6 compares the estimated parameters across amounts of data used to compute attentional modulation profiles for fitting those parameters. If the model-fitting procedure were unbiased, my sense is we would likely see no impact of the number of TRs on the parameters (R^2 should improve, abs(error) should improve, but FWHM, amplitude, baseline, etc should be approximately stable, if noisier). However, instead, it looks like more/less data leads to biased estimates, such that FWHM is biased to be smaller with more noise, and amplitude is biased to be larger. This suggests (to me) that the fit is landing on a spiky function that captures a noise wiggle in the profile. I don't think this is a problem for the primary results across the whole block of 10 TRs, which is the main point of the paper. Indeed, I'm not sure what this figure is really adding, since the single-TR result isn't pursued further (see below). 

Please refer to our response in the public review, comment 4. 

(9) 'Dynamics': The paper, starting in the title, claims to get at the 'dynamics' of attention fields. At least to me, that word implies something that changes over time (rather than across trials). Maybe I'm misinterpreting the intent of the authors, but at present, I'm not sure the use of the word is justified. That said, if the authors could analyze the temporal evolution of the attention field through each block of trials at 1- or 2-TR resolution, I think that could be a neat addition to the paper and would support the claim that the study assays dynamic attention fields. 

We thank the reviewer for giving us a chance to speak more directly to the dynamic aspect of our approach. Here, we specifically use the word “dynamic” to refer to trial-to-trial dynamics.  Importantly, our temporal interval analysis suggests that we can recover information about the attentional field at a relatively fine-grained temporal resolution (a few seconds, or 2 TRs). Following this methodological proof-of-concept to dynamically track the attentional field, we are excited about future work that can more directly investigate the manner in which the attentional field evolves through time, especially in comparison to other methods that first require training on large amounts of data.

(10) Correction for multiple comparisons across ROIs: it seems that it may be necessary to correct statistical tests for multiple comparisons across each ROI (e.g., Fig. 5 regression tests). If this isn't necessary, the authors should include some justification. I'm not sure this changes any conclusions, but is worth considering. 

We appreciate the opportunity to explain our reasoning regarding multiple comparisons. We thought it appropriate not to correct as we are not comparing across regions and are not treating tests of V1, V2, and V3 as multiple opportunities to support a common hypothesis. Rather, the presence or absence of an effect in each visual region is a separate question. We would typically perform correction for multiple comparisons to control the familywise error rate when conducting a family of tests addressing a common hypothesis. We have added this to the Methods section (lines 192-195): 

“No multiple comparison correction was applied, as the different tests for each region are treated as separate questions. However, using a threshold of 0.017 for p-values would correct for comparisons across the three brain regions.”

However, we are happy to provide corrected results. If we use Bonferroni correction across ROIs (i.e. multiply p-values by three), there are some small changes from significant to only trending towards significance, but these changes don’t affect any core results. The changes that go from significant to trending are:

Associated with Figure 5 – In V3, the relationship of cue width to amplitude goes from a p-value of 0.017 to 0.051.

Associated with Figure 6 –

V1: the effect of cue width on FWHM goes from p = 0.043 to 0.128.

V2: the effect of TR on both FWHM and R2 goes from p = ~0.02 to ~0.06. 

V3: the effect of cue width on amplitude goes from p = 0.024 to 0.073.

Author response:

The following is the authors’ response to the original reviews

Public Reviews: 

Reviewer #1 (Public review):

Summary: 

Authors benchmarked 5 IBD detection methods (hmmIBD, isoRelate, hap-IBD, phasedIBD, and Refined IBD) in Plasmodium falciparum using simulated and empirical data. Plasmodium falciparum has a mutation rate similar to humans but a much higher recombination rate and lower SNP density. Thus, the authors evaluated how recombination rate and marker density affect IBD segment detection. Next, they performed parameter optimization for Plasmodium falciparum and benchmarked the robustness of downstream analyses (selection detection and Ne inference) using IBD detected by each of the methods. They also tracked the computational efficiency of these methods. The authors work is valuable for the tested species and the analyses presented appear to support their claim that users should be cautious calling IBD when SNP density is low and recombination rate is high. 

Strengths: 

The study design was solid. The authors set up their reasoning for using P. falciparum very well. The high recombination rate and similar mutation rate to humans is indeed an interesting case. Further, they chose methods that were developed explicitly for each species. This was a strength of the work, as well as incorporating both simulated and empirical data to support their goal that IBD detection should be benchmarked in P. falciparum. 

Weaknesses: 

The scope of the optimization and application of results from the work are narrow, in that everything is finetuned for Plasmodium. Some of the results were not entirely unexpected for users of any of the tested software that was developed for humans. For example, it is known that Refined IBD is not going to do well with the combination of short IBD segments and low SNP density. Lastly, it appears the authors only did one largescale simulation (there are no reported SDs). 

We thank the reviewer for highlighting the strengths and weaknesses of the study. 

First, we would like to highlight that: (1) while we use Plasmodium as a model to investigate the impact of high recombination and low marker density on IBD detection and downstream analyses, our IBD benchmarking framework and strategies are widely applicable to IBD methods development for many sexually recombining species including both Plasmodium and non-Plasmodium species. (2) Although some results are not completely unexpected, such as the impact of low marker density on IBD detection, IBD-based methods have been increasingly used in malaria genomic surveillance research without comprehensive benchmarking for malaria parasites despite the high recombination rate. Due to the lack of benchmarking, researchers use a variety of different IBD callers for malaria research including those that are only benchmarked in human genomes, such as refined-ibd. Our work not only confirmed that low marker density (related to high recombination rate) can affect the accuracy of IBD detection, but also demonstrated the importance of proper parameter optimization and tool prioritization for specific downstream analyses in malaria research. We believe our work significantly contributes to the robustness of IBD segment detection and the enhancement of IBDbased malaria genomic surveillance.

Second, we agree that there is a lack of clarity regarding simulation replicates and the uncertainty of reported estimates. We have made the following improvements, including (1) running n = 3 full sets of simulations for each analysis purpose, which is in addition to the large sample sizes and chromosomal-level replications already presented in our initial submission, and (2) updating data and figures to reflect the uncertainty at relevant levels (segment level, genome-pair level or simulation set level).   

Reviewer #2 (Public review):

Summary: 

Guo et al. benchmarked and optimized methods for detecting Identity-By-Descent (IBD) segments in Plasmodium falciparum (Pf) genomes, which are characterized by high recombination rates and low marker density. Their goal was to address the limitations of existing IBD detection tools, which were primarily developed for human genomes and do not perform well in the genomic context of highly recombinant genomes. They first analysed various existing IBD callers, such as hmmIBD, isoRelate, hap-IBD, phased-IBD, refinedIBD. They focused on the impact of recombination on the accuracy, which was calculated based on two metrics, the false negative rate and the false positive rate. The results suggest that high recombination rates significantly reduce marker density, leading to higher false negative rates for short IBD segments. This effect compromises the reliability of IBD-based downstream analyses, such as effective population size (Ne) estimation. They showed that the best tool for IBD detection in Pf is hmmIBD, because it has relatively low FN/FP error rates and is less biased for relatedness estimates. However, this method is less computationally efficient. Their suggestion is to optimize human-oriented IBD methods and use hmmIBD only for the estimation of Ne. 

Strengths: 

Although I am not an expert on Plasmodium falciparum genetics, I believe the authors have developed a valuable benchmarking framework tailored to the unique genomic characteristics of this species. Their framework enables a thorough evaluation of various IBD detection tools for non-human data, such as high recombination rates and low marker density, addressing a key gap in the field. This study provides a

comparison of multiple IBD detection methods, including probabilistic approaches (hmmIBD, isoRelate) and IBS-based methods (hap-IBD, Refined IBD, phased IBD). This comprehensive analysis offers researchers valuable guidance on the strengths and limitations of each tool, allowing them to make informed choices based on specific use cases. I think this is important beyond the study of Pf. The authors highlight how optimized IBD detection can help identify signals of positive selection, infer effective population size (Ne), and uncover population structure. They demonstrate the critical importance of tailoring analytical tools to suit the unique characteristics of a species. Moreover, the authors provide practical recommendations, such as employing hmmIBD for quality-sensitive analyses and fine-tuning parameters for tools originally designed for non-P. falciparum datasets before applying them to malaria research. 

Overall, this study represents a meaningful contribution to both computational biology and malaria genomics, with its findings and recommendations likely to have an impact on the field. 

Weaknesses: 

One weakness of the study is the lack of emphasis on the broader importance of studying Plasmodium falciparum as a critical malaria-causing organism. Malaria remains a significant global health challenge, causing hundreds of thousands of deaths annually. The authors could have introduced better the topic, even though I understand this is a methodological paper. While the study provides a thorough technical evaluation of IBD detection methods and their application to Pf, it does not adequately connect these findings to the broader implications for malaria research and control efforts. Additionally, the discussion on malaria and its global impact could have framed the study in a more accessible and compelling way, making the importance of these technical advances clearer to a broader audience, including researchers and policymakers in the fight against malaria. 

We thank the reviewer for highlighting the need to better contextualize the work and emphasize its relevance to malaria control and elimination efforts. We have edited the introduction and discussion sections to highlight the importance of studying Plasmodium as malaria-causing organisms and why IBD-based analysis is important to malaria researchers and policymakers. We believe the changes will better emphasize the public health relevance of the work and improve clarity for a general audience.  

We would like to clarify that we are not recommending that researchers “optimize human-oriented IBD methods and use hmmIBD only for the estimation of Ne.” We recommended hmmIBD for Ne analysis; however, hmmIBD can be utilized for other applications, including population structure and selection detection. Thus, we generally recommend using hmmIBD for Plasmodium when phased genotypes are available. To avoid potential misunderstandings, we have revised relevant sentences in the abstract, introduction, and discussion. One reason to consider human-oriented IBD detection methods in Plasmodium research is that hmmIBD currently has limitations in handling large genomic datasets. Our ongoing research focuses on improving hmmIBD to reduce its computational runtime, making it scalable for large Plasmodium wholegenome sequence datasets.

Recommendations for the authors: 

Reviewer #1:

(1) Additional experiments 

(i) More simulation replicates would be valuable here. The way that results are presented, it appears as though there are no replicates. Apologies if I am incorrect, but when looking through the authors code the --num_reps defaults to one simulation and there are no SDs reported for any figure. Perhaps the authors are bypass replicates by taking a random sample of lineages? Some clarification here would be great. 

