On 2018-08-29 14:16:01, user Eryn McFarlane wrote:

Dear Authors,

We are a group of Phd students and Postdocs at the University of Edinburgh that meet weekly to discuss life history papers. We noticed that the tone of our discussions could be a little negative, so, to counteract this, we decided that the most positive thing would be to review pre-print papers, and then share our reviews with the authors. Hopefully, this acts to both give us experience as reviewers, and provide feedback to researchers who have posted their manuscripts on bioarkiv.

We hope that this review is useful to you, and will help to improve your paper. Please feel free to contact us if you have any questions or clarifications.

Best wishes,

Eryn McFarlane<br /> eryn.mcfarlane@ed.ac.uk<br /> on behalf of UoE Life History Journal Club

Major Comments on ‘Latitudinal variation in Life History Reveals a Reproductive Disadvantage in the Texas Horned Lizard (Phrynosoma cornutum)’

This paper addresses some interesting questions about whether life history trade offs are expected to vary according to latitude (and associated environmental variables), particularly in ecotherms which are expected to be physiologically sensitive to heat gradients. Hughes et al. use museum samples from four different populations, collected over 52 years to answer this question. Below, in no particular order, are our main suggestions to improve this manuscript.

Eggs in the ovary vs. clutch size during a breeding season. We would like to see this metric verified against lizards who have laid a full clutch size. In other systems, we are aware of the possibility of 1) biological constraints that limit the number of visible eggs in the ovaduct, meaning that as the visible eggs are hatched, more eggs will be produced and 2) the possibility for females to re-absorb eggs/fetuses they choose not to bring to maturity. For these reasons, we would want to see that the eggs measured here are correlated with the number of eggs a female would lay during her breeding season.

Statistics: We think it would be appropriate to account for both the month (or day, if possible) the animal was collected and the year the animal was collected in all models. Given that animals were collected at different points in the breeding season, without accounting for date, it’s difficult to know if any differences are just due to a bias in when the animals were collected. This would be particularly true if there was a bias in when animals in each site were collected (i.e. were those in Kansas just sampled later in the year?). Similarly, the authors should account for year in their models. Given that climate change has been demonstrated to have affected phenology in a number of different species, we would expect that the window for laying may have changed as the study has gone on.<br /> There are a number of places that the authors don’t employ statistics where we believe they should. For example, the differences in breeding season between the study sites should be assessed statistically, rather than by eye, while accounting for sampling dates and years.<br /> From the description of the counties for sampling in each state, there appears to be a lot of variation in the lat/long that each animal was sampled at. Why not use the lat/long for each animal, rather than lumping them into three state level populations? This would allow for a finer scale assessment of the effects of latitude, particularly since New Mexico and Texas are much closer together than they are to Kansas. <br /> In some cases (i.e. for individual egg measurements), it seems that multiple eggs are taken from the same female. These eggs are not independent. This needs to be controlled for statistically, such as by using a random effect of female id. Otherwise, there is pseudoreplication in the model.

Red thread: We saw the interesting potential in this paper (it’s why we picked it!), but we found it quite hard to follow in some places. For example, the introduction could follow a more traditional structure of starting very broadly, and narrowing down to your questions, while trying to keep each paragraph quite focussed. Similarly, we found it difficult to link between the methods and the results in some places, as results are reported that were not clear from the methods. For example, we’re not sure where ‘Monthly activity’ comes from (i.e. are there analyses done here? What are the sample sizes for each sample size for each month?); age/body size at sexual maturity, we’re not sure how these were inferred at all, given that all samples were dead? We think that more clarity in the methods, and a focus on a one:one ratio between methods and results would help to make the story clearer.

Collection description: We have a lot of questions about where your samples came from, and how they were collected, and stored. It seems likely that there is a lot more data than has been reported here (i.e. exact coordinates, exact dates of sample collection). Were all of the samples collected the same way? How was that done? If they were, for example, all roadkill, how would that bias your results? How were they dissected? Were they all dissected by the same person?<br /> Similarly, we suspect that there is a lot more possible data out there that could help to answer some of the questions posed here. For example, is there NOAA data for each of the sites? This would help to pull apart differences due to latitude per se and differences due to temperature or precipitation. Such analyses would be really interesting, although perhaps too data demanding. As it is now, without this information, it’s difficult to tell if the patterns reported are due to latitude, or something correlated with latitude.

On 2018-07-31 05:50:17, user Guillaume Petit wrote:

Dear Hayden Schmidt, Robin Betz Ron Dror and Andrew Kruse,

We found your article on BioRxiv, read it and discussed it at our research group journal club. Our comments are summarised below.

Overall, we thought this manuscript was very interesting with new and original results, and everyone enjoyed reading it.

In the introduction, perhaps it would be worth mentioning for the broader readership why the σ1 receptor is so named.

For the crystallography and structural biology section: <br /> We appreciate how much hard work it takes to produce and study membrane proteins. Nevertheless, we thought that some of the data in Table 1 could be expanded and commented on. For example, the signal to noise ratio and half set correlation coefficients are very low in the highest resolution shell and the B-factors are very high for all three structures. We recommend including R(pim) and B Wilson values as well as R(free) values for the high-resolution shells. Given the weak data, the structures have been carefully refined because the geometry statistics show that they have been tightly restrained. We recommend providing a comment in the results section on the quality of the raw data and another one in the discussion section of the implications of the data quality for the modelled structures. This would help readers and end-users who might not be familiar with crystallography statistics to ensure that the coordinates are used with appropriate caution. A question that we wondered about was why 7 crystals were needed for the NE-100 complex structure but only one for each of the other two complexes? Could a comment be added to explain that? Additionally, we think Fig 1d and 1e would benefit from being presented in stereo and perhaps with electron density displayed around the residues and ligands. In Fig. 2b, 2d and 2f of the supplementary data, the electron density quality suggests that the orientation of the ligand may have been difficult to determine. Can you comment on how the final orientation was selected and whether other orientations were trialled? Finally, it would be helpful to include a comment on the quality of these three liganded structures in comparison to the previously published structure of the 1-receptor-ligand. Are they better? Worse? Similar?

Kinetics analysis: More background information would be helpful to understand the kinetics and scintillation experiments. What formula was used for the two steps model? What is the relationship between Kd, kfast and kslow? In Table 2, the errors for each measurement and a description of how they were calculated need to be added. We also recommend that you add the full word definition for the N.D. abbreviation in the figure description. Finally, we suggest that you move the “Saturation binding in Sf9 membranes” and “Measurement of ligand dissociation in Sf9 membranes” sections in the online method chapter, to the supplementary data since the corresponding results are also found there.

Molecular dynamics: We recommend including a comment on the limitations of using a simulation of the monomer when the protein forms a trimer in in vitro experiments. Are there plans to simulate the trimer in the future? If so, how would that be done, or why can’t it be done now/easily? For the future it would be worth defining what mutations on helix alpha 4 could be done to confirm the simulation results. Are there other antagonist molecules that could be used to validate the results observed with (+)-pentazocine? What would be the next step to confirm the models?

Small corrections: <br /> In the second sentence of the discussion section agonist is used twice, we believe that one of these should probably be antagonist. <br /> In the online methods section: first sentence, a word is missing after the “and”. In the same sentence we suggest changing the text to the receptor is expressed in Sf9 cells and then purified. (Not expressed and purified in Sf9 cells).

Hopefully you will find these comments helpful. We wish you all the best for the publication of this interesting article!

Kind regards

The Martin Lab (https://www.griffith.edu.au...

(Draft prepared by PhD student Guillaume Petit: guillaume.petit@griffithuni.edu.au, with contributions from all of the Martin Lab)

On 2018-05-09 16:50:03, user Ben Tully wrote:

Journal Club Preprint Review<br /> Parallel Evolution of Key Genomic Features and Cellular Bioenergetics Across the Marine Radiation of a Bacterial Phylum <br /> Reviewed by:<br /> Drs. Benjamin Tully, Michael Morando, Sarah Hu, Michael D. Lee; Graduate students Heidi Aronson, Gerid Ollison, Asa Conover; & One Anonymous reviewer

Overall, the group thought the paper was interesting and well executed and the most powerful results was the evidence of convergent genomic evolution. The following comments are for the few areas where we had questions or thought the paper would be stronger with some clarification or adjustments. We have broken our commentary down into major and minor comments, with major comments structured around larger ideas and minor comments designed to ask specific questions brought up during the journal club.

Major comments:<br /> Two main topics and recurring themes could have been more effectively communicated – specifically “streamlining” and “switching”. While these terms are fleshed out over the course of the manuscript (either in the main text or methods), there are portions of the manuscript where it is unclear what their significance is, or it is poorly constrained.

“Streamlining”<br /> There was a prolonged discussion about the term ‘streamlining’ amongst the group. It was the understanding of the group that this term as generally defined (such as the in the cited Giovanonni et al. 2014) includes concepts regarding how changes in closely related organisms towards lower GC, reduction in pseudogenes and paralogs, low coding density and a possible reduction in genome size could be markers for “streamlining”. <br /> There was concern that the measures used to streamlining were not accurate. The metrics provided (intergenic spacer, N-ARSC, C-ARSC), while corollary to these metrics, do not directly address these factors outright. For example, in Ln. 89-92: “with the genomes of epipelagic Marinimicrobia containing signatures of streamlining such as lower % GC content and shorter intergenic regions”, it seems to us that this application of intergenic-region length is a little ambiguous without gene count and/or genome size accounted for, and that a better metric is coding percentage. The Giovanonni et al. 2014 paper mentions intergenic regions only in the context of ratios of non-coding to coding (“low ratios of intergenic spacer DNA to coding DNA”). Interpretation of this result would also be assisted by either including clarification in Figure 1B that “Size” is “Estimate Size” or providing the raw %completeness and %redundancy values.<br /> Ln 117-9: “…streamlined in all other aspects.” While there is some evidence suggesting this, we think that inherently intergenic space length is not the most accurate measure (as detailed above) and that N-ARSC and C-ARSC may to suggest adaptation to environmental niche/nutrient regimes, which may be related to genomic streamlining, but is not evidence itself.<br /> For another concern raised amongst the group was that our currently understood evolutionary mechanisms for streamlining either involve relatively extremely large effective populations sizes (such as with marine picocyanobacteria), or relatively extremely small effective population sizes (such as with obligate endosymbionts). Is there evidence or data that can suggest which avenue may be driving streamlining in epipelagic clades?

“Switching”<br /> The term ‘switching’ was problematic for most of the group. The way this term was interpreted amongst the group was as the example provided by Simon et al. 2017 (https://www.ncbi.nlm.nih.go... in regard to Roseobacter, with a specific example such as: a marine clade, holds a subclade that diverged to freshwater, and within that freshwater clade there are members than “switched” back to a marine lifestyle. It wasn’t clear to us that there were specific examples provided here of this type of ‘switching’ as opposed to divergence from a common ancestor into new niches more than once. We feel the convergent genomic evolution is clear and solid, but we had a hard time teasing apart whether “switching” was meant how we were interpreting it, and then finding evidence for it. It was suggested that providing a detailed tree with loss/gain markers may assist in this, but it was also discussed that there may be issues due to the incomplete nature of the genomes. In this same vein, the term “parallel evolution” is used in the title, so we think you may want to increase discussion of evidence of ‘switching’ and change the title or keep the title the same and use examples of convergent evolution.

Minor comments:<br /> Genome quality. Using a cutoff of 40% completeness seems a bit low? How would a higher cut off impact the number of genomes analyzed? While included in the table about the genomes used, it may be useful to have a figure (suggested: histogram) looking at completeness? There are several traits that are determined by presence/absence (proteorhodopsin) or based on the fraction of genes recovered (NDH) – does such a low cutoff impact these conclusions?

Methodology questions that should be addressed:<br /> • What were the cutoffs used to determine if a genome was epipelagic vs mesopelagic? <br /> • How were polytomies on the genome tree reconciled with the TPM calculation? Wouldn’t genomes that appear identical on a genome tree of 120 markers competitively recruit the same reads? There was a discussion of selecting a representative of identical MAGs – was this applied evenly to all Tara originating MAGs? From TOBG (Tully), TARA.MAG (Delmont), and UBA (Parks)?<br /> • Explicitly stating how the heatmaps in Fig 1 and 2 were normalized would be helpful, i.e. by row, by column, or across the entire heatmap.

NADH Respiratory Complexes. For the difference between canonical and noncanonical NDH – are these being visualized? As it stands, using a cutoff of 6 and 5 subunits, respectively, on incomplete genomes seems to imply that a genome can have many of the subunits still missing, can you tell if nuoDEF is ‘missing’ without a visualization of the contig? If you are visualizing these contigs, it would be great to include a figure that displays this. Could nuoDEF be encoded in a different part of the genome and just not recovered? Is nuoA-M normally syntenic? It is tough to glean this information from the methods. For the presence of NQR, can organisms utilize the established sodium motive force without a sodium pumping ATPase? Can sodium pumping via NDH be a form of osmotic stabilization?

Fraction of recruited reads. As it stands there is not enough information in Figure 1 to determine how abundance values/TPM/relative fraction of Marinimicrobia differs between the epipelagic and mesopelagic samples. It would be great to detail the scales of ‘Genome Abundance’ in the heatmap of Figure 1 and provide more details as to what is being displayed. Readers in the group came up with two completely valid ways of interpreting the data, one assuming raw relative abundance values, the other assuming normalized relative abundance values – this needs to be clarified. Also, ‘Genome Abundance’ should be explicitly defined as ‘Relative Fraction’ of recruited reads or TPM if that is what is being displayed.

Are the 90 metagenome samples from Tara the same referenced in Delmont et al? Is it just the bacterial/archaeal fraction? There are a 100+ more Tara samples that could be analyzed so some discussion as to why these one over other would be helpful.

Very minor grammatical issues:

Line 52: recent work has

Line 63 and elsewhere: “Marinimicrobial” with an “L” at the end is just an ad hoc adjective, it isn’t the proper noun/phylum, so shouldn’t be capitalized

Line 73 got displaced in this version, probably not actually missing

Line 102: Fig. 2B

Line 119: “to be more”

Line 121: “requires a particular coding potential, that” (I think a comma after “potential” helps this sentence)

On 2018-04-19 13:36:27, user Joe Pomerening wrote:

Great work -- I'll be sure to read the whole article word-for-word. Just wanted to add the comment, while I've been out of the academic game for sometime, particularly the cell cycle field, I think investigators are going to need to accept that the boundaries between *all phases are not nearly as discrete as we schematize and *want to believe. In fact, both S- and M-phase-entries are likely more fuzzy than one would imagine, though the outcomes are clearly quite all-or-none. The linking of post-M-phase progression is an incredibly interesting area, and I believe is where the greatest potential for oncogenesis lies. A really nice story by García-Higuera's group showed that if Cdh1 is ablated, cells start replication way to soon and suffer from a shortage of dNTPs, showing indeed, timing is everything. Anyway, cheers on a nicely done story, good luck with the publication, and may the field be able to accept/comprehend that phase initiation/physiologic response to catalytic enzymes (CDKs, APC's, etc.) will not be as neatly delineated as crossing a line shown in a G1->-S->G2->M schematic.

On 2018-04-02 17:04:21, user Pat Schloss wrote:

My research group reviewed the preprint by Hirten and colleagues as part of our journal club and prepared this collaborative review. None of us have been asked to provide a review of the manuscript for a journal and we do not know its status.

This preprint aims to describe the outcomes of fecal microbiota transplant (FMT) as a treatment for recurrent Clostridium difficile infection (CDI) in patients with and without IBD. The authors have a specific focus on whether IBD patients receiving FMTs are more or less likely to respond to, or have complications arising from, the procedure as a treatment for recurrent CDI. Overall, we think the longitudinal clinical component of the study was particularly well-suited to address the questions laid forth by the investigators, however, the subsequent analysis and grammatical errors within the paper made it difficult to both follow the narrative and reach the same conclusions. As an example, while engraftment of microbial communities following FMT was stated as one of the secondary outcomes the authors were interested in, the data presented aren't sufficient for making any conclusions regarding colonization of donor-derived microbes. Likewise, there are several instances of missing information such as adequate background and justification in the introduction, experimental details in the materials and methods, and the requisite information to interpret the plots in the figure legends. We believe that while the research is worthwhile, the aforementioned issues significantly hinder any conclusions made in the manuscript and need to be addressed.

General comments:

1. In the study, they find that "23 out of 118 (19.5%) patients with follow up at 2 months and 31 out of 83 (37.3%) patients with follow up at 6 months suffered from recurrent CDI after the initial FMT." These failure rates make us wonder if the FMTs can even be considered successful. Given these high failure rates, we wonder how meaningful the results of this study are. The low rates are addressed briefly in the discussion by saying "Many studies exclude subjects with severe CDI, a known predictor of CDI recurrence, which may explain the lower success rate of FMT observed in our cohort compared to others." This explanation, however, is somewhat contradicted when discussing predictors of short term relapse (failed FMT) which included "severe CDI" suggesting that other studies must have also included severe cases in their cohorts. Some clarity regarding these points would greatly appreciated.

2. Although "microbiome engraftment" is a critical concept in this paper, it is never specifically defined or discussed in the context of current literature. Likewise, while engraftment is listed as a secondary outcome, they did not define what a successful engraftment would actually look like. The authors should expand upon the meaning of the phrase and they should also review CDI FMT literature, framing this study in terms of what has been seen previously.

3. Throughout the manuscript, FMT is being used to refer to materials used for the transplant while it really means the process. For example, "FMT was obtained from healthy donors..." should be "Material for FMT was obtained...." This needs to be corrected in several instances.

4. The Methods section needs additional details on how 16S rRNA gene sequences were processed. Additionally, specific details regarding software (parameters used, version, etc.) are absent but are required for proper interpretation of the analysis pipeline. The details that are provided in the Supplemental Material are inadequate and they really should be in the main body of the paper given their importance to the overall story.

5. The last section within the results where the functional analysis of the patient microbiomes is described doesn't warrant its own subsection. The information contained is too broad and disjointed as it's presented and either needs to be expanded on, included elsewhere, or removed altogether. While interesting, it doesn't appear to contribute anything to the main narrative as defined by the primary and secondary outcomes laid out in the introduction.

6. The figure legends were missing almost all information required to interpret the plots and, in some cases, the labels provided were even in the wrong order. Specific methodological and statistical methods need to be stated for each panel or groups of panels.

7. The manuscript needs thorough editing for language and grammar. There are multiple places where it is unclear what pronouns refer to, mixtures of tenses, and confusing sentence structure.

8. For the microbiome analysis, the study included a 9 vs. 9 study design but there isn't any indication whether that would be sufficient to detect the effects of interest. Power calculations need to be provided indicating what effect sizes the study design would allow the investigators to detect for their primary research questions.

9. If the authors used phylogenetic methods, how did they get OTUs for the Random Forest approach? If they generated OTUs, then why not also analyze OTU-based metrics of alpha and beta-diversity. The reference-based UniFrac methods that the authors likely used are strongly biased by what is in the database and are known to have numerous problems relative to de novo clustering methods.

10. Comparison of the microbiota over time should be done with paired tests using each subject as their own control.

11. In the text relating to Figure 2A, the authors use "bacterial alpha diversity", but the y-axis of the figure says "phylogenetic diversity" while an identical plot in Figure 2C uses "alpha diversity" for the y-axis. In addition to this, the y-axes in these plots should start at zero, not 5 or 2.5. The same is true for Figure 3A.

Further Questions:

1. Did the 18 people subjected to the microbiome analyses have a difference in recurrence rates?

2. What percent of the IBD patients went into remission?

3. Was there a relationship between donor and the requirement for escalation of medication (IBDe) vs. the stable group (IBDs)?

Specific Comments (P = page, p = paragraph):

1. P4p2: "reducing bacterial diversity and the abundance of Bacteroidetes and Firmicutes phyla"

2. P4p2: The authors reference an "aberrant microbiome with a donor-like microbiome," however, the supporting data are mixed and don't present a clear conclusion. The aberrant microbiota are supplemented with microbiota from a donor, but it doesn't consistently take on the structure of the donor.

3. P4p2: When stating, "frequent use of concomitant immunosuppressive agents" we assumed that this is in reference to IBD and not CDI treatment, but the writing could be made clearer.

On 2018-03-27 17:35:43, user Haley Dylewski wrote:

Hello! We are graduate students at the University of Tennessee reading BioRxiv submissions and we enjoyed your paper! We have compiled our thoughts into a review and hope you find it helpful!

The authors hypothesize that initial TLR4 expression and concentration changes dictate how sepsis syndrome is initiated. A model consisting of three ODE’s was constructed to simulate initial TLR4 flux between relevant compartments of the cell. The proposed model consists of three ODEs that describe three regions in phase space, each space representing a unique cellular compartment relevant to TLR4 activation. For the most part the authors do a good job explaining the physiological basis of their model as well as discussing their assumptions and reasonings.<br /> The paper starts off strong, providing detailed rationale for the study and a strong biological background for the process described. The description of the model and the biological processes it represents seem sound however, the paper becomes weaker after the model is presented. The authors do not discuss the significance of the model’s outputs in a meaningful way: What information do the phase portraits offer about the system dynamics? What can be interpreted biologically and how exactly was the model applied to clinical situations? <br /> Overall, the authors seem to be addressing an impactful problem and I encourage them to pursue this work further.

Major Comments:

1. Alternative models were not considered in this paper. In the application of the model, the authors ultimately relate mRNA production rate to patient outcomes. Such a relationship seems like it could be represented by a linear regression; I think it is important that the authors compare their model to a simpler one to justify using their model and ultimately make their paper stronger.

2. Though the model design is based on biology, the application of the output is not adequately addressed. The authors predict patient outcomes using the model but do not specify how they do so (it seems that the signal resolution of patient data was compared to the simulated systems). What is the rationale for choosing phase portraits as the output? Does the model provide insight into the system or is its purpose simply to be a predictor of patient outcomes.

3. Some of the greek letters are missing from the text. This may be due to the format of bioRxiv but makes some discussion unclear. We would suggest checking the produced pdf when approving the ms. in bioarxiv.

4. Phi is the crux of this model however the variable is not sound:

a. There are no units associated with it. Without units it is hard to interpret what the variable means. <br /> b. The use of phi in the model is not adequately justified. Phi represents the rate tlr4 mRNA is produced. This parameter appears to be treated functionally as the TLR4 flux entering the system as a result of LPS stimulation. The authors did not clearly explain simplifications assumed in this relationship. Eukaryotic protein production is complex; is the rate of mRNA production representative of the flux in this system? Or is this variable chosen for convenience? There needs to be some kind of mathematical relationship linking rate of mRNA production to rate of protein production, otherwise justification for omitting such a critical relationship should be stated.<br /> c. Three different response systems are modeled representing varying levels of LPS stimulation. The parameter differentiating these conditions is phi however how the values were chosen is not clear to me. How was the cut off of each response determined? It is said that phi “has been determined experimentally”. There is a reference on the measurement but perhaps, because of importance of this parameter, there should be a short explanation of how the measurement was done.

1. Similar to 4-a, none of the parameters have unitis. If the model was made dimensionless, this needs to be clearly illustrated. This is critical for physiological interpretation and reproducibility.

2. The values for the parameters are said to have been “varied until a stable limit cycle was attained”. What does this mean? And does using this method choose parameter values that adequately describe the physical system? It would be good to provide a comparison between the experimentally quantified parameters and the parameters chosen based on the stable limit cycle.

3. At the bottom of page 5, it is mentioned that the model leaves out additional populations of TLR4 in the cell. The reason for omitting this from the model should be discussed.

4. Is it possible that the model predictions would become negative? It appears that in eq. 1 yz are subtracted independently of x - is that well justified?

Minor Comments:<br /> 1. The Supplemental data file does not contain the Tables referenced. It does contain access to the actual model code which is helpful.

On 2018-03-23 18:51:44, user Pat Schloss wrote:

The manuscript by Contijoch and colleagues presents a very intriguing collection of experiments that evaluate the variation in DNA density within the fecal material of sixteen mammalian species. I am excited about this work because it highlights that microbial density may be a confounding variable in microbiome studies. Although it would be difficult to ascertain by this method, I have wondered whether how much of a disease like cystic fibrosis is driven by bacterial density rather than a specific set of pathogens. Although I think this is an important contribution to the field, I have several concerns about the methods and the interpretation of the data. Needless to say, the experiments and analysis have really piqued my curiosity.

1. To throw a wet blanket on the analysis, I could argue that the differences and changes in density are of questionable biological significance. If we assume that DNA density is a proxy for density, then the differences the authors see are much less than a single log in density. Although the numbers are a bit questionable, if we assume that typical feces has 10^12 bacteria per gram, a change in 10-50% would still leave a significant amount of microbial biomass. It would be interesting to get the authors' thoughts on their data from a cell count perspective rather than the more abstract DNA density. I am curious what they think is a biologically meaningful difference in density.

2. The authors appear to assume that fecal DNA is coming from living organisms. However, previous studies have indicated that a minority of bacteria in feces are from intact cells. Ben-Amor and colleagues found that 49% of cells were intact, 19% were injured or damaged cells, and 32% were dead (doi: 10.1128/AEM.71.8.4679-4689.2005). This is important because it would impact their transfer experiments and it may be possible that different mammalian species have different fractions of live/dead bacteria in their feces. In spite of this potential confounder, it is still interesting that the DNA load varies so much across species and between individuals of the same species.

3. The authors did not comment on the fact that some mammalian species vary widely in their DNA density. The density in rats, pigs, and mice varies more than their median density. It would be nice to know whether all individuals within the species consumed the same diet or whether there were other differences that may account for intra-species variation.

4. I fear the authors may have over interpreted the meaning of the variation in carrying capacity. They imply that the carrying capacity is an intrinsic variable for each species. I wonder if it isn't also a product of the taxa within the sample. Some taxa may have "sharp elbows" and exclude other taxa and their density. It would be interesting to see something like a Mantel test relating the difference in density to the difference in beta-diversity within each species. Is density related to community structure?

5. Throughout the manuscript, the authors describe differences in "community fitness". The authors need to provide a better definition of fitness in this context. I am unclear whether it's a measure of the ability of a transferred community to have the same carrying capacity as the host (or the donor) or whether it's a measure of something else. Regardless, I worry that if it is tied to the ability to colonize a germ free animal of a different species that it is a poor metric. Again, we know that much of the DNA in feces is from dead bacteria, there is host-dependent selection for what type of microbes can live in an environment, and a one-time gavage of microbiota is unlikely to enable taxa that are part of a climax community to colonize. It's a bit too artificial of a measure of fitness with a bunch of troubling caveats.

6. The authors show that differences in density relate to differences in gene expression and host response. Unfortunately, there is no commentary on what the genes they identified were and whether there are plausible relationships between differences in microbiota and their density and host response. A fear is that such analyses are prone to false positives - even with correction for multiple comparisons. Given that the authors used host tissue from the cecum and the rest of the gastrointestinal track for these analyses, it would be nice to see confirmation that the DNA density in the feces correlated with its density in other locations.

7. Throughout the manuscript the authors measure density as the "ug of DNA per mg feces". It is unclear to me whether this was based on the wet or dry weight of the fecal material. I would argue that it should be on a dry basis in all of the analyses to control for differences in stool consistency. I know the authors have presented evidence that there's no correlation between density and water content, but it would be interesting to see the authors correct their data for moisture content. For example, is the variation in mouse microbiota density partly attributed to variation in water content? The colors in 1C do not allow me to easily discriminate between the 16 species, but it appears that there is more variation in moisture content than density for the mouse samples and several other species' samples as well.

Other comments...

1. L45 "rDNA" should be "rRNA gene" throughout the manuscript.

2. L65 "sixteen different mammals". Should be "sixteen mammal species"

3. Throughout the authors use the mean and SEM to report their results. These data do not appear to be normally distributed. I would find the results more compelling if they presented the median and interquartile range.

On 2018-03-18 13:46:56, user Aurelien ROUX wrote:

I have read this paper with a critical mind. I provide here a list of concerns about this manuscript, based on previous publications using similar techniques, many of which I am a co-author. Also, for sake of transparency, I am in direct competition with this study as colleagues have obtained in my group opposite results (no fission and no force change with the same set of proteins) made with similar tube pulling assays. However, I think that some of the claims made by this study are sufficiently incompatible with the known mechanics of membranes to be commented, so that the reader can make an educated opinion with a detailed comment. I provide here only a list of concerns, and I do not comment on the quality of the work, besides the points raised below. As such, this is not a formal review, and thus does not aim at proposing experiments or controls to improve the quality of the work.<br /> There are several main problems with this study:<br /> The force increase: <br /> One of the important claims of the authors is the change in tube force (force needed to hold the tube) upon local protein binding. Force increase or decay as a response of protein binding to membranes has already been observed for dynamin (Roux et al., 2010), BAR proteins (Prevost et al., 2015; Simunovic et al., 2016; Singh et al., 2012; Sorre et al., 2012; Wu and Baumgart, 2014) Epsin (Capraro et al., 2010) clathrin (Saleem et al., 2015) and the ESCRT-III protein Snf7 (Chiaruttini et al., 2015). Using the tube pulling assay described in this study, the tube force always drops when a protein binds specifically to the tube (curvature sensor), because the protein stabilizes the tube shape. A force increase is seen in cases where the protein binds only onto the GUV, as it is the case for Snf7, because it increases membrane tension that has a direct effect onto the tube force (tube force = F = 2π√2κσ where σ is the tension and κ the bending rigidity, (Chiaruttini et al., 2015)). Cases where protein binds to both GUV and tube are more complex to describe, but usually lead to tube force drop because the stabilizing effect of the protein overcomes the increased tension of proteins binding to the GUV (Saleem et al., 2015; Sorre et al., 2012).

1-The author claim that they see an increase of tube force, correlated with a local polymerization of ESCRT-III proteins into the tube. First, a polymerization of ESCRT-III in the tube, based on above mentioned studies, is expected to drop the force, not to increase it, as the ESCRT scaffold should stabilize the tube shape. The most likely explanation for this force increase is that the ESCRT proteins polymerize onto the GUV, increasing its tension, as seen in Chiaruttini et al. Cell 2015 (Fig 5G-H). Also, the authors have a clear dependence of the force increase with the ATPase activity of Vps4 (fig 2), which was shown to activate turnover and polymerization of large ESCRT-III assemblies (Mierzwa et al., 2017), reinforcing the idea that the force is arising from the polymerization of ESCRT onto the GUV, and not on the tube. Unfortunately, the poor quality of the confocal images provided in fig 4A-F (see following comments below) does not allow to see if ESCRT proteins polymerize onto the GUV membrane. In fig 4I, the authors plot the fluorescence intensity of the Snf7 at the GUV membrane as a function of time, but from the image shown in 4C and 4F, it is impossible to distinguish the membrane bound pool from the bulk solution in the GUV lumen. <br /> Vps2/Vps24 have inhibiting function on Snf7 polymerization that can be levered by the addition of Vps4 and ATP (Mierzwa et al. NCB (2017)). Thus, a possible mechanism to explain the authors’ data is that upon ATP uncaging, Vps4 removes the inhibition of Vps2/Vps24 and promotes polymerization of the ESCRT-III proteins onto the GUV. This increases the tension, and the tube force.

2-Second, when a protein partially polymerizes onto the membrane tube it cannot change the force, because the membrane is fluid and cannot act as a force transmitter (Roux et al., 2010; Simunovic et al., 2016). The protein thus acts as a swimmer in the swimming pool, moving the lipids around rather than applying forces on the membrane boundaries. Thus, it is very unlikely that the force increase measured by the authors is generated by the ESCRT-III punctae along the tube.

3-the force values. The authors claim that the force generated by the ESCRT-III polymerization is responsible for fission. However, when they have 2um of proteins, they have a high force value (max 65pN. Fig 2), which should be more effective for fission, but observe no fission. On the contrary, at a lower ESCRT-III concentration, 200nM, they have a much lower force increase, (below 20pN, Fig 3D), which should be much less effective in promoting fission, and they observe fission in 50% of the cases. Knowing the force and the bending rigidity of POPC membranes used in this study (10 kT, see (Marsh, 2006)), one can calculate the resulting membrane tension at the highest tube force of 65 pN using the formula F = 2π√2κσ. It gives values of tension in the order of mN/m, which are in the range of lysis tension values (usually 1-10 mN/m). It is thus expected that at the highest force (with 2uM proteins), the authors should see fission, just because they should break the membrane by reaching lysis tension.

In conclusion to the force comments, the authors do not provide a mechanism (or model) to explain how local polymerization of the ESCRT-III complex could generate force increase in the tube. They do not provide either an explanation how the force increase could participate in fission. In particular, the increase in force tube suggest the force is applied along the tube axis, whereas fission requires forces perpendicular to the tube axis (constriction) which normally do not affect the tube force. For instance, in fission events mediated by punctual clusters of dynamin along the tube, no force change is observed prior to fission (Morlot et al., 2012).

The fission rate, efficiency and localization.

The time of fission is somewhat surprising. All events reported in this paper take more than 150 seconds apparently and some are very long about 600 seconds. About 50% of the tubes do not break after 1000s. In comparison (numbers taken from (Morlot et al., 2012)), the average time for dynamin-mediated fission is below 10s if the GTP concentration is above 150uM, with 100% efficiency. The dynamin fission time is still below 100s, with more than 65% efficiency if the GTP concentration is only 5uM. Thus, if the events reported in this manuscript are really fission events (see comments 2 below), the rate is extremely low and the reaction non-efficient. This may indicate a missing factor. <br /> An inherent limitation of the force trace to follow fission of the tube is that instantaneous force drop can be due to detachment of the membrane tube from the bead, and not to fission. Because the force is rising in this manuscript, increasing the probability of detachment of the membrane from the bead, and the time for fission is above 100s, the probability is high that the events shown in figure 3 are tube detachments and not fission. Of course, the fact that the authors do not observe such events with 2uM proteins, while having higher force, supports that the membrane/bead link is solid, but by experience, the solidity of such link varies a lot from experiments to experiments.<br /> Thus, to fully validate fission, it is required to show time-lapse imaging that correlates the position of the protein coat with the fission event, identified by a clear break in the tube with visible stumps after fission, one attached to the bead (Morlot et al., 2012; Simunovic et al., 2017). In this study, the fission event is not clearly identifiable on the images presented in Fig 4F. Instead of a clear cut in the membrane channel, one can see the tube rather fainting away instead of breaking. This is consistent with the hypothesis that the force increases because of a rise in membrane tension, that would reduce progressively the tube radius. <br /> But the most awkward images are the ESCRT-III protein coat punctual localization in the tube (fig 4F). It consists of a single pixel, certainly very bright (see arrows in images 49.10s to 50.95s in fig 4F). One would expect that if a diffraction-limited spot of ESCRT-III protein was seen, it would cover at least several pixels. Moreover, images and movies look like they have been time averaged (see below), which could artificially increase the duration time of a puncta present in the bulk solution, and that coincidently localized with the tube on a single image. <br /> For instance, movie S2 shows some unexpected noise correlations between frames (compare noise around the time stamp in images of the Vps2 channel between images at time -1.96s and -2.33).

This strongly suggests that the movies have been time interpolated. This may not be a problem if it is clearly stated and provided that the quantifications and conclusions are not affected by the interpolation. But the time averaging is not stated in the text nor in the Mat&Meth. If time averaging has been performed, this is clearly a problem for the interpretation of Fig 4F: the single pixel interpreted as localized polymerization of the ESCRT-III proteins and visible on multiple frames could be in fact a noise pixel present on a single image and time averaged.

There are also unanswered questions, which affects the reliability of the study.

1-The group of Jim Hurley published two papers (Wollert and Hurley, 2010; Wollert et al., 2009) in which the main claim was that fission was Vps2/Vps24 dependent while it was Vps4 independent, and that Vps4+ATP was only needed for recycling. The only sentence mentioning the discrepancy between their previous studies and their new findings is line 56-59: “Early attempts at in vitro reconstitution of ESCRT-mediated budding and scission using giant unilamellar vesicles (GUVs) suggested that the process was independent of Vps4 and ATP (21,22), except for the final post-scission recycling step.” The authors must provide the fundamental differences between the two assays that explain this discrepancy.<br /> 2-Why is the reaction blocked at higher protein concentration?<br /> 3-What’s the cATP concentration? Is it constant in all experiments? How much is uncaged during UV illumination?

Minor points:<br /> -While I understand the interpretation that instantaneous intensity drops correlate with fission of the tube in figure H, J, L (intensities measured on the tube), I do not understand what the instantaneous force drops observed in figure I, K and M (measured on the GUVs) correlate with, as no fission or explosion of the GUVs are expected.<br /> -Line 119: ”Snf7 intensity in the GUV, however, is essentially unchanged (Fig. 4I).” The quality of the images presented is too low (saturation is too high) to support this statement.<br /> -Line 124: ”We can rule out such a bulk stiffening mechanism in our system given the lack of recruitment of Snf7 to the GUV membrane and the lack of correlation between GUV Snf7 intensity and force generation.” As said above, it is impossible to see whether ESCRT-III proteins are binding or not to the GUV on the images presented in this manuscript, and how and where the fluorescence measurement on the GUV remain unclear in the text and Math&Meth.<br /> -Line 156: “We also found that scission by ESCRT III and Vps4 can occur mid tube” this statement is difficult to verify because the quality of images presented is too low to conclude anything.

REFERENCES:<br /> Capraro, B.R., Yoon, Y., Cho, W., and Baumgart, T. (2010). Curvature sensing by the epsin N-terminal homology domain measured on cylindrical lipid membrane tethers. Journal of the American Chemical Society 132, 1200-1201.<br /> Chiaruttini, N., Redondo-Morata, L., Colom, A., Humbert, F., Lenz, M., Scheuring, S., and Roux, A. (2015). Relaxation of Loaded ESCRT-III Spiral Springs Drives Membrane Deformation. Cell 163, 866-879.<br /> Marsh, D. (2006). Elastic curvature constants of lipid monolayers and bilayers. Chem Phys Lipids 144, 146-159.<br /> Mierzwa, B.E., Chiaruttini, N., Redondo-Morata, L., von Filseck, J.M., Konig, J., Larios, J., Poser, I., Muller-Reichert, T., Scheuring, S., Roux, A., et al. (2017). Dynamic subunit turnover in ESCRT-III assemblies is regulated by Vps4 to mediate membrane remodelling during cytokinesis. Nat Cell Biol 19, 787-798.<br /> Morlot, S., Galli, V., Klein, M., Chiaruttini, N., Manzi, J., Humbert, F., Dinis, L., Lenz, M., Cappello, G., and Roux, A. (2012). Membrane shape at the edge of the dynamin helix sets location and duration of the fission reaction. Cell 151, 619-629.<br /> Prevost, C., Zhao, H., Manzi, J., Lemichez, E., Lappalainen, P., Callan-Jones, A., and Bassereau, P. (2015). IRSp53 senses negative membrane curvature and phase separates along membrane tubules. Nat Commun 6, 8529.<br /> Roux, A., Koster, G., Lenz, M., Sorre, B., Manneville, J.B., Nassoy, P., and Bassereau, P. (2010). Membrane curvature controls dynamin polymerization. Proc Natl Acad Sci U S A 107, 4141-4146.<br /> Saleem, M., Morlot, S., Hohendahl, A., Manzi, J., Lenz, M., and Roux, A. (2015). A balance between membrane elasticity and polymerization energy sets the shape of spherical clathrin coats. Nat Commun 6, 6249.<br /> Simunovic, M., Evergren, E., Golushko, I., Prevost, C., Renard, H.F., Johannes, L., McMahon, H.T., Lorman, V., Voth, G.A., and Bassereau, P. (2016). How curvature-generating proteins build scaffolds on membrane nanotubes. Proc Natl Acad Sci U S A 113, 11226-11231.<br /> Simunovic, M., Manneville, J.B., Renard, H.F., Evergren, E., Raghunathan, K., Bhatia, D., Kenworthy, A.K., Voth, G.A., Prost, J., McMahon, H.T., et al. (2017). Friction Mediates Scission of Tubular Membranes Scaffolded by BAR Proteins. Cell 170, 172-184 e111.<br /> Singh, P., Mahata, P., Baumgart, T., and Das, S.L. (2012). Curvature sorting of proteins on a cylindrical lipid membrane tether connected to a reservoir. Phys Rev E Stat Nonlin Soft Matter Phys 85, 051906.<br /> Sorre, B., Callan-Jones, A., Manzi, J., Goud, B., Prost, J., Bassereau, P., and Roux, A. (2012). Nature of curvature coupling of amphiphysin with membranes depends on its bound density. Proc Natl Acad Sci U S A 109, 173-178.<br /> Wollert, T., and Hurley, J.H. (2010). Molecular mechanism of multivesicular body biogenesis by ESCRT complexes. Nature 464, 864-869.<br /> Wollert, T., Wunder, C., Lippincott-Schwartz, J., and Hurley, J.H. (2009). Membrane scission by the ESCRT-III complex. Nature 458, 172-177.<br /> Wu, T., and Baumgart, T. (2014). BIN1 membrane curvature sensing and generation show autoinhibition regulated by downstream ligands and PI(4,5)P2. Biochemistry 53, 7297-7309.

On 2018-02-14 16:38:34, user Pat Schloss wrote:

I was excited to see the preprint from Calus and colleagues describing NanoAmpli-Seq. This is a method of sequencing long amplicons using the Oxford Nanopore sequencing platform. For my set of applications within microbial ecology, this exciting sequencing platform still appears to be a method in search of an application. This preprint lays out an improved method of sequencing full-length 16S rRNA genes. This is an important issue because (as they note) the number of full-length sequences going into our reference databases is slowing and is unlikely to be representative of the diversity we are now seeing in surveys using MiSeq to sequence fragments of the 16S rRNA gene. Further, we'd really like to have longer reads for improved classifications. Reading the Introduction one will see that my previous work developing methods for sequencing 16S rRNA genes using the MiSeq and PacBio figure prominently in their motivation. It should also be noted that I do not know the current status of this manuscript and have not been invited to review it for a journal.

The authors do an admirable job of tempering expectations and pointing out that the sequence quality is still not to the level that we find on other platforms. The authors mention that they get a sequencing accuracy of 99.5%, in contrast to the 99.98% accuracy we see with the other methods. In some ways this manuscript reads like, "We've done our best to solve the error rate problem, here's where we are, take it from here." These type of "landmark" papers are important, but I can't help but think of things to try. Perhaps other approaches were attempted (they mention three INC-Seq aligners), but they don't seem to be mentioned and there is not an extensive description of any parameter sweep tests.

I think it would be helpful if the authors could improve their legend for Figure 3 - this is the critical figure for describing the method. The authors should note that the A, B, C of the legend seem to correspond with the three shaded boxes, not the A, B, C, ... J within those boxes. The method appears to run the output for the Nanopore sequencer through the INC-Seq software and use that as the starting point for their flow with chopSeq. My understanding of the first step in D is to re-orient the reads and trim the reads to start and end with the correct primers. They then remove the tandem repeats. Instead, I wonder why the authors didn't start over with the INC-Seq software to make a better assembler that is aware of the primers and other issues from sequencing 16S rRNA genes. In our development of the PacBio pipeline, the creation of the consensus sequence made the biggest impact. As PacBio improved their assembler, the data quality far better than anything we could do. If they did this, the authors could calculate better quality scores, assess a aggregate consensus sequence quality score that could be used to filter the consensus sequences.

On P14 they state, "This suggests that consensus sequence accuracy is reliably high only for OTUs where a minimum of 50 reads are available for use in constructing the consensus sequence" and on the next page that they used a three concatemer threshold set for INC-Seq. Given the ability to generate massively long reads on the Nanopore, why not run the sequencer longer to sequence more concatemers? Also, what happens to the error rate when the authors require more concatemers? Again, the PacBio aggregate quality score for a consensus sequence is linked to the level of coverage. I'm wondering if such information could be obtained either from the INC-Seq software or from making their own version of the assembler.

As mentioned above, I found the overall description of the bioinformatics methods to be jargony and a bit glossy on details. First, I was a bit confused by the authors description of why they partitioned the consensus reads into thirds for the nanoClust step. I'm also not clear how this would work - did they cluster the three partitions separately and then bring them back together somehow? Second, they removed singletons, which probably deflates their error rate relative to my reported PacBio error rates. I know that this is contentious, but I think that removing singletons from a 'real' sample would be pretty risky and likely to create a bias against rare organisms in poorly sequenced samples. Third, I wonder why the authors didn't align the sequences prior to getting a consensus sequence using something like a NAST-based profile alignment. They could then cluster similar sequences together using something like oligotyping or our pre-clustering method. This should be considerably faster (and I suspect more robust) than VSEARCH followed by MAFFT.

Another problem that the authors do not mention is the possible biased abundances generated by RCA. They assume that RCA followed by fragmentation and debranching would yield the same number of fragments per piece of circularized DNA. I don't know that this is true. I wonder whether random barcodes could be added to the PCR primers so that when the fragments are amplified, circularized, fragmented, and sequenced, it would be possible to know which fragments came from the same RCA reaction. That way each RCA reaction could only be used once in downstream analyses.

I wonder whether the authors included chimeric sequences when calculating their error rates. Chimeras are not sequencing errors and should not be included in calculating the error rates. This may help to reduce their error rate a bit.

The authors are to be commended for providing their detailed methods as supplemental materials, this is excellent. One thing we learned from publishing our Kozich methods was that in addition to this, it would be great to provide a link to a GitHub page that has the "live" version of the method with any recent updates they've made to the protocol. We have a GitHub page for ours now, but wish we would have included the link to the page in our paper since the one in the supplement is now quite out of date.

Some smaller points...

1. There are other methods beside PacBio for generating full length 16S rRNA gene sequences using HiSeq. Perhaps it would be worth mentioning these in passing? They cite using EMIRGE to extract 16S rRNA gene sequences from metagenomic libraries, but it has also been used by stitching together short amplicon data (doi: 10.1371/journal.pone.0056018).

2. It's hard to keep track of what generation we're on! Instead of using "Second" and "Third" generation in the abstract and introduction, how about just using the platform names. Also, the generation model implies one generation is better than another when the authors' data indicates that "better" still depends on the application.

3. The Abstract is jargony. There are a lot of terms used that are not defined when someone reads only the abstract. What is INC-Seq? The acronym is spelled out, but can the authors give a brief description of what it is? What is "chopSeq"? What is "nanoClust"?

4. On P11. "Inspections of the read to reference alignment length ratio indicated that the major source of sequence error for both INC-Seq and chopSeq corrected reads originated from deletions; i.e. percent similarity of the read to the reference decreased in proportion to the read to reference alignment ratio for all experiments and INC-Seq aligners us". I don't see how the "i.e." explains the first sentence

On 2018-01-25 20:11:24, user Heather Bruce wrote:

This comment was posted a few versions back and isn't showing up here, but I think the discussion is important, so I'm reposting it.

SPXR said:<br /> Two shortcomings are: (1) lack of explicit comparison of the "large" and "small" plates of Oncopeltus with respect to the pleurae of other insects, and (2) assumption that the abdominal appendages of insects and other Pancrustacea are uniramous. With respect to 1, the pleurae of insects comprise the two pleural arcs (coxosternite: trochantin, precoxa; anapleurite: episternum, epimeron), as defined by Snodgrass (1935, Fundamentals of Insect Morphology). It is frustrating to read a paper making claims about the "body wall" of insects without ever using the term "pleuron", which appears to betray lack of comparative morphological knowledge. That said, shortcoming 2 above is less grievous, but still disheartening: The authors claim that the abdominal styli of Archaeognatha and Zygentoma are epipods, apparently forgetting that the abdominal appendages of Pancrustacea are biramous, with an endopod ("telopod") and exopod, with a number of protopodal epipods.

Please pardon the tone of this message. The work is very encouraging for the resolution of leg and pleural homologies overall!

My response:<br /> Thank you for your comments, I’m very happy for the opportunity to discuss this!

Regarding (1), we made a decision to remove as much jargon as possible so that the paper would be accessible to a wide audience. As you are probably aware, insect and crustacean morphology nomenclature can be quite daunting, and we didn’t want to lose the reader at Figure 1! In the original version of the manuscript, I went with the terms in Snodgrass 1927, where he makes a nice case for the insect subcoxa theory. So, I homologized the crustacean coxa with the insect trochantin, and the crustacean precoxa with the insect epimeron/episternum. Terminology aside, another reason not to use the insect nomenclature is that there may not be terms that correspond precisely to the ancestral crustacean structures. For example, the epimeron/episternum might only represent the lateral/pleural portion of the precoxa leg segment that was incorporated into the insect body wall, but the precoxa might also include a portion of the notum, above and adjacent to the wing. Another issue was that I did not come across a term that distinguishes the body wall part of the trochantin from the plate-like outgrowth of the trochantin, which extends over the insect coxa. It was important to distinguish these two regions, because only the plate-like outgrowth of the trochantin is deleted following the loss of wing/epipod genes (Clark-Hachtel 2013, Ohde 2013, Medved 2015, Wang, 2017), and therefore it was to this region only that I homologized the crustacean coxal epipod. Our solution to these problems was to use pictures and plain language to show our homology schema. However, I’m happy to wade into the jargon weeds with you here :)

As you probably know, “biramous” refers to a leg with an exopod, while “uniramous” legs lack an exopod, but may have epipods and endites (Boxshall 2004, Boxshall 2009). Regarding your point (2), we do not claim that the abdominal appendages of Archaeognatha or Pancrustacea are uniramous (Parhyale abdominal appendages are quite biramous, as are the thoracic and/or abdominal appendages of many crustaceans). From our manuscript, “the thoracic stylus of jumping bristletails (Fig. 4, st) is the epipod of the crustacean basis”. From a morphological standpoint, Tiegs 1940 says that Archaeognathan thoracic styli are unsegmented, and do not have intrinsic musculature, which are hallmarks of epipods (Boxshall 2004, Boxshall 2009). In contrast, the abdominal styli, while they may or may not be segmented (Matsuda 1976 vs Staniczek 2014), apparently have intrinsic musculature (Matsuda 1976, Matsuda 1957, Tiegs 1940), which suggests that they are exopods (Boxshall 2004, Boxshall 2009). However, since thoracic and abdominal styli both emerge from the insect coxa/crustacean basis (our manuscript, and following discussion), it is somewhat curious if they are not homologous structures. I certainly welcome any good sources you may have on this subject!

Basal hexapods aside, a more satisfying answer regarding the identity of the lateral nubs of insect embryonic abdominal appendages lies in a comparison of Sp6-9/btd and Dll expression. The crustacean basis/insect coxa expresses Sp6-9 and btd (our manuscript). It carries the exopod and endopod, which each express Dll (Fig. S1, Hejnol 2004, Williams 2002, Panganiban 1995). Thus, if insect abdominal appendages had exopods, they should express Dll. However, most insects do not express Dll in the abdomen (this is why many molecular researchers didn’t know that insects form abdominal appendages as embryos and regarded them in adults as novel structures). While Dll, and thus exopods, are not expressed in insect A2-8, there are paired, leg-like domains of btd expression on each abdominal segment of some insects (Schaeper 2010), which, according to our leg segment homology model (Fig. 4), suggests that these appendages are comprised of three leg segments: the precoxa (pink), crustacean coxa (red), and insect coxa (orange, expresses Sp6-9/btd), but not the trochanter (yellow, expresses Dll). See also the beautiful SEM images of the lateral nubs of the embryonic abdominal appendages in terrestrial carabid beetles in Kobayashi 2013 compared to the gills in aquatic carabid beetles in Komatsu 2012. Komatsu 2012 note that the gills of the aquatic beetle do not develop from the insect coxa, but from a proximal region, the subcoxa, which fuses to the body wall. This is most apparent by examining the nub/gill of the A1 pleuropod, which emerges from a position proximal to the insect coxa. Notably, the A1 pleuropodia, which is longer, expresses both Sp6-9/btd and Dll at the tip, while the A2-8 appendages, which are shorter, express only Sp6-9/btd (Schaeper 2010, Beerman 2004, Beerman 2001, Rogers 2002). This is explained by our model (Fig. 4): the longer A1 pleuropod is comprised of at least four leg segments (precoxa, crustacean coxa, insect coxa, trochanter) expressing both Sp6-9/btd and Dll, while the shorter A2-8 appendages have three leg segments (precoxa, crustacean coxa, insect coxa), expressing only Sp6-9/btd. Since the A2-8 appendages do not express Dll, they do not have exopods, and cannot be considered biramous.

We are planning to submit this manuscript to a journal soon, and due to space limits, we could not include as much of the background supporting information as we would have liked. However, I am currently writing a review that more fully discusses the morphological, molecular, and embryological evidence for the model we propose in this manuscript. I hope this was helpful :)

On 2018-01-22 03:30:20, user BenjaminSchwessinger wrote:

Thanks for posting this preprint. The detail of analysis and the availability of all code is great. it is excellent to see more plant pathogenic obligate biotrophic fungi sequenced. My 'feel' is that these genomes may well look pretty different to some of the better studied non-obligate oomycetes and fungi e.g. 'two speed' genome with effectors clustering to TEs. I could conceived that at least a subset of effectors may well be required in obligate biotrophs as they have to infect the host to complete the life-cycle.

Some thoughts and questions:

• Would be great to see some read length statistics on your PacBio sequencing to get a better understanding why the genome is still in a good number of contigs.

l. 146 Instead of beginning and end of contig I would use 5' and 3' prime of the sequence.

l. 185 ff. I got confused here as the numbers didn't add up for me 6039 single-copy groups give rise to 6,844 one-to-one mappings? I think I get it after reading it several times, yet some rephrasing may well help. Else proteinortho with the synteny flag may have also been an option for doing this analysis.

l. 223ff: The observation of smaller parts of the genome being reshuffled in DH14 vs. RACE1 is pretty interesting. We saw something similar comparing the two haploid genomes in wheat stripe rust fungus (see Figure 2, https://www.biorxiv.org/con.... Wonder how this all happens. Else http://assemblytics.com/ may also be a useful too in future to compare two genomes with each other in regards to structural variations.

l. 265ff: Great analysis on paralogous. We still need to do this for our candidate effectors, yet we saw an overall 'clustering' of candidate effectors. I liked the part of looking if SPs are enriched on certain contigs. Does this also hold true if you consider gene content and not only contig length?

Figure 4A would be easier to interpret if it were normalized to the number of genes analyzed and n given within the figure.

l. 353 ff: Mirrors what we found in wheat stripe rust and others in P. coronata, where candidate effectors do not reside close to TEs in general and not in gene sparse regions. We also see that candidate effectors such as CEPS in Figure S2 C have no really close neighbours. This is pretty intriguing to me. Any thoughts on this? Have you tested if CSEPs are somewhat linked to BUSCOs following the idea that some effectors are necessary in obligate biotrophs. If that is the case for you guys as well, i would be happy to look into if the BUSCOs or effectors tor which this is true are conserved.

l. 380 ff: The analysis of a TE burst in Bgh is very interesting indeed. I think it would profit from a bit more detail on what kinds of TEs were found and how much each family covered. Figure 5 also lacks some details about the usage of all these acronyms used in the figure eg. BOTR? Increasing font size and including a key in the legend would be great.

What I wonder with BGH is where did all the old TEs go? Wouldn't you expect to have some of the older TEs still present around the same age/%id as in the other Blumeria? Within the Blumeria how many TE families were specific to each species? Could it be that your database does not include the most recent TEs from other fungi?

Supplemental figure[:-3]: Not sure that joyplots are the best representation here. A circos plot maybe a better visualization.

Great work. Gave me some good pointers for my own work.

On 2018-01-04 21:08:32, user Jeffrey Ross-Ibarra wrote:

Although current data strongly suggests a single domestication of maize (Matsuoka et al. 2002), knowing the geographic location of domestication is of interest for a multiple reasons. It may be of use agronomically, allowing us to identify portions of the range of maize’s wild ancestor teosinte most likely to harbor novel genetic diversity. But it is also of interest scientifically in terms of our understanding of how domestication occurs. Is maize descended primarily from a single population on one hillside and spread from there? Or was maize domestication a more dispersed process, involving selection and gene flow across a number of populations by multiple groups?

By studying a nice sampling of maize and teosinte populations from across Mexico, Moreno Letelier et al. (2017) seek to reasses the genetic evidence for specific geographic origins of maize domestication. Using a number of different methods, they claim “the likely ancestor of maize may be an extinct population of teosinte from Jalisco or the Pacific coast”.

I should state from the start that I don’t know where maize was domesticated. The SouthWest Mexican lowlands <1800m<br /> seems pretty likely given all the evidence, but whether Jalisco or Michoacan or Balsas I don’t think the genetic data have yet said with any certainty.

Below I detail some concerns with the analyses presented here.

Jalisco as ancestor

Moreno Letelier et al. (2017) build dendrograms of genetic distance (Figure 3) among all their samples, finding that parviglumis from Jalisco is closer to maize than populations from the Balsas. I don’t doubt this result, but as we discuss in Van Heerwaarden et al. (2011), this could be due to gene flow instead of ancestry. Current gene flow from parviglumis to maize is known in Jalisco (see e.g. discussion in Serratos (1997)), and should be discounted as an explanation before trying to infer ancestry from genetic distance alone. Indeed, in their own TreeMix analysis (Figure 4), Jalisco populations of teosinte form a single group with other teosintes, and are thus no more “ancestral” than any other (but see below for issues with TreeMix analyses). Given the really nice data the authors have, I’d be tempted to do something like redoing the analyses of Van Heerwaarden et al. (2011), especially if combined with denser geographic sampling.

I’m not sure where the inference of an “extinct” population comes from, as this idea seems mentioned only in the abstract.

TreeMix

The authors use TreeMix (Pickrell and Pritchard 2012) to test for gene flow. This method first builds a population tree using allele frequencies, then adds edges (arrows) of migration to account for excess covariance in allele frequencies between populations. However, the authors chose to compare all domesticated maize as a single group to individual populations of teosinte. This means any post-domestication gene flow between maize and teosinte (which is presumably restricted to sympatric populations) is either missed entirely or interpreted as gene flow between all maize and teosinte. Indeed, the gene flow shown on Fig. 4 is between maize and mexicana, as has been well documented in the highlands of central Mexico (Hufford et al. 2013), but is limited to populations there and perhaps the Southwest US (Fonseca et al. 2015).

A clue that this analysis might be problematic comes from the monophyletic grouping of all teosinte (both mexicana and parviglumis) separate from maize. Taking this at face value would suggest those subspecies split after domestication, which seems somewhat unlikely given both genetic (Ross-Ibarra, Tenaillon, and Gaut 2009) and ecological (Hufford et al. 2012) evidence they’ve been distinct for some time.

I think it would be preferable to sample a number of maize populations and include each in the analysis, hopefully allowing TreeMix to do a better job building the correct tree and localizing gene flow. SeeDs of Discovery data, for example, provides publicly-available SNP data for ~5,000 maize landraces.

ABBA-BABA

The authors then apply the ABBA-BABA test (Durand et al. 2011), which tests for assymetry in counts of shared derived alleles between two taxa in an ingroup with a third taxon. If the tree depicting the relationship between species is correct, then both ingroup taxa should share similar numbers of derived alleles with the third taxon. Asymmetry in numbers of shared derived alleles then suggests gene flow. Here, the authors use only maize from the highlands of central Mexico for this test, citing Freitas et al. (2003) that these landraces were likely the first to be domesticated. But the widespread gene flow from mexicana into highland maize makes a problematic choice to use for understanding the origin of maize domestication (Van Heerwaarden et al. 2011). Moreover, both trees show teosinte populations sharing a common ancestor more recently than either do with maize, which seems problematic. The first tree (((Jalisco,Balsas),maize),Tripsacum) shows the two parviglumis populations splitting post maize domestication, which is only plausible if one is a very recently derived colonist. The second tree (((*mexicana*,Balsas),maize),Tripsacum) shows parviglumis and mexicana diverging after their common ancestor with maize, which as discussed above is likely wrong. Significant D (or fd) statistics here may thus mainly reflect that the tree is wrong. Perhaps instead the questions of maize origin might be one of comparing a “Jaslico-ancestral” tree (((Jalisco,maize),Balsas),Tripsacum) to a “Balsas-ancestral” tree (((Balsas,maize),Jalisco),Tripsacum) – I’m dubious ABBA-BABA is the appropriate way to go about this though.

From the lit

Both Van Heerwaarden et al. (2011) and Hufford et al. (2013) are papers produced by my lab, so I’m clearly not objective, but in several places the authors seem to ignore or misinterpret results from these papers, highlighting instead results from their own work which are pretty similar.

Recognizing that gene flow from mexicana likely causes biases in identifying ancestral maize populations, Van Heerwaarden et al. (2011) used a broad sampling of >1,000<br /> landraces to estimate ancestral maize allele frequencies. We identified numerous samples from Western Mexico (including multiple samples from Jalisco) as those most genetically similar to the putative ancestor of modern maize. Notably, however, we did not suggest “ancestral teosinte alleles in the Western region, rather than the Balsas Basin” (emphasis mine) – we actually didn’t have the resolution to really say one way or the other (see our Figure 3B). In fact, in spite of our lack of resolution, we mostly interpreted our data as consistent with archaeology and previous genetics as supporting a Balsas origin. In spite of its inclusion as evidence supporting a possible Jalisco origin, Moreno Letelier et al. (2017) seem to forget our paper later, however, claiming that “dense enough sampling in the mountains of Jalisco… were not considered in previous studies as a potential center of domestiation”, and noting “the inclusion of Jalisco populations here, which have not been used previously in other studies”.

Hufford et al. (2013) used the same genotyping platform as Moreno Letelier et al. (2017) to test for gene flow between mexicana and highland maize. But while Moreno Letelier et al. (2017) claim “previous studies could not differentiate between contemporary processes and ancestral introgression”, we explicitly used HapMix (Price et al. 2009) to estimate the timing of admixture from tracts of inferred ancestry. Our analysis was problematic for a number of reasons – for example assuming a single bout of admixture – but nonetheless revealed that maize alleles in mexicana were mostly young while mexicana alleles in maize could be quite old, consistent with adaptive introgression from mexicana into maize upon colonization of the highlands and selection against gene flow from maize into mexicana (see Fig. S4 in Hufford et al. (2013)). The authors later compare their inferred 9.6% introgression from mexicana into maize to experimental results showing 1-2% (citing our review (Hufford et al. 2012), but presumably referring to results from Ellstrand et al. (2007)), but don’t mention the nearly identical 9.8% estimate from Hufford et al. (2013) using STRUCTURE (Pritchard, Stephens, and Donnelly 2000) (our HapMix estimate was 19.1%). Their result that “there are more introgressed alleles from mexicana to maize than in the opposite direction” also echoes our finding that “gene flow appeared asymmetric, favoring teosinte introgression into maize”.

Fnally, Moreno Letelier et al. (2017) seem to imply that climate data pointing to the existence of refugia in Western Mexico favor a Jalisco origin for maize. But the paper they cite – Hufford et al. (2012) – instead argues “there has been little change in the subspecies’ ranges from the time of domestication to the present”, and at least by my reading makes no reference to specific geographic areas as more likely domestication origins.

References<br /> Durand, Eric Y, Nick Patterson, David Reich, and Montgomery Slatkin. 2011. “Testing for Ancient Admixture Between Closely Related Populations.” Molecular Biology and Evolution 28 (8). Oxford University Press: 2239–52.

Ellstrand, Norman C, Lauren C Garner, Subray Hegde, Roberto Guadagnuolo, and Lesley Blancas. 2007. “Spontaneous Hybridization Between Maize and Teosinte.” Journal of Heredity 98 (2). Oxford University Press: 183–87.

Fonseca, Rute R da, Bruce D Smith, Nathan Wales, Enrico Cappellini, Pontus Skoglund, Matteo Fumagalli, José Alfredo Samaniego, et al. 2015. “The Origin and Evolution of Maize in the Southwestern United States.” Nature Plants 1. Nature Publishing Group: 14003.

Freitas, Fabio Oliveira, Gerhard Bendel, Robin G Allaby, and Terence A Brown. 2003. “DNA from Primitive Maize Landraces and Archaeological Remains: Implications for the Domestication of Maize and Its Expansion into South America.” Journal of Archaeological Science 30 (7). Elsevier: 901–8.

Hufford, Matthew B, Paul Bilinski, Tanja Pyhäjärvi, and Jeffrey Ross-Ibarra. 2012. “Teosinte as a Model System for Population and Ecological Genomics.” Trends in Genetics 28 (12). Elsevier: 606–15.

Hufford, Matthew B, Pesach Lubinksy, Tanja Pyhäjärvi, Michael T Devengenzo, Norman C Ellstrand, and Jeffrey Ross-Ibarra. 2013. “The Genomic Signature of Crop-Wild Introgression in Maize.” PLoS Genetics 9 (5). Public Library of Science: e1003477.

Matsuoka, Yoshihiro, Yves Vigouroux, Major M Goodman, Jesus Sanchez, Edward Buckler, and John Doebley. 2002. “A Single Domestication for Maize Shown by Multilocus Microsatellite Genotyping.” Proceedings of the National Academy of Sciences 99 (9). National Acad Sciences: 6080–4.

Moreno Letelier, Alejandra, Jonas A. Aguirre Liguori, Maud I Tenaillon, Daniel Piñero, Brandon S Gaut, Alejandra Vazquez Lobo, and Luis E Eguiarte. 2017. “Was Maize Domesticated in the Balsas Basin? Complex Patterns of Genetic Divergence, Gene Flow and Ancestral Introgressions Among Zea Subspecies Suggest an Alternative Scenario.” BioRxiv. Cold Spring Harbor Laboratory. doi:10.1101/239707.

Pickrell, Joseph K, and Jonathan K Pritchard. 2012. “Inference of Population Splits and Mixtures from Genome-Wide Allele Frequency Data.” PLoS Genetics 8 (11). Public Library of Science: e1002967.

Price, Alkes L, Arti Tandon, Nick Patterson, Kathleen C Barnes, Nicholas Rafaels, Ingo Ruczinski, Terri H Beaty, Rasika Mathias, David Reich, and Simon Myers. 2009. “Sensitive Detection of Chromosomal Segments of Distinct Ancestry in Admixed Populations.” PLoS Genetics 5 (6). Public Library of Science: e1000519.

Pritchard, Jonathan K, Matthew Stephens, and Peter Donnelly. 2000. “Inference of Population Structure Using Multilocus Genotype Data.” Genetics 155 (2). Genetics Soc America: 945–59.

Ross-Ibarra, Jeffrey, Maud Tenaillon, and Brandon S Gaut. 2009. “Historical Divergence and Gene Flow in the Genus Zea.” Genetics 181 (4). Genetics Soc America: 1399–1413.

Serratos, J Antonio. 1997. Gene Flow Among Maize Landraces, Impoved Maize Varieties, and Teosinte: Implications for Transgenic Maize. CIMMYT.

Van Heerwaarden, Joost, John Doebley, William H Briggs, Jeffrey C Glaubitz, Major M Goodman, Jose de Jesus Sanchez Gonzalez, and Jeffrey Ross-Ibarra. 2011. “Genetic Signals of Origin, Spread, and Introgression in a Large Sample of Maize Landraces.” Proceedings of the National Academy of Sciences 108 (3). National Acad Sciences: 1088–92.

On 2017-12-28 19:16:57, user Larry Matt York wrote:

The preprint entitled, "Trait components of whole plant water use efficiency are defined by unique, environmentally responsive genetic signatures in the model C4 grass Setaria" investigates components of water use efficiency in 189 genotypes of a recombinant inbred line population using a controlled environment automated phenotyping system that controls water content of pots and measures plant size using imagery. Overall, the paper is well-written, methods are largely satisfactory, and conclusions are valid. However, there may be some gaps in explanation of the experimental design and while it's understandable this is new system generating a ton of data, I don't feel enough is being done to use the time series data, which focuses on making daily calculations. Further discussion of the SLOD method would be appreciated as it may account for some time dependence. These are explained more below.

Methods are quoted largely from previous related manuscripts, which is fine with me. However, the number of replicates was not reported. Based on the number of genotypes, 189, and the stated number of individuals, 1138, we can assume there were 3 reps or blocks within which the water treatment levels were randomized along with the genotypes (although there is a remainder when dividing 1138 by 189 - why?). However, stating the number of replicates in the methods would be standard. One sentence is confusing, though, "This strategy effectively…within both treatment blocks." Does this imply only two blocks, one for well watered and one for water limited? In this case, there would only be one replicate of WW and WL, so impossible to do statistical comparisons of the water treatment levels. Personally, I feel some type of schematic of physical layout is always necessary to ensure correct description of design.

Line 171: I believe multiple linear regression is a more common term, multivariate would imply multiple dependent variables but I think you only had mass. Given the confusion you should also specify if fresh and dry weight were estimated simultaneously (multivariate) or separately (multiple). As a side note, you could try models that include the interactions of the predictors, which is the same as multiplying predictors together to create a new term.

Line 224: Maybe I'm missing something, but I don't see how calculations every other day limit replication? Are you saying you use the values for each day as replicates? Is that accurate? Replication should be the statistical replication, which I think is 3. That would seem an odd choice to me, based on my understanding. The explanation of equation 1 partially answers this, but I'm not familiar with that approach. Has it been used elsewhere other than in your own work?

Line 257: Seems like doing analysis for each time point individually is sort of the obvious way, but I'm not sure it leverages the power of the timer series data the most? Are there not more complex models that include time series for QTL analysis? How to more effectively handle time series data will be a major consideration for the future of phenomics.

Lines 293-315: Redundant with methods, which should not be necessary in the Results section. If some of the information is not in methods, put it there and delete from here.

Line 209: The talk of both treatment blocks is confusing, as described earlier for statistical design. I think you have three blocks with water and genotype randomized within (at least I hope so).

Line 328: For discussion, is it possible to update the water weight during the experiment using the biomass estimates?

Line 331: Have you considered non-linear curve fitting? Loess shows it's variable during the life cycle, but also looks like a saturating curve might approximate. Then, the parameter estimates of the curve could be new traits.

Figures. Put legends on the figures, not just in text. For a good plot, you shouldn't need to read the caption.

-Larry M York, Noble Research Institute

On 2017-11-07 01:27:39, user Gustavo Rocha wrote:

The work is not ground-breaking and the methodology is relatively simple, but the results do certainly expand on the knowledge we Brazilian researchers have on our own flora. I was wondering whether it was considered or not to carry out similar studies with other ginger variants; it is known that the major compound of Zingiber officinalis, for instance, is gingerol, for example. Even though these different plants are still named “ginger”, chemical compositions may vary greatly. Under the same trail of thought, I was also wondering whether it would be better to assess MIC and MBC of the whole oil, and not of zerumbone by itself. It was fortunate that this compound was the major one found in the extracted oil, but other flavonoids found in the composition of the whole oil might improve the antimicrobials actions of zerumbone due to synergistic mechanisms. It would have been interesting to see a comparison between zerumbone and the whole oil. Should MBC and MIC be the same, there would be no need to extract and isolate zerumbone should it ever come to be used as a therapeutic agent, saving money and time for the industries. Also, other ginger samples obtained at different seasons of the year could have different compositions of essential oil, which could cause zerumbone to not necessarily be the major compound, and in these circumstances, having the whole oil characterized might be better than just the isolated compound. I also think it is a bit “bold” to claim zerumbone could be used specifically to treat tooth decay diseases; it does work against a strain of bacteria, but it is a long way from zerumbone to be actually used in a formulation on human beings to treat this kind of disease; the potential is certainly there, however, as is with many of our yet to be studied plants.

On 2017-10-11 15:38:59, user Pat Schloss wrote:

The preprint by Robert Edgar sets out to take on the issue of what similarity threshold should be used to delineate bacterial species using partial and full-length 16S rRNA gene sequences. This is well covered territory and I'm not sure that many people would defend to the death the assertion that a 97% cutoff describes species-level taxa. It is helpful to have a discussion about the various threshold people use to bin sequences into OTUs. I think that the broader discussion and the discussion in this specific preprint in favor of a high threshold (e.g. 99.9 or 100%) has come off as being rather dogmatic. My comments below include suggestions for taking a more nuanced view. Ultimately, I think Edgar's and others' goal of pushing the field to a high threshold is an attempt to get a tool to do something it is not capable of doing. Specifically, 16S rRNA gene fragment sequences cannot delineate bacterial species and cannot tell us about phenotype. If scientists have these types of questions there are far more powerful tools at their disposal than debating the appropriate threshold for defining OTUs.

To be transparent, a considerable amount of the material that Edgar uses as a point of contrast to his work are papers that I have published over the past few years and I am the creator of mothur. As of writing this review, I have not been asked to review this manuscript for a journal, but would be happy for any editor to use my comments. Judging from the style of writing, my sense is that this preprint is unlikely to have already been submitted to a journal.

Major comments.

1. The general approach Edgar has taken is to use a variety of metrics to compare the composition of operational taxonomic units (OTUs) generated by database-independent approaches to the taxonomic assignment for those sequences. By identifying the distance that optimizes these thresholds, he arrives at the conclusion that the widely used 97% threshold is too low. Although this approach may be new, this conclusion is not (see the numerous papers published by Tiedje and Konstantinidis. I have significant concerns about his method and do not think Edgar has appropriately described the limitations of his approach. His is a problematic approach because systematicists are inconsistent in how they lump and split strains into bacterial species. From the perspecitve of the 16S rRNA gene, some species are finely split (e.g. Bacillus cereus, subtilis, anthracis) and others are lumped (e.g. Pseudomonas putida). There is broad consensus within microbiology that the 16S rRNA gene is unable to delineate bacterial species or phenotype. Furthermore, a 250 nt region of that gene is even less able to delineate a species. Considering that a minority of bacteria have actually been assigned a species-level classification, using taxonomy as the ground truth for assessing a threshold is problematic. Previous attempts have replaced the DNA-DNA hybridization approach of Stackebrandt and Goebel with genome-scale phylogenies and attempted to correlate that structure with 16S rRNA gene sequence diversity. These caveats as well as a more thorough review of attempts to find a better cutoff are warranted in a revised manuscript.

2. One of the reasons to favor a less restrictive threshold (e.g. 97%) is that there is considerable intragenomic variation in addition to considerable intraspecies variation. Using a higher threshold risks splitting sequences from the same genome into different OTUs. Previously, Edgar has indicated that he thinks this variation is the result of sequencing artifacts or contamination (see bottom of page 9, https://doi.org/10.1101/081... they are not. As an example of intragenomic variation, E. coli ATCC 70096 has 7 copies of the 16S rRNA gene and 6 of these are different from each other in the full length version of the gene. Fortunately, within the V4 region the 7 copies are identical. Alternatively, Staphylococcus aureus ATCC BAA-1718 and Staphylococcus epidermidis ATCC 12228 both have 5 copies of the 16S rRNA gene. Considering the V4 region of these species, 4 of the 5 copies in each genome are identical between the two species. The remaining S. aureus copy is 1 nt different from the other S aureus copies; however the remaining S. epidermidis copy is 1.7 and 2.0% different from the other S. epidermidis and S. aureus copies. The less restrictive threshold would lump the two species together; however, the more restrictive threshold suggested by Edgar would generate 3 OTUs. None of these reflect the biology he claims and the method would split sequences from the same strain into different OTUs. Given the ubiquity of these strains in skin-associated communities, it would make sense to take a more guarded recommendation than to make dogmatic pronouncements about using high thresholds. In the Discussion, Edgar brushes off intraspecies variation concerns and seems to ignore the case where an investigator would like to make an inference regarding the association between the relative abundance of individual OTUs and different treatment groups. Furthermore, he seems to think it would be possible to correct for the inflated alpha diversity metrics obtained by splitting sequences from the same species into different OTUs - the same seems reasonable to say about lower threshold. Although Edgar's Pcs calculations seem to account for intraspecies variation, it does not seem to factor in intrastrain variation.

3. Edgar states "Also, state-of-the-art denoisers have been shown to accurately recover biological sequences from 454 and Illumina amplicon reads (Quince et al., 2009; Callahan et al., 2016; Edgar, 2016) suggesting that the best strategy for amplicon reads is to cluster denoised sequences, in which case the clustering problem is well-modeled by error-free sequences from known species." Again, I would encourage caution in pushing these methods as the strengths and weaknesses of the approaches are not well established. Some of the methods are aggressive in removing rare sequences that may be true sequences, others seem to overfit complicated models, and as described above, others may be splitting 16S rRNA genes from the same genome into different OTUs. Furthermore, the lack of randomness in sequencing errors has not been addressed thoroughly, which creates the possibility that a spurious sequence with sufficient sequencing coverage could be treated as a new OTU rather than be folded into a similar OTU. Finally, these methods have not been well validated for the breadth of sequencing platforms that people are using. I am far more confident in the quality of sequences generated from fully overlapping 250 nt MiSeq reads for the V4 region than I am for single HiSeq reads of the V4 region. There is a trend for people to push the length of the region and throughput at the expense of quality. In short, I agree that a species likely requires a very high threshold for 16S rRNA gene sequences; however, I am not convinced by the papers he has cited that the data accumulated in the literature is of sufficient quality to trust OTUs generated with high thresholds. Combined with the reality of intragenomic variation, I see value in having a more nuanced recommendation.

4. I am happy to receive Edgar's critique regarding the methods used in mothur. I do not see how his section comparing mothur and pairwise alignments or adverse triplets helps make his points about the OTU threshold. I would suggest removing these sections unless he can find a way to tie them in better to his bigger claims - I certainly wouldn't lead off the Discussion with a critique of my use of the Matthew's Correlation Coefficient. That is a weak way to summarize his story. The following two comments will address these specific comments that, again, I do not feel have a direct connection to the goal of the paper.

A. The comparison between NAST-based profile alignments and pairwise alignments has previously been published. We too saw that pairwise alignment had smaller distances than profile alignments (doi: 10.1371/journal.pcbi.1000844 and doi: 10.1371/journal.pone.0008230). By definition, a pairwise alignment optimizes the similarity between the two sequences. In contrast, by using a profile-based alignment where the reference is aligned to the secondary structure of the 16S rRNA molecule, additional information is incorporated. This frequently increases the distance between sequences because it incorporates this extra information. I have also addressed this previously in the literature (doi: 10.1038/ismej.2012.102). I agree that the example Edgar shows is a problem. It is a well-known issue with profile alignments - if there are problems in the reference, there will be problems with the alignment. When using the SILVA reference alignment, such errors can be corrected by fixing the reference alignment. Furthermore, I would point out that an advantage of using a profile alignment like the NAST aligner in mothur is that it is considerably fast compared to a pairwise alignment. Generating pairwise alignments for N sequences would take N times longer than a profile alignment (i.e. profile alignments scale linearly while pairwise alignments scale quadratically). With large datasets pairwise alignments can be prohibitive while it only takes seconds with a profile alignment.

B. Regarding the section, "Comments on the MCCsw metric"... I readily acknowledge that because evolution does not care to conform to a similarity threshold when creating species, there will be "adverse triplets" around any threshold. As I've pointed out above, there are adverse triplets in the case of S. epidermidis V4 sequences and full length E. coli 16S rRNA gene sequences. In fact, this is why we have developed the MCC metric. It evaluates how well an algorithm balances the need to split and lump similar 16S rRNA gene sequences when assigning sequences into a bin. We have used MCC in a fundamentally different method than Edgar has in this paper. We used it assuming that the taxonomic databases are not helpful. He uses it assuming that it is the ground truth. Perhaps there is room for both views, but given the points I raised above, I am happy to stick with my approach over Edgar's.

On 2017-09-14 03:15:20, user Yuri Lazebnik wrote:

Dear Naomi,

Thank you very much for your insightful comment and for your interest in the R-factor.

Please let us reply point by point.

“The idea of classifying hypotheses as supported or refuted by ongoing works, as a means to identify "strongly supported" or "strongly refuted" claims is an interesting one. I would like to see further discussion of how this could be applied.”

Thank you for considering our idea interesting! We will be happy to discuss it.

We would prefer to avoid qualifiers, such as “strongly”, because what is strong evidence for one scientist can be nonsense to another, as many a scientific discussion or a set of opposing reviews would testify.

“Namely, it seems the R-factor is something that should be applied to a specific scientific claim, as opposed to a whole research article. Being able to quickly identify the evidence that supports (green), refutes (red) or relates unclearly (yellow) to a claim, directly from the claim in said literature, could aid comprehension (not to mention discoverability) of the surrounding literature, and highlight claims that are well-supported or lacking in independent replications. Do the authors feel that one paper is sufficiently related to one central claim for application of the R-factor the paper? Alternatively, I would argue that judging the "veracity" of component evidence presented within an article could be more informative.”

We agree completely and tried to emphasize the focus on a claim as a unit of evaluation in our preprint. We will update the preprint to articulate this focus explicitly. Whether an article would have one claim or more depends on the report. In the latter case, applying the R-factor to all claims would be reasonable.

In the examples mentioned in our preprint and in our current research we deal with the main claims because these claims are commonly articulated in the titles of the articles by their authors. This choice minimizes the possibility of misunderstanding what the authors concluded and facilitates the automation of identifying what an article claims.

“Further, limiting these data to the "cited by" literature from that paper could skew the perspective, depending on which article you are viewing the claim in - to understand the overall "veracity" of a claim, it seems the reader would need to navigate back to the first mention of that claim in order to find the longest chain of evidence. Instead, I would be interested to explore the feasibility of a claim-centric (as opposed to paper-centric) count, and to understand whether this is already achieved by existing practises (such as meta-analyses of the literature). Perhaps an alternative approach would be to ensure that meta-analyses that include an article are more clearly visible from that article (e.g. highlighted in a "cited-by" section), and an extension to that would be to link that more recent work to the specific assertions that it relates to in the current article.”

The point about the “trees” of evidence for a claim is indeed excellent! We envision that these trees will be extractable from the R-factor resource and would be one of its most powerful features, enabling the user to grasp quickly the history of the claim and thus the novelty or the lack thereof of the articles referring to it. We are beginning to build a prototype of the “tree viewer”, which we call the Linker: http://bit.do/mock_up (you can zoom in and out, click on the links and nodes, and move around the graph). We keep in mind the century long history of ignoring the claim that the ulcer disease is caused by a bacterium as an example of how a timely reconstruction of the “trees” of evidence could help accelerate discovery.

“I would also be interested in whether the authors' have any thoughts on the reporting bias towards positive results (it may be hard to judge replicability, if failed replications remain in desk drawers), as well as on more nuanced evaluations of related evidence: is some evidence stronger than others? Is it feasible to define a scientific claim, or is it dependent on context/species/other factors?”

Indeed, the R-factor can only reflect what scientists have published, which means that the results that are now in the drawers would not be considered. However, we anticipate that the use of the R-factor and the increasing popularity of preprints can change this. Currently “negative” results stay in the drawers because the value of reporting them is uncertain while the effort of reporting them is substantial. We think that the opportunity to affect the R-factor of a praised paper that everyone in the field knows is wrong and the ease of reporting the results through a preprint service like bioRxiv would help to keep the drawers empty.

We would like to emphasize that the R-factor of a claim does not measure the replicability of the study that reported it, but whether the claim has been confirmed. For example, testing a claim in a different experimental system, which is a common practice, is not a replication by definition and thus the result of such testing would be missed by the replication approaches, but would be included in the R-factor. Likewise, a replication study can test whether the reported result is reproducible, but not whether it is misinterpreted. The R-factor evaluates the chance that a scientific claim, which is an interpretation of the results, is correct, irrespective of whether this claim is based on valid results, a guess, or misunderstanding, which all have their role in science.

“Finally, I would be concerned about applying such a metric to individual researchers. An examination of unintended consequences for such a metric would be useful to discuss.”

We welcome this discussion, but the R-factor of researchers will be derived from the R-factors of their reports by extension. We do not see how this extension can be blocked and question whether it should be blocked. We would suggest that an open and transparent score could be better than a reputation based on grapevine, the membership in the old boys clubs, or on unqualified praise in the media. We envision that once the dust settles, people will see in numbers what they already know intuitively, namely that no one is perfect in their scientific judgment and that some outliers on both sides of the distribution are present. We would also like to emphasize that the R-factor will be but one of the measures used to evaluate scientists and hope that non-quantifiable evaluating criteria will also stay in place.

Thanks again for your insightful comments, which made us think and wish to discuss the issues you raised further.

Best regards,

The Verum team.

On 2017-05-02 14:56:24, user Peter Doshi wrote:

I very much enjoyed reading this proposal. I agree with the need for dramatic improvements in the way journals handle the post-publication modification to articles.

Some general reactions/thoughts:

1. Newspapers vs. Scientific Journals. I find it difficult to pinpoint the key difference between newspaper articles and scientific journals, making me wonder why the simple approach many newspapers have taken to amending articles cannot work for scientific journals, or at least be the basis for the approach journals take? I think the key would be that journals would do a better job at allowing an audit trail. The audit train would make transparent the nature and timing of the changes, make obvious to the reader which version they are viewing at any given time, and add on electronic features such as the ability to compare any two versions a reader wants to compare, showing tracked-changes version between those two versions.

2. What to call it. I agree with the authors that terms like “correction” and, in particular, “retraction” are problematic in that they are perceived to necessarily convey more than the straightforward act of a post-publication change to an article. I agree that the term “amendment” is neutral, but I have trouble with it. My trouble is that one dictionary definition of “amendment” is a “minor change in a document”, whereas you are conceiving this as an overarching term including changes that may be large. My second difficulty is that it suggests adding something to the document, as in an appendix, not necessarily changing the document itself (albeit in ways that are transparent). Did you consider “alteration”, “version”, or “revision”? Journals generally use “revision” to characterize different version of a manuscript in the pre-publication phase. Is there any good reason not to use it post-publication? There can be minor revisions and major revisions, insubstantial, substantial, and complete revisions… so the term has the flexibility I think you’re looking for.

3. In terms of contextualizing the topic, I think something needs to be said describing the old world of print only vs. the new world of print and online. With print, there was a clear ORIGINAL publication. No matter how flawed, once printed on paper, one couldn’t amend the true original in the library stacks, but only issue further statements ABOUT the article (corrections, editorials, notices of concern, retraction NOTICES). With online comes the possibility of editing the original – or at least what appears to be the original (i.e. the version people will see when they attempt to access the publication from the publisher’s website). This added complexity can help reduce the propagation of errors (small or large) that may have existed in a publication.