We agree with the reviewer’s constructive suggestions. We have increased the number of simulation sets to (n = 3) in addition to the existing replicates at the chromosomal level. We did not use a larger n for full sets of simulation replicates for two reasons: (1) full replication is quite computationally intensive (n=3 simulation sets already require a week to run on our computer cluster with hundreds of CPU cores). (2), the results from different simulation sets are highly consistent with each other, likely due to our large sample size (n= 1000 haploid genomes for each parameter combination).  The consistency across simulation sets can be exemplified by the following figures (Author response image 1 and 2) based on simulation sets different from Figures and Supplementary Figures included in the manuscript. 

Author response image 1.

Additional simulation sets repeating experiments shown in Fig 2.

Author response image 2.

Post-optimization Ne estimates based on three independent simulation sets (Fig 5 shows data simulation set 1).

In our updated figures, we address the uncertainty of measurements as follows:

(1) For IBD accuracy based on overlapping IBD segments, we present the mean ± standard deviation (SD) at the segment level (IBD segment false positives and false negatives for each length bin) or genome-pair level (IBD error rates at the genome-wide level). Figures in the revised manuscript show results from one of the three simulation set replicates. The SD of IBD segment accuracy is included in all relevant figures. In the S2 Data file, we chose not to show SDs to avoid text overcrowding in the heatmaps; however, a detailed version, including SD plotting on the heatmap and across three simulation set replicates, is available on our GitHub repository at https://github.com/bguo068/bmibdcaller_simulations/tree/main/simulations/ext_data. 

(2) For IBD-based genetic relatedness, the uncertainty is depicted in scatterplots.

(3) For IBD-based selection signal scans, we provide the mean ± SD of the number of true selection signals and false selection signals. The SD is calculated at the simulation set level (n=3). 

(4) For IBD network community detection, the mean ± SD of the adjusted Rand index is reported at the simulation set level (n=3). A representative simulation set is randomly chosen for visualization purposes.

(5) For IBD-based Ne estimates, each simulation set provides confidence intervals via bootstrapping. We found Ne estimates across n=3 simulation sets to be highly consistent and decided to display Ne from one of the simulation sets.

(6) For the measurement of computational efficiency and memory usage, the mean ± SD was calculated across chromosomes from the same simulation sets.

We have included a paragraph titled "Replications and Uncertainty of Measures" in the methods section to clarify simulation replications. Additionally, a table of simulation replicates is provided in the new S1 Data file under the sheet named “02_simulation_replicates.”

(ii) I might also recommend a table or illustrative figure with all the simulation parameters for the readers rather than them having to go to and through a previous paper to get a sense of the tested parameters. 

We have now generated tables containing full lists of simulation/IBD calling parameters. We have organized the tables into two sections: simulation parameters and IBD calling parameters. For the simulations, we are using three demographic models: the single-population (SP) model, the multiple-population (MP) model, and the human population demography in the UK (UK) model, each with different sets of parameters. Parameters and their values are listed separately for each demographic model (SP, MP and UK). For the IBD calling, we have five different IBD callers, each with different parameters. We have provided lists of the parameters and their values separately for each caller. In total, there are 15 different combinations of 3 demographic models in simulation and five callers in IBD detection (Author response image 3). We provide a table for each of the 15 combinations. We also provide a single large table by concatenating all 15 tables. In the combined table, demographic model-specific or IBD caller-specific parameters are displayed in their own columns, with NA values (empty cells) appearing in rows where these parameters are not applied (see S2 Data file).

Author response image 3.

Schematic of combined parameters from simulations and IBD detection (also included in the S2 Data file)

(2) Recommendations for improving the writing and presentation 

Overall, the writing was great, especially the introduction. 

Three thoughts: 

(i) It would be great if the authors included a few sentences with guidance on the approach one would take if their organism was not human or P. falciparum. 

We have updated our discussion with the following statement: “Beyond Plasmodium parasites, there are many other high-recombining organisms such as Apicomplexan species like Theileria, insects like Apis mellifera (honeybee), and fungi like Saccharomyces cerevisiae (Baker's yeast). For these species, our optimized parameters may not be directly applicable, but the benchmarking framework established in this study can be utilized to prioritize and optimize IBD detection methods in a context-specific manner.”

(ii) I think there was a lot of confusion about the simulations as they were presented between the co-reviewer and I. Clarification on whether there were replicates and how sampling of lineages occurred would be helpful for a reader. 

We have added a paragraph with heading “Replications and uncertainty of measures” under the method section to clarify simulation replicates.  Please also refer to our response above for more details (Reviewer #1 (1) Additional experiments).

(iii) Maybe we missed it, but could the authors add a sentence or two about why isoRelate performed so poorly (e.g. lines 206-207) considering it was developed for Plasmodium? This result seems important. 

IsoRelate assumes non-phased genotypes as input; therefore, even if phased genotypes are provided, the HMM model used in isoRelate (distinct from the hmmIBD model) may not utilize them. Below, we present examples of IBD segments between true sets and inferred sets from both isoRelate and hmmIBD, where many small IBD segments identified by tskibd (ground truth) and hmmIBD (inferred) are not detected by isoRelate (inferred), although isoRelate still captures very long IBD segments. These patterns are also illustrated in Fig. 3 and S3 Fig. We acknowledge that isoRelate may outperform other methods in the context of unphased genotypes. However, we chose not to benchmark IBD calling methods using unphased genotypes in simulations, as the results may be significantly influenced by the quality of genotype phasing for all other IBD detection methods. The characterization of deconvolution methods is beyond the scope of this paper. We have added a paragraph in the discussion to reflect the above explanation.

Author response image 4.

Example IBD segments inferred by isoRelate and hmmIBD compared to true IBD segments calculated by tskibd.

(3) Minor corrections to the text and figures 

Lines 105-110 feel like introduction because the authors are defining IBD and goals of work 

We have shortened these sentences and retained only relevant information for transition purposes. 

Line 121-122 The definition of false positive is incorrect, it appears to be the exact text from false negative 

We apologize for the typo and have corrected the definition, so that  it is consistent with that in the methods section. 

Lines 177-180 feels more like discussion than results 

We have removed this sentence for brevity. 

Figure 1: 

Remove plot titles from the figure 

Write out number in a 

The legend in b overlaps the data so moving that inset to the right would be helpful 

We have removed the titles from Figure 1. In Figure 1a, we have changed the format of  the y-axis tick labels from scientific notation to integers.  In Figure 1b, we have adjusted the size and location of the legend so that it does not overlap with the data points.

Figure 2-3 & S4-5: 

It was hard to tell the difference between [3-4) and [10-18) because the colors and shapes are similar. It might be worth using a different color or shape for one of them? 

We have changed the color for the [10-18) group so that the two groups are easier to distinguish.

Figure 3 & S3-5: 

Biggest suggestion is that when an axis is logged it should not only be mentioned in the caption but also should be shown in the figure as well. 

We have updated all relevant figures so that the log scale is noted in the figure captions (legends) as well as in the figures (in the x and/or y axis labels).

Supplementary Figure S2 

(i) It would be nice to either combine it with the main text Figure 1 (I don't believe it would be overwhelming) or add in the other two methods for comparison 

We have now plotted data for all five IBD callers in S1 Fig for better comparison. 

(ii) the legend overlaps the data so relocating it to the top or bottom would be helpful 

We have moved the legend to the bottom of the figure to avoid overlap with the data.

Reviewer #2:

I don't have any major comments on the paper. It is well-written, although perhaps a bit long and repetitive in some sections. Make sure not to repeat the same concepts too many times. 

We have consolidated and removed several paragraphs to reduce repetition of the same concepts.

I am not a methodological developer, but it seems you have addressed several challenges regarding IBD detection in P. falciparum. You have also acknowledged the study's caveats, which I agree with. 

Thank you for the positive comments.

Minor comments: 

-In my opinion, the paper would benefit from including the workflow figure in the main text rather than keeping it in the supplementary materials. This would make it more accessible and useful for readers. 

We have moved the original S1 Fig to be Fig 1 in the main text.

-Some of the figures (e.g. Fig. 2, 4) should be larger for better clarity and interpretation. 

We have updated Fig 2 and Fig 4 (now labeled as Figure 3 and 5) to make them larger for improved clarity and interpretation.

-While the focus on P. falciparum is understandable, it would have been valuable to include examples of other species and discuss the broader implications of the findings for a broader field. 

We have updated the third-to-last paragraph to discuss implications for other species, such as Apicomplexan species like Theileria, insects like Apis mellifera (honeybee), and fungi like Saccharomyces cerevisiae (Baker's Yeast). We acknowledge that optimal parameters and tool choices may vary among species due to differences in demographic history and evolutionary parameters. However, we emphasize that the methods outlined are adaptable for prioritizing and optimizing IBD detection methods in a context-specific manner across different species.

-Figure 6 is somewhat confusing and could use clearer labeling or additional explanation to improve comprehension. 

We have updated the labels and titles in the figure to improve clarity. We also edited the figure caption for better clarity.

-Although hmmIBD outperformed other tools in accuracy, its computational inefficiency due to single-threaded execution poses a significant challenge for scaling to large datasets. The trade-off between accuracy and computational cost could be discussed in more detail. 

We have added a paragraph in the discussion section to highlight the trade-off between accuracy and computation cost. We noted that we are developing an adapted tool to enhance the hmmIBD model and significantly reduce the runtime via parallelizing the IBD inference process.

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.

Author response:

The following is the authors’ response to the original reviews

Public Review:

Reviewer #1 (Public review): 

Summary: 

Odor- and taste-sensing are mediated by two different systems, the olfactory and gustatory systems, and have different behavioral roles. In this study, Wei et al. challenge this dichotomy by showing that odors can activate gustatory receptor neurons (GRNs) in Drosophila to promote feeding responses, including the proboscis extension response (PER) that was previously thought to be driven only by taste. While previous studies suggested that odors can promote PER to appetitive tastants, Wei et al. go further to show that odors alone cause PER, this effect is mediated through sweet-sensing GRNs, and sugar receptors are required. The study also shows that odor detection by bitter-sensing GRNs suppresses PER. The authors' conclusions are supported by behavioral assays, calcium imaging, electrophysiological recordings, and genetic manipulations. The observation that both attractive and aversive odors promote PER leaves an open question as to why this effect is adaptive. Overall, the study sheds new light on chemosensation and multimodal integration by showing that odor and taste detection converge at the level of sensory neurons, a finding that is interesting and surprising while also being supported by another recent study (Dweck & Carlson, Sci Advances 2023).

Strengths: 

(1) The main finding that odors alone can promote PER by activating sweet-sensing GRNs is interesting and novel.

(2) The study uses video tracking of the proboscis to quantify PER rather than manual scoring, which is typically used in the field. The tracking method is less subjective and provides a higherresolution readout of the behavior.

(3) The study uses calcium imaging and electrophysiology to show that odors activate GRNs. These represent complementary techniques that measure activity at different parts of the GRN (axons versus dendrites, respectively) and strengthen the evidence for this conclusion. 

(4) Genetic manipulations show that odor-evoked PER is primarily driven by sugar GRNs and sugar receptors rather than olfactory neurons. This is a major finding that distinguishes this work from previous studies of odor effects on PER and feeding (e.g., Reisenman & Scott, 2019; Shiraiwa, 2008) that assumed or demonstrated that odors were acting through olfactory neurons.

We appreciate the reviewer’s positive assessment of the novelty and significance of our work.

Weaknesses/Limitations: 

(1) The authors may want to discuss why PER to odors alone has not been previously reported, especially as they argue that this is a broad effect evoked by many different odors. Previous studies testing the effect of odors on PER only observed odor enhancement of PER to sugar (Oh et al., 2021; Reisenman & Scott, 2019; Shiraiwa, 2008) and some of these studies explicitly show no effect of odor alone or odor with low sugar concentration; regardless, the authors likely would have noticed if PER to odor alone had occurred. Readers of this paper may also be aware of unpublished studies failing to observe an effect of PER on odor alone (including studies performed by this reviewer and unrelated work by other colleagues in the field), which of course the authors are not expected to directly address but may further motivate the authors to provide possible explanations.

We appreciate the reviewer’s comment. We believe that the difference in genotype is likely the largest reason behind this point. This is because the strength varied widely across genotypes and was quite weak in some strains including commonly used w[1118] empty Gal4 and w[1118] empty spit Gal4 as shown in Figure1- figure supplement 3 (Figure S3 in original submission). However, given that we observed odor-evoked PER in various genotypes (many in main Figures and three in Figure1- figure supplement 3 including Drosophila simulans), the data illustrate that it is a general phenomenon in Drosophila. Indeed, although Oh et al. (2021) did not emphasize it in the text, their Fig. 1E showed that yeast odor evoked PER at a probability of 20%, which is much higher than the rate of spontaneous PER in many genotypes. Therefore, this literature may represent another support for the presence of odor-evoked PER. We have expanded our text in the Discussion to describe these issues.

Another possibility is our use of DeepLabcut to quantitatively track the kinematics of proboscis movement, which may have facilitated the detection of PER.

(2) Many of the odor effects on behavior or neuronal responses were only observed at very high concentrations. Most effects seemed to require concentrations of at least 10-2 (0.01 v/v), which is at the high end of the concentration range used in olfactory studies (e.g., Hallem et al., 2004), and most experiments in the paper used a far higher concentration of 0.5 v/v. It is unclear whether these are concentrations that would be naturally encountered by flies.

We acknowledge that the concentrations used are on the higher side, suggesting that GRNs may need to be stimulated with relatively concentrated odors to induce PER. Although it is difficult to determine the naturalistic range of odor concentration, it is at least widely reported that olfactory neurons including olfactory receptor neurons and projection neurons do not saturate, and exhibit odor identity-dependent responses at the concentration of 10^-2 where odor-evoked PER can be observed. Furthermore, we have shown in Figure 6 that low concentration (10^-4) of banana odor, ethyl butyrate, and 4-methycyclohexanol all significantly increased the rate of odor-taste multisensory PER even in olfactory organs-removed flies, suggesting that low concentration odors can influence feeding behavior via GRNs in a natural context where odors and tastants coexist at food sites. Finally, we note that odors were further diluted by a factor of 0.375 by mixing the odor stream with the main air stream before being applied to the flies as described in Methods.

(3) The calcium imaging data showing that sugar GRNs respond to a broad set of odors contrasts with results from Dweck & Carlson (Sci Adv, 2023) who recorded sugar neurons with electrophysiology and observed responses to organic acids, but not other odors. This discrepancy is not discussed.  

As the reviewer points out, Dweck and Carlson (Sci Adv, 2023) reported using single sensillum electrophysiology (base recording) that sugar GRNs only respond to organic acids whereas we found using calcium imaging from a group of axons and single sensillum electrophysiology (tip recording) that these GRNs respond to a wide variety of odors. Given that we observed odor responses using two methods, the discrepancy is likely due to the differences in genotype examined. We now have discussed this point in the text.

(4) Related to point #1, it would be useful to see a quantification of the percent of flies or trials showing PER for the key experiments in the paper, as this is the standard metric used in most studies and would help readers compare PER in this study to other studies. This is especially important for cases where the authors are claiming that odor-evoked PER is modulated in the same way as previously shown for sugar (e.g., the effect of starvation in Figure S4).

For starved flies, we would like to remind the reviewer that the percentage of trials showing PER is reported in Fig. 1E, which shows a similar trend as the integrated PER duration. For fed flies, we have analyzed the percentage of PER and added the result to Figure 2-figure supplement 1C (Figure S4 in original submission).

(5) Given the novelty of the finding that odors activate sugar GRNs, it would be useful to show more examples of GCaMP traces (or overlaid traces for all flies/trials) in Figure 3. Only one example trace is shown, and the boxplots do not give us a sense of the reliability or time course of the response. A related issue is that the GRNs appear to be persistently activated long after the odor is removed, which does not occur with tastes. Why should that occur? Does the time course of GRN activation align with the time course of PER, and do different odors show differences in the latency of GRN activation that correspond with differences in the latency of PER (Figure S1A)?

Following the reviewer’s suggestion, we now report GCaMP responses for all the trials in all the flies (both Gr5a>GCaMP and Gr66a>GCaMP flies), where the time course and trial-to-trial/animal-toanimal variability of calcium responses can be observed (Figure 3-figure supplement 2).

Regarding the second point, we recorded responses to both sucrose and odors in some flies and found that calcium responses of GRNs are long-lasting not only to odors but also to sucrose, as shown in Author response image 1. This may be due in part to the properties of GCaMP6s and slower decay of intracellular calcium concentration as compared to spikes.

Author response image 1.

Example calcium responses to sucrose and odor (MCH) in the same fly (normalized by the respective peak responses to better illustrate the time course of responses). Sucrose (blue) and odor (orange) concentrations are 100 mM, and 10^-1 respectively. Odor stimulation begins at 5 s and lasts for 2 s. Sucrose was also applied at the same timing for the same duration although there was a limitation in controlling the precise timing and duration of tastant application. Because of this limitation, we did not quantify the off time constant of two responses.

To address whether the time course of GRN activation aligns with the time course of PER, and whether different odors evoke different latencies of GRN activation that correspond to latencies of PER, we plotted the time course of GRN responses and PER, and further compared the response latencies across odors and across two types of responses in Gr5a>GCaMP6s flies. As shown in Author response image 2, no significant differences were found in response latency between the six odors for PER and odor responses. Furthermore, Pearson correlation between GRN response latencies and PER latencies was not significant (r = 0.09, p = 0.872).

Author response image 2.

(A) PER duration in each second in Gr5a-Gal4>UAS-GCaMP6s flies. The black lines indicate the mean and the shaded areas indicate standard error of the mean. n = 25 flies. (B) Time course of calcium responses (ΔF/F) to nine odors in Gr5a GRNs. n = 5 flies. (C) Latency to the first odor-evoked PER in Gr5a-Gal4>UAS-GCaMP6s flies. Green bar indicates the odor application period. p = 0.67, one-way ANOVA. Box plots indicate the median (orange line), mean (black dot), quartiles (box), and 5-95% range (bar). Dots are outliers. (D) Latency of calcium responses (10% of rise to peak time) in Gr5a GRNs. Green bar indicates the odor application period. p = 0.32, one-way ANOVA. Box plots indicate the median (orange line), mean (black dot), quartiles (box), and 5-95% range (bar). Dots are outliers.

(6) Several controls are missing, and in some cases, experimental and control groups are not directly compared. In general, Gal4/UAS experiments should include comparisons to both the Gal4/+ and UAS/+ controls, at least in cases where control responses vary substantially, which appears to be the case for this study. These controls are often missing, e.g. the Gal4/+ controls are not shown in Figure 2C-G and the UAS/+ controls are not shown in Figure 2J-L (also, the legend for the latter panels should be revised to clarify what the "control" flies are). For the experiments in Figure S5, the data are not directly compared to any control group. For several other experiments, the control and experimental groups are plotted in separate graphs (e.g., Figure 2C-G), and they would be easier to visually compare if they were together. In addition, for each experiment, the authors should denote which comparisons are statistically significant rather than just reporting an overall p-value in the legend (e.g., Figure 2H-L).

We thank the reviewer for the input. We have conducted additional experiments for four Gal4/+controls in Figure 2 and added detailed information about control flies in the figure legend (Figure 2C-F).

For the RNAi flies shown in Figure 2 and Figure 2-figure supplement 3, we used the recommended controls suggested by the VDRC. These control flies were crossed with tubulin-Gal4 lines to include both Gal4 and UAS control backgrounds.

Regarding Figure S5 in original submission (current Figure 2-figure supplement 2), we now present the results of statistical tests which revealed that PER to certain odors is statistically significantly stronger than that to the solvent control (mineral oil) for both wing-removed and wing-leg-removed flies.

For Figure 2C-F, we now plot the results for experimental and control groups side by side in each figure.

Regarding the results of statistical tests, we have provided more information in the legend and also prepared a summary table (supplemental table). 

(7) Additional controls would be useful in supporting the conclusions. For the Kir experiments, how do we know that Kir is effective, especially in cases where odor-evoked PER was not impaired (e.g., Orco/Kir)? The authors could perform controls testing odor aversion, for example. For the Gr5a mutant, few details are provided on the nature of the control line used and whether it is in the same genetic background as the mutant. Regardless, it would be important to verify that the Gr5a mutant retains a normal sense of smell and shows normal levels of PER to stimuli other than sugar, ruling out more general deficits. Finally, as the method of using DeepLabCut tracking to quantify PER was newly developed, it is important to show the accuracy and specificity of detecting PER events compared to manual scoring.  

A previous study (Sato, 2023, Front Mol Neurosci) showed that the avoidance to 100 μM 2methylthiazoline was abolished, and the avoidance to 1 mM 2MT was partially impaired in Orco>Kir2.1 flies. However, because Orco-Gal4 does not label all the ORNs and we have more concrete results on flies in which all the olfactory organs are removed as well as specific GRNs and Gr are manipulated, we decided to remove the data for Orco>kir2.1 flies and have updated the text and Figure 2 accordingly.