4. This point is not just stylistic. I think it gets at the heart of whether or not the first published version should means anything special. We are used to thinking it does. But the authors discuss protocols (under “A proposal for the future”) which raises the question of publishing documents that have mostly not undergone editorial processes. So when does the first version start, and what does it represent? Is it the first version that the authors ever drafted or is it the version accepted for publication i.e. the culmination of many revisions pre-publication? Is the idea that once a document is made public (i.e. published), then thereafter, all changes, big or small, will be tracked?

5. What does one do in the event that editors are convinced of an error that needs correcting but the author(s) adamantly refuse? I know the correction notice can carry words to the effect that the editors are fixing what they deem to be an error but if the authors disagree, will the actual article be amended yet still carry the authors names in the byline? That seems highly problematic as it attributes words to them that they do not stand by. The only way I can see to deal with this is to issue, depending on severity of error, a retraction against authors will or, alternatively, a linked ‘expression of concern’ but not change the actual text of the article. Any kind of modification of the original where even one author dissents seems problematic. It would get even more complex if some authors agree with the amendment yet others do not. Do we get version forking with editors to decide which version is served up as “current”?

6. I would avoid introducing protocols into the single-stream publication proposal. Protocols are one of many essential documents involved in research. A research paper another one of those essential documents – but again there are many important documents with research. Protocols often go through their own many revisions and, practically speaking, are different files on one’s computer that may exist simultaneously to a manuscript that is in preparation. It seems to me your proposal should track the versioning of a single document – e.g. the journal-destined research report – possibly pre-, but definitely post-publication in a journal.

7. Stylistically, the concept the authors put forward (of conceptualizing the amendment process as containing two distinct elements of (1) editing articles and (2) publishing a notice about the edit) is important and I think can be made clearer earlier on, perhaps giving it its own heading “The amendment model: publish a notice and edit the article itself”.

8. Also stylistically, I would put more emphasis on the point that in the case of a correction, irrespective of the size of the correction, articles available online will be edited so that by default, the version served up to a reader when they visit the article on the web will be the CURRENT version (reflecting all edits/corrections to date), not the version that appeared when the article was first published (with a notice that a correction exists). I think this is a big break from current practices at many journals.

9. The authors note that every publisher has their own strategy for content delivery, and do not make specific recommendations for or against how to display amendments. But it seems to me that display strategies are part of what has got many people feeling uncomfortable about corrections. Many authors probably would prefer to avoid a big bold all caps notice that THERE HAS BEEN A CORRECTION TO THIS ARTICLE at the top of their published article? I think therefore that a specific recommendation for how the reader should be alerted about the existence of amendments should be made. The authors suggest a difference in display between minor vs. other amendments, but I wonder if there should just be one approach in line with the notion of de-stigmatizing amendments.

10. As far as locations for noting the existence of post-publication amendments, newspapers are doing it below the article, often set apart with italicized text. Where will this flagging occur in scholarly publishing? What about proposing certain article meta-data become standard. Just the way Acknowledgements and COI declarations are now fairly standard elements of articles, could a “Current version: X (version history)” line become standard, with a link to a separate document that contains the explanation of the corrections? Or perhaps all articles should contain a "Version history (up to [YYYYMMDD]): On YYYYMMDD, we fixed a typo. On YYYYMMDD, we removed an author for reasons described here (DOI-to-editorial-note-about-research-misconduct)..."

On 2017-03-29 05:37:38, user M Hooper wrote:

Excellent and radical suggestion about amendments. For me, it raised three suggestions and questions:

1. If I see an article that has been subject to a wholesale amendment, I will wonder why. I don’t think it’s possible to remove the stigma of amendments without providing the reasons for the amendment. I think reasons could be provided immediately below the “Declaration”.

The article convinces me that drawing a distinction between (i) amendments, and (ii) the reasons for them, will be good for the culture of making amendments. Consequently, it will be good for the accuracy of the academic record more broadly, and good for the community, practitioners, and policy makers. But it’s not so obvious to me that such a sharp distinction will be good for ethics. A reader deserves to know if the reason for some amendment is that the authors fabricated data. Even admitting the many faults of the term “retraction”, it has sometimes played this helpful role, and it has sometimes been a good stick for ethics to brandish.

One of the problems your suggestion solves is that the term “retraction” has harmed innocent-authors, and it has deterred innocent-authors from doing good things (like correcting the record). But “retraction” has also helped stigmatise some very bad practices, which is a nice effect.

The reason “retraction” is a bad term is that it applies to both cases involving fault and cases involving no-fault. The most obvious solution is to just say we need two terms instead of one. You didn’t choose that option, and I think you were wise not to. Choosing a neutral umbrella term has all the benefits you describe.

Nonetheless, *something* has to do the job of separating one from the other - cases of misconduct from causes involving no fault. As I said, I think this should be done by providing the reason *immediately below* the declaration of amendment.

1. Will it be possible for an author of a paper to lose her authorship in a later amendment? Suppose I authored the original paper, but have since refused to be involved in substantial amendments. Moreover, suppose my original contribution was to the sections of the paper that have since been amended such that my original contribution is now eliminated from the current version. Should I still be an author?

2. If amendments become acceptable and normal, journals will have to decide the kinds of amendments that they will allow. This will be tricky if authors want to make amendments for minor things. What if I just change my mind about something minor in the discussion, for example? What if I have since thought of a more elegant way to phrase my introduction? What if critics, in subsequent published works, have accused me of treating the literature carelessly; may I now just amend my literature review to make their criticisms false? (I imagine these issues will more problematic in the humanities, but could well be wrong.)<br /> Anyway, great paper.

On 2017-05-02 14:16:16, user Peter Civáň wrote:

Dear Jae and Michael,

Thanks for this interesting paper! I’m glad the debate goes on and people are trying to make sense out of the contradictions.

You made several good points here and I totally agree that the genomic window size of the CLDGRs is critical for clustering patterns that are based on genetic distance.

However, the situation is not as simple as “the smaller genomic windows provide more correct genealogy”. Surely, we know that sh4 and prog1 coding sequences are fixed in all cultivated rice, so if we focus on a genomic window narrow enough (e.g. just the coding sequence, or in an extreme case just the FNP), we will inevitably recover a monophyletic O. sativa group (or better say paraphyletic O. rufipogon). The question is, how far from the gene can we go and collect genealogically informative signal (undisturbed by recombination)? Neither I nor you have answered this question.

Consider the situation on the attached figure. Keep in mind that the “domestication gene” can be a very ancient allelic variant that emerged in wild populations long before the domestication, and also keep in mind that wild rice populations are quite dynamic (in terms<br /> of recombination and glacial-interglacial movement). Then we can imagine a situation where we have multiple combinations of alleles (Xa–Xe) with different genetic backgrounds within the wild population. Let’s imagine two independent domestication events, leading to two cultigens (I and II). The allele Xd is selected in both cases and fixed in both cultigens. If we focus on the narrow window, we recover monophyly of the cultigens. If we focus on the<br /> large window, we recover polyphyletic cultigens. In this particular cartoon, the latter would be correct.

I cannot be sure that this is indeed the case of indica and japonica, because I did not identify the entire haplotypes with their recombination points (the quality of the data just doesn’t allow that). I think both of us may be over-interpreting the selective sweep analysis a bit. Maybe we need to focus on other kinds of data and methods (your recent coalescence analysis is one example). Maybe our paper (Civan and Brown. Origin<br /> of rice (Oryza sativa L.) domestication genes. Genet Resour Crop Evol. In press) will bring some new insights, and hopefully, there will be more stuff coming from me and Terry soon.

https://uploads.disquscdn.c...

On 2017-04-13 02:21:17, user Dave Baltrus wrote:

As the "big data revolution" progresses and biology is confronted with ever more complicated patterns to interpret, evolutionary terms are being increasingly invoked to explain perceived patterns. "Frequency dependence" is one of these terms. The purpose of this manuscript from Brisson is to begin to clarify when it is/is not appropriate to use the term "negative frequency dependent selection (NFDS)" in the context of evolutionary explanations. Brisson does a great job of laying out definitions and explanations for use of this term over the last century or so, and does so while describing how such selection regimes could help to explain the amount of diversity we see in the world. I'm a proponent of clearly laying out the case for when nuanced evolutionary terms are applied inappropriately, and Brisson does a good job of describing instances where patterns may suggest negative frequency dependent selection but where this specific evolutionary model doesn't apply. He makes this case throughout the manuscript and does so in a way that is clear and concise. I think this manuscript could go a long way towards clearing up some confusion in the literature if the right people see it at the right time.

I have no major qualms with this preprint, it's laid out and written quite well. However, I do think that it would make the case slightly more clear if, in cases where the pattern suggest NFDS falsely, if some examples were imagined that would allow the patterns to fall under the purview of NFDS. For example...what would need to happen to make the "killing the winner" scenario actually fall under NFDS? I'm not sure if there is actually a clear way to do this or if it would muddle things, but if possible it would be good to include additions that could make these situations fall under NFDS as counterpoints.

I really enjoyed this preprint both for its subject matter and clarity, and I hope to see it well received across communities.

On 2017-04-11 15:14:46, user Rahul Nahar wrote:

We have seen such a phenomenon even on Hiseq2500 which also uses bridge amplification and thus I think it might be present on Nextseq 500 as well though may be to a slightly lower extent than Hiseq4000.

On 2017-03-07 13:14:22, user Pat Schloss wrote:

The preprint from Herren and McMahon describes a new metric - cohesion - to describe the overall connectedness within a community using temporal data. I was excited to see this preprint because I am familiar with McMahon's long history of developing rich time series data for microbial communities in Wisconsin lakes. I also have a lot of my own time series data from humans and mice where we struggle to incorporate time into the analysis to understand the interactions between bacterial populations.

A significant struggle in analyzing time course community data is the ability to synthesize observations for large numbers of taxa over time. Many of the existing methods people use attempt to adapt methods from cross sectional studies. For example, a study may sample a large number of lakes, people, soils, etc and characterize their microbial communities. They'll then calculate correlations across those samples based on the relative abundance of the populations. Alternatively, they'll used presence/absence data to generate co-occurrence matrices. The problem with these studies is that the next step is to often infer something about the interactions between the populations - even if the populations would never possibly co-occur. Herren and McMahon's efforts to study the connectedness of individual populations and their cohesion is very welcome because it has the potential to get us closer to describing the actual interactions between populations.

To briefly summarize the approach, the method starts by calculating the Pearson correlation between all pairs of populations across time and then discounts the correlation that would be expected if all interactions were random. This is important because of the compositional nature of the data and the effects of different population sizes. Next, the method calculates the average positive and negative corrected correlation for each population. These become the positive and negative connectedness values for each population. Finally the positive and negative cohesion values for each community is calculated by determining the sum of the product of the connectedness value and the relative abundance for that population.

The following are general critiques and questions, which I appreciate may be beyond the scope of the current manuscript (note, I am not a reviewer for the manuscript at a journal):

1. To develop the cohesion metric for a community, the authors sum over all of the populations in the community. This raised three questions for me. First, independent of the relative abundances in each sample, is the *number* of positive and negative connections for each population relevant? It might be worthwhile exploring which populations have more positive/negative connections than others. What does that distribution look like? Second, does the connectedness metric value itself have any value? What are the populations that are highly connected with other populations. Finally, the method generates a cohesion value for each time point. If I think of Lake Mendota as a community that was sampled over time, it would be interesting to know whether it has been more cohesive than Lake Monona over the 19 years of sampling. Thinking of my own work, I would be interested in knowing whether mice that are more susceptible to C. difficile colonization are less cohesive than those that are resistant. Again, this would require a composite score, not individual scores for each time point.

2. Continuing on my self-serving thread, I wonder how sensitive the method is to the time interval between samples and the number of samples. In my experiments I may have 20 daily samples from a mouse - is this sufficient? What if we miss a day - how will having a jump between points affect the metrics? As the authors state, the Lake Mendota dataset has 293 samples collected over 19 years (e.g. 1.3 samples/month). This is a very unique dataset that is unlikely to be repeated elsewhere. What if we were to get more frequent samples? What if they were more spaced out? What if we only had a year's worth of data? It would be interesting to see the authors describe how their cohesion values change when they subset the dataset to simulate more realistic sampling schemes.

3. A significant challenge in developing these types of metrics is not knowing what the true value of the metric is in nature. I appreciate Herren and McMahon's effort to validate the metrics by comparing their results to count data and to explaining the variation in Bray-Curtis distances. The manuscript reads almost like they want their method to recapitulate what is seen with those distances. But we already have Bray-Curtis distances, if that's the goal, then why do we need the cohesion metric? It would be interesting to see the authors simulate data from communities with varying levels of cohesion and abundance to see that the method gets back the expected cohesion value. Perhaps it would be possible to generate an ODE-based model to generate the data instead of variance/covariance data. There is one simulation described at the end of the Results (L300); however, it is unclear whether the lack of a meaningful R-squared value was the expected result or not.

4. Throughout the manuscript, the authors make use of parametric statistics such as Pearson's correlation coefficients and the arithmetic mean. Given that relative abundance data are generally not normally distributed and are likely zero-inflated, I wonder why the authors made these choices. I would encourage the authors to instead use Spearman correlation coefficients and median values. Related to this point, a concern with using these correlation coefficients is the problem of double zeros where two populations may be absent from the same communities. These will appear to be more correlated with each other than they really are, which is why we don't use these metrics for community comparison - we use things like Bray-Curtis. I wonder whether subtracting the null model counteracts the problem of double zeroes.

5. The authors translate their count data into relative abundance data before calculating their correlation and Bray-Curtis values. I wonder if the authors subsampled or rarefied their data to a common number of individuals. Both of these metrics are sensitive to uneven sampling. Even if the counts are converted to relative abundances, this would not remove the effects. For example, if one sample has 1000 individuals and another has 100, the limit of detection on the first would be 10-fold higher than the second. There may be populations that represent 0.5% of both communities that would not be seen in the second. If they haven't already, I would encourage the authors to subsample their dataset to a common number of individuals.

6. The "Description of datasets" section of the Methods describes the various datasets in general terms, but what is the nature of the data? How were the phytoplankton counted? How many individuals were sampled from each sample?

7. It would be great to have the code that was used made publicly available on GitHub

8. The authors present the material in a format that I have not previously seen in the microbial ecology literature (i.e. ISMEJ where this appears to be destined for review). The authors flip back and forth between presenting a different stage of the algorithm and validating that step. I think this is a bit more aligned with how one would present the material in a talk than in a paper. I've seen similar methods development described before where there might be a methods section on algorithm development and then the results section would test the assumptions and performance of the algorithm. I'm curious to see whether this structure persists through the editorial process.

On 2017-02-23 21:54:41, user Dave Baltrus wrote:

(Stepping up to break the ice and comment formally here instead of just on twitter)

1. I think the Ben Schwessinger experience described here (https://blushgreengrassataf... is worth a mention for a couple of different reasons. It's the first time that I can recall that a journal had to step up and actually deal with a situation where scooping by preprint (or because of preprint) may have occurred. As such the policy at PLoS has been refined. When things change, there are always the uneasy situations like this that force people to make difficult (and sometimes wrong) decisions

2. I think it's also worthwhile to mention sites like PubPeer. Public reviews and comments on preprints are part of overlapping discussions but aren't necessarily the same discussion. Feels like there's something to be said about that although I'm not sure what that is right now.

3. My whole take on "but it's not peer reviewed" is that those that will be reading the preprints in order to cite them are well qualified as reviewers themselves. If you don't trust the paper or don't like it, don't cite it. If you read through the paper and don't see fault with experiments, why not cite it? We all have blindspots but it's not like we don't review papers all the time and critique them anyway even if they've been through peer review.

4. I think we should make a greater effort to write positive comments on preprints and not just use this as a forum for review. Positive comments can help those who maybe aren't in the literature figure out which preprints are great and which have holes (by their lack of positive comments). I see this as important if preprints are going to be written about by the popular press and digested by those who aren't necessarily experts. We as experts need to endorse good papers just as we will trash the bad papers.

5. I had the first preprint in biorXiv under Microbiology, why are you taking this achievment away from me Schloss?

6. Looping back on number 4...if we are going to be the ones reviewing grants and papers and we see a preprint cited, we can actually review this work. Some are going to use it to get around page limits but, like you point out, we as scientists should be pretty good at snuffing shoddy and rushed work out and so that this could also theoretically backfire on the person trying an end run on page limits. Sure it may give you more space to write, but if you do a terrible job you may otherwise poison the impression of a grant reviewer that might otherwise like your grant. I'm tired of having to see (in press) or (in prep) when work is cited in a paper or grant. If it's an important enough story for the grant, I want to be able to read the story myself and preprints allow this.

7. There are different costs and benefits for preprints depending on the field you are in and the point in your career. I don't know that we've figured this out at all yet or if there is a great answer across the board. It seems as though the pop gen fields have taken to preprints more than other fields, but in my experience evolutionary biology in general tends to be less "scoopy" or "eat their young" than other fields. I'd like the world to exist where everyone can freely post preprints and get credit, but I can see this going horribly wrong in fields that are much more competitive and potentially containing more selfish PIs. I mean this not as a positive or negative commentary on different fields, but it's quite obvious to me that some fields are more cutthroat than others for a variety of reasons and the cost/benefit analysis for preprints in these fields will be different.

On 2017-01-30 20:23:17, user Alexandro Rodriguez-Rojas wrote:

This is a nice idea. However, the authors say 'We assume that interactions between the strains are solely due to resource competition'. I think that competition is often more complex than resources speed use. Let's imagine a few different situations. What would happen if that one strain is more susceptible to metabolic wastes, acidification of the medium or has an altered quorum sensing? What if the growth depends on a public good such as siderophores? In this last example the strain that growths worst (alone), when is co-cultured with the one that growths better (also alone), would cheat by stealing the public good that is unable to produce, outcompeting its peer. What if one of the microbes produce a toxin, an antibiotic or a phage? Validation of the model in this kind of scenarios would be a great plus to this new technique. I hope this helps and I'm looking forward to seeing that the model is independent of more complex interactions or it may be even useful to unveil them.

On 2017-01-04 19:35:12, user JN wrote:

Nice paper--I like the valacyclovir question/angle on a familiar theme. The paper can trace its scientific lineage to the work of Montaner, Lima and Williams and others work in the 00's. Although younger and perhaps unaware of "ancient history", the authors could consider acknowledging earlier work which in turn was built on Anderson and May's early work on HIV and AIDS epidemiologic modeling. When we did our Lancet paper in 2008 my only regret is not discussing how it was a logical outcome of two decades of research/modelling around HIV natural history and the potential for treatment. It may have made it less shocking to the HIV community--the fierce and, in some settings ongoing resistance, to the idea that treatment has an important role in both keeping people healthy and preventing HIV transmission has directly translated into delayed implementation of test and treat services for people living with HIV--see www.hivpolicywatch.org for latest policy status. This is reflected in many models that restrict treatment while focusing on scaling prevention--interesting idea but not realistic to not prioritize treating people with HIV and then layering on prevention modalities.

Not sure where the 70% ART coverage comes from but it is important to think carefully about the impact of ART--many models downgrade ART efficacy or effectiveness by loading in pessimistic reduction in transmission risk and retention parameters that are not supported by the latest population based studies from Botswana and other countries. Most major models out there are not that clear about the definitions of coverage and/or the actual risk reduction parameters. I suspect that this will continue to be a battleground as some modelers prefer pessimistic assumptions for ART (but not PrEP!) and others choose well-performing program data.

The good news is that the models will continue to help us think about the optimal strategy to both keep the 37M people alive while controlling and elimination the epidemic in many settings....

On 2016-12-27 23:16:53, user Peter Ellis wrote:

Another comment that occurs to me at this point - when you were looking at the "co-amplified" X genes for signatures of selection, how did you define co-amplification? If I am reading the paper right, it looks like you looked specifically at the direct homologues of the Y-linked ampliconic genes, i.e. Sstx, Slx, Slxl1 and Srsx.

In looking for signatures of selection around X-linked genes, I think it is imperative to first consider which X genes are likely to be affected by the conflict. The Slx/Sly conflict seems to be mediated by varying the strength of PSCR, i.e. a GLOBAL regulation of sex chromosome expression in spermatids. The prediction therefore is that if Sly-mediated repression increases, EVERY dosage-sensitive, spermatid-expressed gene on the X and Y will come under selection to increase its activity.

This is what we saw in our 2011 paper - the proliferation of Slx and Sly in the Palaearctic clade is associated with an increase in copy number at almost all the X-linked ampliconic genes, not just the direct homologues of the Y-linked ampliconic genes. We also showed that the net transcription level of the X amplicons stayed approximately constant across species despite an increase in copy number. We interpreted this as showing that the X linked genes are being selected to maintain functionality despite increasing postmeiotic repression.

In your data we would therefore predict a signature of selection not just at the specific homologues of Y-linked ampliconic genes, but at many of the other X-ampliconic genes. This would confound attempts to detect selection by comparing the X-Y homologous genes to the rest of the chromosome.

Similarly, a selective signature from the conflict may not be restricted to ampliconic genes. All we can predict is that as Sly repression increases, X- and Y-linked genes are forced to respond _in some way_. That does not only mean gene amplification. Any given gene could respond by an increase in copy number (more copies) - but it could also respond with an increase in promoter strength (more transcripts per copy), improved translation efficiency (more protein per mRNA molecule) or an increase in protein function (more functional activity per protein molecule).

For example, there is a single Zfy gene in rat. In mouse this has become duplicated to give Zfy1 and Zfy2 (gene copy number change), Zfy2 has acquired a new spermatid-specific promoter (increased transcription from one gene copy), and Zfy2 has additionally become a stronger transcriptional activator (increased function per mRNA transcript). I can't prove (yet) that this is linked to the Slx/Sly conflict, but it looks to me like it may be.

Whatever the form of response, if it was driven by selection, it should in principle leave some signature around many of the spermatid-expressed genes on the X. How does the analysis in figure S4 change if you look at the DNA surrounding all the spermatid-expressed genes on the X? Given that there are rather a lot of them(!) it may be that they all run into one and you won't be able to find a specific loss of diversity around each gene, just a loss of diversity across the X as a whole.

If you do try this, you may need to treat spermatid-specific genes separately from genes expressed more widely. Widely-expressed genes will be constrained by the fact that increasing their activity in spermatids may also increase their expression in other cell types, however spermatid-specific genes will be freer to respond to the conflict. I think this is what's going on in Larson et al 2016a when they report that some genes show transcriptional alteration in pre-meiotic spermatogonia in the different species and F1 hybrids. I think what may have happened here is that some widely-expressed X-linked genes have been selected for stronger promoter activity to overcome Sly-mediated repression in spermatids. This keeps overall transcription reasonably constant in spermatids, but now leaves them overdosed in the spermatogonia.

And finally (!)<br /> The potential selective signature of the Slx/Sly conflict may not be restricted to the sex chromosomes - there are also a few ampliconic autosomal loci that appear to be regulated by Slx and Sly. These include Speer genes (Cocquet et al 2009, 2012) and a block of genes on chromosome 14 (Larson et al 2016a, fig 4C). It might be that a look at these areas would show something interesting. Possibly it would even be easier to see a signature of selection here, since so far as I'm aware these are discrete blocks of genes rather than chromosome-wide regulatory effects.

On 2016-12-23 13:38:50, user Peter Ellis wrote:

What an absolutely fascinating paper.

I have a few questions and comments - some of them likely quite naive as statistical genetics is not my area!

********************************

Lines 167-176:<br /> You counted gene copies directly and confirmed the earlier finding that musculus has much higher copy numbers of Slx and Sly relative to domesticus (Fig. 5). However you also showed that the proportion of the red/blue/yellow amplicons is the same in each species (Fig. S3A), and that the domesticus Yq is if anything slightly larger on average that musculus Yq (Fig. S3B).

How can these observations be squared with each other? If domesticus Yq is larger than musculus Yq, and they both have same proportion of the red amplicon containing Sly - how can musculus have a larger copy number of Sly? I'm not sure what these different measurements are telling us.

********************************

Lines 184-190: <br /> You looked for a signal of selection at the co-amplified loci on the X, but observed no reduction in genetic diversity surrounding the X ampliconic regions.

Given that one mode (most likely mode?) of expansion of these clusters is by nonallelic homologous recombination, does this affect the calculation? It seems plausible that it would, since the same effective mutation - expansion of the cluster - can occur recurrently on different haplotypes and also spread horizontally between haplotypes by recombination within the gene cluster. This doesn't apply to males, and so the males would have a much greater reduction in diversity associated with selection on the amplicons.

********************************

Lines 194-199:<br /> You find that for X and autosomal genes, there is more variation between tissues and less between species, compared to the Y chromosome. e.g. PC1 and PC2 for X+A genes represent tissue specificity whereas PC2 for Y genes represents species differences.

To what extent is this due to Y genes being almost exclusively testis specific? When genes are expressed in multiple tissues, there's room for a lot of complexity, which will show up in the PCA analysis. When genes are expressed in only one tissue, one principle component is sufficient to encapsulate that fact, and so PC2 will necessarily relate to something else. <br /> What happens if you compare Y-linked genes to testis-specific (or spermatid-specific) genes on the X and autosomes? Does the Y still show up as having increased expression divergence between species? I suspect it will, but it would be nice to check.

********************************

Lines 217 onwards:<br /> Yes, there's definitely more complexity here and it's not just a linear function of Slx:Sly ratio. In our original paper (Cocquet et al 2012) and the preceding shSLX knockdown paper, we found that knocking down Slx on its own didn't really affect X gene expression as a whole, although there was a sex ratio skew. It may be that there are thresholding effects - e.g. as long as you have "enough" Sly around to prevent Slx from accessing chromatin, then adding more Sly beyond that point won't affect X gene expression any more.

Deficiency in the multicopy Sycp3-like X-linked genes Slx and Slxl1 causes major defects in spermatid differentiation.<br /> Cocquet J, Ellis PJ, Yamauchi Y, Riel JM, Karacs TP, Rattigan A, Ojarikre OA, Affara NA, Ward MA, Burgoyne PS.<br /> Mol Biol Cell. 2010 Oct 15;21(20):3497-505.

Julie has also recently shown that SSTY proteins interact with all the Slx/Slxl1/Sly family and may affect their ability to enter the nucleus - so not only do Slx/Slxl1/Sly likely compete for binding to particular chromatin sites, they may also compete for some factor that transports them into the nucleus.

SSTY proteins co-localize with the post-meiotic sex chromatin and interact with regulators of its expression.<br /> Comptour A, Moretti C, Serrentino ME, Auer J, Ialy-Radio C, Ward MA, Touré A, Vaiman D, Cocquet J.<br /> FEBS J. 2014 Mar;281(6):1571-84. doi: 10.1111/febs.12724.

********************************

Lines 248-251 and Figure 7B:<br /> What is the gene copy number in the lines used for the DXD and MXM crosses? Given that you've now documented extensive variability within as well as between species, I think it would be useful to include this information in the figure.

What was the denominator for the Slx/y family here? Did you count both Slx and Slxl1, or just Slx? Does the interpretation change if you use just one or the other? It's not clear to me that we yet know whether Sly is directly competing with Slx, Slxl1 or both.

It might also be interesting to normalise the activity for the gene copy number in each case. Slx and Sly have a fundamental difference in that (if the underlying hypothesis is true that Slx promotes expression from the sex chromosomes and Sly represses it), Slx has a positive feedback on itself, while Sly has a negative feedback on itself.

Thus a comparatively small change in Slx copy number could have a disproportionately large effect, while a large change in Sly copy number will be "buffered" by the negative feedback. In the 2/3 Yq deletion mice, expression of Yq genes drops by less than 50%, since each copy is transcribed at an intrinsically higher level. I suspect this may be a contributory factor to the sheer size of the Yq amplicons - a small amplification on the X triggers a much greater degree of amplification on the Y, because the Y has to fight through the fog of its own negative feedback.

********************************

Lines 308-310<br /> Do you mean to say that you cannot detect a signature of sex ratio skewing, or that you can definitively rule out sex ratio skewing? In a conflict scenario such as the one hypothesised, then the historical situation could well be one of constant change - sometimes the X has the upper hand and the sex ratio is female biased, sometimes the other way round. Would that not obscure the signature of any particular episode of skewing?

********************************

Lines 370-371<br /> You say, "Sex-ratio distortion has been observed in the offspring of males with X:Y copy-number mismatch in some experiments (Cocquet et al., 2009; Case et al., 2015) but not in others (Turner et al., 2012; Albrechtová et al., 2012)."

The Turner paper did show some effects in the predicted direction. From their Table 2:<br /> Domesticus offspring = 31/59 = 52.5% female<br /> Hybrid domesticus (with domesticus Y ) = 58/105 = 55.2% female<br /> Hybrid musculus (with musculus Y) = 88/206 = 42.7% female<br /> Musculus = 42/76 = 55.3% female

With low numbers in each group, these differences are not all significant (power calculation for a 10% skew requires 400 in each group for 80% power), but I certainly don't think it can be ruled out, particularly since they didn't explicitly break down the groups based on the proportion of the X chromosome coming from the introgressed background in each case, i.e. their hybrid groups may include animals where only autosomal loci have ingressed and the sex chromosomes are congruent. Indeed, their own conclusion was that "the trend in our data is consistent with a sex ratio distorter on the musculus Y which is effective only on a partially domesticus background"

The Albrechtova paper made no measurements of sex ratio and I'm not sure why you're citing it here. They looked at sperm counts and sperm velocity in an area with an introgressed Y which is already known to affect sex ratio, and found that,

"In the section of the HMHZ we studied, the YMUS chromosome has introgressed across the zone in apparent disregard of Haldane's rule and this introgression is associated with a shift in the sex ratio in favour of males [6]. In the current study, we find that in the presence of the invading Y chromosome the most extreme reduction of SC in hybrid individuals is more than rescued, to the extent that an apparently domesticus male with the introgressed YMUS chromosome is expected to have higher SC than one with its consubspecific Y."

i.e. introgression of the musculus Y is favoured because it rescues adverse sperm phenotypes in hybrid males. Their reference 6 is to the following paper, which is relevant and should be cited in your paper.

Macholán M., Baird S. J. E., Munclinger P., Dufková P., Bímová B., Piálek J. 2008. Genetic conflict outweighs heterogametic incompatibility in the mouse hybrid zone? BMC Evol. Biol. 8, 271–284

********************************

Lines 378-383<br /> Here, there are two independent deletions of ~2/3 of Yq that should be cited - the one from Conway et al that you already have, which arose on an RIII background, and also one from Josefa Styrna that arose on a B10.BR background. The paper from Macholán et al is also probably best mentioned here as a "real world" example of sex ratio alteration associated with Y chromosome introgression.

Influence of partial deletion of the Y chromosome on mouse sperm phenotype.<br /> Styrna J, Klag J, Moriwaki K.<br /> J Reprod Fertil. 1991 May;92(1):187-95.

Regarding the paper by Fischer et al on C57Bl/6JBomTac, all they say in the paper is that there are no reports of sperm abnormalities or sex ratio skewing in this line. So far as I'm aware, nobody's looked yet, so this is certainly worth checking. I don't think we can assume anything from the current absence of evidence, though.

On 2016-09-28 08:27:01, user Gordana Rasic wrote:

Gordana Rašić<br /> In the spirit of open science, we are sharing the reviewers' comments on this paper and our responses.

Enjoy!

Reviewer #1: This is a straight forward, clear presentation. It addresses and important issue and the conclusions are supported by the data. Thus I have no problem recommending it be published.

One sentence, however, confused me. line 255-258. I do not believe the cited paper sowed Aaa and Aaf are "one genetic cluster". More accurately, that sentence could read: At least in one locality in Africa (Senegal) the two established subspecies Aaa and Aaf are integrating with no sign of genetic subdivision when brought into sympatry, so it is not surprising....."

 We thank the reviewer for the overall positive assessment of our work. We agree that the stated sentence is confusing (line 255-258), and we have changed it following the reviewer’s suggestion (line 265-269).

Might also cite Tsuda et al. Japan Society of Medical Entomology and Zoology 54:73 (2003).

 As per reviewer’s recommendation, we now cite the paper by Tsuda et al. (line 236-238).

Reviewer #2: This manuscript investigates to what extent worldwide disseminated domestic Ae. aegypti specimens morphologically identified as the pale variety queenslandensis and the type form from Australia and Singapore are reproductively isolated ("how freely they interbreed"). A total of 74 sympatric pale and type Ae. aegypti were genotyped for a 1170 bp-long mitochondrial sequence and 16,569 nuclear SNPs. <br /> Although I am not an expert on Aedes taxonomy, I have identified a few issues that should be better explained/corrected before this manuscript is considered as publishable material.

1. Published references are cited in a very loose manner. Sometimes even with disregard to their original meaning (i.e. Powell & Tabachnick 2013).

 While we appreciate reviewer’s critical assessment of our work, we cannot agree with this conclusion and are not able to address it without a concrete example of what is being disregarded.

Our citation of the e.g. Powell & Tabachnick paper (2013) refers to their statement regarding McClelland’s 1967 conclusion that the classical subdivision within Aedes aegypti is a gross oversimplification and that “...Aedes aegypti cannot be split into definite interspecific entities...” Powell & Tabachnick (2013) conclude on page 16, paragraph 1: “...In the 45 years since, this advice has often been ignored, even in recent times”.

Our reference (underlined) to Powell & Tabachnick conclusion (above) states: <br /> ...“McClelland [7] suggested that subdivision into forms seems oversimplistic and should be abandoned unless correlation between genetic and color variation can be demonstrated [7]. His recommendations have been largely disregarded [9]) despite the fact that multiple genetic marker systems (allozymes, microsatellites, nuclear and mitochondrial SNPs) have failed to find a clear differentiation between forms and markers [10][11][12].” (page 4, line 82-87).

We have now changed this sentence to: “In their latest review of Ae. aegypti history, Powell and Tabachnick [9] point out that McClelland’s recommendations have often been ignored for the past 45 years...”, to further clarify the context for this citation (line 88-89).

1. Chan et al (2014) did not consider Ae. aegypti aegypti and Ae. aegypti queenslandensis as separate entities.

 This is correct and we did not attempt to argue that Chan et al. (2014) considered them as separate entities. We said that their finding of a relatively high mitochondrial divergence between the two forms “..., although lower than a commonly adopted threshold of 3% for species delineation in insects [14], suggests that the two forms may not freely interbreed. ” (line 94-97). Hence, we decided to further test this hypothesis.

1. No significant differences in oral infection of DENV-2 between pale (Ae. aegypti queenslandensis) and dark (Ae. aegypti aegypti) were ever observed (Wasinpiyamongkol et al. 2003).

 That is correct, but nowhere in the text do we argue to the contrary. In fact, the findings of Wasinpiyamongkol et al. (2003) further support our conclusions and we have now included this citation (line 268-269).

1. The taxonomy of the variation seen within Ae. aegypti, as presented, is flawed and incomplete.<br /> I feel that the scientific issue selected to be addressed has not been properly defined or characterized.

 It is little hard to respond to this. Our work was not intended to present a taxonomic description of phenotypic variation, and we followed the well-established color/scalling criteria of Mattingly and McClelland (described in the text). The focus of our work was to test if the two forms are genetically distinct using the mtDNA and nuclear SNP variation.

Reviewer #3: An interesting and useful contribution to understanding of Aedes aegypti population biology / genetics, and the date presented further allay any potential concerns that deployment of Wolbachia or RIDL-based control may be stymied by mating barriers, at least in Asia or Latin America. The study seems well conducted and methodologically sound.

 We thank the reviewer for the overall positive assessment of our work.

85 'his recommendations have been largely disregarded' - I don't think this is really true - it is not a widely held view among contemporary mosquito biologists that Ae. aegypti outside of Africa should be divided into forms based on colour or exist as reproductively isolated sub-populations, especially given several recent population genetic papers providing evidence to the contrary. The Chen paper seems an exception in this respect; perhaps the anomalous results in that paper may have been a result of collections conducted over a period of a number of years.

 Please see above our explanation of this statement (citation) and the rationale for further testing of the Chan et al (2014) findings.

It might be useful in intro or discussion to give a little more information on the putative queenslandensis form, e.g. Mediterranean populations were recorded as belonging to this light form prior to their eradication, and possible behavioural / oviposition differences.

 As per reviewer’s recommendations, we have added more information on the Mediterranean light form in the Introduction (line 81-84).

268-9 do the light colour variants ever arise in the lab populations used for release? (which will have been outcrossed with wild material).

 The light color individuals indeed show up (albeit very rarely) in our laboratory populations originating from the release areas. We have now added this statement to Discussion (line 239-242).

Table 1 - suggest move to online.

 Done.

Minor<br /> 68 replace urged with e.g. caused

 Replaced with “motivated” (line 68).

79 Ae.

 Corrected (line 79).

81 aegypty

 Corrected (line 81).

201 Moore not More; refs 10 & 35 same

 Corrected (line 204) and removed a duplicate reference (ref. 35).

282 aegupti

 Corrected (line 292).

references e.g. some paper titles in title case, some lowercase

 Corrected throughout.

End of comments.

On 2016-07-15 09:05:13, user Adam Eyre-Walker wrote:

We have known since Seglen’s seminal paper in the 1990s that the distribution of the number of citations for papers published in a journal is highly skewed, that there is considerable overlap in the citation distribution between journals and that there is a poor correlation between the number of citations a paper receives and the journal IF. These observations have been used to suggest that the journal IF should not be used to assess the merit or quality of a particular paper. Usually it is suggested that either the paper is read or that article level metrics are used to assess the merit or quality.

Reading the paper may be considered the gold standard but it is impractical in many circumstances in which one is interested in assessing merit; if for example, you have 100 CVs to look through, you can’t possible read all their papers, or even the best three. Even the papers of those on the shortlist may be too many and you may not be an expert in the field under consideration.

As for citations, as all researchers know articles are cited for all sorts of reasons, often incorrectly. The only quantitative analysis I know of, concluded that the vast majority of the variation in the number of citations a paper receives is just noise, and has nothing to do with the underlying merit of the paper (http://journals.plos.org/pl...:IMc0c9cv2v-9IfdpEuhFmiJxdk8 "http://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.1001675)"). I suspect the same is true for other article level metrics.

I find there is a strange disconnect in arguments about the IF. The journal IF must contain some information about the merit of the papers published in a journal because we, the scientific community, are the ones that determine where things get published and what gets cited. We don’t publish any old paper in Nature and Science; we publish what we believe is the best and most interesting science. Now sometimes, may be even often, we will get this wrong, but an informed decision is made to publish a paper in a particular journal. In a sense all the IF represents is someone else’s opinion about the merit of a paper. I think this might be one of the reasons people are uncomfortable with the IF along with the fact that the IF is clearly subject to error as a measure of merit. However, all measures of merit are subject to error and there is no evidence that the IF is any worse (http://journals.plos.org/pl...:IMc0c9cv2v-9IfdpEuhFmiJxdk8 "http://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.1001675)"). I’m not suggesting that the IF should be used blindly to assess papers and researchers, but suggesting that it contains little or no information about the merit of a paper seems illogical to me.

On 2016-03-18 13:55:54, user Fabien Campagne wrote:

Interesting visualization work. I think in addition to the stated aim, but from my point of view potentially as important, is the visualization of workflows under execution. Developing workflows would be helped by looking at such plots annotated with timing info, or success failure conditions, because the workflow may not work right away and better development tools would make the process easier. I think aggregation of provenance data, if error conditions are captured would be very useful as a workflow development and debugging help.

It this is of interest, please contact me, we are looking for good ways to visualize workflows as they are executing/being developed. See GobyWeb (http://arxiv.org/abs/1211.6...:Gc-90yQBd1sOO8d6oWuJaiBF6Ec "http://arxiv.org/abs/1211.6666)") and its successor, NextflowWorkbench (http://biorxiv.org/content/...:0w3VsVwWYggHNGxgXnlqN3tRYmE "http://biorxiv.org/content/early/2016/02/24/041236)").

On 2016-02-25 00:05:06, user Meru Sadhu wrote:

Thank you, David, for the kind words and comments. We agree that the most immediate applications of the CRISPR-based recombination mapping will be in unicellular organisms and cell culture. We also think the method holds a lot of promise for research in multicellular organisms, although we did not mean to imply that it “will be an efficient mapping method for all multicellular organisms”. Every organism will have its own set of constraints as well as experimental tools that will be relevant when adapting a new technique. To best help experts working on these organisms, here are our thoughts on your questions.

You asked about mutagenesis during recombination. We Sanger sequenced 72 of our LOH lines at the recombination site and did not observe any mutations, as described in the supplementary materials. We expect the absence of mutagenesis is because we targeted heterozygous sites where the untargeted allele did not have a usable PAM site; thus, following LOH, the targeted site is no longer present and cutting stops. In your experiments you targeted sites that were homozygous; thus, following recombination, the CRISPR target site persisted, and continued cutting ultimately led to repair by NHEJ and mutagenesis.

As to the more general question of the optimal mapping strategies in different organisms, they will depend on the ease of generating and screening for editing events, the cost and logistics of maintaining and typing many lines, and generation time, among other factors. It sounds like in Drosophila today, your related approach of generating markers with CRISPR, and then enriching for natural recombination events that separate them, is preferable. In yeast, we’ve found the opposite to be the case. As you note, even in Drosophila, our approach may be preferable for regions with low or highly non-uniform recombination rates.

Finally, mapping in sterile interspecies hybrids should be straightforward for unicellular hybrids (of which there are many examples) and for cells cultured from hybrid animals or plants. For studies in hybrid multicellular organisms, we agree that driving mitotic recombination in the early embryo may be the most promising approach. Chimeric individuals with mitotic clones will be sufficient for many traits. Depending on the system, it may in fact be possible to generate diploid individuals with uniform LOH genotype, but this is certainly beyond the scope of our paper. The calculation of the number of lines assumes that the mapping is done in a single step; as you note in your earlier comment, mapping sequentially can reduce this number dramatically.

On 2016-02-20 22:58:29, user David Stern wrote:

This is a lovely method and should find wide applicability in many settings, especially for microorganisms and cell lines. However, it is not clear that this approach will be, as implied by the discussion, an efficient mapping method for all multicellular organisms. I have performed similar experiments in Drosophila, focused on meiotic recombination, on a much smaller scale, and found that CRISPR-Cas9 can indeed generate targeted recombination at gRNA target sites. In every case I tested, I found that the recombination event was associated with a deletion at the gRNA site, which is probably unimportant for most mapping efforts, but may be a concern in some specific cases, for example for clinical applications. It would be interesting to know how often mutations occurred at the targeted gRNA site in this study.

The wider issue, however, is whether CRISPR-mediated recombination will be more efficient than other methods of mapping. After careful consideration of all the costs and the time involved in each of the steps for Drosophila, we have decided that targeted meiotic recombination using flanking visible markers will be, in most cases, considerably more efficient than CRISPR-mediated recombination. This is mainly due to the large expense of injecting embryos and the extensive effort and time required to screen injected animals for appropriate events. It is both cheaper and faster to generate markers (with CRISPR) and then perform a large meiotic recombination mapping experiment than it would be to generate the lines required for CRISPR-mediated recombination mapping. It is possible to dramatically reduce costs by, for example, mapping sequentially at finer resolution. But this approach would require much more time than marker-assisted mapping. If someone develops a rapid and cheap method of reliably introducing DNA into Drosophila embryos, then this calculus might change.

However, it is possible to imagine situations where CRISPR-mediated mapping would be preferable, even for Drosophila. For example, some genomic regions display extremely low or highly non-uniform recombination rates. It is possible that CRISPR-mediated mapping could provide a reasonable approach to fine mapping genes in these regions.

The authors also propose the exciting possibility that CRISPR-mediated loss of heterozygosity could be used to map traits in sterile species hybrids. It is not entirely obvious to me how this experiment would proceed and I hope the authors can illuminate me. If we imagine driving a recombination event in the early embryo (with maternal Cas9 from one parent and gRNA from a second parent), then at best we would end up with chimeric individuals carrying mitotic clones. I don't think one could generate diploid animals where all cells carried the same loss of heterozygosity event. Even if we could, this experiment would require construction of a substantial number of stable transgenic lines expressing gRNAs. Mapping an ~20Mbp chromosome arm to ~10kb would require on the order of two-thousand transgenic lines. Not an undertaking to be taken lightly. It is already possible to perform similar tests (hemizygosity tests) using D. melanogaster deficiency lines in crosses with D. simulans, so perhaps CRISPR-mediated LOH could complement these deficiency screens for fine mapping efforts. But, at the moment, it is not clear to me how to do the experiment.

On 2016-02-24 21:32:08, user Fabien Campagne wrote:

My lab developed the Goby framework, which you included in the benchmark.

Could you clarify which command line options you used when running each tool for these comparisons?

For Goby, you need to know that default options are equivalent to GZIP compression. They are not the state of the art approaches that we published in Campagne et al PLOS 2013. If you want these, you need to activate them (see command line flags described in our paper).

On page 4, you write " Goby were run with Java v1.7. All were run with default parameters", so I am think you may have benchmarked against the GZIP codec.

The data you present seem to suggest this as well, since our prior evaluations comparing CRAM and Goby found a large compression efficiency difference for Goby on RNA-Seq reads (of course, it is possible CRAM has made major progress since we conducted our benchmark).

On 2015-12-17 23:02:04, user Jon Brock wrote:

Thanks for sharing this. I'm really glad that autism researchers are starting to (a) look at cognitive heterogeneity; and (b) use preprint servers!

Some comments:

First, this is bugbear of mine but I find it quite unhelpful to talk about the RMET as a measure of mentalizing. In truth, it's a (relatively difficult) 4AFC test of emotion recognition. We can argue about whether learning the meanings of certain emotion words used in the test is contingent on having a fully functioning "theory of mind". But it's clear that the RMET is measuring something very different to other "mentalizing" tests in which the participant infers mental states based on the protagonists behaviour and/or events that are witnessed or described.

Second, I agree that there's potentially useful information at the item level that is lost by just totting up the number of correct items. But it's not clear to me that your study is demonstrating this to be true. In other words, what does subdividing the ASD group into "impaired" and "unimpaired" subgroups based on the clustering algorithm tells us that we wouldn't get by subdividing them according to some cut-off based on raw score? We learn that the "unimpaired" group have higher overall scores and higher VIQs, but we kind of know that already.

Third, related to the previous point, you show that a classifier trained on your subgroups in one dataset does a good job of predicting subgroup in an independent dataset; but how much of this "replicability" is driven by differences in overall performance? It would be helpful to get some more explicit details of what went into the classifier, but I assume that it's essentially providing a threshold on a weighted sum of all the items in the test. You've already shown that your subgroups (on which the classifier is trained) differ in overall performance (ie the unweighted sum of all the items). So it would be pretty odd if the classifier *didn't* perform well in a replication sample where subgroups also differed in overall performance. Indeed, in the TD group, where there aren't huge differences in overall performance, the classifier doesn't translate to the replication sample.

Hopefully my comment will help you clarify the article. I really like the approach of digging into the item-level data. At the very least I think it tells us something useful about the structure of the RMET - and which items are discriminating well between people who do versus do not have difficulties with labelling complex emotions. I'm just not convinced (yet) of some of the bolder claims you're making!

Finally, some references you may find useful:

Roach, N. W., Edwards, V. T., & Hogben, J. H. (2004). The tale is in the tail: An alternative hypothesis for psychophysical performance variability in dyslexia. PERCEPTION-LONDON-, 33(7), 817-830.

Towgood, K. J., Meuwese, J. D., Gilbert, S. J., Turner, M. S., & Burgess, P. W. (2009). Advantages of the multiple case series approach to the study of cognitive deficits in autism spectrum disorder. Neuropsychologia, 47(13), 2981-2988.

Brock, J. (2011). Commentary: complementary approaches to the developmental cognitive neuroscience of autism–reflections on Pelphrey et al.(2011). Journal of Child Psychology and Psychiatry, 52(6), 645-646.

On 2015-11-23 15:28:13, user Philippe Fort wrote:

Yes, interesting story. Your paper is very exhaustive in the analysis of the p53 retrogene family in Proboscideans. <br /> I myself looked at these pseudogene sequences several years ago in the elephant genome and found that they had a much higher dN/dS ratio than the active gene, suggesting that they had no particular role in the cell metabolism. However, this was a global analysis and did not explore the possibility that only part of the protein may be important and that a single retrogene may be expressed and be under selection. So nice job for the identification of all copies in Proboscideans.<br /> Nevertheless, I think your paper needs more robustness on the biological role of TAP53RTG12, since a major experiment is missing and the most important figures are not totally convincing.<br /> - The experiment missing should answer "Does knocking down TAP53RTG12 in elephant dermal cells reduce mitomycin D sensitivity"? (by the way, Figure 6 which shows hypersensitivity to DNA damage is not oncluded in the pdf). <br /> - Figure4B and 7:<br /> Could you explain which are the data shown in Figure 4B? Besides, I was expecting a graph showing gene copy number vs body mass (in the present panel, we don't know which samples are paired!) <br /> Figure 7 is not clearly explained. Since data are dose-responses, it would be better to treat them as such (non linear fit and F-Test). <br /> It is not clear to me why drug doses at which TAP53RTG12 expressing cells display a maximal p53 response elicit a so small effect on caspase activation (even if it is statistically significant, is it biologically relevant?).

On 2015-07-16 04:41:22, user Michael Eisen wrote:

Vale has put his finger on an important problem. The process of publication has far too great an influence on the way we do science, let alone communicate it. And it would be great if we all used preprint servers and strived to publish work faster and in a less mature form than we currently do. I am very, very supportive of Vale’s quest (indeed it has been mine for the past twenty years) – if it is successful, the benefits to science and society would be immense.

However, in the spirit of the free and open discussion of ideas that Vale hopes to rekindle, I should say that I didn’t completely buy the specific arguments and conclusions of this paper.

My first issue is that the essay misdiagnoses the problem. Yes, it is bad that we require too much data in papers, and that this slows down the communication of science and the progress of people’s careers. But this is a symptom of something more fundamental – the wildly disproportionate value we place on the title of the journal in which papers are published rather than on the quality of the data or its ultimate impact.

If you fixed this deeper problem by eliminating journals entirely and moving to a system of post-publication review, it would remove the perverse incentives that produce the effects Vale describes. However Vale proposes a far more modest solution – the use of pre-print servers. The odd thing with this proposal, as Vale admits, is that pre-print servers don’t actually solve the problem of needing a lot of data to get something published. It would be great for all sorts of reasons if every paper were made freely available online as early as possible – and I strongly support the push for the use of pre-print servers. But Vale’s proposal seem to assume that existing journal hierarchy would remain in place, and that most papers would ultimately be published in a journal. And this wouldn’t fundamentally alter the set of incentives to journals and authors that has led to problems Vale writes about. To do that you have to strip journals of the power to judge who is doing well in science – not just have them render that decision after articles are posted in a pre-print server. Unless the rules of the game are changed, with hiring, funding and promotion committees looking at quality instead of citation, universal adoption of pre-print servers will both be harder to achieve, and will have a limited effect on the culture of publishing.

Indeed, I would argue that we don’t need “pre-print” servers. What we need is to treat the act of posting your paper online in some kind of centralized server as the primary act of publication. Then it can be reviewed for technical merit, interest and importance starting at the moment it is “published” and continuing for as long as people find the paper worth reading.

Giving people credit for the impact their work has over the long-term would encourage them to publish important data quickly, and to fill in the story over time, rather than wait for a single “mature” paper. Similarly, rather than somewhat artificially create a new type of paper to publish “key findings” I think people will naturally write the kind of paper Vale wants if we change the incentives around publication by destroying the whole notion of “high-impact publications” and the toxic glamour culture that surrounds it.

Another concern I have about Vale’s essay is that he bases his argument for pre-print servers on a set of data analyses that, while I found them interesting, I didn’t find them compelling. I think I get what Vale’s doing. He wants to promote the use of pre-print servers, and realizes that there is a lot of resistance. So he is trying to provide data that will convince people that there are real problems in science publishing so that they will endorse his proposals. But by basing calls for change on data, there is the real risk that other people will also find the data less than compelling and will dismiss the Vale’s proposed solutions as unnecessary as a result, when in fact the things Vale proposes would be just as valuable even if all the data trends he cites weren’t true

So let’s delve into the data a bit. First, in an effort to test the widely held sentiment that the amount of data required for a paper has increased over time, he attempted to compare the amount of data contained in papers published in Cell, Nature and JCB during the first six months of 1984 and of 2014 (it’s not clear why he chose these three journals).

The first interesting observation is that the number of biology papers published in Nature has dropped slightly over thirty years, and the number of papers published in JCB has dropped in half (presumably as the result of increased competition from other journals). To quantify the amount of data a paper contained, Vale analyzed figures in each of the papers. The total number of figures per paper was largely unchanged (a product, he argues, of journal policies), but the number of subpanels in each figure went up dramatically – two to four-fold.

I am inclined to agree with him, but it is worth noting that there are several alternative explanations for these observations.

As Vale acknowledges, practices in data presentation could have changed, with things that used to be listed as “data not shown” may now be presented in figures. I would add that maybe the increase in figure complexity reflects the fact that it is far easier to make complex figures now than it was in 1984. For example, when I did my graduate work in the early 1990’s it was very difficult to make figures showing aspects of protein structure. Now it is simple. Authors may simply be more inclined to make relatively minor points in a figure panel now because it’s easier.

A glance at any of these journals will also tell you that the complexity of figures varies a lot from field to field. Developmental biologists, for example, seem to love figures with ten or twenty subpanels. Maybe Cell, Nature and JCB are simply publishing more papers from fields where authors are inclined to use more complex figures.

Finally, the real issue Vale is addressing is not exactly the amount of data included in a paper, but rather the amount of data that had to be collected to get to the point of publishing a paper. It’s possible that authors don’t actually spend more time collecting data, but that they used to leave more data “in the drawer”.

The real point is that it’s really hard to answer the question of whether papers now contain more data than they used to. And it’s even harder to determine whether the amount of data required to get a paper published is more of less of an obstacle now than it was thirty years ago.

I think I understand why Vale did this analysis. His push to reform science publishing is based on a hypothesis – that the amount of data required to publish a paper has increased over time – and, as a good scientist, he didn’t want to leave this hypothesis untested. However, I would argue that differences between 1984 and today are irrelevant. Making it easier to publish work, and giving people incentives to publish their ideas and data earlier, is simply a good idea – and would be equally good even if papers published in 1984 required more data than they do today.

Vale goes on to speculate about why papers today require more data, and chalks it up primarily to the increased size of the biomedical research community, which has increased competition for coveted slots in high-ranking journals while it has also increased the desire for such publications, and that this has allowed journals to be even more selective and to put more demands on authors. (It’s really quite interesting that the number of papers in Cell, Nature and (I assume)Science has not increased in 30 years even as the community has grown).

This certainly seems plausible, but I wonder if it’s really true. I wonder if, instead, the increase in expectations of “mature” work have to do with the maturation of the fields in question. Nature has pretty broad coverage in biology (although it’s coverage is by no means uniform), but Cell and JCB both represent fields (molecular biology and cell biology) that were kind of in their infancies, or at least early adolescences, 30 years ago. And as fields mature, it seems quite natural for papers to include more data, and for journals to have higher expectations for what constitutes an important advance. You can see this happening over much shorter timeframes. Papers on the microbiome for example used to contain very little experimental data – often a few observations about the microbial diversity of some niche – but within just a few years, expectations for papers in the field have changed, with the papers getting far more data-dense. It would be interesting to repeat the kind of analysis Vale did, but to try and identify “new” fields (whatever that means), and see whether fields that were “new” in 2014 have papers of similar complexity to “new” fields in 1984.

The second bit of data Vale produced is on the relationship between publications and the amount of time spent in graduate school. Using data from UCSF’s graduate program, he found that current graduate students “published fewer first/second author papers and published much less frequently in the three most prestigious journals.” The average time to a first author papers for UCSF students in the 80’s was 4.7 years, and now it is 6.0. And the number of students withScience, Nature or Cell papers has fallen in half.

Again, one could pick this analysis apart a bit. Even if you accept the bogus notion that SNC publications are some kind of measure of quality, there are more graduate students both in the US and elsewhere, but the number of slots in those journals has remained steady. Even if criteria for publication were unchanged over time, one would have expected the number of SNC papers for UCSF graduate students to have gone down simply because of increased competition. If SNCpapers are what these students aspire to (which is probably sadly largely true) then it makes sense that they would spend more time trying to make better papers that will get into these journals. It’s not clear to me that this requires that papers have more data, but rather than they have better data. But either way, once could look at this and argue that the problem isn’t that we need new ways of publishing, but rather that we need to stop encouraging students to put their papers into SNC. I suspect that all of the trends Vale measures here would be reversed if UCSF faculty encouraged all of their graduate students to publish all of their papers in PLOS ONE.

One could also argue that the trends reflect not a shift in publishing, but rather a degradation in the way we train graduate students. In my experience most graduate student papers reflect data that was collected in the year preceding publication. Maybe UCSF faculty, distracted perhaps by grant writing, aren’t getting students to the point where they do the important, incisive experiments that lead to publication until their fifth year, instead of their fourth.

And again, while the increased time to first publication has increased dramatically in the last 30 years, it’s hard to point to 1984 as some kind of Golden Age. That typical students back then weren’t publishing at all until the end of their fifth year in graduate school is still bad.

So, in conclusion, I think there is a lot to like in this essay. Without explicitly making this point, the observations, data and discussion Vale present make a compelling case that publishing is having a negative impact on the way we do science and the way we train the next generation. I have some issues with the way he has framed the argument and the degree of conservativeness in his solutions. But I think Vale has made an important contribution to the now decades old fight to reform science publishing, and we would all be better off if we heeded his advice.

On 2015-07-15 21:25:25, user Stephen Curry wrote:

This is an excellent contribution to the live and ongoing debate about the problems in scholarly publishing. The idea of preprints is not new, though it’s a fairly late arrival in the life sciences, incarnated here in bioarXiv and in PeerJ Preprints.

In the UK the Royal Society (think 'National Academy') held a two-part meeting in April and May of this year to discuss the Future of Scholarly Scientific Communications (https://royalsociety.org/ev.... It covered a broad range of issues (peer review, research assessment, reproducibility, fraud, the journal article and publisher profits) but on a surprising number of occasions the debate circled back to the problem of perverse incentives, the most notable one being the hold of the impact factor on people's careers. This retards science and encourages a spectrum of fraudulent behaviours as researchers strive to get in to the 'best' journals. The wider adoption of preprints would clearly help to mitigate some of the worst effects by tapping into the nascent culture of openness and by enabling much more rapid dissemination of results than at present. (see my digest of the meeting here: http://occamstypewriter.org...

The adoption of preprints represents a cultural shift, to be sure, but if the physicists can manage it, there's no good reason for life scientists not to be able to follow suit! We need to start rewarding people for publishing stuff quickly – and for participating in the open commentary that preprints invite.

Author response:

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

eLife Assessment

In this important work, it is demonstrated that certain high-resolution cryo-EM structures can be obtained by using concentrated cell extracts without purification. The compelling results with the mammalian ribosomes demonstrate the utility of this approach for this molecule and complexes with elongation factor 2. Moreover, this work also demonstrates the utility of 2D template matching for particle picking for structure determination by single-particle averaging pipelines.

We thank the reviewers for their valuable comments and suggestions, which have helped us to improve the manuscript. We provide a response to the referees’ comments below.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript by Seraj et al. introduces a transformative structural biology methodology termed "in extracto cryo-EM." This approach circumvents the traditional, often destructive, purification processes by performing single-particle cryo-EM directly on crude cellular lysates. By utilizing high-resolution 2D template matching (2DTM), the authors localize ribosomal particles within a complex molecular "crowd," achieving near-atomic resolution (~2.2 Å). The biological centerpiece of the study is the characterization of the mammalian translational apparatus under varying physiological states. The authors identify elongation factor 2 (eEF2) as a nearly universal hibernation factor, remarkably present not only on non-translating 80S ribosomes but also on 60S subunits. The study provides a detailed structural atlas of how eEF2, alongside factors like SERBP1, LARP1, and IFRD2, protects the ribosome's most sensitive functional centers (the PTC, DC, and SRL) during cellular stress.

Strengths:

The "in extracto" approach is a significant leap forward. It offers the high resolution typically reserved for purified samples while maintaining the "molecular context" found in in situ studies. This addresses a major bottleneck in structural biology: the loss of transiently bound or labile factors during biochemical purification.

The finding that eEF2 binds and sequesters 60S subunits is a major biological insight. This suggests a "pre-assembly" hibernation state that allows for rapid mobilization of the translation machinery once stress is relieved, which was previously uncharacterized in mammalian cells.

The authors successfully captured eIF5A and various hibernation factors in states that are traditionally disrupted. The identification of eIF5A across nearly all translating and non-translating states highlights the power of this method to detect ubiquitous but weakly bound regulators.

The manuscript beautifully illustrates the "shielding" mechanism of the ribosome. By mapping the binding sites of eEF2 and its co-factors, the authors provide a clear chemical basis for how the cell prevents nucleolytic cleavage of ribosomal RNA during nutrient deprivation.

Weaknesses:

(1) While 2DTM is a powerful search tool, it inherently relies on a known structural "template." There is a risk that this methodology may be "blind" to highly divergent or novel macromolecular complexes that do not share sufficient structural similarity with the search model. The authors should discuss the limitations of using a vacant 60S/80S template in identifying highly remodeled stress-induced complexes. For instance, what happens if an empty 40S subunit is used as a template? In the current work, while 60S and 80S particles are picked, none are 40S. The authors should comment on this.

Thank you for your comment. As noted by the reviewer, 2DTM inherently favors particles that share sufficient similarity with the search template and may underrepresent highly remodeled or structurally divergent complexes. Importantly, once particles are identified, subsequent 2D/3D classification and refinement are not constrained by the template used for particle picking. Consistent with this, we observe classes displaying additional or altered densities absent in the original template, indicating that template matching does not preclude the detection of remodeled ribosomal states, although highly divergent species may still escape detection.

Regarding the use of a 40S subunit as a template for 2DTM, we tested two templates: a complete 40S subunit and the 40S body alone. Using these 40S templates, we captured several 40S-, 43S-, and 48S-containing complexes, as well as 80S particles. As expected, no individual 60S classes emerge with 40S-TM. 40S-TM yielded 80S classes similar to those with 60-TM, although the number of particles was lower than that in 60S template matching, resulting in lower resolution of these classes. Since this study focuses on ribosome hibernation, we chose to proceed with the 60S-TM results and do not report results using 40S-TM. We reported 40S-TM results in another study from our groups (Zottig et al., bioRxiv, 2025), which focuses on translation initiation on 40S subunits and was deposited as preprint after this submission.

We have added a comment and reference describing the use of the 40S template in the initial section of Results and Discussion: “This result echoes our concurrent finding that using 40S or partial 40S templates yields a variety of initiation complexes and 80S classes, revealing densities beyond those in the template [44].”

(2) In the GTPase center, the authors identify density for "DRG-like" proteins. However, due to limited local resolution in that specific region, they are unable to definitively distinguish between DRG1 and DRG2. While the structural similarity is high, the functional implications differ, and the identification remains somewhat speculative. The authors should acknowledge this in the text.

We agree with this comment and address it in the main text:

“Whereas the overall shape and secondary structure resemble DRG1 or DRG2, the local resolution is insufficient to distinguish between these or other similarly structured proteins. Both yeast and mammalian counterparts are reported to function with a companion factor (Tma146p or Gir2 in yeast; or DFRP1 and DFRP2 in mammals), but our maps do not contain density that could correspond to DFRP1/2 near the putative DRG1/2 density. Future work will elucidate the function of these or other DRG-like GTPases in the context of an elongation complex.”

(3) While "in extracto" is superior to purified SPA, the act of cell lysis (even rapid permeabilization) still involves a change in the chemical environment (pH, ion concentration, and dilution of metabolites). The authors could strengthen the manuscript by discussing how post-lysis changes might affect the occupancy of factors like GTP vs. GDP states.

Thank you for pointing this out. Cell lysis can indeed lead to a change in the chemical environment, although we do not know how post-lysis changes may specifically affect the occupancy of factors, such as GTP- vs. GDP-bound states. We tried to minimize this effect by performing a rapid permeabilization. Our efforts to optimize our protocols are ongoing, and we expect to have a better answer to this question in the future.

Nevertheless, to address this reviewer’s concern, our discussion states: “Additional optimization of buffer conditions may be required to more accurately represent the translation states observed in cells, as ionic conditions are known to affect the conformation of the ribosomes (e.g. rotated/non-rotated) and binding of protein factors”.

(4) The study provides excellent snapshots of stationary states (translating vs. hibernating), but the kinetic transition, specifically how the 60S-eEF2 complex is recruited back into active translation, is not well discussed. On page 13, the authors present eEF2 bound to 60S but do not mention anything regarding which nucleotide is bound to the factor. It only becomes clear that it is GDP after looking at Figure S9. This should be clarified in the text. Similarly, the observations that eEF2 is bound to GDP in the 60S and 80S raise questions as to how the factor dissociates from the ribosome. This could also be discussed.

Thank you for bringing this to our attention. We now state in the main text that eEF2 is bound with GDP on the 60S subunit.

As for the kinetic transitions of 60S-eEF2 complexes, like this reviewer, we are fascinated by the possible roles and mechanisms of the 60S-eEF2 complex. The averaged particle ensembles derived from cryo-EM data do not report on the kinetics or transition pathways directly. We acknowledge in the main text that “Future studies will bring insights into the roles of the protein(s) and into the functions and transitions of 60S•eEF2 complexes to the pool of translating ribosomes”.

Overall Assessment:

The work reported in this manuscript likely represents the future of structural proteomics. The combination of high-resolution structural biology with minimal sample perturbation provides a new standard for investigating the cellular machines that govern life. After addressing minor points regarding template bias, protein identification, and transition dynamics, this work may become a landmark in the field of translation.

Reviewer #2 (Public review):

In this manuscript, the authors describe using "in extracto" cryo-EM to obtain high-resolution structures of mammalian ribosomes from concentrated cell extracts without further purification or reconstitution. This approach aims to solve two related problems. The first is that purified ribosomes often lose cellular cofactors, which are often reconstituted in vitro; this precludes the ability to find novel interactions. The second is that while it is possible to perform cryo-EM on cellular lamella, FIB milling is a slow and laborious process, making it unfeasible to collect datasets sufficiently large to allow for high-resolution structure determination. Extracts should contain all cellular cofactors and allow for grid preparation similar to standard single-particle analysis (SPA) approaches. While cryo-EM of cell extracts is not in itself novel, this manuscript uses 2D template matching (2DTM) for particle picking prior to structure determination using more standard SPA pipelines. This should allow for improved picking over other approaches in order to obtain large datasets for high-resolution SPA.

This manuscript has two main results: novel structures of ribosomes in hibernating states; and a proof-of-principle for in extracto cryo-EM using 2DTM. Overall, I think the results presented here are strong and serve as a proof-of-principle for an approach that may be useful to many others. However, without presenting the logic of how parameters were optimized, this manuscript is limited in its direct utility to readers.

Thank you for this valuable comment. We have expanded our Methods section “Optimization of 2DTM in RRL data “to present the logic behind parameter optimization, with the paragraph beginning with “We optimized high-resolution template matching procedures…”

Reviewer #3 (Public review):

Summary:

The authors describe a new structural biology framework termed "in extracto cryo-EM," which aims to bridge the gap between single-particle cryo-EM of purified complexes and in situ cryo-electron tomography (cryo-ET). By utilizing high-resolution 2D template matching (2DTM) on mammalian cell lysates, the authors sought to visualize the translational apparatus in a near-native environment while maintaining near-atomic resolution. The study identifies elongation factor 2 (eEF2) as a major hibernation factor bound to both 60S and 80S particles and describes a variety of hibernation scenarios involving factors such as SERBP1, LARP1, and CCDC124.

Strengths:

(1) The use of 2DTM effectively overcomes the signal-to-noise challenges posed by the dense and viscous nature of cellular extracts, yielding maps as high as 2.2 Å.

(2) The discovery of eEF2-GDP as a ubiquitous shield for ribosomal functional centers, particularly its unexpected stabilization on the 60S subunit, provides a compelling model for ribosome preservation during stress.

Weaknesses:

(1) Representative nature of cell samples and lower detection limit

The cells used in this study (MCF-7, BSC-1, and RRL) are either fast-growing cancer cell lines or specialized protein-synthetic systems. For cells with naturally low ribosomal abundance (such as quiescent primary cells), achieving the target concentration (e.g., A260 > 1000 ng/uL) would require an exponentially larger starting cell population.

Is there a defined lower limit of ribosomal concentration in the raw lysate below which the 2DTM algorithm fails to yield high-resolution classes? In ribosome-sparse lysates, A260 becomes an unreliable proxy for ribosome density due to the high background of other RNA species and proteins. How do the authors estimate specific ribosome abundance in such heterogeneous fields?

We have not tested these specific points, but we found that 2DTM can successfully result in high-resolution reconstructions even with 1-2 particles per micrograph. This would require a substantially larger dataset than in this work yet could provide a viable strategy for diluted or low-abundance samples. Other optimizations, including lysate concentration, may help as well. We have the following text to reflect these points:

“Additional optimization of buffer conditions may be required to more accurately represent the translation states observed in cells, as ionic conditions are known to affect the conformation of the ribosomes (e.g. rotated/non-rotated) and binding of protein factors [91-94]. For cells or samples with lower abundance of ribosomes or other macromolecules/complexes of interest, a lysate concentration step or collection of a larger dataset may be considered.”

(2) Quantitation in heterogeneous lysates and crowding effects

The authors utilize A260 as a key quality control measure before grid preparation. However, if extreme physical concentration is required to see enough particles, the background concentration of other cytoplasmic components also increases. This may lead to molecular crowding or sample viscosity that interferes with the formation of optimal thin ice. How do the authors calculate or estimate the specific abundance of ribosomes in the cryo-EM field of view when they represent a much smaller percentage of the total cellular content?

We reported A260 as a reference that may be useful to achieve particle distributions resembling those in our work, rather than as a key quality control measure. Accordingly, we do not use it to estimate ribosome concentration or the specific abundance of ribosomes; instead, we’d recommend adjusting the sample concentration/dilution by grid screening.

This reviewer mentions the important aspect of ice thickness. We found that the highest population of ribosome particles is found in thicker ice regions, and these particles have been used to make up the majority of our datasets leading to high-resolution reconstructions. We have added this observation to “Optimization of 2DTM in RRL data”.

(3) Optimization of sample preparation

The authors describe lysates as dense and viscous, requiring multiple blotting steps (2-3 times) for 3-8 seconds. Have the authors tested whether a larger molecular weight cutoff (e.g., 100 kDa) during concentration could improve the ribosome-to-background ratio without losing small factors like eIF5A (approx. 17 kDa)? Could repeated blotting of a concentrated, viscous lysate introduce shearing forces or increased exposure to the air-water interface that perturbs the native conformation of the complexes?

We strived to minimize the number of steps in sample preparation, so we did not extensively test concentration steps. We also found that a concentration step can be omitted; the eIF5A-containing structure from the RRL dataset was determined without this step. We agree with the reviewer that repeated blotting may change ribosome complex equilibrium and result in a different distribution of functional states than in cells. However, we did not find evidence of perturbation of the native conformations of complexes, as the positions of ribosomes and factors are nearly identical to those observed in previous studies, including the recent high-resolution structures from cells that we cite.

(4) The regulatory switch and mechanism of eEF2

The finding that eEF2-GDP occupies dormant ribosomes is striking. What drives eEF2 from its canonical role in translocation to this hibernation state? Is this transition purely driven by stoichiometry (lack of mRNA/tRNA) and the GDP/GTP ratio, or is there a role for post-translational modifications? How do these eEF2-bound dormant ribosomes rapidly re-enter the translation pool upon stress relief?

We are glad that this reviewer is fascinated by the eEF2-GDP occupancy on dormant ribosome (just like we are)! These are important open questions that require further research, as our cryo-EM analyses cannot directly address the kinetic or mechanistic aspects of the mentioned processes. We did explore the known modification/phosphorylation sites in eEF2 densities but did not find evidence for such modifications, which does not rule out the possibility of transient or new modifications.

(5) Hibernation diversity and LARP1 contextualization

The study reveals that hibernation strategies vary across cell types. Does the high hibernation rate in RRL reflect a physiological state, or does it hint at “preparation-induced stress” due to resource exhaustion or mRNA degradation in the cell-free system? How do the authors reconcile their discovery of LARP1 on 80S particles with recent 2024 reports that primarily describe LARP1 as an SSU-bound repressor?

Based on the high abundance of hibernating ribosomes in RRL (relative to many other samples we have tested so far), we speculate that this scenario may result from the stresses induced during lysate preparation: first, the rabbits are treated with phenylhydrazine inducing cell stress, then lysates are treated with micrococcal nuclease to degrade endogenous mRNAs. In addition, the specialization of reticulocytes may contribute to the distinct expression of stress/hibernation factors.

As for LARP1, our finding is consistent with the 2024 work by Saba et al, who reported LARP1 binding to both 40S subunits and 80S ribosomes. They also noted that LARP1-bound ribosomes are “non-translating”, consistent with our structures.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) In Figure 3, it would be easier for the reader if the authors would report the % of particles in each class. Also, indicating body rotation and head swiveling values would help.

Because our high-resolution maps result from a combination of data sets (e.g., RRL with an mRNA and RRL without an mRNA), we specify the particle percentages in the corresponding classification schemes in supplemental figures. To avoid excessive labeling in this figures, body rotation and head swiveling values for the new classes are shown in Figure 4.

(2) Page 16, what is 'elongation factor 1'? It doesn't seem the authors refer to eEF1A?

Thank you for pointing out this inconsistency, this is indeed eEF1A. We have corrected the text.

(3) Page 16, after 'individual 60S subunits', there is a missing full stop.

Thanks. Corrected.

Reviewer #2 (Recommendations for the authors):

I am not an expert in ribosome biology and do not have any specific comments on the various states presented here. Instead, I will mainly focus on the image processing aspects of this manuscript.

Major points:

(1) Were any AI-based particle pickers, such as crYOLO, topaz, or warp tested? While more traditional template-based or LoG pickers were shown to be inferior to 2DTM, it is unclear if AI methods would perform just as well. Given that a major point of this manuscript is the image processing pipeline, and that these AI tools have been widely adopted in the field, I think this is an important consideration.

We used other particle pickers before using 2DTM and have listed them in the Supplementary Information: please see Table S1 for a complete list of particle pickers evaluated in this study. Since our present work focuses on a sample preparation method, a more extensive evaluation of particle picking methods is beyond the scope of this study.

(2) While the methods used to obtain the structures presented are detailed, I think it would also be useful to provide some logic for how parameters were determined or optimized. This would serve as a useful foundation for readers who wish to try out this in an extracto approach on their own specimens. Some of these optimizations seem quite specific, such as optimization of angular search parameters, but with no clear logic: e.g., why is the out-plane search coarser than the in-plane search; what is the effect of increasing the angular step sizes? Some seem inconsistent, e.g., why is e2pdb2mrc.py sometimes used and the cisTEM simulate used other times? Some are poorly described, such as "the defocus search turned on for micrographs with thicker ice" where there is no mention of how ice thickness is assessed and how thick is too thick. I think a workflow figure with accompanying text would help the reader understand the logic used in this work and how to apply that logic to their own projects.

To address the comments in (2), we provide separate responses addressing each comment:

(1) Provide some logic for how parameters were determined or optimized:

The logic behind determining and optimizing search parameters is a balance between search precision and computational cost. In practice, users must weigh the benefit of finer sampling against the substantial increase in runtime, particularly for large datasets. For example, enabling defocus searching with a 200 Å step size and a 1000 Å range increases the computational time by approximately 11-fold compared to running the same search with defocus disabled (since each defocus plane in the positive and negative direction are searched), making such increases prohibitive, when GPU resources are limited. In such cases, reducing the defocus search to a 250 Å step size and a 500 Å range can dramatically shorten runtime while preserving nearly the same number of reliable matches. In summary, we found that optimizing the defocus search, in-plane, out-plane angles, and the image/micrograph pixel size can substantially reduce the processing speed while sacrificing only a small percentage of particles.

We have expanded our parameter optimization paragraph in “Optimization of 2DTM in RRL data”, as mentioned in a previous response.

(2) Some seem inconsistent, e.g., why is e2pdb2mrc.py sometimes used and the cisTEM simulate used other times?

e2pdb2mrc.py is simpler to use and was used in the beginning of the project. Later, we switched to using the simulate program since it preformed slightly better. Either software is suitable to generate templates for 2DTM.

(3) Some are poorly described, such as "the defocus search turned on for micrographs with thicker ice" where there is no mention of how ice thickness is assessed and how thick is too thick.

We did not quantitatively assess ice thickness; instead, we tested whether it is advantageous to include the defocus search. To this end, we first performed CTF estimation and grouped micrographs based on their fit resolution. From each group, we selected ten micrographs representing the highest and lowest fit resolutions. Template matching was then performed using identical parameters, once with defocus search enabled and once with it disabled. The number of picked particles for each micrograph under both conditions was compared. When a significant difference was observed most commonly for icy micrographs with low fit resolution we enabled defocus search for that group of images. The difference between having the defocus search on vs off sometimes resulted in having 2x more matches. We found these images/datasets appeared to have a higher background compared to in-vitro reconstituted samples. The template-matching results from these micrographs were subsequently combined with results from groups processed with defocus search disabled.

To address this point, we have included this description in “Optimization of 2DTM in RRL data”.

(4) I think a workflow figure with accompanying text would help the reader understand the logic used in this work and how to apply that logic to their own projects.

Thanks for this suggestion. We have added a workflow figure as Figure 1—figure supplement 2.

Minor Points:

(1) While the image processing described seems appropriate, I think it is still necessary to include Fourier shell correlation plots for the final structures as supplemental data.

Thank you for pointing out this inadvertent omission. We have added FSC curves in Figure 3—figure supplement 3.

(2) One of the initial workflows used is a Relion 3 pipeline, which is, at this point, quite dated. Is there a reason Relion 4 or 5 was not used instead?

The project started when Relion 3 was the latest version.

Many people assume that if someone wants privacy, they must be doing something suspicious, but this chapter shows that privacy is often about dignity, safety, and control over personal information. For example, people may want private conversations to avoid embarrassment, protect themselves from harassment, or separate different parts of their lives. I think this is especially relevant today because social media often pressures people to share everything publicly. Sometimes choosing privacy is actually a healthy boundary.

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

Learn more at Review Commons

Reply to the reviewers

Manuscript number: RC-2025-02954

Corresponding author(s): Ana-Maria Lennon-Duménil and Sandra Iden

1. General Statements [optional]

We thank the three reviewers for the time and caution taken to assess our manuscript, and for their constructive feedback that will help improve the study. We herewith provide a revised manuscript that addressed the key points raised by the reviewers.

2. Point-by-point description of the revisions

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

Summary: The manuscript by Delgado et al. reports the role of the actin remodeling Arp2/3 complex in the biology of Langerhans cells, which are specialized innate immune cells of the epidermis. The study is based on a conditional KO mouse model (CD11cCre;Arpc4fl/fl), in which the deletion of the Arp2/3 subunit ArpC4 is under the control of the myeloid cell specific CD11c promoter.

In this model, the assembly of LC networks in the epidermis of ear and tail skin is preserved when examining animals immediately after birth (up to 1 week). Subsequently however LCs from ArpC4-deleted mice start displaying morphological aberrations (reduced elongation and number of branches at 4 weeks of age). Additionally, a profound decline in LC numbers is reported in the skin of both the ear and tail of young adult mice (8-10 weeks).

To explore the cause of such decline, the authors then opt for the complementary in vitro study of bone-marrow derived DCs, given the lack of a model to study LCs in vitro. They report that ArpC4 deletion is associated with aberrantly shaped nuclei, decreased expression of the nucleoskeleton proteins Lamin A/C and B1, nuclear envelop ruptures and increased DNA damage as shown by γH2Ax staining. Importantly, they provide evidence that the defects evoked by ArpC4 deletion also occur in the LCs in situ (immunofluorescence of the skin in 4-week old mice).

Increased DNA damage is further documented by staining differentiating DCs from ArpC4-deleted mice with the 53BP1 marker. In parallel, nuclear levels of DNA repair kinase ATR and recruitment of RPA70 (which recruits ATR to replicative forks) are reduced in the ArpC4-deleted condition. In vitro treatment of DCs with the topoisomerase II inhibitor etoposide and the Arp2/3 inhibitor CK666 induce comparable DNA damage, as well as multilobulated nuclei and DNA bridges. The authors conclude that the ArpC4-KO phenotype might stem, at least in part, from a defective ability to repair DNA damages occurring during cell division.

The study in enriched by an RNA-seq analysis that points to an increased expression of genes linked to IFN signaling, which the authors hypothetically relate to overt activation of innate nucleic acid sensing pathways.

The study ends by an examination of myeloid cell populations in ArpC4-KO mice beyond LCs. Skin cDC2 and cDC2 subsets display skin emigration defects (like LCs), but not numerical defects in the skin (unlike LCs). Myeloid cell subsets of the colon are also present in normal numbers. In the lungs, interstitial and alveolar macrophages are reduced, but not lung DC subsets. Collectively, these observations suggest that ArpC4 is essential for the maintenance of myeloid cell subsets that rely on cell division to colonize or to self-maintain within their tissue of residency (including LCs).

MAJOR COMMENTS

1. ArpC4 and Arp2/3 expression The authors argue that LCs from Arpc4KO mice should delete the Arpc4 gene in precursors that colonize the skin around birth. It would be important to show it to rule out the possibility that the lack of phenotype (initial seeding, initial proliferative burst) in young animals (first week) could be related to an incomplete deletion of ArpC4 expression. Also important would be to show what is happening to the Arp2/3 complex in LCs from Arpc4KO mice.

__Response: __We thank this reviewer for the careful assessment of our manuscript. Regarding this specific comment, we would like to clarify that we do not expect ArpC4 to be deleted in LC precursors, as CD11c is only expressed once the cells have entered the epidermis. Instead, we expect the deletion to take place after birth around day 2-4 (Chorro et al., 2009). For this reason, we performed a deletion PCR of epidermal cells at postnatal day 7 (P7), a time at which the proliferative burst occurs. This analysis revealed CD11c-Cre-driven recombination in the ArpC4 locus (Fig. S2C). This experiment indicates that ArpC4 deletion does not alter LC proliferation and postnatal network formation.

We apologize if this was not clear enough and have (1) revised the manuscript text to clearly explain the time at which ArpC4 will be deleted early during development when using the CD11c-Cre transgene, and (2) better emphasized the rationale for the deletion PCR (page 4).

In the in vitro studies with DCs, the level of ArpC4 and Arp2/3 deletion at the protein level is also not documented.

__Response: __We have previously analyzed the expression of ArpC4 in BMDCs in a recent study, confirming its loss in CD11c-Cre;ArpC4fl/fl cells at the protein level: Rivera et al. Immunity 2022; doi: 10.1016/j.immuni.2021.11.008. PMID: 34910930 (Fig. S2D). Therefore, in the current manuscript we only refer to that paper (Results, first paragraph).

The authors explain that surface expression of the CD11c marker, which drives Arpc4 deletion, gradually increased during differentiation of DCs: from 50% to 90% of the cells. Does that mean that loss of ArpC4 expression is only effective in a fraction of the cells examined before day 10 of differentiation (e.g. in the RNA-seq analysis)?

__Response: __The reviewer is correct, there is heterogeneity in CD11c expression, which is inherent of this DC culture model, implying that Arpc4 gene deletion will be partial. However, despite this, we were able to detect significant differences between the transcriptome of control and CD11c-Cre;ArpC4fl/fl DCs in early phases during differentiation, emphasizing that the phenotype of ArpC4 loss is robust.

We have included a notion on this heterogeneity in the revised manuscript text (page 5).

Intra-nuclear versus extra-nuclear activities of Arp2/3

The authors favor a model whereby intra-nuclear ArpC4 helps maintaining nuclear integrity during proliferation of DCs (and possibly LCs). However, multiple pools of Arp2/3 have been described and accordingly, multiple mechanisms may account for the observed phenotype: i) cytoplasmic pool to drive the protrusions sustaining the assembly of the LC network and its connectivity with keratinocytes ; ii) peri-nuclear pool to protect the nucleus ; iii) Intra-nuclear pool to facilite DNA repair mechanisms e.g. by stabilizing replicative forks (the scenario favored by the authors).

__Response: __The referee is correct, and this is discussed in our manuscript (page 11, upper paragraph): we cannot exclude that several pools of branched actin are influencing the phenotype we here describe.

Unfortunately, we have previously tested several antibodies against ArpC4, but in our hands, and despite comprehensive optimization, they did not yield specific signals that would enable us to assess changes in subcellular localization in murine cells. Upon this reviewer's comment, we have now reassessed the available tools. We have tested an antibody against ArpC2 (Millipore, Anti-p34-Arc/ARPC2, 07-227-I-100UG), which however did not produce any specific signals either. Instead, we found an ArpC5 antibody that yielded a filamentous staining in the cytoplasm plus nuclear staining in distinct foci of control bone marrow-derived DCs, indicating that Arp2/3 components may in principle act in the nucleus in these cells (see revised Figure S3F,G).

It is recommended that the authors try to gather more supportive data to sustain the intra-nuclear role. Documenting ArpC4 presence in the nucleus would help support the claim. It could be combined with treatments aiming at blocking proliferation in order to reinforce the possibility that a main function of ArpC4 is to protect proliferating cells by favoring DNA repair inside the nucleus.