For the Gr5a mutant and its control, we have added detailed information about the genotype in the figure legend and in the Methods. We have used the exact same lines as reported in Dahanukar et al. (2007) by obtaining the lines from Dr. Dahanukar. Dahanukar et al. has already carefully examined that Gr5a mutant loses responses only to certain types of sugars (e.g. it even retains normal responses to some other sugars), demonstrating that Gr5a mutants do not exhibit general deficits.

As for the PER scoring method, we manually scored PER duration and compared the results with those obtained using DeepLabCut in wild type flies for the representative data. The two results were similar (no statistical difference). We have reported the result in Figure1-figure supplement 1C.

(8) The authors' explanation of why both attractive and aversive odors promote PER (lines 249-259) did not seem convincing. The explanation discusses the different roles of smell and taste but does not address the core question of why it would be adaptive for an aversive odor, which flies naturally avoid, to promote feeding behavior.  

We have extended our explanation in the Discussion by adding the following possibility: “Enhancing PER to aversive odors might also be adaptive as animals often need to carry out the final check by tasting a trace amount of potentially dangerous substances to confirm that those should not be further consumed.”

Reviewer #2 (Public review): 

Summary: 

A gustatory receptor and neuron enhances an olfactory behavioral response, proboscis extension. This manuscript clearly establishes a novel mechanism by which a gustatory receptor and neuron evokes an olfactory-driven behavioral response. The study expands recent observations by Dweck and Carlson (2023) that suggest new and remarkable properties among GRNs in Drosophila. Here, the authors articulate a clear instance of a novel neural and behavioral mechanism for gustatory receptors in an olfactory response.

Strengths: 

The systematic and logical use of genetic manipulation, imaging and physiology, and behavioral analysis makes a clear case that gustatory neurons are bona fide olfactory neurons with respect to proboscis extension behavior.

Weaknesses: 

No weaknesses were identified by this reviewer.  

We appreciate the reviewer’s recognition of the novelty and significance of our work.

Reviewer #3 (Public review): 

Summary: 

Using flies, Kazama et al. combined behavioral analysis, electrophysiological recordings, and calcium imaging experiments to elucidate how odors activate gustatory receptor neurons (GRNs) and elicit a proboscis extension response, which is interpreted as a feeding response. 

The authors used DeepLabCut v2.0 to estimate the extension of the proboscis, which represents an unbiased and more precise method for describing this behavior compared to manual scoring.

They demonstrated that the probability of eliciting a proboscis extension increases with higher odor concentrations. The most robust response occurs at a 0.5 v/v concentration, which, despite being diluted in the air stream, remains a relatively high concentration. Although the probability of response is not particularly high it is higher than control stimuli. Notably, flies respond with a proboscis extension to both odors that are considered positive and those regarded as negative.

The authors used various transgenic lines to show that the response is mediated by GRNs.

Specifically, inhibiting Gr5a reduces the response, while inhibiting Gr66a increases it in fed flies. Additionally, they find that odors induce a strong positive response in both types of GRNs, which is abolished when the labella of the proboscis are covered. This response was also confirmed through electrophysiological tip recordings.

Finally, the authors demonstrated that the response increases when two stimuli of different modalities, such as sucrose and odors, are presented together, suggesting clear multimodal integration.

Strengths: 

The integration of various techniques, that collectively support the robustness of the results.

The assessment of electrophysiological recordings in intact animals, preserving natural physiological conditions.

We appreciate the reviewer’s recognition of the novelty and significance of our work.

Weaknesses: 

The behavioral response is observed in only a small proportion of animals.  

We acknowledge that the probability of odor-evoked PER is lower compared to sucrose-evoked PER, which is close to 100 % depending on the concentration. To further quantify which proportion of animals exhibit odor-evoked PER, we now report this number besides the probability of PER for each odor shown in Fig. 1E. We found that, in wild type Dickinson flies, 73% and 68 % of flies exhibited PER to at least one odor presented at the concentration of 0.5 and 0.1.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

Minor comments/suggestions: 

- Define "MO" in Figure 1D.  

We have defined it as mineral oil in the figure legend.

- Clarify how peak response was calculated for GCaMP traces (is it just the single highest frame per trial?).

We extended the description in the Methods as follows: “The peak stimulus response was quantified by averaging ΔF/F across five frames at the peak, followed by averaging across three trials for each stimulus. Odor stimulation began at frame 11, and the frames used for peak quantification were 12 to 16.” We made sure that information about the image acquisition frame rate was provided earlier in the text.

- Clarify how the labellum was covered in Figure 3 and show that this does not affect the fly's ability to do PER (e.g., test PER to sugar stimulation on tarsus) - otherwise one might think that gluing the labella could affect PER.

In Figure 3, only calcium responses were recorded, and PER was not recorded simultaneously from the same flies. To ensure stable recording from GRN axons in the SEZ, we kept the fly’s proboscis in an extended position as gently as possible using a strip of parafilm. In some of the imaging experiments, we covered the labellum with UV curable glue, whose purpose was not to fix the labellum in an extended position but to prevent the odors from interacting with GRNs on the labellum. We have added a text in the Methods to explain how we covered the labellum.

- Clarify how the coefficients for the linear equation were chosen in Figure 3G.  

We used linear regression (implemented in Python using scikit-learn) to model the relationship between neural activity and behavior, aiming to predict the PER duration based on the calcium responses of two GRN types, Gr5a and Gr66a. The coefficients were estimated using the LinearRegression function. We added this description to the Methods. 

- Typo in "L-type", Figure 4A.  

We appreciate the reviewer for pointing out this error and have corrected it.

- Clarify over what time period ephys recordings were averaged to obtain average responses.

We have modified the description in the Methods as follows: “The average firing rate was quantified by using the spikes generated between 200 and 700 ms after the stimulus contact following the convention to avoid the contamination of motion artifact (Dahanukar and Benton, 2023; Delventhal et al., 2014; Hiroi et al., 2002).

- The data and statistics indicate that MCH does not enhance feeding in Figure 6G, so the text in lines 207-208 is not accurate.

We have modified the text as follows: “A similar result was observed with ethyl butyrate, and a slight, although not significant, increase was also observed with 4-methylcyclohexanol (Figure 6G).”

- P-value for Figure S9 correlation is not reported.  

We appreciate the reviewer for pointing this out. The p-value is 0.00044, and we have added it to the figure legend (current Figure 5-figure supplement 1).

Reviewer #2 (Recommendations for the authors): 

Honestly, I have no recommendations for improvement. The manuscript is extremely well-written and logical. The experiments are persuasive. A lapidary piece of work.

We appreciate the reviewer for the positive assessment of our work.

Reviewer #3 (Recommendations for the authors): 

- I suggest explaining the rationale for selecting a 4-second interval, beginning 1 second after the onset of stimulation.

Integrated PER duration was defined as the sum of PER duration over 4 s starting 1 s after the odor onset. This definition was set based on the following data.

(1) We used a photoionization detector (PID) to measure the actual time that the odor reaches the position of a tethered fly, which was approximately 1.1 seconds after the odor valve was opened. Therefore, we began analyzing PER responses 1 second after the odor onset (valve opening) to align with the actual timing of stimulation.

(2) As shown in Fig.1D and 1F, the majority of PER occurred within 4 s after the odor arrival.

We have now added the above rationale in the Methods.

- I could not find the statistical analysis for Figures 1E and 1G. If these figures are descriptive, I suggest the authors revise the sentences: 'Unexpectedly, we found that the odors alone evoked repetitive PER without an application of a tastant (Figures 1D-1G, and Movie S1). Different odors evoked PER with different probability (Figure 1E), latency (Figure S1A), and duration (Figures 1F, 1G, and S2)'.

We have added the results of statistical analysis to the figure legend.

- In Figure 2, the authors performed a Scheirer-Ray-Hare test, which, to my knowledge, is a nonparametric test for comparing responses across more than two groups with two factors. If this is the case, please provide the p-values for both factors and their interaction

We now show the p-values for both factors, odor and group as well as their interaction in the supplementary table. 

- In line 83, I suggest the authors avoid claiming that 'these data show the olfactory system modulates but is not required for odor-evoked PER,' as they are inhibiting most, but not all olfactory receptor neurons. In this regard, is it possible to measure the olfactory response to odors in these flies?  

We thank the reviewer for the comment. Because Orco-Gal4 does not label all the ORNs and because we have more concrete results on flies in which all the olfactory organs are removed as well as specific GRNs and Gr are manipulated, we decided to remove the data for Orco>kir2.1 flies and have updated the text and Figure 2 accordingly.

- In Figure 2, I wonder if there are differences in the contribution of various receptors in detecting different odors. A more detailed statistical analysis might help address this question.

Although it might be possible to infer the contribution of different gustatory receptors by constructing a quantitative model to predict PER, it is a bit tricky because the activity of individual GRNs and not Grs are manipulated in Figure 2 except for Gr5a. The idea could be tested in the future by more systematically manipulating many Grs that are encoded in the fly genome.

- For Figures 2J-L, please clarify which group serves as the control.  

We have added this information to the legend. 

- In Figure 3, I recommend including an air control in panels D and F to better appreciate the magnitude of the response under these conditions.

The responses to all three controls, air, mineral oil and water, were almost zero. As the other reviewer suggested to present trial-to-trial variability as well, we now show responses to all the controls in all the trials in all the animals tested in Figure 3-figure supplement 2.

- I had difficulty understanding Figure 3G. Could the authors provide a more detailed explanation of the model?

We used linear regression (implemented in Python using scikit-learn) to model the relationship between neural activity and behavior, aiming to predict the PER duration based on the calcium responses of two GRN types, Gr5a and Gr66a. The weights for GRNs were estimated using the LinearRegression function. The weight for Gr5a and Gr66a was positive and negative, respectively, indicating that Gr5a contributes to enhance whereas Gr66a contributes to reduce PER.

To evaluate the model performance, we calculated the coefficient of determination (R²), which was 0.81, meaning the model explained 81% of the variance in the PER data.

The scatter plot in Fig. 3G shows a tight relationship between the predicted PER duration (y-axis) plotted against the actual PER duration (x-axis), demonstrating a strong predictive power of the model.

We added the details to the Methods.

- In Figure S4a, the reported p-value is 0.88, which seems to be a typo, as the text indicates that PER is enhanced in a starved state.

Thank you for pointing this out. We have modified the figure legend to describe that PER was enhanced in a starved state only for the experiments conducted with odors at 10^-1 concentration (current Figure 2-figure supplement 1).

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors attempted to dissect the function of a long non-coding RNA, lnc-FANCI-2, in cervical cancer. They profiled lnc-FANCI-2 in different cell lines and tissues, generated knockout cell lines, and characterized the gene using multiple assays.

Strengths:

A large body of experimental data has been presented and can serve as a useful resource for the scientific community, including transcriptomics and proteomics datasets. The reported results also span different parts of the regulatory network and open up multiple avenues for future research.

Thanks for your positive comments on the strengths.

Weaknesses:

The write-up is somewhat unfocused and lacks deep mechanistic insights in some places.

As the lnc-FANCI-2 as a novel lncRNA had never been explored for any functional study, our report found that it regulates RAS signaling. Thus, this report focuses on lnc-FANCI-2 and RAS signaling pathway but also includes some important screening data, which are important for our readers to understand how we could reach the RAS signaling.

Reviewer #2 (Public review):

The study by Liu et al provides a functional analysis of lnc-FANCI-2 in cervical carcinogenesis, building on their previous discovery of FANCI-2 being upregulated in cervical cancer by HPV E7.

The authors conducted a comprehensive investigation by knocking out (KO) FANCI-2 in CaSki cells and assessing viral gene expression, cellular morphology, altered protein expression and secretion, altered RNA expression through RNA sequencing (verification of which by RT-PCR is well appreciated), protein binding, etc. Verification experiments by RT-PCR, Western blot, etc are notable strengths of the study.

The KO and KD were related to increased Ras signaling and EMT and reduced IFN-y/a responses.

Thanks for your positive comments. It did take us a few years to reach this scientific point for understanding of lnc-FANCI-2 function.

Although the large amount of data is well acknowledged, it is a limitation that most data come from CaSki cells, in which FANCI-2 localization is different from SiHa cells and cancer tissues (Figure 1). The cytoplasmic versus nuclear localization is somewhat puzzling.

Regarding lnc-FANCI-2 localization, it could be both cytoplasmic and nuclear in cervical cancer tissues, HPV16 or HPV18 infected keratinocytes, and HPV16+ cervical cancer cell line CaSki cells which contain multiple integrated HPV16 DNA copies. But surprisingly, it is most detectable in the nucleus in HPV16+ SiHa cells which contain only one copy of integrated HPV16 DNA (Yu, L., et al. mBio 15: e00729-24, 2024). No matter what, knockdown of lnc-FANCI-2 expression from SiHa cells induces RAS signaling leading to an increase in the expression of p-AKT and p-Erk1/2 (suppl. Fig. S6B).

Reviewer #3 (Public review):

Summary:

A long noncoding RNA, lnc-FANCI-2, was reported to be regulated by HPV E7 oncoprotein and a cell transcription factor, YY1 by this group. The current study focuses on the function of lnc-FANCI-2 in HPV-16 positive cervical cancer is to intrinsically regulate RAS signaling, thereby facilitating our further understanding of additional cellular alterations during HPV oncogenesis. The authors used advanced technical approaches such as KO, transcriptome and (IRPCRP) and LC- MS/MS analyses in the current study and concluded that KO Inc-FANCI-2 significantly increases RAS signaling, especially phosphorylation of Akt and Erk1/2.

Strengths:

(1) HPV E6E7 are required for full immortalization and maintenance of the malignant phenotype of cervical cancer, but they are NOT sufficient for full transformation and tumorigenesis. This study helps further understanding of other cellular alterations in HPV oncogenesis.

(2) lnc-FANCI-2 is upregulated in cervical lesion progression from CIN1, CIN2-3 to cervical cancer, cancer cell lines, and HPV transduced cell lines.

(3) Viral E7 of high-risk HPVs and host transcription factor YY1 are two major factors promoting lnc-FANCI-2 expression.

(4) Proteomic profiling of cytosolic and secreted proteins showed inhibition of MCAM, PODXL2, and ECM1 and increased levels of ADAM8 and TIMP2 in KO cells.

(5) RNA-seq analyses revealed that KO cells exhibited significantly increased RAS signaling but decreased IFN pathways.

(6) Increased phosphorylated Akt and Erk1/2, IGFBP3, MCAM, VIM, and CCND2 (cyclin D2) and decreased RAC3 were observed in KO cells.

Thanks for your positive comments. It has taken us almost nine years to reach this point to gradually understand lnc-FANCI-2 functions, which are more complex than our initial thoughts.  

Weaknesses:

(1) The authors observed the increased Inc-FANCI-2 in HPV 16 and 18 transduced cells, and other cervical cancer tissues as well, HPV-18 positive HeLa cells exhibited different expressions of Inc-FANCI-2.

Both HPV16 and HPV18 infections induce lnc-FANCI-2 expression in keratinocytes (Liu H., et al. PNAS, 2021). However, HPV18+ cervical cancer cell lines HeLa and C4II cells (Figure S1A and S1B) do not express lnc-FANCI-2 as we see in HPV-negative cell lines such as HCT116, HEK293, HaCaT, and BCBL1 cells. Although we don’t know why, our preliminary data show that the lnc-FANCI-2 promoter functions well and is sensitive to YY1 binding in lnc-FANCI-2 expressing CaSki and C33A cells in our dual luciferase assays but is much less sensitive to YY1 binding in HeLa and HCT116 cells, indicating some unknown cellular factors negatively regulating lnc-FANCI-2 promoter activity.

Author response image 1.

A firefly luciferase (FLuc) reporter containing either the wild-type (−600 wt) or YY1-binding-site-mutated lnc-FANCI-2 promoter was evaluated in CaSki, HeLa, C33A, and HCT116 cells for its promoter activity, with Renilla luciferase (RLuc) activity driven by a TK promoter serving as an internal control. The two YY1-binding motifs (A and B) with a X for mutation are illustrated in the right diagram.

(2) Previous studies and data in the current showed a steadily increased Inc-FANCI-2 during cancer progression, however, the authors did not observe significant changes in cell behaviors (both morphology and proliferation) in KO Inc-FANCI-2.

Thanks. We do see decreases in cell proliferation, colony formation, and cell migration, accompanied by increased cell senescence, from the lnc-FANCI-2 KO cells to the parent WT cells.  These data are now added to the revised Fig. 1 and the revised supplemental Fig. S3.

(3) The authors observed the significant changes of RAS signaling (downstream) in KO cells, but they provided limited interpretations of how these results contributed to full transformation or tumorigenesis in HPV-positive cancer.

As we stated in the title of this function of lnc-FANCI-2, the lnc-FANCI-2 intrinsically restricts RAS signaling and phosphorylation of Akt and Erk in HPV16-infected cervical cancer. Presumably, high RAS-AKT-ERK signaling inhibits tumor cell survival due to senescence induction as we show in our new Figure 1 and supplemental Fig. S3. A similar report was found in a lung cancer study (Patricia Nieto, et al. Nature 548: 239-243, 2017).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major comments:

(1) A major issue is that parts of the manuscript read like a collection of experimental results. However, some of the results do not contribute directly to the central story. Besides confusing the reader, the large amount of apparently disparate results can raise more questions. For example:

a) Why is lnc-FANCI-2 highly expressed in HPV16-infected cervical cancer cell lines (but not in HPV18-infected cells)?

b) How do p53 and RB repress the expression of lnc-FANCI-2?

c) What regulates the sub-cellular localization of lnc-FANCI-2?

d) How does lnc-FANCI-2 negatively regulate RAS signalling?

e) How does MAP4K4 bind to lnc-FANCI-2?

f) Do lnc-FANCI-2 and MAP4K4 require each other to regulate RAS signalling?

g) How does RAS signalling regulate the transcription of MCAM and IGFBP3?

h) How does MCAM feedback on RAS? Do the different MCAM isoforms impact on RAS signalling differently?

i) How does IGFBP3 feedback on ERK but not AKT?

j) How do the other mentioned proteins like ADAM8 fit into the regulatory network?

k) Each question will require a lot more work to address. I think it would be good if the authors could think through carefully what the key message(s) in the current manuscript should be and then present a more focused write-up.

Thanks for the critical comments. Because this study is the first time to explore lnc-FANCI-2 functions, we would like to be collective. We believe these data are important to guide any future studies. We really appreciate our reviewer listing many questions related to HPV infection, cell biology, RAS signaling, cancer biology from questions a to k. To address each question in a satisfactory way will be a separate study, but fortunately, our report has pointed out such a direction with some preliminary data for future studies. Here below are our responses to each question from a to k:

a) Both HPV16 and HPV18 infection induce lnc-FANCI-2 expression in keratinocytes (Liu H., et al. PNAS, 2021). However, HPV18+ cervical cancer cell lines HeLa and C4II cells (Figure S1A and S1B) do not express lnc-FANCI-2 as we see in HPV-negative cell lines such as HCT116, HEK293, HaCaT, and BCBL1 cells. Although we don’t know why, our preliminary data show that lnc-FANCI-2 promoter functions well and is sensitive to YY1 binding in lnc-FANCI-2 expressing CaSki and C33A cells but is much less sensitive to YY1 in HeLa and HCT116 cells, indicating some unknown cellular factors negatively regulating lnc-FANCI-2 promoter activity.

b) We don’t know whether p53 and pRB could repress the expression of lnc-FANCI-2 although C33A cells bearing a mutant p53 and mutant pRB express high amount of lnc-FANCI-2. However, KD of E2F1 had no effect on lnc-FANCI-2 promoter activity in CaSki cells (Liu, H., et al. PNAS, 2021).

c) RNA cellular localization can be affected by many factors, including splicing, export, and polyadenylation. As lnc-FANCI-2 is a long non-coding RNA, its regulation of cellular location could be more complicated than mRNAs and thus could be a future research direction.  

d) The conclusion that lnc-FANCI-2 negatively regulates RAS signaling is based on both lnc-FANCI-2 KO and KD studies.  Please see the proposed hypothetic model in Figure 8E.

e) The MAP4K4 binding to lnc-FANCI-2 was demonstrated by our IRPCRP-Mass spectrometry (Fig. 8A and 8C), although the exact binding site on lnc-FANCI-2 was not explored. As you probably know, many enzymes today turn out an RNA-binding enzyme (Castello A., et al. Trends Endocrinol. Metab. 26: 746-757, 2015; Hentze MW., et al. Nat. Rev. Mol. Cell Biol. 19: 327-341, 2018)    

f) Yes, they are slightly relied on each other in regulating RAS signaling. We found that KD of MAP4K4 in parent CaSki cells (Figure 8D) led to more effect on RAS signaling (MCAM, IGFBP3, p-Akt) than that in lnc-FANCI-2 KO ΔPr-A9 cells. In contrast, the latter displayed more p-Erk1/2 than that induced by KD of lnc-FANCI-2 in the parental CaSki cells (Figure S7C).