__Response: __We thank this reviewer for this very helpful comment. As outlined in the previous response, we have aimed at obtaining subcellular localization data for Arp2/3 complex components, and along with that study a potential intranuclear localization. Beyond that, in comparison to commonly cultured cell types, however, we face two hurdles addressing the nuclear Arp2/3 role in full: 1) Due to poor transduction rates and epigenetic silencing, we cannot sufficiently express exogenous constructs such as ArpC4-NLS in DCs to assess the subcellular localization of Arp2/3 complex components. 2) We have performed preliminary tests to block proliferation in DCs, using the cyclin D kinase 1 inhibitor RO3306 at different concentrations and incubation times during DC differentiation. Unfortunately, most cells were found dead after treatment. Further lowering the inhibitor concentrations (below 3.5uM) will likely not block the cell cycle, rendering this approach unsuited.

As mentioned above, we have tested the suitability of additional antibodies directed against Arp2/3 complex components to assess their subcellular localization, with the aim to discriminate peripheral cytoplasmic vs. perinuclear vs. intranuclear localization. These new data that report nuclear and cytoplasmic ArpC5 in control DCs are now presented in revised figure S3F,G. In addition, we toned down our current phrasing in the discussion, also emphasizing the possibility that cytoplasmic or perinuclear pools of the complex may indirectly help maintain the integrity of the genome in LCs (page 12).

Nuclear envelop ruptures

The nuclear envelop ruptures are not sufficiently documented (how many cells were imaged? quantification?). The authors employ STED microscopy to examine Lamin B1 distribution. The image shown in Figure 4A does not really highlight the nuclear envelop, but rather the entire content. Whether it is representative is questionable. We would expect Lamin B1 staining intensity to be drastically reduced given the quantification shown in Figure 3D. In addition, although the authors have stressed in the previous figure that Arpc4-KO is associated with nucleus shape aberrations, the example shown in Figure 4A is that of a nucleus with a normal ovoid shape.

It is recommended to quantify the ruptures with Lap2b antibodies (or another staining that would better delineate the envelop) in order to avoid the possible bias due to the reduced staining intensity of Lamin B1.

__Response: __NE ruptures are quantified by imaging NLS-GFP-expressing DCs in microchannels to visualize leakage of their nuclear content (Fig. 4B,C). The STED image mentioned by the referee (Fig. 4A,D) was only shown to further illustrate examples of NE ruptures, here using Lamin B1 as an immunofluorescence marker for the NE. We do agree with the reviewer that it was not chosen optimally to represent the ArpC4KO phenotype regarding nuclear shape and Lamin B1.

We have now provided representative examples of nuclear illustrations of the ArpC4KO phenotype vs. control cells. In addition, we performed STED microscopy of Lap2b immunostained DCs as suggested by the referee (revised Fig. 4A,B).

A missing analysis is that of nuclear envelop ruptures as a function of nucleus deformations.

__Response: __As stated in the manuscript (page 5, third paragraph), the morphology of DCs is quite heterogeneous. As mentioned above, nuclear rupture events were quantified by live-imaging of NLS-GFP expressing DCs, enabling the tracing of rupture events. Live imaging is the only robust manner to measure nuclear membrane rupture events as they are transient due to rapid membrane repair (Raab et al. Science 2016). The NLS-GFP label itself, however, is not accurate enough to also quantify nuclear deformations. The latter therefore was quantified after cell fixation, using DAPI and/or immunostaining for NE envelope markers (Figures 3 and S3).

As suggested by the referee, we have now quantified nuclear deformations using Lap2b staining of the nuclear envelope (revised Fig. 4A,B), demonstrating reduced circularity and increased elongation of ArpC4KO nuclei.

Fig 4B-C: same frequency of Arpc4-KO and WT cells displaying nuclear envelop ruptures in the 4-µm channels; however image show a rupture for the Arpc4-KO and no rupture for the WT cells (this is somehow misleading). Are ruptures similar in Arpc4-KO and WT cells in this condition?

__Response: __We apologize for choosing an image that does not represent well our quantification, our mistake. The revised manuscript now contains an image that better reflects our quantification (revised Fig. 4C).

Fig 4D-E: is their a direct link between nuclear envelop ruptures and ƴH2A.X?

__Response: __At present, we can only correlate the findings of increased gH2Ax and elevated events of nuclear envelope ruptures in ArpC4KO DCs. Rescue experiments are very difficult to impossible in DCs (e.g. restoring Lamin A/C and B1 levels in the KOs and subsequently assessing the amount of DNA damage). While we are afraid that we cannot address a potential link between NE ruptures and DNA damage by experiments in a manner feasible within this manuscript's revision, we have discussed this interesting aspect based on observations in immortalized cell culture systems (page 10). However, we would like to note that this was indeed shown for different cell types in Nader et al. Cell 2021. This effect results from access of cytosolic nuclease Trex1 to nuclear DNA. We have added this point in our revised manuscript (page 11).

Interesting (but optional) would be to understand what is happening to DNA, histones? Is their evidence for leakage in the cytoplasm?

__Response: __This is an interesting question. To assess this, we have now performed immunostainings for double-stranded DNA in the cytoplasm, following published protocols (Spada et al., 2019; PMID 31727239). This analysis revealed significantly increased cytoplasmic dsDNA in ArpC4KO DCs (revised Fig. 4G,H), indeed suggesting leakage into the cytoplasm following ArpC4 loss.

RNA seq analysis

The RNA-seq analysis suffers from a lack of direct connection with the rest of the study. The extracted molecular information is not validated nor further explored. It remains very descriptive. The PCA analysis suggests a « more pronounced transcriptomic heterogeneity in differentiating Arpc4KO DCs ». However it seems difficult to make such a claim from the comparison of 3 mice per group. In addition, such heterogeneity is not seen in the more detailed analysis (Fig 5F). The authors claim that « day 10 control and Arpc4KO DCs showed no to very little differences in gene expression, in contrast to cells at days 7-9 of differentiation ». This is not obvious from the data displayed in the corresponding figure. In addition, it is not expected that cells that may take a divergent differentiation path at days 7-9 may would return to a similar transcriptional activity at day 10.

A point that is not discussed is that before day 10 of DC differentiation, Arpc4 KO is expected to only occur in about 50% of the cell population. This is expected to impact the RNA-seq analysis.

Not all clusters have been exploited (e.g. cluster 3 elevated, cluster 6 partly reduced). I suggest the authors reconsider their analysis and analysis of the RNA-seq analysis (or eventually invest in complementary analysis).

__Response: __Despite a comprehensive analysis of the different transcriptomes of control and ArpC4 mutant cells during DC differentiation, we decided to focus the presentation and discussion of our RNAseq results on the most notable findings. Of these, the elevated innate immune responses in ArpC4KO DCs (Fig. 5E,H) caught our particular attention, as this seemed highly meaningful in light of DC and LC functions.

As suggested by the referee, in the revised manuscript, we better connected the RNAseq data to the other cellular and molecular analyses shown, complementing these results by investigating the potential involvement of innate immune responses in the ArpC4KO phenotype (page 7).

What causes the profound numerical drop of LC in the epidermis?

A major open question is what causes the massive drop of LCs. Although differentiating Arpc4KO DCs start accumulating DNA damage upon proliferation, they succeed in progressing through the cell cycle. There is even a slightly elevated expression of cell cycle genes at day 7 of differentiation in the DC model.

Only a trend for increased apoptosis is observed in ear and tail skin. It would be important to provide complementary data documenting increased death (or aberrant emigration?) of LCs in the 4-8 week time window.

__Response: __We agree with the reviewer that this is an important question. We exclude that elevated emigration causes the decline of LCs in ArpC4KO epidermis, as ArpC4-mutant LCs are significantly reduced (and not increased) in number in skin-draining lymph nodes (Fig. 7E). To assess whether increased cell death contributed to LC loss, we have tried to identify LCs that are just about to die. As the reviewer noted, we could only observe a trend of apoptosis-positive LCs in mutant epidermis. We assume that this is because of a quick elimination of compromised LCs following DNA damage, with only a short time passing until LCs with impaired genome integrity will be cleared from the system, making it very difficult to detect gH2Ax-positive cells that are positive for markers of cell death.

Despite these limitations to detect DNA-damage-positive but viable LCs in vivo, we have now collected 6-week-old mice to analyze LC numbers and apoptosis (cleaved Caspase-3), complementing our data derived from 7-day and 4-week-old mice (Figures S2A,B,E,F). While we did observe the expected trends for reduced LC numbers and increased DNA damage of ArpC4KO LCs as seen in adolescent mice, we were unable to detect a significant increase of apoptotic LCs in ArpC4KO animals at 6 weeks of age (revised Suppl. Fig. 4A-D). We assume that this is due to the outlined short-lived stages of apoptotic cells. Alternatively, it seems possible that ArpC4KO LCs were lost via cell death pathways other than apoptosis, a matter which we feel is beyond the scope of this manuscript. Accordingly, we revised our discussion to include this possibility (page 11-12).

Functional consequences

Although the study reports novel aspects of LC biology, the consequence of ArpC4 deletion for skin barrier function and immunosurveillance are not investigated. It would seem very relevant to test how this model copes with radiation, chemical and/or microorganism challenges.

__Response: __We fully agree with this reviewer that this is a very interesting point. Therefore, next to assessing the steady-state circulation of LCs and DCs, we also addressed the consequence of ArpC4 loss for LC function in chemically challenged skin: we performed skin painting experiments using the contact sensitizer fluorescein isothiocyanate (FITC), diluted in the sensitizing agent dibutyl phthalate (DBP), to detect cutaneous-derived phagocytes within draining lymph nodes. These experiments revealed that migration of ArpC4KO LCs (as well as of ArpC4KO DCs) to skin-draining lymph nodes was impaired (Fig. 7C-E), confirming an in vivo role of ArpC4 for immune cell migration to lymphatic organs following a chemical challenge. The revised manuscript contains a more detailed note to properly explain the FITC painting experiment and highlight its importance (page 9).

MINOR COMMENTS:

1- Figure 1D

Gating strategy: twice the same empty plots. The content seems to be missing... Does this need to be shown in the main figure?

__Response: __We apologize for this problem that might be due to file conversion of PDF reader software. In our PDF versions (including the published bioRxiv preprint) we do see the data points; however, we have earlier experienced incomplete FACS plots during manuscript preparation.

For the revised manuscript, we double-checked the results after converting the figures into PDFs. Here is a screenshot:

2- Figure 2

Best would be to keep same scale to compare P1 and P7 (tail skin, figure 2A)

Response: We have replaced the examples with micrographs of comparable scale (revised Fig. 2A).

Overlay of Ki67 and MHC-II does not allow to easily visualize the double-positive cells (Fig 2C)

Response: We now provided single-channel image next to the merged view and improved the visualization of double-positive cells (revised Fig. 2C).

Quality of Ki67 staining different for Arpc4-KO (less intense, less focused to the nuclei): a technical issue or could that reflect something?

Response: We thank the reviewer for spotting this. We have re-assessed all Ki67 micrographs and noted that the originally chosen examples indeed were not fully representative. We have selected more representative examples of Ki67-positive cells in control and mutant tissues, reflecting no difference in the principal nature of Ki67 staining (revised Fig. 2C).

Fig 2C: Panels mounted differently for ear and tail skin (different order to present the individual stainings, Dapi for tail skin only).

Response: We agree and have harmonized the sequence of panels in figure 2 accordingly (revised Fig. 2C).

3- LC branch analysis (Fig 1 and 2)

While Fig 1 indicates that ear skin LCs form in average twice as few branches as tail skin LCs (3-4 versus 8-9 branches per cell), Fig 2 shows the opposite (10-12 versus 6-7 branches per cell).

Is this due to a very distinct pattern between the 2 considered ages (4 weeks versus 8-10 weeks)? Could the author double-check that there is no methodological bias in their analysis?

Response: We thank the reviewer for hinting to this apparent inconsistency. Indeed, our initial analysis suffered from a bias in detecting LC dendrites, as the tissue cellularity and overall morphology significantly differs between 4-week-old and adult animals: In adult animals, the immunostainings showed a higher baseline background signal for the skin epithelium compared to P28. We had noted this beforehand and had adjusted the imaging pipeline accordingly, with a more stringent thresholding to eliminate background signals in the case of adult tissues. While we were able to detect the described ArpC4 phenotype, this strategy resulted in a reduced ability to detect dendrites (both in control and mutant tissues), explaining the seemingly reduced number of dendrites in adult vs. 4-week-old tissues.

We have double-checked both the micrographs and the corresponding quantifications and did not identify errors. Instead, our assumption -that a too high stringency for background reduction in adults caused the discrepancy- turned out correct. We now performed detailed analyses of LC morphology at 4-week and adult stages by confocal microscopy, using a 63x objective rather than a 40x objective as done previously. The new results confirm that with this approach the number of LC dendrites across these ages are largely comparable, while the phenotypes of ArpC4 loss are retained. The revised manuscript now contains a completely new analysis based on image acquisition with a 63x objective (revised Fig. 1E-G).

4- Fig 3 E-G

How many animals were examined (n=5)? Reproducible accros animals? Why was it done with 4-week animals (phenotype not complete? Event occurring before loss in numbers...)

Response: As mentioned in the figure legend for Fig. 3F we have analysed N = 4 control and N= 5 KO mice. We chose the 4-week time-point as this was the stage when the loss of LCs first became apparent (even though non-significant at this age). We aimed to learn whether changes in nuclear morphology and nuclear envelope markers represented early molecular and cellular events following ArpC4 loss. Compared to later stages, this strategy poses a reduced risk to detect indirect effects of ArpC4 loss. We added a notion in the revised manuscript text to clarify this (page 5).

Staining Lamin A/C globally more intense in the Arpc4-KO epidermis (also seems to apply to the masks corresponding to the LCs). Surprising to see that the quantification indicates a major drop of Lamin A/C intensity in the LCs.

Response: We again thank the reviewer for this careful assessment. As with many tissue stainings, there is inter-sample variability. We have now revisited the micrographs and did not find a significant global reduction of Lamin A/C in the entire epidermis (including keratinocytes/KCs). The drop of Lamin A/C intensity is restricted to ArpC4KO LCs -and not KCs- and in line with the reduced Lamin A/C expression data in DCs (Fig. 3C,D). The revised manuscript now shows more representative examples (revised Fig. 3E).

Legend Fig 4D replace confocal microscopy by STED microscopy

Response: We replaced "confocal microscopy" by "STED microscopy".

6- Figure 4F

Intensity/background of γH2Ax staining very distinct between the 2 micrographs shown for WT and Arpc4-KO epidermis.

Response: We revisited the micrographs and now selected more representative examples (revised Fig. 4I).

7- Figure 7C, F, H

Gating strategies: would be better to harmonize the style of the plots (dot plots and 2 types of contour plots have been used...)

Response: We agree and provided a harmonized plot illustration in the revised manuscript (revised Fig. 7).

8- Figure 7H

Legend of lower gating strategy seems to be wrong (KO and not WT).

Response: We thank the reviewer for pointing out this mistake. The revised Figure 7H shows a corrected figure display.

Reviewer #1 (Significance (Required)):

Strengths: the general quality of the manuscript is high. It is very clearly written and it contains a very detailed method section that would allow reproducing the reported experiments. This work entails a clear novelty in that it represents the first investigation of the role of ArpC4 in LCs. It opens an interesting perspective about specific mechanisms sustaining the maintenance of myeloid cell subsets in peripheral tissues. This work is therefore expected to be of interest for a large audience of cellular immunologists and beyond. Challenging skin function with an external trigger would lift the relevance for a even wider audience (see main point 6).

__Response: __see main point 6.

Limitations: in its current version the manuscript suffers from a lack of solidity around a few analysis (see main points on ArpC4 and Arp2/3 protein expression, nuclear envelop rupture analysis,...). It also tends to formulate a narrative centered on the ArpC4 intra-nuclear function that is not definitely proven.

The field of expertise of this reviewer is: cellular immunology and actin remodeling.

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

SUMMARY This is a study in experimental mice employing both in vitro and, importantly, in vivo approaches. EPIDERMAL LANGERHANS CELLS serve as a paradigm for the maintenance of homeostasis of myeloid cells in a tissue, epidermis in this case. In addition to well known functions of the ACTIN NETWORK in cell migration, chemotaxis, cell adherence and phagocytosis the authors reveal a critical function of actin networks in the survival of cells in their home tissue.

Actin-related proteins (Arp), specifically here the Arp2/3 complex, are necessary to form the filamentous actin networks. The authors use conditional knock-out mice where Arpc4 (an essential component of the Arp2/3 complex) is deleted under the control of CD11c, the most prominent dendritic cell marker which is also expressed on Langerhans cells. In normal mice, epidermal Langerhans cells reside in the epidermis virtually life-long. They initially settle the epidermis around and few days after birth an establish a dense network by a burst of proliferation and then they "linger on" by low level maintenance proliferation. In the epidermis of Arpc4 knock-out mice Langerhans cells also start off with this proliferative burst but, strikingly, they do not stay but are massively reduced by the age of 8-12 weeks.

The analyses of this decline revealed that

-- the shape (number of nuclear lobes) and integrity of cell nuclei was compromised; they were fragile and ruptured to some degree when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- DNA damage, as detected by staining for gamma-H2Ax or 53BP1 accumulated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- recruitment of DNA repair molecules was inhibited when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- gene signatures of interferon signaling and response were increased when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- in vivo migration of dendritic cells and Langerhans cells from the skin to the draining lymph nodes in an inflammatory setting (FITC painting of the skin) was impaired when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- the persistence of the typical dense network of Langerhans cells in the epidermis, created by proliferation shortly after birth, is abrogated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing. Importantly, this was not the case for myeloid cell populations that settle a tissue without needing that initial burst of proliferation. For instance, numbers of colonic macrophages were not affected when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing.

Thus, the authors conclude that the Arp2/3 complex is essential by its formation of actin networks to maintain the integrity of nuclei and ensure DNA repair thereby ascertaining the maintenance proliferation of Langerhans cells and, as the consequence, the persistence of the dense epidermal netowrk of Langerhans cells.

Up-to-date methodology from the fields of cell biology and cellular immunology (cell isolation from tissues, immunofluorescence, multiparameter flow cytometry, FISH, "good old" - but important - transmission electron microscopy, etc.) was used at high quality (e.g., immunofluorescence pictures!). Quantitative and qualitative analytical methods were timely and appropriate (e.g., Voronoi diagrams, cell shape profiling tools, Cre-lox gene-deletion technology, etc.). Importantly, the authors used a clever method, that they had developed several years ago, namely the analysis of dendritic cell migration in microchannels of defined widths. Molecular biology methods such as RNAseq were also employed and analysed by appropriate bioinformatic tools.

MAJOR COMMENTS:

• ARE THE KEY CONCLUSIONS CONVINCING? Yes, they are.

• SHOULD THE AUTHORS QUALIFY SOME OF THEIR CLAIMS AS PRELIMINARY OR SPECULATIVE, OR REMOVE THEM ALTOGETHER? No, I think it is ok as it stands. The authors are wording their claims and conclusions not apodictically but cautiously, as it should be. They point out explicitely which lines of investigations they did not follow up here.

• WOULD ADDITIONAL EXPERIMENTS BE ESSENTIAL TO SUPPORT THE CLAIMS OF THE PAPER? REQUEST ADDITIONAL EXPERIMENTS ONLY WHERE NECESSARY FOR THE PAPER AS IT IS, AND DO NOT ASK AUTHORS TO OPEN NEW LINES OF EXPERIMENTATION. I think that the here presented experimental evidence suffices to support the conclusions drawn. No additional experiments are necessary.

• ARE THE SUGGESTED EXPERIMENTS REALISTIC IN TERMS OF TIME AND RESOURCES? IT WOULD HELP IF YOU COULD ADD AN ESTIMATED COST AND TIME INVESTMENT FOR SUBSTANTIAL EXPERIMENTS. Not applicable.

• ARE THE DATA AND THE METHODS PRESENTED IN SUCH A WAY THAT THEY CAN BE REPRODUCED? Yes, they are.

• ARE THE EXPERIMENTS ADEQUATELY REPLICATED AND STATISTICAL ANALYSIS ADEQUATE? Yes.

__Response: __We thank the reviewer very much for assessing our work, for providing constructive suggestions, and for acknowledging the strength of the study.

MINOR COMMENTS:

• SPECIFIC EXPERIMENTAL ISSUES THAT ARE EASILY ADDRESSABLE. None

• ARE PRIOR STUDIES REFERENCED APPROPRIATELY? Essentially yes. Regarding the reduction / loss of the adult epidermal Langerhans cell network, it may be of some interest to also refer to / discuss to another one of the few examples of this phenomenon. There, the initial burst of proliferation is followed by reduced proliferation and increased apoptosis when a critical member of the mTOR signaling cascade is conditionally knocked out (Blood 123:217, 2014).

Response: We thank the reviewer for pointing out this important work. We now included the paper into the revised manuscript (page 12).

• ARE THE TEXT AND FIGURES CLEAR AND ACCURATE? Yes they are. Figures are well arranged for easy comprehension.

• DO YOU HAVE SUGGESTIONS THAT WOULD HELP THE AUTHORS IMPROVE THE PRESENTATION OF THEIR DATA AND CONCLUSIONS?

1. Materials & Methods. The authors write, regarding flow cytometry of epidermal cells: "Briefly, 1cm2 of back skin from 8-14 weeks old female wild-type and knockout littermates was dissociated in 0.25 mg/mL Liberase (Sigma, cat. #5401020001) and 0.5 mg/mL DNase (Sigma, cat.#10104159001) in 1 mL of RPMI (Sigma) and mechanically disaggregated in Eppendorf tubes, FOLLOWED BY INCUBATED for 2 h at 37 {degree sign}C." Followed by what?

__Response: __We apologize for this mistake. The text should read: "... followed by incubation for 2 h at 37 {degree sign}C and filtration using a 100µm cell strainer. Thereafter, blocking was performed in PBS supplemented with 0.5% bovine serum albumin and 2 mM EDTA at 4 {degree sign}C, followed by antibody labeling of cells in single cell suspension". The text has been corrected in the revised manuscript (page 17).

Materials & Methods. BMDC electronmicroscopy. What is "IF". Please specify.

__Response: __We also regret this mistake in the method text. It should read: "... For electron microscopy analysis, after PDMS removal, cells were fixed using 2.5% glutaraldehyde ...". The text has been corrected in the revised manuscript (page 21).

RESULTS in gene expression analyses. The authors observe some increase in apoptosis (as detected by cleaved-Caspase-3 staining). Is this observation in immunofluorescence also evident in the RNAseq data (where the IFN changes were seen), i.e., in Figure 5.

__Response: __We have checked our RNAseq data regarding any changes in apoptosis-related genes, however, apart from a few transcripts that are upregulated in ArpC4KO cells, we do not find a pronounced enrichment of apoptosis-related genes. We included volcano plot data in revised Suppl. Fig. 5H to share these DEGs.

Figure 7 F and G. Perhaps the authors may want to swap upper and lower panels in F or G, so that macrophage FACS plots and bar graphs are in the same row - ob, obiously, DC plots and bars likewise.

__Response: __We agree and have harmonized the panel sequence in the revised manuscript (revised Fig. 7F, G; panels swapped in G, display harmonized).

Figure 7H. "Gating strategy in ArpC4WT Lung (previously gated in Live CD45+ cells)" - The lower row is knock-out, not WT. This is indicated correctly in the legand, but in the figure both rows are labeled as WT.

__Response: __Indeed, the legend information is correct, but the corresponding figure panel is incorrect. We now provide a corrected version (revised Fig. 7H).

The reference by Park et al. 2021 is missing in the list.

__Response: __We have added the reference to the revised bibliography.

Figure 1D. Sure, the bar graphs are meant to say "CD11c"? The FACS plots show "CD11b".

__Response: __We have checked the panels and corrected where necessary (revised fig. 1D).

As to cDC1. In Figure 1D the FACS plot shows an absence of CD103+ cDC1 cells. In contrast, In Figure 7A-left side panel, there is not difference in cDC1 cells between WT and KO mice. Is therefore the flow cytometry plot in Figure 1D not representative regarding cDC1 cells? Correct?

__Response: __The reviewer is correct about this apparent discrepancy. We have not observed differences in the control vs. ArpC4KO cDC1 population, hence Figure 7 represents our findings. For figure 1, we have by mistake chosen a non-representative plot, with the aim of illustrating the gating strategy. We apologize for this mistake and now provide a corrected and representative FACS plot figure in the revised manuscript (revised Fig. 1D).

Reviewer #2 (Significance (Required)):

• DESCRIBE THE NATURE AND SIGNIFICANCE OF THE ADVANCE (E.G. CONCEPTUAL, TECHNICAL, CLINICAL) FOR THE FIELD. This is a conceptual advance. It adds a big step to our understanding of how immune cells in tissues (which all come from the bone marrow or are seeded before birth from embryonal hematopoietic organs such as yolk sac and fetal liver) can remain resident in these tissues. For cell types such as Langerhans cells, which establish their final population density within their tissues of residence, the presented finding convincingly buttress the role of proliferation and thereby the role for the actin-related protein complex 2/3 (Arp2/3).

• PLACE THE WORK IN THE CONTEXT OF THE EXISTING LITERATURE (PROVIDE REFERENCES, WHERE APPROPRIATE). While we know much about actin-related proteins (Arp), as correctly cited by the authors, this knowledge is derived mostly from in vitro studies. The submitted study translates the findings to an in vivo setting for the first time.

• STATE WHAT AUDIENCE MIGHT BE INTERESTED IN AND INFLUENCED BY THE REPORTED FINDINGS. Skin immunologists foremost, but these findings are of interest to the entire community of immunologists, but also cell biologists.

• DEFINE YOUR FIELD OF EXPERTISE. My expertise is in skin immunology, in particular skin dendritic cells including Langerhans cells.

We acknowledge the referee for their positive assessment of our manuscript.

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

Summary:

The manuscript identifies a role of the Arp2/3 complex, the major regulator of actin branching in cells, for controlling the homeostasis of murine Langerhans cells (LCs), a specialized subset of dendritic cells in the skin epidermis. The findings of the study are based on the analysis of CD11c-Cre Arpc4-flox mice, a conditional knockout mouse model, which interferes with Arp2/3 function in Langerhans cells and other CD11c-expressing myeloid cells, e.g. dendritic cell or macrophage subsets. By using immunofluorescence and flow cytometry analysis of epidermis and skin tissues, the authors provide a detailed analysis of LC numbers at different developmental stages (postnatal day 1, 7, 28, and adult mice) and demonstrate that Arpc4-deficiency does not interfere with the establishment of LC networks until postnatal day 28. However, LCs in ear and tail skin are substantially reduced in Arpc4-deficient mice at 8-12 weeks of age. In parallel to their in vivo model, the authors analyze cultures of bone marrow-derived dendritic cells (BMDCs) from control and CD11c-Cre Arpc4-flox mice. Arpc4-deficiency in BMDCs, which develop over 8-10 days in culture, results in nuclear shape and lamina abnormalities, as well as signs of increased DNA damage. Aspects of this phenotype are also detected in Langerhans cells in epidermal preparations. Transcriptomic analysis of BMDCs highlights a gene signature of increased expression of the interferon response pathway and alterations in cell cycle regulation. Arpc4-deficient BMDCs show increased expression of DNA damage markers and reduced expression of certain DNA repair factors. Based on these correlative findings from the BMDC model, the authors conclude that the decline in LC numbers might develop from the accumulation of DNA damage over time, which the authors phrease "pre-mature aging of Langerhans cells". Lastly, the authors show a heterogenous picture how Arp2/3 depletion affects distinct DC populations in CD11c-Cre Arpc4-flox mice. While some tissue-resident DC subsets appear normal in numbers, others are declined in numbers in the tissue. This may be related to their proliferation potential in tissues.

Major comments:

• Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

1) The authors claim that Arpc4 deficiency selectively compromises myeloid cell populations that rely on proliferation for tissue colonization (Figure 7). The presented data might give hints for such a general hypothesis, but solid experimental proof to prove this is lacking. When comparing myeloid cell subsets from foru different irgans, the authors refer to published data that some dendritic cell subsets are more proliferative in tissues than others and that CD11cCre Arpc4-flox mice appear to have reduced cell numbers in these populations. However, the presented data are purely correlative and no functional connection to cell proliferation has been made to the phenotypes. While some dendritic cell subsets (Langerhans cells, alveolar DCs) show reduced cell numbers in CD11cCre Arpc4-flox mice, other myeloid cell cells subsets are unaffected (e.g. dermal cDC1 and 2, colon macrophages).There could be plenty of other reasons that might underly the observed discrepancies between these cell subsets, e.g. Arp2/3 knockout efficiency and myeloid cell turnover in the tissue are just two examples, which have not been taken into consideration. Direct measurement of cell proliferation, e.g. BrdU labeling, and the observed phenotype would be missing to make such claims. The data could either be removed. Experimentally addressing these points could take 3-6 months.

Response and revisions: We thank the referee for bringing this point. We agree that these results give hints that support our conclusion but that do not address this question directly. However, we would like to emphasize that our conclusion is based on studies from others showing that alveolar macrophages self-maintain themselves through proliferation (Bain et al. Mucosal Immunology 2022). In contrast, it has been reported that a large fraction of colonic macrophages are derived from monocytes that are being recruited to the gut through life (Bain et al. Mucosal Immunity 2023). We now added these points in our revised manuscript. Moreover, during revision we confirmed deletion of the ArpC4 allele by genotyping PCR of FACsorted colon macrophages (revised Suppl. Fig. 7C and revised methods). In addition, we stress that we do not exclude that different intracellular Arpc4-dependent processes might contribute to the phenotypes observed (beyond maintenance of DNA integrity) (page 11). This will help mitigate our conclusions and leave open the potential implication of alternative mechanisms.

2) The authors claim that DC subsets (e.g. dermal cDCs), which develop from pre-DCs, are not affected by Arp2/3 depletion (Figure 7, although the FACS plot in Fig. 1D would suggest a different picture for cDC1). This is surprising in light of the data with bone marrow-derived DCs (BMDCs), the major in vitro model of this study, which develop from CDPs that again develop from pre-DCs. BMDCs did show aberrant nuclei and signs of DNA damage. How would the authors then explain the discrepancies of the BMDC model with DC subsets, where the authors feel that the pre-DC origin explains the phenotypic difference? This is a general concern of the data interpretation and conclusions.

__Response: __We thank the referee for bringing this point that indeed requires clarification. Two non-exclusive hypotheses could explain this apparent discrepancy:

• The ontogeny of bone-marrow-derived DCs: Depending on the protocol used, there might be variations in the precursors DCs develop from. We use one of the first protocols, which was pioneered by Paola Ricciardi-Castagnoli lab (Winzler et al. Exp.Med. 1997). It relies on a supernatant from J558 cells transfected with GMCSF, which contains additional cytokines and mainly generate DC2-like DCs. Langerhans cells are closer to DC2s, which resemble more macrophages than DC1s. We thus chose this protocol rather than the protocols that use Flt3-L, which produce both DC1s and DC2s developed from common dendritic-cell precursors (CDPs). It is thus possible that our BM-derived DCs develop from other precursor cells closer to monocyte precursors.
• As shown in Figure 5C, kinetics of acquisition of CD11c expression, and thus deletion of the Arpc4 gene, might be distinct in vivo and in vitro. In vivo, as stated in our manuscript, DCs acquire CD11c as preDCs and undergo few rounds of divisions after. In vitro, as shown by our cycling experiments, BM-derived DCs continuously cycle, so they will keep dividing after having acquired CD11c (around day 7) and deleting the Arpc4 gene. We now mentioned these hypotheses in the discussion of our revised manuscript to explain the apparent contradiction raised by the referee (pages 10 and 12).

3) In line with point 2, the authors never show that BMDCs show reduced proliferation, reduced cell numbers or increased cell death in Arpc4-deficient cell cultures, as a consequence of the detected DNA damage and impaired DNA repair. In fact, Figure 5C even shows that cell growth rates between control and KO are equal. This is a major mismatch in the current study. Since the authors use the BMDC model to explain the declining cell numbers in Langerhans cells (which derive from fetal liver cells), this phenotype is not mirrored by the BMDC culture and it remains open whether the observed changes in nuclear DNA damage and repair are indeed directly linked to the observed phenotype of declining cell numbers in the tissue. These aspects require argumentation why cell growth is unchanged in KO cells. Additional experiments addressing these points with sufficient biological replicates (cultures from different mice) could take 2-3 months, including preparation time.

__Response____: __We thank the referee for bringing this point, which was probably not properly discussed in the first version of our manuscript. Indeed, Arpc4KO BM-derived DCs do not show the premature cell death phenotype observed in LCs in vivo, as stated by the referee. There are at least two putative non-exclusive explanations for this. First, unlike LCs, which are long-lived cells, BM-derived DCs can be kept in culture for only 10-12 days. As DNA damage-induced cell death takes time (LCs only start to die about 3-4 weeks after network establishment), the lifespan of BM-DCs could simply not be long enough to observe this phenotype. Second, in the epidermis, LCs are physically constrained and continuously exposed to diverse signals that might increase their sensitivity to DNA damage and thereby induction of subsequent cell death.

We have attempted to clarify this point in our revised manuscript by providing putative explanations for the death phenotype of Arpc4-deficient LCs not being observed in BM-derived DCs. We further explained that this does not invalidate this cellular model as it was used to raise hypotheses on the putative role played by ArpC4 in myeloid cells, i.e. maintenance of DNA integrity, which was then confirmed in vivo (ArpC4KO LCs do indeed display DNA damage in the epidermis) (page 12). Without this "imperfect cellular model", we would have probably not been able to uncover this novel function of Arp2/3 in immune cells.

4) The authors refer to a "pre-mature aging" phenotype of Arpc4-deficient BMDCs and LCs, based on reductions in Lamin B, Lamin A and increases in gH2AX and 53BP1. I find this term and overstatement of the current data and suggest that other markers for cell senescence, such as p53, Rb, p21 and b-Galactosidase are then also used to make such strong claim on "aging" and cell senescence. Experimentally addressing this point with sufficient biological replicates could take 2-3 months, including preparation time.

__Response: __We now assessed senescence signatures in our RNAseq analysis of Arpc4WT and Arpc4KO-derived DCs, as suggested by the referee. These results revealed several senescence-related DEGs upregulated in ArpC4KO DCs, such as serpinB2 (revised Suppl. Fig. 5G, volcano plots) as well as a general enrichment of a senescence-related signature when using the senescence gene set (Aging Atlas Consortium, 2021; revised Fig. 5I). These data support our notion of a premature aging phenotype following ArpC4 loss in BMDCs.

5) The study does not provide a mechanism how the Arp2/3 complex would mediate the observed effects on DNA damage and repairs has not been addressed in the cell model, and only potential scenarios from other non-myeloid cell lines are discussed. It remains unclear whether the observed phenotypes in Arpc4-depleted myleoid cells relate to the direct nuclear function of Arp2/3 or the cytosolic function of Arp2/3, including its roles in cytoskeletal regulation that may have secondary effects on the nuclear alterations. This is a general concern of the presented data, data on mechanism might require more than 6 months.

__Response____: __The referee is correct: Our manuscript shows that Arp2/3 deficiency in specific myeloid cells impacts on their survival in vivo and proposes that this could result at least in part from impaired maintenance of DNA integrity in these cells. We do not know whether this also applies to non-myeloid cells, which, although very interesting, is beyond the scope of the present study. In addition, we do not have any experimental tool to distinguish whether the DNA damage phenotype of Arpc4KO cells involves the nuclear or cortical pool of F-actin, this is why we have left this question open in the discussion of our manuscript.

6) OPTIONAL: The authors make a strong case arguing that the increased interferon expression signature (based on the transcriptomics data) reflects the nuclear ruptures in Arpc4-deficient cells and adds to the observed phenotype. If this is so, what happens then in STING knockout cells in the presence of CK666 inhibitor?

__Response____: __During revision, we now tested the putative role of STING in the ArpC4-KO phenotype. We found that abrogation of STING function in ArpC4KO mice did not rescue LC survival, excluding the possibility that aberrant STING activation triggers LC loss in these animals (revised Fig. S5E,F). Therefore, we tempered our conclusion (page 7).

• Are the data and the methods presented in such a way that they can be reproduced?

1) The analyses include quite a number of intensity calculations of immunofluorescence signals (Fig. 3D, E; Fig. 4E, Fig. 5B and 6B)? The background stainings are often variable or very high. In some cases it is even unclear whether stainings are really detecting protein and go beyond background staining (Fig. 6A, Fig. 5F). How were immunofluorescence data acquired and dealt with different background staining intensities?

__Response____: __We extended our description of the microscopes used for image acquisition as well as the downstream analyses for each experiment, which indeed vary depending on the signals observed with distinct antibodies or constructs.

2) It remained unclear to me on which basis the nuclear deformations in Fig. 3G, H were calculated?

__Response____: __We also extended the mentioning of methods used to quantify nuclear deformations.

3) The detailed phenotype of control mice is a bit unclear. It appears as if these were Cre-negative animals. Did the authors have some proof-of-principle experiments showing that CD11cCre Arpc4 +/+ animals have comparable phenotypes to Cre-negative animals?

__Response____: __We have never observed any decline in LC numbers in other mouse lines/genotypes (for example in cPLA2flox/flox;CD11c-Cre mice shown in the manuscript, Fig. S6B), excluding a putative role for the Cre in LC death. To nevertheless thoroughly check this aspect, we now quantified gH2Ax immunostaining of LCs of both Cre-positive and Cre-negative animals. These analyses revealed no Cre-mediated effect on DNA damage in LCs (revised Suppl. Fig. 4E,F).

• Are the experiments adequately replicated and statistical analysis adequate?

For most experiments, the number of biological replicates (mice, or BMDC cultures from different mice) and individual values (n, cells) are indicated. Statistical analysis appears adequate.

Minor comments:

• Prior published studies on Arp2/3 function in immune cells are referenced accordingly. A number of additional pre-print manuscripts on this topic have not been cited and could be considered referencing.

__Response: __We now cited additional, relevant preprints and peer-reviewed work (page 12).

• The text is very clearly and very well written. Figures are clear and accurate for most cases. There are some open questions:

• Fig. 1B: The number of dots betwenn graph and legend do not match. The dots are not n=12 for both genotypes. Additionally: What do the symbols in the circles in the graph stand for? This is also in another later figure unclear.

• Fig. 2C: The current IF presentation (overlay MHCII with Ki67) is not very helpful. An additional image that shows only the Ki67 signal in the MHCII mask would be very helpful.

• Fig. 4B: BMDCs of which culture day were used for these experiments?

• Fig. 4A and D shows the same representative cells for two biological messages, which is only moderately convincing regarding a "general" phenotype.

• Fig. 5, B: Scale bars are missing.

__Response: __We have fixed all these points (revised Fig. 1B, 2C, 4B, 4A&D, 5B).

Reviewer #3 (Significance (Required)):

Strengths and Advance:

The study provides strong data and a very detailed analysis of how the Arp2/3 complex regulates stages of Langerhans cell development and homeostasis. The role of the Arp2/3 complex as regulator of actin branching, which is involved in many cellular functions, has previously not been reported for this cell type. Previous research in immune cells have already studied the Arp2/3 complex, but studies were focussed on its role in migration and the majority of published phenotypes related to cell migration. While there are already a number of in vitro studies showing that the Arp2/3 complex can regulate aspects of cell cycle control or cell death in non-immune cells, most of these studies were performed with immortalized, non-immune cell lines, which can be more easily manipulated to dissect mechanistic aspects of the cellular phenotype, but are limited in their physiological interpretation. Hence, it is a major strength of this study to investigate the effects of Arp2/3 in a primary immune cell type, directly in the native and physiological environment. This is important because in vitro data from other cell types cannot be easily extrapolated to any other cell type and it is critical for our understanding to collect physiological data from tissues, where the biology really happens. The finding that the Arp2/3 complex regulates the tissue-residency of Langerhans cell through processes that are unrelated to migration are partially unexpected, shifting the view of this protein complex's physiological role to other cell biological processes, e.g. regulation of cell proliferation.

Limitations: The limitations of the study are detailed in the five major points listed above. The study accumulates many experiments that characterize the phenotype of Arpc4-depleted cells, showing signs of DNA damage in Langerhans cells and cultures of BMDCs. How the Arp2/3 complex would mechanistically mediate the observed effects on DNA damage and repairs have not been addressed. It also remains open whether this is due to the effects of the Arp2/3 complex in the nucleus or the cytosol, which would be biologically extremely important to understand. Above that, there are some discrepancies regarding the phenotype of the BMDC model, which does neither entirely match the Langerhans cell phenotype in the tissue (reduced proliferation, LC derive from different progenitors), nor other endogenous DC populations, which should also derive from similar progenitors.

Audience and reviewer background:

In its current form, the manuscript will already be of interest for several research fields: Langerhans cell and dendritic cell homeostasis, immune cell trafficking, actin and cytoskeleton regulation in immune cells, physiological role of actin-regulating proteins. My own field of expertise is immune cell trafficking in mouse models, leukocyte migration and cytoskeletal regulation. I cannot judge the analysis and clustering of the bulk RNA sequencing data.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary:

• This is a study in experimental mice employing both in vitro and, importantly, in vivo approaches. EPIDERMAL LANGERHANS CELLS serve as a paradigm for the maintenance of homeostasis of myeloid cells in a tissue, epidermis in this case. In addition to well known functions of the ACTIN NETWORK in cell migration, chemotaxis, cell adherence and phagocytosis the authors reveal a critical function of actin networks in the survival of cells in their home tissue.

• Actin-related proteins (Arp), specifically here the Arp2/3 complex, are necessary to form the filamentous actin networks. The authors use conditional knock-out mice where Arpc4 (an essential component of the Arp2/3 complex) is deleted under the control of CD11c, the most prominent dendritic cell marker which is also expressed on Langerhans cells. In normal mice, epidermal Langerhans cells reside in the epidermis virtually life-long. They initially settle the epidermis around and few days after birth an establish a dense network by a burst of proliferation and then they "linger on" by low level maintenance proliferation. In the epidermis of Arpc4 knock-out mice Langerhans cells also start off with this proliferative burst but, strikingly, they do not stay but are massively reduced by the age of 8-12 weeks.

• The analyses of this decline revealed that

a) the shape (number of nuclear lobes) and integrity of cell nuclei was compromised; they were fragile and ruptured to some degree when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

b) DNA damage, as detected by staining for gamma-H2Ax or 53BP1 accumulated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

c) recruitment of DNA repair molecules was inhibited when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

d) gene signatures of interferon signaling and response were increased when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

e) in vivo migration of dendritic cells and Langerhans cells from the skin to the draining lymph nodes in an inflammatory setting (FITC painting of the skin) was impaired when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

f) the persistence of the typical dense network of Langerhans cells in the epidermis, created by proliferation shortly after birth, is abrogated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing. Importantly, this was not the case for myeloid cell populations that settle a tissue without needing that initial burst of proliferation. For instance, numbers of colonic macrophages were not affected when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing.

• Thus, the authors conclude that the Arp2/3 complex is essential by its formation of actin networks to maintain the integrity of nuclei and ensure DNA repair thereby ascertaining the maintenance proliferation of Langerhans cells and, as the consequence, the persistence of the dense epidermal netowrk of Langerhans cells.

• Up-to-date methodology from the fields of cell biology and cellular immunology (cell isolation from tissues, immunofluorescence, multiparameter flow cytometry, FISH, "good old" - but important - transmission electronmicroscopy, etc.) was used at high quality (e.g., immunofluorescence pictures!). Quantitative and qualitative analytical methods were timely and appropriate (e.g., Voronoi diagrams, cell shape profiling tools, Cre-lox gene-deletion technology, etc.). Importantly, the authors used a clever method, that they had developed several years ago, namely the analysis of dendritic cell migration in microchannels of defined widths. Molecular biology methods such as RNAseq were also employed and analysed by appropriate bioinformatic tools.

Major comments:

• ARE THE KEY CONCLUSIONS CONVINCING? Yes, they are.

• SHOULD THE AUTHORS QUALIFY SOME OF THEIR CLAIMS AS PRELIMINARY OR SPECULATIVE, OR REMOVE THEM ALTOGETHER? No, I think it is ok as it stands. The authors are wording their claims and conclusions not apodictically but cautiously, as it should be. They point out explicitely which lines of investigations they did not follow up here.

• WOULD ADDITIONAL EXPERIMENTS BE ESSENTIAL TO SUPPORT THE CLAIMS OF THE PAPER? REQUEST ADDITIONAL EXPERIMENTS ONLY WHERE NECESSARY FOR THE PAPER AS IT IS, AND DO NOT ASK AUTHORS TO OPEN NEW LINES OF EXPERIMENTATION. I think that the here presented experimental evidence suffices to support the conclusions drawn. No additional experiments are necessary.

• ARE THE SUGGESTED EXPERIMENTS REALISTIC IN TERMS OF TIME AND RESOURCES? IT WOULD HELP IF YOU COULD ADD AN ESTIMATED COST AND TIME INVESTMENT FOR SUBSTANTIAL EXPERIMENTS. Not applicable.

• ARE THE DATA AND THE METHODS PRESENTED IN SUCH A WAY THAT THEY CAN BE REPRODUCED? Yes, they are.

• ARE THE EXPERIMENTS ADEQUATELY REPLICATED AND STATISTICAL ANALYSIS ADEQUATE? Yes.

Minor comments:

• SPECIFIC EXPERIMENTAL ISSUES THAT ARE EASILY ADDRESSABLE. None

• ARE PRIOR STUDIES REFERENCED APPROPRIATELY? Essentially yes. Regarding the reduction / loss of the adult epidermal Langerhans cell network, it may be of some interest to also refer to / discuss to another one of the few examples of this phenomenon. There, the initial burst of proliferation is followed by reduced proliferation and increased apoptosis when a critical member of the mTOR signaling cascade is conditionally knocked out (Blood 123:217, 2014).

• ARE THE TEXT AND FIGURES CLEAR AND ACCURATE? Yes they are. Figures are well arranged for easy comprehension.

• DO YOU HAVE SUGGESTIONS THAT WOULD HELP THE AUTHORS IMPROVE THE PRESENTATION OF THEIR DATA AND CONCLUSIONS?

• Materials & Methods. The authors write, regarding flow cytometry of epidermal cells: "Briefly, 1cm2 of back skin from 8-14 weeks old female wild-type and knockout littermates was dissociated in 0.25 mg/mL Liberase (Sigma, cat. #5401020001) and 0.5 mg/mL DNase (Sigma, cat.#10104159001) in 1 mL of RPMI (Sigma) and mechanically disaggregated in Eppendorf tubes, FOLLOWED BY INCUBATED for 2 h at 37 {degree sign}C." Followed by what?

• Materials & Methods. BMDC electronmicroscopy. What is "IF". Please specify.

• RESULTS in gene expression analyses. The authors observe some increase in apoptosis (as detected by cleaved-Caspase-3 staining). Is this observation in immunofluorescence also evident in the RNAseq data (where the IFN changes were seen), i.e., in Figure 5.

• Figure 7 F and G. Perhaps the authors may want to swap upper and lower panels in F or G, so that macrophage FACS plots and bar graphs are in the same row - ob, obiously, DC plots and bars likewise.

• Figure 7H. "Gating strategy in ArpC4WT Lung (previously gated in Live CD45+ cells)" - The lower row is knock-out, not WT. This is indicated correctly in the legand, but in the figure both rows are labeled as WT.

• The reference by Park et al. 2021 is missing in the list.

• Figure 1D. Sure, the bar graphs are meant to say "CD11c"? The FACS plots show "CD11b".

• As to cDC1. In Figure 1D the FACS plot shows an absence of CD103+ cDC1 cells. In contrast, In Figure 7A-left side panel, there is not difference in cDC1 cells between WT and KO mice. Is therefore the flow cytometry plot in Figure 1D not representative regarding cDC1 cells? Correct?

Significance

• DESCRIBE THE NATURE AND SIGNIFICANCE OF THE ADVANCE (E.G. CONCEPTUAL, TECHNICAL, CLINICAL) FOR THE FIELD. This is a conceptual advance. It adds a big step to our understanding of how immune cells in tissues (which all come from the bone marrow or are seeded before birth from embryonal hematopoietic organs such as yolk sac and fetal liver) can remain resident in these tissues. For cell types such as Langerhans cells, which establish their final population density within their tissues of residence, the presented finding convincingly buttress the role of proliferation and thereby the role for the actin-related protein complex 2/3 (Arp2/3).

• PLACE THE WORK IN THE CONTEXT OF THE EXISTING LITERATURE (PROVIDE REFERENCES, WHERE APPROPRIATE). While we know much about actin-related proteins (Arp), as correctly cited by the authors, this knowledge is derived mostly from in vitro studies. The submitted study translates the findings to an in vivo setting for the first time.

• STATE WHAT AUDIENCE MIGHT BE INTERESTED IN AND INFLUENCED BY THE REPORTED FINDINGS. Skin immunologists foremost, but these findings are of interest to the entire community of immunologists, but also cell biologists.

• DEFINE YOUR FIELD OF EXPERTISE. My expertise is in skin immunology, in particular skin dendritic cells including Langerhans cells.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Shahbazi et al used a recurrent neural network model trained to control a musculoskeletal model of the arm to investigate how neural populations accommodate activity patterns underpinning savings. The paper draws upon the recent finding of a "uniform shift" in preparatory activity in monkey motor cortex associated with savings, and leverages full access to a computational model to establish causality.

Strengths:

The paper is well written, and the figures are clearly presented. The key finding that the uniform shift first reported based on neural recordings by Sun et al. emerges in artificial neural networks performing a similar task is interesting and well-backed by their analyses. Manipulating this uniform shift to show that it drives behavioural savings is an important causal confirmation of the proposal by Sun et al.

Weaknesses / Comments:

As mentioned earlier, the core results are well backed by the analyses. Most of my comments relate to adding more controls and additional questions that could be explored with the model to strengthen the paper.

(1) Savings are quantified as more rapid relearning of the FF upon re-exposure (e.g., Figure 3). This finding is based on backpropagation through time, but would this hold when using a different optimiser, e.g., FORCE?

This is an interesting question, and indeed, there are an increasing number of studies addressing how different neural network learning rules may affect the kinds of representations that arise after learning (Codol et al., 2024). However the focus of the present paper is not on which neural network approaches or which specific optimisers produce savings, rather, the focus is on the basis and neural geometry of savings when it emerges.

We have added a short paragraph to the Discussion section [lines 349-355] to address this:

“The present results are based on RNNs trained in an error-based approach using backpropagation through time (Werbos, 1990) using the Adam optimizer (Kingma and Ba, 2014). Other techniques for training RNNs have been proposed including the FORCE algorithm (Sussillo and Abbott, 2009). In addition, several recent reports have demonstrated success using reinforcement learning approaches to train neural networks in the context of sensorimotor control tasks (Lillicrap et al., 2015; Codol et al., 2024a). An interesting avenue for future work is to determine how the present results may or may not generalize to different neural network architectures and learning rules.”

(2) The authors should include a "null model" showing that training on a different reaching task following NF, as opposed to FF2, won't show something akin to a uniform shift during preparation due to the adoption of TDR and having similar targets.

This is a critical point. Training on a different reaching task other than FF2 (e.g. a different force field) will indeed result in a uniform shift, but critically, a shift in a different direction in neural state space than the uniform shift associated with FF2. The central focus of the present paper is to show that when there remains a non-zero projection of preparatory neural activity along the direction of the uniform shift associated with a given learning task, this residual projection underlies savings when networks are subsequently re-exposed to the same task.

In the Results section we had included a short paragraph to describe control simulations that we performed that address this concept. We have expanded this text and added a Figure and the results of statistical tests to better describe this control [lines 179-187]:

“As an additional control we trained networks after the growing up phase on an opposing force field (CCW) and then as above, exposed the networks to a NF washout phase, and then to a CW force field. In this case no savings was observed in the CW force field, either for initial lateral deviation, or for learning rate (Figure 3). In fact, we observed that initial lateral deviation is larger for the novel force field (t(39)=-4.918, p=1.6e-5). This observation is in line with the finding that learning opposing force fields sequentially results in interference (Sun et al., 2022). The results of these control simulations underscore that the savings effect observed in our main study was learning-specific—it was due to prior learning of the CCW force field, and not a general effect of learning any novel dynamics.”

(3) The analyses of network activity during movement preparation (Figure 4) nicely replicate the key finding in Sun et al, but I think the authors could leverage the full access to their network and go further, e.g., by examining changes (or the lack of) during execution in FF2 with respect to FF (and perhaps in a future NF2 with respect to NF), including whether execution activity lives also lives in parallel hyperplanes, etc.

We agree that a visualization of the neural activity during movement would be beneficial to the reader. To address this we have added a new Figure (Fig. 6) and associated text [lines 210-219]. The Figure shows the neural trajectories when the RNNs are first exposed to the FF1 and when they are first exposed to FF2 (after NF2 washout). Trajectories are plotted in 3D corresponding to the first 3 principal components, starting at the go cue and ending 200 ms into the movement, for each of the 8 movement targets.

“The neural trajectories for preparation and for movement can be visualized in principal component space. Figure 6 shows trajectories during planning and early execution for initial FF1 and FF2 exposure. Hidden unit activity was subjected to a principal components analysis, and neural trajectories within the first three PCs are shown for movements to each of the eight movement targets. Filled circles indicate neural state 200 ms prior to the go cue. During the preparatory period trajectories travel along PC1 and then disperse across PC2 and PC3 into the circular pattern indicated by the filled stars, which indicate time of the go cue (also see Figure 5A). After the go cue neural trajectories shift back along PC1 and rotate along oscillatory patterns characteristic of populations of motor cortical neurons in non-human primates during movement (Churchland and Shenoy, 2024).”

(4) Related to the above, while the results are interesting and the paper is well done, I kept wishing that the authors had done "more" with their model. This could be one or two final sections on "predictions" that would nicely complement their "validation" of the uniform shift, and that, in my opinion, would greatly increase the impact of the paper. In particular:

(a) What would be the effect of learning more "tasks"? For example, is there a limit on how many fields can be learned? (You show something related by manipulating network size, but this is slightly different.)

These are interesting questions and to some extent they are already addressed in the paper. Of course, the number of tasks that a network is able to learn, will be related to how much those tasks overlap in a control space. Indeed, this idea goes back to early theoretical accounts of connectionist models such as Hopfield nets and capacity for representing information (Hopfield, 1982; Hopfield et al., 1983). The control simulations that we described in the paper [lines 179-187 and Figure 4] are a test of one extreme version of this, in which two tasks are in direct opposition to each other (opposite force fields), and in this situation no savings emerges. We believe it is an interesting question, but beyond the scope of the present paper to undertake a comprehensive exploration of the nature of task-overlap in upper limb reaching learning tasks.

(b) Figure 5 is a nice causal demonstration that the uniform shift is related to savings. However, and related to comment #3, it'd be interesting to see more details about how the behaviour and the network activity changes as preparatory activity shifts along this axis, in particular regarding how moving the preparatory states affect the organisation and dynamics of upcoming execution activity -these are the kind of intuitions that modelling studies like this one can provide.

This has been addressed above by the changes we made to address the reviewer’s comment #3.

(c) The authors focus on a task design that spans baseline, FF, NF, FF2 to replicate the original study by Sun et al. However, it would be interesting if they generated predictions for neural changes to other types of tasks that have been studied behaviourally. These could include, for example: (i) modelling a visuomotor rotation or a mirror reversal task; (ii) having to adapt to a FF in the opposite direction; (iii) investigating the role of adding an explicit context and having the networks learn multiple FF; and (iv) trying to learn FF fields in opposite directions, perhaps restricted to specific targets. As the authors know, all these questions and more have been studied with similar behavioural paradigms, and it would be nice to see what neural predictions are generated by this model.

See responses above e.g. to comment 4. We have clarified the text and provided a new Figure to illustrate our opposite FF control simulations. The other suggestions about visumotor rotations, and contextual cues, are interesting and potentially important questions that we are working on, but we believe are beyond the scope of the current paper which is focused specifically around the question of savings in FF learning.

(5) On the Discussion: When extrapolating from neural network results to animals, the fact that your networks can learn implicitly doesn't mean that animals do learn implicitly. Indeed, I think the consensus view is that different perturbations may lead to the expression of different types of savings (e.g., FF vs VR, which seems to be more explicit). Besides, these different mechanisms may be primarily implemented by brain regions less directly tied to motor control (e.g., cerebellum, parietal cortex?), which are not directly implemented in the authors' model.

Of course the reviewer is correct that our simulations are not evidence that savings in motor tasks learned by animals is only implicit, and we do not make any such claims in the paper. The model we describe in the present paper is not meant to be a comprehensive model of motor learning in humans/animals. Indeed, the pure “context free” type of learning that we implement in our simulations basically cannot occur in animals, because there is always some information that provides contextual information. Indeed there are computational models of motor learning that include these effects, e.g. the COIN model (Heald et al., 2021). Our model however provides a useful window into what the context-free component of savings may look like. The approach we describe in the present paper is a powerful way to probe the context-free component of savings in isolation in a way that is not possible (at least not readily) in animals/humans. We have modified the text in the Discussion [lines 372-379] to better articulate this point.

“The simulations described here do not constitute evidence that savings in motor learning tasks is exclusively implicit in animals and humans. The purely context-free learning implemented in our simulations is highly unrealistic, as some form of contextual information is invariably available. Indeed, computational models of motor learning that incorporate contextual effects already exist, e.g. (Heald et al. 2021). Nevertheless, our simulations provide a useful window into what the context-free component of savings may look like. This approach offers a powerful means of probing the context-free component of savings in isolation—something that is not readily achievable in animal or human experiments.”

Reviewer #2 (Public review):

Summary:

Shahbazi et al. trained recurrent neural networks (RNNs) to simulate human upper limb movement during adaptation to a force field perturbation. They demonstrated that throughout adaptation, the pattern of motor commands to the muscles of the simulated arm changed, allowing the perturbed movements to regain their typical, perturbation-free straight-line paths. After this initial learning block (FF1), the network encountered null-fields to wash out the adaptation, before re-experiencing the force in a second learning block (FF2). Upon re-exposure, the network learned faster than during initial learning, consistent with the savings observed in behavioral studies of adaptation. They also found that as the number of hidden units in the RNN increased, so did the probability of exhibiting savings. The authors concluded that these results propose a neural basis for savings that is independent of context and strategic processes.

Strengths:

The paper addresses an important and controversial topic in motor adaptation: the mechanism underlying motor memory. The RNN simulation reproduces behavioral hallmarks of adaptation, and it provides a useful illustration of the pattern of muscle activity underlying human-like movements under both normal and perturbing conditions. While the savings effect produced by the network, though significant, appears somewhat small, the simulation demonstrating an increase in savings with a greater number of hidden units is particularly intriguing.

Weaknesses:

(1) To be transparent, savings in motor adaptation have been a primary focus of my own research. Some core findings presented in this paper are at odds with the ideas I and others have previously put forward. While I don't want to impose my agenda on the authors of this paper, I do think the authors should address these issues.

(a) The authors acknowledge the ongoing debate in the literature regarding the mechanisms underlying savings, particularly whether it stems from explicit or implicit learning processes. However, it remains unclear how the current work addresses this debate. There is already a considerable body of research, particularly in visuomotor adaptation, demonstrating that savings is predominantly driven by explicit strategies. For example, when people are asked to report their strategy, they recall a strategy that was useful during the first learning block (Morehead et al. 2015). Furthermore, savings are abolished under experimental manipulations designed to eliminate strategic contributions (e.g., Haith et al., 2015; Huberdeau et al., 2019; Avraham et al., 2021). The authors briefly state that their findings support the hypothesis that a neural basis of memory retention underlying savings can be independent of cognitive or strategic learning components, and that savings can be characterized as implicit. While these statements may be true, it is not clear how this work substantiates these claims.

We have addressed a similar point raised by Reviewer 1, see point #5 above. Our work represents an example of how savings can occur from implicit mechanisms in the absence of explicit contextual cues. Our goal is not to resolve the debate about how this occurs in humans/animals. Rather, our model provides a useful window into what the context-free component of savings may look like. Our approach is a powerful way to probe the context-free component of savings in isolation in a way that is not possible (at least not readily) in animals/humans. We have modified the text in the Discussion [lines 372-379] to better articulate this point.

“The simulations described here do not constitute evidence that savings in motor learning tasks is exclusively implicit in animals and humans. The purely context-free learning implemented in our simulations is not meant to be a full model of biological learning, as in biological systems some form of contextual information is invariably available. Indeed, computational models of motor learning that incorporate contextual effects already exist, e.g. (Heald et al. 2021). Nevertheless, our simulations provide a useful window into what the context-free component of savings may look like. This approach offers a powerful means of probing the context-free component of savings in isolation—something that is not readily achievable in animal or human experiments.”

(b) Our research has also demonstrated that if implicit adaptation is completely washed out after the initial learning block, it not only fails to exhibit savings but is actually attenuated relative to the first learning block (Avraham et al., 2021). This phenomenon of attenuation upon relearning can also be seen in other studies of visuomotor adaptation (e.g., Leow et al., 2020; Yin and Wei, 2020; Hamel et al., 2021; Hamel et al., 2022; Wang and Ivry, 2023; Hadjiosif et al., 2023). More recently, we have shown that this attenuation is due to anterograde interference arising from the experience with the washout block experience (Avraham and Ivry, 2025). We illustrated that the implicit system is highly susceptible to interference; it doesn't require exposure to salient opposite errors and can occur even following prolonged exposure to veridical feedback. The central thesis of this paper, namely that implicit savings can emerge through RNNs, is at odds with these empirical results. The authors should address this discrepancy.

These empirical results are interesting and intriguing, and we agree that they are relevant in the context of the debate about the relative contributions and interactions between explicit and implicit learning systems and savings. Importantly, contextual interference is impossible in our model, since there are no contextual cues about which force field is present or absent. Interactions between an explicit system and an implicit learning system are also impossible in our model, since there is no possibility of context-driven explicit learning or memory. The approach we have taken in the present paper is not to model a full explicit plus implicit learning system but rather to probe how savings may emerge from a purely implicit learning mechanism alone and to compare the neural geometry underlying this implicit-drive savings to the neural recording results from monkey electrophysiology studies. Nevertheless we have added some text to the Discussion [lines 380-391] to situate our findings in the context of the studies mentioned above by the reviewer.

“Recent empirical work suggests that relearning after washout of implicit adaptation can be attenuated rather than facilitated, a phenomenon attributed to anterograde interference from the washout phase (Avraham et al., 2021; Hadjiosif et al., 2023; Hamel et al., 2022, 2021; Leow et al., 2020; Wang and Ivry, 2025; Yin and Wei, 2020). The savings observed in our simulations differs from these behavioral findings. Crucially, our model excludes both contextual interference (since no cues signal which force field is present) and explicit-implicit interactions (since context-driven explicit learning is absent). Our goal was not to model a complete explicit-implicit system, but rather to probe how savings may emerge from a purely implicit mechanism and to compare the underlying neural geometry to monkey electrophysiology data. Our results suggest that high-dimensional neural circuits possess an intrinsic capacity for savings via persistent preparatory traces. How and when this capacity may be masked by interference or explicit-implicit interactions in biological systems remains an open question for future work.”

(2) This brings me to the question about neural correlates: The results are linked to activity in the primary motor cortex. How does that align with the well-established role of the cerebellum in implicit motor adaptation? And with the studies showing that savings are due to explicit strategies, which are generally associated with prefrontal regions?

The modeling approach we use in the present paper is area agnostic, and we do not include different neural modules to represent specific brain areas such as cerebellum or prefrontal regions. In the current approach we specifically exclude explicit strategies, as a way to specifically probe implicit mechanisms alone. Also see response to reviewer 1 comment 5 above.

(3) The analysis on the complexity of the neural network (i.e., the number of hidden units) and its relationship to savings is very interesting. It makes sense to me that more complex networks would show more savings. I'm not sure I follow the author's explanation, but my understanding is that increased network complexity makes it more difficult to override the formed memory through interference (e.g., from the experience with NF2). Also, the results indicate that a network with 32 units led to a less-than-chance level of networks exhibiting savings (Figure 3b). What behavioral output does this configuration produce? Could this behavior manifest as attenuation upon relearning? Furthermore, if one were to examine an even smaller, simpler network (perhaps one more closely reflecting cerebellar circuits), would such a model predict attenuation rather than savings?

These are interesting questions, and are potentially important, for future work to explore. Our interpretation of the results of smaller networks is that these small RNNs fail to show savings presumably because the learned FF behavior is 'erased' during washout because of the limited capacity to retain the FF learning in a distinct neighborhood in neural state space. Our paper is focused specifically on the relationship between savings, implicit learning, and neural capacity via network size, in the context of the monkey electrophysiology results in motor cortex. It would be interesting in future work to explore a cerebellar-like modeling approach.

(4) The authors emphasize that their network did not receive any explicit contextual signals related to the presence or absence of the force field (FF), thus operating in a 'context-free' manner. From my understanding, some existing models of context's role in motor memories (e.g., Oh and Schweighofer, 2019; Heald et al., 2021) propose that memory-related changes can be observed even without explicit contextual information, as contextual changes can be inferred from sudden or significant environmental shifts (e.g., the introduction or removal of perturbations). Given this, could the observed savings in the current simulation be explained by some form of contextual retrieval, inferred by the network from the re-presentation of the perturbation in FF2?

It is important to note that this is not possible in the context of the modeling approach described in the present paper. For example, in trial 1 of FF2, because the network has no contextual cue signaling the FF’s presence, the network has no information before movement begins that a FF will be present during movement (recall that the FF is velocity-dependent, and so is zero before movement begins). Once the network encounters the FF during movement, some component of its response I suppose could be described as contextual inference derived from effector state (similar to the account described in the COIN model), but strictly speaking the model is only responding to what it encounters in the moment. Any change in behaviour due to prior learning (e.g. savings) is due to the interaction between the residual learning-related neural state (e.g. the uniform shift), the effector state in the moment, and the errors encountered during movement. We don’t interpret this as “inference” in the traditional sense of an explicit learning system.

(5) If there is residual hidden unit activity related to the FF at the end of the NF2 phase, how does the simulated movement revert back to baseline? Are there any differences in the movement trajectory, beyond just lateral deviation, between NF1 and NF2? The authors state that "changes in the preparatory hidden unit activity did not result in substantive changes in the motor commands (Figure 5b), which emphasizes that the uniform shift resides in the null space of motor output." However, Figure 5b appears to show visible changes in hidden unit activity. Don't these changes reflect a pattern of muscle activity that is the basis for behavior? These changes are indeed small, but it seems that so is the effect size for savings (Figure 3a). Could this suggest that there is not, in fact, a complete washout of initial learning during NF2 within the network?

This is precisely the point of the paper, i.e. to show that neural activity during the preparatory period before movement onset is different, even though the behaviour during the preparatory period is the same (i.e. no muscle activity and no movement). This recapitulates the empirical findings from the neural data reported in the Sun et al. (2022) paper.

The reviewer asks “Don't these changes reflect a pattern of muscle activity that is the basis for behavior?” Yes indeed they do, but not during the NF and not during the preparatory activity prior to movement onset.

The reviewer asks “Could this suggest that there is not, in fact, a complete washout of initial learning during NF2 within the network?” We addressed this in the paper (Results/Washout) by comparing kinematics after washout to that prior to FF learning; e.g. any differences in lateral deviation of the hand path for the entire reach trajectory was in the range of 0.1 mm, which is less than 0.25 % of the lateral deviation encountered in the FF and only 0.1 % of the reach distance (10 cm).

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Figure 1c, lower panel: Is this from the early or late stage of FF1?

This is an example movement after learning in a null field (NF). We have clarified this in the Figure caption.

(2) Please clarify what the two panels in Figure 1e represent.

We have clarified in the Figure caption that these are activity from two example hidden units.

(3) If Figure 2c is intended to illustrate the changes in motor commands for individual muscles, consider reorganizing the plots by muscle to more clearly show the change for each muscle from NF1 to FF1.

The point here is not to make fine-grained comparisons between specific muscles, rather to show a general example of how muscle activity is different. For the sake of visual simplicity in a Figure that already has many components we have decided to keep Figure 2c the same.

(4) The text mentions that no savings were observed when the network was trained on CCW followed by CW perturbations. However, no data or statistical analysis is presented to support this claim. I wonder if the authors would expect attenuated learning when exposed to the CW perturbation, given a memory of the opposite perturbation.

We have added a Figure to provide data for the FF opposite control.

(5) The relevance of the discussion on choking under pressure to the paper wasn't clear.

We have modified the relevant text in the Discussion section [lines 356-363] to clarify the relevance of the present work to other recent work on how complex features of motor behaviour can arise due to the dynamics of preparatory neural activity in motor cortex.

References

Avraham G, Morehead JR, Kim HE, Ivry RB. 2021. Reexposure to a sensorimotor perturbation produces opposite effects on explicit and implicit learning processes. PLoS Biol 19:e3001147. doi:10.1371/journal.pbio.3001147

Codol O, Krishna NH, Lajoie G, Perich MG. 2024. Brain-like neural dynamics for behavioral control develop through reinforcement learning. bioRxiv. doi:10.1101/2024.10.04.616712

Hadjiosif AM, Morehead JR, Smith MA. 2023. A double dissociation between savings and long-term memory in motor learning. PLoS Biol 21:e3001799. doi:10.1371/journal.pbio.3001799

Hamel R, Dallaire-Jean L, De La Fontaine É, Lepage JF, Bernier PM. 2021. Learning the same motor task twice impairs its retention in a time- and dose-dependent manner. Proc Biol Sci 288:20202556. doi:10.1098/rspb.2020.2556

Hamel R, Lepage J-F, Bernier P-M. 2022. Anterograde interference emerges along a gradient as a function of task similarity: A behavioural study. Eur J Neurosci 55:49–66. doi:10.1111/ejn.15561

Heald JB, Lengyel M, Wolpert DM. 2021. Contextual inference underlies the learning of sensorimotor repertoires. Nature 600:489–493. doi:10.1038/s41586-021-04129-3

Hopfield JJ. 1982. Neural networks and physical systems with emergent collective computational abilities. Proc Natl Acad Sci U S A 79:2554–2558. doi:10.1073/pnas.79.8.2554

Hopfield JJ, Feinstein DI, Palmer RG. 1983. “Unlearning” has a stabilizing effect in collective memories. Nature 304:158–159. doi:10.1038/304158a0

Leow L-A, Marinovic W, de Rugy A, Carroll TJ. 2020. Task errors drive memories that improve sensorimotor adaptation. J Neurosci 40:3075–3088. doi:10.1523/JNEUROSCI.1506-19.2020

Wang T, Ivry RB. 2025. Contextual effects during sensorimotor adaptation are an emergent property of population coding in a cerebellar-inspired model. Sci Adv 11:eadr4540. doi:10.1126/sciadv.adr4540

Yin C, Wei K. 2020. Savings in sensorimotor adaptation without an explicit strategy. J Neurophysiol 123:1180–1192. doi:10.1152/jn.00524.2019

Problem ownership is an important tool of communication for parents to take a moment and think who is truly upset by an issue, them or the child. This is used to prevent unnecessary conflict and allows the child to learn responsibility for their actions as the parent offers advice, but doesn't take full control of the issue.

Key takeaway: As a parent its likely easy to get upset on the behalf of the child and try to take responsibility for the problem, but the parent should instead try to help the child reflect on it and solve it themselves.

Example: A child tells their parent a problem and the parent immediately wants to try solving it themselves, but they realize theyre getting too worked up about it and instead asks the child to tell them what happened and gives advice on how to go about it.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors test the hypotheses, using an effort-exertion and an effort-based decision-making task, while recording brain dynamics with EEG, that the brain processes reward outcomes for effort differentially when they earned for themselves versus others.

Strengths:

The strengths of this experiment include what appears to be a novel finding of opposite signed effects of effort on the processing of reward outcomes when the recipient is self versus others. Also, the experiment is well-designed, the study seems sufficiently powered, and the data and code are publicly available.

Weaknesses:

There is some concern about the fact that participants report feeling less subjective effort, but also more disliking of tasks when they were earning rewards for others versus self. The concern is that participants worked with less vigor during self-versus-others trials and this may partly account for a key two-way Recipient x Effort interaction on the size of the Reward Positivity EEG component. Of note, participants took longer to complete tasks when working for others. While it is true that, in all cases, participants met the requisite task demands (they pressed the required number of buttons) they did so more sluggishly when earning rewards for others. The Authors argue that this reflects less motivation when working for others, which is a plausible explanation. The Authors also try to rule out this diminished vigor as a confounding explanation by showing that the two way interaction remains even when including reaction times (and also self-reported task liking) as a covariate. Nevertheless, it is possible that covariates do not fully account for the effects of differential motivation levels which would otherwise explain the two-way interaction. As such, I think a caveat is warranted regarding this particular result.

We thank Reviewer #1 for the continued positive assessment and for continuing to highlight the caveat regarding the potential influence of differential vigor on the observed RewP interaction effects.

We agree that a caveat is warranted. As detailed in our previous response (R5), we had already conducted control analyses addressing this concern; however, we acknowledge that these results were not incorporated into the manuscript itself. We have now addressed this by adding the covariate analyses to the Result section, along with an explicit caveat in the Discussion.

Before describing the specific revisions, we would like to offer a minor clarification: the covariates in our control analyses were trial-by-trial response speed and self-reported effort ratings, rather than task liking ratings as noted in the summary above. Neither response speed nor effort rating predicted RewP amplitudes, and the critical Recipient × Effort and Recipient × Effort × Magnitude interactions remained significant and essentially unchanged. However, as the reviewer rightly pointed out, covariates may not fully capture the effects of differential motivation. Specifically, we have made the following revisions:

First, we added the covariate control analyses to the Result section: “To rule out the possibility that the differential vigor between self- and other-benefiting trials drove the Recipient × Effort and Recipient × Effort × Magnitude interactions on the RewP, we conducted two control analyses by including trial-by-trial response speed and subjective effort ratings as separate covariates in the RewP model. Neither response speed (b = -0.07, p = .641) nor effort rating (b = 0.10, p = .186) predicted RewP amplitudes, and the critical Recipient × Effort and Recipient × Effort × Magnitude interactions remained significant and essentially unchanged (see Supplementary Table S3 for full regression estimates)” (page 12, para. 1).

Second, we added a caveat to the Discussion section acknowledging this alterative explanation, which reads, “Another concern is that participants exhibited less vigor when working for others, as indicated by slower response speed and lower subjective effort ratings for other- versus self-benefiting trials. Although our control analyses confirmed that neither covariate predicted RewP amplitudes and the critical interactions remained significant, covariates may not fully capture the effects of differential motivation, and this alternative explanation cannot be entirely ruled out” (page 22, para. 2, lines 9–12; page 23, para. 1).

Reviewer #2 (Public review):

Summary:

Measurements of the reward positivity, an electrophysiological component elicited during reward evaluation, have previously been used to understand how self-benefitting effort expenditure influences processing of rewards. The present study is the first to complement those measurements with electrophysiological reward after-effects of effort expenditure during prosocial acts. The results provide solid evidence that effort adds reward value when the recipient of the reward is the self but discounts reward value when the beneficiary is another individual.

Strengths:

An important strength of the study is that amount of effort, the prospective reward, the recipient of the reward, and whether the reward was actually gained or not were parametrically and orthogonally varied. In addition, the researchers examined whether the pattern of results generalized to decisions about future efforts. The sample size (N=40) and mixed-effects regression models are also appropriate for addressing the key research questions. Those conclusions are plausible and adequately supported by statistical analyses.

We sincerely appreciate Reviewer #2’s positive evaluation of our manuscript and thank the reviewer for recognizing the strength of our experimental design and analysis approach.

Author response:

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

eLife Assessment

This important study concerns the propagation of waves in bacterial biofilms, bridging active matter physics and bacterial biophysics. While the experimental observations are solid, the theoretical interpretation and model validation are currently incomplete and require further refinement. This work will be of interest to microbiologists, biophysicists, and researchers studying collective behavior in biological systems.

In the revised manuscript, we have added new experimental results that strengthen the connection between our observations and the modeling framework used to interpret the collective oscillations. We have not introduced a new theoretical model; rather, we employed established active matter models and sought to link the observed phenomena to these frameworks. In particular, our new data demonstrate that the transition between the motile and biofilm-forming states specifically modulates the elasticity and elasto active coupling of the bacterial structure. This behavior is in excellent agreement with the predictions of the active solid model. All the experimental details are given below. We believe that the revised version of the manuscript now establishes this connection more clearly and convincingly.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Overall, this is an interesting paper. The authors have found multiple experimental knobs to perturb a mechanical wave behavior driven by pilli feedback. The authors framed this as nonreciprocal interactions - while I can see how nonreciprocity could play a role - what about mechanical feedback? Phenomenological models are fine, but a lack of mechanistic understanding is a weakness. I think it will be more interesting to frame the model based on potential mechanochemical feedback to understand microscopic mechanisms. Regardless, more can be done to better constrain the model through finding knobs to explain experimental observations (in Figures 3, 4, 5, and 7).

We thank the reviewer for the positive assessment and for highlighting this important point. The reviewer is correct that the phenomenological Kuramoto-based model does not explicitly show the detailed cell–cell interactions. However, the active solid model is formulated on detailed elastic couplings and active forces, which inherently represent mechanical feedback within the biofilm structure. In this framework, nonreciprocity emerges naturally from the tensorial nature of active forces between bacteria—a concept already well established in the active matter literature. Importantly, this mechanism is purely mechanical and closely parallels nonreciprocal hydrodynamic interactions among active particles, which also arise from tensorial couplings.

In our system, elastic interactions within the biofilm matrix, combined with pilus-generated active forces, provide a natural origin for nonreciprocal interactions. To further validate this, we improved our imaging to record single-cell dynamics both at the colony edge and on the biofilm surface. (new supplementary Video). These experiments show that motile bacteria at the leading edge of the biofilm structure do not generate waves, whereas stationary bacteria within the biofilm display local oscillations within the elastic network. This observation supports the view that collective oscillations are a property of the elastic biofilm state rather than of freely motile cells.

Moreover, the main control parameter for these oscillations is the ratio between elastic strength and the active force generated by pili. In the active solid model, this ratio is captured by the parameter π and alpha terms. Experimentally, we can tune this ratio simply by adding or removing water from the biofilm, thereby modulating its elasto active coupling. We further motivated the controllability of this feature experimentally. We let the plate dry nonuniformly and observed that the transition between spiral target and plane waves could emerge spontaneously across the plate (see Figure 3a). This observation also states the importance of moisture in the biofilm. Starting from this point we established the connection between experimental observation and modelling. In our new simulations we also noticed that the transition from spiral to target wave is particularly driven by merging processes of different topological charges +/- 1 spiral pairs. This critical point was also confirmed by modelling which links the process to elasto active coupling. Further we supported our claim by imagining the edge and the biofilm structure. These new results clarify that elastic structure of the biofilm is critically important (Supplementary Figure 3). We have clarified this mechanistic link in the revised manuscript and rewritten the relevant sections to make this connection explicit.

Modification in the manuscript:

“To gain deeper insight into the mechanisms underlying wave formation, we imaged the dynamics of individual bacteria from the fingering regions toward the center of the biofilm. This distinction is critical because, unlike the biofilm center, the edges do not generate waves. We observed that bacteria near the fingering regions remain motile and exhibit collective flow. In contrast, bacteria at the biofilm center are surface-attached and undergo periodic lifting motions. This behavior strongly resembles Mexican-wave dynamics.”

“We further found that the central region of the biofilm is mechanically more elastic, whereas the edge regions—where wave formation is absent—are motile. These observations suggest that gradual biofilm maturation is a key factor that transforms motile bacteria into a periodically moving but spatially constrained state. Consistent with this picture, the PAO1 strain, which has a strong biofilm-forming capability, completely suppresses surface oscillations. In contrast, the PA14 strain exhibits intermediate behavior, sustaining a partial transition between motile and locally constrained dynamics. Remarkably, signatures of this transition and wave generation are already detectable at the earliest stages of finger formation.”

Strengths:

The report of mechanical waves in bacterial collectives. The mechanism has potential application in a multicellular context, such as morphogenesis.

We thank the reviewer for the positive assessment and for highlighting this potential broad impact of our findings.

Weaknesses:

My most serious concern is about left-right symmetry breaking. I fail to see how the data in Figure 6 shows LR symmetry breaking. All they show is in-out directionality, which is a boundary condition. LR SM means breaking of mirror symmetry - the pattern cannot be superimposed on its mirror image using only rigid body transformations (translation and rotation) - as far as I am aware, this condition is not satisfied in this pattern-forming system.

We thank the reviewer for pointing out this critical issue. We acknowledge that we overlooked the distinction between biological and physical definitions of left–right symmetry in our initial submission, and we agree that our terminology was confusing.

In developmental biology, the term “left–right symmetry breaking” is often used to describe asymmetric flows generated by nodal cilia, which subsequently establish developmental asymmetry. This usage differs fundamentally from the physical definition of mirror symmetry breaking, which refers to chirality switching upon mirror reflection. As the reviewer correctly noted, our system does not exhibit mirror symmetry breaking in this strict physical sense.

To avoid confusion, we have revised the manuscript and replaced the term left–right symmetry breaking with left–right asymmetry between the edge and the center of the biofilm. This asymmetry arises from frequency gradients across the biofilm and is not a trivial boundary effect. For circular colonies, this phenomenon is more accurately described as radial asymmetry. We have rewritten the relevant sections of the manuscript to clarify this distinction and prevent misinterpretation.

Reviewer #2 (Public review):

Summary:

This manuscript by Altin et al. examines the dynamics of bacterial assemblies, building on previously published work documenting mechanical spiral waves. The authors show that the emergent dynamics can be influenced by various factors, including the strain of bacteria and water content in the sample. While the topic of this paper would be of broad interest, and the preliminary results are certainly interesting, various aspects of this paper are underdeveloped and require further exploration.

Strengths:

One of the nice features of this system is the ability to transition between the different states based on the addition or withdrawal of water. The authors use a similar experimental model system and mathematical model to previously published work (Reference 49), but extend by showing that the behaviour can be modified through simple interventions. Specifically, the authors show that adding water droplets or drying the sample through heating can result in changes in the observed wave structure. This represents a possible way of controlling active matter.

The mathematical model proposed in this paper involves a phase-oscillator model of Kuramotostyle coupling (similar to previously reported models). A non-reciprocal phase lag is introduced in order to facilitate the patterns seen in experiments. The qualitative agreement in the behaviour is quite striking, showing both spiral waves and travelling waves.

We thank the reviewer for the positive assessment and for pointing out areas that required further development. The reviewer is correct that our work builds on previously reported bacterial spiral wave systems; however, there are several significant differences that we now emphasize more clearly in the revised manuscript.

First, our study involves a different bacterial species and reveals a distinct dynamical process: the waves we report are strictly localized on the surface of the biofilm, in contrast to the bulk oscillations detected through density fluctuations in the earlier work (Ref. 49). The surface waves in our system resemble “Mexican wave”-like motions, in which surface bacteria periodically lift upward. To highlight this key distinction, we performed new imaging experiments that directly visualize this process. (New Video 5 and 6, Author response image 1).

Second, we systematically compared different bacterial strains, including pathogenic species such as P. aeruginosa PA14 and PAO1, alongside our BSL-1 strain. This comparative approach demonstrates that the observed phenomenon spans strains with different pathogenicity levels, and genetic variations while also showing that our strain provides a safer and more broadly usable model system for laboratory investigations.

Third, the modeling frameworks differ. Whereas the referred study relied primarily on phase models similar to those used in cilia systems, we combine a delayed Kuramoto-style oscillator model with an active solid model. This combination provides both a phenomenological description and a physical interpretation of the collective dynamics. We acknowledge that, in the original submission, the physical interpretation of the model in relation to our experimental system was underdeveloped. In the revision, we have now established this link explicitly through the elasticity and elasto active coupling of the biofilm. Specifically, we show that the transition from motile to biofilm states is accompanied by changes in elasticity, which directly influence the observed transitions between different types of wave defects. This connection is consistent with prior theoretical works and has even been only studied in robotic active matter systems.

Together, these clarifications and new results reinforce the novelty of our findings and establish a stronger connection between the experiments and the modeling framework.

Author response image 1.

Comparison between the elastic biofilm core and the motile colony edge. Highresolution video recordings revealing individual bacterial motion highlight the key physical differences driving wave-generating. Time-lapse snapshots show that bacteria at the colony edge move freely and form fingering structures, whereas bacteria in the elastic central biofilm periodically lift vertically, producing a Mexican-wave–like collective motion across the surface. See new Video

Weaknesses:

The principal observation of the paper - that spiral waves emerge in these systems and can be controlled in various ways - is not linked to microscale dynamics at the cell level. It is recognised that hydrodynamics can introduce non-reciprocity, an essential ingredient of this model. However, in this work the authors have not identified a physical mechanism for the lag, e.g., either through steric interactions or hydrodynamic disturbances. This is also relevant in the phase oscillator modelling section. In low Reynolds number flows, dynamics are instantaneously determined. In this light, what does the phase lag term represent?

The reviewer is correct that, at low Reynolds numbers, fluid dynamics are instantaneous and do not generate real temporal delays. However, nonreciprocity in hydrodynamic interactions can still emerge from the tensorial structure of the Blake–Oseen Green’s function. In this formalism, the effective asymmetry can be represented mathematically as a phase-lag–like term. This has been theoretically demonstrated in Ref.40. While this is not a literal time delay, it functions analogously by breaking odd symmetry in the coupling.

In our system, strong long-range hydrodynamic interactions are absent, as the bacteria are embedded in an elastic biofilm matrix. Instead, the dominant interactions are active elastic couplings mediated by pili and biofilm structure. The elastic solid model behaves in a way that is conceptually similar to the hydrodynamic case: pili-induced deformations of the elastic medium produce anisotropic stresses that play a role analogous to the tensorial hydrodynamic Green’s function. Thus, the phase-lag term in our Kuramoto-based model can be interpreted as an effective representation of these nonreciprocal elastic interactions.

We have clarified this point in the revised manuscript by explicitly connecting the phenomenological phase-lag term to the underlying elastic coupling in biofilms.

What is the origin of the coupling term, b? Can this be varied systematically or derived from experimental measurements or parameters?

The term b represents the enhanced elasto-active coupling of the pili process. The length of the Pili varies, and the elongated Pili has more potential to modulate the coupling between bacteria which is known to depend on a critical threshold. This process resembles the pinning dynamics and is driven by the activity of molecular motors within the pili machinery. However, the detailed mechanisms that set the effective coupling strength remain highly complex and are not yet fully understood.

At present, we do not have a direct way to systematically manipulate b in experiments. A major technical limitation is the nanoscale nature of type IV pili: these protein assemblies are extremely small and difficult to monitor or manipulate directly. Even basic tools such as GFP-based labeling have proven challenging to implement, which restricts our ability to track the detailed dynamics of these structures in live biofilms.

While we cannot currently derive b directly from experimental parameters, we emphasize in the revised manuscript that b should be understood as an effective parameter capturing the excitability of pili retractions. We also highlight this limitation and note that future advances in molecular imaging and manipulation of pili will be essential for quantitatively linking b to microscopic processes.

Classification of wave properties is an important aspect of this paper, but is not accomplished in a quantitative sense. What is the method for distinguishing between travelling and spiral waves? There is a range of quantitative tools that could be used to investigate these dynamics (and also compare quantitatively with the models). For example, examining the correlation functions and order parameters could assist with the extraction of wave features (see extensive literature on oscillator models).

We thank the reviewer for emphasizing this important point. In the revised manuscript, we have incorporated the classic Kuramoto order parameter (S) to characterize the dynamics in our model simulations. However, this metric is not directly applicable to our experimental system, because we cannot resolve the phase of individual bacteria at large scales.

Instead, we have focused on a flux-based parameter, as previously used in Ref. 40, which can be measured experimentally from collective surface dynamics. Interestingly, we find that the directional flux extracted from our experimental movies closely matches the trends predicted by the model order parameter. We suspect that this similarity arises from the combination of our optical illumination method and the characteristic surface modulations of the biofilm. While we currently lack a rigorous theoretical justification for this correspondence, so we want to keep this discussion in the review document.

In summary, we now use the classic Kuramoto order parameter in simulations and rely on the experimentally accessible flux measure for our experimental data. This dual approach allows us to compare model and experiment in a consistent manner.

Author response image 2.

Critical order parameters of the coupled biofilm system. (a) The Kuramoto global order parameter increases continuously as the system becomes globally synchronized. In contrast, in the nonreciprocally coupled system the order parameter saturates at a critical level. (b) In the experimentally observed biofilm, however the flux generated by the coupled oscillations provides a more appropriate measure of synchronization. Blue curves indicate directionally propagating planar waves, red curves correspond to spiral wave formation, and green curves represent the globally synchronized reciprocal system.

Author response image 3.

Comparison of flux profiles of the simulations with experimental measurements. Directional optical illumination enhances the flux term on the surface of the biofilm.

The methodology of changing the dynamics through moisture content appears to be slightly underdeveloped, e.g., adding water involves a droplet, and removing water is accomplished by heating (which presumably could cause other effects). Could the dynamics not be controlled more directly by varying the humidity?

We thank the reviewer for this valuable suggestion. Our results indicate that water content in the biofilm plays a key role in driving the transition to the biofilm state by modulating its elasticity. During the initial submission, we did not know how to systematically vary humidity without simultaneously altering temperature. Standard approaches typically involve water evaporation in controlled chambers, which inherently changes both parameters.

Following the reviewer’s recommendation, we first measured the ambient moisture levels inside closed culture plates. To our surprise, the relative humidity was already ~98%, leaving virtually no room to increase it further. We then attempted to decrease humidity by flowing dry synthetic air, but even under these conditions we could not reduce it below ~85%, and achieving this required unrealistically high flow rates. Moreover, we noticed that in closed-lid NGM plates, evaporation is already substantial, and when the lid is left open the evaporation rate reaches ~1 µm/s. This rapid surface thinning severely limits the quality of long-term time-lapse imaging.

Taken together, these technical constraints explain why we have to reliy on localized perturbations such as water droplets and heating rather than global humidity control. We have clarified this point in the revised manuscript and now explicitly discuss both the challenges and limitations of humidity-based approaches.

At the same time, the authors also mention that temperature itself plays a role in shaping the behaviour. What is the mechanism for this? Is it just through evaporation? Since the frequency increases with temperature, could it just be that activity increases with temperature?

We thank the reviewer for raising this critical point. We believe that temperature has two distinct impacts operating on different timescales.

Short timescale (~minutes): We observed that biofilm oscillations respond to temperature changes very rapidly and in a reversible manner. This timescale is too short to be explained by modulation of water content or bulk elasticity of the biofilm. Instead, we attribute the immediate frequency increase to enhanced biological activity of the bacteria at elevated temperatures.

Long timescale (~tens of minutes to hours): During processes such as the transition from planar to spiral waves, prolonged heating can significantly alter the biofilm structure. These changes are not reversible and likely involve modifications of elasticity and other structural properties.

In the modeling framework, the short-timescale effect is represented as an increase in the active force term, while the long-timescale effect is captured by concurrent changes in both the active force and the elastic properties of the biofilm. We have clarified this mechanism and its representation in the revised manuscript.

Reviewer #3 (Public review):

Summary:

This manuscript presents a novel investigation into unidirectionally propagating waves observed on the surface of Pseudomonas nitroreducens bacterial biofilms. The authors explore how these waves, initially spiral in form, transition into combinations of spiral, target, and planar patterns. The study identifies the periodic extension-retraction cycles of type IV pili as the driving mechanism for wave propagation, which preferentially moves from the colony's edge to its center. Furthermore, the manuscript proposes two theoretical models-a phase-oscillator model and a continuum active solid model-to reproduce these phenomena, and demonstrates how external manipulations (e.g., water droplets, temperature, PEG) can control wave patterns and direction, often correlating with oscillation frequency gradients. The work aims to bridge the fields of activematter physics and bacterial biophysics by providing both experimental observations and theoretical frameworks for understanding these complex biological wave phenomena.

We thank the reviewer for the positive assessment of our work and for highlighting both the novelty and the key contributions of our study.

Strengths:

The experimental discovery of unidirectionally propagating waves on bacterial biofilms is highly intriguing and represents a significant contribution to both microbiology and active-matter physics.

The detailed observations of wave pattern transitions (spiral to target to planar) and their response to various environmental perturbations (water, temperature, PEG) provide valuable empirical data. The identification of type IV pili as the driving force offers a concrete biological mechanism. The observed correlation between frequency gradients and wave direction is a compelling finding with potential for broader implications in understanding biological pattern formation. This work has the potential to stimulate further research in the collective behavior of living systems and the physical principles underlying biological organization.

We thank the reviewer once again for emphasizing the importance of wave directionality. We also believe that this phenomenon may provide insight into early symmetry-breaking processes observed in developmental biology, where oxygen or nutrient gradients in dense environments could play a similar role.

Weaknesses:

The manuscript attempts to link unidirectional wave propagation to non-reciprocal couplings but ultimately shows that the wave direction is determined by the gradient of the oscillation frequency. The couplings in the two theoretical models are both isotropic and thus cannot dictate the wave direction. A clear distinction should be made between non-reciprocity as a source of wave generation and non-uniformity as a controlling factor of wave direction.

We greatly appreciate the reviewer’s careful evaluation, particularly for highlighting this important and often confusing distinction. The relationship between nonreciprocity, spontaneous symmetry breaking, and frequency gradients has also been a challenging concept for us and required significant effort to clarify.

Recent theoretical studies have established that traveling wave formation requires nonreciprocity, which provides a framework for understanding phenomena ranging from spiral to target and planar waves. In our system, nonreciprocity arises between the displacement field (U) and the pili force vector (P): as a result in broken phase U effectively “chases” P, breaking PT symmetry locally and thereby enabling the generation of local directional flux and traveling waves. In this sense, nonreciprocity is essential for travelling wave generation and spontaneous symmetry breaking in either direction.

However, we now agree that global directionality (always from right to left, or edge to center) is set by an independent factor—namely, the oscillation frequency gradient across the biofilm. Thus, while nonreciprocity determines whether waves can travel, frequency gradients determine the large-scale direction in which they propagate. Put differently, PT symmetry is already broken spiral waves due to nonreciprocity, but global asymmetry (frequency gradients) is required to align the overall propagation in one direction.

We have clarified this distinction in the revised manuscript, emphasizing that nonreciprocity is a necessary ingredient for travelling wave generation, whereas global asymmetry controls global wave direction.

Modification in the manuscript:

“We should note that traveling waves indicate broken PT symmetry between these fields triggered by nonreciprocity, with spiral waves serving as a classic signature of this phenomenon. A further transition from spiral to planar waves reflects an overall asymmetry in the frequency profile, which is not directly related to PT-symmetry breaking.”

The relationship between the phase oscillator model and the active solid model is unclear. Given that U and P are both dynamical variables evolving in three-dimensional space, defining the phase Φ precisely in the phase space spanned by U and P could be challenging. A graphical illustration of the definition of Φ would be beneficial. To ensure reproducibility of the numerical results, the parameter values used in the numerical simulations and an explicit definition of the elastic force in the active solid model should be provided.

We agree with the reviewer that the relationship between the phase oscillator model and the active solid model can be confusing, but establishing this link is essential to connect different modeling approaches in the literature. As the reviewer notes, in a fully three-dimensional setting with freely moving bacteria, defining the oscillation phase (Φ) in the phase space spanned by U and P is indeed complicated.

However, our recent imaging results show that bacteria within the biofilm do not undergo large translational motions but instead exhibit periodic “Mexican wave”-like oscillations. These oscillations are confined to a restricted phase space, which allows us to define Φ in a straightforward way. In this context, the phase oscillator model becomes a natural reduction of the dynamics.

Similarly, in the active solid (or active gel) model, we can plot not only the displacement and force vectors but also the local phase, which shows strong agreement with the phenomenological Kuramoto-style model. To make this connection clearer, we have now included a schematic illustration in the revised manuscript that explicitly shows how Φ is defined in the reduced phase space, and we provide the parameter values used in the simulations as well as the explicit definition of the elastic force in the active solid model to ensure reproducibility.

The link between the theoretical models and experimental results is weak. For example, the propagation of the kink from the lower to the higher part of the surface (Figure 1e) could be addressed within the framework of the active solid model. The mechanism of transition from spiral to target waves (Figure 3a), b)) requires clarification, identifying which model parameter is crucial for inducing this transition. The wave propagation toward the lower frequency side is numerically demonstrated using the phase oscillator model, but a physical or intuitive explanation for this phenomenon is missing. Also, the wave transitions induced by the addition of water droplets and temperature rise are not linked to specific parameters in the theoretical models.

We thank the reviewer for highlighting this important weakness, which was also consistently noted by the other reviewers. We fully agree that the link between our theoretical models and experimental results required significant strengthening.

With improved imaging in the revised study, we were able to uncover additional connections that help establish this link more clearly. We acknowledge that our ability to measure detailed biofilm parameters is limited, which restricts us from providing fully quantitative mappings. Nonetheless, based on the reviewers’ suggestions, we carried out additional imaging and simulations to compare bacterial dynamics at the colony edge and within the biofilm surface. These data confirm that cells within the biofilm undergo restricted, “Mexican wave”-like oscillations, emphasizing the critical role of elasticity in governing the collective dynamics.

Experimentally, we found that adding water or PEG, or alternatively inducing drying, strongly modulates the effective elasticity of the biofilm. Within the active solid framework, elasticity and the elasto-active coupling are the key parameters controlling the system. By tuning these parameters in simulations, we could reproduce the qualitative transitions observed experimentally. Specifically, we observed that:

At low elasticity, topological defects are mobile and can move, merge, or annihilate, leading to the emergence of planar waves.

At high elasticity, defects remain pinned, across the biofilm surface, dominating the dynamics.

These observations suggest that the motility of defects is the crucial parameter governing the transition between spiral, target, and planar waves. Although we cannot independently manipulate each parameter in experiments, varying the moisture content provides an effective and experimentally accessible control.

Finally, our simulations and new analyses reveal that spiral defect cores can move and merge to form target waves or annihilate entirely—processes that we also observe experimentally. This rich dynamical behavior underscores the importance of elasticity in shaping pattern transitions, and we believe it warrants further theoretical exploration. We have clarified this connection and its implications in the revised manuscript.

First, we compare defect dynamics in both Kuramoto-based simulations and the active solid model. Both systems exhibit similar defect-survival behavior. As shown in the review , pairs of unlike (+/−) defects can stably persist only at high nonreciprocity. We further quantify this behavior by plotting the separation distances between unlike defect pairs and find that short-range defect separations are possible exclusively in the high-nonreciprocity regime Supplementary Figure 11.

This high-nonreciprocity regime corresponds to the dry biofilm state. Increasing moisture reduces elasticity, leading to the loss of stable defect dynamics and promoting the annihilation of unlike defect pairs, which in turn drives the system toward target-wave formation and ultimately planar waves. Conversely, heating the biofilm removes water, enhances elasticity, and increases the system’s ability to sustain closely separated defect pairs.

Experimentally, we further observe that removing water by heating enhances surface nonuniformities, which readily trigger defect-pair formation. To investigate this mechanism, we performed additional simulations in which local nonuniformities were introduced Supplementary Figure 12. Consistent with experiments, defect-pair generation occurs only at high nonreciprocity, where pairs of unlike defects can be stably maintained. Experimental observation (Author response image 4) also show that surface nonuniformities on the biofilm surface similarly trigger the formation of closely separated defect pairs. We have updated the details of the defect dynamics in the revised manuscript to clarify the transition between these waves.

Author response image 4.

Experimental observation showing that small surface nonuniformities on the biofilm surface trigger the formation of closely separated defect pairs. Arrows indicate the position of the nonuniformities

Modification in the manuscript:

Defect dynamics controlling the transition between spiral to target waves

“To better understand the dynamics of the transition between different form of the waves we focused on numerical simulations. We noticed that the motility of defects is the crucial parameter governing the transition between spiral, target, and planar waves varying the moisture content provides an effective and experimentally accessible control this motility. Our analyses revealed that spiral defect cores can move and merge to form target waves or annihilate entirely—processes that we also observe experimentally. This rich dynamical behavior underscores the importance of elasticity in shaping pattern transitions. First, we compare defect dynamics in both Kuramotobased simulations and the active solid model. Both systems exhibit similar defect-survival behavior. As shown in Supplementary Figure10, pairs of unlike (+/−) defects can stably persist only at high nonreciprocity. We further quantify this behavior by plotting the separation distances between unlike defect pairs and find that short-range defect separations are possible exclusively in the high-nonreciprocity regime (Supplementary Figure11). This high-nonreciprocity regime corresponds to the dry biofilm state. Increasing moisture reduces elasticity, leading to the loss of stable defect dynamics and promoting the annihilation of unlike defect pairs, which in turn drives the system toward target-wave formation and ultimately planar waves. Conversely, heating the biofilm removes water, enhances elasticity, and increases the system’s ability to sustain closely separated defect pairs. Experimentally, we further observe that removing water by heating enhances surface nonuniformities, which readily trigger defect-pair formation (Supplementary Video9). To investigate this mechanism, we performed additional simulations in which local nonuniformities were introduced (Supplementary Video12-13). Consistent with experiments, defect-pair generation occurs only at high nonreciprocity, where pairs of unlike defects can be stably maintained. Experimental observation (Supplementary Video9) also show that surface nonuniformities on the biofilm surface similarly trigger the formation of closely separated defect pairs.”

All the recommended points have been addressed in the revised manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study investigates how collective navigation improvements arise in homing pigeons. Building on the Sasaki & Biro (2017) experiment on homing pigeons, the authors use simulations to test seven candidate social learning strategies of varying cognitive complexity, ranging from simple route averaging to potentially cognitively demanding selective propagation of superior routes. They show that only the simplest strategy-equal route averaging-quantitatively matches the experimental data in both route efficiency and social weighting. More complex strategies, while potentially more effective, fail to align with the observed data. The authors also introduce the concept of "effective group size," showing that the chaining design leads to a strong dilution of earlier individuals' contributions. Overall, they conclude that cognitive simplicity rather than cumulative cultural evolution explains collective route improvements in pigeons.

Strengths:

The manuscript addresses an important question and provides a compelling argument that a simpler hypothesis is necessary and sufficient to explain findings of a recent influential study on pigeon route improvements, via a rigorous systematic comparison of seven alternative hypotheses. The authors should be commended for their willingness to critically re-examine established interpretations. The introduction and discussion are broad and link pigeon navigation to general debates on social learning, wisdom of crowds, and CCE.

We thank the reviewer for their positive comments.

Weaknesses:

The lack of availability of codes and data for this manuscript, especially given that it critically examines and proposes alternative hypotheses for an important published work.

We thank the reviewer for their comment. The code and data for our manuscript are an important aspect of the study, and we had intended to make them publicly available upon publication. The link to our code and data on fig share can be found here: (https://doi.org/10.6084/m9.figshare.28950032.v1). We have now revised the manuscript to include a link to our dataset.

Reviewer #2 (Public review):

Summary:

The manuscript investigates which social navigation mechanisms, with different cognitive demands, can explain experimental data collected from homing pigeons. Interestingly, the results indicate that the simplest strategy - route averaging - aligns best with the experimental data, while the most demanding strategy - selectively propagating the best route - offers no advantage. Further, the results suggest that a mixed strategy of weighted averaging may provide significant improvements.

The manuscript addresses the important problem of identifying possible mechanisms that could explain observed animal behavior by systematically comparing different candidate models. A core aspect of the study is the calculation of collective routes from individual bird routes using different models that were hypothesized to be employed by the animals, but which differ in their cognitive demands.

The manuscript is well-written, with high-quality figures supporting both the description of the approach taken and the presentation of results. The results should be of interest to a broad community of researchers investigating (collective) animal behavior, ranging from experiment to theory. The general approach and mathematical methods appear reasonable and show no obvious flaws. The statistical methods also appear.

Strengths:

The main strength of the manuscript is the systematic comparison of different meta-mechanisms for social navigation by modeling social trajectories from solitary trajectories and directly comparing them with experimental results on social navigation. The results show that the experimentally observed behavior could, in principle, arise from simple route averaging without the need to identify "knowledgeable" individuals. Another strength of the work is the establishment of a connection between social navigation behavior and the broader literature on the wisdom of crowds through the concept of effective group size.

We thank the reviewer for their positive comments.

Weaknesses:

However, there are two main weaknesses that should be addressed:

(1) The first concerns the definition of "mechanism" as used by the authors, for example, when writing "navigation mechanism." Intuitively, one might assume that what is meant is a behavioral mechanism in the sense of how behavior is generated as a dynamic process. However, here it is used at a more abstract (meta) level, referring to high-level categories such as "averaging" versus "leader-follower" dynamics. It is not used in the sense of how an individual makes decisions while moving, where the actual route followed in a social context emerges from individuals navigating while simultaneously interacting with conspecifics in space and time. In the presented work, the approach is to directly combine (global) route data of solitary birds according to the considered "meta-mechanisms" to generate social trajectories. Of course, this is not how pigeon social navigation actually works-they do not sit together before the flight and say, "This is my route, this is your route, let's combine them in this way." A mechanistic modeling approach would instead be some form of agent-based model that describes how agents move and interact in space and time. Such a "bottom-up" approach, however, has its drawbacks, including many unknown parameters and often strongly simplifying (implicit) assumptions. I do not expect the authors to conduct agent-based modeling, but at the very least, they should clearly discuss what they mean by "mechanism" and clarify that while their approach has advantages-such as naturally accounting for the statistical features of solitary routes and allowing a direct comparison of different meta-mechanisms is also limited, as it does not address how behavior is actually generated. For example, the approach lacks any explicit modeling of errors, uncertainty, or stochasticity more broadly (e.g., due to environmental influences). Thus, while the presented study yields some interesting results, it can only be considered an intermediate step toward understanding actual behavioral mechanisms.

We thank the reviewer for their comment and thoughtful suggestions. We agree that the inherent behavioral mechanisms and the biological basis of these mechanisms cannot be determined just through the navigational data alone. For instance, it remains unexplored if pigeons are adapting their behavior based only on social cues from their partners or using other navigational features such as landmarks or roads, location of the sun, geomagnetic cues or prior learnt routes. However, we do agree (as also pointed by the reviewer) that these behavioral rules generate an emergent ‘meta-mechanism’ where the bird pairs are behaving as if their preferred routes are averaged during a flight. It will be important in future work to explore the biological basis of these mechanisms, but our current approach allows us to only describe the mechanisms in a meta sense with any confidence. Considering this, we believe that our analysis is a more top-down approach towards describing the outcomes of these underlying mechanisms in an abstract sense. We would also like to point the reviewer to Dalmaijer, 2024 [1] who used a bottom up approach, using naive agents and showed that cumulative route improvements emerged in the absence of any sophisticated communication in the same dataset, in agreement with our approach. We have now added a paragraph: “It is also important to clarify that we use the terms…… that lead to these meta-mechanisms arising remain an open question.” found in lines 120-129 in our Introduction to make this clarification.

(2) While the presented study raises important questions about the applicability and viability of cumulative cultural evolution (CCE) in explaining certain animal behaviors such as social navigation, I find that it falls short in discussing them. What are the implications regarding the applicability of CCE to animal data and to previously claimed experimental evidence for CCE? Should these experiments be re-analyzed or critically reassessed? If not, why? What are good examples from animal behavior where CCE should not be doubted? Furthermore, what about the cited definitions and criteria of CCE? Are they potentially too restrictive? Should they be revised-and if so, how? Conversely, if the definitions become too general, is CCE still a useful concept for studying certain classes of animal behavior? I think these are some of the very important questions that could be addressed or at least raised in the discussion to initiate a broader debate within the community.

We thank the reviewer for their comments and interesting questions regarding our study. We agree with the reviewer that our study opens up new avenues for critically analysing the criteria previous studies have used for providing evidence of CCE in non-human animals. According to our literature review, we found that the field has been usually motivated in thinking about CCE in a ‘process’ focused manner (Reindl et al. [2]) in regards to individuals being able to compare strategies and selecting ones resulting in higher individual fitness. This preferential selection of strategies – termed innovations — allows for the stereotypical ratcheting effect seen in CCE. In our study, we propose that in the case of homing pigeons, the ratcheting effect is more of a statistical outcome rather than deliberate individual judgement. We believe that this strategy is also amenable to certain task types (which in our study was homing route choice) and may change for others (for example solving a puzzle box) and the task also needs to be sufficiently complex for animals to benefit from the use of social information (Caldwell et al. 2008 [3]). Thus, we recommend future work to address what classes of problems would fit well within the definition of “emergent” CCE and which ones don’t. Keeping this framework in mind, studies should clearly state what definition of CCE they are using and should be critically evaluated for their underlying task type and cognitive mechanisms to deem them as CCE. Considering these points, we have now expanded our Discussion to include a paragraph: “Our results highlight the need for more…..range of task types and cognitive abilities.” found in lines 420-433 to highlight these key questions.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I do not have any major objections, but I am clarifying my points as major or minor depending on the effort required to address (mostly via rewriting and clarifications).

Major comments:

(1) A schematic summary of the original study: Since the current manuscript builds directly on Sasaki & Biro (2017), it would greatly help readers if you included a concise schematic figure summarizing the original experiment. For instance, a simple panel could depict the chain design (experienced + naïve replacements), the control treatments, and the key empirical findings (improvements in route efficiency across generations, and route similarity within vs. between chains). Presenting this visually would save readers the effort of reconstructing the design and main results from text alone, especially for those unfamiliar with the original paper. It would also clarify exactly what empirical patterns your simulations are intended to reproduce.

We thank the reviewer for this comment. We have now revised the manuscript with a schematic illustration adapted from the original study by Sasaki and Biro (2017). We hope this clarifies the experimental design and results we aimed to highlight in our work.

(2) Reproducibility: Code and data are only "available on request." I believe eLife has strong policies on open science; a lack of immediate open access to analysis would be a barrier. I find it jarring that a paper intending to reproduce and improvise a previously published paper does not make the codes and data available for peer review or to readers without an explicit request.

We have taken the feedback into consideration and updated the Data Availability section with a link to our Fig share dataset.

(3) One huge drawback of the current format of the manuscript, where Methods come after Results, is that one has to really struggle to understand and appreciate Figures 2 and 3. I would strongly urge authors to have a shorter methods section embedded either as a subsection before the Results, or within the results section, as described in each figure. Perhaps a lot of my confusion also comes from not having known the previous paper, but it may be true for other readers, too. More specifically, for Figure 3, how is social weight for the experiments inferred? Figure 3 caption talks of mean difference, but one has to check the manuscript at multiple places throughout to really understand what this difference is (the definition) and how it is computed.

While we agree that our manuscript includes the Methods section at the end, we tried to structure our text to tell a story (as stated in our manuscript title). To this end, we organized the text into short titled subsections that briefly convey the relevant background, identify the knowledge gap and outline our approach. We chose this structure to reserve the indepth details about model implementation and statistical analysis for the Methods.

Additionally, we made sure to include references to methodological details in relevant segments of the Introduction and Results section so as to not bog down the reader by model complexities and keep a coherent narrative that delivers the message of our study. To further address the background of our work, we have now added a schematic of the original study in response to a previous comment by the reviewer, which we hope helps the reader better understand our work. We hope this explanation clarifies the intention behind our writing choice and decision to retain the current structure.

(4) The introduction of the 'effective group size' concept is a potentially valuable and intuitive way to interpret chain dynamics, but the explanation is somewhat buried in the Results/Methods; I suggest highlighting it more prominently (e.g., in the Discussion or with a schematic in the Results) so readers can readily grasp this useful idea.

We thank the reviewer that they found our concept of ‘effective group size’ useful. However, we do believe that we introduced the idea and rationale behind using this method in the Results: “We asked to what extent……to an equivalent group size” found in lines 305-314. We reserved a detailed description of this method in the Methods section. However, to further emphasize the importance of the concept we have now added a text: “This is further supported….. slightly better than two individuals.” found in lines 389-394 in the Discussion. 

Minor comments:

(1) Line 12: "what is the navigation mechanism(s)" - the (s) is a bit awkward. Either remove (s) or ask what the mechanisms are.

We have fixed the typo to clarify the statement.

(2) Line 78: "Such 'ratchet'-like improvements is referred to..." → "are referred to."

We have fixed the typo to clarify the statement.

(3) Figure 3 caption: "color scheme in the plots are same" → should be "is the same."

We have fixed the typo to clarify the statement.

(4) Clarification on reporting confidence intervals: The manuscript reports confidence intervals (CIs) for the model-based comparisons (e.g., Figures 2-3). This might seem unnecessary for simulation studies, since running more iterations can arbitrarily shrink uncertainty. However, in your case, the CIs are justified because the simulations are anchored to a finite empirical dataset (only 9 solo trajectories), sampled with replacement, and analyzed with mixed-effects models that incorporate bird identity as a random effect. Thus, the intervals reflect biological sample variability rather than simulation noise. This must be clarified.

We have added a clarifying statement: “...and reflect the biological uncertainty in the empirical dataset, not simulation noise” found in lines 241 and 293 in the captions of Figures 2 and 3 in accordance with the reviewer’s comment. 

(5) One part of the issue is that details of methods come much later in the manuscript, perhaps following journal style. Therefore, I recommend explicitly highlighting this rationale in the Results, so readers do not misinterpret the CIs as simply reflecting simulation error.

We believe that the clarifying statements we have now added in the captions of Figures 2 and 3 should convey this interpretation of CIs and further changes in the Results may not be required.

With these proposed changes we hope that we improved upon the clarity of our manuscript.

References:

(1) Dalmaijer ES (2024) Cumulative route improvements spontaneously emerge in artificial navigators even in the absence of sophisticated communication or thought. PLoS Biol. 22:e3002644.

(2) Reindl, E., Gwilliams, A.L., Dean, L.G. et al. (2020) Skills and motivations underlying children’s cumulative cultural learning: case not closed. Palgrave Commun 6, 106.

(3) Caldwell CA, Millen AE (2008) Studying cumulative cultural evolution in the laboratory. Phil. Trans. R. Soc. B 363:3529-3539.

Author response:

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

Reviewer #1 (Public review):

(1) While the manuscript is written for a scientific audience, the authors are likely aware that findings like this will be of broad appeal to the field of neurology, where treatments for memory loss are desperately needed. For this reason, the authors could consider including a statement regarding an interpretation of this meta-analysis from a clinical standpoint. Statements such as 'safe and effective' imply a clinical indication, and yet the manuscript does not engage with clinical trials terminology such as blinding, parallel arm versus crossover design, and trial phase. While the authors might prefer not to engage with this terminology, it can be confusing when studies delivering intervention-like five days of consecutive TMS (e.g., Wang et al., 2014) are clustered with studies that delivered online rhythmic TMS, which tests target engagement (e.g., Hermiller et al., 2020). While the 'sessions' variable somewhat addresses the basic-science versus intervention-like approach, adding an explicit statement regarding this in the discussion might help the reader navigate the broad scope of approaches that are utilized in the meta-analysis.

We appreciate the suggestion to enhance interpretability of our report by broader audiences. First, to avoid confusion, we have eliminated “safe” and “effective” descriptors from the main summary of findings in the Abstract (pg. 1) and Discussion (pg. 6). Second, we now describe that reviewed studies included those categorized as traditional clinical trials, as well as non-clinical studies that generally follow clinical trial designs (i.e., multi-day intervention-like studies), in addition to more basic-oriented studies that are geared towards target engagement (Introduction, pg. 2). Third, we now clarify that the Design and Control factors (Figure 3) correspond to fairly standard distinctions in the clinical trials literature and were intended to capture major study design factors choices that are used in both clinical-trial and non-trial studies (Methods, pg. 9; Table S1). Finally, we now clarify that future clinical trials would be needed to evaluate HITS for any specific indication, and that our findings motivate such investigations but do not conclusively indicate efficacy for any given indication (Abstract, pg. 1; Discussion, pg. 7).

Reviewer #1 (Recommendations for the authors):

(1) The color scheme of Figure 1 was a bit confusing. All of the colors used for the flagged regions were incredibly similar. At first glance, it looks like the hippocampus was targeted directly due to the subtle color difference. Could the authors use colors that are more different? Similarly, zooming into the specific locations shows blue dots encompassed by teal. I am not sure what I am looking at here.

We have updated the figure for clarity.

(2) Given the broad appeal of the current study, I would encourage the authors to include a brief visual depiction of "HITS." This could help the more casual reader to understand the general approach.

We have included this in Figure 1A.

Reviewer #2 (Public review):

(1) While the introduction centers on the role of the hippocampus in episodic memory and posits hippocampal neuromodulation by TMS as causative, the true mechanism may be more complex. Clean hippocampal lesions in primates cause focal loss of spatial and place memory, and I am aware of no specific evidence that the hippocampus does more than this in humans. Moreover, there is evidence that lateral parietal TMS also reaches neighboring temporal lobe regions, which contribute to episodic memory. The hippocampus may, therefore, be a reliable deep seed for connectivity-based targeting of the episodic memory network, but might not be the true or only functional target.

We regret to have implied that we think the hippocampus is the true or only functional target. We agree with the reviewer that the hippocampus is “a reliable deep seed for connectivity-based targeting of the episodic memory network” and that the specific locus/loci of the HITS effects and mechanisms are not yet clear. We now emphasize that although hippocampus is used to define the targeted network, effects of TMS are likely distributed throughout the network, citing relevant studies that have shown that brain activity changes due to HITS are certainly not restricted to the hippocampus (Introduction, pg. 2).

(2) The meta-analysis combines studies with confirmation of targeting and target-network engagement from fMRI and studies without independent evidence of having stimulated the putative target (e.g., Koch et al). That seems like a more important methodological distinction than merely the use of any individual targeting method. In my experience, atlas-based estimates are at least as accurate as eyeballing cortical areas in individuals. Hence, entering individual functional targeting as a factor might reveal an effect on efficacy.

Our current definition of the “Targeting” factor appears to satisfy this concern. That is, we distinguish studies that used “individual functional targeting” (i.e., resting-state fMRI or DTI connectivity in each individual to select the target) from those that did not (i.e., atlas or other group-average approach). Notably, the Targeting factor modulation effect failed to survive correction for multiple comparisons. We think this satisfies the reviewer criticism, unless the reviewer is suggesting that we categorize studies based on whether they included evaluation of target engagement (e.g., tested for change in fMRI activity or connectivity of the network due to HITS) versus those that measured only behavioral outcomes. We did not include this distinction as a factor, as our analysis focuses on behavioral effects of HITS, and it is not clear what the neural effects would have been in studies in which they were not measured. Notably, we are providing the full raw dataset of effect sizes in a public repository with our final version of record, such that any other categorization schemes could be assessed by others.

(3) The funnel plot and Egger's regression for episodic memory outcomes suggested possible bias, and the average sample size of 23 is small, contributing to the likelihood of false positive results. It would be informative, therefore, to know how many or which studies had formal power estimates and what the predicted effect sizes were.

Regarding the average sample size of 23, we note that we used Hedges’ g for the effect size measure because it corrects for bias associated with small samples (pg. 10). Further, small sample sizes contribute to noisy estimates of true effects, allowing outliers to contribute to false positives and low power to contribute to false negatives, but without any reason to systematically yield bias towards false positives. Regarding potential publication bias, although we cannot rule this out based only on the statistics, we think that bias against publication of negative results is unlikely. First, HITS experiments are time consuming and expensive, and most in the field seem to be motivated to publish, whatever the outcome. Second, the notion of memory enhancement via brain stimulation is controversial, and groups have certainly been motivated, if not overly eager, to publish “failure to replicate” studies for HITS (e.g., the failure-to-replicate publication by Hendrikse et al. 2020, which was then re-analyzed by many of the original authors to arrive at different conclusions in Cash et al. 2022). Given these considerations, we think that it is very unlikely that publication bias had any major impact on our conclusions, but of course it cannot be conclusively excluded. Finally, we note that our finding of HITS selectivity for recollection enhancement is likely not affected by publication bias, as this selectivity versus other memory and non-memory outcomes was found only within published studies (i.e., it is very unlikely that publication bias would have led researchers to withhold publication of studies that found effects of HITS on recognition but not on recollection).

(4) In the Discussion, the authors might provide a comparison between the effect size for memory improvement found here with those reported for other brain-targeted interventions and behavioral strategies. It may also be worthwhile pointing out that HITS/memory is one of the very few, or perhaps the only, neuromodulatory effects on cognition that has been extensively reproduced and survived rigorous meta-analysis.

We now emphasize that this is, to our knowledge, the only neuromodulatory effect on cognition that is selective, has been extensively reproduced, and survived rigorous meta-analysis (Discussion, pg. 6). However, we wish to avoid the clinical overinterpretation of our findings that might result if we were to compare directly to effect size estimates for other current therapies, which have been evaluated for specific clinical indications. For example, antibody and pharmacological interventions for Alzheimer’s dementia typically have been associated with similar effect sizes to our estimate for HITS. However, those estimates derive from systematic review of randomized controlled trials measuring clinically relevant outcomes at relatively long delays, whereas the HITS studies we review include a mix of controlled and uncontrolled trials, vary in whether clinical outcomes were assessed, and mostly assessed outcomes at shorter delays. Thus, it could be misleading to directly compare the effect sizes. We instead continue to highlight that the HITS effects are promising and warrant rigorous testing for any given clinical indication.

(5) The section of the Discussion on specificity compares HITS to transcranial electrical stimulation without specifying an anatomical target or intended outcome. A better contrast might be the enormous variety of cognitive and emotional effects claimed for TMS of the dorsolateral prefrontal cortex.

We now also note that TMS of lateral frontal cortex has not been associated with similarly high specificity (Discussion, pg. 6). Note however that we cannot exclude anti-depressant or other psychological effects of HITS, as such outcomes were not consistently assessed in HITS studies and so were not included in our analyses.

(6) With reference to why other nodes in the episodic memory network have not been tested, current flow modeling shows TMS of the medial prefrontal cortex is unlikely to be achievable without stronger stimulation of the convexity under the coil, in addition to being uncomfortable. The lateral temporal lobe has been stimulated without undue discomfort.

We now additionally indicate that medial prefrontal stimulation may be ineffective given conventional TMS (Discussion, pg. 7). However, we are aware of no studies that have stimulated the portion of middle temporal gyrus that shows strong connectivity with hippocampus. We have tried this location, which positions the coil on or slightly above the ear and bordering on the temple area that is very sensitive to most. We were not able to minimize pain/discomfort for most subjects in pilot experiments, and so had to abandon it. Perhaps others have succeeded? If the reviewer has any specific references that could be included we would be happy to add them and update this section accordingly.

(7) Finally, a critical question hanging over the clinical applicability of HITS and other neuromodulation techniques is how well they will work on a damaged substrate. Functional and/or anatomical imaging might answer this question and help screen for likely responders. The authors' opinion on this would be informative.

We appreciate this point but don’t think there are enough data to assess the level of substrate damage needed to frustrate any stimulation benefits. The only thing we can say is that HITS was equally effective for mild to moderate Alzheimer’s dementia as it was for other non-neurodegenerative groups (nonsignificant effect of the Population factor, Figure 3B), suggesting that whatever degree of damage present in that group is insufficient to prevent the stimulation effects. We now highlight this point and raise the issue that, presumably, some level of damage would render HITS ineffective (Discussion, pg. 8).

Reviewer #3 (Public review):

(1) My only significant concern is how studies are categorized in the 'Timing' factor (when stimulation is applied). Currently, protocols in which TMS is administered across days are categorized as 'pre-encoding' in the Timing factor. This has the potential to be misleading and may lead to inaccurate conclusions. When TMS is administered across multiple days, followed by memory encoding and retrieval (often on a subsequent day), it is not possible to attribute the influence of TMS to a specific memory phase (i.e., encoding or retrieval) per se. Thus, labeling multi-day TMS studies as 'pre-encoding' may be misleading to readers, as it may imply that the influence of TMS is due to modulation of encoding mechanisms per se, which cannot be concluded. For example, multi-day TMS protocols could be labeled as 'pre-retrieval' and be similarly accurate. This approach also pools results from TMS protocols with temporal specificity (i.e., those applied immediately during encoding and not on board during memory testing) and without temporal specificity (i.e., the case of multi-day TMS) regarding TMS timing. Given the variety of paradigms employed in the literature, and to maximize the utility/accuracy of this analysis, one suggestion is to modify the categories within the Timing factor, e.g., using labels like 'Temporally-Specific' and 'Temporally Non-specific'. The 'Temporally-Specific' category could be subdivided based on the specific memory process affected: 'encoding', 'retrieval', or 'consolidation' (if possible). I think this would improve the accuracy of the approach and help to reach more meaningful conclusions, given the variety of protocols employed in the literature.

We agree in principle with this criticism and think that the most straightforward way to address it is to relabel the “Pre-Encoding” category as “Pre-Task”. The issue with labeling/considering single-session stimulation delivered immediately before encoding as “Pre-encoding” is that this makes the assumption that this stimulation doesn’t also affect retrieval (i.e., is temporally specific). We do not have certainty about the timecourse of how a single session of stimulation affects brain activity. We think the “Pre-Task” label and interpretation is the best way to address this, to avoid suggesting that we are confident about the timecourse/selectivity of stimulation effects. Notably, the “Sessions” factor directly compares among designs that delivered stimulation in a single session versus in multiple consecutive sessions, and was a nonsignificant modulator. Thus, our analyses already compare studies that are relatively temporally specific versus those that, likely, are less so. In addition to relabeling, we have also added clear caveats to address the interpretive constraint imposed by the unknown timecourse of stimulation effects (Discussion, pg. 6-7) and revised the Abstract to reflect this change.

(2) As the scope of the meta-analysis is limited to TMS applied to parietal or superior occipital cortex, it is important to highlight this in the Introduction/Abstract. The 'HITS' terminology suggests a general approach that would not necessarily be restricted to parietal/nearby cortical sites.

This was previously highlighted only in the Methods and Discussion (with a Discussion paragraph dedicated to the issue of target selection; see also Comment 6 from Reviewer 2). We now also note this in the Introduction (pg. 2) and Abstract.

Minor:

(1) To reduce the number of study factors tested, data reduction was performed via Lasso regression to remove factors that were not unique predictors of the influence of TMS on memory. This approach is reasonable; however, one limitation is that factors strongly correlated with others (and predict less unique variance) will be dropped. This may result in a misrepresentation, i.e., if readers interpret factors left out of this analysis as not being strongly related to the influence of TMS on memory. I do see and appreciate the paragraph in the Discussion which appropriately addresses this issue. However, it may be worth also considering an alternative analysis approach, if the authors have not already done so, which explicitly captures the correlation structure in the data (i.e., shown in Figure S2) using a tool like PCA or an appropriate factor analysis. Then, this shared covariance amongst factors can be tested as predictors of the influence of TMS - e.g., by testing whether component scores for dominant PCs are indeed predictive of the influence of TMS. This complementary approach would capture rather than obfuscate the extent to which different factors are correlated and assess their joint (rather than independent) influence on memory, potentially resulting in more descriptive conclusions. For example, TMS intensity and protocol may jointly influence memory.

We argue that feature selection via Lasso regression is a better approach for our research question than PCA, factor analysis, or other latent variable methods. The main reason is that PCA would sacrifice the interpretability of our findings with respect to the design of future experiments using or testing HITS. That is, because PCA creates composite components that are linear combinations of multiple variables, we would lose the ability to provide clear, actionable guidance to researchers about which specific study design choices (e.g., stimulation intensity, protocol type, timing) influence memory outcomes. Given that a major goal of our meta-analysis is to inform future experimental design, we believe that it is essential to maintain interpretability of the individual factors that must be decided when designing a study. Regarding factor analysis, this approach would require making a priori theoretical decisions about how to group individual moderators, which could introduce subjective bias into the analysis and would introduce other complications such as a need for validation of the resulting factor scores. We believe that the exploratory nature of our investigation, examining which among many possible study design factors substantially determine TMS efficacy, is better suited to a data-driven selection approach like Lasso. While the reviewer correctly notes that Lasso may drop factors that are correlated with stronger predictors, this feature can be considered advantageous in terms of identifying factors for inclusion in future study designs. That is, this can help identify the most parsimonious set of independent predictors, such that researchers can focus on the study design elements that matter most when controlling for other factors. Notably, we provide the table of factor relationships (Figure S2) so that interested readers can inspect how dropped factors were related to those that were retained.

It is also important to note that we have provided the full dataset with our resubmission, which has been deposited in Dryad with a link in the Data Availability section (pg. 15). Thus, others are free to explore alternative analytical approaches should they wish to examine the data from different perspectives or to answer different questions.

(2) Given the specific focus on TMS applied to parietal cortex to modulate hippocampal and related network function, it would be fruitful if the authors could consider adding discussion/speculation regarding whether this approach may be effectively broadened using other stimulation methods (e.g., tACS, tDCS), how it may compare to other non-invasive brain stimulation methods with depth penetration to target hippocampal function directly (transcranial temporal interference, or transcranial focused ultrasound), and/or how or whether other stimulation sites may or may not be effective.

We briefly discuss a meta-analysis of tACS studies which reported nonspecific effects, including for parietal targets overlapping those used for HITS (Discussion, pg 6). We briefly speculate about how tES effects remain mechanistically uncertain. We are afraid that further speculation about other stimulation modalities and targets would be beyond the scope of this focused meta-analysis, given especially the few datapoints for newer approaches such as TI or tFUS.

(3) Studies were only included in the meta-analysis if they contained objective episodic memory tests. How were studies handled that included both objective and subjective memory, or other non-episodic memory measures? For example, Yazar et al. 2014 showed no influence of TMS on objective recall, but an impairment in subjective confidence. I assume confidence was not included in the meta-analysis. Similarly, Webler et al. 2024 report results from both the mnemonic similarity task (presumably included) and a fear conditioning paradigm (presumably excluded). Please clarify in the methods how these distinctions were handled.

Studies were included in our meta-analysis if they included at least one objectively scorable test of episodic memory. We only included objectively scorable test performance in our analysis, excluding scores from any other subjective measures if they were also reported. This is now clarified in Methods (pg. 9).

(4) The analysis comparing memory to non-memory measures is important, showing the specificity of stimulation. Did the authors consider further categorizing the non-memory tasks into distinct domains (i.e., language, working memory, etc.)? If possible, this could provide a finer detail regarding the selectivity of influences on memory vs. other aspects of cognition. It is likely that other aspects of cognition dependent on hippocampal function may be modulated as well, i.e., tasks with high relational/associative processing demands.

This is an interesting idea, but it is beyond our expertise to categorize these other tasks based on the nature of processing demands that they capture. Note that the task names are provided in the data table that we are making available online with our submission of record (via Dryad), such that other groups could address this question if interested.

(5) In the analysis of the Intensity factor, how were studies using Active (rather than resting) MT categorized? Only resting MT is mentioned in Table S1. This is important as the original theta-burst TMS protocol from Huang et al. 2005 determines intensity based on Active Motor Threshold.

MT was resting/passive in all reviewed studies except for one (Tambini et al. 2018), which used 80% of active MT. We categorized this as <100% MT for the Intensity factor, as it was <100% of MT as defined in that study. Although one could make the argument that 80% AMT might instead correspond to 100+% RMT, this change would have very little influence on our results or conclusions. We now clarify this in Table S1.

(6) Is there a reason why the study by Koen et al. 2018 (Cognitive Neuroscience) was not included? TMS was performed during encoding to the left AG, and objective memory was assessed, so it would seemingly meet the inclusion criterion.

The failure to include Koen et al. 2018 was our error. Koen et al. 2018 is the only study that used “online” stimulation, delivered during the trials when memoranda were displayed for encoding in the task. In contrast, all other reviewed studies delivered “offline” stimulation either before the memoranda was presented (“Pre-Task”) or after the encoding period but before retrieval (“Post-Encoding”). Therefore, categorization for the “Timing” factor would be problematic for its inclusion in the main analysis. We therefore now include Koen et al. 2018 in the “Supplementary Results” section as well as the corresponding main Results section on “Similar outcomes in studies that were excluded from meta-analysis”. We also note in the relevant discussion that “online” stimulation, as done in Koen et al. 2018, is typically considered disruptive (e.g., Beynel et al. 2019 Neuroscience & Biobehavioral Reviews; Yeh & Rose 2019 Frontiers in Psychology), which should be taken into account when considering the findings of Koen et al. 2018 relative to other reviewed studies that used “offline” designs.

(7) It would be helpful to briefly differentiate the current meta-analysis from that performed by Yeh & Rose (How can transcranial magnetic stimulation be used to modulate episodic memory?: A systematic review and meta-analysis, 2019, Frontiers in Psychology) (other than being more current).

Beyond being more current and therefore including many more studies in which stimulation targets were based on hippocampal connectivity (which tend to have been published more recently), the differences with Yeh & Rose 2019 are subtle. Our review focuses on assessment of network targeting and whether effects were specific to episodic memory versus other tasks, which differs somewhat from the focus of Yeh & Rose 2019. The main difference in conclusions likely derives from there being more network-focused memory TMS experiments now than were available for Yeh & Rose’s review. We also differentiate episodic memory into recollection versus other components to test specificity and analyze modulation by many study design factors relevant to HITS studies that were not emphasized in Yeh & Rose’s review. Note that we now cite Yeh & Rose for those interested in potential differences.

(8) For transparency and to facilitate further understanding of the literature and potential data re-use, it would be great if the authors consider sharing a supplementary table or file that describes how individual studies/memory measures were categorized under the factors listed in Table S1.

As promised in our original submission, we are providing the full data table, including how individual studies and memory measures were categorized, as an open dataset in Dryad. The Dryad dataset is cited in “Data availability” (pg. 15).

Reviewer #3 (Recommendations for the authors):

Please explicitly state in the Methods (Meta-analysis of effect modifiers section) that the criteria used for categorizing each measure into a factor (e.g., probing Recollection, Recognition, etc.) are fully described in Table S1; this will help readers to find these details (it took me a while!).

This is now emphasized (pg. 10).

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer 1 (Public review):

(1) "The timescales of the peptide recognition and unbinding process are much longer than what can be sampled from unbiased simulations. Therefore, the proposed mechanism of recognition should only be considered a hypothesis based on the results presented here. For example, peptides that do not dissociate within one one-microsecond MD simulation are considered to be stable binders. However, they may not have a viable way to bind to the narrow protein cleft in the first place."

We thank the Reviewer for this valuable feedback and we agree with the Reviewer. Our work on the IRE1 cLD activation mechanism is focused on generating a hypothesis of the binding mechanism driven by MD simulations. We recognize the limitations in defining a stable binder due to the time scales sampled. However, our primary focus was to sample and characterize a possible binding pose in the center of the cLD dimer. We contextualized our statements about stable binders and limited our claims to stating that the protein-peptide complex is stable within 1 µs-long simulations. However, we believe that our finding that the cLD dimer groove is not able to accommodate peptides is solid, as the steric impediment described is present in all our replicas, both with and without peptides, in a cumulative sampling time of 24 µs without peptides and 66 µs with peptides. Additionally, we included a plot showing the distribution of groove width across all replicas.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) The title was changed from “Unfolded polypeptides can stably bind to hIRE1α cLD dimer” to “Unfolded polypeptides bind to hIRE1α cLD dimer surface”

Addition to the text. (Figure 15 A legend) “(A) Distributions of the groove width of peptide-bound cLD dimers throughout all simulations performed. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

(2) Oftentimes, representative structures sampled from MD simulation are used to draw conclusions (e.g., Figure 4 about the role of R161 mutation in binding affinity). This is not appropriate as one unbinding event being observed or not observed in a microsecond-long trajectory does not provide sufficient information about the binding strength of the free energy difference.

We thank the Reviewer for the insightful comment. As explained in the previous point, we believe that our simulations provide useful hypotheses. We are aware of the limitations due to the timescale and agree that these limitations cannot be overcome with standard equilibrium simulations. To address these limitations, used orthogonal methods, specifically MM/PB(GB)SA calculations, to calculate binding free energies from existing trajectories. We added predictions of all the peptides using AlphaFold 3, to confirm the binding region. Importantly, we now provide experimental results to assess the binding affinity of cLD dimer mutants E102R and Y161R.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “AlphaFold3 predictions of the complexes indicate that the peptides adopt the same preferred orientation, despite being predominantly helical (Supplementary Fig. 16A). We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

Addition to the text. (Figure 16 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD dimer in complex with peptides. Colors represent the confidence of the prediction (plDDT). (B) Difference in enthalpy (enthalpy of binding, ∆H) as an estimate of the binding free energies of unfolded polypeptides to hIRE1α cLD dimer derived from MM/PBSA calculations of our peptide simulations.”

Addition to the text. (Figure 4 G legend) “(G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Results section: Point mutations destabilize unfolded peptide binding to cLD) “To experimentally test whether these residues are involved in hIRE1α LD’s interaction with peptides, we expressed and purified these mutants and conducted fluorescence anisotropy experiments using fluorescently labeled MPZ1N-2X peptide. We could purify both E102R and Y161R mutants to high purity (Supplementary Fig. 18C). They both behaved similarly to the wild type during purification. Notably, both E102R and Y161R mutants demonstrated around two-fold lower binding affinity (Fig. 4G, E102 K_1/2= 6.35 µM and Y161R K_1/2= 5.4 µM, Supplementary Table 3) compared to the wildtype (K_1/2= 2.14 µM, Supplementary Table 3), revealing that the protein’s central area is crucial for binding unfolded proteins and that binding activity occurs within the pocket defined by E102 and Y161.”

Addition to the text. (Figure 4G legend) “(G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Supplementary Table 3)

Reviewer 2 (Public review):

(1) Improving presentation to include more computational details.

We thank the Reviewer for raising this critical point. We agree that the manuscript is tailored for a biology audience, as the data are particularly relevant for that community. Nevertheless, we also understand the importance of providing sufficient methodological detail for computational readers. We added more references to the methods for computational information in the main text.

(2) More quantitative analysis in addition to visual structures.

We added an uncertainty estimate for the HDX calculations using bootstrapping and included additional information on bond distances for E102 and Y161. We also incorporated time-series data showing the distance of the peptide from the groove across all replicas.

Addition to the text. (Figure 1C legend) “(C) The deuterated fraction obtained from experimental results (dashed line, shaded area indicates the error we calculated from bootstrapping) published by Amin-Wetzel et al. and the fraction computed from MD simulations (solid lines, blue for TIP3P water and orange for TIP4PD water) for the PDB and AF model at incubation time point 0.5 min. This time point corresponds to experimental incubation times, not MD simulation time. Each point represents the mean value derived from three replicas and two monomers per replica. The error bars were obtained from bootstrapping. Below each absolute value plot, we report the discrepancy, which is defined as the difference between the simulated and experimental deuterated fractions, with the shaded area indicating the corresponding error.”

Addition to the text. (Figure 15B legend) “(B) Minimum groove-peptide distance over time for all simulations of cLD dimer in complex with a peptide. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

Reviewer 3 (Public review):

A potential weakness of the study is the usage of equilibrium (unbiased) molecular dynamics simulations, so that processes and conformational changes on the microsecond time scale can be probed. Furthermore, there can be inaccuracies and biases in the description of unfolded peptides and protein segments due to the protein force fields. Here, it should be noted that the authors do acknowledge these possible limitations of their study in the conclusions.

We appreciate the Reviewer’s thoughtful comment. As noted in our response to Reviewer 1, we addressed the concern about sampling by applying orthogonal methods and experimental techniques. We agree with the Reviewer that some form of enhanced sampling is necessary if we want to assess binding in a more quantitative way, e.g., via free energy calculations. However, we also realize that applying any enhanced sampling scheme to our system is very challenging, given its large size and the complex peptide-protein interactions, which are not easily captured in a few collective variables. After a careful assessment and some preliminary tests, we decided that estimating free energies using enhanced sampling would necessitate a separate paper due to both the conceptual complexity of the project and the size of the necessary sampling campaign.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Some enhanced sampling or path sampling simulations may be carried out to identify the peptides’ binding and unbinding mechanisms to the protein. This can show whether the disordered peptides studied in this work do indeed bind to the protein.

We thank the Reviewer for this constructive criticism. We acknowledge the limitations associated with investigating binding and unbinding mechanisms of disordered peptides within the time scales accessible to our equilibrium simulations. However, the primary objective of our study was to sample and characterize a plausible binding pose at the center of the cLD dimer. We wanted to understand if unfolded model peptides require an open groove able to contain them to bind to IRE1’s core luminal domain or if binding also in the absence of an open groove.

Enhanced sampling is, of course, an important strategy to overcome the limits of equilibrium simulations. However, we note that implementing enhanced sampling approaches in this system poses significant challenges due to its large size and the complexity of peptide–protein interactions, which cannot be easily captured using a limited set of collective variables. We decided that a thorough application of enhanced sampling would therefore constitute a separate study. Instead, we decided to validate our simulations in two ways: 1) we ran a new set of free energy calculations, and 2) we tested key predictions in experiments, adding significant new data to strengthen the conclusions of our manuscript.

To evaluate whether the binding free energies of MPZ-derived peptides to human IRE1α cLD dimers are consistent with experimentally reported binding constants, we employed the MM/PBSA (Molecular Mechanics/Poisson–Boltzmann Surface Area) method. Calculations were performed over the final 250 ns of each simulation replica using the Single Trajectory Protocol (STP), which avoids the need for additional simulations. This approach provides an estimate of the effective binding free energy (i.e., enthalpy of binding) by accounting for bonded and non-bonded interactions, as well as solvation contributions. The entropic contribution, being computationally more demanding and subject to additional approximations, was not included. Binding enthalpies were obtained for MPZ1-N (in different initial orientations), MPZ1-C, MPZ1-N-2X, and MPZ1-N-2X-RD. The results indicated small differences in effective binding energies between the shorter peptides (MPZ1-N and MPZ1-C), whereas MPZ1-N-2X exhibited the lowest binding energy and MPZ1-N-2X-RD the highest, consistent with experimental trends. These findings support the reliability of our model and sampling strategy as a framework for analyzing peptide binding conformations to cLD.

We identified residues E102 and Y161 as key contributors to the binding of unfolded peptides in our simulations. Contact analysis revealed these residues as binding hotspots, centrally located within the observed interaction regions. To probe their relevance, we conducted simulations of cLD dimers with single arginine mutations in these residues, aimed at disrupting these hotspots through charge repulsion. These simulations revealed increased instability of the MPZ1N2X on the cLD dimer surface. We further validated these findings experimentally using fluorescence anisotropy assays. Fluorescently labeled MPZ1N-2X was titrated with purified cLD mutants (E102R and Y161R), and anisotropy measurements were fitted to derive  K_1/2 values. Both mutations resulted in approximately a two-fold reduction in binding affinity relative to the wild-type cLD, confirming the importance of these residues in stabilizing peptide binding.

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “Thus, we investigated how the point mutations of two key residues, E102R and Y161R, would affect peptide binding by simulating the cLD mutant in complex with MPZ1N-2X (Fig. 4C-E). We initialized the systems in the pose described for the other peptide-cLD systems described earlier (Fig. 3B, t = 0 µs). In simulations of the wild-type (WT) cLD dimer, the peptide generally remained near the center (Fig. 4C,F). By contrast, MPZ1N-2X displayed reduced binding to E102R, fully dissociating in one TIP4P-D replica (Fig. 4E,F). A similar trend was observed for Y161R, where one partial dissociation event occurred (Fig. 4D,F). Comparative analysis of MPZ1N-2X contact sites on the WT and mutant cLD dimers (Supplementary Fig. 17B-D) revealed that, in the presence of mutations, the peptide engages a broader surface region rather than remaining centrally localized, while forming fewer contacts with the specific residues (Supplementary Fig. 18A-B).”

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “To experimentally test whether these residues are involved in hIRE1α LD’s interaction with peptides, we expressed and purified these mutants and conducted fluorescence anisotropy experiments using fluorescently labeled MPZ1N-2X peptide. We could purify both E102R and Y161R mutants to high purity (Supplementary Fig. 18C). They both behaved similarly to the wild type during purification. Notably, both E102R and Y161R mutants demonstrated around two-fold lower binding affinity (Fig. 4G, E102  K_1/2= 6.35 µM and Y161R  K_1/2= 5.4 µM, Supplementary Table 1) compared to the wildtype (K_1/2= 2.14 µM, Supplementary Table 1), revealing that the protein’s central area is crucial for binding unfolded proteins and that binding activity occurs within the pocket defined by E102 and Y161.”

Addition to the text. (Figure 4 legend) “(E) Side view snapshot after 1 µs of simulation of E102R hIRE1α cLD dimer (gray) in complex with MPZ1N-2X (orange). The amino acid R102 on both monomers is represented in magenta sticks. (F) Time series of the minimum groove-peptide distance for MPZ1N-2X simulated in complex with wild-type, E102R, and Y161R hIRE1α cLD dimer in TIP3P (3 replicas) and TIP4P-D (3 replicas) water. The darker lines show the rolling average over 25 frames, while the shaded lines represent the raw data. (G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Methods section: Binding free energy calculations (MM/PBSA)) “The binding free energy of noncovalently bound complexes of human IRE1 cLD and peptides was calculated with MM/PBSA (Molecular mechanics/PoissonBoltzmann Surface Area) method via gmx_MMPBSA (version 1.6.4)[1, 2]. The Poisson-Boltzmann method was used to estimate the electrostatic contribution to solvation free energy as recommended for data obtained with the CHARMM force field. The contribution of the entropic term was omitted, obtaining effective binding free energy values, or enthalpy of binding (∆H). We used the Single Trajectory Protocol (STP), using the cLD-peptide simulations as input. The calculations were performed on the last 250 ns of each replica. Single-term total non-polar solvation free energy (inp = 1) was used. The charmm_radii (PBRadii= 7) was used to build amber topology files [3]. The default parameters were applied for other terms.”

Addition to the text. (Methods section: Protein purification) “To express hIRE1α LD (24-443) human cDNA sequences were cloned into pET47b(+) to create a coding sequence with N-terminal His6-tag. Mutations of hIRE1α LD were introduced by overlap extension PCR and restriction cloning into pET47b(+). For expression of the proteins, the plasmid of interest was transformed into Escherichia coli strain BL21DE3* RIPL (Agilent Technologies). Cells were grown in Luria Broth until OD600=0.6-0.8. Protein expression was induced with 0.6 mM IPTG, and cells were grown in 20°C overnight. For purification, cells after harvesting were resuspended in Lysis Buffer (50 mM HEPES pH 7.2, 400 mM NaCl, 20 mM imidazole, 5% glycerol, 5 mM β-mercaptoethanol) and were lysed in Constans Systems cell disruptor at 25 000 psi. The supernatant was collected after centrifugation for 45 minutes at 48000×g in 4°C. Supernatant was loaded onto Ni-NTA column (Cytiva) and the protein eluted with a linear gradient of imidazole from 20 to 500 mM. Fractions containing the protein were diluted 1:8 with anion exchange wash buffer (50 mM HEPES pH 7.2, 5 mM β-mercaptoethanol), loaded onto HiTRAP-Q ion exchange column (Cytiva) and eluted with a linear gradient from 50 mM to 1 M NaCl. Afterwards, the His6tag was removed by cleavage with Precission protease (GE Healthcare, 1 µg of enzyme per 100 µg of protein). The cleavage was performed overnight in 4°C. The protein sample after cleavage was loaded onto a Ni-NTA column, and the flow-through containing protein without the tag was collected. The protein was further purified on a Superdex 200 10/300 gel filtration column equilibrated with Buffer A (25 mM HEPES pH 7.2, 150 mM NaCl, 2 mM DTT). Protein concentrations were determined using extinction coefficient at 280 nm predicted by the Expasy ProtParam tool (http://web.expasy.org/protparam/).”

Addition to the text. (Methods section: Fluorescence anisotropy) “For fluorescence anisotropy measurements, the MPZ1-N-2X peptide attached to 5 carboxyfluorescein (5-FAM) at its N-terminus was obtained from GenScript at >95% purity. Binding affinities of hIRE1α LD mutants to FAM-labeled peptides were determined by measuring the change in fluorescence anisotropy on a Tecan CM Spark Micro Plate Reader with excitation at 485 nm and emission at 525 nm with increasing concentrations of hIRE1α LD variants. Measurements were performed in Buffer A supplemented with Tween 20 (25 mM HEPES pH 7.2, 150 mM NaCl, 2 mM DTT, 0.025% Tween 20). Fluorescently labeled peptides were used in a concentration of 90 nM. The reaction volume of each data point was 25 µL and the measurements were performed in 384-well, black flat-bottomed plates (Corning) after incubation of peptide with hIRE1α LD variants for 30 min at 25◦C. Binding curves were fitted using Prism Software (GraphPad) using the following equation: F_bound = r_free +( r_max − r_free)/(1+10((Log K_1/2 −x)·n_H)), where F_bound is the fraction of peptide bound, r_max and r_free are the anisotropy values at maximum and minimum plateaus, respectively. n_H is the Hill coefficient and x is the concentration of the protein in log scale. Curve-fitting was performed with minimal constraints to obtain K_1/2 values with high R² values. However, as this equation does not consider the equilibria between hIRE1α LD dimers/oligomers, these apparent K_1/2 values do not reflect the dissociation constant.”

(2) Wherever possible, conclusions related to binding affinity should not be drawn from single unbinding events. For example, the title of Figure 4, "Single point mutation of cLD alters the binding affinity of unfolded peptide," should be softened. Similar changes should be made throughout the manuscript where such claims have been presented.

We thank the Reviewer for highlighting this important point. In the revised manuscript, we have adjusted the text to remove or soften conclusions related to binding affinity that were based on single unbinding events in the MD simulations.

Addition to the text. (Figure 4 title) “Single point mutations of cLD alter the binding of unfolded peptide MPZ1N-2X.”

Addition to the text. (Results section title: Unfolded polypeptides can stably bind to hIRE1α cLD dimer) “Unfolded polypeptides bind to hIRE1α cLD dimer surface.”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1αα cLD dimer surface) “Our goal was to elucidate a potential binding pose and identify the relevant features of unfolded proteins and the cLD that affect the binding.”

Reviewer #2 (Recommendations for the authors):

(1) A table of all simulated trajectories, including simulation conditions, number of replicas, box size, number of atoms, equilibration length, recording time step, number of frames for further analysis.

We thank the Reviewer for this helpful suggestion. We have added a summary table of all simulations, including the requested details, to the Supplementary Information (Table 1).

Addition to the text. (Supplementary figures and tables: Table 2)

(2) The current NVT equilibration time was 0.125ns, and then no productive NPT simulations were mentioned as equilibration. Even though this is a simulation of mostly folded structures, it still takes some time for these amino acids to relax within the force field.

We thank the Reviewer for this constructive comment and acknowledge the validity of the concern. However, our simulations were extensively sampled, and equilibration was achieved within the first 50 ns of the production runs. Therefore, the segments of the trajectories from which we draw conclusions correspond to equilibrated states (see RMSD analysis, Figure 1). Additionally, binding free energy calculations (MM/PBSA) were carried out on the last 250 ns of the simulation replicas.

(3) At least three histograms were presented in Figure 2C, which I guess is from multiple simulations, and does not seem to be discussed.

We thank the Reviewer for pointing out the lack of reference to Figure 2C. We added the correct reference to the text where the groove width of luminal domains of human and yeast is discussed.

Author response image 1.

RMSD analysis of human IRE1_α_ cLD dimer simulated in complex with unfolded peptides.

Addition to the text. (Results section: The putative groove of human IREα cLD is dynamic but unable to contain peptides ) In simulations of the dimeric structures, the average groove width was 7.3 ± 0.1 Å for the human cLD and 8.9 ± 0.1 Å for the yeast cLD, averaged over three TIP3P and three TIP4P-D replicas per system (Fig. 2C).

(4) The comment regarding the CHARMM force field on Page 6 is not justified. Actually the force field the authors used (CHARMM36m, Jing et al Nat Methods 2016) did include scaling of TIP3P LJ parameters to correctly capture the dimensions of the intrinsically disordered proteins (IDPs). However, the authors cited a couple of examples of literature of previous versions of CHARMM force fields and commented that it cannot capture IDP dimensions with TIP3P.

We thank the Reviewer for pointing out this source of confusion. We cited the main papers of CHARMM as [4, 5], which were misleading, and following the Reviewer’s advice, we removed these citations.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “Current all-atom force fields used in MD simulations are mainly designed to reproduce the dynamics of folded and globular proteins [6].”

(5) I am fine that the authors used TIP4PD with CHARMM36m, but caution should be taken for such a combination of protein and water force fields. Note that when optimizing force fields for IDPs, one often has to balance protein-water interactions by either enhancing protein-water interactions, enhancing water dispersions, or reducing protein-protein interactions. So, all such optimization is dependent on both protein and water force fields. TIP4PD was designed to pair with Amber99sb-ildn or, most recently, Amber99sb-disp instead of CHARMM36m. This could result in rescaling of LJ parameters.

We thank the Reviewer for raising this issue. We argue that the TIP4P-D water model has been used in combination with the CHARMM36m force field [7] and has been shown to yield satisfactory results for disordered regions.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “The TIP4P-D water model was developed to address limitations of existing force fields in reproducing the structural ensembles of intrinsically disordered proteins and regions. It incorporates enhanced dispersion and moderately stronger electrostatic interactions to improve the balance between water dispersion and electrostatics [8]. Zapletal et al. [7] showed that for proteins containing both folded and disordered regions, the CHARMM36m force field [9] in combination with the TIP4P-D water model provides a robust framework, preventing collapse of disordered regions while preserving folded regions. Acknowledging that the behavior of disordered regions can be case-specific, we conducted molecular dynamics simulations of the two cLD dimer models using the CHARMM36m force field with both TIP3P and TIP4P-D water models.”

(6) I suggest referring to the methodology part for simulation details as much as possible when presenting the story.

We thank the Reviewer for this suggestion. In the revised manuscript, we now refer the reader to the Methodology section for detailed descriptions of the HDX-MS data analysis and the MM/PBSA free energy calculations.

Addition to the text. (Results section: Hydrogen-deuterium exchange experimental data validate the cLD dimer structure) “From our simulations, we calculated the theoretical deuterated fraction using the method by Bradshaw et al.[10] and compared it to the experimental data (Fig. 1C-D and Supplementary Fig. 10) (see Methods).”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

(7) Error bars and methodology of error analysis should be provided for all cases of all-atom simulations if possible, since convergence is always an issue when considering these conformational changes within microseconds of all-atom simulations.

We thank the Reviewer for the important observation. We agree and added error methodology for the estimation of theoretical deuterated fractions (Fig. 1C).

Addition to the text. (Figure C legend) “Each point represents the mean value derived from three replicas and two monomers per replica. The error bars were obtained from bootstrapping.”

Addition to the text. (Methods section: Hydrogen-deuterium exchange fractions calculation from MD simulations) “To reproduce the time points after incubation in deuterium (D₂O), we computed deuterated fractions separately for each of the two monomers constituting a dimer for the time points 0.5 min (30 s) and 5 min (300 s). Then, we computed the mean and standard deviation over the data coming from replicas of the same cLD dimer model (AF or PDB model) and the same water model (TIP3P or TIP4P-D). To estimate the uncertainty of the mean values obtained from our datasets and the dataset from Amin-Wetzel et al. ([11] Figure 3—source data 1), we applied a non-parametric bootstrap resampling procedure. For each sequence range from HDX-MS analysis, we treated the measurements from the N=6 independent datasets as independent samples, accounting for 3 replicas each with two monomers (6 monomers total). We then generated 10,000 bootstrap replicates by sampling the datasets with replacement, maintaining the same number of samples N in each resample. For each replicate, we calculated the mean at each sequence position. The resulting distribution of bootstrap means was used to compute the standard deviation as an estimate of the standard error. We computed the difference between simulation and experimental data (deuterated fraction discrepancy), and for each residue, we selected as the ‘best structure’ the model with the discrepancy closest to zero among PDB-TIP3P, PDB-TIP4P-D, AF-TIP3P, and AF-TIP4P-D systems.”

(8) Technically I would call DR1 and DR2 linker regions within a folded structure. Their motions are quite restrained by the fold part. I therefore, am not sure how much TIP4PD really helps in contrast to a scaled TIP3P. A plot of structures colored with PLDDT score or b-factor within the PDB should be provided. Quantitative metrics of these regions (e.g. chi chi-squared) might help justify the choice of the AF model against the PDB model. Currently, the two models look very similar in Figures 1c and 1d. Similarly, quantitative metrics as a function of different simulation time windows will help justify the convergence of the simulation and indicate the flexibility of these regions.

We thank the Reviewer for this thoughtful comment. In response, we analyzed the AlphaFold2 and AlphaFold3 predictions, which consistently assign very low pLDDT values (<50) to the DR2 region, while DR1, is predicted with higher but still low confidence (50 < pLDDT < 70). These scores indicate intrinsic uncertainty in the structural definition of both regions, supporting their flexibility despite being located within a folded context.

Addition to the text. (Results section: The hIRE1_α_ cLD forms a stable dimer) “All five AlphaFold 2 predictions closely resembled the top-ranked model used for our simulations (Supplementary Fig. 7C). In contrast, the five AlphaFold 3 predictions yielded greater variability in DR2 organization and longer helices in DR2, but still consistently maintain low pLDDT scores in this region, indicating disorder (Supplementary Fig. 7D).”

Addition to the text. (Figure 7 C-D legend) “(C) Superposition of the 5 structures predicted by AlphaFold 2 Multimer for the cLD dimer and colored by confidence prediction score (pLDDT). (D) Superposition of the 5 structures predicted by AlphaFold 3 for the cLD dimer and colored by confidence prediction score (pLDDT).”

(9) Fluorescence anisotropy seems to be an important set of experimental data to justify the binding of multiple unfolded peptides to IRE. I suggest the authors include a bar plot of binding affinity of different variants in Figure 3. The raw titration curves should also be included in SI.

We thank the Reviewer for this valuable suggestion. The binding affinities reported in previous studies are summarized in Table 2; the reader is referred to those works for the corresponding raw titration curves. The binding affinities for the cLD mutants analyzed in the present study are provided in Table 3, and the associated titration curves are shown in Figure 4G.

Addition to the text. (Figure 4G legend) “Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Supplementary figures and tables: Table 3) See Tab. 1

(10) The authors should discuss the dependence of initial orientations of unfolded peptides on the final results. The authors claimed that after 1 microsecond simulations, the orientation of these peptides to IRE changed. Quantitative metrics showing both the binding (e.g., number of contacts) and binding orientation (contact region or angles) should be provided to tell whether the simulation is converged. The comparison to the experimental data lacks quantitative metrics. The authors mentioned the dissociation of MPZ1N-2X-RD in half of the simulations; they might want to provide such a metric for all peptides. Technically, 1 microsecond brute-force simulation is quite short for observing such a binding event, and enhanced sampling methods (e.g. metadynamics) might be necessary for investigating binding. However, at least the presentation and interpretation of the current results should be improved for comparing simulations and experiments.

We thank the Reviewer for the insight. We expanded the discussion of the peptide orientation and added an analysis of the peptide angle with respect to the cLD central groove and contacts. Additionally, we inserted AlphaFold 3 predictions of all the simulated complexes.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1_α_ cLD dimer surface) “In initial simulations with peptides valine8 and MPZ1-N, we positioned the polypeptides over the cLD, aligning them parallel to the principal axis of the central groove in accordance with the proposed binding mode. We refer to this pose as the "0◦ orientation", as the peptide forms a 0 ◦ angle with the principal axis of the groove. We observed that the peptides could rearrange into an orientation perpendicular to the central groove axis, while maintaining contact with the dimer (Fig. 3A, Supplementary Fig. 13A, valine8 TIP4P-D, and Supplementary Fig. 14). Conversely, when MPZ1-N was initially oriented perpendicularly to the groove, it did not transition to a parallel (0◦) orientation (Supplementary Fig. 14). We refer to these poses as the "90◦ orientation" and "270◦ orientation".”

Addition to the text. (Supplementary Figures and Tables Fig. 14) “(A) Peptide orientation with respect to the central groove principal axis. The angle was computed as the dihedral angle described by the Cα atoms of Y161 residues (groove principal axis) and the C_α_ atoms of residues L1 and A12 of the MPZ1N peptide. The dark lines indicate the rolling average of the fraction of native contacts over 10 frames, while the shaded lines indicate the value per frame. (B) Number of contacts between hIRE1α cLD dimer and MPZ1N peptide. The dark lines indicate the rolling average of the fraction of native contacts over 50 frames, while the shaded lines indicate the value per frame. The analysis were performed on three sets of simulations: "90 degrees" orientation, the peptide is initially placed perpendicular to the central groove principal axis; "270 degrees" orientation, the peptide is initially placed perpendicular to the central groove principal axis but flipped 180 degrees with respect to the 0 degree; "0 degrees" orientation, the peptide is placed parallel to the groove principal axis.”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “AlphaFold3 predictions of the complexes indicate that the peptides adopt the same preferred orientation, despite being predominantly helical (Supplementary Fig. ??A).”

Addition to the text. (Supplementary Figures and Tables Fig. 16A) “(A) Prediction of AlphaFold 3 for hIRE1α cLD dimer in complex with peptides. Colors represent the confidence of the prediction (plDDT).”

(11) I also have a couple of questions regarding the point mutant Y161R. a) The motivation of mutating Y161 to R is more speculative (Figures 4a,b) than quantitative. The authors might want to show an intermolecular contact map between IRE and unfolded peptides or IRE contact probability along residue indexes to show the interaction hotspots. Figure S11 only showed the structure instead of any metrics for such a purpose. b) It might be better to also show a histogram of the distances of Figure 4e and 4f. Figure 4f actually suggested 1 microsecond simulation is quite short to observe the dissociation event. c) Testing the mutation within the experiment, if possible, would clearly strengthen this part of the manuscript.

We thank the Reviewer for these constructive suggestions. We have added an analysis of intermolecular contacts for the Y161R and E102R mutants (Fig. 18A–B), which highlights the interaction hotspots between IRE1 residues and the unfolded peptides. To further characterize peptide–groove interactions, we now provide minimum peptide–groove distance time series for all peptides (Fig. 15B). Moreover, to experimentally support our simulations, we performed fluorescence anisotropy measurements on the MPZ1N-2X peptide with cLD WT and mutant constructs. These experiments confirm our computational observations (Fig. 4F–G and Fig. 18C).

Addition to the text. (Figure 18 legend) “(A) Number of contacts between residues 102 on both monomers and the MPZ1-N-2X peptide during simulations of WT hIREα LD and mutants E10R and Y161R. The dark lines indicate the rolling average of the fraction of native contacts over 25 frames, while the shaded lines indicate the value per frame. (B) Number of contacts between residues 161 on both monomers and the MPZ1-N-2X peptide during simulations of WT hIREα LD and mutants E10R and Y161R. The dark lines indicate the rolling average of the fraction of native contacts over 25 frames, while the shaded lines indicate the value per frame. (C) Protein purification of WT hIREα LD and mutants E10R and Y161R.”

Addition to the text. (Figure 4F-G legend) “(F) Time series of the minimum groove-peptide distance for MPZ1N-2X simulated in complex with wild-type, E102R, and Y161R hIRE1α cLD dimer in TIP3P (3 replicas) and TIP4P-D (3 replicas) water. The darker lines show the rolling average over 25 frames, while the shaded lines represent the raw data. (G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Figure 15B legend) “(B) Minimum groove-peptide distance over time for all simulations of cLD dimer in complex with a peptide. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

(12) Similar comments of quantitative analysis (e.g. contact map as a function of simulation time) apply to the last part of results when discussing the intermolecular interactions. Observations such as "the interface predicted by AlphaFold showed stability across MD simulation replicas lasting 200 ns" were provided, but there is no quantitative analysis. How consistent was this observation across multiple replicas of simulations, and how many replicas were used?

We thank the Reviewer for this valuable suggestion. To provide a quantitative assessment, we performed new triplicate simulations of the BiP–cLD monomer complex and plotted the fraction of native contacts over time. These results, which demonstrate the consistency of the interface across replicas, are now included in the Supplementary Material.

Addition to the text. (Figure 19 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ATP-bound BiP. The colors are as in Fig. 5B. (B) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ADP-bound BiP. (C) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with BiP not bound to any nucleotide. (D) Structure of hIRE1α cLDBiP-ATP after 2 µs of simulation. (E) Structure of hIRE1α cLD-BiP-ADP after 2 µs of simulation. (F) Structure of hIRE1α cLD-BiP after 2 µs of simulation.”

Addition to the text. (Figure 20 legend) “Fraction of native contacts between BiP and cLD monomer in simulations of the structures predicted by AlphaFold 3 without ligands or in complex with ADP or ATP. The dark lines indicate the rolling average of the fraction of native contacts over 100 frames, while the shaded lines indicate the value per frame. The fraction of native contacts (Q) was calculated according to the definition of Best et al. [12]: . For N pairs of native contacts (i, j), where is the distance of the pair in the initial configuration (here the AlphaFold 3 prediction), r_(i,j)(X) is the distance at frame X, β is a smoothing parameter (β = 50 nm⁻¹), λ is the tolerance of the reference distance (λ \= 1.8) and the cutoff used to define a contact between heavy atoms was 0.45 nm.”

(13) The figure legends are noted using lowercase letters but are described using uppercase.

We thank the Reviewer for pointing that out, and we changed everything to capital letters.

Reviewer #3 (Recommendations for the authors):

(1) Figure 1: I am confused about the HDX-MS results shown in Figure 1. Here, I must also mention that I am not familiar with comparing HDX-MS experiments with MD simulations. The authors mention that they show the deuterated fraction computed from MD simulations for the PDB and AF model at time points 0.5 min and 5 min. However, this time certainly does not correspond to the MD simulation time, thus, it is unclear to me where the difference between the results comes from. Are the two time points some input parameters to the script used to calculate the deuterated fraction? Thus, I would ask the authors to better explain what is the difference in the results between the two time points. Especially, since the general reader might not be familiar with comparing HDX-MS experimental results to MD simulations. Furthermore, I would ask the authors to clarify in the Figure 1 caption that these time points do not correspond to the MD simulation time.

We thank the Reviewer for pointing us to this possible source of confusion. The time points are effectively input parameters to the calculations of theoretical deuterated fractions from MD simulations. We expanded the explanation of the method in the method section and clarified in the Figure 1 caption that these time points do not correspond to the MD simulation time.

Addition to the text. (Methods section: Hydrogen-deuterium exchange fractions calculation from MD simulations) “To determine the deuterated fraction of a peptide segment from simulations, the protection factor for each residue i, Pi, must be computed from the simulation snapshots, following the approach of Best and Vendruscolo [13]: . Here, N_C,i and N_H,i are the number of H-bonds and heavy-atom contacts of the backbone amide of residue i, and the scaling factors β_C and β_H are set to 0.35 and 2.0, respectively. The simulated deuterated fraction of a peptide segment, , defined by residues m_j +1 to n_j, was then calculated at any exchange time point t as:

Where m_j and n_j are the first and last residue numbers of the j-th protein fragment, respectively. The intrinsic exchange rate constants for each residue type () were obtained from Bai et al. with updated acidic residues and glycine [14, 15].”

Addition to the text. (Figure 1 legend: ) “This time point corresponds to experimental incubation times, not MD simulation time.”

Addition to the text. (Figure 10 legend: ) “Time points correspond to experimental incubation times, not MD simulation time.”

(2) For AlphaFold 2 Multimer prediction, the authors only considered the top predicted structure. However, AF2-M, one generally obtains 5 structures, and it is also possible to obtain more structures by using an additional random seed. Thus, it would be interesting if the authors would consider the difference between the 5 structures they obtained from the AF2-M prediction. Are they all very similar? (Especially considering the DR1 and DR2 segments, that is the main difference between the PDB and AF2 structures). Analyzing the different predicted AF2 structures would give more insight into the accuracy of the AF2-M predicted model.

We thank the Reviewer for this insightful suggestion. All AF2-M predicted structures were found to be highly similar, and we now include them in Figure 7E for comparison.

Addition to the text. (Figure 7E legend) “(E) Superposition of the 5 structures predicted by AlphaFold 2 Multimer for the cLD dimer and colored by confidence prediction score (pLDDT).”

(3) On Page 6, the authors talk about a "an early PDB model". First, I find the nomenclature "early" confusing here; perhaps it would be better to talk about "an initial PDB model", but I leave it up to the authors to think about if they want to change that. More importantly, reading the Comp. detail on Page 23, it is not so clear what the difference is between the "early" and "final" PDB models, and how the difference in their setups leads to different results. The information is somewhat there on Page 6 and Page 23, but it can be made much clearer. Thus, I would ask the authors to better explain the difference between the early and final PDB models.

We thank the Reviewer for this helpful comment. In the revised manuscript, we have clarified the terminology and provided a more explicit explanation of the differences between the two IRE1 models, both in the Results section and in the Methods.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “An initial PDB model with modified side chain orientations in residues L116 and Y166 due to the modelling of neighbouring missing DR1, caused the dimer to dissociate in one-third of the replicas. [...] The final PDB model, with correctly oriented L116 and Y166 (Supplementary Fig. 9B), was stable in simulations in both TIP3P and TIP4P-D water (Supplementary Fig. 7B).”

Addition to the text. (Methods section: IRE1_α_ core Luminal Domain (cLD) structural models - Human PDB dimer) “An initial PDB model was briefly equilibrated in NPT, and a conformation with a groove width of approximately 0.6 nm was selected. This snapshot was used as the initial structure for the initial “PDB model” simulations, in which the dimer dissociates.”

(4) Page 12: "In early simulations", again, I find the nomenclature "early" confusing here. Perhaps it would be better to talk about "In initial simulations" or "In preliminary simulations", but I leave it up to authors to think about this.

We thank the Reviewer for pointing out this possible source of confusion. We improved the text by referring to these simulations based on the different orientations of the peptide on the cLD dimer in the modeled complex.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1_α_ cLD dimer surface) “In initial simulations with peptides valine8 and MPZ1-N, we positioned the polypeptides over the cLD, aligning them parallel to the principal axis of the central groove in accordance with the proposed binding mode. We refer to this pose as the "0° orientation", as the peptide forms a 0° angle with the principal axis of the groove. We observed that the peptides could rearrange into an orientation perpendicular to the central groove axis, while maintaining contact with the dimer (Fig. 3A, Supplementary Fig. 13A, valine8 TIP4P-D, and Supplementary Fig. 14). Conversely, when MPZ1-N was initially oriented perpendicularly to the groove, it did not transition to a parallel (0°) orientation (Supplementary Fig. 14). We refer to these poses as the "90° orientation" and "270° orientation".”

Here, we provide a detailed description of the additional changes made to the manuscript.

Additional edits to the manuscript

Following discussions with Prof. Dr. David Ron, we refined our BiP model by removing the signal peptide (residues 1–18). Using AlphaFold 3, we predicted BiP–cLD heterodimeric complexes in the presence of ADP, ATP, or without nucleotide. Each of the three complexes was simulated in TIP3P water, in three independent replicas of 1 µs each.

Addition to the text. (Results section: hIRE1α cLD intermolecular interactions guide the activation process) “We used AlphaFold 3 to model the interaction between a cLD monomer and BiP (residues E19–L654) in the presence of ATP and ADP (Fig. 5B, Supplementary Fig. 19A). Prediction quality was limited in the apo and ADP-bound states (pTM = 0.48, ipTM = 0.59; pTM = 0.49, ipTM = 0.61, respectively), whereas ATP binding improved accuracy (pTM = 0.66, ipTM = 0.72). The predicted interfaces involved DR2, particularly residues 314PLLEG-318, forming a short parallel β-sheet with the substrate-binding domain (SBD) of BiP through two hydrogen bonds. All AlphaFold 3 models were stable across three 1-µs simulations (Supplementary Fig. 19B), with cLD–BiP interfaces retaining 60–80% of initial contacts (Supplementary Fig. 20). In the apo and ADP-bound states, the nucleotide-binding domain (NBD) showed high Predicted Aligned Error (PAE) relative to the cLD, indicating uncertain positioning of the two domains relative to each other. Notably, in the ADP-bound state, which is thought to interact with hIRE1α cLD, the NBD remained mobile but proximal to the αB-helices, thereby restricting access to this region. Together, the AlphaFold 3 predictions suggest that BiP engages hIRE1α cLD by sterically hindering the oligomerization interface defined by DR2 and the αB-helices [16].”