g) We believe RAS signaling regulates most likely the transcription of MCAM and IGFBP3 through phosphorylated transcription factors (Figure 8E diagram).

h) As a signal molecule with at least 13 ligands/coreceptors (Joshkon A., et al. Biomedicines 8: 633, 2020), the increased MCAM appears to sustain RAS signaling (Fig. 7J and Fig. 8E). We are assuming the full-length cytoplasmic MCAM plays a predominant role in RAS signaling due to its abundance than the cleaved nuclear MCAM missing both transmembrane and cytoplasmic regions. Plus, RAS signaling mainly occurs in the cytosol.  

i) Exact mechanism remains unknown. Lnc-FANCI-2 KO cells exhibit high expression levels of IGFBP3 RNA and protein and p-Erk1/2, but not so much for p-Akt, possibly due to IGFBP3 regulation of MAPK for Erk phosphorylation, but not much so on PI3K for Akt phosphorylation.

j) The dysregulation of RAS signaling and ADAM protein activity is implicated in various cancers. ADAM proteins can modulate RAS signaling by cleaving and releasing ligands that activate or inactivate RAS-related pathways (Schafer B., et al. JBC 279: 47929-38, 2004; Ohtsu H., et al. Am J Physiol Cell Physiol 291: C1-C10, 2006; Dang M, et al. JBC 286: 17704-17713, 2011; Kleino I, et al. PLoS One 10: e0121301, 2015). Some ADAM proteins are Involved in the migration and invasion of cancer cells, and its loss can promote the degradation of KRAS (Huang Y-K., et al. Nat Cancer 5: 400-419, 2024). In this revision, we have a brief discussion on ADAMs and RAS signaling.

k) We agree with our reviewer that each question will require a lot more work to address. As this study is to explore the lnc-FANCI-2 function for the first time, however, we prefer to include all of these data that have been selectively included in this write-up. We hope reviewer 1 will be satisfied with our response to each question from a to j. 

(2) Figures S1A & S1C - Replicates are needed.

Yes, we have repeated all of the experiments. The quantification shown in Figure S1A and S1C was performed in triplicate, and error bars have been added to the updated figure.

3) Figure S1D - There seems to be some lnc-FANCI-2 RNA in the nucleus of CaSki cells as well. Please quantify the relative amount of lnc-FANCI-2 in the nucleus vs cytoplasm.

Yes, a small fraction of lnc-FANCI-2 is in the nucleus of CaSki cells as we reported (Liu H., PNAS, 2021, Movies S1 and S2). We did quantify by fractionation and RT-qPCR the relative amount of lnc-FANCI-2 in the nucleus vs cytoplasm in Figure S1C. 

(4) Figure S2B - (a) For ΔPr-A9 cells, it looks like there is an increase in E6 and a decrease in E7, instead of "little change" as the authors claimed. (b) I suggest checking the protein levels for all the control and KO clones.

Thanks for the questions. We had some variation in E6 and E7 detection and the submitted one was one representative.  We grew again the lnc-FANCI-2 KO clones A9 and B3 and reexamined the expression of HPV16 E6/E7 proteins and their downstream targets, p53 and E2F1. As shown in new Figure S3A expt II, we saw again some variations in the detections (~20-30%) and these variations do not reflect a noticeable change for their downstream targets. Thus, we do not consider these changes significantly enough to draw a conclusion in our study, but rather most likely from sampling in the assays.

(5) In the Proteome Profiler Human sReceptor Array analysis, multiple proteins were highlighted as having at least 30% change. But it is unclear how they relate to RAS signaling.

Thanks for this comment.  Cellular soluble receptors are essential for RAS signaling, EMT pathway and IFN responses. For example, the dysregulation of RAS signaling and ADAM protein activity is implicated in various cancers. ADAM proteins can modulate RAS signaling by cleaving and releasing ligands that activate or inactivate RAS-related pathways (Schafer B., et al. JBC 279: 47929-38, 2004; Ohtsu H., et al. Am J Physiol Cell Physiol 291: C1-C10, 2006; Dang M, et al. JBC 286: 17704-17713, 2011; Kleino I, et al. PLoS One 10: e0121301, 2015). Some ADAM proteins are Involved in the migration and invasion of cancer cells, and its loss can promote the degradation of KRAS (Huang Y-K., et al. Nat Cancer 5: 400-419, 2024). In this revision, we have a brief discussion on ADAMs and RAS signaling.

(6) Does knockdown of MAP4K4 lead to an increase in MCAM and IGFBP3?

Yes, the MAP4K4 KD from parental WT CaSki cells does lead an increase in MCAM (~70%) and IGFBP3 (~30%) which is like the knockdown of lnc-FANCI-2 shown in the revised Figure 8D.

Minor comments:

(7) In the opinion of this reviewer the title is somewhat unwieldy.

Thanks. We have shortened the title as “The lnc-FANCI-2 intrinsically restricts RAS signaling in HPV16-infected cervical cancer”

(8) The abstract can be more focused and doesn't have to mention so many gene names. In fact, the significance paragraph works better as an abstract. For the significance, the authors can provide another write-up on the implications of their research instead.

Thanks. We have revised the abstract and added the implications of this research.

(9) The last sentence of the introduction feels a little abrupt. It would be good to elaborate a little more on the key findings.

Thanks for this critical comment. We have revised as in the following: In this report, we demonstrate that lnc-FANCI-2 in HPV16-infected cells controls RAS signaling by interaction with MAP4K4 and other RNA-binding proteins. Ablation of lnc-FANCI-2 in the cells promotes RAS signaling and phosphorylation of Akt and Erk. High levels of lnc-FANCI-2 and low level of MCAM expression in cervical cancer patients correlate with improved survival, indicating that lnc-FANCI-2 plays a critical role in regulating RAS signaling to affect cervical cancer progression and patient outcomes.

(10) Typo on line 191: Should be ADAM8 and not ADMA8.

Corrected.

Reviewer #2 (Recommendations for the authors):

The paper contains a vast amount of data and would greatly benefit from an expanded version of the schematic of Figure 8E summarizing the main results. Including additional details on FANCI-2 regulation by HPV (primarily from previous studies) and its implications for HPV16-driven carcinogenesis would provide a more comprehensive overview.

Thanks for the suggestion. We have modified our Figure 8E to include HR-HPV E7 and YY1 in regulation of lnc-FANCI-2 transcription.

Further specific comments:

(1) The introduction may be shortened to increase readability (e.g. lines 77-90; 94-105).

We have shortened the introduction by deletion of the lines 94-105 from our initial submission.

(2) Lines 55-57 the number of cervical cancer diagnoses and mortality need to be updated to the latest literature. The reference is from 2012.

Thanks. We have revised and updated accordingly with a new citation (Bray F., et al: Global cancer statistics 2022: GLOBOCAN estimates of incidence and mortality worldwide for 36 cancers in 185 countries. CA Cancer J Clin 74, 229-263 (2024))

(3) Line 61: Progression rate of CIN3 is incorrect (31% in 30 years according to reference 5).

Thanks. Corrected.

(4) Lines 108-112 are difficult to understand and should be rewritten.

Thanks. Revised accordingly.

(5) Line 116 Is this correct or should 'but' be 'and'?

Thanks. Corrected accordingly.

(6) Figure 1A top: The difference between cervical cancer and normal areas is hard to see in the top figure. The region labeled as "normal" does not resemble typical differentiating epithelium or normal glandular epithelium, though this is difficult to assess accurately from the image provided. I suggest adding HE staining and also the histotypes.

We have added an H&E staining panel in the corresponding region to Figure 1A, which clearly shows the normal and cancer regions. Both cervical cancer tissues were cervical squamous cell carcinoma.

(7) HFK-HPV16 & 18 cells (Figure 1B) are not described in the Materials & Methods.

Thanks. We revised our Materials and Methods by citing our two previous publications.

(8) Figure 2E (RNA scope on FANCI-2 KO) only shows 2 to 3 cells, which makes it somewhat difficult to assess downregulated expression in the KO. I suggest replacing these with pictures showing more cells (i.e. >10) to strengthen the results.

We have replaced the image in Figure 2E to include more cells.

(9) The spindle-like morphology in deltaPr-A9 cells shown in FigS2A is not very distinct. Including images at higher magnification could help clarify this feature.

Good comment. We have enlarged the images for better view and revised the context.

(10) Both protein and RNA expression analysis have been performed on WT CaSki cells and FANCI-2 KO cells. If I am correct there is little overlap between the significantly changed gene products. What does this mean? Have you looked into the comparison?

The DEGs identified from RNA-seq indicated a genome wide transcriptome change, while the protein array we used only covered 105 soluble protein receptors. However, we did find 9/15 (60%) membrane proteins in cell lysates (PODXL2, ECM1, NECTIN2, MCAM, ADAM9, CDH5, ADAM10, ITGA5, NOTCH1, SCARF2, ADAM8, TIMP2, LGALS3BP, CDH13, and ITGB6) exhibited consistent changes in expression (underlined) by both RNA-seq and protein array assays. We have revised the text with this information (page 11). Other six proteins (40%) had inconsistent expression correlation in two assays could be due to post-translational mechanisms, such as protein stability, modifications and secretion, etc.  

(11) Figure S7, which represents TCGA data and survival is quite complex. It would be more effective to display a similar figure for FANCI-2, as was done for MCAM in Figure 7I, to simplify the comparison and enhance clarity.

Thanks. However, the suggested figure for lnc-FANCI-2 was published in PNAS paper already (Liu H., et al. PNAS, 2021).  The Figure S8 in this revision is the result from our in-house GradientScanSurv pipeline, a new way to correlate the expression and survival more accurately.

What do the Figures look like if you analyse only HPV16+ patients versus HPV18+ patients, considering that FANCI-2 upregulation in cell lines is related to HPV16 and not 18? Is there an effect of histotype? Or tumor stage?

HPV18 infected keratinocytes express high level of lnc-FANCI-2. Two HPV18⁺ HeLa and C4II cell lines and HPV-negative cell lines, such as HCT116 cells, which do not express lnc-FANCI-2 could be due to the presence of some unknow repressive factors. We found that lnc-FANCI-2 promoter functions well in responding to YY1 binding in CaSki and C33A cells expressing lnc-FANCI-2 but does not so in HeLa and HCT116 cells in our dual luciferase assays. 