Addition to the text. (Figure 5 legend) “(B) BiP-cLD monomer complex as predicted by AlphaFold (BiP in shades of purple, cLD in orange) before the simulation (t = 0 µs) and at the end of the simulation (t = 1 µs). The SBD (residues E19-D408) is colored in light purple, and the NDB (residues C420-E650) in dark purple, and the interdomain linker (residues D409-V419) and KDEL motif (residues K651-L654) in light purple.”

Addition to the text. (Figure 19 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ATP-bound BiP. The colors are as in Fig. 5B. (B) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ADP-bound BiP. (C) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with BiP not bound to any nucleotide. (D) Structure of hIRE1α cLDBiP-ATP after 2 µs of simulation. (E) Structure of hIRE1α cLD-BiP-ADP after 2 µs of simulation. (F) Structure of hIRE1α cLD-BiP after 2 µs of simulation.”

Addition to the text. (Methods section: cLD monomer in complex with BiP) “The BiP-cLD heterodimer systems were predicted with AlphaFold 3 using the AlphaFold server[17] at https://alphafoldserver.com/. The hIRE1α cLD sequence used is the same used for predicting the dimer: the PDB 2HZ6 sequence, Uniprot identifier O75460 with mutations C127S and C311S, and residues P29-P368. The BiP sequence used is taken from UniProt identifier P11021, residues E19L654. We predicted three complexes: one without any nucleotide, one containing ADP, and another containing ATP. Simulations of the BiP-cLD complex were run in TIP3P water.”

We have updated the Zenodo repository with additional data and calculations, and the corresponding link is provided in the manuscript.

References

(1) Mario S. Valdés-Tresanco, Mario E. Valdés-Tresanco, Pedro A. Valiente, and Ernesto Moreno. gmx_mmpbsa: A New Tool to Perform End-State Free Energy Calculations with GROMACS. Journal of Chemical Theory and Computation, 17(10):6281–6291, October 2021. Publisher: American Chemical Society.

(2) Bill R. III Miller, T. Dwight Jr. McGee, Jason M. Swails, Nadine Homeyer, Holger Gohlke, and Adrian E. Roitberg. MMPBSA.py: An Efficient Program for End-State Free Energy Calculations. Journal of Chemical Theory and Computation, 8(9):3314–3321, September 2012. Publisher: American Chemical Society.

(3) Fanhao Wang, Yuzhe Wang, Laiyi Feng, Changsheng Zhang, and Luhua Lai. Target-Specific De Novo Peptide Binder Design with DiffPepBuilder. Journal of Chemical Information and Modeling, 64(24):9135–9149, December 2024. Publisher: American Chemical Society.

(4) Alexander D. MacKerell Jr., Bernard Brooks, Charles L. Brooks III, Lennart Nilsson, Benoit Roux, Youngdo Won, and Martin Karplus. CHARMM: The Energy Function and Its Parameterization. In Encyclopedia of Computational Chemistry. 2002.

(5) Bernard R. Brooks, Robert E. Bruccoleri, Barry D. Olafson, David J. States, S. Swaminathan, and Martin Karplus. CHARMM: A program for macromolecular energy, minimization, and dynamics calculations. Journal of Computational Chemistry, 4(2):187–217, 1983.

(6) Junxi Mu, Hao Liu, Jian Zhang, Ray Luo, and Hai-Feng Chen. Recent Force Field Strategies for Intrinsically Disordered Proteins. Journal of Chemical Information and Modeling, 61(3):1037–1047, March 2021.

(7) Vojtech Zapletal, Arnošt Mládek, Kateˇ ˇrina Melková, Petr Louša, Erik Nomilner, Zuzana Jasenáková, Vojtˇ ech Kubᡠn, Markéta Makovická, Alice Laníková, Lukᚡ Žídek, and Jozef Hritz. Choice of Force Field for Proteins Containing Structured and Intrinsically Disordered Regions. Biophysical Journal, 118(7):1621–1633, April 2020.

(8) Stefano Piana, Alexander G. Donchev, Paul Robustelli, and David E. Shaw. Water dispersion interactions strongly influence simulated structural properties of disordered protein states. Journal of Physical Chemistry B, 119(16):5113–5123, April 2015.

(9) Jing Huang, Sarah Rauscher, Grzegorz Nawrocki, Ting Ran, Michael Feig, Bert L. de Groot, Helmut Grubmüller, and Alexander D. MacKerell. CHARMM36m: an improved force field for folded and intrinsically disordered proteins. Nature Methods, 14(1):71–73, January 2017.

(10) Richard T. Bradshaw, Fabrizio Marinelli, José D. Faraldo-Gómez, and Lucy R. Forrest. Interpretation of HDX Data by Maximum-Entropy Reweighting of Simulated Structural Ensembles. Biophysical Journal, 118(7):1649–1664, April 2020.

(11) Niko Amin-Wetzel, Lisa Neidhardt, Yahui Yan, Matthias P. Mayer, and David Ron. Unstructured regions in IRE1 specify BiP-mediated destabilisation of the luminal domain dimer and repression of the UPR. eLife, 8, December 2019.

(12) Robert B. Best, Gerhard Hummer, and William A. Eaton. Native contacts determine protein folding mechanisms in atomistic simulations. Proceedings of the National Academy of Sciences, 110(44):17874–17879, October 2013. Publisher: Proceedings of the National Academy of Sciences.

(13) Robert B. Best and Michele Vendruscolo. Structural Interpretation of Hydrogen Exchange Protection Factors in Proteins: Characterization of the Native State Fluctuations of CI2. Structure, 14(1):97–106, January 2006.

(14) Yawen Bai, John S. Milne, Leland Mayne, and S. Walter Englander. Primary structure effects on peptide group hydrogen exchange. Proteins: Structure, Function, and Bioinformatics, 17(1):75–86, 1993. _eprint: https://onlinelibrary.wiley.com/doi/pdf/10.1002/prot.340170110.

(15) David Nguyen, Leland Mayne, Michael C. Phillips, and S. Walter Englander. Reference Parameters for Protein Hydrogen Exchange Rates. Journal of the American Society for Mass Spectrometry, 29(9):1936–1939, September 2018. Publisher: American Society for Mass Spectrometry. Published by the American Chemical Society. All rights reserved.

(16) G Elif Karagöz, Diego Acosta-Alvear, Hieu T Nguyen, Crystal P Lee, Feixia Chu, and Peter Walter. An unfolded protein-induced conformational switch activates mammalian IRE1. eLife, 6:e30700, 2017.

(17) Josh Abramson, Jonas Adler, Jack Dunger, Richard Evans, Tim Green, Alexander Pritzel, Olaf Ronneberger, Lindsay Willmore, Andrew J. Ballard, Joshua Bambrick, Sebastian W. Bodenstein, David A. Evans, Chia-Chun Hung, Michael O’Neill, David Reiman, Kathryn Tunyasuvunakool, Zachary Wu, Akvile Žemgu-˙ lyte, Eirini Arvaniti, Charles Beattie, Ottavia Bertolli, Alex Bridgland, Alexey˙ Cherepanov, Miles Congreve, Alexander I. Cowen-Rivers, Andrew Cowie, Michael Figurnov, Fabian B. Fuchs, Hannah Gladman, Rishub Jain, Yousuf A. Khan, Caroline M. R. Low, Kuba Perlin, Anna Potapenko, Pascal Savy, Sukhdeep Singh, Adrian Stecula, Ashok Thillaisundaram, Catherine Tong, Sergei Yakneen, Ellen D. Zhong, Michal Zielinski, Augustin Žídek, Victor Bapst, Pushmeet Kohli, Max Jaderberg, Demis Hassabis, and John M. Jumper. Accurate structure prediction of biomolecular interactions with AlphaFold 3. Nature, pages 1–3, May 2024.

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

Learn more at Review Commons

Reply to the reviewers

We would like to thank the reviewers for their positive and constructive feedback.

We apologise for the delay in coming back. The first author has moved to the LMB, and the Trost lab has been relocating to the University of Manchester, which delayed our ability to respond quickly.

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

Reviewer Comments

The manuscript by Chatterjee et al. describes a novel ultra-sensitive isolation and deep proteomics workflow to investigate phagosome dynamics of bacterium-containing phagosomes. The method enables dual proteome coverage of both host and pathogen, and the authors report quantitative changes in the host and bacterial proteomes using Salmonella isogenic mutants defective in intracellular survival. They further leverage these datasets to assess the relevance of selected Salmonella genes in intracellular fitness.

Overall, the manuscript presents a powerful and technically impressive approach that will be of significant interest to the infection biology community. The study is well conceived and addresses an important gap in the field. However, several clarifications and additions would strengthen the work and improve interpretability of the results.

Specific Comments

Line 76: The authors should consider including the following relevant citations: PMID: 30079117 and PMID: 31009521.

We thank the reviewer for pointing this out. We have now included the suggested references

Line 104: Please define the abbreviation BFP clearly upon first use.

We thank the reviewer; we have defined the abbreviation upon first instance.

Figure 1A, Step 2: From the schematic, it is unclear whether the pellet or the supernatant is used for the subsequent step in which the CellVue dye is added. Please clarify.

We thank the reviewer for bringing this to our attention. We have now modified Figure 1A.

Figure 1B: It would be informative to report the percentage of S. Typhimurium that are double positive, especially in the BFP + Claret condition. A small bar plot for each condition would help visualize and compare the proportion of Claret-labelled bacteria.

We have now included a figure for the percentage of BFP + Claret for STM in S1H.

Figure 1C: The distinction between the upper and lower images is unclear. Do they represent different particles or different fields of view of the same sample? Please clarify.

They both are from different fields of view.

Line 122: The statement is not entirely accurate. Cells that lyse via pyroptosis will leave behind cellular remnants, including nuclei, that may still co-sediment with intact cells in such preparations.

We have modified the sentence accordingly.

Line 128: CellVue and Claret appear to be used interchangeably-are they the same reagent? Please clarify and use consistent terminology throughout.

We have rectified this inconsistency in our revised manuscript.

Line 136: Please explain the basis for the stated estimates. If this is common knowledge within the field, additional explanation would still be helpful for non-experts.

We have clarified this further in the manuscript. Obviously, these numbers are estimates but give the reader an idea with how little material we are working.

Lines 143 & 145: Please define "protein IDs" and indicate how many correspond to host proteins versus Salmonella proteins.

We have defined this in our revised manuscript. Also, to avoid any confusion, these proteomics methods were optimised using a commercially available HeLa protein digest, and hence no Salmonella proteins are detected here.

Figure 2D: Please specify the number and type of replicates used. Also indicate the plot type (e.g., violin plot) and the statistical test used to determine significance.

We have updated figure legend for 2D and 2E stating the number of biological replicates, i.e. n=4 and n=3.

Line 244: Please consider citing PMID: 32514074 and PMID: 23162002.

*We have included these references. *

Line 253: Have the authors considered how their observations regarding MHC relate to prior findings (PMID: 27832589)?

*Thank you for suggesting this paper and we enjoyed reading it. However, since the paper suggested by the reviewer focusses on cell surface MHC molecules and we are looking at the phagolysosomal compartment, we feel it may be difficult to make connections. *

Line 265: Clarify which "cell" is being referred to-the host cell or the bacterial cell.

We have modified the sentence to reduce confusion.

Line 278: Have the authors considered how their observations on glycolytic proteins relate to earlier work (PMID: 19380470 and PMID: 37594988)?

*Thank you for pointing out these papers. We have cited both of these and added another sentence that intracellular STM utilises host metabolites. *

Line 285: The claim that "PhoP-dependent effectors actively remodel..." requires clarification. If the authors are referring to all PhoP-regulated genes as "effectors," this terminology may cause confusion, as "effectors" in the Salmonella field typically denotes T3SS-secreted proteins. While some T3SS effectors are PhoP-regulated, PhoP controls many additional genes, and the observed phenotypes may reflect broader defects in intracellular survival rather than absence of secreted effectors specifically. Rewording is recommended.

Thank you for your suggestion, we have modified the same in text.

Line 313: Have the authors examined later time points (e.g., 8 hpi), when the SCV is more established and SPI-2 effector expression is higher?

We did not test the 8 hpi timepoint because our primary aim was to identify the induction of SPI-2 effectors at earlier stages. Testing later timepoints would be problematic, as PhoP mutants show poor survival at these times, which would confound comparisons between STM WT and PhoP mutants.

Line 317: Were secreted SPI-2 effectors detectable using PhagoCyt, and if so, how did they behave?

We detected some of the secreted effectors as well, and they are in accordance with the literature. As expected, most of them were detected only in WT at 4 hpi.

For example, PipB2, SseL and SctB1 are significantly decreased in the PhoP mutant compared to the STM WT at 4 hpi.

Line 319: Have the candidate Salmonella mutants been evaluated at later time points (6-8 hpi)? Stronger phenotypic differences may emerge when intracellular replication relies more heavily on SPI-2 function.

We acknowledge that there may be larger differences at later time points; However, we wanted to be comparable with the data within the manuscript, i.e. within the 4 hour time-point that we have kept throughput. Moreover, at later timepoint we see increase macrophage cell death and therefore refrain from doing timepoints much longer after the 4 hour mark.

Figure 5B: For all mutant strains, please also report in vitro growth to determine whether the phenotypes reflect general growth defects or are specific to the intracellular environment.

We have performed the growth curve for the PhoP mutant, which is in the supplemental figure 1.

Line 336: As above, please reconsider the use of the term "effectors." Unless evidence is provided that these are bona fide secreted SPI-2 effectors, an alternative term would avoid confusion.

We have modified the sentence to reduce confusion.

Supplementary Figure 5: The volcano plots appear pixelated. Please provide higher-resolution versions.

Thank you for pointing this out. We have rectified this.

Reviewer #1 (Significance (Required)):

General assessment:

This study introduces a highly sensitive dual host-pathogen proteomics workflow for profiling bacterium-containing phagosomes. Its key strengths are the technical innovation and the mechanistic insight gained using Salmonella mutants. The main areas needing improvement are clarification of methodological details and tighter interpretation of some biological claims.

Advance:

To my knowledge, this is the first study to achieve such deep, simultaneous proteomic coverage of both host and intracellular bacteria within purified phagosomes. This represents a notable technical advance and provides new mechanistic insight into intracellular adaptation and immune regulation.

Audience:

The work will interest a specialized audience in infection biology, host-pathogen interactions, and proteomics, with broader relevance for researchers studying organelle isolation or intracellular pathogens. The workflow and datasets will be useful as a resource for future studies.

Reviewer expertise:

Expertise in host-pathogen interactions, bacterial intracellular survival, macrophage biology, and functional proteomics. Limited expertise in MS instrumentation.

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

In this work, Chatterjee, Rubio and colleagues use a novel flow cytometry-based method to isolate phagosomes from Salmonella infected macrophages. This method is applied both to wild-type and to a mutant (deletion of phoP) that does not express virulence genes, prior to the proteome characterization of these phagosomes and the bacteria that they contain. The experiments were done at an early point of infection (30 min) and a later time point (4 h). The authors first identified mitochondrial proteins in their analysis, which had previously been considered contaminants from the preparation of phagosomes. However, some Salmonella effector proteins are known to affect mitochondria, and the authors demonstrate that inhibition of Complex I showed decreased Salmonella intracellular viability. Comparing WT and the phoP mutant also highlighted two Salmonella proteins that enhance intracellular survival. In addition, the authors show that their method recapitulates previously known proteins involved in Salmonella infection. The study is well designed and clearly written.

I have only some minor comments that I hope will strengthen the work:

It would be interesting to compare the results with a whole cell proteome analysis, and to other approaches that involve subcellular fractionation (both in the context of Salmonella infection) to: a) highlight proteins that are specifically changing in abundance in the phagosomes (but not necessarily in the cell), and b) to show that this approach is able to capture previously unknown phenomena. To avoid the performing additional experiments, the authors can compare their dataset to previous proteomic datasets of Salmonella infection. We have compared this with the ultracentrifugation methods STM WT 4h vs STM WT uptake (Figure 6A).

A color scale for the heatmap in Fig 2C is needed. I assume that this heatmap shows intensity and not fold-changes, and thus suggest that the authors use a single-color gradient for easier visualization.

*This has now been included. *

Best regards,

André Mateus

Reviewer #2 (Significance (Required)):

General assessment: This study provides a novel approach to study intracellular pathogenic bacteria. The method is applied to Salmonella, but can potentially be used for any bacteria, including non-genetically tractable organisms. A strength of the approach is that it captures the bacterial proteome, which is mostly undetectable when studying infected cells. Further, by enriching phagosomes, it allows measuring the spatial distribution of proteins to these organelles. The study could be improved by distinguishing proteome changes that are caused by trafficking of proteins to phagosomes vs general changes in protein abundance.

Advance: Apart from a new methodology, the authors use the approach to identify novel aspects of Salmonella infection biology, e.g., the importance of mitochondrial proteins in host defense or novel Salmonella proteins that are involved in intracellular survival. Audience: The audience for this study is mostly those in the field of infection biology, particularly Salmonella. The dataset generated can be used to identify novel aspects of Salmonella infection, and the described method could be applied to other pathogens.

My field of expertise: Proteomics, microbiology.

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

In the manuscript "Flow cytometry-based isolation of Salmonella-containing phagosomes combined with ultra-sensitive proteomics reveals novel insights into host-pathogen interactions", the authors describe a new method for analysis of composition pathogen-containing phagosomes and the pathogens within. Combination of FACS-based single phagosome analysis and sorting combined with optimised highly sensitive proteomic analysis of sorted vesicles has potential for identification of so far overlooked host-pathogen interactions. Although this is well described in the manuscript, some controls are missing.

Major comments:

1) The sorting of labelled bacteria is a crucial bottleneck in the whole procedure. The gating strategy presented in the Fig. 1B suggest that the initial "bacterial phagosome size" is limited from the bottom based on the noise signal but not from top. Therefore any not broken THP-1 cell remaining in the sample would be also included in the analysis. In respect to very high sensitivity of the mass spectrometry procedure and high abundance of housekeeping genes in host cells, this contamination could well explain the appearance of mitochondria, ribosome, and nuclear envelope proteins identified in Fig 2B and undermine the following results. Therefore, the gating strategy should be more stringent and data from this more stringent gating shall be compared with the current data sets. Since the authors use BFP+ Salmonella and do not analyse the claret+BFP- events, a BFP vs FSC gating step could help to distinguish free bacteria, bacteria in vesicles, and not or only partially broken host cells.

We use a series of centrifugations to ensure that we do not have intact cells in the prepared samples. We have also visualised the final samples under the microscope and did not observe any intact cells. Because of the side/forward scatter gating, intact cells are not within the field of sorting. In Figure 1B we show that free bacteria are not within the gating strategy that we used. Finally, we visually inspected >100 pictures of sorted phagosomes by imaging flow cytometry and did not see any intact cells or free bacteria.

2) Since the authors present data previously well accepted as contaminations from other fractions, these shall be carefully validated by other methods. For example the contact of mitochondria with SCV could be validated using a FRET- or split FP- based assays. Change of abundance of surface proteins on SCV in individual timepoints shall be validated using antibody-based flow cytometry on isolated SCVs. Most relevant antibodies are already described in the manuscript or available commercially (IL4R, IFNgR, integrins, TLRs). Microscopy-based quantification could help with the soluble proteins present within SCVs.

We agree with the reviewer that this would be very interesting. However, we feel that this is outside of the scope of this paper and will be very laborious and time consuming, practically a whole project in itself.

3) Since the authors describe an alternative method to methods used previously, they shall discuss the differences in results obtained by the formerly used methods.

We have now provided a dataset that is with SCVs isolated using ultracentrifugation as a comparatively analysis to our method (Figure S6A and Table S8). __The data show that the ultracentrifugation-isolated phagosomes have many more proteins from any organelle (__Figure S6B), suggesting that they are less pure than the phagosomes isolated by the PhagoCyt approach.

4) Only 15 Salmonella proteins downregulated between 0.5 and 4 h timepoints were identified. However, at least genes from SPI-1 and flagella would be expected to be downregulated at 4 h p.i. How do the authors explain this discrepancy? In contrast, are the SPI-2 genes among those identified as upregulated?

In our supplementary table 6 (comparison between WT 4h vs WT uptake), we see that there are 458 Salmonella proteins that are only present in uptake samples, these were not included in limma analysis since they are completely absent in the WT 4h. We decided to report these as “unique” proteins rather than perform imputation. In Figure 5B, we specifically highlight STM proteins down-regulated, which include flagellar proteins and SPI-1 proteins.

To answer your second question, yes, several SPI-2 genes (effectors and other regulatory proteins) are upregulated at 4 hpi. 131 Salmonella proteins are significantly upregulated, and 55 proteins are exclusively present in the WT 4hpi samples. Some selected examples are in Figure 5A.

Minor comments:

1) Fig 1, the figure caption seems to remain parts of an older version, mentioning blue bars not present in the current version?

The figure caption appears to be correct for us; the “blue” is in the unstained BFP Salmonella, which is hidden behind the purple, which is the BFP Salmonella + CellVue Claret.

2) Fig 1A point 1, how were the dead cells removed? Normal centrifugation is not able to discriminate dead and living cells well enough as percoll gradient centrifugation for example would be. Such gradient centrifugation is not mentioned in the Methods section though.

We have not used Percoll-based centrifugation to remove dead cells; instead, we have washed the adherent macrophages in dishes 3-4 times with ice-cold PBS to remove dead, floating cells, and then washed the pellet several times with PBS to ensure we are not taking any dead cells into the sample preparation.

3) Fig 1A point 2, did the authors check for the composition of the pellet fraction in each centrifugation step? What are the losses and cross contaminations of the other fraction?

No, we have not checked the composition of each fraction using mass spec; however, we did run some western blots to correctly identify the major organelle contribution in each fraction.

4) Suppl. Fig 1, caption for panels F and G are missing. The axis in the panel G is misleading - the bacteria obtained in "output" contain proliferating intracellular bacteria that originate only from a fraction of the "input" bacteria. Since the figure clearly show increase in the number of intracellular bacteria and all the extracellular bacteria should be killed by gentamicin, all bacteria in the "output" probably proliferate intracellularly and, therefore, originate from the same fraction of the "input" throughout the whole assay. Showing these results as CFU per well/plate/surface area or cell count would be more exact, in this case the "input" data shall be shown as a separate data point.

We thank the reviewer for this observation. We have now modified the figure legends. These are normalised per cell, and we think they provide accurate results.

5) Fig 1B, could the authors show the percentages in individual quadrants for the green "Sample with BFP Salmonella + claret"?

Yes, there is the plot that depicts the percentage in Supplementary Figure 1H, this varies between WT and PhoP mutant, and hence, we decided to not show this in one figure.

6) All proteins identified as significantly up or down represented shall be listed in a supplementary file.

They are listed in the supplemental tables.

7) Fig 2C suggests that some mitochondrial proteins are similarly present at the SCV containing WT Salmonella at 4h as ∆phoP mutant at 0.5 h p.i. Could the authors speculate how is that? The scale of blue/orange transition shall be shown in Fig 2C.

We speculate that Salmonella WT alters the maturation of the SCVs is heavily arrested by the pathogen and hence resemble the early SCV of a mutant that is unable to arrest the SCV degradation stages.

8) In the Fig 2D, the authors show decrease of CFU obtained from THP-1 cells treated with Rotenone. However, rotenone is known to induce host cell apoptosis. Were the presented data normalized to amount of living host cells in the sample? For example measurement of protein concentration in the sample lysate after washing away the dying host cells should enable this.

Yes, we have normalised the data to the account for the percentage of live cells using live dead staining. However, in the timepoints used, we did not observe significant cell death.

9) Microscopy-based observation of mitochondria relocation to SCVs in time shall strengthen the claim that mitochondria-derived ROS are involved in anti-Salmonella host defense.

There are multiple literature PMID: 38356294, PMID: 41444067, PMID: 15866946, PMID: 41198672 that support our data in this regard.

10) The Salmonella proteins identified in the Fig 5 shall be validated using qPCR.

We think that data from qPCR would not be accurate to validate Salmonella proteins, as it has been shown that Salmonella mRNAs can have sub-minute half-lives (PMID: 38527194). We used rather conservative proteomics analysis settings, that have shown in a recent pre-print of our lab to have 0% false discoveries and 0.4% false quantitative rate ( https://doi.org/10.1101/2025.09.22.677725). We acknowledge that another reviewer did not find this experiment to be essential.

Reviewer #3 (Significance (Required)):

The manuscript was reviewed mainly from the Salmonella and flow cytometry/FACS expertise point of view. The main interest in the study lies within its methodological advances - combination of single vesicle analysis using flow cytometry/FACS with highly sensitive mass spectrometry analysis. In comparison to other similar studies in the field, this combination significantly expands the possibilities of sorting of distinct subpopulations of vesicles from the same cells. This will make the article of interest to scientists in the broad field of host-pathogen interactions and immunology.

**Referee cross-commenting**

Reviewer 3 - @Reviewer #1: I see your point and leave it at the editors to judge how important this comment is. My reasoning was this: Fig 5

serves as a proof of concept that PhagoCyt has the power to make new discoveries in Salmonella biology. While behavior of some of the proteins

shown if Fig 5 is well described (e.g. flagella or SPI-1 T3SS components and effectors), some are novel and to prove the functionality of the

method, these results should be confirmed by some other well accepted mean. Given the great sensitivity of PhagoCyt, other proteomic

approaches are unlikely to help in this case (e.g. flagella or SPI-1 T3SS components and effectors are not detectable by western blot at 4 h p.i.).

Therefore, I suggest qPCR (but would accept any other method as well) as a very sensitive and well accepted approach, but leave at the authors

to chose what proteins they want to use for the validation.

Reviewer 1- I agree with comments raised by the other two reviewers, except the following point from Reviewer 3 '10) The Salmonella proteins

identified in the Fig 5 shall be validated using qPCR.' It is not clear which proteins are being referred to and it is unclear to this reviewer how this

experiment(s) would improve the manuscript in its current form.

Reviewer 3- I agree with all comments raised.

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

Learn more at Review Commons

Reply to the reviewers

We thank all three reviewers for their careful and constructive engagement with our manuscript. We are encouraged by their overall positive assessment of the work. Reviewer 1 described this as "an important study" that addresses a significant gap in understanding systemic, inter-organ responses to hypoxia, and noted the potential relevance of our findings to mammalian IL-6 biology. Reviewer 2 highlighted the study as being of "high significance" and described it as "a foundation study that will be the motivation for numerous high-impact papers in the future", noting its broad relevance to understanding hypoxia in both health and disease. In the revised manuscript, we have addressed all of the reviewers' comments and critiques. This includes performing several new experiments, expanding our Discussion, and making a number of clarifications to the text, figures, and methods as detailed below.

Reviewer #1

__(Evidence, reproducibility and clarity (Required)): __The authors describe a role of Unpaired 3 (Upd3) in tissue communication in responses to hypoxia in Drosophila adult flies. Upd3 mRNA is strongly upregulated in hypoxia, along with well-characterized JAK/STAT downstream target genes, in both adult fly males and females, as well as in larvae. Interestingly, adult females but not males require Upd3 for 15 to 24 h survival in hypoxia, as Upd3 mutant females but not males die to a much larger proportion in these conditions. Adult females they display strong hypoxic upregulation of Upd3 in the gut, assessed by RT-PCR or through a Gal4 transcriptional reporter, mainly in epithelial enterocytes. Enterocyte-specific RNAi-mediated KD indicated that this enterocyte expression of Upd3 represents about 40% of Upd3 expression in the whole body. Enterocyte-specific KD of Upd3 in adult females significantly reduced survival in hypoxia, suggesting that this expression is critical for hypoxic adaptation. Tissue-specific analysis of the expression of the STAT target genes, SOCS36E, TotA and TotM revealed that stimulation of the JAK/STAT pathway in hypoxia is widespread, although more pronounced in abdominal tissues. Indeed, overexpression of Upd3 in enterocytes provokes upregulation o both target genes TotA and TotM. Consistent with this RNAi-dependent inhibition of the JAK/STAT pathway in the fat body and oenocytes significantly reduced survival of female flies in hypoxia. Nitric oxide synthase (NOS) is strongly upregulated in adult female abdomens upon hypoxic exposure, and KD of NOS in fat body and oenocytes reduced hypoxic survival. Surprisingly, the found that ubiquitous KD of HIFa/Sima led to mitigation of Upd3 hypoxic induction and, more clearly, to JAK/STAT target gene induction. HIF KD flies displayed increased lethality in hypoxia, and this lethality was slightly mitigated in Upd3 heterozygous flies. The authors conclude that increased lethality of HIF-minus flies in hypoxia stems at least in part from excessive levels of Upd3. The authors then find that HIF/Sima-dependent inhibition of Upd3 expression is non-cell autonomous, since KD of Sima specifically in the gut does not affect expression of Upd3 in this organ. Instead, Sima KD at the fat body led to significant increase of Upd expression in the gut, suggesting that a Sima-born signal communicates these two organs, leading to restriction of Upd3 intestinal expression. ROS does not seem to be the signal that communicates the fat body with the gut, as expression of catalase in the fat body did not affect expression of Upd3 in the gut.

(Significance (Required)): This is an important study, because most previous studies have focused on cell-autonomous responses to hypoxia, but much less is known about systemic responses to low oxygen conditions, particularly in relation to inter-organ communication during this responses. This work defines the cytokine unpaired 3, homolog of human interleukin 6, as a major regulator of systemic responses to hypoxia. Future studies will determine if interleukin 6 plays similar roles in mammals. This work might be of interest for a broad audience interested in responses to hypoxia, as well as general physiology.

We thank Reviewer 1 for their careful reading and comments on the manuscript. We are pleased that they found this to be "an important study" that addresses a gap in understanding systemic, inter-organ responses to hypoxia. We have addressed each of their concerns in the revised manuscript as outlined below.

__MAJOR CONCERNS __ 1) Figure 1 lacks statistical analysis. It is important to determine if the apparent differences in gene expression are statistically significant.

We have now added the statistical analyses to the revised version of the figures.

2) Is NOS expression in fat body/oenocytes JAK/STAT-dependent? Block the pathway in hypoxia specifically in this cells and check.

To address this, we blocked JAK/STAT signaling specifically in fat body/oenocytes under hypoxia and examined the expression of Nos, as well as bnl and Hipk - two additional genes we find are regulated by gut-derived Upd3 and required for hypoxia tolerance.

Interestingly, fat body/oenocyte-specific knockdown of STAT92E suppressed hypoxia-induced Hipk expression but did not affect Nos or bnl expression in these tissues. These results suggest that gut-derived Upd3 can control fat body/oenocyte expression of hypoxia regulators through both direct and indirect (relay) mechanism There is precedent for indirect, relay in the context of other Upd3/Upd2-mediated inter-organ responses. For example, in response to CO2, neuronal Upd3 controls blood cell differentiation in the lymph gland; however, this effect is not direct - Upd3 first signals to the fat body to induce Dilp6 expression, and Dilp6 then signals to the lymph gland to regulate hematopoiesis. A second example involves gut-derived Upd2: upon infection, Upd2 controls olfactory behavior, but does so via a relay in which Upd2 signals to glial cells, which in turn alter apolipoproteins expression, and these then modify olfactory neuron function.

We have incorporated the new tissue-specific data into the manuscript and expanded the Discussion to address both direct and indirect modes of Upd3 action. (Fig 5 and lines 427-441)

3) The authors relate the HIF-dependent limitation of Upd3 induction in hypoxia to regulation of cytokine-dependent immune responses in mammals; specifically they propose a parallel with a cytokine storm. This relationship is unclear to this reviewer, as in the Drosophila response Upd3 fulfils a signalling function (rather than immunological). I suggest they consider modifying this assumption.

We appreciate this comment. Our intent in drawing a comparison to mammalian cytokine storm response was to illustrate the concept of fine-tuning cytokine responses, where too little or too much signaling can be deleterious, as we observe when comparing upd3 mutants to upd3-overexpressing animals. We have revised the Discussion to retain this concept while tempering the suggestion that our findings directly mirror cytokine storm pathologies in human (lines 511-536).

4) Mitigation of lethality of HIF KD flies in Upd3 heterozygotes is very modest. Thus, the conclusion that one of the mechanisms by which HIF mediates adaptation to hypoxia is through inhibition of Upd3 expression is not sufficiently supported by the data. It seems like an over-interpretation of the results.

We agree that the rescue is modest, and we would argue this may be expected given HIF-1's role as a master regulator that coordinates many gene expression changes required for hypoxia tolerance. Loss of HIF-1 therefore likely disrupts multiple essential processes simultaneously - including metabolic reprogramming and tracheal remodeling - that may not be restored by reducing upd3 dosage. We take the reviewer's point that this should not be framed as a primary mechanism. The partial reversal of lethality in upd3 heterozygotes nonetheless implicates excessive Upd3 signaling as one small component of what HIF-1 does to promote hypoxia adaptation, and we have revised the manuscript language to reflect this more measured interpretation (lines 529-536).

5) HIF expression is well-known to reduce ROS levels in hypoxia by controlling mitochondrial activity through a wide array of mechanisms. Thus, this reviewer feels that the experiments utilized to rule out a role of ROS in fat body-to-gut communication are insufficient. Catalase reduces hydrogen peroxide levels, but not necessarily other reactive oxygen species. The authors might try to express other ROS scavengers such as superoxide dismutase. In addition, expression of scavengers should be carried out both at the fat body and gut.

We thank the reviewer for this important point. We have now addressed it by overexpressing CatA, SOD1, or SOD2 individually in either fat body or enterocytes and measuring hypoxia-induced upd3 expression in each case. In all six conditions, hypoxia-induced upd3 expression was unaffected (Figs. S6B–G). Together, these experiments scavenge both hydrogen peroxide and superoxide in both tissues and collectively argue against a role for ROS in mediating upd3 induction

__MINOR CONCERNS __ 6) The authors state that hypoxic upregulation of Upd3 in the gut occurs mostly in "large epithelial enterocytes". In Figure 3B, it is evident that GFP does not express in all cells; please utilize cell-type specific markers to identify which cells do express the cytokine.

We appreciate this suggestion. Despite multiple requests to different laboratories, we were unable to obtain antibodies suitable for marking enterocyte subtypes in this context. To address the question of cell identity genetically, we used drivers specific for enterocytes (mex-GAL4) or progenitor cells (stem cells and enteroblasts; esg-GAL4) to drive RNAi-mediated knockdown of upd3 and then measured the effect on hypoxia-induced upd3 expression in whole guts. These experiments indicate that hypoxia-induced upd3 expression occurs mostly in enterocytes, with a smaller contribution from progenitor cells. This mirrors previous findings showing that infection-induced upd3 induction occurs in both enterocytes and enteroblasts, and supports our conclusion that enterocytes are the predominant source of hypoxia-induced Upd3. We have incorporated these results into the revised manuscript (Fig 3C and Fig S2C).

7) The title of Fig 4 caption reads "Gut-derived upd3 controls adipose expression of hypoxia regulators." Only one hypoxia regulator has been analysed: Nitric Oxide Synthase. Please change the title to "Gut-derived upd3 controls adipose expression of Nitric Oxide Synthase."

In the revised manuscript we now show that gut-derived Upd3 controls the expression of Nos, bnl, and Hipk in fat body and oenocytes, and that all three genes are required for hypoxia tolerance. We have therefore revised the figure title, to better reflect the findings presented in this version.

8) Supplementary Figures 1 A and B lack statistical analysis.

We have now included the statistical analyses in the revised manuscript figures.

Reviewer 2

---

__(Evidence, reproducibility and clarity (Required)): __This study by Ding and colleagues identifies a novel role for the cytokine Unpaired-3 (upd3) and the JAK/STAT signaling pathway coordinate a whole-body response to systemic hypoxia in Drosophila. The authors describe how low-oxygen conditions rapidly induce upd3 expression in both larvae and adults. Interestingly, this pathway's importance is sex-specific, as female flies require upd3 for survival in hypoxia, while males do not.

Intriguingly, the authors identify the intestine as a crucial source of the hypoxia-induced upd3. This gut-derived upd3 then signals to the fat body and oenocytes, promoting the expression of nitric oxide synthase, which is essential for hypoxia tolerance. Furthermore, the study reveals an unexpected role for the transcription factor HIF-1α/sima as a molecular brake. Instead of simply promoting the hypoxia response, sima prevents the overproduction of upd3, demonstrating that a precise dosage of this cytokine is necessary for survival. The findings define a novel gut-to-fat/oenocyte signaling axis that coordinates systemic hypoxia adaptation and highlights the fly as an ideal system for studying interorgan communication during bouts of hypoxia. Overall, I find this manuscript an important step forward in understanding the link between hypoxia signaling and inflammation.

__ (Significance (Required)): __This study is of high significance, as it not only demonstrates that a clear role for cytokine signaling in the Drosophila hypoxia response, but also demonstrates this response requires interorgan communication between adipose tissue and the intestine. Moreover, the study reveals a clear role for Hif1alpha in modulating upd3 expression, suggesting that this highly conserved transcription factor play a key role in fine tuning the inflammatory response.

I think these findings are of broad interest and are potentially relevant to two aspects of public health. First, I believe the findings should be of particular interest to anyone studying hypoxic injuries, such as stroke and ischemia-reperfusion. Secondly, the observations could be relevant to a previous study that revealed an important role for hypoxia signaling in the mosquito larval intestine. Thus, this study could be important for revealing new mechanisms for inhibiting mosquito development, which would be of broad public health interest.

Finally, I would highlight how this study raises a number of important question. Why are there sex-specific differences for upd3 in the hypoxia response? What is the signal from the fat body to the intestine? How does sima modulate upd3 signaling. Thus, I think this manuscript represents a foundation study that will be the motivation for numerous high-impact papers in the future.__ ____ __ We thank Reviewer 1 for their careful reading and comments on the manuscript. We are pleased that they found this to be "a study of high significance” that will be importance for our understanding of hypoxia and health. We have addressed each of their concerns in the revised manuscript as outlined below.

__Major Concerns and Suggestions: __ I have no real for the manuscript as written - the experiments are well designed and control, the results, as presented, support the major conclusions. While there are clearly open questions, including what it the basis of the sex-specific effects, how does sima modulate upd3 expression, and what is the signal communicating fat body sima activity with intestinal upd3 expression, these open questions do NOT diminish the importance of the study.

My only major concern is that the current draft lacks a discussion of previous studies in the mosquito Aedes aegypti, where hypoxia signaling plays a key role in larval development (https://doi.org/10.1073/pnas.1719063115). This body of literature should be incorporated into the discussion, as it hints at a conserved molecular mechanism.

We thank the reviewer for pointing us to this important study. Valzania et al. demonstrate that gut hypoxia acts as a systemic signal in Aedes aegypti larvae, activating HIF to coordinate fat body metabolism and whole-body growth. We agree this is relevant context for our findings, as both studies support the idea that the gut can function as a hypoxia sensor that controls whole-body physiology through effects on the fat body. We have incorporated this into our Discussion (lines 488-492).

Minor comments:

Please include a list of fly stocks used in the methods with complete genotypes. Whenever possible, include the RRID number for the stock - these can be found on the BDSC page for the stock.

We have now added the list of fly stocks as well as a supplemental table with full genotypes.

Line 477-479 - provide citations that sima regulates glycolysis in the fly.

We have now added these citations

Lines 501-505 - please state if gasses were premixed or mixed in lab. Also, were flies contained in standard food vials during the exposure?

We have now provided more detail on these points – the gases were premixed and flies were on standard food vials during the exposure.

Lines 507-513 - how long after the hypoxia exposure were the flies assayed?

We have now provided more detail on this point in the methods (lines 592-596) – the flies were assessed 24hrs after hypoxia exposure.

In figures that display qRT-PCR data, please note that data were normalized to reference genes listed in Table S2.

We have now added this methodological point.

Please reference Flybase in either the acknowledgements or methods and include citations to the latest Flybase papers published in Genetics.

We have now acknowledged Flybase and referenced the relevant papers

Genetics nomenclature is inconsistent throughout the study, a few examples included: Figure legend 1 - italicize gene names Figure 2 legend - italicize upd3-null Line 259 - Capitalize gal4 Figure 4 legend - NOS is written in all capital, but in line 270, written as Nos. Please be consistent. Line 297 - gal4 is lower case, in contrast with elsewhere.

We have now made these corrections

Additional suggestions:

While not required for publication, it would be interesting to examine intestinal upd3 expression when sima is inappropriately stabilized in the fat body of animals under normoxic conditions. This could be achieved by driving a fatiga-RNAi construct within the fat body.

We did carry out this experiment but didn’t see any effect of fat body fatiga RNAi on gut upd3 levels.

Reviewer 3

---

Evidence, reproducibility and clarity (Required)): __Summary: While local cellular and organ adaptations to hypoxia are well-documented, organism-wide responses to systemic hypoxia are still not well understood. In this paper, the writers were interested in investigating how organisms adapt to systemic hypoxia. From their investigations, they were able to show that gut-derived upd3 is crucial to animals' tolerance to hypoxia. They also show that the master hypoxia regulator Sima is required to keep the upd3 level in check to avoid the deleterious effect of excess upd3. They also showed that the fatbody Sima is important in the regulation of gut-upd3 level, showing an inter-organ communication network in the adaptation to systemic hypoxia. One of their findings shows sex dimorphism in hypoxia tolerance; however, they did not show the mechanism behind this. I think the major weakness is not knowing how the animal actually fail to survive. What causes reduced survival should be explored. Generally, the studies show how animals adapt to systemic hypoxia, this knowledge is important in systemic hypoxia pathology.

__

__Significance (Required)): __This paper explores how the organism copes with hypoxia, and explored how Upd from the gut plays a role in mediating this response in the fat body and the oenocytes

We thank Reviewer 1 for their careful reading and comments on the manuscript. We have addressed each of their concerns in the revised manuscript as outlined below.

__Major comment: __

Figure 1: The authors clearly showed that Upd3 level was up in the hypoxia condition and is important for animal tolerance to hypoxia. Apart from Upd3, are there other members of the unpaired family increasing and involved in hypoxia tolerance?

We thank the reviewer for this question. We examined expression of all three unpaired family members and found that both upd2 and upd3 are induced by hypoxia, while upd1 is not. We also have preliminary evidence that upd2 mutants show reduced hypoxia survival, and that this effect is not additive with loss of upd3. While these early results are intriguing, this paper is focused on defining the role of upd3 in hypoxia tolerance, and exploring upd2, both alone and in combination with upd3, across different aspects of hypoxia biology we see as the basis of future investigations.

Notably, co-induction of upd2 and upd3 by the same stress is a recurring theme in Drosophila biology, yet their respective contributions to organismal physiology are complex - sometimes overlapping, sometimes distinct - and in many studies only one family member has been characterized in detail. Indeed, our current understanding of how upd2 and upd3 each contribute to responses to infection, high-fat diet, and other stresses has emerged from the collective findings of multiple independent studies rather than from any single paper addressing both cytokines simultaneously. For example, during infection both Upd2 and Upd3 are induced in the gut to promote stem cell-mediated repair, yet only Upd2 has been shown to additionally signal to the brain to control olfactory behavior. Similarly, on a high-fat diet both cytokines are upregulated, but with distinct effects on different aspects of organismal biology: enterocyte-derived Upd3 promotes intestinal stem cell divisions, hemocyte-derived Upd3 controls fat body lipid levels, and fat body-derived Upd2 alters nephrocyte function. We see the current study as a foundation for broader investigations into unpaired cytokine biology in hypoxia. Indeed, Reviewer 2 noted that this manuscript "represents a foundation study that will be the motivation for numerous high-impact papers in the future", and we anticipate that the effects of Upd2 and Upd3 in hypoxia will prove similarly pleiotropic and resolving their respective contributions to different aspects of organismal biology in low oxygen will require dedicated future investigation.

Figure 2: From the method, female and male flies were subjected to different durations of hypoxia, 24-28 hours for females and 16-18 hours for males. What happens when subjecting different sexes to similar periods of hypoxia?

We thank the reviewer for this question. Males and females show inherently different sensitivities to hypoxia, as they do for other environmental stresses such as starvation. To reliably detect genetic effects on hypoxia tolerance, it is important to use exposure conditions that produce partial lethality in controls (50-80% survival), ensuring experiments are conducted within the appropriate range of hypoxic sensitivity for each sex. Because males and females differ in their sensitivity, no single timepoint satisfies this criterion for both sexes. When males are exposed for the same duration used in female experiments (24-28h), all animals - controls and experimental genotypes alike - die, precluding any meaningful comparison. Conversely, exposing females to the shorter timepoint used for males (16-18h) produces no detectable lethality, making it equally uninformative. The sex-specific exposure durations we use are therefore an experimental design choice that allows us to assess hypoxia tolerance appropriately in each sex.

Upon concluding that gut derived upd affects fat and oenocytes, it is a bit strange that the qPCR is done in the abdomen, which is presumably where the gut is. Should the gut be excluded in these assays?

We thank the reviewer for raising this point. For abdominal qRT-PCR experiments examining fat body and oenocyte gene expression, we dissected and removed the gut and ovaries prior to RNA extraction, leaving an abdominal sample enriched in fat body and oenocytes. We have clarified this in the Methods and Results section of the revised manuscript (Lines 245-246 and 626-627).

It is important to establish how the animals die under hypoxia.

We thank the reviewer for raising this important question. Our results show that gut-derived Upd3 is required for hypoxia tolerance in part through its control of Nos, bnl, and Hipk expression in fat body and oenocytes, and that knockdown of each of these genes individually reduces hypoxia survival. However, precisely why animals die when upd3 or these downstream effectors are lost remains an open question, and we discuss much of what we outline below in the revised manuscript Discussion (lines 443-466).

All three effectors are signaling molecules, and we speculate that they likely coordinate further downstream processes required for hypoxia tolerance, either within fat body and oenocytes or by acting on other tissues. In particular, both bnl, an FGF ligand, and nitric oxide, produced downstream of Nos, have established roles in tracheal development and remodeling, raising the possibility that Upd3-dependent regulation of tracheal responses to hypoxia contributes to survival. Nitric oxide can also regulate nitrosylation and has been shown to affect the unfolded protein response, a conserved pathway induced by hypoxia. bnl, in addition to its role in tracheal remodeling, has been shown to regulate metabolic changes in target tissues. Hipk is a kinase with likely many downstream targets and has been shown in flies to control metabolism and mitochondrial function. Together, these observations suggest that Upd3 engages a broad downstream signaling network, the full scope of which remains to be defined.

We think this situation is analogous to other environmental stresses such as starvation, where survival requires the coordinated regulation of a spectrum of physiological processes across multiple tissues, and where even well-characterized regulators are known to engage many downstream targets and pathways. We see the current paper as establishing the gut-to-fat body Upd3 requirement for hypoxia tolerance, and we suggest this lays a foundation for future exploration of the full spectrum of Upd3 targets and investigation of how they coordinate adaptive responses to low oxygen.

Figure 3-6: Controls for RNAi experiments - is there any reason for not using RNAi-specific control, such as mcherry-RNAi, lacZ-RNAi, etc, rather than a wildtype control in all the RNAi-mediated knockdowns? Please address this. Don't necessarily have to repeat all the experiments using RNAi-specific control, but repeating just a few to show that both wild-type and UAS-RNAi-specific controls show similar results would be important.

We thank the reviewer for raising this point. To address potential non-specific effects of RNAi expression on hypoxia tolerance, we expressed control GFP RNAi or mCherry RNAi transgenes using the main Gal4 drivers employed in this study: mex-Gal4 (gut) and desat;r4-Gal4 (fat body and oenocytes), and found no effect on hypoxia survival compared to wild-type controls (Fig S2E and S4B). These results indicate that RNAi expression per se does not adversely affect hypoxia tolerance, and that the survival effects we observe reflect specific knockdown of the genes of interest.

Although gut-derived upd3 contributes largely (40%) to hypoxia tolerance, what other tissues' upd3 is important for hypoxia tolerance?

We thank the reviewer for this important question. We find that upd3 is induced in multiple tissues during hypoxia, including the head, thorax, and abdomen. However, when we knocked down upd3 using drivers targeting the major cell types in these tissues, including muscle, neurons, and fat body/oenocytes, we observed no significant effect on hypoxia survival, in contrast to the robust effect seen with gut-specific knockdown. These new data, included in the revised manuscript, suggest that gut-derived Upd3 is a primary contributor to hypoxia tolerance (Fig S3).

That said, we do not conclude that the gut is the only relevant source. Other tissues we have not yet examined, including hemocytes, glia, and tracheal cells, may also contribute, and it is possible that Upd3 produced from multiple tissues acts redundantly, such that knockdown in any single tissue other than the gut is insufficient to cause a survival defect. By analogy with other stress contexts such as nutrient deprivation and infection, where upd cytokines are produced from multiple tissues and exert distinct effects on different aspects of physiology, we anticipate that Upd3 from tissues other than the gut may well contribute to hypoxia tolerance. However, fully defining these contributions will require detailed tissue-specific experiments that are beyond the scope of the current paper and will be the focus of future investigations. We have expanded on this point in the Discussion of the revised manuscript (lines 420-425).

Can you use a hypoxia readout to experimentally show that the gut is the main sensor of hypoxia compared to other tissues? Looking at the data, the fatbody could also be major sensors of hypoxia. Therefore, investigating hypoxia readout in these and other tissues would further strengthen the direction of communication.

We thank the reviewer for this suggestion, however, we wish to clarify that we are not claiming the gut is the main or primary sensor of hypoxia. All tissues are likely capable of sensing low oxygen and mounting cell-autonomous responses, and in some cases perhaps also non-autonomous signals to other tissues. Our findings specifically show that one consequence of gut hypoxia sensing is upregulation of Upd3, which then acts as an inter-organ signal to coordinate responses in target tissues such as the fat body and oenocytes. The fat body itself also senses hypoxia and mounts its own responses, as we and others have shown, including HIF-dependent regulation of gut Upd3 expression described in this paper. An analogous situation exists during nutrient starvation, where all cells autonomously sense and respond to nutrient deprivation, but on top of these cell-autonomous responses, specific tissues also mediate inter-organ signaling to coordinate whole-body physiological adaptations. We propose that hypoxia responses are organized similarly, and that the gut-to-fat body Upd3 signaling axis we describe here represents one such inter-organ communication pathway. We have clarified this point in the revised manuscript (lines 468-492).

__Minor comment:

__

Should check the alignment of the confocal image in Figure 3b, especially the top panel.

We have now fixed the images to better align them

Figure 6: "gut-specific sima knockdown (mex>sima-RNAi) did not significantly alter intestinal upd3 mRNA levels compared to controls (mex>+) under hypoxic conditions (Figure 6C)." This statement refers to Figure 6B, not Figure 6C

We have now corrected this

Since the fat body Sima non-autonomously control the gut upd3 level, can you also show this functionally important by investigating the animal's survival or other functional studies?

We thank the reviewer for this suggestion. Ideally, we would manipulate sima and upd3 independently and in parallel, knocking down sima specifically in the fat body while simultaneously reducing upd3 in the gut, to directly test the functional importance of this inter-organ axis for survival. In principle this could be achieved using orthogonal binary expression systems such as the GAL4/UAS and QF/QUAS systems in combination, but this would require the development of new genetic tools. An additional challenge is that based on our results, such experiments would require fine-tuned reduction of gut upd3, sufficient to suppress the elevated levels caused by fat body sima knockdown, but not so low as to itself compromise survival, as we have shown that loss of upd3 is detrimental. For these reasons, while we agree these would be, in principle, interesting experiments, they would technically be challenging to carry out.

Strangely, all the statistically significant data/results from both supplementary and main figures had a one-star significance even in graphs with very obvious differences and less sample variation.

We thank the reviewer for this observation. In all figures, a single asterisk is used to denote statistical significance at p < 0.05, regardless of whether the actual p value is substantially lower. This is a presentation convention we adopted consistently across all figures rather than a reflection of the strength of the underlying differences.

Author response:

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

Joint Public Reviews:

In this manuscript, the authors proposed an approach to systematically characterise how heterogeneity in a protein signalling network affects its emergent dynamics, with particular emphasis on drug-response signalling dynamics in cancer treatments. They named this approach Meta Dynamic Network (MDN) modelling, as it aims to consider the potential dynamic responses globally, varying both initial conditions (i.e., expression levels) and biophysical parameters (i.e., protein interaction parameters). By characterising the "meta" response of the network, the authors propose that the method can provide insights not only into the possible dynamic behaviours of the system of interest but also into the likelihood and frequency of observing these dynamic behaviours in the natural system.

The authors studied the Early Cell Cycle (ECC) network as a proof of concept, specifically focusing on PI3K, EGFR, and CDK4/6, with particular interest in identifying the mechanisms that cancer could potentially exploit to display drug resistance. The biochemical reaction model consists of 50 equations (state variables) with 94 kinetic parameters, described using SBML and computed in Matlab. Based on the simulations, the authors concluded the following main points: a large number of network states can facilitate resistance, the individual biophysical parameters alone are insufficient to predict resistance, and adaptive resistance is an emergent property of the network. Finally, the authors attempt to validate the model's prediction that differential core sub-networks can drive drug resistance by comparing their observations with the knock-out information available in the literature. The authors identified subnetworks potentially responsible for drug resistance through the inhibition of individual pathways. Importantly, some concerns regarding the methodology are discussed below, putting in doubt the validity of the main claims of this work.

While the authors proposed a potentially useful computational approach to better understand the effect of heterogeneity in a system's dynamic response to a drug treatment (i.e., a perturbation), there are important weaknesses in the manuscript in its current form:

(1) It is unclear how the random parameter sets (i.e., model instances) and initial conditions are generated, and how this choice biases or limits the general conclusions for the case studied. Particularly, it is not evident how the kinetic rates are related to any biological data, nor if the parameter distributions used in this study have any biological relevance.<br /> (2) Related to this problem, it is not clear whether the considered 100,000 random parameter samples sufficiently explore parameter space due to the combinatorial explosion that arises from having 94 free parameters, nor 100,000 random initial conditions for a system with 50 species (variables).<br /> (3) Moreover, the authors filter out all the cases with stiff behaviour. This filtering step appears to select model parameters based on computational convenience, rather than biological plausibility.<br /> (4) Also, it is not clear how exactly the drug effect is incorporated into the model (e.g., molecular inhibition?), nor how it is evaluated in the dynamic simulations (e.g., at the beginning of the simulation?). Moreover, in a complex network, the results may differ depending on whether the inhibition is applied from the start or after the network has reached a stable state.<br /> (5) On the same line, the conclusions need to be discussed in the context of stability, particularly when evaluating the role of initial conditions. As stable steady states are determined by the model parameters, once again, the details of how the perturbation effect is evaluated on the simulation dynamics are critical to interpret the results.<br /> (6) The presented validation of the model results (Fig. 7) is only qualitative, and the interpretation is not carefully discussed in the manuscript, particularly considering the comparison between fold-change responses without specifying the baseline states.

We thank the reviewers for their thoughtful and constructive comments. In response to their comments, we have undertaken a substantial revision to address all the comments, improve clarity, transparency, and robustness while preserving the paper’s core contribution: a principled, scalable framework (MDN) for mapping how molecular heterogeneity and network architecture shape adaptive drug-response dynamics. At a high level, we clarified the study design and analysis goals, tightened definitions, and added methodological detail where it most advances interpretability. Importantly, these updates leave the analytical pipelines and major conclusions unchanged.

Conceptually, we now make explicit that our objective is coverage of the output space of qualitative dynamics supported by the network topology, not exhaustive enumeration of parameter space. To support this, we added a convergence analysis and clarified that “triplicates” refers to independent ensembles used to demonstrate reproducibility. We also refined how we describe and implement initial conditions (as conserved total abundances that encode expression heterogeneity) and reframed filtering as minimal numerical/feasibility checks, using rejection sampling to obtain the prespecified ensemble size. Solver choices and input modelling (constant step mitogen/drug) are now spelled out succinctly.

We expanded the model specification and rationale (complete reaction list with rate laws and brief biological justifications in the Supplement) and unified terminology throughout. Figures and legends have been overhauled for readability and accuracy, with missing labels added and ordering corrected. For validation, we clarified the nature of the single-cell reporter readout, improved Figure 7’s presentation, and emphasised - consistent with our aims - that comparisons are qualitative.

Finally, we have rewritten the Discussion to centre on interpretation, implications, and connect our findings to the literature. It now: (i) frames MDN as a systems-level framework that links molecular heterogeneity to qualitative signalling “meta-dynamics” and adaptive escape under constant drug pressure; (ii) highlights two key findings: an asymmetry in control (interaction kinetics exert stronger, more consistent influence than protein abundance) and a topology-driven convergence whereby a vast parameter space funnels into a finite set of recurrent behaviours; (iii) shows that resistance is a network-level property, with many possible routes but a small set of recurrent hubs/modules dominating; and (iv) provides a qualitative alignment with single-cell reporter data while clarifying the intent and limits of that comparison. Moreover, we now explicitly discuss limitations (rate-law simplifications, broad priors, determinism, and modular abstractions) and outline next steps for future research, including data-constrained priors and stochastic extensions.

We believe these revisions materially strengthen the manuscript and fully address all the reviewers’ comments. A detailed, point-by-point response follows.

Joint Recommendations for the Authors:

(1) It is confusing exactly what are the different sets evaluated in each cases, e.g. "generated 100,000 model instances, each with the same set of ICs but a unique set of randomly generated parameter values" (lines 299-300), "generated 100,000 model instances (in triplicate), each with the same set of 'nominal' parameter values (see supplementary Table S1), and a unique set of ICs, and repeated the analysis as performed previously" (lines 366-368), "combined the 1000 IC sets with each parameter set to create 1000 model instances" (lines 382-383), "repeated for 1000 parameter sets, allowing us to observe how frequently IC variation induced adaptive resistance independent of the chosen parameter set" (lines 386-387). A small table or just a clearer explanation is needed.

In response to these comments, we have revised the main text to clarify the process of model instance generation. Specifically, we have made changes at page 7: line 297 - page 8: line 302, page 8: lines 305 - 310, page 9: lines 372-378, and page 9: line 384 – page 10: line 399 in the revised main text.

We have also added a new Figure (Figure S1) to the supplementary file to allow readers to visualise the model generation process for each relevant set of experiments. Supplementary figures are referenced in the main text where appropriate.

(2) The authors mentioned performing each simulation in triplicate, which is puzzling as the model is based on deterministic ODEs with fixed parameters for each simulation. Under such conditions, one would anticipate identical results from multiple simulations with the same initial conditions and fixed parameters. Perhaps the authors expect the model to exhibit chaos or aim to assess the precision of the parameter estimates through triplicate simulations. Further clarification from the authors would be valuable to comprehend the rationale behind conducting triplicate simulations in a deterministic setting.

We agree that repeating deterministic ODE simulations with identical inputs would be redundant. In our study, “triplicate” referred instead to generating three independent ensembles of 100,000 unique model instances each, where model parameters (or initial conditions) were randomly resampled. These ensembles were analysed separately to assess whether the inferred meta-dynamic distributions converged robustly. Indeed, the distributions from the three replicates were nearly indistinguishable, confirming that the results are reproducible and not artefacts of a particular random draw.

We have revised the main text to clarify this distinction (page 8: lines 305 - 310) and added an extended explanation for meta-dynamic behaviour convergence in the new section Error Convergence in the supplementary text (page 6: lines 184 - 210).

(3) While the lack of a connection between model parameters and biological data (mentioned in the public review) may not be a fatal flaw in the manuscript, the concern about the 100,000 random samples being insufficient to explore the parameter space is valid. In a thought experiment, considering the high and low rate for each parameter and the combinatorial explosion of possibilities (2^94), the number of simulations performed (100,000) represents only an extremely small fraction of the entire parameter space (~1/10^(23)). This limitation might not accurately capture the true heterogeneity present inside a solid tumour. One potential solution is to determine biological bounds on model parameters through data fitting, which can provide more meaningful constraints for the simulations. Alternatively, increasing the number of simulations and adopting more efficient sampling techniques can enhance the coverage of possible parameter sets.

We thank the reviewer for this insightful comment. We agree that the 94-dimensional parameter space is vast, and that 100,000 simulations represent only a fraction of the total combinatorial possibilities. However, the objective of our study is not to exhaustively sample the entire parameter space, but rather to sufficiently sample the ‘output space’ - that is, the complete spectrum of qualitative dynamic behaviours the network topology can generate. The key question is whether 100,000 model instances are sufficient for the distribution of these output dynamics to converge.

To formally address this, we have performed a convergence analysis, which is now detailed in the new supplementary section "Error Convergence" (Supplementary text page 6: lines 184 - 210) and illustrated in Supplementary Figure S12. This analysis demonstrates that the mean squared error (MSE) between dynamic distributions from N and 2N simulations exponentially decreases as N increases, and the distribution of protein dynamics changes negligibly well before reaching 100,000 instances. Furthermore, performing the entire analysis in triplicate with independent random seeds yielded nearly identical meta-dynamic maps (average standard deviation < 0.04%), giving us high confidence that we have robustly captured the network's behavioural repertoire.

We believe this convergence occurs because the system is degenerate: many distinct parameter sets within the high-dimensional space map to the same qualitative outcome (e.g., 'rebound' or 'decreasing'). Our goal was to capture the set of possible outcomes, not every unique parameter combination that leads to them.

Regarding the parameter range, we intentionally chose a broad, unbiased range (10^-5 to 10<sup4></sup>)as a proof-of-concept to delineate the theoretical upper limit of heterogeneity the network can support, thereby capturing even rare but potentially critical resistance dynamics. We agree with the reviewer that a future direction is to constrain these ranges using biological data. Such an approach would transition from defining what is possible (the focus of this manuscript) to predicting what is probable in a specific biological context. We have added this important point to the Discussion (page 16: lines 663-679) to highlight this avenue for future work.

(4) One of the manuscript's main results indicates that protein interactions play a more significant role in driving adaptive resistance than protein expression. To explore the impact of protein expression, the authors fixed a nominal parameter set and generated 100,000 initial concentrations of the 50 proteins in the ODE model. However, the simulations' equilibrium concentrations in the "starvation" and "fed" phases, which form the initial condition for the treated phase, are uniquely determined by the nominal model's kinetic parameters and not the initial conditions, which remain identical for each simulation. From a dynamical systems perspective, stable steady states are determined by the model parameters and attract all initial conditions within their basin of attraction. As a result, a random sampling of the initial conditions has a limited impact on the model dynamics. The authors' conclusion that "the ability of expression to induce resistance also seems to be dependent on the master parameter set" can be explained by this dynamical systems perspective, where the resistance state corresponds to a stable steady state determined by the master parameter set. Considering this, the evidence presented in the manuscript may not fully support the authors' conclusion regarding the importance of protein expressions relative to protein dynamics. The discrepancy might be attributed to a possible misunderstanding of this point, and further clarification from the authors could be helpful.

We thank the reviewer for the thoughtful perspective. We agree that, in a monostable system with fixed kinetic parameters and fixed conserved totals, varying only the initial split among moieties (e.g., X vs pX) will not change the final steady state; trajectories converge to the same attractor. In our analysis, however, “initial conditions” predominantly refer to total protein abundances (e.g., X_tot = X + pX + complexes), used as a proxy for expression heterogeneity. These totals are invariants on the simulated timescale (no synthesis/degradation in the pre-equilibration phases), and therefore alter the value of the steady state under a given parameter set. In other words, our IC sampling mostly varies conserved totals rather than merely redistributing a fixed total; hence the equilibrium reached after the starvation/fed pre-equilibrations depends on the sampled totals and the kinetics. This can be seen in the new Supplementary Figure S4, showing that changing the ICs does shift the eventual steady state even when kinetic parameters are fixed.

We have revised the text to: (1) define ICs explicitly as total abundances for multi-state species, (2) distinguish “initial split” from “conserved totals,” and (3) clarify that expression effects are context-dependent rather than universally dominant (page 4: lines 139-141 and page 10: lines 413-416)

(5) Additionally, it is important to note that the random sampling of 100,000 initial concentrations might not sufficiently explore the vast space of possible initial conditions. In the thought experiment mentioned earlier, where each protein can have high or low expression concentrations, there are approximately 2^(50) = ~10^(15) possible combinations of initial concentrations. Thus, the 100,000 random simulations only represent around ~1/10^(10) of the possible initial conditions in this simplistic scenario. Consequently, this limited sampling of initial conditions may not provide enough information to draw meaningful conclusions, even if the initial conditions were more directly linked to kinetic rates.

Please see our response to Comment (3). Briefly, our ICs are continuous total abundances (conserved moieties), not binary high/low states; many IC configurations converge to the same qualitative attractors, so we estimate distributional properties rather than enumerate all combinations. Our convergence diagnostics (independent replicates and sample-size doubling) show that the meta-dynamic distributions stabilise well before N=100,000 (see Supplementary Figure S12). We have clarified this in the Supplementary Information (Error Convergence section) with the new convergence results.

(6) The authors implement a parameter selection step in the manuscript, where they filter out parameter sets that lead to what they term non-biological simulations. However, the rationale for determining if a given parameter set results in a stiff system of ODEs remains unclear. The authors cite references [38,39] to support the claim that stiff equations are not biologically plausible. Still, upon review, it is evident that [38] does not include the term "stiff," and [39] discusses using implicit methods to simulate stiff ODE models without specifically commenting on the biological plausibility of stiff systems. The manuscript lacks direct evidence to justify the conclusion that filtering out parameter sets that result in stiff ODE systems is reasonable. Since the filtering step accounts for the majority of discarded parameter sets, a stronger foundation is required to support the statement that stiff equations are non-biological.

We thank the reviewer for pointing out the issue in our original justification. The reviewer is correct: stiff systems are a common feature of biological models, and our claim that they are likely ‘biologically implausible’ was not well substantiated. The filtering of these model instances was, in fact, due to a computational limitation rather than a biological principle. The issue was that these parameter sets produced systems of ODEs that were so numerically stiff they were unsolvable within a reasonable timeframe by the SUNDIALS ODE solver suite, which is specifically designed for such systems.

Following the reviewer's comment, we investigated the source of this prohibitive stiffness. We discovered it was not an intrinsic property of the parameter sets themselves, but rather an artifact of our simulation setup. The extreme stiffness occurred almost exclusively during the initial integration timesteps, caused by the large initial discrepancy between the concentrations of active and inactive protein forms. This large discrepancy created the conditions for overtly stiff solutions i.e. unsolvable with implemented ODE solve settings. To overcome this problem, we set a large maximum number of steps in the ODE solver for the first couple of time points, enabling the solver to overcome the excessively stiff portion of the solve. We found that the vast majority of the previously 'unsolvable' model instances could now be successfully simulated. Consequently, the number of parameter sets discarded due to solver failure is now negligible (< 1%), and this filtering step no longer accounts for the majority of discarded parameter sets. Most importantly, the distributions of dynamics were not significantly altered by this adaptation.

We have revised the " Sampling and filtering of model instances (page 5: lines 174 – 189)" part in the Methods section to reflect this more accurate understanding. We have corrected our original claim regarding the biological plausibility of stiff systems and corrected our use of the references. Ref [38] was included to demonstrate that models of biological systems are stiff, which was a major conclusion of that paper, and [39] was originally included to demonstrate that solving ODEs is reliant on solvers that can integrate stiff systems. Upon review, ref [39] has been removed.

Overall, this investigation has made our analysis more robust by allowing us to include a wider, more representative range of parameter sets, and has tangibly improved the quality of our study.

(7) Additionally, it is important to consider the standard method for accounting for stiff systems, as presented in [39], which involves using implicit numerical methods for ODE simulation. The authors mention using numerical methods from the SUNDIALS suite, which includes implicit methods, but the specific numerical method used remains unclear. Furthermore, it would be valuable for the authors to disclose the number of parameter sets that were filtered to obtain the final set of 100,000 accepted parameter sets. This information would provide insights into the extent of filtering and the proportion of parameter sets that were excluded during the selection process.

We apologise for the lack of specific detail and have now updated the text. To clarify, all ODE simulations were performed using the CVODE solver from the SUNDIALS suite. This solver employs an implicit, variable-order, variable-step Backward Differentiation Formula (BDF) method, which is robust and specifically designed for handling the stiff systems common in biological network modelling. We have now explicitly stated this in the "ODE model construction, modelling, and simulations (page 4: lines 162 – 164)" section of the Methods.

Regarding the filtered parameters, we have included a revised and detailed discussion of this in the "Sampling and filtering of model instances (page 5: lines 174 – 189)" part in the Methods section (see our response to comment (6) above). Briefly, after applying the filters, ~40–45% of instances did not reach steady state within the simulation timeframe, and ~50–55% did not meet the minimum drug-response criterion. Approximately 10% satisfied all criteria and were retained for analysis. Importantly, we employed ‘rejection sampling’ and continued drawing until we had N = 100,000 accepted instances that satisfied all the criteria.

(8) An important step in the simulation process described by the authors is the simulation of the "fasted" and "fed" states until an equilibrium is reached. However, it is not clear how the authors determine if the system has reached an equilibrium. It would be helpful if the authors could provide more information regarding the criteria used to assess equilibrium in the simulations. Regarding the "fed" state, it is not explicitly stated whether the mitogen stimulus is assumed to be constant throughout the "fed" experiment. Considering the dynamic nature of mitogen stimulation in biological systems, it would be beneficial if the authors could clarify this assumption and discuss its biological relevance.

We apologise for the lack not specifying this in the original text. A simulation was considered to have reached equilibrium when the concentration of every protein species changed by < 1% over the final 100 time steps of the simulation phase. We have now added this criterion to the "Sampling and filtering of model instances (page 5: lines 177 – 179)" part of the Methods section.

Regarding the second part of the comment, in our simulations, both the mitogenic and the drug inputs were modelled as constant, stepwise functions that, once turned on, remained at a fixed concentration for the remainder of the simulation. The biological rationale for this choice was to rigorously test for bona fide adaptive resistance. By maintaining a constant mitogenic and drug pressure, we can ensure that any observed recovery in the activity of downstream proteins is due to the internal rewiring and adaptation of the signalling network itself, rather than an artefact of the removal or decay of the external stimulus/drugs. We have now clarified this rationale in the "ODE model construction, modelling, and simulations (page 4: lines 168 – 171)" part of the Methods section.

(9) The "Description of Model Scope and Construction" section in the Supplementary Information should include explicitly the model reactions and some discussion about their specific form (e.g., why is '(((kc2f1*pIR*PI3K) / (1 + (pS6K/Ki2))) + (kc2f2*pFGFR*PI3K))' representing the phosphorylation rate of PI3K, with pS6K in the denominator?).

The reviewer is right to ask for model justification. We have expanded the Supplementary “Description of Model Scope and Construction” section (page 2: line 63 – page 5: line 185) to include a complete reaction list with rate laws and a brief rationale for each. We also explain the specific PI3K phosphorylation term: activation by pIR and pFGFR is attenuated by pS6K via a denominator, which captures the well-described S6K-mediated negative feedback that reduces activation (e.g., via IRS1 phosphorylation).

(10) In line 349, the statement "Given that CDK46cycD is only strongly suppressed in just under 60% of the model instances (Figure 3C)" lacks clarity regarding where to look to interpret the 60% value. If this means that 4 out of the 7 model instances are resistant, and the other 2 proteins also have the same percentage of resistance, then there is no apparent reason to focus solely on CDK46cycD.

The reviewer is correct; the figure reference was an error, which has been rectified in the main text (page 9: line 355). The actual figure reference was to Supplementary Figure 2A, which shows the heatmap of all the frequencies for each protein dynamics for all the active protein forms. CDK4/6cycD shows a sustained decreasing dynamic for 59.93% of model instances, which is where this number was derived. We have also now explicitly referenced this number in the supplementary Figure 2A legend.

We focus on CDK4/6cycD because it is the direct pharmacological target of CDK4/6 inhibitors. Our point was to suggest that even when the target is suppressed in the majority of instances (~60%), this does not reliably propagate to uniform downstream inhibition across the network, thus highlighting emergent, network-driven adaptive responses.

(11) We observed that in Fig. 5A, the authors show that multiple pathways are blocked. However, it is unclear whether they reduced the value of one parameter in the experiment or simulated multiple combinations of parameter inhibition. Considering the large number of parameters (94) in the model, if the authors simulated all possible combinations of parameter inhibition, the number of combinations would be significantly more than 94. An actual inhibitor typically has an inhibitory effect on multiple molecules. Therefore, it would be necessary to identify the parameters that lead to drug resistance when multiple molecules are inhibited. However, examining the inhibition patterns for all 94 parameters would be practically impossible. As a potential approach, we suggest using ensemble learning techniques, such as random forests, to handle this problem efficiently. With a dataset of binary outputs indicating the presence or absence of resistance for a sufficient number of inhibition patterns, ensemble learning can be applied to find the parameters that contribute to drug resistance. Popular feature selection algorithms like Boruta could be utilised to identify the most relevant parameters. The results obtained by ensemble learning are similar to the ranking in Fig. 5C, potentially providing a more robust validation of the authors' findings. By incorporating these additional analyses, the authors could strengthen the reliability and significance of their results related to parameter inhibition and drug resistance.

We appreciate the suggestion and the opportunity to clarify. Figure 5A depicts multiple pathways were interrogated, but in the analysis, parameters were inhibited one at a time (OAT) - not in combination. We have revised the figure legend and added a section named “Protein knockdown perturbation analyses (page 6: lines 228 – 233)” in the Methods section to make this explicit. Moreover, some additional text in the main text has been slightly modified to make this clearer (page 11: lines 462-463, page 24: lines 856-857).

We chose the OAT design intentionally to obtain causal, first-order attribution of control points across a broad parameter ensemble without confounding from simultaneous co-inhibition. This provides an interpretable ranking of primary drivers (Figure 5C) that is consistent with the paper’s mechanistic focus. We agree that a multi-target inhibition approach could be a useful next step; however, an exhaustive combinatorial screen is beyond the scope of this proof-of-concept. In such future studies, the ensemble learning, as suggested by the reviewer, could be layered onto our MDN framework to assess robustness of the ranking under co-inhibition.

(12) In explaining the parameterization of the model, we find an implication of a quantitative model. However, upon examining the results in Fig. 7D, we observe that they are only qualitatively correct. When comparing Figs. 7A and 7C, we note that many model instances are immediately suppressed, and the time scale remains unknown. We believe it would be essential for the authors to explain how the model of this study maintains its quantitative nature despite the results in Fig. 7. If such an explanation cannot be provided, it raises concerns regarding the biological reliability of several findings within this study.

While our framework is built on quantitative ODEs, the validation we present in Figure 7 is indeed qualitative. This is an intentional and key feature of our study's design. Our goal was not to build a calibrated, quantitative model of a specific cell line (e.g., MCF10A), but rather to establish a proof-of-concept theoretical framework that systematically explores the full spectrum of dynamic behaviours a given network topology can possibly generate. To achieve this, we intentionally sampled parameters from a very broad, unbiased range to delineate the theoretical upper limit of heterogeneity. This in silico population is therefore designed to be far more heterogeneous than any single isogenic cell line.

The striking qualitative agreement seen between our meta-dynamic distributions and the single-cell data in Figure 7D is thus not a failure of quantitative prediction, but rather a strong validation of our core premise: that a significant degree of signalling heterogeneity exists in cell populations and that our framework can effectively capture its emergent properties.

Regarding the specific comment on Figure 7C, we apologise for the lack of clarity. Nominally, we chose to simulate for 24 hours however, the x-axis in our simulations represents arbitrary time units, as the timescale is dependent on the meaning/units of the parameter values. The goal is to compare the qualitative shape of the response (e.g., rebound, sustained decrease), not the absolute time in hours. Moreover the rapid initial suppression seen in many of our model instances (Fig 7C) is a direct parallel to the rapid suppression seen in the experimental data (Fig 7A). This initial phase is followed by a wide variety of adaptive behaviours (or lack thereof) in both our simulations and the real cells, which is the key phenomenon we are studying.

We have revised the text (page 14: lines 598-601) and Figure 7’s legend to state more explicitly that our validation is qualitative and to clarify the purpose of our broad, uncalibrated approach. We have also added a note in the Discussion (page 18: lines 744-747) that calibrating this framework with cell-line-specific data is a natural next step for generating quantitative, context-specific predictions.

(13) Related to the previous point, the experimental data is presented as fold-change during CDK4/6 inhibition, and we notice that the initial fold-change at time 0 varies between 1 and 1.8. The difference in initial fold-change is unclear to us, as our understanding of fold-change typically corresponds to the change from baseline, typically represented by the protein concentration at time 0.

Furthermore, while the experimental data exhibits uniformly decreasing CDK4/6 activity, a substantial number of simulations indicate constant CDK4/6cycD, showing a significant qualitative discrepancy between the simulations and experimental findings. This disparity makes it difficult for us to interpret the comparison between the two datasets effectively, given the complexities in comprehending the experimental fold-change figure.

As Figure 7 serves as the primary validation of model simulations in the manuscript, we believe that the current presentation may not provide a compelling reason to believe that the model accurately captures experimental data. To enhance clarity and validation, we suggest overlaying the experimental data over the simulations or considering the median and 10/90% percentile of the experimental data, which may potentially offer improved readability and facilitate a more robust interpretation of the comparison.

The experimental data from Yang et al. (ref 55, main text) measures kinase activity using a nucleus-to-cytoplasm translocation reporter system, wherein a bait protein is phosphorylated by the target kinase causing it to translocate from the nucleus to the cytoplasm. Hence, the y-axis represents the ratio of nuclear vs. cytoplasmic fluorescence, not a fold-change from a t=0 baseline. The variation in the starting value (between 1 and 1.8) reflects the inherent heterogeneity in the reporter's localization across individual cells even before the drug is added. We have updated the y-axis label and revised Fig. 7’s legend to state this explicitly.

The most likely explanation for the discrepancy between experimental dynamics and our simulation dynamics is that the experimental data comes from an isogenic cell line that is largely sensitive to CDK4/6 inhibition. Our simulations are derived from a very wide parameter sweep, where the intent is to represent all possible cell states. It is quite striking that that there is such a high correlation between the experimental data and simulations, indicating that perhaps the heterogeneity of even isogenic cell lines is significantly greater than might be intuited; a point we now mention in the revised Discussion (page 17: lines 716-727).

It is worth noting again, that our analysis is intentionally constructed to be as heterogeneous as possible, and is not trained on any biological data that might otherwise constrain the output-behaviour space. The isogenic cell line almost certainly represents a much more constrained output-behaviour space than our analysis.

The y-axis label has also been updated accordingly. As mentioned in (12) this result is intended as a qualitative validation, showing that cell lines indeed have highly variable signalling dynamics. Given the range of parameters tested, we think it is surprising that the degree of agreement between the experiment and our analysis is as high as it is. Again, we believe this suggests that heterogeneity may be more prevalent than is intuited. We do not believe we have made any strong quantitative claims in the main text, and we certainly aim to work towards biological, quantitative validation in the future. Finally, we altered the wording of the results heading (page 14: line 562) to make it clear that we are only making qualitative claims and removed the claim that the evidence was strong.

With these clarifications and corrections, we believe the validation is now much more compelling. The key point is not a perfect quantitative match, but the strong similarity in the distribution of heterogeneous behaviours.

(14) The authors mention simulating treatment with 10nM of CDK4/6i or Ei, but specific details on how this treatment is included in the model simulations are not provided. This lack of information makes it challenging to fully evaluate the comparison between model simulations and experimental evidence in Figure 7. It would be highly appreciated if the authors could clarify how the treatment with CDK4/6i or Ei is incorporated into the simulations to facilitate a better understanding and interpretation of the results.

To clarify, the effects of the inhibitors were incorporated directly into the kinetic rate laws of their respective target reactions.

CDK4/6 inhibitor (CDK4/6i): This was modelled as an inhibitor of the formation of the active CDK4/6-cyclin D complex. We have now explicitly detailed this in the description for reaction R27 in the "Description of Model Scope and Construction" section of the Supplementary Information.

Estrogen Receptor inhibitor (Ei): This was modelled as an inhibitor of the estrogen-dependent activation of the Estrogen Receptor. This is now explicitly detailed in the description for reaction R15 in the same supplementary section.

It is however important to reiterate that our goal in Figure 7 is qualitative, shape-based comparison; therefore, we used a fixed fractional inhibition (reported in Methods) rather than a calibrated IC50/Hill model.

(15) The authors state strong support for their modelling conclusions based on the literature. However, we still have concerns regarding the validation of the model against CDK2 or CDK4/6 data in Figure 7, as it appears less convincing to us. Furthermore, the authors list known resistance mechanisms that are replicated in their modelling. Nevertheless, we find the conclusion somewhat weakened by Figure S10, where approximately 80% of the nodes are implicated in some form of resistance pathway. This raises questions about the model's selectivity, as many proteins included in the model seem to drive resistance in some manner. In the Supplementary Information, the authors mention excluding or abstracting some protein species from the mitogenic and cell cycle pathways to manage computational resources effectively. This abstraction makes it difficult to determine if the proteins identified as potential drivers of resistance genuinely drive resistance or might represent abstractions of other potential drivers. To enhance the manuscript's clarity and address potential concerns about the model's selectivity and abstraction, we suggest providing more details and discussion in the main text.

The reviewer's observation that a large number of nodes are implicated in resistance pathways in Figure S10 is correct. However, we argue this is not a weakness of the model's selectivity, but rather a key finding that reflects the biological reality of adaptive resistance. The literature is replete with a wide and growing number of distinct mechanisms of resistance even to a single class of drugs (1,2), which supports the idea that cancer can co-opt a wide variety of network nodes to survive.

Figure S10 is not a binary map where every implicated node is equal, instead it is a likelihood map, where the colour and weight of the connections represent how often a particular interaction participates in driving resistance across the theoretical full range of possible network dynamics. The figure shows that while many nodes can contribute to resistance, they do so in a hub-like manner i.e. small subsets of nodes coordinate to drive resistance. This provides a rationalised, data-driven prioritisation of the most dominant and recurrent resistance strategies. We draw two important conclusions from this work 1) Resistance likely occurs due to resistance hubs, not individual proteins, and 2) that the frequency of a resistance hub in an MDN analysis is likely proportional to the frequency of that hub emerging as a resistance mechanism in a population of cells and patients.

Regarding the issue of abstraction, the reviewer is correct that this is an inherent feature of any tractable systems model. In our case, several species in the mitogenic/cell-cycle pathways are module-level proxies to control model size. The highly implicated "hub" nodes in our model likely represent critical cellular processes that are themselves composed of several individual protein interactions.

To address these concerns, we have significantly revised the Discussion (page 16: lines 681 – 694) to: (1) frame resistance as a network-level phenomenon; (2) show that our frequency-based ranking is selective, prioritising the most probable, recurrent mechanisms; and (3) clarify that - given model abstraction -our findings implicate critical processes (modules), not just single proteins, as the drivers.

Overall, these changes do not alter our main conclusions: adaptive resistance is an emergent, network-level property; many routes exist, but a smaller set of nodes/modules consistently carry the largest influence across heterogeneous contexts.

(16) We consider that the figures and legends, including the supplementary information, are inadequately explained. The information provided is insufficient for us to comprehend the figures fully, leading to the need for interpretation on our part as readers. This could potentially introduce biases when trying to understand the claims made by the authors. To improve our understanding, it would be essential for the authors to assign appropriate labels to the figures and provide comprehensive explanations in the legends. For example, in Fig 3, we suggest labelling the tree diagrams in panels A and B, as well as the colour bars. We also recommend applying the same approach to other figures, adding accurate axis labels and descriptions of colour gradients to enhance clarity.

We thank the reviewer for this critical feedback. To address this comment, the figure legends have been revised where appropriate and greatly expanded to improve their comprehension. Moreover, we have added explicit labels to all previously unlabelled components, such as the cluster dendrograms and colour code bars in Figure 3A, B.

(17) To enhance readability, we recommend interchanging the order of Figures 1 and 2 in the sequence they appear in the main text. Alternatively, the text can be adjusted to refer to the figures in the correct order. Additionally, attention should be given to the bottom of Fig 1, which appears to be cropped or cut off. Furthermore, the incorrect word spacing in some figure elements, such as Fig. 3A title, Fig. 5B title, and Fig. 6B y-label, should be corrected for improved visual presentation.

Following the reviewer’s comment, the order of Figures 1 and 2 has been switched to reflect the order in which they are referred to in the main text. These Figures have been re-exported to fix unintentional word spacing errors.

(18) We recommend that the language used to refer to the initial conditions in the manuscript is clarified and homogenised. Currently, the authors use different terms such as "basal expression," "protein expression," "state variable values," or "initial conditions" to refer to them. This variation in terminology can be confusing for readers. In particular, the use of "basal expression" is problematic, as it typically refers to the leaky value of a reaction in the absence of an inducer, making it another biophysical parameter of the system rather than an initial condition. To enhance clarity and consistency, we suggest the authors decide on a single term to refer to the initial conditions throughout the manuscript and provide a clear explanation of its meaning to avoid any confusion. This will help readers better understand the concept being discussed and prevent any potential misinterpretations.

We thank the reviewer for this very helpful suggestion. To resolve this and improve clarity, we have homogenized the language throughout the manuscript. We now clarify the use the following 3 terms in their specific contexts:

We use “protein abundances” exclusively for the conserved total abundances of multi-state species (e.g., Xtot = X + pX + complexes) that are sampled across instances to represent expression heterogeneity.

We use ‘initial conditions’ to refer to initial values of the state variables in a model simulation. This term is related to protein abundance as the setting of initial conditions for conserved species sets the protein abundance. This is explicitly stated in the text (page 3: lines 87 - 91).

We use “state variables” to refer to the time-dependent model species.

We avoid the term “basal expression” in technical descriptions. Where a biology-facing phrase is helpful, we use “protein expression level”. This is used when referring to the biological concept that the initial conditions are intended to represent, i.e. the heterogeneity in protein amounts across a cell population.

We have performed a thorough search-and-replace to ensure this new convention is applied consistently and have removed the potentially confusing term "basal expression" from the revised manuscript.

(19) Why are saturable functions (e.g., Michaelis-Menten functions) ignored in the model? What are the potential consequences?

The main objective of this work was to perform a large-scale, systematic exploration of a high-dimensional parameter space (94 parameters) to map the full repertoire of qualitative dynamic behaviours a network topology can support. Using saturable functions like Michaelis-Menten kinetics would have roughly doubled the number of parameters to be explored (from k to Vmax and Km for each enzymatic reaction), making a parameter sweep of this scale computationally intractable. We therefore prioritised the breadth of the parameter search over the depth of kinetic detail, which we believe is the appropriate choice for a proof-of-concept study focused on heterogeneity.

This simplification has potential consequences. A major one is that our model cannot capture phenomena that arise specifically from enzyme saturation, such as zero-order kinetics or certain forms of ultrasensitivity (switch-like responses). However, we argue that this is an acceptable trade-off for two main reasons: (1) Our analysis is based on classifying broad, qualitative response shapes (increasing, decreasing, rebound, etc.). Mass-action kinetics are fully capable of generating this rich spectrum of behaviours; and (2) by varying the mass-action rate constants over nine orders of magnitude (from 10^-5 to 10<sup4></sup>), our parameter sweep effectively samples a vast range of reaction efficiencies. A very low rate-constant can approximate the behaviour of a saturated, low-efficiency enzyme, while a high rate-constant can approximate a highly efficient, non-saturated one. In this way, the broad sweep of the rate parameter partially reflects the effects that would be captured by varying Vmax and Km.

For transparency, we have added a brief rationale to the “ODE model construction, modelling, and simulations” part of the Methods (revised main text, page 4: lines 153-155) and the "Description of Model Scope and Construction" section in the Supplementary file (Supplementary text page 2: lines 63-73).

(20) Given the relevance of the concept of "heterogeneity" in this work, a short discussion about biochemical noise and its implications on the analysis (e.g., why it is not included, and if it will be a next step) would be appreciated.

Our MDN modelling framework represents heterogeneity by creating an ensemble of deterministic models, where each model instance has a unique set of kinetic parameters and/or initial protein abundances. We propose that this is a powerful way to mechanistically represent the functional consequences of all sources of cellular variation. Over time, the effects of genetic mutations, epigenetic states, and even the time-averaged impact of intrinsic biochemical noise will manifest as changes in the effective interaction strengths and protein concentrations within a cell. Our large-scale parameter/IC sweep is designed to systematically explore the full range of dynamic behaviours that can emerge from this underlying biological variation. Therefore, our approach does not compete with stochastic modelling but is complementary to it. While stochastic simulations can capture the dynamic trajectories of single cells, our framework provides a panoramic view of the entire spectrum of possible stable phenotypes that can emerge at the population level. We agree that modelling intrinsic biochemical noise (stochasticity arising from finite copy numbers), e.g. using chemical Langevin or SSA, is a possible extension in future work but expected to be very computationally expensive. We have added a brief discussion on this as future direction in the revised Discussion.

(21) We have noticed that the first four paragraphs of the Discussion section overlap with the Introduction, as they mainly reiterate the significance of the study itself rather than focusing on the specific results obtained. To avoid redundancy and provide a more cohesive and informative discussion, we recommend that the authors shift the focus of the Discussion section towards presenting potential interpretations, even if they are not definitive, of the results obtained. By doing so, the Discussion will serve as a valuable platform for deeper analysis and insightful observations, allowing readers to better comprehend the implications and significance of the research findings.

We thank the reviewer for this structural feedback. Following the reviewer's feedback, we have significantly rewritten and restructured the Discussion section. The redundant introductory material has been removed.

The rewritten Discussion centres on interpretation, implications, and connect our findings to the literature. It now: (i) frames MDN as a systems-level framework that links molecular heterogeneity to qualitative signalling “meta-dynamics” and adaptive escape under constant drug pressure; (ii) highlights two key findings: an asymmetry in control (interaction kinetics exert stronger, more consistent influence than protein abundance) and a topology-driven convergence whereby a vast parameter space funnels into a finite set of recurrent behaviours; (iii) shows that resistance is a network-level property, with many possible routes but a small set of recurrent hubs/modules dominating; and (iv) provides a qualitative alignment with single-cell reporter data while clarifying the intent and limits of that comparison. Moreover, we now explicitly discuss limitations (rate-law simplifications, broad priors, determinism, and modular abstractions) and outline next steps for future research, including data-constrained priors and stochastic extensions.

We believe this substantial revision has transformed the Discussion into a much more insightful and valuable part of the manuscript that directly addresses the reviewer's concerns.

(22) The supplemental text file containing the model equations can be a bit challenging to read and understand. It would be greatly beneficial if the authors could consider generating a file using a typesetting program.

We have now included a typeset list of state variable equations and ODEs, along with the original model files.

(23) The authors mentioned that some model parameterizations result in negative solutions, which is surprising. Access to the model equations would help understand why this happens and is crucial for researchers who may want to use this approach. Clarifying the model equations' presentation would enhance transparency and aid other researchers in applying this method for similar research questions.ach. Clarifying the model equations' presentation would enhance transparency and aid other researchers in applying this method for similar research questions.

The reviewer is correct to be surprised by the mention of negative solutions, as negative concentrations are physically impossible. We clarify that these are not a result of any structural flaw in our model's equations but are a well-known, although rare, numerical artifact of floating-point arithmetic in computational solvers.

Our model is constructed using standard mass-action and first-order kinetics, which structurally guarantee non-negativity. However, when a species' concentration approaches the limits of machine precision (i.e., becomes a very small number extremely close to zero), the ODE solver can, in rare instances, numerically undershoot zero, resulting in a small negative value. If this occurs, it can lead to instability in subsequent integration steps.

This is not a biological phenomenon but a computational one. Therefore, the standard and appropriate procedure, which we follow, is to implement a filter that discards any simulation trajectory where such a numerical instability occurs.

(24) The reference listed for the CDK4/6 and CDK2 measurements is Yang et al. [55] in the figure caption, but as Xe et al. in lines 559-561 of the manuscript.

The text has been updated to match citation.

(25) We suggest that the authors revise and cite a previous study conducted by Yamada et al. (Scientific Reports, 2018), which presents an approach to expressing cell heterogeneity as a probability distribution of model parameters.

Following this suggestion, we have revised the Discussion (see response to comment (21)) to include and discuss Yamada et al. (Scientific Reports, 2018), which models cell heterogeneity as a probability distribution over parameter values.

(26) In the manuscript, on line 677, the authors state, "This indicates that there is an upper limit to the degree to which parameter sets can influence the qualitative shape of a protein's dynamic within a given network topology." We wish to highlight that this finding may not be particularly surprising. Given that the parameters were randomly determined within a specific range, it is understandable that altering the number of parameter samples would not substantially impact the distribution of model instances.

We thank the reviewer for this insightful comment, which allows us to clarify the significance of this finding. While it is true that any sampling from a fixed distribution will eventually converge statistically, our conclusion is not about statistics but about the intrinsic, constraining properties of the network's topology. The novelty is not that the distribution converges, but that it converges to a surprisingly limited and finite repertoire of qualitative dynamic behaviours. A complex, non-linear network with nearly 100 free parameters could theoretically generate an almost endless variety of complex dynamics. Our finding is that this specific biological topology acts as a powerful filter, robustly channelling the vast majority of the near-infinite parameter combinations into a small, recurring set of functional outputs (increasing, decreasing, rebound, etc.).

The reason for this finite limit is mechanistic, as the reviewer's comment prompted us to investigate further. Our parameter sweep already covers an extremely wide, 9-order-of-magnitude range. As we pushed parameter values to even greater extremes in exploratory simulations, we found they do not generate novel, complex dynamic shapes. Instead, they tend to drive network nodes into saturated states- either permanently "on" (maximally activated) or permanently "off" (minimally activated). In both cases, the node becomes unresponsive to upstream perturbations.

Therefore, further expanding the parameter range would be unlikely to uncover new behavioural categories; it would simply increase the proportion of model instances classified as "no-response." This demonstrates a fundamental principle: the network topology itself enforces an upper limit on its dynamic complexity. We think this inherent robustness is what allows for reliable cellular signalling in the face of constant biological variation. We believe this is a non-trivial finding, and we have revised the Discussion (page 16: lines 664 - 680) to state this conclusion and its implications more clearly.

Author response:

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

We thank the editor and reviewers for their thoughtful and constructive feedback. We appreciate that all reviewers recognized the value of our study in linking adult neurogenesis and synaptic plasticity to representational drift in the olfactory system. They described the model as elegant and well-motivated, and agreed that it provides new theoretical insight into how stability and adaptability can coexist in sensory representations. The reviewers also identified areas where our manuscript could be strengthened, and as outlined in our revision plan we have:

(1) Refined our description of mitral/tufted cell stability and expand on within-session and across-day variability.

(2) Substantially expanded the Discussion to compare our modeling assumptions with experimental findings and recent anatomical evidence. Additionally, we have included the limitations of the study and areas for future investigation.

(3) Included a clearer description of the STDP implementation, plastic synapses, and their functional effects.

(4) Add a short section outlining model-based predictions that can guide future experiments. We also made minor textual edits to improve precision and flow, including citing prior conceptual work and clarifying model procedures.

These changes have strengthened both the conceptual framing and technical clarity of the paper. We are grateful for the reviewers’ careful reading and valuable suggestions.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors build a network model of the olfactory bulb and the piriform cortex and use it to run simulations and test their hypotheses. Given the model's settings, the authors observe drift across days in the responses to the same odors of both the mitral/tufted cells, as well as of piriform cortex neurons. When representing the M/T and PCx responses within a lower-dimensional space, the apparent drift is more prominent in the PCx, while the M/T responses appear in comparison more stable. The authors further note that introducing spike-time dependent plasticity (STDP) at bulb synapses involving abGCs slows down the drift in the PCx representations, and further link this to the observation that repeated exposure to the same odorant slows down drift in the piriform cortex.

The model is clearly explained and relies on several assumptions and observations:

(1) Random projections of MTC from the olfactory bulb to the piriform cortex, random intra-piriform connectivity, and random piriform to bulb connectivity.

(2) Higher dimensionality of piriform cortex representations compared to M/T responses, which enables superior decoding of odor identity in the piriform cortex.

(3) Spike time-dependent plasticity (STDP) at synapses involving the abGCs.

The authors address an open topical problem, and the model is elegant in its simplicity. I have however, several major concerns with the hypotheses underlying the model and with its biological plausibility.

Concerns:

(1) In their model, the authors propose that MTC remain stable at the population level, despite changes in individual MTC responses.

The authors cite several experimental studies to support their claims that individual MTC responses to the same odors change (some increase, some decrease) across days. Interpreting the results of these studies must, however, take into account the variability of M/T responses across odor presentation repeats within the same session vs. across sessions. In the Shani-Narkiss et al., Frontiers in Neural Circuits, 2023 study referenced, a large fraction of the variability across days in M/T responses is also observed across repeats to the same odorant in the same session (Shani-Narkiss et al., Figure 4), while the authors have M/T responses in the same session that are highly reproducible. This is an important point to consider and address, since it constrains how much of the variability in M/T responses can be attributed to adult neurogenesis in the olfactory bulb versus to other networks' inhibitory mechanisms, which do not rely on neurogenesis. In the authors' model, the variability in M/T responses observed across days emerges as a result of adult-born neurogenesis, which does not need to be the main source of variability observed in imaging experiments (Shani-Narkiss et al., Figure 4).

We agree with the reviewer and believe this is a critical discussion point. Indeed, both in Shani-Narkiss et al, Kay and Laurent, 1999, and in our lab, we observe trial-to-trial variability that occurs in the same recording session; as the reviewer correctly points out, this cannot be due to neurogenesis. These fluctuations may be trial to-trial noise, or reflect dynamics associated with other behaviors such as running (Chockanathan, et al. 2021) and decision making (Kay and Laurent, 1999). There is growing repertoire of literature showing that neural variability in early sensory coding appears to depend on behavioral fluctuations and internal states (Niell and Stryker for example). This variability that happens within a session in the Shani-Narkiss et al work may reflect some of these behaviorally relevant features of early olfactory coding, something that our model cannot account for. This is an excellent discussion point and we have included text (line 153-157, and line 321-330) in the manuscript to note this aspect of the data and how one can think of it in the context of our results.

Another study (Kato et al., Neuron, 2012, Figure 4) reported that mitral cell responses to odors experienced repeatedly across 7 days tend to sparsen and decrease in amplitude systematically, while mitral cell responses to the same odor on day 1 vs. day 7 when the odor is not presented repeatedly in between seem less affected (although the authors also reported a decrease in the CI for this condition). As such, Kato et al. mostly report decreases in mitral cell odor responses with repeated odor exposure at both the individual and population level, and not so much increases and decreases in the individual mitral cell responses, and stability at the population level.

Thank you for raising this important point regarding the findings of Kato et al. (2012). We agree that their results suggest increased sparsening and stability in M/T cell odor responses with repeated exposure. However, as noted in Yamada et al. (2017), the experimental literature on this question remains mixed. Yamada and colleagues reported a “drastic reorganization of ensemble odor representation” across days and emphasized that “sensory experience does not necessarily cause a major sparsening of the odor response,” explicitly contrasting their findings with those of Kato et al. (2012).

Our model captures the dynamics observed in Yamada et al. (2017), providing a mechanistic explanation for how significant reorganization can emerge in M/T ensembles despite stable low-dimensional population structure. In both Yamada et al (2017) and Kato et al (2012) the investigators have nuanced differences in experimental design (method of head fixation, behavioral paradigm used, training etc.), all of which are known to affect olfactory responses and therefore the degree of sparsity and overlap in population codes. Our model does not include any of these behavioral features that may differentially engage the olfactory circuit and thus affect population responses. Notably, in previous work, we highlight how even simple changes to top down feedback that reflect one phenomenological manipulation to functional connectivity in the olfactory circuit could have disparate effects on the degree of sparsity in neural representations over time whereby this manipulation would be activated by some behavior broadly. In our current model, there is no behavior that would allow us to study the critical features of the neural activity code in the M/T cells. Instead we focus on one specific aspect, adult neurogenesis which we can explicitly manipulate and affect in a biologically meaningful way. The review’s point however is well taken and important, and we have added text to the Discussion (line 336-344) to highlight the differing experimental outcomes and to clarify how our model aligns with the Yamada et al. results.

(2) In Figure 1, a set of GCs is killed off, and new GCs are integrated in the network as abGC. Following the elimination of 10% of GCs in the network, new cells are added and randomly assigned synaptic weights between these abGCs and MTC, GCs, SACs, and top-down projections from PCx. This is done for 11 days, during which time all GCs have gone through adult neurogenesis.

Is the authors' assumption here that across the 11 days, all GCs are being replaced? This seems to depart from the known biology of the olfactory bulb granule cells, i.e., GCs survive for a large fraction of the animal's life.

Thank you for raising this important point regarding the lifespan of granule cells (GCs). We agree that developmentally born GCs are not fully replaced. Indeed, multiple studies indicate that some developmentally born GCs can survive for very long periods, up to 18-24 months, essentially the lifetime of the animal (Kaplan, 1985; Petreanu & Alvarez-Buylla, 2002). However, the fraction of total GCs that such long lived GCs constitute remains an open question, in part because of challenges to measure the lifetime survival of newborn neurons. What there is consensus on is the significant size of the granule-cell population undergoing continuous turnover through adult neurogenesis (reviewed in Lepousez et al., 2013).

We should clarify that we do not assume that 100% of the granule cell population turns over in an 11 day period. We use “day” to represent a static epoch over which we can implement plasticity rules across two time scales. Critically, we also randomize the turnover treating every cell in the GC population as equally likely to be replaced. Prior experimental evidence suggests that some GCs are more likely to persist (possibly as a result of experience, Magavi et al., 2005) which may in some regards make our result on stabilization following repeated sensory exposure more dramatic (as the GCs that show the largest change following STDP may also be the ones that are the most stable, and therefore least likely to turnover). We do not include this in our model as we could not identify a framework for “selecting” which GCs would persist that would not be tautological. The point the reviewer raises is critical, and a discussion of these points is warranted - which we now include in the manuscript (line 352-361).

Additionally, there is some evidence that behaviors, such as novelty, can increase the rate of adult neurogenesis (Kamimura et al., 2022, H.van Praag et al.,1999, Gheusi and Lledo., 2014) , suggesting a complex reciprocal relationship between the mechanisms that generate the cells shaping how olfactory stimuli are encoded for and the encoding process itself; our model also does not include any of these dynamic features which represent an additional layer of complexity, which may further provide an intermediate time scale, one of behavioral selection and action, that is slower than the milliseconds on which spike time dependent plasticity happens, but faster than the time scale of neurogenesis. We include this point in the discussion also (line 352-361). 

Our 11-day simulation however is designed to uncover how plasticity across multiple timescales (STDP and adult neurogenesis) at the network level shapes odor representations as multiple rounds of GC turnover occur. Changing the timescale and magnitude replacement in the simulations (either in terms of days or percent cells replaced) would affect the degree to which drift happens, but not phenomenon. Additionally, the representational structure in our model at intermediate time points (e.g., days 8~10) would correspond well to scenarios in which some fraction of developmentally born GCs persists in the circuit. Thus, our simulations span a range of possible empirical regimes, from high turnover to partial preservation. We have added discussion to the revised manuscript (line 352-361) clarifying this point and acknowledging the biological heterogeneity in GC lifespans.

(3) The authors' model relies on several key assumptions: random projections of MTC from the olfactory bulb to the piriform cortex, random intra-piriform connectivity, and random piriform to bulb connectivity. These assumptions are not necessarily accurate, as recent work revealed structure in the projections from the olfactory bulb to the piriform cortex and structure within the piriform cortex connectivity itself (Fink et al., bioRxiv, 2025; Chae et al., Cell, 2022; Zeppilli et al., eLife, 2021).

How do the results of the model relating adult neurogenesis in the bulb to drift in the piriform cortex representations change when considering an alternative scenario in which the olfactory bulb to piriform and intra-piriform connectivity is not fully distributed and indistinguishable from random, but rather is structured?

Thank you for pointing us to these important studies. We fully agree with the reviewer that the structure of the olfactory system might not be purely random, but we do not believe these papers contradict the level of abstraction used in our model.

Zeppilli et al. (2021) map molecularly defined projection neuron subtypes and their preferential targeting of different cortical and subcortical regions, but they do not report any fine-scale topographic organization of bulb → piriform connectivity that would contradict a view of randomly distributed input to piriform cortex. Studies from our lab using retrograde tracers in the blub show some spatial clustering of piriform cortical neurons whose axons project to the bulb (Padmanabhan et al., 2016, 2019), but these studies do not identify any “functional organization” or structure. Chae et al., (2022) focus on distinct long-range functional loops (mitral ↔ piriform vs tufted ↔ AON) and the differential role of cortical feedback, but again, at the level of cortical regions rather than individual cells and connectivity. Notably, our model does not consider AON.

Finally, Fink et al. (2025) reports a “like-to-like” excitatory connectivity motif within the piriform cortex and an experience-dependent reorganization of inhibitory synapses. As the authors note, “... this like-to-like motif is unlikely to reflect common input from the olfactory bulb”, so it does not conflict with our assumption of broadly random bulb → piriform input. This “like-to-like” motif is reflected in our model by wiring a certain subpopulation of piriform cells. On the other hand, we agree that the experience dependent changes in inhibitory connectivity within PCx are highly relevant for learning related plasticity but fall outside the scope of our study. We intentionally omitted piriform plasticity to isolate the contributions of adult neurogenesis in the bulb and plasticity acting on adult-born granule cells. But incorporating such cortical plasticity is an important direction for future work. We added a discussion (line 395-405) on this important point raised by the reviewer in the revised manuscript.

(4) I didn't understand the logic of the low-dimensional space analysis for M/T cells and piriform cortex neurons (Figures 2 & 3). In the authors' model, the full-ensemble M/T responses are reorganized over time, presumably due to the adult-born neurogenesis. Analyzing a lower-dimensional projection of the ensemble trajectories reveals a lower degree of re-organization. This is the same for the piriform cortex, but relatively, the piriform ensembles displayed in a low-dimensional embedding appear to drift more compared to the M/T ensembles.

This analysis triggers a few questions: which representation is relevant for the brain function - the high or the low-dimensional projection? What fraction of response variance is included in the low-dimensional space analysis? How did the authors decide the low-dimensional cut-off? Why does STDP cause more drift in piriform cortex ensembles vs. M/T ensembles? Is this because of the assumed higher dimensionality of the piriform cortex representations compared to the mitral cells?

Thank you for these thoughtful questions. We clarify the logic and purpose of the low-dimensional analyses and address each point below.

(1) Which representation is relevant for brain function, the high-dimensional or low-dimensional one?

We believe both representations are meaningful, with each capturing different aspects of the neural code. The high-dimensional activity reflects the full variability of individual cell responses, while the low-dimensional projection captures the dominant population level components that downstream areas are most likely to use for readout. We found that the low-dimensional representations are more stable in the bulb than in PCx, suggesting that information is used differentially between the two areas. The bulb provides a stable, sensory-anchored population code that reliably represents odor identity over time, consistent with both electrophysiological and behavioral studies (Nagayama et al., 2004, Chen et al., 2009, Davison and Katz, 2007, Cavaretta et al., 2018). This is consistent with its role as the first stage of information processing in the olfactory system which provides faithful representations that downstream circuits receive. The piriform cortex, by contrast, transforms this stable input into a more flexible representation. Drift in its low-dimensional space may reflect ongoing plasticity (Schoonover et al., Nature, 2021), integration of contextual signals, or higherdimensional computations characteristic of PCx (Fink et al., bioRxiv, 2025), suggesting its role more as an associative cortex instead of a pure sensory cortex.

(2) What fraction of variance is included in the low-dimensional space, and how was the cutoff chosen?

In our simulations, these PCs captured the majority of variance relevant for odor identity (~60–70% for M/T cells and ~55–65% for piriform cortex). We now report these fractions explicitly in Methods (line 937-939).

(3) Why does STDP cause more drift in piriform-cortex ensembles than in M/T ensembles? Does this reflect higher dimensionality in piriform cortex?

In our model, STDP does not cause more drift in PCx. It actually reduces drift and stabilizes PCx representations relative to the condition without STDP (as shown in Fig. 4C2). STDP has a much smaller effect in the bulb because: (1) M/T cells continue to receive stable odor input from the glomeruli and (2) the low-dimensional M/T representation is already stable even without plasticity. We have edited the manuscript to reiterate this point in both the results and discussion.

The reviewer is correct that the piriform cortex naturally exhibits more drift than the bulb, and their comment that this is due to its substantially higher representational dimensionality is spot on. The PCx contains many more neurons, receives highly divergent OB → PCx inputs, and has dense recurrent connectivity, all of which create many more degrees of freedom through which representations can drift. Additionally, because individual PCx neurons are sampling from a substantially more diverse combinatorial space of inputs (include feedback to piriform from an array of regions, Illig, 2005, Majak et al., 2004, Chapuis et al., 2013), the “dimensionality” of the population code is likely higher dimensional. While STDP stabilizes the dimensions of the PCx representation that are reinforced during plasticity, due to the large number of orthogonal dimensions available, some residual drift remains. Additionally, as the reviewer notes, there are some forms of plasticity, such as inhibitory plasticity in PCx that are not included in the model, that may also have an impact on both the representations, and the underlying dimensionality of those representations. We include these points in the discussion (line 381-394).

(5) Could the authors comment whether STDP at abGC synapses and its impact on decreasing drift represent a new insight, and also put it into context? Several studies (e.g., Lledo, Murthy, Komiyama groups) reported that abGC integrates in the network in an activity-dependent manner, and not randomly, and as such stabilizes the active neuronal responses, which is consistent with the authors' report.

Related, I couldn't find through the manuscript which synapses involving abGCs they focus on, or what is the relative contribution of the various plastic synapses shown in the cartoon from Figure 4 A1 (circles and triangles).

We thank the reviewer for raising this question. As the reviewer pointed out, several studies have shown that abGCs integrate into the bulb circuit in an activity dependent manner. They preferentially form synapses onto mitral/tufted cells that respond to behaviorally important odors, this “selection of surviving cells” is not included in our model. Instead, we use STDP at the synaptic level. This is of course not analogous, but provides a computational framework wherein the selection of surviving abGCs could be incorporated in future studies. It is perhaps notable that in our large scale simulations, synaptic changes at the population level may reflect some of this activity-dependent selection.

To that end, our model provides a new insight and suggests a broader function for adult neurogenesis. For example, when certain odors are reinforced in an activity dependent manner, abGCs born during that period may stabilize the circuits that respond to those odors. The resulting reduction of drift would help keep the representation of those odors stable over time, even while other parts of the circuit continue to change. We now highlight this idea in the Discussion (line 366-373).

For the second part of the question: in our model, STDP acts on two sets of connections. It applies to the synapses onto abGCs from M/T cells, GC/SAC cells, and PCx neurons. It also applies to the synapses that abGCs project to, including those onto M/T cells and GC/SAC cells. We have clarified this in the revised Methods (line 10011004).

(6) The study would be strengthened, in my opinion, by including specific testable predictions that the authors' models make, which can be further food for thought for experimentalists.

How does suppression of adult-born neurogenesis in the OB impact the stability of mitral cell odor responses? How about piriform cortex ensembles?

We appreciate the reviewer’s suggestion and formalize the following two predictions from our model:

Prediction 1: Suppressing adult neurogenesis will reduce spontaneous representational drift in the PCx. Increasing spike-timing-dependent plasticity during periods of experience with a specific odor will selectively stabilize representations of that odor.

Prediction 2: Adult neurogenesis will not affect AON representations of odor identity or concentration in the same way that PCx representations are altered and drift.

We include these two ideas in the discussion as experimentally testable predictions.

Reviewer #2 (Public review):

Summary:

The authors address a critical problem in olfactory coding. It has long been known that adult neurogenesis, specifically in the form of adult-born granule cells that embed into the existing inhibitory networks on the olfactory bulb, can potentially alter the responses of Mitral/Tufted neurons that project activity to the Piriform Cortex and to other areas of the brain. Fundamentally, it would seem that these granule cells could alter the stability of neural codes in the OB over time. The authors develop a spiking network model to explore how stability can be achieved both in the OB over time and in the PC, which receives inputs. The model recapitulates published activity recordings of M/T cells and shows how activity in different M/T cells from the same glomerulus shifts over time in ways that, in spite of the shift, preserve population/glomerular level codes. However, these different M/T cells fan out onto different pyramidal cells of the PC, which gives rise to instability at that level. STDP then, is necessary to maintain stability at the PC level as long as odor environments remain constant. These results may also apply to a similar neurogenesis-based change in the Dentate Gyrus, which generates instability in CA1/3 regions of the hippocampus

Strengths:

A robust network model that untangles important, seemingly contradictory mechanisms that underlie olfactory coding.

Weaknesses:

The work is a significant contribution to understanding olfactory coding. But the manuscript would benefit from a brief discussion of why neurogenesis occurs in the first place - e.g., injury, ongoing needs for plasticity, and adapting to turnover of ORNs. There is literature on this topic. It seems counterintuitive to have a process in the MOB (and for that matter in the DG) that potentially disrupts the ability to generate stable codes both in the MOB and PC, and in particular a disruption that requires two different mechanisms - multiple M/T cells per glomerulus in the MOB and STDP in the PC - to counteract.

We appreciate the reviewer’s suggestion and added discussion on this point in the revised manuscript (line 431-435).

Given that neurogenesis has an important function, and a mechanism is in place to compensate for it in the MOB, why would it then be disrupted in fan-out projections to the PC? The answer may lie in the need for fan-out projections so that pyramidal neurons in the PC can combinatorially represent many different inputs from the MOB. So something like STDP would be needed to maintain stability in the face of the need for this coding strategy.

This kind of discussion, or something like it, would help readers understand why these mechanisms occur in the first place. It is interesting that PC stability requires that odor environments be stable, and that this stability drives PC representational stability. This result suggests experimental work to test this hypothesis. As such, it is a novel outcome of the research.

We agree with the reviewer. The fan-out from the bulb to the piriform cortex is essential for the combinatorial coding that allows PCx neurons to represent many odor features and mixtures. This architecture gives the piriform cortex great coding capacity, but it also makes the system sensitive to small changes in its inputs. As a result, drift that originates in the bulb can spread more easily in PCx. A stabilizing mechanism is therefore needed downstream. In our model, STDP provides this stabilization by reinforcing the dimensions that carry meaningful odor structure. This allows the piriform cortex to keep a stable population code even when its inputs change over time. Neurogenesis supplies the flexibility, the fan-out supplies the expressive power, and STDP supplies the stability. All three elements work together to support a system that must recognize odors reliably while still adapting to new sensory experiences. We have added discussion on this point in the revised manuscript (line 395-405).

Reviewer #3 (Public review):

Summary

The authors set out to explore the potential relationship between adult neurogenesis of inhibitory granule cells in the olfactory bulb and cumulative changes over days in odorevoked spiking activity (representational drift) in the olfactory stream. They developed a richly detailed spiking neuronal network model based on Izhikevich (2003), allowing them to capture the diversity of spiking behaviors of multiple neuron types within the olfactory system. This model recapitulates the circuit organization of both the main olfactory bulb (MOB) and the piriform cortex (PCx), including connections between the two (both feedforward and corticofugal). Adult neurogenesis was captured by shuffling the weights of the model's granule cells, preserving the distribution of synaptic weights. Shuffling of granule cell connectivity resulted in cumulative changes in stimulus-evoked spiking of the model's M/T cells. Individual M/T cell tuning changed with time, and ensemble correlations dropped sharply over the temporal interval examined (long enough that almost all granule cells in the model had shuffled their weights).

Interestingly, these changes in responsiveness did not disrupt low-dimensional stability of olfactory representations: when projected into a low-dimensional subspace, population vector correlations in this subspace remained elevated across the temporal interval examined. Importantly, in the model's downstream piriform layer, this was not the case. There, shuffled GC connectivity in the bulb resulted in a complete shift in piriform odor coding, including for low-dimensional projections. This is in contrast to what the model exhibited in the M/T input layer. Interestingly, these changes in PCx extended to the geometrical structure of the odor representations themselves. Finally, the authors examined the effect of experience on representational drift. Using an STDP rule, they allowed the inputs to and outputs from adult-born granule cells to change during repeated presentations of the same odor. This stabilized stimulus-evoked activity in the model's piriform layer.

Strengths

This paper suggests a link between adult neurogenesis in the olfactory bulb and representational drift in the piriform cortex. Using an elegant spiking network that faithfully recapitulates the basic physiological properties of the olfactory stream, the authors tackle a question of longstanding interest in a creative and interesting manner. As a purely theoretical study of drift, this paper presents important insights: synaptic turnover of recurrent inhibitory input can destabilize stimulus-evoked activity, but only to a degree, as representations in the bulb (the model's recurrent input layer) retain their basic geometrical form. However, this destabilized input results in profound drift in the model's second (piriform) layer, where both the tuning of individual neurons and the layer's overall functional geometry are restructured. This is a useful and important idea in the drift field, and to my knowledge, it is novel. The bulb is not the only setting where inhibitory synapses exhibit turnover (whether through neurogenesis or synaptic dynamics), and so this exploration of the consequences of such plasticity on drift is valuable. The authors also elegantly explore a potential mechanism to stabilize representations through experience, using an STDP rule specific to the inhibitory neurons in the input layer. This has an interesting parallel with other recent theoretical work on drift in the piriform (Morales et al., 2025 PNAS), in which STDP in the piriform layer was also shown to stabilize stimulus representations there. It is fascinating to see that this same rule also stabilizes piriform representations when implemented in the bulb's granule cells.

The authors also provide a thoughtful discussion regarding the differential roles of mitral and tufted cells in drift in piriform and AON and the potential roles of neurogenesis in archicortex.

In general, this paper puts an important and much-needed spotlight on the role of neurogenesis and inhibitory plasticity in drift. In this light, it is a valuable and exciting contribution to the drift conversation.

We appreciate the reviewer’s comment and thank them for their thoughtful feedback.

Weaknesses

I have one major, general concern that I think must be addressed to permit proper interpretation of the results.

I worry that the authors' model may confuse thinking on drift in the olfactory system, because of differences in the behavior of their model from known features of the olfactory bulb. In their model, the tuning of individual bulbar neurons drifts over time.

This is inconsistent with the experimental literature on the stability of odor-evoked activity in the olfactory bulb.

In a foundational paper, Bhalla & Bower (1997) recorded from mitral and tufted cells in the olfactory bulb of freely moving rats and measured the odor tuning of well-isolated single units across a five-day interval. They found that the tuning of a single cell was quite variable within a day, across trials, but that this variability did not increase with time. Indeed, their measure of response similarity was equivalent within and across days. In what now reads as a prescient anticipation of the drift phenomenon, Bhalla and Bower concluded: "it is clear, at least over five days, that the cell is bounded in how it can respond. If this were not the case, we would expect a continual increase in relative response variability over multiple days (the equivalent of response drift). Instead, the degree of variability in the responses of single cells is stable over the length of time we have recorded." Thus, even at the level of single cells, this early paper argues that the bulb is stable.

This basic result has since been replicated by several groups. Kato et al. (2012) used chronic two-photon calcium imaging of mitral cells in awake, head-fixed mice and likewise found that, while odor responses could be modulated by recent experience (odor exposure leading to transient adaptation), the underlying tuning of individual cells remained stable. While experience altered mitral cell odor responses, those responses recovered to their original form at the level of the single neuron, maintaining tuning over extended periods (two months). More recently, the Mizrahi lab (Shani-Narkiss et al., 2023) extended chronic imaging to six months, reporting that single-cell odor tuning curves remained highly similar over this period. These studies reinforce Bhalla and Bower's original conclusion: despite trial-to-trial variability, olfactory bulb neurons maintain stable odor tuning across extended timescales, with plasticity emerging primarily in response to experience. (The Yamada et al., 2017 paper, which the authors here cite, is not an appropriate comparison. In Yamada, mice were exposed daily to odor. Therefore, the changes observed in Yamada are a function of odor experience, not of time alone. Yamada does not include data in which the tuning of bulb neurons is measured in the absence of intervening experience.)

Therefore, a model that relies on instability in the tuning of bulbar neurons risks giving the incorrect impression that the bulb drifts over time. This difference should be explicitly addressed by the authors to avoid any potential confusion. Perhaps the best course of action would be to fit their model to Mizrahi's data, should this data be available, and see if, when constrained by empirical observation, the model still produces drift in piriform. If so, this would dramatically strengthen the paper. If this is not feasible, then I suggest being very explicit about this difference between the behavior of the model and what has been shown empirically. I appreciate that in the data there is modest drift (e.g., Shani-Narkiss' Figure 8C), but the changes reported there really are modest compared to what is exhibited by the model. A compromise would be to simply apply these metrics to the model and match the model's similarity to the Shani-Narkiss data. Then the authors could ask what effect this has on drift in piriform.

The risk here is that people will conclude from this paper that drift in piriform may simply be inherited from instability in the bulb. This view is inconsistent with what has been documented empirically, and so great care is warranted to avoid conveying that impression to the community.

We thank the reviewer for highlighting this important issue. We agree that the interpretation of our model requires care to avoid implying that the olfactory bulb exhibits spontaneous drift. As the reviewer points out, the empirical literature shows that M/T-cell tuning is highly stable for infrequently experienced odors, but can change with daily, persistent odor exposure (e.g., Kato et al., 2012; Yamada et al., 2017).

We thank the reviewer for highlighting the Bhalla and Bower paper, as it is foundational and actually raises a number of interesting and important points. As the authors noted, there was significant variability in trial-to-trial responses over sessions and days in single neurons. This is likely due to on-going dynamics (Laurent, 1999), the impact of behaviorally relevant top-down feedback (Chen and Padmanabhan, 2022), decision making (Kay and Laurent, 1999), and an array of factors that our model does not include. In that manuscript, the authors note “the variability of the same neuron recorded over different days…was not statistically different from the within day comparisons.” While these results appear prima facie to be different from our results, there are several reasons why they may not be the case.

First, different metrics are used for measuring neuronal stability, which may contribute to some of the differences. Second, and perhaps more importantly and interestingly, the authors in that study noted the significant trial-to-trial variability within day, which is not present in our study because our model has none of the richness of behavior that Bhalla and Bower found in the freely behaving rat. This variability within day (which is much higher than what we report) would reduce the impact of drift across days - a result that would complicate how plasticity across multiple timescales occurs. We thank the reviewer for the insights on this critical study and include these points in our discussion (line 321-330).

Neural responses to odor representations are incredibly variable across different time scales (Padmanabhan and Urban 2010, Angelo et al 2011, Kapoor and Urban 2006, Friedrich and Laurent, 2001, Smear et al 2011, Wesson et al 2008). In our model, none of this selection of survival related to behavior is included, nor are there specific rules about which synapses may be preferentially strengthened (due to neuro modulation corresponding to behavioral choice and reinforcement learning). Instead, we aimed to recapitulate the experimental design of a few studies (Kato et al 2012, Yamada et al, 2017) to understand how neurogenesis and drift are related. Over the simulated 10 days, the odor is presented every day, and the network is otherwise frozen between sessions—meaning the model lacks mechanisms that would normally support recovery during intervals without odor exposure. Under these conditions, adult neurogenesis effectively interacts with repeated experience, producing gradual changes in individual M/T-cell tuning. Thus, our results should be interpreted as modeling experience dependent changes over the timescale of neurogenesis, not as evidence for spontaneous drift in the bulb. We now state this explicitly in the Discussion to prevent confusion and expand the discussion to incorporate some of these critical ideas (line 321-330).

Major comments (all related to the above point)

(1) Lines 146-168: The authors find in their model that "individual M/T cells changed their responses to the same odor across days due to adult-neurogenesis, with some cells decreasing the firing rate responses (Fig.2A1 top) while other cells increased the magnitude of their responses (Fig. 2A2 bottom, Fig. S2)" they also report a significant decrease in the "full ensemble correlation" in their model over time. They claim that these changes in individual cell tuning are "similar to what has been observed by others using calcium imaging of M/T cell activity (Kato et al., 2012 and Yamada et al., 2017)" and that the decrease in full ensemble correlation is "consistent with experimental observations (Yamada et al., 2017)." However, the conditions of the Kato and Yamada experiments that demonstrate response change are not comparable here, as odors were presented daily to the animals in these experiments. Therefore, the changes in odor tuning found in the Kato and Yamada papers (Kato Figure 4D; Yamada Figure 3E) are a function of accumulated experience with odor. This distinction is crucial because experience-induced changes reflect an underlying learning process, whereas changes that simply accumulate over time are more consistent with drift. The conditions of their model are more similar to those employed in other experiments described in Kato et al. 2012 (Figure 6C) as well as Shani-Narkiss et al. (2023), in which bulb tuning is measured not as a function of intervening experience, but rather as a function of time (Kato's "recovery" experiment). What is found in Kato is that even across two months, the tuning of individual mitral cells is stable. What alters tuning is experience with odor, the core finding of both the Kato et al., 2012 paper and also Yamada et al., 2017. It is crucial that this is clarified in the text.

We thank the reviewer. As the issue raised here is related to the previous comment, we have clarified this in the revised text to avoid any misleading comparison and specify what aspects of our computational model map onto experimental studies and what aspects we cannot recapitulate and as a result, the places where our comparisons are limited.

(2) The authors show that in a reduced-space correlation metric, the correlation of lowdimensional trajectories "remained high across all days"..."consistent with a recent experimental study" (Shani-Narkiss et al., 2023). It is true that in the Shani-Narkiss paper, a consistent low-dimensional response is found across days (t-SNE analysis in Shani-Narkiss Figure 7B). However, the key difference between the Shani-Narkiss data and the results reported here is that Shani-Narkiss also observed relative stability in the native space (Shani-Narkiss Figure 8). They conclude that they "find a relatively stable response of single neurons to odors in either awake or anesthetized states and a relatively stable representation of odors by the MC population as a whole (Figures 6-8; Bhalla and Bower, 1997)." This should be better clarified in the text.

We agree with the reviewer that some of the cells in Shani-Narkiss Figure 8B showed relatively stable responses (while others did not). However, there is a clear monotonic increase in the “Average differences” over time, from “Same day” to “1 month” to “6 month”, as quantified in their Figure 8B. Although the author concluded that they "find a relatively stable response of single neurons”, we would argue that their data also provided evidence for what we would term “relatively unstable responses” as found in our model. But per reviewer’s suggestion, we better clarify it in the text now (line 194197).

(3) In the discussion, the authors state that "In the MOB, individual M/T cells exhibited variable odor responses akin to gain control, altering their firing rate magnitudes over time. This is consistent with earlier experimental studies using calcium-imaging." (L3146). Again, I disagree that these data are consistent with what has been published thus far. Changes in gain would have resulted in increased variability across days in the Bhalla data. Moreover, changes in gain would be captured by Kato's change index ("To quantify the changes in mitral cell responses, we calculated the change index (CI) for each responsive mitral cell-odor pair on each trial (trial X) of a given day as (response on trial X - the initial response on day 1)/(response on trial X + the initial response on day 1). Thus, CI ranges from −1 to 1, where a value of −1 represents a complete loss of response, 1 represents the emergence of a new response, and 0 represents no change." Kato et al.). This index will capture changes in gain. However, as shown in Figure 4D (red traces), Figure 6C (Recovery and Odor set B during odor set A experience and vice versa), the change index is either zero or near zero. If the authors wish to claim that their model is consistent with these data, they should also compute Kato's change index for M/T odor-cell pairs in their model and show that it also remains at 0 over time, absent experience.

We appreciate the reviewer’s suggestion and edited the text to make it more accurate (line 319-320).

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

(1) Line 28 "a graduate alteration in sensory perception". We do not know if drift results in changes in perception. If anything, behavioral evidence suggests that perception remains stable in spite of drift. For example, in Driscoll et al. (2017) mice are able to successfully navigate a virtual T maze despite drift, and in Schoonover et al. (2021), mice maintain aversive responses following fear conditioning, despite drift in the piriform. Finally, spatial navigation appears unimpaired despite pronounced drift in the hippocampus (e.g., Climer et al., 2025). It would be more appropriate to say "stimulusevoked activity patterns" than "sensory perception" or other words that refer to neuronal activity rather than cognition or behavior.

We edited the text to make it more accurate per the reviewer’s suggestion (line 27).

(2) In the introduction, the authors state: "This representational drift has led to the hypothesis that PCx, rather than being a primary sensory area, may be more like an association cortical region." (L76-78). However, the hypothesis that PCx operates as an association cortex comes originally from Haberly's work and thinking (e.g., Haberly and Bower, 1984, elaborated in extensive detail in Haberly, 2001). I think it would be appropriate to acknowledge that here.

We added the references to make acknowledge that per the reviewer’s suggestion (line 77).

(3) In the methods, the authors elegantly describe how they induce neurogenesis in their model using weight reshuffling (L805-814). I think it could really help the reader understand the model if this idea were also included in the results section. As the results section currently reads, it seems as if their model implemented neurogenesis in a different fashion: "To do this, following elimination of 10% of the GCs in the network, we added new cells and randomly assigned synaptic weights between these abGCs and M/Ts". I appreciate that in their model, shuffling all the weights of a given GC randomly is akin to "elimination", but I feel like at first blush the results section risks giving an impression a bit different than that actually used in the model.

We edited the text to make it more accurate per the reviewer’s suggestion (line 110-112).

Author response:

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

Reviewer #1 (Public review):

This work develops a simple, rapid, low-cost methodology for assembling combinatorially complete microbial consortia using basic laboratory equipment. The motivation behind this work is to make the study of microbial community interactions more accessible to laboratories that lack specialized equipment such as robotic liquid handlers or microfluidic devices. The method was tested on a library of Pseudomonas aeruginosa strains to demonstrate its practicality and effectiveness. It provided a means to explore the complex functional interactions within microbial communities and identify optimal consortia for specific functions, such as biomass production.

The primary strength of this manuscript lies in its accessibility and practicality. The method proposed by the authors allows any laboratory with standard equipment, such as multichannel pipettes and 96-well plates, to readily construct all possible combinations of microbial consortia from a given set of species. This greatly enhances access to full factorial designs, which were previously limited to labs with advanced technology.

Another strength of the manuscript is the measurement and analysis of the biomass of all possible combinations of 8 strains of P. aeruginosa. This analysis provides a concrete example of how the authors' new methodology can be used to identify the best-performing communities and map pairwise and higher-order functional interactions.

Notably, the authors do exceptionally well in providing a thorough description of the methodology, including detailed protocols and an R script for customizing the method to different experimental needs. This enhances the reproducibility and adaptability of the methodology, making it a valuable resource for researchers wishing to adopt this methodology.

We thank the reviewer for their thoughtful comments and positive assessment of our work. Below we detail the changes we have introduced in the manuscript to clarify issues raised by the reviewer.

While the methodology is robust and well-presented, there are some limitations that should be acknowledged more thoroughly. First, the method's scalability is an important factor. The authors indicate that it should be effective for up to 10-12 species, but there is no discussion of what sets this scale: time, amount of labor, consumables, the likelihood of error, sample volume, etc.

The 10-12 species estimation is based on our own experience implementing the protocol, and set primarily by time, labor, and consumables (as rightly pointed out by the reviewer) rather than conceptual limitations of the approach. We have added clarifications in the Discussion (lines 401-405) regarding these scalability-limiting factors.

Second, this methodology is tailored to construct communities where the abundance of each strain is identical in each combination. Therefore, combinations with a different number of strains also differ in the total initial amount of microbial cells. Second, variations in the initial proportions of the same set of strains cannot be readily explored.

Note that the “density homogenization” step is optional and it could be skipped entirely, which would result in a same species being present at variable densities across consortia: specifically, skipping this step would make the density of a species in a consortium inversely proportional to the number of species in that consortium. Further variations in initial abundance could be explored by treating a same strain at two (or more) starting abundances as distinct inputs of the protocol – though this would naturally increase the number of combinations to test.

We have included a paragraph in the Discussion (lines 416-423) describing how we can, in principle, extend our protocol to explore abundance effects.

Third, the manuscript only discusses how to construct the combinations, and not how to assay them afterward (e.g. for community function, interspecific interactions, etc.). While details on how to achieve these goals are clearly outside the scope of this work, the use of biomass as an example function may obfuscate this caveat, which should be stated more explicitly.

We agree that the manuscript focuses exclusively on the construction of microbial communities and does not address how these communities should be assayed afterward. This is an intentional scope decision. The proposed protocol is fully compatible with a wide range of functional, interaction-based, or omics-based assays. Absorbance is mentioned as an illustrative example of a possible readout, rather than as a recommended or exclusive parameter. We have revised the text to explicitly state that the assessment of community function or interspecific interactions lies outside the scope of this work and must be tailored to the specific biological question being addressed.

Reviewer #1 (Recommendations for the authors):

A few specific technical notes and notes about clarity:

(1) It may be worth being more explicit about how to produce replicates. For example, producing technical replicates by inoculating multiple times from the same set of combinations, while biological replicates require making the combinations multiple times.

We have updated the main text to clarify this point (line 780-781).

(2) Figure 2C: May be worth adding some context to these performance numbers. What are typical accuracies? What would they be in a liquid handler?

Assessing typical accuracies is nuanced since the error depends not only on the assembly steps, but also on potential intrinsic variation of the specific community function being tested and the method used to quantify it. One of the main reasons for including the experiment using colorant combinations was precisely to minimize these other sources of variation. In this experiment, we find that the error we quantify is consistent with cumulative pipetting variation (as a reference, a typical lab micropipette has an error of 0.5-1%). This is now explicitly mentioned in the manuscript.

(3) Figure 5A: I realize it is unlikely that strains go extinct in these experiments. But it is still worth clarifying that the number of strains is the number inoculated, rather than the one present at the time of measurement.

We updated the caption of Figure 5A as recommended by the reviewer.

(4) Figure 5B: I realize this is just for illustration purposes, but you should provide more information about the magnitude of the difference in performance of these combinations and the confidence in their ranking (or variability in performance across replicates).

Following this suggestion, we have added a paragraph where we report the variation across replicates for the highest-performing consortia (lines 318-323). Indeed, while variation across replicates is small, it is enough to produce an overlap between the confidence intervals of the function of some of the highest-performing consortia. This is now explicitly acknowledged in the manuscript.

(5) Figure 5C: I believe the bold black lines indicate the combinations shown in panel D, but that is not explicitly stated.

We have updated the caption of Figure 5C.

Reviewer #2 (Public review):

A simple and effective method for combinatorial assembly of microbes in synthetic communities of <12 species.

Overall, this manuscript is a useful contribution. The efficiency of the method and clarity of the presentation is a strength. It is well-written and easy to follow. The figures are great, the pedagogical narrative is crisp. I can imagine the method being used in lots of other contexts too.

The authors could better clarify what HOIs mean. They could address challenges with assaying community function. However, neither of these “weaknesses” affects the primary goal of the paper which is methodological.

We thank the reviewer for the positive assessment. With respect to HOIs, we recognize that defining and quantifying them is a non-trivial subject within the broader field of microbial ecology (see e.g. ref. 24 within the manuscript). Since our aim with this manuscript is methodological, as the reviewer notes, here we have done our best to avoid introducing new or ambiguous definitions. For this reason, we simply adopt a definition given in previous works (including refs. 10, 19, 24, 29, 37, and 38 in the manuscript), where the context-dependence of pairwise interaction terms is taken as a signature of HOIs. With respect to the challenges in assaying community function, please see our responses below.

Reviewer #2 (Recommendations for the authors):

Overall, this manuscript is a useful contribution, I appreciate the authors taking the time to write it up! I have a few relatively minor comments.

(1) It would be nice in the introduction to address why we might want the full factorial construction of communities in the first place. This is an especially relevant question in light of the authors' 2023 Nat E&E paper where they showed that the function of communities can often be learned even when only a fraction of all possible communities is measured. This is addressed in part in the paragraph on line 34, but I think it might be worth expanding a bit given the focus on the paper.

We sincerely appreciate the reviewer’s feedback. In fact, one of the reasons that make full factorial construction desirable is precisely to test theoretical and computational models of community function, including (but not only) the statistical models developed in our 2023 Nature E&E paper. In that work, we showed that low-order models can explain a substantial fraction of the variation in community function in previously-published datasets, but we also predict that the same models could fail under complex structures of microbial interactions (e.g., strong high-order interactions). The protocol we present here enables the empirical quantification of such interactions, making this prediction (and others) directly testable. We have included that clarification in the revised manuscript (lines 56-58).

(2) Around line 74, I think it is worth mentioning that even this elegant design will face insurmountable practical challenges (time, liquid handling operations, number of plates will explode) for full factorial design with 20, 30, 40 species or more. This is relevant for some very complex synthetic consortia that some microbiome groups are constructing (e.g. hCom2 from Huang/Fishbach groups) https://www.sciencedirect.com/science/article/pii/S0092867422009904.

We agree with the reviewer that full factorial designs become impractical for very large species pools. These limits are now more clearly mentioned in the revised manuscript. We refer the reviewer to our response to comment #1 by Reviewer 1 for further details.

(3) The binary construction is a really nice clean way to explain the protocol. Appreciate the pedagogy!

We thank the reviewer for the appreciation.

(4) In the experiment with pseudomonas strains the consortia are grown in LB. This medium will support growth to relatively high OD (>1). At these densities, the change in OD with density is almost certainly not linear with cell density, and this nonlinearity likely depends on strain identity. In this case, the assumption of additivity may not hold. As a result, some of the observed "interactions" may simply be non-linearity in the assay and not the abundance of bacteria in the communities. Of course, this does not affect the assembly protocol in any way, but it does complicate the interpretation of interactions via this assay. I think this is worth pointing out since other researchers may have to think carefully about the assay they use when constructing these synthetic consortia. I think in this methods paper it is important to emphasize this so other researchers do not mistakenly identify interactions due to issues with the assay.

We thank the reviewer for pointing out this important aspect. In our experiment, we use Abs₆₀₀ simply as an example of a measurable community-level function. The reviewer is absolutely correct in that mapping absorbance to biomass is nuanced at large OD values, where this relationship becomes non-linear. While this is not an issue from the perspective of the protocol itself, it is indeed an important consideration for users who may want to obtain reliable quantifications of biomass. We have updated the manuscript to explicitly mention this potential issue (lines 307-313). We have also emphasized the fact that our focus on Abs₆₀₀ is strictly for illustrative purposes, and we have removed all instances where a direct mapping from Abs₆₀₀ to biomass was implied in the text.

(5) Subtle point regarding HOIs. HOI (or pairwise) statistical interactions need not quantitatively be the same as interactions in a lotka volterra sense. I realize the authors do not explicitly use the term "interaction" in an gLV model formalism but this is how the majority of readers will interpret this term. I believe it is a research question as to how pairwise gLV interactions manifest themselves in terms of functional interactions. For example, a purely pairwise LV model could easily have HOI "functional interactions" if the function is total abundance since abundances depend nonlinearly on LV interactions. I think this part of the manuscript could be confusing to readers for this reason. I think the term "functional interaction" really helps with this issue, but just asking the authors to make sure this is clear.

I say this because ref: 37 is focused on HOIs in an LV sense. Here, as the authors are aware, they are computing statistical "interactions" in the sense of epistasis. Given that they are computing this epistasis averaged across all community compositions a more appropriate citation might be [https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1004771] where the same quantity is computed in a protein context.

We thank the reviewer for pointing out this important issue. Indeed, we use the term “interaction” in a statistical sense (as the deviation of the observed community function from a null, additive expectation) rather than in a Lotka-Volterra sense. We agree that the reference suggested by the reviewer is more appropriate in this context. We have updated the reference list accordingly.

(6) Figure 5G - a little hard to see. Any way to show this data more clearly? It looks like all interactions have a mean of 0 because of the way the data are presented.

The reviewer is indeed correct in that, as defined, the interactions that we quantify are back ground dependent, and their average across backgrounds lies near zero for all species. More than an issue with the representation, we think that this is an important empirical observation: it indicates that a same species pair may interact positively or negatively depending on its ecological context. We believe that the current representation is most appropriate for making this clear, but we would be open to discussing alternatives if the reviewer had a specific suggestion in mind.

Reviewer #3 (Public review):

The authors developed a useful methodology for generating all combinations of multiple reagents using standard lab equipment. This methodology has clear uses for studying microbial ecology as they demonstrated. The methodology will likely be useful for other types of experiments that require exhaustive testing of all possible combinations of a given set of reagents (e.g., drug-drug antagonism and synergy).

The authors provided a useful R script that generates a detailed experimental protocol for building the desired combination from any number of reagents. The produced document is useful and has clear instructions. The output of the computer script will be strengthened if graphical output is also provided (similar to the one provided in Figure 1C).

The authors show that the error rate of the method doesn't go up with the number of combinations using dyes (Figure 2).

The authors demonstrate the value of their methodology for studying interactions within microbial consortia by assembling all possible combinations of eight strains of Pseudomonas aeruginosa. The value of their methodology for this application is well-founded. However, it is also unclear why specific experimental choices were made for this application. It is unclear why authors continue to show the absorbance measurements of strain assemblies over the entire wavelength spectrum and not just for ABS 600 nm (Figures 3 and 4). It is also unclear why the authors provided information on the "sum of the three spectra" as this reference line is meaningless and not a reasonable null model for estimating how well specific strain combinations will grow together.

Figure 5 illustrates the various analysis types that can be performed on the data collected from growing combinations of eight Pseudomonas aeruginosa strains. It is a very informative figure since it provides a "roadmap" on the various ways in which the dataset produced can be explored. The information in Figures 5 and S6 will likely be very useful for a wide audience.

Reviewer #3 (Recommendations for the authors):

(1) Congratulations. I think the manuscript lays out a simple and very elegant methodology that will be useful for many. While I think the method is overall well explained and rationalized, the paper can greatly benefit from further expansion of Figure 5 at the expense of Figures 3 and 4.

We thank the reviewer for their thoughtful assessment of our work. We have considered the recommendations and discuss the following points in response.

(2) Unless I am missing something, there is no reason to present data collected across the entire wavelength spectrum for microbial assemblies (Figures 3 and 4). Moreover, using the same color palette for bacterial strains (Figure 3A) and colorants (Figure 2) is highly confusing. I suggest considering using only the 600 nm wavelength for any data collected from microbial assemblies and using a very different color palette for bacteria and colorants to avoid misinterpretation of the data.

We thank the reviewer for this suggestion. Our goal with Figures 3-4 was to illustrate the convenience of the protocol and the ease with which many measurements can be performed in parallel once the combinatorial assembly has been completed. While we focus on Abs₆₀₀ for all subsequent analyses, we chose to display the full spectra in Figs. 3-4 in hopes that future studies can make use of our rich dataset to interrogate questions on microbial interactions, with the option to focus on other wavelengths (which can effectively be treated as different community-level functions in their own right; for instance, we have previously used Abs₄₀₅ as a proxy for siderophore concentration). We think there is value in Figs. 3-4 in their current form to make this clear to readers.

(3) Unlike dye absorbance, bacterial carrying capacity has an upper limit, so summing individual population absorbance as a reference line seems unjustified. If the summation of absorbance is meant to provide a "null model" for expected growth, a more suitable model should be considered (e.g., max spectra or a weighted sum of the spectra from individual members).

We agree with the reviewer that our null model is not biologically constrained, and we did not intend to imply that the additive expectation was derived from biological principles. Instead, this additive expectation should be interpreted as a simple statistical baseline with minimal assumptions. The use of an additive baseline for quantifying microbial interactions has been addressed in the literature (see, e.g., references 10, 19, 24, 29, 37, and 38), and so here we chose to conform to this convention to avoid introducing new, non-standard quantifications of pairwise and higher-order interactions. We have revised the text to make this more explicit.

(4) The R script is a valuable tool. I think that a valuable improvement will be to also generate visual representations as part of the script’s output such as the colored plates in Figure 1C that are specific to the generated protocol.

We have updated the script so that it now also outputs a table specifying the location of each consortium within the plates. We chose to make this a text, rather than a graphics output, to ensure cross-device compatibility.

(5) The discussion rightly acknowledges the potential to extend the protocol to larger libraries using liquid handlers. To facilitate this implementation, it might be beneficial to modify the script output so that the ‘volume’, ‘plate’, and ‘column’ values are tab- or comma-delimited.

We thank the reviewer for the suggestion. We have modified the output so that it is now tab-delimited.

(6) Figures 3 and 4 do not provide a lot of insight. I would suggest combining them into a single figure and using only absorbance values at 600 nm. It would also be interesting to add a histogram of these absorbance values and possibly show histograms for subgroups (e.g. all assemblies with more than 3 strains vs all assemblies with 3 or fewer strains).

With respect to Figs. 3 and 4, we refer the reviewer to our response to comment #2. With respect to the histogram/subgroups plot, we understand that this would be a slightly modified version of the current Fig. 5A, where we show means and standard deviations across all subgroups of 1 to 8 species, and so we find it unclear what this figure would add.

(7) With the recommendations of removing or reworking Figures 3 and 4, and the fact that Figure 5 is data-rich (and extremely useful), it would be beneficial to split Figure 5 and include the data shown in Figure S6 in the main figure. The analysis in Figure 6S is valuable and it might be beneficial to elevate this analysis to a primary figure and provide a detailed explanation of its rationale and methods in the main text.

We appreciate this suggestion. In our view, we find that both the text and the figures benefit from a heavy focus on the assembly protocol, as this is the main contribution of this work. While we do think it is valuable to highlight the type and amount of data that can be collected with a full factorial assembly, as well as the types of analyses that can be performed with this data, we are afraid that allocating more space to these analyses may distract readers from the methodology itself. We have therefore chosen to keep the original structure for Figs. 5 and S6.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Here, Pinto and colleagues set out to investigate whether the cow udder is a potential mixing site for the influenza virus. The authors have demonstrated that bovine mammary epithelial cells can be infected with both avian and human influenza A viruses, supporting the idea that the cow udder may be a potential site for reassortment. Furthermore, they demonstrate that the bovine-adapted IAV replicates to similar titers in avian epithelial cells when compared to an AIV precursor virus. Thus, suggesting there is no fitness trade-off, and confirms the potential for spill-back of the cattle B3.13 into poultry, which has already been observed. Overall, I believe the authors achieved their aims. However, there are instances in which the results do not entirely support the conclusions (noted in weaknesses). Given the ongoing questions surrounding highly pathogenic avian influenza A virus in dairy cows, this work provides valuable evidence for the potential of the cow udder as a site of reassortment. These findings highlight the need for surveillance of influenza A virus incursions into livestock species, particularly cows. Some specific strengths and questions regarding weaknesses have been outlined below.

Strengths:

(1) The authors use a diverse range of cell types and influenza A virus strains, as well as a wide range of techniques to address the questions at hand.

(2) The use of cells from multiple bovine breeds for the MAC-T, bMEC and explants suggests the phenomenon is not unique to a single breed.

(3) The results suggesting there is no fitness trade-off for Cattle Texas in an avian host are interesting, and confirm the potential for spill-back of the cattle B3.13 into poultry, which has been observed.

Weaknesses:

I have listed my complete questions/concerns below. However, there are two main weaknesses of the article in its current state. Firstly, there is no apples-to-apples comparison in terms of determining a preference for IAV to infect the cow udder over other organs (Q4). The mammary gland and respiratory tract are represented by epithelial cells, but for other organs, fibroblasts were chosen. I think the fairer comparison would be to compare epithelial cells from different organs to demonstrate a preference for the mammary gland. Secondly, the main premise of the article relies on bMEC and MAC-T (primary and immortalised mammary epithelial cells), facilitating higher viral growth than the cells from other organs. Yet throughout the article, a 10x higher dose of IAV is used in the bMEC cells compared to everything else (Q6). This raises the question of how much of the results are due to a preference for the mammary epithelial cells, and how much is simply due to the increased dose.

When we set out to test if cow mammary gland cells were particularly susceptible to IAV infection compared to other bovine cell types, we used what was available in the Roslin Institute in the first instance – a mix of primary and continuous cells from various anatomical sites: three epithelial cell types (two mammary, one respiratory tract) two immune cell types and four sets of fibroblasts from various organs. Given the representation of different anatomical sites, cell types and differentiation statuses, we considered this a suitably diverse panel with which to characterise infection dynamics of a broad range of IAVs, before more focussed investigations using the mammary bMEC and explant tissues. Both mammary epithelial cell types grew our library of influenza challenge strains significantly better than the BAT-II respiratory epithelial cells, as well as the two immune cell types and all four fibroblast populations. Of the fibroblast cells, those derived from the brain grew IAV significantly better than the skin and turbinate fibroblasts, while blood-derived macrophages grew virus significantly better than the lymphocytes and non-brain fibroblasts. Therefore, there are “apple to apple” comparisons as well as apple to pear comparisons that give significant differences. We therefore think that our conclusions (in the abstract) that mammary cells are particularly replication competent for IAV, (at the end of the introduction) that “a wide range of cow-derived cells are susceptible” and that (in the results section) that “mammary cells showed the highest susceptibility” are entirely justifiable. We do not claim that mammary cells are the only permissive bovine cells, but our evidence suggests they are highly susceptible.

We used a higher MOI for bMECs because test experiments with WT PR8 and the Cattle Texas 6:2 reassortant showed that MOI 0.01 infections gave more variable results than ones run at MOI 0.1, perhaps because of the intrinsic variability of mixed primary cell populations. We therefore chose to go with the higher MOI. However, the end-point titres between the two conditions were not significantly different, so we do not think this choice is a confounding issue. We will add the comparison of the two MOIs as a supplementary figure in the formal revision.

Reviewer #2 (Public review):

The authors use a library of influenza A viruses from different strains, classified in lab-adapted, human, avian, and swine according to the animal from which they were isolated. They propose that the cow mammary gland serves as a mixing vessel for influenza A viruses. As a first approach, the authors assess susceptibility to infection across different cell types, including continuous and primary cell lines, bovine mammary cells, and mammary explants. All these cells support polymerase activity. Then, they analyzed changes in the bovine virus's viral fitness relative to an avian precursor. The authors use single-gene replacement to study whether and which RNP segments improve viral transcription. As part of this section, they also test IFN-specific antagonism by NS1 to assess the input of segment 8. Quantitative glycomic analysis was performed on the continuous bovine mammary cell line to demonstrate the presence of both a2,3 and a2,6, which is consistent with their observation that these cells can be co-infected with human and avian IAVs simultaneously. The main question, however, is: what is the glycome in the explants, or directly from tissues?

We report quantitative glycomics for the primary bovine mammary epithelial cells as well as the continuous line the referee highlights. However, we agree with R2 that a detailed glycomic analysis of primary bovine mammary tissue would allow a better understanding of the actual glycosylation status in vivo. This has now been undertaken by the authors and is available as a bioRxiv preprint:

Bovine H5N1 influenza viruses have adapted to more efficiently use receptors abundant in cattle

Jack A. Hassard, Jiayun Yang, Bernadeta Dadonaite, Jonathan E.Pekar, Jin Yu, Samuel A. S. Richardson, Rute M. Pinto, Kristel Ramirez Valdez, Philippe Lemey, Jessica L. Quantrill, JinghanXue, Tereza Masonou, Katie-Marie Case, Jila Ajeian, Maximillian N. J. Woodall, Rebecca A. Ross, Nicolas Hudson, Kan Zhong, Hongzhi Cao, Samuel Jones, Hannah J. Klim, Brian R. Wasik, Desi N. Dermawan, Jean-Remy Sadeyen, Dirk Werling, DylanYaffy, Joe James, Alessandro Nunez, Paul Digard, Ian H. Brown, Daniel H. Goldhill, Pablo R. Murcia, Claire M. Smith, Yan Liu, Jesse D. Bloom, Munir Iqbal, Wendy S. Barclay, Stuart M.Haslam, Thomas P. Peacock: bioRxiv 2026.04.02.715584; doi:https://doi.org/10.64898/2026.04.02.715584

Overall, the manuscript is clearly written and provides new insights into the behaviour of the cattle isolate, now compared with a representative group of model or precursor HAs of different origins.

It would be great if a consistent nomenclature for the IAV strains could be used in the study. There is a mix of origin (Texas), animal from which the virus was isolated (mallard), or abbreviations that do not follow guidelines (IAV07). Are the USSR and Udorn not lab-adapted?

We chose the abbreviated names for a variety of reasons. Partly from common usage (e.g. PR8, Udorn), partly for consistency with other already published papers from the FluTrailMap consortia (e.g. Cattle Texas; Dholakia et al 2026), partly to make diversity obvious in certain figures (e.g. H3N1, H5N2 etc) and partly to avoid confusion between viruses that originate from the same geographic area (e.g. AIV07, AIV09, H5N8-20 etc which are all Ck/England/isolate numbers). Overall, we found it more confusing to use the expanded nomenclature. Re AIV07 which the referee criticises for not following naming guidelines – if this is a reference to the EURL nomenclature, AIV07 is the abbreviation for the specific virus A/Chicken/England/053052/2021, our representative virus for EURL genotype EA-2020-C, as we say in the text. We should however have included this nomenclature in Table 1, which otherwise provides a cross-reference for all the names. This will be added in the formal revision to help with clarity.

As to whether USSR and Udorn are lab adapted – that depends on definitions. There is a continuum of adaptive changes and/or sequence drift starting from the very first growth of an isolate in the laboratory. The viruses we define here as lab adapted are ones that have been deliberately adapted to other hosts or which have very long passage histories in multiple host species resulting in known functionally significant changes. For example, PR8, with 100s of passages in mice, ferrets and embryonated hens eggs (doi: 10.3390/v12060590), makes it unarguably lab-adapted. We admit that A/USSR/77 and A/Udorn/307/1972 are probably further along this adaptive pathway than more recent isolates such as A/Norway/3433/2018, but are unaware of any specific reason that would put them into our lab adapted category.

The experimental setup includes bovine mammary primary and continuous cells, as well as mammary explants. Some of the most significant differences, for example, in viral fitness studies and co-infection experiments, are observed in these explants. Perhaps there could be some additional focus on this observation. The implications in comparison to the results obtained in cultured cells could be described. How will the human and other HA subtype viruses fare in the explants?

We agree that this is an important and interesting question, and have tested the strains we used for co-infections, human seasonal H1N1 “Norway” and low pathogenic avian influenza “H3N1”, in the mammary explants. Both replicate, the avian virus to 20-fold higher titres. We will add this new information to the revised manuscript.

Reviewer #3 (Public review):

Summary:

This excellent manuscript by Pinto, Sharp, and colleagues examines bovine tissue tropism for influenza viruses. They find that bovine flu, as well as other strains, has strong replication in mammary tissue. They also map the genetic changes to influenza that improve replication in bovine cells. Overall, the study is well designed and executed, and the results are very timely.

Strengths:

(1) The experiments are well-controlled.

(2) The figures are well-constructed and easy to follow.

(3) The Methods and legends are detailed, with sufficient information.

Weaknesses:

(1) A comparison to human cells would strengthen the overall impact of the results. Are human mammary cells also uniquely susceptible to influenza? Are bovine mammary cells special in some way?

This is an interesting question but we have not tested mammary gland cells from humans (or any other species of mammal), but we have reported elsewhere (Dholakia et al., Nat Commun. 2026 Jan 16;17(1):1603. doi: 10.1038/s41467-026-68306-6.) that Cattle Texas grows well in a variety of human respiratory cells. Here we are considering the bovine mammary organ as a potential reassortment site for IAVs; human mammary organs are unlikely to create this opportunity.

(2) For the virus infection studies with segment 8 swaps, it should at least be noted that some of the phenotypes could be driven by NEP.

We agree, and will change the text to acknowledge this in a revised version.

(3) The data demonstrating that bMEC can support co-infection are compelling and important, but would be strengthened with a comparison from a different cell type or species. Do mammary cells uniquely support higher co-infection?

We have data showing that co-infection also occurs in the continuous MAC-T udder cell line and will include these data in a revision. We have not tested bovine cells from other organs for co-infection potential as they do not seem to be significant sites of infection in vivo.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In their manuscript, Andriani et al. show intracellular zinc is exported from sperm during capacitation and suppresses the alkalinization-induced hyperpolarization in sperm. Intracellular zinc inhibits Slo3 current, which is enhanced by the co-expression of gamma subunit Lrrc52. Computational studies reveal that the Zn binding site on mSlo3 is located near E169 and E205, which are involved in the sustained zinc inhibition of mSlo3 current. The authors propose that intracellular zinc plays a key role in sperm capacitation by inhibiting the Slo3 channel.

Strengths:

Overall, the work appears well-designed (e.g., oocyte patch-clamp experiments), and clearly presented. Three-dimensional structural modeling and flooding simulations are executed.

Weaknesses:

The simple mutagenesis analysis of E169 and E205 showed partial abolishment, but the molecular mechanism by which zinc inhibits Slo3 current is not yet fully shown. The authors should consider performing more extensive experiments, such as creating double mutants or combination mutants involving other residues. Additionally, could other mechanisms explain the role of zinc in regulating the Slo3 current?

We thank the reviewer’s thoughtful comments regarding the mutagenesis analysis and the possible mechanisms underlying zinc regulation of Slo3. Regarding the suggestion to perform double or combination mutants, we agree that such experiments would provide valuable mechanistic insight. However, due to limited resources, we were not able to perform these additional experiments within the scope of this study. Our current results show that mutations at E169 and E205 partially abolish zinc inhibition, which suggests that the inhibitory mechanism is not mediated through a single residue and is likely more complex.

Alternative mechanisms that may contribute to zinc modulation of Slo3 include indirect effects through modulation of nearby charged residues, structural rearrangements influenced by zinc binding, or the presence of multiple zinc binding sites within Slo3 channel other than the sites discovered through this study. At present, these mechanisms remain speculative and further studies will be required to clarify their contributions. This study provides the foundational basis for understanding how zinc inhibits the Slo3 channel and serves as an important starting point for defining the molecular mechanism in more detail.

We already acknowledged in the Discussion section that the precise molecular basis of zinc inhibition remains unknown and that future work involving more extensive mutational and structural analyses will be essential to fully resolve this issue.

We also added the discussion section as follows:

“It is worth noting that the incomplete loss of zinc sensitivity in these mutants suggests that additional mechanisms may participate in zinc modulation of Slo3. These may include modulation of nearby charged residues, structural rearrangements influenced by zinc binding, or the presence of multiple zinc binding sites. Comparisons with Slo2.2 (J. Zhang et al., 2023), KCNQ4 (Gao et al., 2017), and voltage-gated calcium channels (Sun et al., 2007) further support the possibility of diverse molecular determinants for zinc inhibition. Our VCF, mutagenesis, and simulation data together indicate that zinc influences voltage sensor movement in mSlo3, which may suggest a distinct inhibitory mechanism that warrants further investigation.”

While elucidating the mechanism of Slo3 is interesting, there is substantial literature indicating how zinc regulates channel functions at a molecular level. Given this, the manuscript should provide a deeper understanding by clearly elucidating the molecular mechanism of the regulation of Slo3 current by zinc.

Thank you for highlighting a very important point that requires deeper discussion and explanation regarding how zinc regulates Slo3 current at the molecular level. As reported, Slo3 is gated by membrane depolarization and, at the same time, this channel is also gated by intracellular pH, particularly alkalinization (Leonetti et al., 2012; Schreiber et al., 1998; X. Zhang et al., 2006). This makes the gating mechanism of this channel complex. The molecular mechanism underlying pH regulation of the Slo3 channel remains unknown (M. D. Lyon et al., 2023). We tested different pH conditions and membrane voltage to elucidate the effect of zinc on the Slo3 channel. Our data suggests that zinc inhibition in mSlo3 channels is dependent on pH (Fig. 2A-E), voltage (Fig. 2G-H; Fig.2—figure supplement 1A, B) and exhibits a long-lasting inhibitory effect (Fig. 2I, K).

However, as much as we are aware that these data alone cannot explain the molecular mechanisms of zinc’s effect on Slo3 current, our mutagenesis experiments also did not provide a straightforward answer. The single amino acid mutations examined in this study, which contain clustered negative residues, did not significantly alter zinc-mediated current reduction compared to the wild type. As the reviewer pointed out, mutating one single amino acid may not be sufficient to fully identify other contributing residues within the predicted mSlo3 zinc-binding site. Therefore, more extensive mutagenesis studies will be required to fully elucidate the molecular mechanism of zinc inhibition in mSlo3, which could not be fully understood in this study.

On the other hand, when we analyzed the percentage of current recovery of all the mutants, E169A and E205A showed significant current recovery upon the wash-out by pH 8.0 alone. Consistent with MD simulations, our electrophysiological recordings demonstrated that the long-lasting inhibitory effect of zinc was partly abolished by these mutations. Thus, our findings highlight the contribution of E169A, located at the lower end of S3 domain and E205A, located at the lower region of S4 domain, to zinc-mediated inhibition of mSlo3 current.

Additionally, since the molecular mechanism of pH regulation on Slo3 channel remains unknown, the molecular basis of its dual gating has yet to be elucidated, making it difficult to draw a single definitive conclusion from our current research data on how zinc inhibits mSlo3 current. Nevertheless, this study provides the foundation for understanding possible mechanisms of zinc inhibition. Our VCF data suggest that zinc influences the movement of VSD of mSlo3, and together with our mutagenesis and MD simulations results, these findings represent an important first step toward elucidating the molecular mechanism of zinc inhibition of the mSlo3 current.

Intracellular zinc exerts inhibitory effect on mSlo3, similar to what has been reported for Slo2.2 channels (J. Zhang et al., 2023), high- and low-voltage activated calcium channel families (Sun et al., 2007) and KCNQ4 channels (Gao et al., 2017). These studies identified different regions, amino acids, and possible mechanisms of zinc inhibition among these ion channels. For instance, in Slo2.2 channels, which belong to the same Slo family as Slo3, the zinc-binding site was identified in the RCK2 domain, where cysteine and histidine residues form a canonical zinc binding motif (J. Zhang et al., 2023). In KCNQ4 channels, zinc inhibits the channel activity in a non-canonical manner that depends on its physiological activator, the membrane lipid PI(4,5)P₂ (Gao et al., 2017). Although zinc exerts the inhibitory effects on those various voltage-gated potassium and calcium channels, the mechanisms differ. Our data suggests another distinct mechanism of zinc inhibition in the mSlo3 channel with the identified sites located in the VSD, where zinc influences the voltage-sensor motion, and consequently affects the complex gating of Slo3.

We revised the discussion section as follows, which is also related to the previous comment:

“It is worth noting that the incomplete loss of zinc sensitivity in these mutants suggests that additional mechanisms may participate in zinc modulation of Slo3. These may include modulation of nearby charged residues, structural rearrangements influenced by zinc binding, or the presence of multiple zinc binding sites. Comparisons with Slo2.2 (J. Zhang et al., 2023), KCNQ4 (Gao et al., 2017), and voltage-gated calcium channels (Sun et al., 2007) further support the possibility of diverse molecular determinants for zinc inhibition. Our VCF, mutagenesis, and simulation data together indicate that zinc influences voltage sensor movement in mSlo3, which may suggest a distinct inhibitory mechanism that warrants further investigation.”

The manuscript includes no experimental data on the mechanism of intracellular zinc export during sperm capacitation, despite being crucial for the regulation of sperm function.

We thank the reviewers for the valuable comment in this regard. We agree that mechanism of intracellular zinc export during capacitation is crucial for the regulation of sperm function, and it would be an important finding if we could provide the experimental data on this. However, there are significant technical difficulties in performing such experiments. Two protein families facilitate the transport of zinc across cellular and intracellular membranes in opposite directions: ZnT and ZIP. ZIP12 has been reported to be highly expressed in mouse testis (Zhu et al., 2022), as well as ZnT-1 (Elgazar et al., 2005). To date, there are no known inhibitors for zinc transporters, and there is also no suitable antibodies available for these transporters, which makes it difficult to design experiments to examine the intracellular zinc transport during sperm capacitation. Apart from the two reported zinc transporters, the functional significance of other ZnTs and ZIPs, particularly those related to capacitation, remains largely unclear, leaving the mechanisms of zinc transport in sperm during capacitation poorly understood. Moreover. homozygous Znt-1 knockout mice exhibit a lethal phenotype (Andrews et al., 2004).

Reviewer #2 (Public review):

Summary:

In this paper, Andriani and colleagues are examining the potential role of Zn flux in sperm and its effect on Slo3 channels. This is an interesting question that is likely critical to how sperm function properly and Slo3 channels are a possible candidate for a downstream molecule that is impacted by Zn. In this paper, the authors use Zn imaging, sperm motility assays, and electrophysiology to show that Zn flux impacts sperm function. They then go on to look at the impact Zn has on Slo3 current and propose a binding site based on MD simulations. While the ideas are interesting, the experiments are not well described in many places making understanding the results very difficult. In addition, critical controls are missing throughout the paper.

Strengths:

The question of how Zn flux impacts membrane potential and sperm motility is an important one. Moreover, Slo3 presents an interesting candidate or the target of Zn regulation. The combination of methods used here also has the potential to uncover mechanisms of Zn regulation of Slo3.

Weaknesses:

Much of the paper lacks experimental description which makes interpretation quite difficult, or a detailed discussion is missing. Examples include:

(1) Figure 1, particularly the Zn imaging, is not sufficiently described. How is the fluorescence intensity measured? A representative ROI? The whole tail and head? Are the sperm immobile? If not, there is evidence that motion artifacts can significantly distort these sorts of measures from Calcium measurements in Cilia. Were there controls done? Is the small amount of Zn seen in the tail above the background?

We sincerely thank the reviewer for pointing out important details that we should provide in this study in order to make it well understood. We would like to answer and respond to the points raised by reviewer as follows:

Fluorescence intensity is measured by the signal taken from the whole head and the proximal part of tail in sperm. We have included this in the materials and methods.

Materials and Methods

“Fluorescence intensity is measured by the signal taken from the whole head and the proximal part of tail in sperm.”

Yes sperm is immobile during zinc imaging.

We added the control data of zinc imaging without capacitation medium and incorporated the data into the graph in Figure 1B. For the control in non-capacitation medium, we use HS medium as newly explained in the methods, results, related figure (Figure 1B), and figure legends.

Yes the small amount of Zn seen in the tail above the background. As shown in Fig. 1A we confirmed that the signal intensity at the proximal region of the tail was higher than the background. Therefore, the data for this region were calculated after background subtraction.

(2) The second half of Figure 1 is also not well described. What is the extracellular solution in the recordings? When you apply the Zn ionophore, do you expect influx or efflux? I assume efflux is based on the conclusions but this should be discussed explicitly.

The extracellular solution in the recordings for Figure 1 is HS solution (HEPES-buffered saline solution), a standard non-capacitation medium. We will include this information in the materials methods.

Materials and methods

“HS-based solution was used as the extracellular solution.”

We assume that intracellular zinc levels increase upon application of zinc ionophore. Previous work has reported that sperm contain approximately 35.7 ng/10⁶ cells in the head and flagellum (Henkel et al., 1999). When zinc pyrithione is applied, it facilitates the influx of Zn²⁺ from the surrounding medium into the cell, thereby increasing intracellular zinc concentration. Zinc pyrithione functions both as a zinc source and as a transport facilitator, allowing Zn² to cross the otherwise impermeable lipid membrane without compromising membrane integrity.

(3) Figure 2H labels the Y axis, "normalized current". Normalized to what? Why do neither of the curves end at 1? A better description of what this figure represents is needed.

Normalization for figure 2H was performed by dividing the absolute current of mSlo3 at pH 8.0 of each voltage by the absolute current at the pre-determined highest voltage that still produced a stable mSlo3 current (i.e., good patch, good clamp). In this analysis, +140 mV was chosen as the highest voltage for normalization, since in few cells the patch was lost at +160mV and +180mV. Similar to the control condition, the absolute current of mSlo3 in the presence of 100 µM zinc was normalized to the absolute current of the control at +140 mV. This information has been included in the figure legends and the Materials Methods section of the revised manuscript.

Materials Methods section:

Figure legends for figure 2H has been updated.

(4) The alpha fold simulations are not well described. How many Zn binding sites were found? Are all of the histidine mutations in Figure 4 Supplement 1 the ones that were found?

We thank the reviewer for the question. In our AlphaFold3 input, we only input the transmembrane region of the protein. From there, we found four sites located as follows:

Given that we are only interested in the intracellular side of the membrane, we are only interested in the site with the highest pLDDT value (confidence values). On the IC side, there are only two sites, where the other sites are located near the pore domain. The site is near E310 and K319.

Author response image 1.

AlphaFold3 prediction of the Zn binding site on IC side of Slo3

The histidines in Fig. 4—figure supplement 1 are all histidines that are not in the transmembrane region. These residues were not included in the initial inputs for AlphaFold3. However, we conducted MD simulations including these residues and we were able to show that a few of these residues are in contact with Zn. We have now plotted the minimum distance between each of these residues and Zn in the flooding simulations.

Author response image 2.

MD simulations of histidines residues located in IC of Slo3

Minimum distances between histidines in Fig. 4—figure supplement 1 and Zn²⁺ from the flooding simulations. Different colors indicate different repeats.

(5) There is no discussion of physiological intracellular Zn concentration. How much Zn is inside the sperm? How much if likely Free vs buffered? Is 100uM a reasonable physiological concentration?

We estimated the intracellular zinc concentration in sperm based on human sperm data, which report a zinc concentration of approximately 35.7 ng/10⁶ cells in the head and flagellum (Henkel et al., 1999). Considering the volume of a typical human sperm is about 15 µm³ (Laufer et al., 1977), this translates to an estimated intracellular zinc concentration of approximately 400 mM, although the concentration of free zinc must be much lower than this level. Although exact intracellular zinc concentrations in mouse sperm are not well-documented, this estimate supports the observation of elevated zinc in non-capacitated sperm.

There are a number of areas where the interpretation is not well supported by the data including:

(6) You say in the Figure 4 supplement, that "we did not observe any significant decrease in the percentage of current inhibition." But that is a pretty misleading statement. There are large changes (increases) in the amount of zinc inhibition. These might be allosteric changes but I don't think you can safely eliminate these as relevant Zn binding sites. Also, some of these mutations appear to allow at least some unbinding of Zn.

In our MD simulations, H720 is not at the zinc binding site and therefore, mutation to arginine would indeed eliminate its binding. We are showing this in the minimum distance analysis between Zn and H720 and show that they are further than 4 Å from each others (n=3), as shown in author response image 2.

Chimera of Slo3/Slo1 RCK2 also showed large increases in the amount of zinc inhibition, and this might serve as a potential binding site. We agree that the statement: “we did not observe any significant decrease in the percentage of current inhibition.” is misleading, therefore we revised our interpretation and statement into:

We revised the result section as follows:

“However, the percentage of current inhibition varied across the mutated constructs, showing either increases or no appreciable change (Fig. 4—figure supplement 1B, C).”

(7) Following up on the above point, it seems unfair to conclude that the D162S, E169A, and E205 mutants are part of the inhibitory binding site for Zn when the mutation has no effect on inhibition and only an effect on the washout. The mutations on the intracellular side also had an impact on the washout so it seems equally likely that they are the critical residues based on your data.