(12) It remains puzzling that FANCI-2 upregulation was previously shown to already occur in CIN lesions and increase further in cervical cancer, while the current data indicate that FANCI-2 suppresses AKT activation. If I am correct Akt activation has been linked to cervical carcinogenesis. Similarly, line 434 states that increased MCAM might promote cervical tumorigenesis, implying that low FANCI-2 would stimulate tumorigenesis. If I understand correctly, the increase in FANCI-2 observed in CIN lesions would reflect a "brake" on the carcinogenic pathway and its sustained increase in cancer might indicate that growth is still (partly) controlled. As mentioned earlier, a Figure illustrating the relation between FANCI-2, HPV, and the carcinogenic process would be beneficial for clarity.

Yes. Increased MCAM, but low level of lnc-FANCI-2, correlates with poor cervical cancer survival. We have revised Figure 8E to illustrate this relation better.  

(13) May part of the potentially conflicting findings be explained by CaSki cells being of metastatic origin? Related to this, does the expression of FANCI-2 or MALM depend on the tumor stage?

Thanks for this important suggestion. Unfortunately, we found that the expression of lnc-FANCI-2 and MCAM is not associated with cervical cancer stage based on the TCGA data (http://gepia.cancer-pku.cn/index.html). See the data below:

Author response image 2.

Despite some lingering uncertainty, the extensive experiments conducted using KO and KD cells do provide compelling evidence that lnc-FANCI-2 function is linked to RAS signaling and EMT.

Thanks for your positive review and instructive comments.

Reviewer #3 (Recommendations for the authors):

(1) The authors observed the increased Inc-FANCI-2 in HPV 16 and 18 transduced cells, and other cervical cancer tissues as well, HPV-18 positive HeLa cells exhibited different expressions of Inc-FANCI-2. I suggest authors provide more discussions on this difference, for example, HPV genotypes. HPV genome status in host cells? Cell types?

Thanks. We found the keratinocyte infections with HPV16, HPV18, and other HR-HPVs could induce lnc-FANCI-2 expression (Liu H., et al. PNAS, 2021). In this report, we found HPV18⁺ HeLa and C4II cells and other HPV-negative cell lines do not. Our preliminary data on lnc-FANCI-2 promoter activity assays showed the presence of a negative regulatory factor (s) in non-lnc-FANCI-2 expressing cells. See the data in Author response image 1.

We have revised our discussion by inclusion these sets of the luciferase data as data not shown.

(2) I suggest the authors discuss more details on how the changes of RAS signaling in KO cells help our further understanding of the molecular mechanisms for HPV-associated full-cell transformation and malignancy in addition to the well-known functions of HPV E6 and E7.

Thanks. We have modified the Figure 8E as suggested by reviewer 2 and revised the discussion further.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

Detecting unexpected epistatic interactions among multiple mutations requires a robust null expectation - or neutral function - that predicts the combined effects of multiple mutations on phenotype, based on the effects of individual mutations. This study assessed the validity of the product neutrality function, where the fitness of double mutants is represented as the multiplicative combination of the fitness of single mutants, in the absence of epistatic interactions. The authors utilized a comprehensive dataset on fitness, specifically measuring yeast colony size, to analyze epistatic interactions.

The study confirmed that the product function outperformed other neutral functions in predicting the fitness of double mutants, showing no bias between negative and positive epistatic interactions. Additionally, in the theoretical portion of the study, the authors applied a wellestablished theoretical model of bacterial cell growth to simulate the growth rates of both single and double mutants under various parameters. The simulations further demonstrated that the product function was superior to other functions in predicting the fitness of hypothetical double mutants. Based on these findings, the authors concluded that the product function is a robust tool for analyzing epistatic interactions in growth fitness and effectively reflects how growth rates depend on the combination of multiple biochemical pathways.

Strengths:

By leveraging a previously published extensive dataset of yeast colony sizes for single- and double-knockout mutants, this study validated the relevance of the product function, commonly used in genetics to analyze epistatic interactions. The finding that the product function provides a more reliable prediction of double-mutant fitness compared to other neutral functions offers significant value for researchers studying epistatic interactions, particularly those using the same dataset.

Notably, this dataset has previously been employed in studies investigating epistatic interactions using the product neutrality function. The current study's findings affirm the validity of the product function, potentially enhancing confidence in the conclusions drawn from those earlier studies. Consequently, both researchers utilizing this dataset and readers of previous research will benefit from the confirmation provided by this study's results.

Weaknesses:

This study exhibits several significant logical flaws, primarily arising from the following issues: a failure to differentiate between distinct phenotypes, instead treating them as identical; an oversight of the substantial differences in the mechanisms regulating cell growth between prokaryotes and eukaryotes; and the adoption of an overly specific and unrealistic set of assumptions in the mutation model. Additionally, the study fails to clearly address its stated objective-investigating the mechanistic origin of the multiplicative model. Although it discusses conditions under which deviations occur, it falls short of achieving its primary goal. Moreover, the paper includes misleading descriptions and unsubstantiated reasoning, presented without proper citations, as if they were widely accepted facts. Readers should consider these issues when evaluating this paper. Further details are discussed below.

(1) Misrepresentation of the dataset and phenotypes

The authors analyze a dataset on the fitness of yeast mutants, describing it as representative of the Malthusian parameter of an exponential growth model. However, they provide no evidence to support this claim. They assert that the growth of colony size in the dataset adheres to exponential growth kinetics; in contrast, it is known to exhibit linear growth over time, as indicated in [Supplementary Note 1 of https://doi.org/10.1038/nmeth.1534]. Consequently, fitness derived from colony size should be recognized as a different metric and phenotype from the Malthusian parameter. Equating these distinct phenotypes and fitness measures constitutes a fundamental error, which significantly compromises the theoretical discussions based on the Malthusian parameter in the study.

The reviewer is correct in pointing out that colony-size measurements are distinct from exponential growth kinetics. We acknowledge that our original text implied that the dataset directly measured the exponential growth rate (Malthusian parameter), when in fact it was measuring yeast colony expansion rates on solid media. Colony growth under these conditions often follows a biphasic pattern in that there is typically an initial microscopic phase where cells can grow exponentially, but as the colony expands further then the growth dynamics become more linear (Meunier and Choder 1999). We have revised our text to state clearly what the experiment measured.

However, while colony size does not exhibit exponential growth kinetics, several studies have argued that the rate of colony expansion is related to the exponential growth rate of cells growing in non-limiting nutrient conditions in liquid culture. This is because colony growth is dominated by cells at the colony boundaries that have access to nutrients and are in exponential growth. Cells in the colony interior lack nutrients and therefore contribute little to colony growth. This has been shown both in theoretical and experimental studies, finding that the linear growth rate of the colony is directly linked to the single-cell exponential growth rate (Pirt 1967; Gray and Kirwan 1974; Korolev et al. 2012; Gandhi et al. 2016; Meunier and Choder 1999). In particular, the above studies suggest that the linear colony growth rate is directly proportional to the square root of the exponential growth rate. Therefore, one would expect that the validity of the product model for one fitness measure implies its validity for the other measure. In addition, colony size was found to be highly correlated with the exponential growth rate of cells in non-limiting nutrients in liquid culture (Baryshnikova et al. 2010; Zackrisson et al. 2016; Miller et al. 2022). For these reasons, we treated the colony size and exponential growth rate as interchangeable in our original manuscript. 

To address the important point raised by the reviewer, we now explain more clearly in the text what the analyzed data on colony size show and why we believe it is reflective of the exponential growth rate. Finally, we note that our results supporting the product neutrality function are consistent with the work of (Mani et al. 2008), which used smaller datasets based on liquid culture growth rates (Jasnos and Korona 2007; Onge et al. 2007).

The text in Section 2.3 now reads:

“Having verified empirically that the Product neutrality function is supported by the latest data for cell proliferation, we now turn our attention to its origins. Addressing this question requires some mechanistic model of biosynthesis. However, most mechanistic models of growth apply directly to single cells in rich nutrient conditions, which may not directly apply to the SGA measurements of colony expansion rates. In particular, colony growth has been shown to follow a biphasic pattern (Meunier et al. 1999). A first exponential phase is followed by a slower linear phase as the colony expands. Previous modeling and empirical work indicates that this second linear expansion rate reflects the underlying exponential growth of cells in the periphery of the colony (Pirt 1967; Gray et al. 1974; Gandhi et al. 2016; Baryshnikova, Costanzo, S. Dixon, et al. 2010; Zackrisson et al. 2016; Miller et al. 2022). More precisely, mathematical models show the linear colony-size expansion rate is directly proportional to the square root of the exponential growth rate under non-limiting conditions. Intuitively, this relationship arises because colony growth is dominated by the expansion of the population of cells in an annulus at the colony border that are exposed to rich nutrient conditions. These cells expand at a rate similar to the exponential rate of cells growing in a rich nutrient liquid culture. In contrast, the cells in the interior of the colony experience poor nutrient conditions, grow very slowly, and do not contribute to colony growth.

This intimate relationship between both proliferation rates allows us to explore the origin of the Product neutrality function in mechanistic models of cell growth. Indeed, if colony-based fitnesses follow a Product model, then

where the superscript c indicates colony-based values for the fitness W and the growth rate λ. Taking into account the relationship between single-cell exponential growth rates and colony growth rates, we can write

where the superscript l denotes liquid cultures. Combining these expressions, we obtain

In other words, from the perspective of the Product neutrality function, fitnesses based on colony expansion rates are equivalent to fitnesses based on single-cell exponential growth rates. The prevalence of the Product neutrality model—both in the SGA data and in previous studies on datasets from liquid cultures (Jasnos et al. 2007; Onge et al. 2007; Mani et al. 2008)—encourages the exploration of its origin in mechanistic models of cell growth.”

(2) Misapplication of prokaryotic growth models

The study attempts to explain the mechanistic origin of the multiplicative model observed in yeast colony fitness using a bacterial cell growth model, particularly the Scott-Hwa model. However, the application of this bacterial model to yeast systems lacks valid justification. The Scott-Hwa model is heavily dependent on specific molecular mechanisms such as ppGppmediated regulation, which plays a crucial role in adjusting ribosome expression and activity during translation. This mechanism is pivotal for ensuring the growth-dependency of the ribosome fraction in the proteome, as described in [https://doi.org/10.1073/pnas.2201585119]. Unlike bacteria, yeast cells do not possess this regulatory mechanism, rendering the direct application of bacterial growth models to yeast inappropriate and potentially misleading. This fundamental difference in regulatory mechanisms undermines the relevance and accuracy of using bacterial models to infer yeast colony growth dynamics.

If the authors intend to apply a growth model with macroscopic variables to yeast double-mutant experimental data, they should avoid simply repurposing a bacterial growth model. Instead, they should develop and rigorously validate a yeast-specific growth model before incorporating it into their study.