We thank the reviewer for this important point. We agree that the absence of a strong reduction in the initial zinc inhibition makes it challenging to assign any single residue as a definitive zinc binding site. However, our interpretation is based not only on the electrophysiological data but also on the MD simulations, which consistently identified E169 and E205 as residues that frequently interact with zinc and stabilize zinc occupancy within the VSD region. Although the mutations did not markedly reduce the peak level of zinc inhibition, both E169A and E205A significantly altered the long-lasting inhibitory component during washout, which is consistent with the MD-predicted interactions. In contrast, the intracellular mutations affected washout but were not supported by MD simulations as potential zinc interaction sites. Taken together, these combined datasets support the idea that E169 and E205 contribute to zinc modulation of Slo3 in the VSD, even though additional residues or mechanisms are likely involved.

(8) Nowhere in the paper do you make the specific link between Zn flux and membrane hyperpolarization via Slo3. You show that Zn flux changes the ability of the sperm to hyperpolarize and you show that Slo3 is inhibited by Zn but the connection between the two is not demonstrated. There appears to be a specific Slo3 blocker. If you use this in sperm, do you no longer see the Zn effect?

Thank you for pointing out the need for clarifying this point. It is already known that sperm capacitation is well associated with the increase of intracellular pH (Vredenburgh‐Wilberg & Parrish, 1995; Y. Zeng et al., 1996), the hyperpolarization of the membrane (Arnoult et al., 1999; Y. Zeng et al., 1995) and the elevation of intracellular Ca²⁺ concentration level (Breitbart, 2002; Publicover et al., 2007) through diverse ion channel activities. To explore whether these pathways are influenced by intracellular zinc, we used patch-clamp techniques to measure the membrane potential (Vm) as shown in Fig. 1D-K. It has been reported that under the whole-cell current clamp of mouse epididymal spermatozoa, resting membrane potential is hyperpolarized after intracellular alkalinization (Navarro et al., 2007). We mentioned this in line 100-108 in the manuscript.

Next, our findings from the experiments using mouse spermatozoa suggest that intracellular zinc inhibits a key process in sperm capacitation, specifically the alkalinization-induced hyperpolarization. Previous studies have identified the pH-and voltage-dependent potassium channel Slo3 is responsible for the principal K⁺ current (I_KSper) in mouse spermatozoa (Navarro et al., 2007; Santi et al., 2010; Schreiber et al., 1998; X. H. Zeng et al., 2011). During capacitation, the rise in pHi leads to the activation of Slo3 channels, resulting in membrane hyperpolarization (Santi et al., 2010). Given this context, we next investigated whether intracellular zinc acts directly on the Slo3 channel and found that zinc inhibits mSlo3 current. We explained this rationale of the experiment in line 143-150.

We add following sentence to add more clarity to the text:

“During capacitation, the rise in pHi leads to the activation of Slo3 channels, resulting in membrane hyperpolarization (Santi et al., 2010).”

Therefore, the text was modified into:

“Our findings suggest that intracellular zinc inhibits a key process in sperm capacitation, specifically the alkalinization-induced hyperpolarization. Previous studies have identified the pH-and voltage-dependent potassium channel Slo3 is responsible for the principal K⁺ current (I_KSper) in mouse spermatozoa (Navarro et al., 2007; Santi et al., 2010; Schreiber et al., 1998; X. H. Zeng et al., 2011). During capacitation, the rise in pHi leads to the activation of Slo3 channels, resulting in membrane hyperpolarization (Santi et al., 2010). Given this context, we next investigated whether intracellular zinc acts directly on the Slo3 channel.”

Regarding the specific inhibitor, as has been pointed out by the reviewer that a new Slo3 inhibitor, VU0546110, exhibited more than 40-fold selective for human Slo3 over Slo1 (M. Lyon et al., 2023). However, the effect of VU0546110 in mSlo3 has not been tested yet. Both mouse and human Slo3 exhibit similar responses to certain inhibitors, but mouse and human Slo3 is also differ in their responses to several other inhibitors (M. D. Lyon et al., 2023), making it uncertain if this VU0546110 will work on mSlo3.

(9) In the second half of Figure 1, the authors suggest that there is "no hyperpolization in 100uM Zn. That is not really true. It is reduced but not absent.

We modified the wording of “no hyperpolarization in 100 µM Zn” to “alkalinization-induced hyperpolarization was reduced in the 100 µM ZnCl₂ group.”

“In contrast, alkalinization-induced hyperpolarization was reduced in the 100 µM ZnCl₂ group”

(10) The claim that Lrcc52 with Slo3 shows a higher current inhibition at pH 7.5 than pH 8 is not well supported because there are only 3 replicates in the 7.5 case. In addition, the claim is made in the test that 100uM ZnCl2 "already inhibited mSlo3+Lrcc52 at pH7.5", contrasted with mSlo3 alone, is not tested statistically.

Thank you for the valuable comment. Although Fig. 3F shows a statistical difference, we agree that having only three replicates at pH 7.5 may somewhat weaken the conclusion. Following this suggestion, we have revised the sentence as follows:

“Alkalinization appeared to increase the percentage of current inhibition by 100 µM ZnCl₂.”

We provided statistical analysis to compare pH 7.5 between mSlo3 alone and mSlo3+Lrrc52 in the Figure 3—figure supplement 1D:

The statistical analysis showed that 100 µM zinc significantly inhibited the mSlo3 + Lrrc52 current at pH 7.5 compared to the mSlo3 current alone. We have incorporated the necessary changes into the revised manuscript and updated the figure legends accordingly.

In a number of places, better controls are needed.

(11) How specific is this effect for Zn? Mg2+, for instance, is also a divalent cation that is in the hundreds of uM range inside the cell. Does it exert the same effect? Each ion certainly has unique preferred coordination geometries, does your predicted binding with MD show what you might expect for tetrahedral coordination with Zn? Did you test other divalent cations functionally or in silicon?

To answer this question, we have tested this by building another AlphaFold3 model, with Mg²⁺ instead of Zn²⁺. We did not opt for the all-atoms MD simulations due to the cost of the simulation. Here, the model shows that Mg are all clustered at the pore domain and does not reside anywhere near the Zn²⁺ site from both MD simulations and the AF3 model.

Author response image 3.

AlphaFold3 model of Slo3 channel with Mg²⁺

The Slo3 AlphaFold model from residue M1 to L330. The colour gradient reflects the pLDDT score range from 1.73 to 95.69. Purple sticks highlighted E169, N171 and E205. In this study, we did not examine other divalent cations in our electrophysiological recordings. Exploring their effects will be an important direction for future research.

(12) For the VCF experiments, a significantly higher concentration of Zn was used (10mM). What is the reason for this? There is no discussion of how much a "puff" is. Assuming you are using the RNA injector it is probably on the order of 50nL or less. Assuming the volume of an oocyte is 1uL that would argue that the final concentration is 500uM or higher. But this is also complicated by potential local effects of high Zn at the injection site, artifacts of injecting that much metal, and the fact that a great deal of the Zn will likely be bound to other things inside the cell. Better controls are needed for this experiment.

As pointed out by the reviewer, the volume of the oocytes is estimated to be approximately 1 µL. We performed manual injections using glass needle typically used for RNA injection. However, because the injections were done manually during real-time VCF recording (as illustrated in the experimental scheme), the exact volume of the solution injected into each oocyte could not be precisely controlled. We estimated that each drop to be approximately 50 nL, resulting in a final concentration around 500 µM, as described by the reviewer.

The rationale for using relatively high concentration was to ensure that the zinc concentration inside the oocyte reached an effective level, since manual injection may sometimes deliver less than 50 nL of solution. In some cases, injections failed entirely due to the technical difficulty of the method. Because VCF recordings are already technically difficult, we aimed to ensure that zinc injection was successful in oocytes that exhibited robust fluorescence signal by injecting an excess amount of zinc that would not disrupt normal oocyte conditions. For example, 10 mM zinc was prepared in an acidic solution (pH 2.5). We verified that this acidic condition did not affect mSlo3 current by performing control injections with the acidic solution alone, since the mSlo3 current is not activated under acidic pH conditions

Author response image 4.

VCF control experimentes: vehicle injection.

Reviewer #3 (Public review):

Summary:

The study titled "Zinc is a Key Regulator of the Sperm-Specific K+ Channel (Slo3) Function" aims to investigate the role of intracellular zinc in sperm capacitation and its regulation of the sperm-specific Slo3 potassium channel. Capacitation is a crucial physiological process that enables sperm to fertilize an egg, and membrane hyperpolarization through Slo3 activation is a well-established event in this process. The authors propose that intracellular zinc dynamically decreases during capacitation and inhibits Slo3-mediated K⁺ currents, thereby playing a regulatory role in sperm function.

Strengths:

(1) Novel Contribution to Sperm Physiology.

The study provides new insights into how zinc dynamics contribute to sperm capacitation, specifically through its direct inhibition of Slo3 activity.<br /> Previous research has focused primarily on extracellular zinc's effect on sperm function; this work expands the discussion to intracellular zinc regulation, an area with limited prior investigation.

(2) Strong Electrophysiological Evidence.

The study employs inside-out patch-clamp recordings in Xenopus oocytes to demonstrate zinc's direct inhibition of Slo3 currents. The observed slow dissociation of zinc from Slo3 suggests a long-lasting regulatory effect, adding to the understanding of ion channel modulation in sperm cells.

(3) Molecular Mechanistic Insights

Using Molecular Dynamics (MD) simulations and mutagenesis, the authors identify potential zinc-binding sites within Slo3's voltage-sensing domain (VSD), particularly E169 and E205. These computational predictions are supported by electrophysiological recordings, strengthening the argument that zinc directly binds and inhibits Slo3.

(4) Physiological Relevance and Functional Implications

The study suggests that zinc inhibition of Slo3 could contribute to sperm motility regulation during capacitation.

The authors provide sperm motility assays as supporting evidence, showing that zinc chelation affects motility only after capacitation has begun, suggesting a dynamic role of intracellular zinc in the capacitation process.

Weaknesses:

While the study presents compelling electrophysiological data and molecular insights, there are several critical gaps that must be addressed before fully supporting the physiological relevance of the findings.

(1) The authors should measure the effects in sperm cells using the patch-clamp technique to directly record Slo3 currents. By normalizing Slo3 currents to cell capacitance at different intracellular zinc concentrations, the authors can quantitatively assess the extent of Slo3 inhibition by zinc and strengthen the physiological relevance of their findings.

We thank the reviewer for the valuable comments to strengthen the physiological relevance of our findings. We provided additional data of Slo3 currents measured using perforated patch-clamp recording in sperm cells in experiments with zinc pyrithione (ZnPy) before and after the addition of 10 mM NH₄Cl. Control experiments were conducted in the absence of ZnPy, in which Slo3 current were recorded before and after the application of 10 mM NH₄Cl. These data have been integrated into Figure 1L-N and Figure 1—figure supplement 1A, B.

It is worth noting that Slo3 current in this recording might contain other endogenous current, as no specific blocker was used. Nonetheless, the data showed that the Slo3 current in sperm tends to be inhibited by zinc, as shown by the plot of absolute Slo3 current after the addition of 10 mM NH₄Cl in the absence of ZnPy (control) and in the presence of 100 µM ZnPy. There was a decrease in the fold change calculated from the absolute current before and after the addition of 10 mM NH₄Cl of ZnPy treated group compared to the control group.

We also provided data with the cell capacitance as suggested; however, cell capacitance obtained from the sperm recordings showed the capacitance throughout the head and midpiece of spermatozoa. On the other hand, Slo3 channels are not expressed in the entire spermatozoa, therefore the cell capacitance acquired from these recordings does not accurately reflect the area where the Slo3 channels are localized. Although we included normalization of Slo3 currents to cell capacitance before and after ZnPy application, this normalization should be interpreted with caution for the reasons mentioned above. The corresponding figure has been included in the supplementary data Figure 1—figure supplement 1A, B.

We added sentences to the result section as follows:

“We also measured Slo3 current using perforated patch-clamp recordings in spermatozoa treated with ZnPy, before and after the addition of NH₄ Cl. Control experiments were conducted in the absence of ZnPy, in which Slo3 current were recorded before and after the application of 10 mM NH₄Cl (Fig. 1L-N; Fig. 1—figure supplement 2A, B). Slo3 current in sperm tended to be inhibited by zinc, as shown by the plot of absolute Slo3 current after the addition of 10 mM NH₄Cl in the absence of ZnPy (control) and in the presence of 100 µM ZnPy (Fig. 1L, M). There was a decrease in the fold change calculated from the absolute current before and after the addition of 10 mM NH₄Cl of ZnPy treated group compared to the control group (Fig. 1N). Taken together, these results confirmed that intracellular zinc indeed inhibits alkalinization-induced hyperpolarization in mouse sperm.”

(2) Lack of Controls in Non-Capacitated Sperm

The claim that zinc is exported from sperm during capacitation needs stronger experimental validation.

The authors did not include a control group of non-capacitated sperm in key fluorescence imaging experiments, making it difficult to confirm that the observed zinc decrease is capacitation-specific rather than a general zinc redistribution process.

To strengthen this conclusion, experiments should be performed in non-capacitating conditions to determine whether intracellular zinc levels remain unchanged.

We added the control group of non-capacitated sperm in key fluorescence imaging experiments, as integrated in Figure 1B.

The following changes in the Results and Figure Legend sections are revised and added:

“We observed that there was a gradual and significant decrease in fluorescence intensity in both regions (Fig. 1B), particularly prominent in the flagellum (Fig. 1C). This decline suggests the active release of intracellular zinc from sperm flagellum occurs during capacitation. In contrast, the fluorescence intensity of the control group of non-capacitated sperm remained unchanged (Fig. 1B).”

Figure Legend 1B was modified accordingly.

(3) Unclear Role of Zinc in Physiological Capacitation

The study clearly demonstrates zinc inhibition of Slo3 but does not sufficiently establish how this affects capacitation at a functional level.

Additional motility and capacitation markers should be analyzed to confirm that zinc influences sperm behavior beyond Slo3 inhibition.

We thank the reviewer for this valuable comment. We fully agree that zinc can influence sperm physiology through multiple mechanisms and that its overall effects on capacitation are complex. However, the main goal of our study is to investigate the mechanism and to determine whether intracellular Zn²⁺ directly inhibits Slo3. Our results from both the heterologous expression system and the sperm membrane potential recordings consistently support this conclusion.

For these reasons, we believe that adding such assays would not clarify the role of Slo3 in capacitation but rather risk confounding interpretation. Instead, we have expanded the Discussion to explicitly acknowledge these limitations and to emphasize that future studies combining genetic or pharmacological modulation of Slo3 with comprehensive capacitation analyses will be required to fully define its physiological impact.

We added sentences to the discussion section in the revised manuscript as follows:

“Although these results support a mechanistic link between zinc and Slo3 activity, future studies that combine genetic or pharmacological modulation of Slo3 with comprehensive capacitation analyses will be required to define its physiological impact in more detail. Within this context, this study highlights the potential importance of intracellular zinc in the regulation of sperm capacitation.”

(4) Insufficient Data on Zinc-Slo3 Specificity

The authors should consider using quinidine, a known washable Slo3 inhibitor, to confirm that zinc acts specifically on Slo3 channels rather than other endogenous ion channels.

The study would benefit from including washout controls in the inside-out patch-clamp recordings, as seen in Figure 3-Supplement 1, to confirm that zinc inhibition is reversible or long-lasting.

We thank the reviewer for raising the point regarding the need to confirm that the current observed in our recordings indeed represents Slo3 current by using a specific blocker such as quinidine, as there is a possibility that endogenous currents might also be present and that zinc could act on those endogenous currents. Performing experiments with quinidine would indeed be crucial to demonstrate the specificity of Slo3 current in our patch-clamp recordings.

However, in our current experimental protocol, we apply ramp pulses multiple times and require a long series of recordings within a single session in one patch as described in the materials and methods as well as Figure 2I, Figure 4—figure supplement 1C, Figure 5B (pH 8.0 → 100 µM zinc → pH 8.0, to observe the washout effect). Incorporating quinidine into this sequence would make the protocol even longer (pH 8.0 → quinidine → washout → pH 8.0 → 100 µM zinc), which increases the likelihood of patch loss before completing the full set.

Furthermore, we have ensured that the recorded current corresponds to Slo3 by using appropriate experimental conditions, specifically the suitable voltage range for activation, a high intracellular pH (pH 8.0), and high-potassium solutions in our recordings.

(5) Missing Discussion of Zinc's Role in CatSper Regulation

The study focuses solely on Slo3 but does not mention CatSper, the principal Ca²⁺ channel essential for sperm capacitation.

Zinc has been reported to inhibit CatSper activity, which could significantly impact sperm function.

The discussion should address whether zinc's effect on Slo3 represents a broader regulatory mechanism influencing multiple ion channels during capacitation.

Thank you for the comment. To the best of our knowledge, there have been no reports showing that CatSper activity is directly regulated by zinc ions.

Furthermore, in our patch-clamp recordings with NH₄Cl and ZnPy, we observed that the normal CatSper current increased even in the presence of ZnPy, which makes it challenging to conclude whether zinc directly affects CatSper channel activity.

We added sentences to the discussion section in the revised manuscript as follows:

“In addition to that, to date, there are only few reports on the effect of zinc on other sperm ion channels, and none have been reported in mouse sperm. One important study was reported by (Jeschke et al., 2021), in which seminal zinc was found to inhibit prostaglandin-induced activation of CatSper, a sperm-specific Ca²⁺ channel, in human sperm. The complex opposing action of seminal zinc and prostaglandins on CatSper may help preventing premature activation of CatSper in the ejaculate and act as a dilution sensor, although this study does not provide direct evidence for zinc acting directly on CatSper (Jeschke et al., 2021).”

Final Assessment

This work presents important findings on zinc regulation of Slo3 channels, supported by strong electrophysiological and molecular analyses. However, the physiological relevance of these findings remains unclear due to missing controls, and needs additional functional assays. Addressing these issues would significantly enhance the manuscript's scientific rigor and impact.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Most of the specific comments and suggestions are in the public review. Minor additional comments primarily focused on presentation and textual errors are here.

(1) There is something strange happening in Figure 6D in the -100ish range. I think it's likely related to the reversal potential of K+.

Thank you for pointing it out. Yes in figure 6D there was strange plot in the range of -100 mV. As the reviewer has pointed out we also think that it is related to the reversal potential of potassium ions.

(2) There are a number of errors in the text that make following it difficult. For instance, multiple times the authors say "In consistent" (line 120 as an example) when I think they mean consistent with.

We changed the “in consistent” with “consistent with” throughout the revised manuscript.

Reviewer #3 (Recommendations for the authors):

The authors provide well-described experiments, particularly those examining the effects of intracellular zinc on Slo3 channels using inside-out patch-clamp recordings. However, some experimental designs intended to assess the physiological relevance of these findings during capacitation require additional controls and data before the authors' claims can be fully supported.

Comments

Major Concerns & Suggested Improvements

Line 65: "In the present study, we find that intracellular zinc is exported during capacitation, indicating that zinc dynamics in spermatozoa play an important role in fertilization."

This claim requires additional experimental data to be fully supported.

Thank you for pointing it out. We have provided data for control experiments of zinc imaging in non-capacitated conditions in Figure 1B.

Line 79: "Intracellular zinc is exported from sperm during capacitation."

The authors should include controls in non-capacitated conditions to determine whether zinc export is specific to capacitation or a general process in sperm cells.

Again, we have provided data for control experiments of zinc imaging in non-capacitated conditions in Figure 1B.

Figures - General Comment:

In all figures, please replace SEM (Standard Error of the Mean) with Standard Deviation (SD) for consistency and a more accurate representation of variability.

SEM (Standard Error of the Mean) has been replaced with SD (Standard Deviation) in all figures (main figures and supplements) as well as in numerical description accordingly.

Figure 1

Panel B:

Include a non-capacitating media control to confirm that the observed decrease in zinc-sensitive dye fluorescence is not due to artifact/photobleaching.

We have provided data for control experiments of zinc imaging in non-capacitated conditions in Figure 1B.

Perform an experiment with capacitating media supplemented with a higher concentration of zinc. If intracellular zinc export is a real effect, added extracellular zinc should prevent or reduce this phenomenon.

We appreciate the reviewer’s suggestion; however, we believe that supplementing the medium with high concentrations of zinc is unsuitable for validating the export phenomenon due to confounding physiological factors. Our preliminary tests demonstrated that increasing extracellular zinc triggers a drastic increase in intracellular zinc as well (Author response image 5). Furthermore, the high concentration of BSA in the capacitation medium acts as a potent zinc buffer, precluding precise control over free Zn²⁺ levels. Therefore, the inherent difficulty in maintaining defined extracellular and intracellular Zn²⁺ gradients makes the interpretation of such data highly problematic. Future studies will focus on identifying the specific zinc transporters involved and characterizing their molecular mechanisms.

Author response image 5.

Zinc addition

Clarify whether the "n" value represents different cells or multiple recordings from the same cell.

n value represents different cells.

Supplemental Figure 1:

Incorporate Δ (delta) comparison between 10 min and 2 hours under control conditions and in the presence of TPEN.

Here we provide data:

Author response image 6.

Δ comparition between control and TPEN

Provide statistical analysis for these comparisons to make the effects of capacitation clearer.

We did the calculation and statistical analysis, however there was no statistical difference, as shown in the author response figure 6 due to high variability of individual data.

Figure 2

Panel C:

Incorporate inhibition at pH 7.4 and 6.0 for direct comparison.

Recording inhibition effect of zinc at pH 6.0 is not possible because there would be no current to begin with, as mSlo3 is gated by both voltage and alkaline pH.

Panel D:

Include a washout control, similar to what is shown in Panel A.

We included a washout control trace to Figure 2D.

Panel E:

Provide a longer reference trace in the absence of zinc to clearly visualize the control condition. The current reference segment is too short to properly assess baseline activity.

Although we do not have a longer reference trace in the absence of zinc for Figure 2E, we instead show the trace recorded under the application of 0.1 µM zinc in Figure 2—figure supplement 1A to illustrate the current behavior.

Panels G-H:

Include inside-out patch-clamp traces and quantification of zinc washout effects.

Inside out patch traces are shown in Figure 2G as we applied step-pulses protocol. The zinc washout effect could not be quantified because the patch was usually lost after the second step-pulse application.

Panels I-K:

Provide additional traces. In Panel I, the inhibition by zinc is clear, but in Panel J, the reduction appears less distinct and could be due to rundown or an artifact. Additional controls should clarify this.

Figure 2K presents the most representative trace among five recorded cells. The apparent reduction is less distinct, likely due to an artifact caused by a bubble in the rapid perfusion system during solution exchange. However, at the end of zinc application (t = 50 s), the current amplitude was clearly reduced compared with that at t = 0–10 s.

Figure 3

Panel D:

Include additional data showing the transition to pH 6 and washout with pH 7.5, similar to the experimental design in Panels A and B.

We included additional data showing raw trace of the application of pH 6.0 in Figure 3D, also included the transition to pH 6 and washout with pH 7.5 in Figure 3E.

Figure 3-Supplement 1:

Include zinc washout experiments. This approach is one of the best ways to evaluate the reversibility of zinc inhibition on the channel.

As mentioned above, in this recording we recorded step pulses up to +180 mV. The zinc washout effect could not be quantified because the patch was usually lost after the second step-pulse application.

Figure 6

Zinc Inhibition Specificity:

The authors should use quinidine, a known washable Slo3 inhibitor, to assess Slo3 activity before and after zinc injection.

This experiment would confirm that zinc specifically inhibits Slo3, rather than affecting other endogenous channels.

We sincerely thank the reviewer for this valuable suggestion. However, given the technical difficulty of these experiments, which involve lengthy VCF recordings and manual zinc injections that significantly compromise oocyte health, it is not feasible to apply quinidine at this stage.

Moreover, we observed voltage-dependent fluorescence changes around the VSD, and this change was influenced by the application of zinc, confirming that zinc specifically inhibits Slo3 rather than affecting other endogenous channels.

Discussion - Key Revisions Needed

Line 308: "Our results demonstrated that intracellular zinc is exported from spermatozoa during capacitation."

This claim needs to be supported by experiments using non-capacitated conditions.

Additionally, measuring maximum and minimum zinc concentrations under different conditions would improve the interpretation of fluorescence intensity changes.

We now include negative control in non-capacitated sperm. The data is incorporated into Figure 1B.

Line 309: "We further discovered that intracellular zinc regulates alkalinization-induced hyperpolarization in mice spermatozoa, mediated by Slo3 channel."

Additional controls are needed to substantiate this claim.

At this stage of the study, we do not have access to Slo3 knockout (KO) mice; therefore, performing additional experiments is not feasible.

Line 316: "Using FluoZin3-AM for zinc imaging, we confirmed the presence of intracellular zinc in sperm (Fig. 1A), which is consistent with previous findings (Henkel et al., 1999). Our observations revealed that treatment with capacitation medium induced a decrease in zinc fluorescence intensity (Fig. 1B, C), suggesting that zinc levels are dynamic during capacitation."

This statement must be supported by negative controls, including non-capacitated sperm conditions.

We now include negative control in non-capacitated sperm. The data is incorporated into Figure 1B.

Line 327: "We also observed that zinc chelator significantly affected the sperm motility only after, but not before, capacitation (Fig. 1-figure supplement 1)."

Data presentation should be revised to highlight the effects of capacitation itself.

The discussion should specify which motility parameters were affected and why others were not.

In the text we mentioned that:

“We incubated the isolated spermatozoa with cell permeable Zn²⁺ chelator N,N,N',N'-Tetrakis(2-pyridylmethyl)ethylenediamine (TPEN) and measured the motility parameters before and after capacitation. We found that VAP (average path velocity), VCL (curvilinear velocity), and VSL (straight-line velocity) were influenced by the TPEN treatment only after the capacitation, as shown in Fig. 1—figure supplement 1. These results demonstrate that the dynamics of zinc levels during capacitation potentially contributes to sperm motility, highlighting the importance of zinc action in sperm physiology.”

Indeed, we observed that zinc chelator significantly affected the sperm motility specifically in VAP (average path velocity), VCL (curvilinear velocity), and VSL (straight-line velocity) only after, but not before, capacitation (Fig. 1—figure supplement 1). Of note, it has been recently reported that all these motility parameters (VAP, VCL, and VSL) are reduced by Slo3-specific inhibitors in human sperm (M. Lyon et al., 2023). These findings are consistent with the idea that endogenous zinc dynamics control sperm motility through Slo3 during the capacitation process.

Figure legend is revised accordingly.

Line 369: "Structural determinants of zinc inhibition in the mSlo3 channel."

The authors should include an analysis of the evolutionary conservation of the mutated sites across Slo1, Slo2, and Slo3.

If Slo3 has a unique regulatory mechanism, these sites should show high sequence variability compared to other Slo channels.

If these sites are highly conserved, the authors should explain how Slo3 differs functionally from Slo1 and Slo2 despite this conservation.

We thank the reviewer for the valuable suggestions regarding the inclusion of additional discussion points on the structural determinants of zinc inhibition in the mSlo3 channel. We performed sequence alignment by using ClustalO between mSlo3, mSlo1, and mSlo2.2. It is worth noting that only human and frog variants of Slo2.1 sequence are available in the database, so we included only Slo2.2 subtype, as our focus was on Slo3 in mouse sperm.

Based on the alignment, E169 (mSlo3 numbering) is conserved among the Slo family channels in mice, while in contrast E205 (mSlo3 numbering) is not. To date, there have been no report examining the corresponding residues to E169 (E191 in mslo1 or E176 in mslo2.2) for their zinc sensitivity. This might be because in both channels the zinc-binding sites are well defined where they are located in RCK1 domain for Slo1 (Hou et al., 2010) and RCK2 domain for Slo2.2 (J. Zhang et al., 2023). The identified binding site in Slo2.2 is conserved in Slo2.1 but not present in Slo1 and Slo3 (J. Zhang et al., 2023), further suggesting that zinc regulation differs among Slo family members. However, this does not rule out the possibility that regions surrounding E191 or E176 could provide to additional insights into zinc regulation in these channels, which could be of interest for future studies.

Interestingly, in contrast to E169, E205 is not conserved across the Slo family, making this residue unique to the mouse Slo3 channel and potentially a determinant of zinc sensitivity in mSlo3. Given that E205 is located in the S4 domain and supported by our VCF results showing that zinc inhibition influences the motion of voltage-sensing domain of mSlo3, E205 represents an important residue to be explored in future studies. Furthermore, as this residue is unique only to Slo3, it highlights the distinct functional properties of Slo3 such as its gating mechanism as it is regulated by both membrane voltage and alkalinization, which has a different voltage range of activation compared to mSlo1 (Li et al., 2024) and involves distinct ligands and gating mechanisms compared to Slo2 (J. Zhang et al., 2023).

We add the sequence alignment results into Figure 5—figure supplement 1F.

We revised the results section as follows:

“Additionally, we performed sequence alignment by using ClustalO between mSlo3, mSlo1, and mSlo2.2. It is worth noting that only human and frog variants of Slo2.1 sequence are available in the database, so we included only Slo2.2 subtype, as our focus was on Slo3 in mouse sperm. Based on the alignment, E169 (mSlo3 numbering) is conserved among the Slo family channels in mice, while in contrast E205 (mSlo3 numbering) is not. (Figure 5—figure supplement 1F).”

We revised the discussion section as follows:

“Based on sequence alignment, E169 (mSlo3 numbering) is conserved among Slo family channels in mice, whereas E205 (mSlo3 numbering) is not (Fig. 5—figure supplement 1F). To date, no studies have examined the corresponding residues to E169 (E191 in mSlo1 or E176 in mSlo2.2) for their potential zinc sensitivity, likely because the established zinc binding sites in these channels are located in the RCK1 domain for Slo1 (Hou et al., 2010) and the RCK2 domain for Slo2.2 (J. Zhang et al., 2023). The identified zinc binding site in Slo2.2 is conserved in Slo2.1 but is absent in both Slo1 and Slo3 (J. Zhang et al., 2023), further suggesting that zinc regulation differs among Slo family members. Although regions surrounding E191 or E176 may still provide additional insights into zinc regulation and could be of interest for future investigation, E205 stands out because, unlike E169, it is not conserved across the Slo family, making it unique to mSlo3 and potentially a specific determinant of zinc sensitivity in this channel.”

Figure legend is revised accordingly.

Line 392: "Physiological relevance of zinc inhibition of the mSlo3 channel in mouse sperm."

The authors should mention the effects of zinc on CatSper channels, as CatSper is also crucial for capacitation.

Slo3 inhibition may represent only one component of zinc's broader regulatory role during capacitation.

We thank the reviewer for raising this important point regarding the physiological relevance of zinc inhibition of the mSlo3 channel in mouse sperm. We agree that we should have also discussed the effect of zinc on CatSper channels, as this channel is crucial for capacitation. To date, there are only few reports on the effect of zinc on CatSper channels, and none have been reported in mouse sperm. One important study was reported by (Jeschke et al., 2021), in which seminal zinc was found to inhibit prostaglandin-induced activation of CatSper in human sperm. The complex opposing action of seminal zinc and prostaglandins on CatSper may help preventing premature activation of CatSper in the ejaculate and act as a dilution sensor, which facilitating sperm to escape into female genital tract (Jeschke et al., 2021). Taking this into consideration, as the reviewer pointed out, zinc inhibition on Slo3 may represent only one component of zinc’s broader regulatory role during capacitation.

We added a sentence to the discussion section in the revised manuscript as follows:

“In addition to that, to date, there are only few reports on the effect of zinc on other sperm ion channels, and none have been reported in mouse sperm. One important study was reported by (Jeschke et al., 2021), in which seminal zinc was found to inhibit prostaglandin-induced activation of CatSper, a sperm-specific Ca²⁺ channel, in human sperm. The complex opposing action of seminal zinc and prostaglandins on CatSper may help preventing premature activation of CatSper in the ejaculate and act as a dilution sensor, although this study does not provide direct evidence for zinc acting directly on CatSper (Jeschke et al., 2021).”

The study presents valuable insights into the role of intracellular zinc in sperm capacitation and Slo3 channel function. However, the physiological impact of these findings remains unclear due to insufficient controls and missing key experimental data. The suggested revisions would strengthen the validity of the claims made by the authors and improve the overall scientific rigor of the manuscript.

Key Areas for Improvement:

Control experiments in non-capacitated conditions.

Increased statistical rigor in figure analyses.

More detailed experiments to confirm specificity of zinc action on Slo3.

Expanded discussion of zinc's role beyond Slo3, including CatSper regulation.

The authors should measure these effects in sperm cells using the patch-clamp technique to directly record Slo3 currents. By normalizing Slo3 currents to cell capacitance at different intracellular zinc concentrations, the authors can quantitatively assess the extent of Slo3 inhibition by zinc and strengthen the physiological relevance of their findings.

By addressing these concerns, the manuscript will provide a more robust foundation for understanding zinc's regulatory role in sperm physiology and capacitation.

Author response:

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

eLife Assessment

The study presents valuable findings of an optimized E. coli cell-free protein synthesis (eCFPS) system that has been simplified by reducing the number of core components from 35 to 7; furthermore, the findings communicate a simplified 'fast lysate' preparation that eliminates the need for traditional runoff and dialysis steps. This study is an advance towards simplifying protein expression workflows, and the evidence provided is solid, starting with nanoluc, a protein that expresses readily in many systems, to applications to more challenging proteins like the functional self-assembling vimentin and the active restriction endonuclease Bsal. Data on the underlying mechanisms and efficiency of the presented system in terms of protein yield relative to other known cell-free systems would greatly enhance the findings' significance and the strength of the evidence. The paper remains of interest to scientists in microbiology, biotechnology and protein synthesis.

We thank the editors for the positive assessment of our optimized E. coli cellfree protein synthesis (eCFPS) system and the "fast lysate" preparation.

As suggested, we have significantly strengthened the evidence by adding:

(1) Mechanism data: We have integrated a detailed analysis of the endogenous metabolic pathways (amino acids and nucleotides) into the Discussion section, supported by literature (Prinz et al. 1997; Yokoyama et al. 2010; Kigawa et al. 1999).

(2) Efficiency comparisons: We have added quantitative comparisons of absolute protein yields between our simplified 7-component system and the conventional 35-component system (now in Figure S3 E-F), demonstrating that our system matches or exceeds traditional titers.

Public Reviews:

Reviewer #1 (Public review):

The authors only provided the data for optimization, leaving the underlying mechanism that explains the phenomena unexplained.

We appreciate this feedback. To address the mechanism of how protein synthesis persists without exogenous additives, we have expanded the Discussion to explain how the "fast lysate" retains active endogenous enzymes. By omitting runoff and dialysis, our system preserves the metabolic capacity to synthesize amino acids (e.g., Cys and Trp from Ser) and nucleotides from residual precursors, as supported by the literature (Prinz et al. 1997; Yokoyama et al. 2010; Kigawa et al. 1999).

Reviewer #2 (Public review):

The production of the lysate requires special instrumentation, limiting accessibility. While the strengths of the study are well-emphasized, the limitations are not mentioned.

We thank the reviewer for this point. While a high-pressure homogenizer is common in many molecular biology labs, we acknowledge it may be a barrier for some. We have now included a dedicated Limitations paragraph in the Discussion addressing accessibility and the inherent challenges of prokaryotic systems in producing complex human proteins requiring post-translational modifications.

Reviewer #3 (Public review):

(1) Clarification on "highly efficient" and the lack of comparison with typical high-yield systems.

We have clarified "highly efficient" as a holistic balance of high yield, robustness, and simplified preparation. Crucially, we added absolute yield data (sfGFP standard curve) to Figure S3E-F demonstrating that our 7-component system performs comparably to or better than traditional high-yield protocols.

(2) How did the authors ensure chemical composition only affected translation and not transcription?

This is a key distinction. We performed new experiments using pretranscribed mRNA templates (Figure S3G) to isolate translational effects. While translation efficiency slightly decreased in the simplified buffer, the overall protein yield increased significantly due to a dramatic boost in transcription efficiency, confirming the system's net performance gain.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

There are specific concerns that need to be addressed:

(1) On page 4, lines 103-109, the authors speculate that protein synthesis persists even in the absence of amino acids like arginine, cysteine, and tryptophan. They suggest that this is likely due to residual amounts of these amino acids present in the cell lysate. Yokoyama et al. demonstrated that these amino acids are generated from other amino acids by endogenous amino acid metabolic enzymes in the cell lysate (J. Biomol. NMR 48, 193, (2010), doi: 10.1007/s10858-010-9455-3.). Cysteine and tryptophan can be derived from serine. In this context, asparagine and glutamine can be disregarded because they are synthesized from aspartate and glutamate, respectively. A more indepth analysis is required to interpret the results accurately.

We thank the reviewer for this insightful comment and for pointing us toward the relevant literature. We agree that the persistence of protein synthesis in the absence of exogenous amino acids like Arg, Cys, and Trp is driven by the robust metabolic capacity of our "fast lysate."

Unlike conventional protocols, our "fast lysate" procedure deliberately omits runoff and dialysis steps, ensuring the maximal retention of active endogenous metabolic enzymes and residual small-molecule pools. As demonstrated by Yokoyama et al. (2010), E. coli cell extracts retain functional enzymes capable of synthesizing acid-sensitive amino acids from precursors or more stable amino acids. We have integrated a detailed mechanistic analysis of these endogenous metabolic pathways into the Discussion section and have cited Yokoyama et al. (2010) to support this interpretation.

(2) On page 4, lines 111-115, the authors demonstrated that protein synthesis could occur even in the absence of CTP or UTP, provided ATP and GTP are present. This phenomenon can also be attributed to the analogous complementary actions of metabolic pathways.

We agree with the reviewer's assessment. The ability of the optimized eCFPS to function without exogenous CTP/UTP relies on the same principle of endogenous metabolic conversion mentioned above. The omission of dialysis ensures that the lysate retains not only residual nucleotide pools but also the full suite of nucleotide metabolic enzymes. Powered by our optimized energy regeneration system, these enzymes maintain sufficient levels of CTP and UTP to support transcription and translation. This explanation has been added to the Discussion section to clarify the robustness of our system.

(3) On Figure 3A, protein synthesis kinetics are presented in a stair plot instead of the commonly used scatterplot. Is there a specific reason for choosing the stair plot?

We chose the stair plot representation to more clearly visualize the cumulative process of protein synthesis and its stabilization over discrete time intervals. Given that sampling occurred every 10 minutes, a stair plot effectively highlights the "plateau" phases and the incremental nature of accumulation, which can sometimes be obscured by dense scatter plots.

(4) On Figure 3C. It is unclear which system is referred to as the "initial" system in Figure 3C. Which data point on Figures 3A and 3B corresponds to this "initial" system?

We apologize for the lack of clarity. In Figure 3C, "initial" refers to the traditional 35-component system prior to our streamlining process. Figures 3A and 3B characterize the performance of the final optimized system alone. To resolve this ambiguity, we have updated the legend for Figure 3 to explicitly define the "initial" system as the pre-optimization control.

(5) In Figure 5D, previously reported eCFPS and the system using "fast lysate" were compared. The only difference between the two systems seems to be the type of lysate used, according to the Supplementary table. Optimal concentrations for the components are the same for both lysates, or is there still room for optimization for "fast lysate"?

The "fast lysate" primarily differs from conventional lysates in its preparation speed and the retention of endogenous cofactors/enzymes. While the optimal salt and energy concentrations remained consistent across both lysates in our tests, the "fast lysate" provides a higher baseline signal due to the endogenous T7 RNA polymerase and metabolic factors. We believe this demonstrates the robustness of the optimized reaction buffer across varying lysate preparation qualities.

(6) The study suggests that the removal of DTT didn't negatively affect protein expression. However, based on my experience, certain proteins, especially those with cysteine residues on their surface, tend to aggregate without DTT. Did the authors attempt to express such proteins, or did they draw this conclusion based on the limited number of proteins tested?

This is a valid concern. We based our conclusion on the functional expression of Bsal and vimentin—two proteins that are inherently prone to aggregation and misfolding. Their successful synthesis suggests that the intrinsic reducing capacity of the lysate (e.g., glutathione and thioredoxin systems) is sufficient for many targets (Prinz et al. 1997). However, we acknowledge that specialized cysteine-rich proteins may still require exogenous DTT. We have addressed this in the Discussion.

Reviewer #2 (Recommendations for the authors):

(1) Line 77-78 "we iteratively evaluated the contribution of individual constituents through luciferase reporter assays" - where is all the data? Please use an appropriate figure citation. Figure 1 cherry picks some components, but I think all data should be included.

We have structured the data presentation to show dispensable components in Figure 1 (where removal does not inhibit reaction) and essential components in Figure 2 (where 0-concentration results in zero activity). This ensures a logical flow of the "streamlining" narrative. All raw data for these screenings have been included in the Source Data files.

(2) Line 127 typo "concentrations".

We thank the reviewer for pointing out this error. The typo "concentrations" has been corrected.

(3) Figure 2: "protein expression levels" measured how?/what is the unit of the vertical bar on the right? I'm assuming that this experiment was conducted for discrete concentrations and thus generated discrete data points. However, the graph makes it seem as if this is continuous data. Kindly change the type of graphing to indicate that this is discrete data, showing each data point.

We appreciate the reviewer's suggestion. Protein expression levels were measured using the Nanoluciferase (NLuc) reporter gene assay. We utilized heatmaps/contour plots because our data are bivariate, representing the simultaneous optimization of two concentrations (e.g., Mg²⁺ and K⁺ in Figure 2A). For such matrix-based screenings, heatmaps are significantly more effective than scatter plots at conveying synergistic trends and identifying optimal reaction landscapes. Notably, this visualization approach for discrete biochemical optimization data was successfully employed by Ban lab in their recent study on translation system optimization (Bothe and Ban 2024). The vertical color bar on the right represents the relative expression ratio, normalized to the maximum yield. Although we have provided a scatter plot of this discrete data for reference (see Author response image 1), we believe it appears visually cluttered due to the high density of data points, making it difficult to discern overarching trends. Heatmaps, by contrast, offer a much clearer representation of the optimal reaction landscape. To maintain transparency, the discrete concentration points tested are clearly reflected by the axis ticks, and all raw discrete data are available in the Source Data files.

Author response image 1.

(4) Also, for all figures: the way the units are presented (DTT/mM) is confusing to me; it could just be something like [DTT] (mM).

We have revised all figures and tables to follow the standard format (e.g., [Component] (unit)) as suggested.

(5) Do the sucrose gradient sedimentation data have replicates? If so, please indicate statistics.

The sucrose gradient data provided (Figure 5C) is intended as qualitative evidence that the "fast lysate" method preserves intact 70S ribosomes across different preparation batches. This experiment has been performed independently multiple times with consistent results, demonstrating the high reproducibility of our preparation method. While we did not perform a quantitative comparative analysis of ribosome concentration, the consistency of the peaks confirms the integrity of the translational machinery.

(6) Line 457: fix the red line.

We thank the reviewer for pointing this out. The formatting issue has been resolved in the revised manuscript.

(7) Please mention the limitations of this study in the discussion.

We thank the reviewer for this suggestion. We have added a paragraph to the Discussion addressing the limitations of prokaryotic systems regarding complex eukaryotic post-translational modifications and chaperone requirements.

(8) Please include all uncropped gels in the source data, alongside the raw data, as you have already done.

As requested, we have provided all original, uncropped gel images in the Source Data files, alongside the raw data, to ensure full transparency and compliance with the journal's data sharing policies.

Reviewer #3 (Recommendations for the authors):

(1) The study lacks a comparison of protein levels with a typical cell-free protein synthesis system.

We have performed new quantitative experiments (now included in Figure S3 E-F) to measure absolute protein yields. Our optimized system achieves yields comparable to, or exceeding, several widely recognized highyield protocols while utilizing significantly fewer components. We have also clarified in the text that "highly efficient" refers to the synergistic balance of high yield, low cost, and simplified preparation time.

(2) What do the authors mean by "highly efficient", often used in the manuscript?

We thank the reviewer for the opportunity to clarify our terminology. We have performed new quantitative experiments (now included in Figure S3) to measure absolute protein yields, demonstrating that our optimized system achieves yields comparable to, or exceeding, several widely recognized highyield protocols while utilizing significantly fewer components.

In the context of this manuscript, we use the term "highly efficient" as a holistic descriptor that encapsulates three key dimensions of the system:

(1) Performance Superiority: Achieving higher expression levels and faster kinetics compared to conventional 35-component systems.

(2) Functional Robustness: The ability to efficiently synthesize challenging targets, such as cytotoxic proteins (BsaI) and aggregation-prone proteins (vimentin), which often fail in simplified systems.

(3) Practical Utility: A drastic reduction in preparation time and cost through the "fast lysate" protocol and the removal of 28 auxiliary components, thereby lowering the barrier to adoption.

This definition aligns with the study's core objective: developing a system where efficiency is measured not only by final yield but by the synergy between high performance and extreme ease of use.

(3) In this article, the term 'optimisation' is used as a synonym for 'simplification'. In biochemistry, optimisation commonly refers to an increase in yield, or the same yield achieved more easily or at a lower cost. In this case, however, we have no idea how this new system compares to a conventional expression system in terms of yield.

We thank the reviewer for this conceptual clarification. We agree that in biochemistry, "optimization" typically implies an improvement in yield or cost-effectiveness. In our study, we use the term to describe the process of achieving a superior balance between system simplicity and protein production. To address the reviewer's concern regarding the lack of a direct yield comparison, we have added new data in Figure S3. This figure provides a sideby-side comparison of protein yields between our simplified 7-component system and the conventional 35-component system. The results demonstrate that our system not only matches the performance of the traditional setup but frequently exceeds it in terms of final protein titer, while significantly reducing the reagent cost and preparation complexity. Thus, the simplification achieved in this work represents a true biochemical optimization of the cell-free synthesis process.

(4) The levels of transcripts of the proteins studied were not determined in any of the experiments performed. Therefore, it is unknown whether the effects of different experimental conditions on NLuc, GFP or other protein expression are due to an effect on transcription, translation, or both.

This is an excellent point. We performed a new set of experiments using mRNA templates instead of DNA to isolate the effects on translation (Figure S3G). Our results indicate that while the system's overall boost in NLuc expression is partially attributable to enhanced transcription efficiency, the translation machinery remains highly robust. We have updated the Results and Discussion to reflect this distinction.

References

Bothe, Adrian, and Nenad Ban. 2024. “A Highly Optimized Human in Vitro Translation System.” Cell Reports Methods 4 (4): 100755.

Kigawa, T., T. Yabuki, Y. Yoshida, M. Tsutsui, Y. Ito, T. Shibata, and S. Yokoyama. 1999. “Cell-Free Production and Stable-Isotope Labeling of Milligram Quantities of Proteins.” FEBS Letters 442 (1): 15–19.

Prinz, W. A., F. Aslund, A. Holmgren, and J. Beckwith. 1997. “The Role of the Thioredoxin and Glutaredoxin Pathways in Reducing Protein Disulfide Bonds in the Escherichia Coli Cytoplasm.” The Journal of Biological Chemistry 272 (25): 15661–67.

Yokoyama, Jun, Takayoshi Matsuda, Seizo Koshiba, and Takanori Kigawa. 2010. “An Economical Method for Producing Stable-Isotope Labeled Proteins by the E. Coli Cell-Free System.” Journal of Biomolecular NMR 48 (4): 193–201.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors' goal was to advance the understanding of metabolic flux in the bradyzoite cyst form of the parasite T. gondii, since this is a major form of transmission of this ubiquitous parasite, but very little is understood about cyst metabolism and growth.

Nonetheless, this is an important advance in understanding and targeting bradyzoite growth.

Strengths:

The study used a newly developed technique for growing T. gondii cystic parasites in a human muscle-cell myotube format, which enables culturing and analysis of cysts. This enabled screening of a set of anti-parasitic compounds to identify those that inhibit growth in both vegetative (tachyzoite) forms and bradyzoites (cysts). Three of these compounds were used for comparative Metabolomic profiling to demonstrate differences in metabolism between the two cellular forms.

One of the compounds yielded a pattern consistent with targeting the mitochondrial bc1 complex, and suggest a role for this complex in metabolism in the bradyzoite form, an important advance in understanding this life stage.

Weaknesses:

Studies such as these provide important insights into the overall metabolic differences between different life stages, and they also underscore the challenge with interpreting individual patterns caused by metabolic inhibitors due to the systemic level of some of some targets, so that some observed effects are indirect consequences of the inhibitor action. While the authors make a compelling argument for focusing on the role of the bc1 complex, there are some inconsistencies in the some patterns that underscore the complexity of metabolic systems.

Thank you for reviewing the revised manuscript.

Reviewer #2 (Public review):

Summary:

A particular challenge in treating infections caused by the parasite Toxoplasma gondii is to target (and ultimately clear) the tissue cysts that persist for the lifetime of an infected individual. The study by Maus and colleagues leverages the development of a powerful in vitro culture system for the cyst-forming bradyzoite stage of Toxoplasma parasites to screen a compound library for candidate inhibitors of parasite proliferation and survival. They identify numerous inhibitors capable of inhibiting both the disease-causing tachyzoite and the cyst-forming bradyzoite stages of the parasite. To characterize the potential targets of some of these inhibitors, they undertake metabolomic analyses. The metabolic signatures from these analyses lead them to identify one compound (MMV1028806) that interferes with aspects of parasite mitochondrial metabolism. In the revised version of the manuscript, the authors present convincing evidence that MMV1028806 targets the mitochondrial electron transport (ETC) chain of the parasite (although they don't identify the actual target in the ETC). The revised manuscript also nicely addresses my other criticisms of the original version. Overall, the study presents an exciting approach for identifying and characterizing much-needed inhibitors for targeting tissue cysts in these parasites.

Strengths:

The study presents convincing proof-of-principle evidence that the myotube-based in vitro culture system for T. gondii bradyzoites can be used to screen compound libraries, enabling the identification of compounds that target the proliferation and/or survival of this stage of the parasite. The study also utilizes metabolomic approaches to characterize metabolic 'signatures' that provide clues to the potential targets of candidate inhibitors. In addition to insights into candidate bradyzoite inhibitors, the study also provides new insights into the physiological role of the mitochondrial electron transport chain of bradyzoites, and raises a host of interesting questions around the functional roles of mitochondria in this stage of the parasite.

Weaknesses:

In the revised manuscript, the authors have included additional oxygen consumption rate data that indicate that MMV1028806 targets the mitochondrial electron transport chain (ETC). These data are convincing. On line 481, the authors state that "treatments with ATQ, BPQ, MMV1028806, and antimycin A resulted in substantially reduced oxygen consumption levels relative to the DMSO control and suggest indeed a blockage of the mETC consistent with the inhibition of the bc1-complex." The OCR assay the authors use is still only an indirect measure of bc1 activity. Given that most OCR-inhibiting compounds in T. gondii are bc1 inhibitors, it is possible (and perhaps likely) that MMV1028806 is targeting this complex. However, the data cannot rule out that it is targeting another component of the ETC (or potentially even a TCA cycle enzyme). Without a direct test that MMV1028806 inhibits bc1 complex activity, the authors should be more cautious in their interpretation (e.g. by acknowledging the limitations of their conclusion, or acknowledging other possible targets). Similarly, the conclusion on line Line 622 that "... we confirmed the bc1-complex as a target" is overstating the findings. The phrasing on lines 683-695 is more appropriate: "... suggesting that it also targets complex III or a functionally linked site within the mitochondrial electron transport chain."

We are grateful for he thorough review of the updated manuscript and the identification the minor issues. We addressed all of them as detailed below. We also tempered our conclusions regarding the identification of the bc1-complex as a target in line 616:

“In addition to abundance data, Additionally, we confirmed the bc1-complex as a target by monitoring the incorporation of ¹³C and ¹⁵N stable isotopes from glucose and glutamine, respectively, into TCA cycle and pyrimidine biosynthesis intermediates suggest the bc1-complex as a target”

Reviewer #3 (Public review):

Summary:

The authors described an exciting 400-drug screening using a MMV pathogen box to select compounds that effectively affect the medically important Toxoplasma parasite bradyzoite stage. This work utilises a bradyzoites culture technique that was published recently by the same group. They focused on compounds that affected directly the mitochondria electron transport chain (mETC) bc1-complex and compared with other bc1 inhibitors described in the literature such as atovaquone and HDQs. They further provide metabolomics analysis of inhibited parasites which serves to provide support for the target and to characterise the outcome of the different inhibitors.

Strengths:

This work is important as, until now, there are no effective drugs that clear cysts during T. gondii infection. So, the discovery of new inhibitors that are effective against this parasite-stage in culture and thus have the potential to battle chronic infection is needed. The further metabolic characterization provides indirect target validation and highlight different metabolic outcome for different inhibitors. The latter forms the basis for new studies in the field to understand the mode of inhibition and mechanism of bc1-complex function in detail.

The authors focused in the function of one compound, MMV1028806, that is demonstrated to have a similar metabolic outcome to burvaquone. Furthermore, the authors evaluated the importance of ATP production in tachyzoite and bradyzoites stages and under atovaquone/HDQs drugs.

Thank you for reviewing the revised manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Thanks for making appropriate updates. I believe it makes the report stronger. Just please double-check proof-reading in newly added text: for example "integration" is misspelled in Figure 4 legend (C, E).

Typos have been corrected throughout the manuscript.

Reviewer #2 (Recommendations for the authors):

I congratulate the authors on an excellent study. I have several minor comments for the authors to consider before publication.

Line 99. Schistosoma –

Corrected

Line 123. What was the pH of the bicarb-free RPMI medium?

Added “at pH 7.2”

Line 218 (and again on line 687). "RHku80" - are these just standard RH strain parasites? Or do the authors mean to imply that the ku80 gene has been knocked out in this line? If the latter, RH∆ku80 may be a better way to describe this line.

We harmonized all mentions of this strain to RH∆ku80.

Line 225. "Parasites were incubated in medium with one of the following treatments ..." How long were the parasites incubated in the different treatments before the plate was read? Was there any preincubation? I think not, but it would help to state this so the reader can appreciate that the effects of the compounds on OCR is likely an immediate (rather than a secondary) effect.

This is indeed a good suggestion. There was no pre-incubation and we added changed the text to: “Parasites were incubated in medium with one of the following treatments immediately before measurement: … “

Figure S2A. Check the spelling of Toxoplasmosis.

Done, we corrected this sentence.

Figure S2B. do you mean 'tachyzoidal' or 'tachyzocidal'? 'bradyzoidal' or 'bradyzocidal'?

We clarified the formulation of the legends for Fig S2.

Figure S2D. The "Tachyzoite lowest cytotoxicity" and "Bradyzoite lowest cytotoxicity" columns are, I think, depicting compound toxicity in host cells. Would it be clearer to rename these columns relative to the host cells being tested? e.g. "HFF/KD3 myotube lowest cytotoxicity"

Good suggestion and we changed the designation accordingly.

Line 369. "We found that tachyzocidal, bradyzocidal and dually active compounds possess a statistically significantly higher lipophilicity and this trend appeared more accentuated for bradyzocidal and dually active compounds." Significantly higher than what? Need to be clearer about the comparison being made: i.e. to non-active compounds.

You are correct and we corrected this sentence accordingly.

Line 500. "we attribute these changes to inhibition of host mitochondria (Fig. 5A)." The reason for referencing Figure 5A here isn't clear. Do the authors mean to point out that host mitochondrial membrane potential is affected by compound treatment? This could be stated more clearly.

We deleted the reference to Fig 5A. We did not systematically measure the effect of the inhibitors on the membrane potential of the host mitochondria. We also changed the sentence to emphasize the speculative nature of this assertion: “we attribute these changes to potential inhibitory effects on host mitochondria”.

Line 840. 'hurdling mechanisms'. The authors don't explain what they mean by this expression.

We truncated the figure title to: “Untargeted metabolomic analysis of bradyzoites treated with bc1-complex inhibitors shows an energy imbalance.”

Author response:

Public Reviews:

Reviewer #1 (Public Review):

By mapping H3K4me2 in mouse oocytes and pre-implantation embryos, the authors aim to elucidate how this histone modification is erased and re-established during the parental-to-zygotic transition, as well as how the reprogramming of H3K4me2 regulates gene expression and facilitates zygotic genome activation.

Employing an improved CUT&RUN approach, the authors successfully generated H3K4me2 profiling data from a limited number of embryos. While the profiling experiments are very well executed, several weaknesses, particularly in data analysis, are apparent:

(1) The study emphasizes H3K4me2, which often serves as a precursor to H3K4me3, a well-studied modification during early development. Analyzing the new H3K4me2 dataset alongside published H3K4me3 data is crucial for comprehensively understanding epigenetic reprogramming post-fertilization and the interplay between histone modifications. However, the current analysis is preliminary and lacks depth.

Thank you very much for your valuable suggestions. The data of histone H3K4me3 in humans and mice has been published，and our previous data revealed the unique pattern of H3K4me3 during early human embryos and oocytes (Science. 2019 Jul 26;365(6451):353-360.) . So, this study mainly focuses on the localization of H3K4me2 in mouse oocytes and preimplantation embryos, how it is erased and re-established during mammalian parental-to-zygote transition, and its function. The combined analysis of H3K4me2 and H3K4me3 is not our main work, but it is not ruled out that there may be new discoveries between these two histones. Previously, our data tended to show that the H3K4me2 not only acts as a precursor of H3K4me3, but also plays its role independently.

(2) Tranylcypromine (TCP) is known as an irreversible inhibitor of monoamine oxidase and LSD1. While the authors suggest TCP inhibits the expression of LSD2, this assertion is questionable. Given TCP's potential non-specific effects in cells, conclusions related to the experiments using TCP should be made with caution.

Thank you for pointing this out, and we thank the reviewer again for the important suggestion. We found that the previous study (.Binda C, Valente S, Romanenghi M, Pilotto S, Cirilli R, Karytinos A, Ciossani G, Botrugno OA, Forneris F, Tardugno M, Edmondson DE, Minucci S, Mattevi A, Mai A. Biochemical, structural, and biological evaluation of tranylcypromine derivatives as inhibitors of histone demethylases LSD1 and LSD2. J Am Chem Soc. 2010 May 19;132(19):6827-33.) indicated that TCP was a non-reversible inhibitor of LSD1 and LSD2 (Human LSD2/KDM1b/AOF1 Regulates Gene Transcription by Modulating Intragenic H3K4me2 Methylation, Mol Cell. 2010 Jul 30; 39(2): 222–233.), but according to our data, the content of LSD1 was very low in the early stages of mouse embryos, which mainly inhibited the function of LSD2.

(3) Some batches of H3K4me2 antibody are known to cross-react with H3K4me3. Has the H3K4me2 antibody used in CUT&RUN been tested for such cross-reactivity? Heatmaps in the figures indeed show similar distribution for H3K4me2 and H3K4me3, further raising concerns about antibody specificity.

We thank the reviewer for the insightful comments. The H3K4me2 antibody was purchased from Millipore (cat. 07030). Figure 2A shows the specific enrichment area of H3K4me2 in promoter and distal region. Some batches of H3K4me2 antibody are known to cross-react with H3K4me3, but the H3K4me2 antibody we used in our CUT&RUN seems to have Low cross-reactivity.

(4) Certain statements lack supporting references or figures (examples on page 9 can be found on line 245, line 254, and line 258).

Thank you for pointing this out, and we will add references to support the statement in the paper as suggested.

(5) Extensive language editing is recommended to clarify ambiguous sentences. Additionally, caution should be taken to avoid overstatement - most analyses in this study only suggest correlation rather than causality.

Thank you for your kind comments. We will revise the expression in the manuscript later.

Reviewer #2 (Public Review):

Chong Wang et al. investigated the role of H3K4me2 during the reprogramming processes in mouse preimplantation embryos. The authors show that H3K4me2 is erased from GV to MII oocytes and re-established in the late 2-cell stage by performing Cut & Run H3K4me2 and immunofluorescence staining. Erasure and re-establishment of H3K4me2 have not been studied well, and profiling of H3K4me2 in germ cells and preimplantation embryos is valuable to understanding the reprogramming process and epigenetic inheritance.

(1) The authors claim that the Cut & Run worked for MII oocytes, zygotes, and the 2-cell embryos. However, it is unclear if H3K4me2 is erased during the stage or if the Cut & Run did not work for these samples. To support the hypothesis of the erasure of H3K4me2, the authors conducted immunofluorescence staining, and H3k4me2 was undetected in the MII oocyte, PN5, and 2-cell stage. However, the published papers showed strong staining of H3K4me2 at the zygote stage and 2-cell stage ((Ancelin et al., 2016; Shao et al., 2014)). The authors need to cite these papers and discuss the contradictory findings.

The authors used 165 MII oocytes and 190 GV oocytes for the Cut & Run. The amount of DNA in MII oocytes is halved because of the emission of the first polar body. Would it be a reason that H3K4me2 has fewer H3K4me2 peaks in MII oocytes than GV oocytes?

First of all, thank you for your valuable advice. The published papers showed strong staining of H3K4me2 at the zygote stage and 2-cell stage (Ancelin et al., 2016), which is interesting. I think we may have used different parameters in the confocal laser shooting process. We used the same parameter to continuously shoot the blastocyst stage from the GV stage. If we only shot the fertilized egg and the 2-cell stage, I think we may also see weak fluorescence at the 2-cell stage under different parameters. We will refer to this reference and discuss it in the resubmitted version.

Moreover, you mentioned the H3K4me2 has fewer H3K4me2 peaks in MII oocytes than GV oocytes, because the MII expelled the polar body. There is no problem with this logic. However, the first polar body expelled from the MII stage is still in the zona pellucida, and we also collected the polar body in the CUT&RUN experiment; Therefore, compared to GV, the DNA content of MII samples is not halved. After further discussion, we believe that the reduction of H3K4me2 peaks in MII stage compared with GV stage may be closely related to oocyte maturation. It is the specific modification of histones in different forms at different times that affects the chromatin structure change appropriately with the different stages of meiosis. At present, it has been confirmed that H3K4me3 gradually decreases from GV to MII stage during the maturation of human oocytes. H3K27me3 did not change from GV to MII stage.

In Figure 3C, 98% (13,183/13,428) of H3K4me2 marked genes in GV oocytes overlap with those in the 4-cell stage. Furthermore, 92% (14,049/15,112) of H3K4me2 marked genes in sperm overlap with those in the 4-cell stage. Therefore, most regions maintain germ line-derived H3K4me2 in the 4-cell stage. The authors need to clarify which regions of germ line-derived H3K4me2 are maintained or erased in preimplantation embryos. Additionally, it would be interesting to investigate which regions show the parental allele-specific H3K4me2 in preimplantation embryos since the authors used hybrid preimplantation embryos (B6 x DBA).

Thank you very much for your suggestion. Further analysis of which regions show the parental allele-specific H3K4me2 in preimplantation embryos will make the study more interesting. We will discuss this in depth in resubmitted vision.

(2) The authors claim that Kdm1a is rarely expressed during mouse embryonic development (Figure 4A). However, the published paper showed that KDM1a is present in the zygote and 2-cell stage using immunostaining and western blotting (Ancelin et al., 2016). Additionally, this paper showed that depletion of maternal KDM1A protein results in developmental arrest at the two-cell stage, and therefore, KDM1a is functionally important in early development.

The authors should have cited the paper and described the role of KDM1a in early embryos.

In the analysis of this experiment, we believe that in the early embryonic development of mice, the expression of KDM1A is lower than that of KDM1B, which is relative. Similarly, the transcriptome data we cite also show that KDM1A is expressed at elevated levels during oocyte maturation and fertilization compared to immature oocytes. In addition, the effects of loss of maternal KDM1a on embryonic development were not discussed. We believe that the absence of maternal KDM1b blocks embryonic development, and we will cite and discus the references later.

(3) The authors used the published RNA data set and interpreted that KDM1B (LSD2) was highly expressed at the MII stage (Figure S3A). However, the heat map shows that KDM1B expression is high in growing oocytes but not at 8w_oocytes and MII oocytes. The authors need to interpret the data accurately.

After re-checking the data, we found that there was a problem with the normalization method of our heat map, and we will re-make the heatmap and submit it in the modified version. With reference to Figure 4A, the content of Kdm1b is indeed higher than that of Kdm1a.

(4) All embryos in the TCP group were arrested at the four-cell stage. Embryos generated from KDM1b KO females can survive until E10.5 (Ciccone et al., 2009); therefore, TCP-treated embryos show a more severe phenotype than oocyte-derived KDM1b deleted embryos. Depletion of maternal KDM1A protein results in developmental arrest at the two-cell stage ((Ancelin et al., 2016)). The authors need to examine whether TCP treatment affects KDM1a expression. Western blotting would be recommended to quantify the expression of KDM1A and KDM1B in the TCP-treated embryos.

We will further dig the transcriptome data to confirm the specificity of TCP to KDM1b. In addition, the intervention of TCP on the whole fertilized egg in this study increased the H3K4me2 content, and the embryo development retarding effect was more significant than that obtained by crossing with normal paternal lines after knocking down KDM1B from the mother.

(5) H3K4me2 is increased dramatically in the TCP-treated embryos in Figure 4 (the intensity is 1,000 times more than the control). However, the Cut & Run H3K4me2 shows that the H3K4me2 signal is increased in 251 genes and decreased in 194 genes in the TCP-treated embryos (Fold changes > 2, P < 0.01). The authors need to explain why the gain of H3K4me2 is less evident in the Cut & Run data set than in the immunofluorescence result.

Thanks a lot for your question. In the experimental group, the fluorescence value of H3K4me2 in IF was increased by 1000 times (Figure 4E), and the expression of H3K4Me2-related genes in CR was up-regulated and down-regulated for a total of 445 changes (Figure 6A). In our opinion, as a semi-quantitative analysis, immunofluorescence cannot be compared with the quantitative analysis method of CR because of the different analysis models and threshold Settings.

References

Ancelin, K., ne Syx, L., Borensztein, M., mie Ranisavljevic, N., Vassilev, I., Briseñ o-Roa, L., Liu, T., Metzger, E., Servant, N., Barillot, E., Chen, C.-J., Schü le, R., & Heard, E. (2016). Maternal LSD1/KDM1A is an essential regulator of chromatin and transcription landscapes during zygotic genome activation. https://doi.org/10.7554/eLife.08851.001

Ciccone, D. N., Su, H., Hevi, S., Gay, F., Lei, H., Bajko, J., Xu, G., Li, E., & Chen, T. (2009). KDM1B is a histone H3K4 demethylase required to establish maternal genomic imprints. Nature, 461(7262), 415-418. https://doi.org/10.1038/nature08315

Shao, G. B., Chen, J. C., Zhang, L. P., Huang, P., Lu, H. Y., Jin, J., Gong, A. H., & Sang, J. R. (2014). Dynamic patterns of histone H3 lysine 4 methyltransferases and demethylases during mouse preimplantation development. In Vitro Cellular and Developmental Biology - Animal, 50(7), 603-613. https://doi.org/10.1007/s11626-014-9741-6

Reviewer #3 (Public Review):

Summary:

This study explores the dynamic reprogramming of histone modification H3K4me2 during the early stages of mammalian embryogenesis. Utilizing the advanced CUT&RUN technique coupled with high-throughput sequencing, the authors investigate the erasure and re-establishment of H3K4me2 in mouse germinal vesicle (GV) oocytes, metaphase II (MII) oocytes, and early embryos.

Strengths:

The findings provide valuable insights into the temporal and spatial dynamics of H3K4me2 and its potential role in zygotic genome activation (ZGA).

Weaknesses:

The study primarily remains descriptive at this point. It would be advantageous to conduct further comprehensive functional validation and mechanistic exploration.

Key areas for improvement include enhancing the innovation and novelty of the study, providing robust functional validation, establishing a clear model for H3K4me2's role, and addressing technical and presentation issues. The text would benefit from the introduction of a novel conceptual framework or model that provides a clear explanation of the functional consequences and molecular mechanisms underlying H3K4me2 reprogramming in the transition from parental to early embryonic development.

While the findings are significant, the current manuscript falls short in several critical areas. Addressing major and minor issues will significantly strengthen the study's contribution to the field of epigenetic reprogramming and embryonic development.

Author response:

eLife Assessment

This useful study presents an improved protocol for long-term in vitro culture of Schistosoma mansoni that enables progression toward sexually dimorphic stages, representing a meaningful advance for studying parasite development and reducing reliance on animal models. The findings show that host-specific culture conditions support essential developmental and metabolic functions required for parasite maturation, although development remains delayed compared to in vivo conditions. The evidence is solid overall, but limited pairing efficiency and the absence of egg production indicate that the system does not yet fully recapitulate complete reproductive development.

On behalf of the co-authors, we thank the three reviewers and the editors for their complimentary remarks as well as the major and minor comments/ concerns. Addressing these concerns have led to revisions that improved the manuscript. In particular, further analyses have generated an updated Figures 3 and 4, and Supplementary Tables S1, and S4-S6.

Public Reviews:

Reviewer #1 (Public review):

Pichon, Rémi et al. describe an in vitro method for transforming Schistosoma cercariae into mature adult worms. The authors show that human serum (HS) supports parasite growth and differentiation more effectively than fetal bovine serum (FBS). They also observed differences in parasite growth and activity, with worms cultured in HS efficiently digesting human red blood cells (hRBC). Cultured worms were able to pair with ex vivo adult worms and produce eggs, indicating functional maturation suitable for downstream applications such as drug screening. While the experimental approach is comprehensive and supports the advantage of HS culture conditions, the pairing efficiency was low (≈7%) and required long culture periods (70-80 days), highlighting limitations that may affect reproducibility.

We acknowledge the reviewer for the positive highlights. Regarding the low in vitro pairing efficiency, we have now edited the manuscript to clarify a misleading statement related to 7%. We decided to remove the value of 7% — which corresponds to the percentage of experiments in which couples were observed, as it does not accurately represent the actual number of observed worm pairs and it is probably misleading. We have updated the text as follows:

Results, lines 230 ff.:

“While the establishment of sexual dimorphism was robust and reproducible across more than 15 independent experiments, pairing between male and female parasites was rare. Pairing was observed only in experiments lasting more than 80 days in which we were only able to observe a few couples. In addition, these pairings were temporary (Figures 6A, B; Supplementary Video S4).”

We also agree with the reviewer that the extended culture periods required to obtain fully sexually dimorphic parasites remain a limitation. As elaborated in Discussion (see below), key factors, probably derived from the host, are missing in the in vitro system explaining both the slow in vitro development and low rate of spontaneous pairing between in vitro developed, sexually dimorphic male and female worms. This was discussed as follows (lines 340-343): “That said, while our system was highly efficient in producing sexually dimorphic worms, spontaneous pairing between male and female parasites was extremely rare, mainly in aged in vitro cultures (from 80 to 100 days in culture) indicating that other factors, e.g., cholesterol, may be missing[35].”

A major strength of the study, in particular, is that the authors clearly differentiate the effects of FBS versus HS on developmental progression. The conversion rate observed in HS cultures is significant and consistent with previously published data.

While the study has several strengths, some aspects of the work are not fully explored. In particular, the role of hRBC supplementation requires further clarification. Although HS-cultured worms were shown to digest hRBC more readily, the implications of this observation remain unclear. Specifically, it would be useful to understand whether hRBC supplementation influences (1) long-term culture stability, (2) molecular pathways associated with development and differentiation, or (3) the pairing capacity of the worms. While addressing these questions may not be the main objective of the study, further discussion of these points would strengthen the manuscript.

We agree that deciphering the role of the human Red Blood Cells (hRBCs) supplementation is critical. Regarding the influence of hRBCs on the long-term culture stability in parasite development it has been well established for more than four decades that schistosomes do need red blood cells to grow in culture [Basch, P. F. Cultivation of Schistosoma mansoni in vitro. II. production of infertile eggs by worm pairs cultured from cercariae. J Parasitol 67, 186-190 (1981); Basch, P. F. Cultivation of Schistosoma mansoni in vitro. I. Establishment of cultures from cercariae and development until pairing. J. Parasitol. 67, 179-185 (1981)]. The molecular pathways underlying development, sexual differentiation and pairing and modulated by hRBCs in culture is currently being investigated by our team. We decided not to include these data and analyses in the current manuscript, as they fall outside its scope.

The manuscript is clearly written and represents a valuable contribution to the field. Overall, the experimental approach is sound, and the results support a useful methodological framework for the in vitro culture of Schistosoma worms and the attainment of sexual maturity, particularly for adult male worms.

We thank the reviewer for highlighting the manuscript’s strengths.

Reviewer #2 (Public review):

Summary:

The authors perform confirmation studies of Paul Basch's seminal schistosome work from 1981, demonstrating the development of transformed schistosomules into sexually dimorphic adult parasites, albeit without successful egg production. In addition to the findings from Basch's earlier work, the authors add some new molecular data in the form of an analysis of proliferative cells in in-vitro-derived animals.

Strengths:

The authors successfully confirm experimental results from earlier schistosome researchers, providing a potential new tool for studying schistosome biology without the need for vertebrate hosts.

We thank the reviewer for highlighting the manuscript’s strengths.

Weaknesses:

The display of data from the authors is sometimes difficult to follow/understand where it comes from. For example:

(1) Line 136: The authors claim that parasites in HS and FBS conditions have substantially different mortality rates (11.3 +/- 2.7 vs 5 +/- 2.3) but a quite high p-value (0.8). Analyzing the raw data myself, I obtained a mean of 8.2 +/- 1.7% vs 4.8% +/- 4.3% with a p-value of 0.15. Either the data are not clearly presented, and I did not follow them, or the data presented in the text do not match the raw data in the supplemental files.

We thank the reviewer for pointing this out; we have now edited Supplementary Tables S1 and S6 by turning them into a long format for the sake of clarity. Accordingly, Results, Methods sections, and indicated supplementary tables were edited as follows:

Results, lines 142 ff.:

“No morphological differences were observed between parasites cultured either in FBS or HS within the first week in culture; in both conditions most parasites were classified as early schistosomula [category 1: 76% ± 30 (average ± SD) in FBS and 73% ± 29 (average ± SD) in HS] with few lung (category 2) and early liver schistosomula (category 3) (Figure 1B, week 1; Supplementary Figure S1). The mean mortality (category 0) at week 1 was slightly higher, but not statistically significant (P= 0.42), in worms cultured in HS [9.75% ± 2.76 (average ± SD)] compared to the mortality registered in FBS-cultured parasites [5.52% ± 5.18 (average ± SD), Supplementary Table S6], consistent with previous findings[39].”

Methods, lines 463-465:

“To evaluate differences in mortality between HS- and FBS-cultured parasites, data from 5 experiments were combined and analysed using a Shapiro-Wilk normality test to test normality of the data and a non-parametric Wilcoxon rank sum exact test (Supplementary Tables S1 and S6).”

Supplementary Tables:

Supplementary Table S1. “Raw counts of parasites within each developmental stage category. Each row corresponds to a picture of parasites in culture medium containing FBS or HS. Each column corresponds to the raw parasite counts at indicated stage development (categories 0 to 5), time in culture (Time in days - D), and experimental condition.”

Supplementary Table S6. “Summary of all statistical tests employed in this study. 1. Statistical tests of parasite mortality and the raw data table used for this test. 2. Statistical tests for worm size comparisons (correspond to Figure 2). 3. Statistical tests for worm black gut comparisons (correspond to Figure 3). BG: Black gut. 4. Statistical tests for EdU positive cells comparisons (correspond to Figure 4). Replicate code: E, M and L correspond to day 2, 8 and 15 respectively; R and W correspond to the presence (R) or absence (W) of RBCs added 13 days after transformation.”

For clarity, in Author response image 1 we provide the R script used to perform the statistical tests on the data shown in Supplementary Table S6 (column Raw count of parasite developmental category per image and experiment)

Author response image 1.

(2) Line 187/Figure 4: Though it is not clearly stated, it appears that the authors treat their EdU counts as an ordinal data set of 61 steps (from 0 to >60) rather than a continuous measure of EdU+ cells per animal. In this author's opinion, the graph strongly suggests a continuous data set, and the fact that this reviewer had to dig through poorly-labeled raw data to discover the nature of the data is problematic. The authors should either switch to a continuous data set or make it explicit that the data shown are ordinal. If counting EdU+ cells is too arduous, the authors could consider comparing the amount of EdU+ area to the amount of DAPI+ area in maximum intensity projections of their confocal images, as this would roughly approximate the amount of proliferative cells in the animals.

As the reviewer correctly pointed out, the data were treated as ordinal because counting worms with more than 60 Edu+ cells became extremely difficult and highly inaccurate. Therefore, we decided to group in a single category, “60 EdU+ cells”, all worms showing more than 60 EdU+ cells. We have now updated Figure 4 where medians are shown instead of media values, Supplementary Table S5 to provide more comprehensive access to the raw counts, and Supplementary Table S6 to indicate the data for EdU+ cells per worm were considered ordinal. Accordingly, we have revised the corresponding sections as follows:

Results, lines 211 ff.:

“HS-cultured schistosomula showed higher numbers of proliferating stem cells, with a median of >48 and >60 EdU+ cells per worm at days 8 and 15, respectively (Figure 4). On the other hand, most FBS-cultured parasites displayed no more than an average of 20 EdU+ cells per worm (Figure 4).”

Methods, lines 520 ff.:

“EdU+ cells per parasite were counted for an average of 100 parasites across three independent experiments (Supplementary Table S5). Worms were grouped based on the number of cells per individual, but all those showing ⪰ 60 EdU+ cells were counted in the same group named ‘60 EdU+ cells'. Therefore, the data were considered ordinal data. Statistical analysis was performed by Kruskal-Wallis test with Dunn multiple comparison post-hoc test, with P≤0.05 considered significant (Supplementary Table S6).”

Figure 4 legend, lines 830 ff.:

“A. Violin plots showing the number of Edu+ cells per worm at indicated time points (2, 8, and 15 days post cercarial transformation) in parasites cultured either in Foetal Bovine Serum (FBS, blue) or Human Serum (HS, light brown). Human Red Blood Cells (hRBCs) were added in the culture at day 13 post cercarial transformation. The small black dots indicate individual worms, and the big black point indicates the median of EdU+ cells per worm. All worms showing ⪰ 60 EdU+ cells were counted and clustered together in the group named ‘60 EdU+ cells’. Hence, the data were treated as ordinal and statistical analysis performed by Kruskal-Wallis test with Dunn multiple comparison post-hoc test, with P≤0.05 (*) considered significant (Supplementary Tables S5 and S6).”

We thank the reviewer for the very interesting suggestion to quantify cell proliferation by calculating the ratio between EdU+ area to DAPI+ area in maximum intensity projections images. Measuring the fluorescence area for each worm in maximum projection is an excellent idea; however, due to the number of EdU+ cells present in some samples, we think this technique would not provide additional information or produce more detailed data compared with our analysis when the number of Edu+ cells exceeds 60 per worm. We will certainly consider this approximation for future studies.

There are some minor issues as well:

(1) Line 122: It is perhaps incorrect to refer to humans as "the" definitive host of schistosomes, as S. japonicum is primarily considered a zoonotic infection with water buffalo/cows being the primary definitive host.

We thank the reviewer for pointing this out; we have now replaced “schistosomes” with “Schistosoma mansoni” (current line 131)

(2) Line 185/298: The authors refer to EdU pulse-chase experiments, but the experiments described here are EdU pulse experiments.

This is a very good point, we thank the reviewer for bringing this up and have accordingly edited by replacing “EdU pulse-chase” with “EdU pulse” experiments in lines 37, 204, and 321.

Reviewer #3 (Public review):

Summary:

This study is significant as it established a protocol for the long-term culture of Schistosoma mansoni newly transformed cercariae, which developed in vitro into sexually dimorphic forms. The impact of two different sera, Fetal Bovine Serum (FBS) and Human Serum (HS), added to the culture medium supplemented with human red blood cells was evaluated. The authors demonstrated that HS-cultured parasites were able to digest red blood cells, a critical step for long-term parasite development. Furthermore, while most FBS-cultured parasites did not progress beyond an early liver stage, sexual dimorphism was clearly evident in the HS-cultured worms, albeit delayed compared to in vivo development.

Strengths:

This study could contribute to further in vitro studies for a better understanding of the unique sexual biology of Schistosoma mansoni and for screening novel schistosomicidal compounds. By increasing parasite development in in vitro studies, this protocol could have a positive impact on the principles of the 3Rs (Replacement, Reduction and Refinement) for animal research.

We thank the reviewer for highlighting the manuscript’s strengths.

Weaknesses:

As the authors mentioned, "pairing between male and female parasites was rare. Pairing was observed in approximately ~7% of the experiments, usually after day ~ 80 in culture. Egg production was also not achieved with this protocol.

Following the reviewer’s point and to clarify a misleading point, we have now decided to remove the value of 7% — which corresponds to the percentage of experiments in which couples were observed. However, this value does not accurately reflect the actual number of observed worm pairs, and it is probably misleading. We have updated the text as follows:

Results, lines 230 ff.:

“While the establishment of sexual dimorphism was robust and reproducible across more than 15 independent experiments, pairing between male and female parasites was rare. Pairing was observed only in experiments lasting more than 80 days in which we were only able to observe a few couples. In addition, these pairings were temporary (Figures 6A, B; Supplementary Video S4).”

In 2011, a group on 4chan started spreading a plan for making a “Forever Along Involuntary Flashmob.” You can see their instructions below:

image in the form of a sort of flier with meme faces of foreveralone and trolls. The text reads: How to make your very own Forever Alone Involuntary Flashmob. 1. create fake online dating profile as mildly cute woman from NYC - just use somechicks facebook to get several believable pics etc. etc. 2. find forever alone guys from NYC on dating site, get them to believe you're interested. 3. Once forever alone guy takes the bait, suggest you meet for a date at this time and location: Pay phones outside 47th Digital store 46th st * Broadway NEW YORK 7:30PM Friday 13th May 2011. 4. watch angry alone guys flashmob rage at earthcam.com/usa/newyork/timessquare/ (select Camera 2). Also Remember: This will only work if we keep spreading these instructions and actually get involved. There is no limit to how many fake profiles and people you can trick or method used. Take time and prepare - think smart, if they suspect you're pushing the time and date too hard it aint gonna work.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript by Lin et al. presents a timely, technically strong study that builds patient-specific midbrain-like organoids (MLOs) from hiPSCs carrying clinically relevant GBA1 mutations (L444P/P415R and L444P/RecNcil). The authors comprehensively characterize nGD phenotypes (GCase deficiency, GluCer/GluSph accumulation, altered transcriptome, impaired dopaminergic differentiation), perform CRISPR correction to produce an isogenic line, and test three therapeutic modalities (SapC-DOPS-fGCase nanoparticles, AAV9GBA1, and SRT with GZ452). The model and multi-arm therapeutic evaluation are important advances with clear translational value.

My overall recommendation is that the work undergo a major revision to address the experimental and interpretive gaps listed below.

Strengths:

(1) Human, patient-specific midbrain model: Use of clinically relevant compound heterozygous GBA1 alleles (L444P/P415R and L444P/RecNcil) makes the model highly relevant to human nGD and captures patient genetic context that mouse models often miss.

(2) Robust multi-level phenotyping: Biochemical (GCase activity), lipidomic (GluCer/GluSph by UHPLC-MS/MS), molecular (bulk RNA-seq), and histological (TH/FOXA2, LAMP1, LC3) characterization are thorough and complementary.

(3) Use of isogenic CRISPR correction: Generating an isogenic line (WT/P415R) and demonstrating partial rescue strengthens causal inference that the GBA1 mutation drives many observed phenotypes.

(4) Parallel therapeutic testing in the same human platform: Comparing enzyme delivery (SapC-DOPS-fGCase), gene therapy (AAV9-GBA1), and substrate reduction (GZ452) within the same MLO system is an elegant demonstration of the platform's utility for preclinical evaluation.

(5) Good methodological transparency: Detailed protocols for MLO generation, editing, lipidomics, and assays allow reproducibility

Weaknesses:

(1) Limited genetic and biological replication

(a) Single primary disease line for core mechanistic claims. Most mechanistic data derive from GD2-1260 (L444P/P415R); GD2-10-257 (L444P/RecNcil) appears mainly in therapeutic experiments. Relying primarily on one patient line risks conflating patient-specific variation with general nGD mechanisms.

We thank the reviewer for highlighting the importance of genetic and biological replication. An additional patient-derived iPSC line was included in the manuscript, therefore, our study includes two independent nGD patient-derived iPSC lines, GD2-1260 (GBA1^L444P/P415R) and GD2-10-257 (GBA1^{L444P/RecNcil}), both of which carry the severe mutations associated with nGD. These two lines represent distinct genetic backgrounds and were used to demonstrate the consistency of key disease phenotypes (reduced GCase activity, elevated substrate, impaired dopaminergic neuron differentiation etc.) across different patient’s MLOs. Major experiments (e.g., GCase activity assays, substrate, immunoblotting for DA marker TH, and therapeutic testing with SapC-DOPS-fGCase, AAV9-GBA1) were performed using both patient lines, with results showing consistent phenotypes and therapeutic responses (see Figs. 2-6, and Supplementary Figs. 4-5). To ensure clarity and transparency, a new Supplementary Table 2 summarizes the characterization of both, the GD2-1260 and GD2-10-257 lines.

(b) Unclear biological replicate strategy. It is not always explicit how many independent differentiations and organoid batches were used (biological replicates vs. technical fields of view).

Biological replication was ensured in our study by conducting experiments in at least 3 independent differentiations per line, and technical replicates (multiple organoids/fields per batch) were averaged accordingly. We have clarified biological replicates and differentiation in the figure legends.

(c) A significant disadvantage of employing brain organoids is the heterogeneity during induction and potential low reproducibility. In this study, it is unclear how many independent differentiation batches were evaluated and, for each test (for example, immunofluorescent stain and bulk RNA-seq), how many organoids from each group were used. Please add a statement accordingly and show replicates to verify consistency in the supplementary data.

In the revision, we have clarified biological replicates and differentiation in the figure legend in Fig.1E; Fig.2B,2G; Fig.3F, 3G; Fig.4B-C,E,H-J, M-N; Fig.6D; and Fig.7A-C, I.

(d) Isogenic correction is partial. The corrected line is WT/P415R (single-allele correction); residual P415R complicates the interpretation of "full" rescue and leaves open whether the remaining pathology is due to incomplete correction or clonal/epigenetic effects.