There is nothing that is prokaryote specific in the Scott-Hwa model. It does not include the specific ppGpp mechanism to regulate ribosome fraction that does not exist in eukaryotes.  The general features of the model, like how the ribosome fraction is proportional to the growth rate have indeed been validated in yeast (Metzl-Raz et al. 2017; Elsemman et al. 2022; Xia et al. 2022). Performing a detailed physiological analysis of budding yeast across varying growth conditions in order to build a more extensive model is beyond the scope of this work. Finally, we note that the Weiße model, which we also analyzed, is also generic and has replicated empirical measurements both from bacteria and yeast (Weiße et al. 2015).

To clarify this point in the text, we have added the following to Section 2.3: 

“Experimental measurements in other organisms suggest that the observations leading to this model, including that the cellular ribosome fraction increases with growth rate, are in fact generic and also seen in the yeast S. cerevisiae (Metzl-Raz et al. 2017; Elsemman et al. 2022; Xia et al. 2022).”

(3) Overly specific assumptions in the theoretical model

he theoretical model in question assumes that two mutations affect only independent parameters of specific biochemical processes, an overly restrictive premise that undermines its ability to broadly explain the occurrence of the multiplicative model in mutations. Additionally, experimental evidence highlights significant limitations to this approach. For example, in most viable yeast deletion mutants with reduced growth rates, the expression of ribosomal proteins remains largely unchanged, in direct contradiction to the predictions of the Scott-Hwa model, as indicated in [https://doi.org/10.7554/eLife.28034]. This discrepancy emphasizes that the ScottHwa model and its derivatives do not reliably explain the growth rates of mutants based on current experimental data, suggesting that these models may need to be reevaluated or alternative theories developed to more accurately reflect the complex dynamics of mutant growth.

In the data from the Barkai lab referenced by the reviewer (reproduced below), we see that the ribosomal transcript fraction is in fact proportional to growth rate in response to gene deletions in contradiction to the reviewer’s interpretation. However, it is notable that the ribosomal transcript fraction is a bit higher for a given growth rate if that growth rate is generated by a mutation rather than generated by a suboptimal nutrient condition. We know that the very simple Scott-Hwa model is not a perfect representation of the cell. Nevertheless, it does recapitulate important aspects of growth physiology and therefore we thought it is useful to analyze its response to mutations and compare those responses to the different neutrality functions.  We never claimed the Scott-Hwa model was a perfect model and fully agree with the referee’s statement above that “... these models may need to be reevaluated, or alternative theories developed to more accurately reflect the complex dynamics of mutant growth.” Indeed, we say as much in our discussion where we wrote: 

“While we focused on coarse-grained models for their simplicity and mechanistic interpretability, they might be too simple to effectively model large double-mutant datasets and the resulting double-mutant fitness distributions. We therefore expect the combination of high throughput genetic data with the analysis of larger-scale models, for instance based on Flux Balance Analysis, Metabolic Control Analysis, or whole-cell modeling, to lead to important complementary insights regarding the regulation of cell growth and proliferation.”

To further clarify this point, we discuss and cite the Barkai lab data for gene deletions see Figure 2 from Metzl-Raz et al. 2017.

(4) Lack of clarity on the mechanistic origin of the multiplicative model

The study falls short of providing a definitive explanation for its primary objective: elucidating the "mechanistic origin" of the multiplicative model. Notably, even in the simplest case involving the Scott-Hwa model, the underlying mechanistic basis remains unexplained, leaving the central research question unresolved. Furthermore, the study does not clearly specify what types of data or models would be required to advance the understanding of the mechanistic origin of the multiplicative model. This omission limits the study's contribution to uncovering the biological principles underlying the observed fitness patterns.”

We appreciate the reviewer’s interest in a more complete mechanistic explanation for the product model of fitness. The primary goal of this study was to explore the validity of the Product model from the perspective of coarse-grained models of cell growth, and to extract mechanistic insights where possible. We view our work as a first step toward a deeper understanding of how double-mutant fitnesses combine, rather than a final, all-encompassing theory. As the referee notes, we are limited by the current state of the field, which has an incomplete understanding of cell growth. 

Nonetheless, our analysis does propose concrete, mechanistically informed explanations. For example, we highlight how growth-optimizing feedback—such as cells’ ability to reallocate ribosomes or adjust proteome composition—naturally leads to multiplicative rather than additive or minimal fitness effects. We also link the empirical deviations from pure multiplicative behavior to differences in how specific pathways re-balance under perturbation, and we suggest that a product-like rule emerges when multiple interconnected processes each partially limit cell growth.

In the discussion, we clarify what additional data and models we think will be required to advance this question. Namely, we propose extending our approach through larger-scale, more detailed modeling frameworks – that may include explicit modeling of ppGpp or TOR activities in bacteria or eukaryotic cells, respectively. We also emphasize the importance of refining the measurement of cell growth rates to uncover subtle deviations from the product rule that could yield greater mechanistic insight. By integrating high-throughput genetic data with nextgeneration computational models, it should be possible to hone in on the specific biological principles (e.g., metabolic bottlenecks, resource reallocation) that underlie the multiplicative neutrality function.

Reviewer #2 (Public review):

The paper deals with the important question of gene epistasis, focusing on asking what is the correct null model for which we should declare no epistasis.

In the first part, they use the Synthetic Genetic Array dataset to claim that the effects of a double mutation on growth rate are well predicted by the product of the individual effects (much more than e.g. the additive model). The second (main) part shows this is also the prediction of two simple, coarse-grained models for cell growth.

I find the topic interesting, the paper well-written, and the approach innovative.

One concern I have with the first part is that they claim that:

"In these experiments, the colony area on the plate, a proxy for colony size, followed exponential growth kinetics. The fitness of a mutant strain was determined as the rate of exponential growth normalized to the rate in wild type cells."

There are many works on "range expansions" showing that colonies expand at a constant velocity, the speed of which scales as the square root of the growth rate (these are called "Fisher waves", predicted in the 1940', and there are many experimental works on them, e.g. https://www.pnas.org/doi/epdf/10.1073/pnas.0710150104) If that's the case, the area of the colony should be proportional to growth_rate X time^2 , rather than exp(growth_rate*time), so the fitness they might be using here could be the log(growth_rate) rather than growth_rate itself? That could potentially have a big effect on the results.

We thank the reviewer for their thoughtful remarks. As they rightly pointed out, a large body of literature supports that colonies expand at constant velocity both from a theoretical and experimental standpoint. 

As discussed in the answer to the first question of Reviewer 1, this body of work also suggests that the linear expansion rate of the colony front is directly related to the single-cell exponential growth rate of the cells at the periphery. Hence, although the macroscopic colony growth may not be exponential in time, measuring colony size (or radial expansion) across different genotypes still provides a consistent and meaningful proxy for comparing their underlying growth capabilities. 

In particular, these studies suggest (consistently with Fisher-wave theory) that the linear growth rate of the colony 𝐾 is proportional to the square root of the exponential growth rate 𝜆. Under the assumption that the product model is valid for a given double mutant and for the exponential growth rate, we would have that

The associated wave-front velocities would then be predicted to be

In other words, if the product model is valid for fitness measures based on exponential growth rates, it should also be valid for fitness measures based on linear colony growth rates. 

We now include this discussion in the revised version of Section 2.3.

Additional comments/questions:

(1) What is the motivation for the model where the effect of two genes is the minimum of the two?

The motivation for the minimal model is the notion that there might be a particular process that is rate-limiting for growth due to a mutation. In this case, a mutation in process X makes it really slow and process Y proceeds in parallel and has plenty of time to finish its job before cell division takes place. In this case, even a mutation to process Y might not slow down growth because there is an excess amount of time for it to be completed. Thus, the double mutant might then be anticipated to have the growth rate associated with the single mutation to process X. We now add a similar description when we introduce the different neutrality functions in Section 2.1.

(2) How seriously should we take the Scott-Hwa model? Should we view it as a toy model to explain the phenomenon or more than that? If the latter, then since the number of categories in the GO analysis is much more than two (47?) in many cases the analysis of the experimental data would take pairs of genes that both affect one process in the Scott-Hwa model - and then the product prediction should presumably fail? The same comment applies to the other coarse-grained model.

From our perspective, models like the Scott-Hwa model constitute the simplest representation of growth based on data that is not trivial. Moreover, the Scott-Hwa model is able to incorporate interactions between two different biological processes. We believe models, like the Scott-Hwa and Weiße models, should be viewed as more than mere toy models because they have been backed up by some empirical data, such as that showing the ribosome fraction increases with growth rate. However, the Scott-Hwa model is inherently limited by its low dimensionality and relative simplicity. We do not claim that such models can provide a full picture of the cell. As argued in the main text, we have chosen to focus on such models because of their tractability and in the hope of extracting general principles. We nonetheless agree with the reviewer that they do not have the capacity to represent interactions between genes in the same biological process. We now note this limitation in the text. 

(3) There are many works in the literature discussing additive fitness contributions, including Kaufmann's famous NK model as well as spin-glass-type models (e.g. Guo and Amir, Science Advances 2019, Reddy and Desai, eLife 2021, Boffi et al., eLife 2023) These should be addressed in this context.

We thank the reviewer for pointing out this part of the literature. We do believe these works constitute a relevant body of work tackling the emergence of epistasis patterns from a theoretical grounding, and now reference and discuss them in the text. 

(4) The experimental data is for deletions, but it would be interesting to know the theoretical model's prediction for the expected effects of beneficial mutations and how they interact since that's relevant (as mentioned in the paper) for evolutionary experiments. Perhaps in this case the question of additive vs. multiplicative matters less since the fitness effects are much smaller.

This is an interesting question. Since mutations increasing the growth rate generated by gene deletions or other systematic perturbations are rare, we did not focus on them. Of course, as the reviewer notes, in the case of evolution experiments, these fitness enhancing mutations are selected for. To address the reviewer's question, we can first consider the Scott-Hwa model. In this case, the analytical solution remains valid in the case of fitness enhancing mutations so that the fitness of the double mutant will be the product neutrality function multiplied by an additional interaction term (see Figure 3). The mathematical derivation predicts that the double mutant fitness can potentially grow indefinitely. Indeed, the denominator can be equal to zero in some cases. In simulations, we see that the observation for deleterious mutations does not seem to hold for beneficial mutations (new supplementary Figure S5 shown below). Indeed, no model seems to replicate double mutant fitnesses much better than any other. This suggests that the growth-optimizing feedback we discuss in section 2.3 may have compound effects that ultimately make double-mutant fitnesses much larger than any model predicts.

We recognize this may be an important point, and discuss it in detail in the revised section 2.3 as well as in the discussion.

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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.