We attempted to generate an isogenic iPSC line by correcting both GBA1 mutations (L444P and P415R). However, this was not feasible because GBA1 overlaps with a highly homologous pseudogene (PGBA), which makes precise editing technically challenging. Consequently, only the L444P mutation was successfully corrected, and the resulting isogenic line retains the P415R mutation in a heterozygous state. Because Gaucher disease is an autosomal recessive disorder, individuals carrying a single GBA1 mutation (heterozygous carriers) do not develop clinical symptoms. Therefore, the partially corrected isogenic line, which retains only the P415R allele, represents a clinically relevant carrier model. Consistent with this, our results show that GCase activity was restored to approximately 50% of wild-type levels (Fig.4B-C), supporting the expected heterozygous state. These findings also make it unlikely that the remaining differences observed are due to clonal variation or epigenetic effects.

(e) The authors tested week 3, 4, 8, 15, and 28 old organoids in different settings. However, systematic markers of maturation should be analyzed, and different maturation stages should be compared, for example, comparing week 8 organoids to week 28 organoids, with immunofluorescent marker staining and bulk RNAseq.

We agree that a systematic analysis of maturation stages is essential for validating the MLO model. Our data integrated a longitudinal comparison across multiple developmental windows (Weeks 3 to 28) to characterize the transition from progenitors to mature/functional states for nGD phenotyping and evaluation of therapeutic modalities: 1) DA differentiation (Wks 3 and 8 in Fig. 3): qPCR analysis demonstrated the progression of DA-specific programs. We observed a steady increase in the mature DA neuron marker TH and ASCL1. This was accompanied by a gradual decrease in early floor plate/progenitor markers FOXA2 and PLZF, indicating a successful differentiation path from progenitors to differentiated/mature DA neurons. 2) Glycosphingolipid substrates accumulation (Wks 15 and 28 in Fig 2): To assess late-stage nGD phenotyping, we compared GluCer and GluSph at Week 15 and Week 28. This comparison highlights the progressive accumulation of substrates in nGD MLOs, reflecting the metabolic consequences of the disease at different mature stage. 3) Organoid growth dynamics (Wks 4, 8, and 15 in new Fig. 4): The new Fig. 4 tracks physical maturation through organoid size and growth rates across three key time points, providing a macro-scale verification of consistent development between WT and nGD groups. By comparing these early (Wk 3-8) and late (Wk 15-28) stages, we confirmed that our MLOs transition from a proliferative state to a post-mitotic, specialized neuronal state, satisfied the requirement for comparing distinct maturation stages.

(f) The manuscript frequently refers to Wnt signaling dysregulation as a major finding. However, experimental validation is limited to transcriptomic data. Functional tests, such as the use of Wnt agonist/inhibitor, are needed to support this claim (see below).

We agree that the suggested experiments could provide additional mechanistic insights into this study and will consider them in future work.

(g) Suggested fixes / experiments

Add at least one more independent disease hiPSC line (or show expanded analysis from GD2-10-257) for key mechanistic endpoints (lipid accumulation, transcriptomics, DA markers).

Additional line iPSC GD2-10-257 derived MLO was included in the manuscript. This was addressed above [see response to Weaknesses (1)-a].

Generate and analyze a fully corrected isogenic WT/WT clone (or a P415R-only line) if feasible; at minimum, acknowledge this limitation more explicitly and soften claims.

We attempted to generate an isogenic iPSC line by correcting both GBA1 mutations (L444P and P415R). However, this was unsuccessful because the GBA1 gene overlaps with a pseudogene (PGBA) located16kd downstream of GBA1, which shares 9698% sequence similarity with GBA1) (Ref#1, #2), which complicates precise editing. GBA1 is shorter (~5.7 kb) than PGBA (~7.6 kb). The primary exonic difference between GBA1 and PGBA is a 55-bp deletion in exon 9 of the pseudogene. As a result, the isogenic line we obtained carries only the P415R mutation, and L444P was corrected to normal sequence. We have included this limitation in the Methods as “This gene editing strategy is expected to also target the GBA1 pseudogene due to the identical target sequence, which limits the gene correction on certain mutations (e.g., P415R)”.

References:

(1) Horowitz M., Wilder S., Horowitz Z., Reiner O., Gelbart T., Beutler E. The human glucocerebrosidase gene and pseudogene: structure and evolution. Genomics (1989). 4, 87–96. doi:10.1016/0888-7543(89)90319-4

(2) Woo EG, Tayebi N, Sidransky E. Next-Generation Sequencing Analysis of GBA1: The Challenge of Detecting Complex Recombinant Alleles. Front Genet. (2021). 12:684067. doi: 10.3389/fgene.2021.684067. PMCID: PMC8255797.

Report and increase independent differentiations (N = biological replicates) and present per-differentiation summary statistics.

This was addressed above [see response to Weaknesses (1)-b, (1)-c].

(2) Mechanistic validation is insufficient

(a) RNA-seq pathways (Wnt, mTOR, lysosome) are not functionally probed. The manuscript shows pathway enrichment and some protein markers (p-4E-BP1) but lacks perturbation/rescue experiments to link these pathways causally to the DA phenotype.

(b) Autophagy analysis lacks flux assays. LC3-II and LAMP1 are informative, but without flux assays (e.g., bafilomycin A1 or chloroquine), one cannot distinguish increased autophagosome formation from decreased clearance.

(c) Dopaminergic dysfunction is superficially assessed. Dopamine in the medium and TH protein are shown, but no neuronal electrophysiology, synaptic marker co-localization, or viability measures are provided to demonstrate functional recovery after therapy.

(d) Suggested fixes / experiments - Perform targeted functional assays:

(i) Wnt reporter assays (TOP/FOP flash) and/or treat organoids with Wnt agonists/antagonists to test whether Wnt modulation rescues DA differentiation.

(ii) Test mTOR pathway causality using mTOR inhibitors (e.g., rapamycin) or 4E-BP1 perturbation and assay effects on DA markers and autophagy.

Include autophagy flux assessment (LC3 turnover with bafilomycin), and measure cathepsin activity where relevant.

Add at least one functional neuronal readout: calcium imaging, MEA recordings, or synaptic marker quantification (e.g., SYN1, PSD95) together with TH colocalization.

We thank the reviewer for these valuable suggestions. We agree that the suggested experiments could provide additional mechanistic insights into this study and will consider them in future work. Importantly, the primary conclusions of our manuscript, that GBA1 mutations in nGD MLOs resulted in nGD pathologies such as diminished enzymatic function, accumulation of lipid substrates, widespread transcriptomic changes, and impaired dopaminergic neuron differentiation, which can be corrected by several therapeutic strategies in this study, are supported by the evidence presented. The suggested experiments represent an important direction for future research using brain organoids.

(3) Therapeutic evaluation needs greater depth and standardization

(a) Short windows and limited durability data. SapC-DOPS and AAV9 experiments range from 48 hours to 3 weeks; longer follow-up is needed to assess durability and whether biochemical rescue translates into restored neuronal function.

We agree with the reviewer. Because this is a proof-of-principle study, the treatment was designed within a short time window. Long-term studies with more comprehensive outcome assessments will be conducted in future work.

(b) Dose-response and biodistribution are under-characterized. AAV injection sites/volumes are described, but transduction efficiency, vg copies per organoid, cell-type tropism quantification, and SapC-DOPS penetration/distribution are not rigorously quantified.

We appreciate the reviewer’s concerns. This study was intended to demonstrate the feasibility and initial response of MLOs to AAV therapy. A comprehensive evaluation of AAV biodistribution will be considered in future studies.

The penetration and distribution of SapC-DOPS have been extensively characterized in prior studies. In vivo biodistribution of SapC–DOPS coupled CellVue Maroon, a fluorescent cargo, was examined in mice bearing human tumor xenografts using real-time fluorescence imaging, where CellVue Maroon fluorescence in tumor remained for 48 hours (Ref. #3: Fig. 4B, mouse 1), 100 hours (Ref. #4: Fig. 5), up to 216 hours (Ref. #5: Fig. 3). Uptake kinetics were also demonstrated in cells, with flow cytometry quantification showing that fluorescent cargo coupled SapC-DOPS nanovesicles, were incorporated into human brain tumor cell membranes within minutes and remained stably incorporated into the cells for up to one hour (Ref. # 6: Fig. 1a and Fig. 1b). Building on these findings, the present study focuses on evaluating the restoration of GCase function rather than reexamining biodistribution and uptake kinetics.

References:

(3) X. Qi, Z. Chu, Y.Y. Mahller, K.F. Stringer, D.P. Witte, T.P. Cripe. Cancer-selective targeting and cytotoxicity by liposomal-coupled lysosomal saposin C protein. Clin. Cancer Res. (2009) 15, 5840-5851. PMID: 19737950.

(4) Z. Chu, S. Abu-Baker, M.B. Palascak, S.A. Ahmad, R.S. Franco, and X. Qi. Targeting and cytotoxicity of SapC-DOPS nanovesicles in pancreatic cancer. PLOS ONE (2013) 8, e75507. PMID: 24124494.

(5) Z. Chu, K. LaSance, V.M. Blanco, C-H. Kwon, B. Kaur, M. Frederick, S. Thornton, L. Lemen, and X. Qi. Multi-angle rotational optical imaging of brain tumors and arthritis using fluorescent SapC-DOPS nanovesicles. J. Vis. Exp. (2014) 87, e51187, 1-7. PMID: 24837630.

(6) J. Wojton, Z. Chu, C-H. Kwon, L.M.L. Chow, M. Palascak, R. Franco, T. Bourdeau, S. Thornton, B. Kaur, and X. Qi. Systemic delivery of SapC-DOPS has antiangiogenic and antitumor effects against glioblastoma. Mol. Ther. (2013) 21, 1517-1525. PMID: 23732993.

(c) Specificity controls are missing. For SapC-DOPS, inclusion of a non-functional enzyme control (or heat-inactivated fGCase) would rule out non-specific nanoparticle effects. For AAV, assessment of off-target expression and potential cytotoxicity is needed.

Including inactive fGCase would confound the assessment of fGCase in MLOs by immunoblot and immunofluorescence; therefore, saposin C–DOPS was used as the control instead.

We agree that assessment of off-target expression and potential cytotoxicity for AAV is important, this will be included in future studies.

(d) Comparative efficacy lacking. It remains unclear which modality is most effective in the long term and in which cellular compartments.

To address this comment, we have added a new table (Supplementary Table 2) comparing the four therapeutic modalities and summarizing their respective outcomes. While this study focused on short-term responses as a proof-of-principle, future work will explore long-term therapeutic effects.

(e) Suggested fixes/experiments

Extend follow-up (e.g., 6+ weeks) after AAV/SapC dosing and evaluate DA markers, electrophysiology, and lipid levels over time.

We appreciate the reviewer’s suggestions. The therapeutic testing in patient-derived MLOs was designed as a proof-of-principle study to demonstrate feasibility and the primary response (rescue of GCase function) to the treatment. A comprehensive, long-term therapeutic evaluation of AAV and SapC-DOPS-fGCase is indeed important for a complete assessment; however, this represents a separate therapeutic study and is beyond the scope of the current work.

Quantify AAV transduction by qPCR for vector genomes and by cell-type quantification of GFP+ cells (neurons vs astrocytes vs progenitors).

For the AAV-treated experiments, we agree that measuring AAV copy number and GFP expression would provide additional information. However, the primary goal of this study was to demonstrate the key therapeutic outcome, rescue of GCase function by AAV-delivered normal GCase, which is directly relevant to the treatment objective.

Include SapC-DOPS control nanoparticles loaded with an inert protein and/or fluorescent cargo quantitation to show distribution and uptake kinetics.

As noted above [see response to Weakness (3)-c], using inert GCase would confound the assessment of fGCase uptake in MLOs; therefore, it was not suitable for this study. See response above for the distribution and uptake kinetics of SapC-DOPS [see response to Weaknesses (3)-b].

Provide head-to-head comparative graphs (activity, lipid clearance, DA restoration, and durability) with statistical tests.

We have added a new table (Supplementary Table 2) providing a head-to-head comparison of the treatment effects.

(4) Model limitations not fully accounted for in interpretation

(a) Absence of microglia and vasculature limits recapitulation of neuroinflammatory responses and drug penetration, both of which are important in nGD. These absences could explain incomplete phenotypic rescues and must be emphasized when drawing conclusions about therapeutic translation.

We agree that the absence of microglia and vasculature in midbrain-like organoids represents a limitation, as we have discussed in the manuscript. In this revision, we highlighted this limitation in the Discussion section and clarified that it may contribute to incomplete phenotyping and phenotypic rescue observed in our therapeutic experiments. Additionally, we have outlined future directions to incorporate microglia and vascularization into the organoid system to better recapitulate the in vivo environment and improve translational relevance (see 7th paragraph in the Discussion).

(b) Developmental vs degenerative phenotype conflation. Many phenotypes appear during differentiation (patterning defects). The manuscript sometimes interprets these as degenerative mechanisms; the distinction must be clarified.

We appreciate the reviewer’s comments. In the revised manuscript, we have clarified that certain abnormalities, such as patterning defects observed during early differentiation, likely reflect developmental consequences of GBA1 mutations rather than degenerative processes. Conversely, phenotypes such as substrate accumulation, lysosomal dysfunction, and impaired dopaminergic maturation at later stages are interpreted as degenerative features. We have updated the Results and Discussion sections to avoid conflating developmental defects with neurodegenerative mechanisms.

(c) Suggested fixes

Tone down the language throughout (Abstract/Results/Discussion) to avoid overstatement that MLOs fully recapitulate nGD neuropathology.

The manuscript has been revised to avoid overstatements.

Add plans or pilot data (if available) for microglia incorporation or vascularization to indicate how future work will address these gaps.

The manuscript now includes further plans to address the incorporation of microglia and vascularization, described in the last two paragraphs in the Discussion. Pilot study of microglia incorporation will be reported when it is completed.

(5) Statistical and presentation issues

(a) Missing or unclear sample sizes (n). For organoid-level assays, report the number of organoids and the number of independent differentiations.

We have clarified biological replicates and differentiation in the figure legend [see response to Weaknesses (1)-b, (1)-c].

(b) Statistical assumptions not justified. Tests assume normality; where sample sizes are small, consider non-parametric tests and report exact p-values.

We have updated Statistical analysis in methods as described below:

For comparisons between two groups, data were analyzed using unpaired two-tailed Student’s t-tests when the sample size was ≥6 per group and normality was confirmed by the Shapiro-Wilk test. When the normality assumption was not met or when sample sizes were small (n < 6), the non-parametric Mann-Whitney U test was used instead. For comparisons involving three or more groups, one-way ANOVA followed by Tukey’s multiple comparison test was applied when data were normally distributed; otherwise, the nonparametric Dunn’s multiple comparison test was used. Exclusion of outliers was made based on cutoffs of the mean ±2 standard deviations. All statistical analyses were performed using GraphPad Prism 10 software. Exact p-values are reported throughout the manuscript and figures where feasible. A p-value < 0.05 was considered statistically significant.

(c) Quantification scope. Many image quantifications appear to be from selected fields of view, which are then averaged across organoids and differentiations.

In this work, quantitative immunofluorescence analyses (e.g., cell counts for FOXP1+, FOXG1+, SOX2+ and Ki67+ cells, as well as marker colocalization) were performed on at least 3–5 randomly selected non-overlapping fields of view (FOVs) per organoid section, with a minimum of 3 organoids per differentiation batch. Each FOV was imaged at consistent magnification (60x) and z-stack depth to ensure comparable sampling across conditions. Data from individual FOVs were first averaged within each organoid to obtain an organoid-level mean, and then biological replicates (independent differentiations, n ≥ 3) were averaged to generate the final group mean ± SEM. This multilevel averaging approach minimizes bias from regional heterogeneity within organoids and accounts for variability across differentiations. Representative confocal images shown in the figures were selected to accurately reflect the quantified data. We believe this standardized quantification strategy ensures robust and reproducible results while appropriately representing the 3D architecture of the organoids.

In the revision, we have clarified the method used for image analysis of sectioned MLOs as below:

Quantitative immunofluorescence analyses (e.g., cell counts for FOXP1+, FOXG1+, SOX2+ and Ki67+ cells, as well as marker colocalization) were performed using ImageJ (NIH) on at least 3–5 randomly selected non-overlapping fields of view (FOVs) per organoid section, with a minimum of 3 organoids per differentiation batch. Each FOV was imaged at consistent magnification (60x) and z-stack depth to ensure comparable sampling across conditions. Data from individual FOVs were first averaged within each organoid to obtain an organoid-level mean, and then biological replicates (independent differentiations, n ≥ 3) were averaged to generate the final group mean ± SEM.

(d) RNA-seq QC and deposition. Provide mapping rates, batch correction details, and ensure the GEO accession is active. Include these in Methods/Supplement.

RNA-seq data are from same batch. The mapping rate is >90%. GEO accession will be active upon publication. These were included in the Methods.

(e) Suggested fixes

Add a table summarizing biological replicates, technical replicates, and statistical tests used for each figure panel.

We have revised the figure legends to include replicates for each figure and statistical tests [see response in weaknesses (1)-b, (1)-c].

Recompute statistics where appropriate (non-parametric if N is small) and report effect sizes and confidence intervals.

Statistical analysis method is provided in the revision [see response in Weaknesses (5)-b].

(6) Minor comments and clarifications

(a) The authors should validate midbrain identity further with additional regional markers (EN1, OTX2) and show absence/low expression of forebrain markers (FOXG1) across replicates.

We validated the MLO identity by 1) FOXG1 and 2) EN1. FOXG1 was barely detectable in Wk8 75.1_MLO but highly present in ‘age-matched’ cerebral organoid (CO), suggesting our culturing method is midbrain region-oriented. In nGD MLO, FOXG1 expression is significantly higher than 75.1_MLO, indicating that there was aberrant anterior-posterior brain specification, consistent with the transcriptomic dysregulation observed in our RNA-seq data.

To further confirm midbrain identity, we examined the expression of EN1, an established midbrain-specific marker. Quantitative RT-PCR analysis demonstrated that EN1 expression increased progressively during differentiation in both WT-75.1 and nGD2-1260 MLOs at weeks 3 and 8 (Author response image 1). EN1 reached 34-fold and 373-fold higher levels than in WT-75.1 iPSCs at weeks 3 and 8, respectively, in WT-75.1 MLOs. In nGD MLOs, although EN1 expression showed a modest reduction at week 8, the levels were not significantly different from those observed in age-matched WT-75.1 MLOs (p > 0.05, ns).

Author response image 1.

qRT-PCR quantification of midbrain progenitor marker EN1 expression in WT-75.1 and GD2-1260 MLOs at Wk3 and Wk8. Data was normalized to WT-75.1 hiPSC cells and presented as mean ± SEM (n = 3-4 MLOs per group). ns, not significant.

(b) Extracellular dopamine ELISA should be complemented with intracellular dopamine or TH+ neuron counts normalized per organoid or per total neurons.

We quantified TH expression at both the mRNA level (Fig. 3F) and the protein level (Fig. 3G/H) from whole-organoid lysates, which provides a more consistent and integrative measure across samples. These TH expression levels correlated well with the corresponding extracellular (medium) dopamine concentrations for each genotype. In contrast, TH⁺ neuron counts may not reliably reflect total cellular dopamine levels because the number of cells captured on each organoid section varies substantially, making normalization difficult. Measuring intracellular dopamine is an alternative approach that will be considered in future studies.

(c) For CRISPR editing: the authors should report off-target analysis (GUIDE-seq or targeted sequencing of predicted off-targets) or at least in-silico off-target score and sequencing coverage of the edited locus. (off-target analysis (GUIDE-seq or targeted sequencing of predicted off-targets) or at least in-silico off-target score and sequencing coverage of the edited locus).

The off-target effect was analyzed during gene editing and the chance to target other off-targets is low due to low off-target scores ranked based on the MIT Specificity Score analysis. The related method was also updated as stated below:

“The chance to target other off-targets is low due to low off-target scores ranked based on the MIT Specificity Score analysis (Hsu, P., Scott, D., Weinstein, J. et al. DNA targeting specificity of RNA-guided Cas9 nucleases. Nat Biotechnol 31, 827–832 (2013). https://doi.org/10.1038/nbt.2647).”

(d) It should be clarified as to whether lipidomics normalization is to total protein per organoid or per cell, and include representative LC-MS chromatograms or method QC.

The normalization was to the protein of organoid lysate. This was clarified in the Methods section in the revision as stated below:

“The GluCer and GluSph levels in MLO were normalized to total MLO protein (mg) that were used for glycosphingolipids analyses. Protein mass was determined by BCA assay and glycosphingolipid was expressed as pmol/mg protein. Additionally, GluSph levels in the culture medium were quantified and normalized to the medium volume (pmol/mL).”

Representative LC-MS chromatograms for both normal and GD MLOs have been included in a new figure, Supplementary Figure 2.

(e) Figure legends should be improved in order to state the number of organoids, the number of differentiations, and the exact statistical tests used (including multiplecomparison corrections).

This was addressed above [see response to Weaknesses (1)-b and (5)-b].

(f) In the title, the authors state "reveal disease mechanisms", but the studies mainly exhibit functional changes. They should consider toning down the statement.

The title was revised to: Patient-Specific Midbrain Organoids with CRISPR Correction Recapitulate Neuronopathic Gaucher Disease Phenotypes and Enable Evaluation of Novel Therapies

(7) Recommendations

This reviewer recommends a major revision. The manuscript presents substantial novelty and strong potential impact but requires additional experimental validation and clearer, more conservative interpretation. Key items to address are:

(a) Strengthening genetic and biological replication (additional lines or replicate differentiations).

This was addressed above [see response to Weaknesses (1)-a, (1)-b, (1)-c].

(b) Adding functional mechanistic validation for major pathways (Wnt/mTOR/autophagy) and providing autophagy flux data.

(c) Including at least one neuronal functional readout (calcium imaging/MEA/patch) to demonstrate functional rescue.

As addressed above [see response to Weaknesses (2)], the suggested experiments in b) and c) would provide additional insights into this study and we will consider them in future work.

(d) Deepening therapeutic characterization (dose, biodistribution, durability) and including specificity controls.

This was addressed above [see response to Weaknesses (3)-a to e].

(e) Improving statistical reporting and explicitly stating biological replicate structure.

This was addressed above [see response to Weaknesses (1)-b, (5)-b].

Reviewer #2 (Public review):

Sun et al. have developed a midbrain-like organoid (MLO) model for neuronopathic Gaucher disease (nGD). The MLOs recapitulate several features of nGD molecular pathology, including reduced GCase activity, sphingolipid accumulation, and impaired dopaminergic neuron development. They also characterize the transcriptome in the MLO nGD model. CRISPR correction of one of the GBA1 mutant alleles rescues most of the nGD molecular phenotypes. The MLO model was further deployed in proof-of-principle studies of investigational nGD therapies, including SapC-DOPS nanovesicles, AAV9-mediated GBA1 gene delivery, and substrate-reduction therapy (GZ452). This patient-specific 3D model provides a new platform for studying nGD mechanisms and accelerating therapy development. Overall, only modest weaknesses are noted.

We thank the reviewer for the supportive remarks.

Reviewer #3 (Public review):

Summary:

In this study, the authors describe modeling of neuronopathic Gaucher disease (nGD) using midbrain-like organoids (MLOs) derived from hiPSCs carrying GBA1 L444P/P415R or L444P/RecNciI variants. These MLOs recapitulate several disease features, including GCase deficiency, reduced enzymatic activity, lipid substrate accumulation, and impaired dopaminergic neuron differentiation. Correction of the GBA1 L444P variant restored GCase activity, normalized lipid metabolism, and rescued dopaminergic neuronal defects, confirming its pathogenic role in the MLO model. The authors further leveraged this system to evaluate therapeutic strategies, including: (i) SapC-DOPS nanovesicles for GCase delivery, (ii) AAV9-mediated GBA1 gene therapy, and (iii) GZ452, a glucosylceramide synthase inhibitor. These treatments reduced lipid accumulation and ameliorated autophagic, lysosomal, and neurodevelopmental abnormalities.

Strengths:

This manuscript demonstrates that nGD patient-derived MLOs can serve as an additional platform for investigating nGD mechanisms and advancing therapeutic development.

Comments:

(1) It is interesting that GBA1 L444P/P415R MLOs show defects in midbrain patterning and dopaminergic neuron differentiation (Figure 3). One might wonder whether these abnormalities are specific to the combination of L444P and P415R variants or represent a general consequence of GBA1 loss. Do GBA1 L444P/RecNciI (GD2-10-257) MLOs also exhibit similar defects?

We observed reduced dopaminergic neuron marker TH expression in GBA1 L444P/RecNciI (GD2-10-257) MLOs, suggesting that this line also exhibits defects in dopaminergic neuron differentiation. These data are provided in a new Supplementary Fig. 4E, and are summarized in new Supplementary Table 2 in the revision.

(2) In Supplementary Figure 3, the authors examined GCase localization in SapC-DOPSfGCase-treated nGD MLOs. These data indicate that GCase is delivered to TH⁺ neurons, GFAP⁺ glia, and various other unidentified cell types. In fruit flies, the GBA1 ortholog, Gba1b, is only expressed in glia (PMID: 35857503; 35961319). Neuronally produced GluCer is transferred to glia for GBA1-mediated degradation. These findings raise an important question: in wild-type MLOs, which cell type(s) normally express GBA1? Are they dopaminergic neurons, astrocytes, or other cell types?

All cell types in wild-type MLOs are expected to express GBA1, as it is a housekeeping gene broadly expressed across neurons, astrocytes, and other brain cell types. Its lysosomal function is essential for cellular homeostasis and is therefore not restricted to any specific lineage. (https://www.proteinatlas.org/ENSG00000177628GBA1/brain/midbrain).

(3) The authors may consider switching Figures 2 and 3 so that the differentiation defects observed in nGD MLOs (Figure 3) are presented before the analysis of other phenotypic abnormalities, including the various transcriptional changes (Figure 2).

We appreciate the reviewer’s suggestion; however, we respectfully prefer to retain the current order of Figures 2 and 3, as we believe this structure provides the clearest narrative flow. Figure 2 establishes the core biochemical hallmarks: reduced GCase activity, substrate accumulation, and global transcriptomic dysregulation (1,429 DEGs enriched in neural development, WNT signaling, and lysosomal pathways), which together provide essential molecular context for studying the specific cellular differentiation defects presented in Figure 3. Presenting the broader disease landscape first creates a coherent mechanistic link to the subsequent analyses of midbrain patterning and dopaminergic neuron impairment.

To enhance readability, we have added a brief transitional sentence at the start of the Figure 3 paragraph: “Building on the molecular and transcriptomic hallmarks of GCase deficiency observed in nGD MLOs (Figure 2), we next investigated the impact on midbrain patterning and dopaminergic neuron differentiation (Figure 3).”

Recommendations for the authors:

Reviewing Editor Comments:

Your paper has been reviewed by three expert reviewers in the GBA field. Although they appreciate the work and its novelty, they raise several concerns. We suggest that you to address these concerns in the next version.

Reviewer #1 (Recommendations for the authors):

Statistical and presentation issues

(1) Missing or unclear sample sizes (n). For organoid-level assays, report the number of organoids and the number of independent differentiations.

This was addressed above [see response to Reviewer 1 Weaknesses (1)- b].

(2) Statistical assumptions not justified. Tests assume normality; where sample sizes are small, consider non-parametric tests and report exact p-values.

We have updated methods to describe the Statistical analysis details [see response to Reviewer 1 Weaknesses (5)-b].

(3) Quantification scope. Many image quantifications appear to be from selected fields of view, which are then averaged across organoids and differentiations.

This was addressed above [see response to Reviewer 1 Weaknesses (5)- c].

(4) RNA-seq QC and deposition. Provide mapping rates, batch correction details, and ensure the GEO accession is active. Include these in Methods/Supplement.

Our RNA-seq data were generated from a single batch of MLOs, with mapping rates exceeding 90%. The GEO accession will be made publicly available upon publication.

Reviewer #2 (Recommendations for the authors):

Please consider the following suggestions for revisions:

(1) Line 86: A bit more explanation/justification for the focus on midbrain-like organoids would be helpful, including introducing the nature of the midbrain pathology to better put some of the MLO findings in context. Is the nGD pathology for the midbrain significantly different / out of proportion to other affected brain regions?

nGD Patients often display impaired vertical gaze and movement disorders. These symptoms correlate with midbrain involvement due to the sensitivity of this region to neuroinflammatory and degenerative processes (Ref #7, #8). Both human and mouse studies indicate that the midbrain exhibits prominent substrate accumulation compared to other brain regions, suggesting a predisposition for greater pathological involvement in GD midbrain (Ref #8, #9, #10, #11). This rationale was added to Line 86 in the revision.

References:

(7) Goker-Alpan O, Ivanova MM. Neuronopathic Gaucher disease: Rare in the West, common in the East. J Inherit Metab Dis.(2024) 47(5):917-934. PMID: 38768609.

(8) Burrow TA, Sun Y, Prada CE, Bailey L, Zhang W, Brewer A, Wu SW, Setchell KDR, Witte D, Cohen MB, Grabowski GA. CNS, lung, and lymph node involvement in Gaucher disease type 3 after 11 years of therapy: clinical, histopathologic, and biochemical findings. Mol Genet Metab. (2015) 114(2):233-241. PMID: 25219293.

(9) Tamar Farfel-Becker, Einat B. Vitner, Samuel L. Kelly, Jessica R. Bame, Jingjing Duan, Vera Shinder, Alfred H. Merrill, Kostantin Dobrenis, Anthony H. Futerman. Neuronal accumulation of glucosylceramide in a mouse model of neuronopathic Gaucher disease leads to neurodegeneration, Human Molecular Genetics, (2014). Volume 23, Issue 4, Pages 843–854.

(10) E. Ellen Jones, Wujuan Zhang, Xueheng Zhao, Cristine Quiason , Stephanie Dale, Sheerin Shahidi-Latham, Gregory A. Grabowski, Kenneth D. R. Setchell, Richard R. Drake, and Ying Sun. High-Resolution MALDI Imaging Mass Spectrometry. SLAS Discovery (2017). Vol. 22(10) 1218–1228

(11) Xu YH, Xu K, Sun Y, Liou B, Quinn B, Li RH, Xue L, Zhang W, Setchell KD, Witte D, Grabowski GA. Multiple pathogenic proteins implicated in neuronopathic Gaucher disease mice. Hum Mol Genet. (2014) 23(15):3943-57. PMID: 24599400.

(2) Lines 359-360: Please specify the carbon-chain length of the sphingoid base of the GluCer species analyzed. Also, is there a citation for the statement that 18:0 and 16:0 are "brain-enriched species"?

The carbon-chain length analyzed ranges from 14:0 to 24:0. The sphingoid base for all GluCer species analyzed is d18:1. For example, the species referred to as GluCer 18:0 corresponds to GluCer(d18:1/18:0). Although both, 16:0 and 18:0 are enriched in the brain, 18:0 is the most abundant species in the brain (Ref #12, #13). We revised "brain-enriched species” to “brain-predominant species (18:0)”.

References:

(12) Nilsson, O., and Svennerholm, L. Accumulation of Glucosylceramide and Glucosylsphingosine (Psychosine) in Cerebrum and Cerebellum in Infantile and Juvenile Gaucher Disease. Journal of Neurochemistry (1982) 39, 709–718.

(13) Sun, Y., Zhang, W., Xu, Y.H., Quinn, B., Dasgupta, N., Liou, B., Setchell, K.D., and Grabowski, G.A. Substrate compositional variation with tissue/region and Gba1 mutations in mouse models--implications for Gaucher disease. PLoS One (2013). 8, e57560.10.1371/journal.pone.0057560.

(3) Figure 2: It would be interesting to compare the MLO findings to prior gene expression data. Are there previously published transcriptome analyses from nGD brain tissue (or other tissues) that the transcriptome data obtained from MLOs may be compared with? What about transcriptome analyses of mouse GD models?

We thank the reviewer for this valuable suggestion. To strengthen the biological context of our transcriptomic findings, we have added a new comparative table (new Supplementary Table 3) in the revised manuscript that summarizes key dysregulated pathways in our human nGD MLOs alongside previously published data from nGD mouse midbrain (Ref#14). The table highlights substantial overlap, including axon guidance, neuron differentiation, dopaminergic/glutamatergic/GABAergic synaptic signaling, lipid metabolism, apoptosis/cell death, and nervous system development, emphasizing the translational relevance of our model. We also note that our dataset uniquely reveals pronounced dysregulation of WNT signaling and anterior-posterior patterning (Fig. 2L and 2M), potentially reflecting human-specific early midbrain defects.

We added the following sentence to Discussion: “Comparative analysis with prior transcriptomic data from nGD mouse midbrain showed consistent dysregulation in axon guidance, synaptic signaling, lipid metabolism, and nervous system development (new Supplementary Table 3), supporting the fidelity of our human MLO model.”

Reference:

(14) Dasgupta N, Xu YH, Li R, Peng Y, Pandey MK, Tinch SL, Liou B, Inskeep V, Zhang W, Setchell KD, Keddache M, Grabowski GA, Sun Y. Neuronopathic Gaucher disease: dysregulated mRNAs and miRNAs in brain pathogenesis and effects of pharmacologic chaperone treatment in a mouse model. Hum Mol Genet. (2015) 24(24):7031-48. PMID: 26420838.

(4) Lines 402-405 & Figure 3D: Is it possible to include a merged image to better visualize the TH and FOXA2 co-staining / potential colocalization?

The merged images of TH (red) and FOXA2 (green) are shown in Fig. 3E. Yellow arrows indicate TH and FOXA2 co-stained cells, which appear yellow in the merged images. The results demonstrate that the number of co-stained cells is reduced in GD2-1260 MLOs compared with WT-75.1 MLOs at both, week 6 and week 8.

(5) Lines 447-448 & Figure 4F, G, J: It would be helpful to provide a direct analysis/visualization of MLO size between the WT-75.1, GD2-1260, and iso-GD2-1260 genotypes (allowing direct comparison of WT and iso). Similarly, the same 3-way analysis would be valuable for assessing dopamine levels.

We have included WT-75.1 in Fig. 4 F/G/J in the revision. All three genotypes, WT-75.1, GD2-1260, and iso-GD2-1260, are presented for analysis compared to WT-75.1. In new Figure 4F, MLO growth is presented by representative MLO images taken under wide field microscopy at day 2, Wk4 and Wk8 of differentiation. In new Fig. 4G, MLOs size was analyzed by NIS elements and presented as the area (µm²) of MLO in image (mean ± SEM). N≥10 MLOs were analyzed for each genotype. In new Fig. 4J. Dopamine levels in MLO culture medium from WT-75.1, GD2-1260 and iso- GD2-1260 MLOs at Wk12 cultured in 3 mL BGM medium for 72 hours were analyzed. Data are presented as mean ± SEM (n = 5 per group). Statistical analysis applied was described in the legend.

(6) Figure 4: What is the explanation/interpretation of the residual autophagy pathway dysfunction in CRISPR-corrected MLOs? nGD requires near-complete loss of GCase activity, so it is a bit curious that autophagic dysfunction would be observed with only ~50% GCase reduction? There is some discussion, but it doesn't fully capture the unexpected nature and implications of this result.

This phenomenon may be explained by a threshold effect in lysosomal function. Gaucher disease is an autosomal recessive disorder. The carriers with heterozygous GBA1 mutation, who retain approximately 50% of normal GCase activity, do not develop disease. This suggests that even partial restoration of GCase activity can reduce glucosylceramide accumulation below a pathological threshold, thereby restoring lysosomal integrity and autophagic flux. In addition, improved GCase activity may help normalize the lipid composition of lysosomal membranes, facilitating the fusion events required for effective autophagy.

(7) Lines 512-516 & Figure 5J: The data shown are inconclusive. Can these Western blot data be quantified, noting the number of replicates for each measurement? Without quantification and statistics, it is difficult to assess the claim that levels of LAMP1, LC3-I, LC3-II, 4E-BP1, and p-4E-BP1 in GD2-1260 treated with SapC-DOPS-fGCase are more similar to GD2-1260 treated following SapC-DOPS than to WT-75.1.

We performed quantitative analysis by comparing WT-75.1 and included the data in new Fig. 5J. The result was revised as:

Analysis of protein levels showed that decreased LAMP1 expression in GD2 1260 MLOs was not altered following SapC DOPS fGCase treatment (Figure 5J). The elevated LC3-II levels, an indicator of impaired autophagic flux, were reduced upon treatment, suggesting enhanced autophagic activity (Figure 5J). Moreover, phosphorylated 4E-BP1 (Thr37/46), but not total 4E-BP1, was improved in SapC-DOPS-fGCase–treated MLOs, reflecting a decrease in mTOR hyperactivation (Figure 5J). We anticipate that a longer duration of SapC-DOPS-fGCase exposure in nGD MLOs may produce a more robust therapeutic effect in rescuing nGD-associated phenotypes, which will be evaluated in future studies.

(8) Lines 518-520: The presented data support "effective restoration of GCase activity," but clarification is needed regarding "correction of GD-related disease phenotypes." Perhaps "selected molecular and biochemical phenotypes" would be more accurate. Data are not shown for several other phenotypes, including TH, FOXA2, and dopamine levels.

This was revised to “selected molecular and biochemical phenotypes “.

(9) Figure 5D-J: Please clarify whether all experiments were conducted 48 hours after treatment, as indicated for Figure 5C. If so, does this suggest that SapC-DOPS treatment exhibits only short-term effects? Were any data collected to evaluate the persistence of the treatment effect?

The treatment duration is specified in the Fig. 5 legend. Fig. 5D–J represent experiments conducted after two weeks of treatment, whereas Fig. 5C reflects a 48-hour treatment. In both Gaucher disease lines, two-week treatment restored GCase activity to wild-type levels and reduced GluSph substrate accumulation. These findings were intended as proof-of-principle to demonstrate therapeutic feasibility; evaluation of treatment persistence beyond two weeks was beyond the scope of this study.

Minor suggestions

(1) Line 80: "A brain organoid derived from hiPSCs of a healthy individual with GBA1 knockout and α-synuclein overexpression exhibited some PD features23." I would suggest enumerating what "PD features" are to distinguish from "clinical features", which I don't think is the intended meaning.

This was revised as “exhibited characteristic PD markers”.

(2) Figure 2I: The reported number of downregulated DEGs is incorrect. It should be 765, not 1429.

This was corrected in Figure 2I.

(3) Line 359: change "enrich" to "enriched".

This word was corrected.

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

Learn more at Review Commons

Reply to the reviewers

Programmed cell death is prominent in developing nervous systems across evolution, but its function remains obscure. Recent work suggests that it might impact behavior, but an examination of its effects on behavior and underlying neuronal circuits in intact organisms has not been determined. In this manuscript we report that programmed cell death sculpts the developing nervous system and shapes innate behavior. Using synaptic labeling, in vivo calcium imaging, targeted rescue of programmed cell death, and automated high-resolution analysis of cell death mutants, we find that loss of programmed cell death alters animal behavior. These findings reveal that neuronal cell death during development provides a reservoir of fates and circuit connections that could be accessed on evolutionary time scales to modify innate behavioral programs. Our manuscript thus answers one of the major outstanding questions in developmental neuroscience—why programmed cell death is so prevalent—by identifying consequences for brain function at the subcellular, cellular, circuit, and behavioral level. This study will be of interest to those interested in evolution of the nervous system and behavior, developmental biology, and neural circuit development.

We thank the reviewers for their careful attention to the manuscript. Both reviewers were enthusiastic about the work. Here we address their suggestions. As noted below, we have already addressed most of their points, and we discuss in detail the remaining point—whether it is possible to perform experiments for a more specific targeting of the undead RIM cell death event to provide additional evidence for its role in altering reversal behavior.

2. Description of the planned revisions

*Reviewer 1: “1. The argument that that differences in reversal behavior are likely attributable to the difference in RIM neuron numbers in the ced-3 rescue studies is very plausible. Nonethless, there remains the possibility that for some reason in animals with 4 RIMs there may be a more global effect on the fate of cells slated to die, unrelated to the number of RIMs. I think there are two ways to test this. (1) quantify the behavior in 2- vs. 4- RIM neurons in animals also containing a marker for other undead neurons, and see if there is any correlation between 4 RIMs and survival of unrelated neurons (but preferably reasonably closely related by lineage- in case that's the issue). (2) Since the authors are able to distinguish the undead cells, can they perform laser ablations on these cells and assess whether behavior is restored to normal values?” *

• *We agree that this point is already very plausible. We also appreciate the reviewer’s suggestions on how to extend this conclusion.

Regarding suggestion (1): Unfortunately there is not a reliable marker for undead neurons (although a current project in the lab is indeed to develop one). However, we note that the undead RIM sister cells adopt a RIM neuron fate in 96% of ced-3 mutants, while with other undead cells investigated neuron fate adoption ranged from 59% (ASEL) to 77% (ASER). This suggests that the undead RIM fate adoption is not strongly correlated with the fates of other undead cells.

Regarding suggestion (2): We attempted to perform laser ablation of undead RIM neurons in ced-3 mutants, but we could not overcome the technical hurdles (despite our lab’s expertise in laser axotomy). We found that we could not reliably remove both undead RIMs without damaging the wildtype RIM that is in close proximity, especially in the quantities of animals necessary for behavioral experiments.

As an alternative, we plan to perform more targeted experiments to manipulate cell death in the undead RIM to address the points raised by both reviewers. Our goal is to generate two strains. In one, programmed cell death is prevented specifically in the RIM neurons in wild type animals. We hope to achieve this by either transgenic expression of a gain-of-function mutation of ced-9, or else by RIM-specific RNAi against egl-1, ced-3 or ced-4. To do this we will use the RIM promoter tdc-1, which is confined to RIM and RIC. The second strain will allow cell death to occur only in RIM (and RIC) in animals that otherwise have no cell death. Here, we will drive wild-type ced-3 or ced-4 under the tdc-1 promoter in the corresponding mutant background.

We note 2 caveats for both of these approaches: 1) RIC also has an undead sister; 2) Most probably, the tdc-1 promoter will not be active in time to block cell death. Caveat #2 is actually the reason why we did not do these experiments initially (instead we used the most specific promoter we could find that is expressed early in the RIM lineage, before RIM is born).

However, we agree that if successful these experiments would complement the existing experiments, and we will build all these strains.

Reviewer 2: “Mosaic rescue of RIM via stochastic loss of a rescue array helped demonstrate the contribution RIMu have to the locomotor phenotype. As the authors emphasise these animals have many other undead cells (outside of the reverse network). A conditional rescue of only the RIMu would greatly improve the strength of the claims made. Would a conditional RIM egl-1 knockdown (via RNAi) be possible to selectively inhibit apoptosis in those neurons. This experiment should be considered OPTIONAL. It may be that such specific promoters do not allow for egl-1 RNAi to function at the right time to rescue death.”

• *We appreciate the reviewer’s suggestion. As stated above, we are working to perform an expanded version of these exact experiments, as well as their converse. However, as the reviewer notes, it is very possible that the timing of expression will prevent these approaches from working (Caveat #2 above).

Reviewer 2: There is a slight issue with interpretation of the data with the mosaic GLR-1::tagRFP Fig 2M which reveals the postsynaptic compartment of one RIM even though there are two present. There seems to be no obvious apposition between pre/post and they somewhat seem to be floating in space. Why is this the case? One would have imagined that the structures in Fig 2L would be tiled composites of both AIB & RIM pre and postsynaptic elements coalescing. Can the authors provide an alternative explanation for this phenotype. Nevertheless, the data on Fig 2L seems solid.. that is animals with extra undead RIM cells have additional cell-type specific synaptic terminals

We have selected a different micrograph that is more representative of the RIM post-synapses in ced-3 mutants. In this animal, the array labeling the post-synapses in RIM has been lost from one of the two RIM neurons, making it easier to discern that the post-synapses are apposed to the AIM pre-synaptic marker (Fig 1M).

Reviewer 2: Clarity should be improved around the use of 'expected number' in figure 1. The description of the metric 'The 'expected number' is defined as the number of neurons of the type present in wild-type animals, plus the number of lineage-proximate undead cells.' suggests that expected (blue) regions of pie charts represents lineages with expected sum total of wt and extra undead cells. However, in reference to panel H 'The wild-type animal has two RIM neurons, and the ced-3(n717) animal has two additional RIMlike cells and is counted as contributing to the orange "more than expected" sector in panel (A)' it is said that the animals with 2 WT accompanied by each undead sister contributes to more than expected (orange) region. These appear inconsistent. Can you qualify?

We thank the reviewer for this point and have added a schematic to clarify the quantification of undead cell fates (Fig. 1).

Reviewer 2: Specific observations shown in supplemental data SI-L despite being cited in the text is not explained or formally referenced. The details of these panels should either be briefly explained/their inclusion qualified in the text or simply remove from the figure

We have added reference to these figures in the main text “Undead cells are even capable of producing complex morphology, such as the highly branched dendrites of the PVD neurons (Figure S1I-L).” (p. 3)

Reviewer 2: The dual image photomicrographs could be in green/ magenta or red/cyan to make colourblind friendly.

We have updated micrograph colors to be colorblind friendly (Fig 1K-M, S1L).

Reviewer 2: Do the authors have data with the pRIMtagRFP egl-nucGFP. If they do it would be useful to show it.

We have added a micrograph of egl-1::GFP and RIM labeled using NeuroPAL (Fig. S2A).

Reviewer 1: 2. The authors speculate, if I understand correctly, that the mechanism by which reversal frequencies are decreased in 4 RIM animals may be that the reversal state is stabilized, resulting in longer reversals and consequently fewer reversal events. This is a nice model that is testable. The authors could, for example, examine the connections of RIM neurons to the AVA neuron, a main command interneuron for reversal initiation, and assess whether there are indeed more such synapses. Furthermore, the authors can assess whether the frequency of AVA firing is decreased. Of course, there are other plausible mechanisms involving connectivity of other neurons onto AVA which could explain the phenomenon. The authors may wish to add a comment regarding this in the discussion.

• *

We thank the reviewer for this suggestion. There are multiple postsynaptic receptors expressed in AVA for RIM neurotransmitters and the contribution of each to reversal behavior is still being debated, making it challenging to dissect the contribution of each of these to the effects on reversal behavior mediated by the undead RIM. Given this, we believe that addressing this point experimentally is beyond the scope of this paper. We have added a sentence in the discussion commenting on this as a future direction for this work “The mechanism of the downstream circuit mediating the effects of the undead RIM could be determined through quantification of AVA postsynaptic receptors and examining reversal behavior of cell death mutants with knockouts of AVA receptors.”

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

Learn more at Review Commons

Reply to the reviewers

1. General Statement We thank all three reviewers for their careful and constructive evaluation of our manuscript. We are pleased that the reviewers recognised the importance of the work we describe and found the experimental approach sound.

This manuscript reports that undesired insertion of the plasmid backbone, including vector sequences not intended to be part of the genome edit, occurs at high frequency during CRISPR/Cas9-mediated HDR in Drosophila. We document this phenomenon across multiple independent genome editing projects, using three different plasmid backbones and targeting distinct genomic loci, demonstrating that it is not an isolated or project-specific artefact. We further introduce pVID, a new donor vector incorporating a ZsGreen negative selection marker that allows straightforward identification and exclusion of lines carrying undesired insertions, providing a practical solution to avoid this genome editing issue.

In response to the reviewers' comments, we have revised the manuscript to: (i) correct and contextualise prior descriptions of this problem, incorporating the references suggested by Reviewer 2; (ii) add a table summarising gRNA characteristics for all editing projects; (iii) expand the discussion of the underlying DNA repair mechanisms, the potential influence of Cas9 source choice, and the relevance of the findings beyond Drosophila; (iv) confirm the stability of problematic template vector insertions across multiple generations; and (v) improve figure clarity, correct typographical errors, and clarify several passages flagged by the reviewers. All responses are described in detail below.

1. Point-by-Point Description of the Revisions

   Reviewer 1

   Major Comment 1 — DNA repair pathways underlying backbone capture • I think the authors should discuss potential DNA repair pathways (e.g., NHEJ, MMEJ) underlying plasmid backbone capture in more detail. Did you check for knockouts within your screened transformants? That could provide insight into the underlying mechanisms.

Response: We screened humanized TDP-43 line for tbph knockouts, since our aim was to fully knock out the Drosophila gene and insert the human ortholog. However, we did not screen any of the other lines described in the manuscript for indels caused by NHEJ, since the dsRed selection we employed would not enable us to recover lines without insertion events. We hypothesise that one of the two gRNAs used being more inefficient than the other causes a single homologous recombination event and insertion of the vector template. However, the underlying mechanism is still unclear, and could be caused by NHEJ, HDR or a combination of these mechanisms as has previously observed (44). We have expanded on potential mechanisms inducing HDR template vector insertion events in the discussion of the revised manuscript.

Major Comment 2 — gRNA characteristics and design parameters • It would be important to describe gRNA characteristics and general design parameters (GC content, distance from cut to intended edit, homology arm length) and analyze whether these correlate with correct HDR vs. plasmid insertion. A table summarizing these details could help reveal potential trends.

Response: At the reviewers suggestion, we have added a table (Table 1) describing the all the characteristics of the gRNAs further in the material and method section. Unfortunately though, no commonality was immediately apparent to us.

Major Comment 3 — Single versus dual gRNA strategies • Did the authors consider exploring whether using a single gRNA reduces backbone insertion frequency compared to dual-gRNA strategies? I understand that two gRNAs are needed for your strategy, but it would be interesting to know whether these outcomes are linked to the dual-gRNA design.

Response: As stated in the discussion, we theorize that perhaps one of the two gRNAs used in our strategies cuts more efficiently and thereby causes a single homologous recombination event and insertion of the vector template. It is possible that originally using a strategy with only one gRNA could cause less insertion of the vector template, however this may be at the cost of gene editing efficiency. Indeed, when Ge et al (17) compared using one versus two gRNAs to induce HDR, they observed more reliable repair events when two gRNAs were used.

Major Comment 4 — Stability of backbone insertions across generations • Did you evaluate whether backbone insertions are stable across generations or prone to rearrangement?

Response: We did keep several of the lines reported in this paper stably across multiple generations, and we have added this observation to the manuscript

Major Comment 5 — Broader applicability in non-model organisms and therapeutic settings • A broader discussion of the potential applications of this approach in non-model insects, mammalian cells, or therapeutic settings where HDR is inefficient would be valuable.

Response: While we only investigated this effect in the creation of CRISPR/Cas9 Drosophila melanogaster models, it is very possible that this could also affect other model organisms or cells. We encourage the use of HDR template negative selection markers in all uses of HDR-mediated CRISPR/Cas9 genome editing.

Major Comment 6 — Cas9 promoter and expression level • The authors also mentioned using a validated Cas9 line (ref #23). What promoter drives Cas9 expression in this line? Did you consider testing different promoters? Since timing of Cas9 expression can be critical, promoter choice may have influenced the results and should be discussed.

Response: We used the nos promoter for the expression of Cas9, as this promoter is expressed in germ cells and is known to have better efficiency than the other germline promotor like vasa (Port et al 2014, Ref #23). However, it is conceivable that the high Cas9 concentration in this line could induce a higher rate of double stranded breaks and thus template vector insertion. We agree it would be interesting to test other Cas9 sources, though this would likely come at the cost of overall editing efficiency. As we describe, the use of pVID now allows negative selection against HDR template vector insertion even with this Cas9 source. We have expanded upon the potential use of other Cas9 sources in the revised discussion.

Reviewer 2

Major comments

None

Minor Comment 1 — Line 38: prior descriptions of backbone insertion in Drosophila Line 38: "this type of unwanted template vector insertion in the case of Drosophila genome editing has to our knowledge not been previously described." Insertion of vector sequences after CRISPR editing in Drosophila and strategies to mitigate such events have been previously described in multiple studies. The authors need to incorporate these into their manuscript. https://doi.org/10.1242/bio.20147682, https://doi.org/10.1080/19336934.2020.1832416, https://doi.org/10.1534/g3.116.032557.

Response: We are very grateful to the reviewer for pointing out these prior observations of vector insertion events of which we were not aware. This prior work has now been fully incorporated and referenced in the revised manuscript, and we have removed this erroneous statement. We feel this manuscript validates and quantifies the extent of HDR template insertion across multiple genome editing strategies and templates plus, with pVID, provides a solution to this vexing problem.

Minor Comment 2 — Line 79: PAM sequence sentence I have difficulties understanding the following sentence: Line 79: "At this location, on both sides of the insertion, the PAM sequence of the target region was edited to match the PAM sequence of the template donor plasmid." I assume what is meant here is that in the donor vector the PAM sequence was mutated to prevent recutting, but that means this sequence is no longer a PAM. Please rephrase for added clarity.

Response: The PAM sequence was indeed edited in the template donor plasmid to prevent re-cutting, and we are referring to this edited version of the PAM sequence in this sentence. We edited this sentence this to clarify that the PAM sequences have been edited.

Minor Comment 3 — Figure 2: panel D arrangement In Figure 2 panel D is arranged between panels E and F.

Response: Thank you for pointing this out. We have corrected this error.

Minor Comment 4 — Primer positions in figures In Figure 2 it would be useful to also indicate the position of the primers used in 2d in the schematic in 2e. The same applies to Fig. 3a and 4a.

Response: We have added the position of the primers in figure 2. Since the primers are targeting the backbone of the plasmid commonly in all projects included in this manuscript, we have chosen to only include one figure of this (figure 2).

Minor Comment 5 — Lines 89–90: duplicated sentence Lines 89, 90: Duplication of the same sentence.

Response: Thank you, we have corrected this mistake.

Minor Comment 6 — VGAT editing: consecutive editing and sgRNA placement Editing of the VGAT gene: In this case correct editing and plasmid insertions could be found on the same chromosomes. This might be caused by concatemer formation of repair intermediates (as has been described in multiple systems) or by consecutive editing events. Can you please specify whether the donor vector was designed to prevent consecutive editing? I'm also a bit confused about the locations of the sgRNA target sites according to Fig. 3a. It appears that part of the insertion (i.e. the ALFA tag) was encoded on the homology arm and not between the target sites. While such strategies have been described, they are often avoided as the efficiency of insertion decreases with increasing distance to the cut site. Was it not possible to us a sgRNA better matching the insertion cassette?

Response: For Vgat genome editing, we followed an existing strategy that has been proven effective, reusing the same gRNAs and overall approach to replace the 9×V5 tag with a 1×ALFA tag (Certel et al. 2022, Ref #28)

Minor Comment 7 — Line 133: mini-white marker unreliability Line 133: Please describe why the mini-white marker was unreliable.

Response: In our first design of the pVID vector, we used mini-white as the negative selection marker. However in a number of white eyed lines, we could still confirm the undesired insertion of the HDR template vector. We speculate that expression of mini-white (which we confirmed was not mutated) was repressed in these lines by an unknown mechanism. Since (Nyberg et al. 2020 , Ref #35) also proposed using mini-white as a negative vector selection marker, we wanted to mention this problem with mini-white negative selection, though we remain unsure of the exact cause. In any case, the use of exogenous ZsGreen in pVID as described in the manuscript fully resolved the issue allowing reliable detection of template vector insertion events as we describe.

Minor Comment 8 — Line 161: "varying frequency" Not sure I understand the sentence in line 161: If 54% of lines had vector insertion, what does the "varying frequency" refer to?

Response: We have edited this sentence to clarify that 54% of lines had vector insertion.

Minor Comment 9 — pVID availability in methods Consider highlighting the availability of pVID also in the methods section that described this plasmid.

Response: This has been added to the methods section.

Reviewer 3 No edits suggested.

We thank Reviewer 3 for their positive assessment of the manuscript and for confirming that no revisions are required.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This foundational study builds on prior work from this group to reveal the complexities underlying ligand-dependent RXRγ-Nur77 heterodimer formation, offering a compelling re-evaluation of their earlier conclusions. The authors examine how a library of RXR ligands influences the biophysical, structural, and functional properties of Nur77. They find that although the Nur77-RXRγ heterodimer shares notable functional similarities with the Nurr1-RXRα complex, it also exhibits unique features, notably, both dimer dissociation and classical agonist-driven activities. This work advances our understanding of the nuanced behaviors of nuclear receptor heterodimers, which have important implications for health and disease.

Strengths:

(1) Builds on previous work by providing a comprehensive analysis that examines whether Nur77-RXRγ heterodimer formation parallels that of the Nurr1-RXRα complex.

(2) Systematic evaluation of a library of RXR ligands provides a broad survey of functional outputs.

(3) Careful reanalysis of previous work sheds new light on how NR4A heterodimers function.

We thank the reviewer for recognizing our work as foundational. In the nuclear receptor field, current understanding of ligand-regulated nuclear receptor activity is based largely on ligand-dependent coregulator recruitment preferences; for example, agonists enhance coactivator recruitment to activate transcription. Building on our recent study of Nurr1-RXRα, the present work suggests that activation of the evolutionarily related NR4A-RXR heterodimer Nur77-RXRγ by RXR ligands is also consistent with a non-classical activation mechanism involving heterodimer dissociation.

Weaknesses:

(1) Some conclusions appear overstated or are not well substantiated by the work presented. It's unclear how the data support a non-classical mode of agonism, for example, based on the data shown.

We thank the reviewer for this important point. We did not intend to claim that Nur77-RXRγ activation is explained exclusively by a non-classical mode of agonism. Rather, our interpretation was that the data are consistent with two possible, non-mutually exclusive mechanisms: (1) a classical pharmacological mechanism involving ligand-dependent coregulator recruitment; and (2) a non-classical mechanism involving ligand-binding domain (LBD) heterodimer dissociation, as we previously described for Nurr1-RXRα. This differs from our prior eLife study of Nurr1-RXRα, in which the data supported the LBD heterodimer dissociation model but not the classical pharmacological model.

In our revised manuscript, we clarify two points that are important for interpreting the Nur77-RXRγ data. First, several experimental limitations of the Nur77-RXRγ studies reduced the extent to which the mechanism could be resolved as rigorously as in our earlier Nurr1-RXRα study. Second, and more importantly, the currently available ligand set lacks Nur77-RXRγ-selective agonists. This limits our ability to determine whether LBD heterodimer dissociation is the sole or principal mechanism of activation, or instead one of several contributing mechanisms.

Taken together, these results support LBD heterodimer dissociation as a plausible and experimentally observable component of Nur77-RXRγ activation and, therefore, as a candidate shared activation mechanism for NR4A-RXR heterodimers. At the same time, because the quantitative evidence is less definitive than in the Nurr1-RXRα system, we agree that conclusions regarding Nur77-RXRγ should be stated more cautiously. This caution is reflected in both the title of our manuscript (“Towards a unified mechanism…”) and the language used throughout the text.

(2) Some assays have relatively few replicates, with only two in some cases.

We thank the reviewer for their attention to experimental rigor. For some assays, the findings were reproduced in two independent experiments, which we considered sufficient to confirm the presence and reproducibility of the effects observed in those particular assay formats. In the original manuscript, we used a general statement in the figure legends (“representative of two or more independent experiments”) across all assay data. In the revised manuscript, we now specify the number of independent experimental replicates for each assay in the corresponding figure legends to improve transparency.

Reviewer #2 (Public review):

Summary:

This study explores the mechanisms by which binding of the nuclear receptor RXRg regulates its heterodimeric partner Nur77. Previously, this group made the interesting discovery that ligand-dependent activation of RXRg bound to a related partner, Nurr1, does not occur through a classical pharmacological mechanism but through agonist-dependent dissociation of the complex through disruption of their ligand binding domain (LBD) interactions. Here, they revisit this paradigm with Nur77. In contrast to Nurr1, the authors do not have the reagents to clearly support a role for LBD dissociation. Following the model of partial ligand-dependent dissociation of the LBD heterodimer, the experimental data (NMR, ITC, SEC) are interesting and quite complex.

Strengths:

The authors do a rigorous job of describing the data and providing possible interpretations and caveats. Revisiting the analysis of Nurr1, they identify the crucial role that selective Nurr1-RXRg agonists played in supporting the LBD dissociation model; without analogous compounds for the Nur77-RXRg complex, it is difficult to invoke this mechanism. Interestingly, treatment with the Nurr1-RXRg selective agonist HX600 suggests it can induce some LBD dissociation. Therefore, there may be some similarities between the regulation of Nurr1 and Nur77 by RXRg.

We thank the reviewer for this thoughtful and balanced summary of our work. We appreciate the reviewer’s recognition of both our prior findings in the Nurr1-RXRα system and the interesting, but more complex, experimental behavior observed here for Nur77-RXRγ. We agree that the absence of Nur77-RXRγ-selective agonists currently limits how definitively the contribution of LBD dissociation can be resolved, and we have revised the manuscript to make this point more explicit and to further temper our conclusions accordingly.

Weaknesses:

Despite evidence supporting a partial role for RXRg LBD dissociation as a mechanism to activate Nur77, other data demonstrate that a fundamentally different regulatory mechanism likely exists in the Nur77-RXRg complex that involves the RXRg disordered NTD. The decision to describe further study of this as outside the scope of this work is unfortunate, as it closed off an avenue that could have provided fruitful data informing the apparently distinct regulatory mechanisms of the Nur77-RXRg complex. Given the uncertainty in the importance of the partial roles of the pharmacological mechanism, LBD dissociation, and the RXRg NTD, this study may have limited impact on the field.

We thank the reviewer for this thoughtful point. We agree that the RXRγ NTD likely contributes to regulation of Nur77-RXRγ transcription, and that our truncation data suggest that regions outside the LBD can influence transcriptional output. At present, however, the effect of RXRγ NTD truncation is not sufficiently mechanistically resolved to distinguish among several plausible explanations.

For example, the RXRγ NTD has been implicated in phase separation and biomolecular condensate formation in cells (PubMed ID 40392852, 40420113, 33971237, 31881311), and perturbing these properties (via RXRγ NTD truncation) could indirectly affect Nur77-RXRγ transcriptional activity. In addition, NTDs of nuclear receptors can participate in coactivator or corepressor interactions (PubMed ID 24284822), raising the possibility that removal of the RXRγ NTD alters transcription by changing recruitment of regulatory factors rather than by directly informing the LBD-centered mechanism examined here. We will clarify in the revised manuscript that these possibilities remain unresolved and represent important directions for future study.

We also agree that defining how multiple RXRγ domains contribute to Nur77-RXRγ regulation would be valuable for the field. However, the focus of the present study is narrower: to test whether, as in our previous eLife study of Nurr1-RXRα, RXR ligands can influence heterodimer function through effects on LBD-LBD interactions. Because the available data do not yet allow a mechanistic dissection of the RXRγ NTD contribution, we believe that a definitive analysis of this question would require a separate set of experiments beyond the scope of the present work. We have revised the manuscript to better acknowledge this limitation and to frame the conclusions accordingly.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Overall, this is a compelling body of work. Additional summary statements and clearer transitions would be helpful throughout.

Here are some points that should be addressed or at least discussed by the authors:

(1) It is unclear in the luciferase assays whether the truncated proteins are functional or not. Were there Western blots or other assays run to confirm protein concentrations?

We thank the reviewer for this point. We did not perform Western blotting or other assays to confirm equivalent expression levels of the truncated RXRγ constructs, and we agree that this is a limitation of the luciferase assay data. As a result, the transcriptional effects observed with the truncation constructs should be interpreted cautiously.

With that said, the increased transcriptional activity observed upon deletion of the RXRγ NTD/AF-1 region suggests that this region may exert a repressive effect on Nur77-RXRγ transcription. This effect could reflect multiple, non-mutually exclusive mechanisms, including altered phase separation or condensate-related properties of RXRγ, or altered recruitment of transcriptional coregulators through the NTD. Because our truncation strategy does not distinguish among these possibilities, we do not believe these data allow a definitive mechanistic interpretation of the NTD contribution.

We have revised the manuscript to clarify this limitation. We also note that the primary focus of the present study is the role of ligands in modulating Nur77-RXRγ function through LBD-mediated interactions, in direct comparison with our previous Nurr1-RXRα study. A more complete mechanistic dissection of how RXRγ domain architecture influences Nur77-RXRγ transcription will require future work.

(2) Why does the Nur77 construct lacking the NTD show increased luciferase activity?

Please see our response above to Reviewer 2’s Public Review, which also addresses this point.

(3) A case is made for the Nur77 LBD driving the activity, but it also could be inferred that the DBD is driving based on the data shown in Figure 1.

We thank the reviewer for this point. We agree that the Nur77 DBD is required for binding to NBRE response elements, and we did not intend to suggest otherwise. The experimental approach in Figure 1 was not designed to dissect the relative contributions of Nur77 domains, since Nur77 was tested only in its full-length form. Instead, the purpose of this experiment was to examine how truncation of RXRγ domains affects Nur77-RXRγ transcriptional activity, in direct comparison with our prior eLife study of Nurr1-RXRα, where RXRα domain truncations helped define the importance of RXR-LBD-mediated regulation. We will revise the text to clarify that Figure 1 does not distinguish whether Nur77 DBD-dependent DNA binding is necessary, but instead addresses whether the pattern of RXRγ domain dependence is consistent with an LBD-centered mechanism of ligand-regulated heterodimer function.

(4) It is stated that the HX600 coactivator recruitment requires further study. Why wasn't it studied here?

We thank the reviewer for this point. The primary focus of this study was to determine how RXR ligands influence Nur77-RXRγ heterodimer activity, particularly in relation to ligand-dependent effects on heterodimer function. A more detailed analysis of HX600-dependent coactivator recruitment would require a broader mechanistic investigation of RXRα and RXRγ homodimer pharmacology and RXR-specific coregulator interactions, which extends beyond the central scope of the present manuscript. We agree that this is an important question and view it as a valuable direction for future work.

(5) Figure 3B, the shifts in monomer populations, error bars aren't shown, the biggest shift is from 0.2 to 0.6, is that statistically meaningful?

We thank the reviewer for this point. The reviewer is correct that error bars were not shown for Figure 3B. These NMR measurements were performed once (n=1), and therefore the shifts in monomer populations shown in Figure 3B cannot be assessed statistically. Because these studies required substantial NMR instrument time and isotopically labeled protein at high concentration, we were not able to perform experimental replicates for this dataset. We have revised the figure legend to explicitly state that these data were collected from a single experiment and have tempered the corresponding language in the manuscript accordingly.

(6) Some ligands are shown in the figures but don't appear to be discussed in the text (at least that I can find), such as SR11237.

We thank the reviewer for pointing this out. We used a panel of 14 commercially available RXR ligands with different pharmacological properties to probe Nur77-RXRγ function, as in our previous Nurr1-RXRα study. In the text, we emphasized ligands that were most informative for the mechanistic conclusions, rather than discussing every compound individually. SR11237, for example, behaved similarly to the broader group of RXR agonists and was therefore shown as part of the full ligand panel but not specifically highlighted in the text. We will clarify this in the revised manuscript.

(7) There is a sentence in the discussion that says "these observations implicate that although RXRg LBD provides the protein-protein interaction interface to bind Nur77...." the authors did not show enough data to support this claim. It should be bolstered.

We thank the reviewer for this point. We agree that this statement was stronger than was warranted by the data presented. Our intent was not to claim that the present study definitively establishes the RXRγ LBD as the sole or fully defined protein-protein interaction interface for Nur77 binding. Rather, based on the domain truncation data together with our prior Nurr1-RXRα study, we intended this statement as a working interpretation consistent with an LBD-centered mechanism. In our revised manuscript, we have softened this language to avoid overstating the conclusion and clarified that the current data support, but do not definitively prove, a role for the RXRγ LBD in mediating functionally relevant interaction with Nur77.

Reviewer #2 (Recommendations for the authors):

Even though this study is not able to make definitive claims about the mechanism(s) of activation of Nur77 in the Nur77-RXRg complex, the work presented here is rigorous and solidly interpreted. Identifying differences between Nurr1 and Nur77 regulation is important, and the work here shows that selective agonists are essential for supporting the non-canonical mechanism they identified before. Although they address potential implications of NTD regulation in the discussion, it feels like a lot of insight into Nur77 regulation is being missed. However, it is clear that addressing this experimentally would require substantially more work. I don't have any specific recommendations. Given current limitations on funding, I think it's fine to focus on the work completed with the acceptance that it likely limits the impact of the work on the field.

We thank the reviewer for this thoughtful and balanced assessment of our work. The goal of this manuscript was to test whether the LBD heterodimer dissociation mechanism that we previously reported for Nurr1-RXRα may represent a conserved feature of NR4A-RXR heterodimers by extending these studies to Nur77-RXRγ. We agree that understanding the role of the RXRγ NTD in Nur77-RXRγ regulation is important and potentially highly informative. At the same time, resolving that question experimentally would require a distinct and more extensive set of studies beyond the scope of the present work. We have therefore chosen to focus this manuscript on the completed LBD-centered studies, while acknowledging that this narrower scope may limit the broader impact of the work.

Minor points:

(1) Without page and line numbers, it is not easy to point out specific text. On the bottom of page 6 of the document, there are two references to Figure 3a, and the arrows that help illustrate RXRg LBD-dependent CSPs; the second figure callout should describe the blue arrow, I believe.

Thank you, we made this change.

(2) Bottom of page 8, "...revealed two compounds [that] standout..."

Thank you, we made this change.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

We truly appreciate all the effort that the reviewer put into reading and understanding our work. With a total of 37 excellent questions, this is one of the most thorough reviews that we have received in a long time.

R1.0: Summary:

In this study, the authors propose a "unifying method to evaluate inter-areal interactions in different types of neuronal recordings, timescales, and species". The method consists of computing the variance explained by a linear decoder that attempts to predict individual neural responses (firing rates) in one area based on neural responses in another area.

The authors apply the method to previously published calcium imaging data from layer 4 and layers 2/3 of 4 mice over 7 days, and simultaneously recorded Utah array spiking data from areas V1 and V4 of 1 monkey over 5 days of recording. They report distributions over "variance explained" numbers for several combinations: from mouse V1 L4 to mouse V1 L2/3, from L2/3 to L4, from monkey V1 to monkey V4, and from V4 to V1. For their monkey data, they also report the corresponding results for different temporal shifts. Overall, they find the expected results: responses in each of the two neural populations are predictive of responses in the other, more so when the stimulus is not controlled than when it is, and with sometimes different results for different stimulus classes (e.g., gratings vs. natural images).

Strengths:

(1) Use of existing data.

(2) Addresses an interesting question.

R1.1: Unfortunately, the method falls short of the state of the art: both generalized linear models (GLMs), which have been used in similar contexts for at least 20 years (see the many papers, both theoretical and applied to neural population data, by e.g. Simoncelli, Paninsky, Pillow, Schwartz, and many colleagues dating back to 2004), and the extension of Granger causality to point processes (e.g. Kim et al. PLoS CB 2011). Both approaches are substantially superior to what is proposed in the manuscript, since they enforce non-negativity for spike rates (the importance of which can be seen in Figure 2AB), and do not require unnecessary coarse-graining of the data by binning spikes (the 200 ms time bins are very long compared to the time scale on which communication between closely connected neuronal populations within an area, or between related areas, takes place).

First, a few points of clarification.

(i) We worked with two-photon calcium imaging data (mice), and with the envelope of multi-unit activity (monkeys). While both of these types of signals are strongly correlated with spikes, neither of them can be truly considered to be a point process.

(ii)The reviewer points to Figure 2AB. The signals that we worked with can be negative. The black traces are the actual signals and show clear negative bouts, especially noticeable in the middle panel in Figure 2B. Of course, this does not mean that there are negative spike rates. This has to do with the way the data are normalized and not with the specific prediction method. However, the reviewer is correct in stating that the method that we used could also yield negative values even for non-negative spike rates.

(iii) We did not bin the macaque data into 200-ms time bins, but rather 25-ms time bins (line 548, Figure 1B legend). Additionally, we have now performed additional analyses with different window sizes, showing that the conclusions still hold (see Supplemental Figure 4 and lines 139-143).

To further address the reviewer’s question, we implemented a Poisson GLM enforcing non-negativity on macaque MUAe data (without spontaneous activity subtraction, ensuring strictly positive values; lines 135-139, Supplemental Figure 1M). The model did not improve predictions over ridge regression, confirming our methodological choice. This method is not directly applicable to mouse calcium data, since the activity after baseline subtraction can be negative.

We did not use Granger or any other causality methods. The question of causality is certainly important, and there are multiple methods developed to assess causality in neural signals. We do not make any claims about causality in our study. A rigorous evaluation of causality is an interesting line of research for future work.

R1.2: In terms of analysis results, the work in the manuscript presents some expected and some less expected results. However, because the monkey data are based on only one monkey (misleadingly, the manuscript consistently uses the plural ‘monkeys’), none of the results specific to that monkey, nor the comparison of that one monkey to mice, are supported by robust data.

We have now added data from 2 additional monkeys, including:

(i) A second monkey (monkey “A”) from the same dataset (Chen et al., 2020), which includes all activity types except the lights off condition (lines 90-96, 120-132, 159, 161, 171, 183-185, 188-194, 200-203, 228-237, 254-258, 292-296, 334-342, 351-353, 358-364, 374-378, 387-393, 400-408, 414, 417-421, 539-540, 544-545, 680-681, 696-698; Supplemental figures 1-6, 8, 11, 12, and 13; Table 2).

(i) We collected new neural activity from one additional monkey (monkey “D”) in collaboration with the Ponce lab (lines 90-96, 120-130, 132-134, 163-164, 228-235, 237-243, 292-296, 351-353, 374-378, 387-389, 539-540, 553-560, 696-698; Supplemental figures 1-2, 4, 6, 9, 11, and 12; Table 2). The new data include responses to the same checkerboard and gray screen images as the original dataset, along with responses during lights-off conditions.

R1.3: One of the main results for mice (bimodality of explained variance values, mentioned in the abstract) does not appear to be quantified or supported by a statistical test.

We have now formally quantified the bimodality of the relationship between one-vs-rest correlation and inter-laminar explained variance (EV) in mice using Hartigan’s dip test, applied to neurons with EV>0.4. The test confirmed significant bimodality in two of the three mice (MP031 and MP032: p<0.001; MP033: p=0.687). These results are now included in the Results section (lines 307-311) and shown in Supplemental Figure 7A,D. In datasets that did not show bimodality by visual inspection (macaque recordings), the same test yielded non-significant results (e.g., p=0.994), confirming that the statistical analysis distinguishes between bimodal and unimodal cases.

R1.4: Moreover, the two data sets differ in too many aspects to allow for any conclusions about whether the comparisons reflect differences in species (mouse vs. monkey), anatomy (L2/3-L4 vs. V1-V4), or recording technique (calcium imaging vs. extracellular spiking).

We also agree with this comment. Our goal is not to provide any direct quantitative comparison between the two species. We emphasize (lines 494-497) that the experiments in the two species differ along multiple dimensions, including: (i) differences in recording modalities (calcium vs. electrophysiology), (ii) associated differences in temporal resolution, neuronal types, and SNR, (iii) cortical targets (layers vs. areas), (iii) sample size, (iv) stimuli, (v) task conditions. In the revised manuscript, we also emphasized that the aim of this work is to investigate inter-areal interactions within each species rather than to draw quantitative comparisons between species (lines 497-499).

Reviewer #1 (Recommendations for the authors):

R1.5 In the analysis of directionality, you stated that subsampling was done randomly. Presumably, there could be multiple subsamples that fulfill the control of split-trial r. Are you only showing results from one subsample or multiple subsamples?

We show the median from 10 subsample permutations. This is now clarified in line 621.

R1.6 About the measurement 1-vs-rest r2. Understanding the definition is important for interpreting the results, but the definition was not clearly written. In lines 195-196, could you be more clear about whether the correlation is between the predicted neuron and other neurons in the predicted population or between the predicted neuron and the mean activity of the predictor population? Also, in line 212, why do you call this self-consistency? Isn't this a correlation between a neuron and the others?

The 1-vs-rest r² value, or self-consistency, is the correlation calculated for each neuron i and does not involve other neurons. Let indicate the response 𝑟 of neuron i during trial t (t=1,..., T where T is the total number of trials). For a given trial t, we compute the average activity of the neuron excluding this trial:

Throughout, the superscript (rest)means “all repetitions excluding repeat 𝑡”. The one-vs-rest correlation for the held-out repetition 𝑡 is:

We then average these correlations across all held-out repetitions:

We now clarify this in the text (lines 304-306 and lines 642-647).

R1.7 In Figure 6 G and I. The "all" condition contains more neurons than either of the other two. In this case, is this comparison fair or meaningful?

The reviewer is also correct here. The comparisons between the <10% and >80% groups contain the same number of predictor neurons, and those are fair comparisons. The “all” condition contains more predictor neurons, and, therefore, those comparisons are not fair. We clarified this point in lines 360-364.

We included the “all” condition here because we think that it is an instructive sanity check in terms of reporting how EV changes with more neurons, and also in terms of understanding why the EV values in the other two conditions are lower. Expanding on this point with a little bit of philosophy, ultimately, when considering a neuron in area B (e.g., V4) and the contributions from neurons in another area A (e.g., V1), one would like to have access to all the inputs (e.g., all the neurons in V1 that are monosynaptically connected to the target neuron in area V4). We do not have access to this type of information, and we do not make any claims about monosynaptic connectivity, let alone exhaustive sampling of inputs to a given neuron. The “all” condition merely provides a quantitative illustration of the fact that EV increases with the number of predictor neurons. This observation may be considered to be somewhat trivial, but it should be pointed out that the conclusion relies on the input neurons sharing information with the target neurons (e.g., perhaps one may not be able to predict V4 activity very well from the responses of millions of neurons in the cerebellum).

R1.8 I believe the results section can be improved by adding some interpretation after each finding.

We thank the reviewer for the suggestion. We generally like to separate results from interpretation. However, to honor the suggestion, we added brief interpretations throughout the results section (lines 142-143, 171-173, 272-273, 279-281, 331-333, and 361-364) and expanded on the interpretations in the Discussion section.

R1.9 Line 52 - 74: It would be better to be more specific about what kind of neuronal interactions, e.g., noise correlation, synchrony, etc.

We added a clarification on the types of interactions we study in lines 68-73.

R1.10 Line 81. Something seems to be missing after "5500". 5500 trials? Neurons?

We thank the reviewer for pointing this out. The number refers to neurons (fixed in line 87).

R1.11 Line 94. The readers would appreciate more explanation of the method.

We have expanded on the explanation, as suggested (lines 106-107).

R1.12 Line 104. The fraction of visually responsive neurons seems to be small. Is this typically for mouse V1? Would this fraction be higher if you also used the peak, as you did for macaque data in your SNR calculation (line 412)? And what is this number for the recorded L4?

The reviewer correctly points out the small number of visually responsive neurons.

We note that we now refer to the subset of neurons used for prediction analyses as visually reliable (VR) neurons (lines 115-116, 125-126, 178-179, 183-184, 211-212, 214-216, 217-226, 283-286), defined conservatively as neurons with SNR > 2 computed from the mean across all stimuli (not the peak to any one stimulus) and split-half reliability >0.8 (Methods, lines 569–590). This choice emphasizes neurons that are consistently informative over the full stimulus set.

Regarding the question of how typical the number of responsive neurons in mice is, the fraction of “responsive” neurons in mouse V1 varies widely depending on the definition and stimulus set but the fractions are substantially lower than those reported in monkeys (with different methods). For those of us more used to the macaque neurophysiology literature, this has been one of the biggest surprises coming from work in rodents. Many studies report a sizable group of non-responsive neurons in mouse V1 (e.g., as little as 37% percent of V1 neurons being responsive in at least 25% of the trials according to de Vries et al., Nat Neur, 2020). Our fraction of visually responsive neurons is small because it couples a conservative SNR metric with a high trial-reliability threshold.

As the reviewer notes, a peak-based metric based on any stimulus would be a less conservative criterion that would increase the fraction of neurons labeled responsive.

R1.13 Line 113. Why not also give an exact percentage number?

We have given the exact percentage number (lines 125-126).

R1.14 Line 128. Is this just because L2/3 has more neurons? If so, then isn't this trivial?

Our intention was to illustrate the best prediction performance we could get in either direction, which means including all L2/3 neurons. We have reworded our text to clarify (lines 149-151).

R1.15 Line 134. Isn't this expected? Since V1 have more units than V4?

The reviewer is correct. As discussed in R1.7 in mice, we sought to report the best prediction performances in either direction. We have edited our text for clarity (lines 149-151).

R1.16 Line 165-168. What's the logical connection between these two sentences? If the former is true, we should expect to see differences. Also, why the same population? Shouldn't you include non-visual neurons?

The two sentences in question are: “The difference in predictability in the absence of a stimulus could in principle change according to the directionality in inter-laminar interactions.” and, “There was no statistically significant difference in the EV fraction between laminar directions (L4→L2/3 vs. L2/3→L4) using the same control population as in Figure 3B (Figure 5A-C and Figure Supplement 2H).”. The key point here was to control for similar reliability values in order to make fair comparisons. We have added an additional comparison between directionalities focusing on nonvisual neurons (SNR<2 & r<0.8), and have also found no statistically significant difference between direction of predictability (Supplemental Figure 3A, right, lines 221-224).

R1.17 Table 2. The information of which session corresponds to which experiment can be put in the table, which would be easier to read.

We have added which sessions correspond to which experiments in Table 2.

R1.18 Figure 1, Captions for panel c and d. I don't see any colored arrows in the figure.

We removed the color descriptions (Figure 1C-D).

R1.19 Figures 3, 4, and others. The annotations of "n.s." are very hard to see.

We changed the color so that it is easier to see now (Figures 3, 4, 6, and Supplementary Figures 1-4, 6, and 8-10).

R1.20 Figure 5, panel A. The legend is too small.

We increased the legend size (Figure 5A).

R1.21 Figure S5, panel D. Why are some of the data points connected?

The paired connections are illustrated specifically in the highly predictable neurons to highlight the two separate distributions of neurons. One group, the highly predictable and highly reliable group, maintains its inter-laminar predictability after projecting out the “non-visual” activity (lines 327-330), whereas the highly predictable yet unreliable group shows a sharp decrease in inter-areal predictability, which corroborates the idea of non-visual components influencing neurons in mouse V1, as shown by Stringer et al. 2019b and consistent with our results.

R1.22 l.91 "Ope" -> open?

We fixed the typo (line 100).

R1.23 Fig. 3C+D: Why is only one session used for this?

One session was used to illustrate the distribution of split-half reliability values per area. Figure 3D contains information about all 5 stimulus sessions (see legend to Figure 3D).

R1.24 "Even without controlling for the number of predictors or their respective split-half correlation values (627-688 sites in V1, 86-115 sites in V4), we found better predictability in the V1 to V4 direction than the reverse ( 𝑝 < 0.001, Figure Supplement 2I)." -> What does "even" mean here? Isn't this simply the null result if there is no true difference and the real reason the authors controlled for size?

The reviewer’s understanding is correct. We have edited our text for clarity (lines 157-160)

R1.25 "We could predict V1 and V4 activity across all stimulus types ( 𝑝 < 0.001, paired permutation test of prediction vs. shuffled frames prediction)." -> better than chance? For all neurons on average? What does this mean? Isn't it trivial and 100% expected that neural activity in the visual cortex is above chance related to the visual input?

We stated that sites in V1 and V4 could predict each other across all stimulus types before describing the differences between them. We agree that this observation is to be expected and indicated so now in the text (lines 185-186).

R1.26 "The predictability was the highest in both directions for neuronal activity in response to a full field checkerboard images (Figure 4D). In the V1 → V4 direction, the EV fraction was higher when predicting a slow-moving small thin bar compared to a fast-moving large thick bar (Figure 4D, left), whereas the opposite was true for the V4 → V1 direction (Figure 4D, right)." -> What does this mean? Is this expected or not? Under what theories of cortical processing?

The differences between EV prediction directions (V1→V4: slow thin bars > fast thick bars; V4→V1: fast thick bars > slow thin bars) could be because V4 responses are more reliable for the slow thin bars whereas V1 responses are more reliable for the fast thick bars (Supplemental Figure 5H–I). To account for this possibility, we controlled for differences in target-related properties by regressing out covariates like SNR, split-half correlation, and variance. In monkey L, regressing out reliability/drive within direction using these covariates, the V4→V1 bar difference between slow thin bars and fast thick bars was not significant and the difference in the V1→V4 difference direction was reduced (Supplemental Figure 5K, lines 198-203). This suggests that the asymmetry primarily reflects stimulus‑dependent reliability of the target population rather than a strong directional selectivity.

To the best of our knowledge, there are no clear predictions that match these observations from existing theories of visual cortical processing, especially given the paucity of computational models that include stimulus velocity when describing the responses in area V4. There has been extensive work on theories of surround suppression, but it seems unlikely that the thick bars would elicit surround suppression given the size of the V4 receptive fields. Many current computational models that aim to fit the responses of neurons in the visual cortex use neural networks that take an image as visual input and yield activations. Most of these models do not incorporate stimulus movement, and even those that do incorporate stimulus dynamics, only indirectly map onto interlaminar stimulus transformations or even between-area stimulus transformations. We hope that the results in this manuscript will help inspire and constrain better models of visual cortical processing.

R1.27 Shouldn't all the predictability analysis be done conditioned on the stimulus in order to tell us more than the trivial "both V1 and V3, or L2/3 and L4, are driven by visual inputs"? (The spontaneous activity analyses are essentially that, for a small subset of the stimuli.)

The key goal of this study is to quantify inter-areal interactions both under visual input and without visual input. This type of analysis is important because inter-areal interactions may depend both on visual inputs but also on neuronal inputs that are not triggered by visual signals. For example, extensive work in mice has now shown that neuronal responses in V1 depend on an animal’s running speed, independently of any visual input. Even within the visual input conditions, we present analyses where we shuffle trial order (e.g., Figure 7, Supplementary Figure 11) to estimate the contribution of trial-by-trial variations that are independent of visual inputs and other analyses where we project out non-visual activity (e.g., Supplementary Figure 7).

R1.28 "In visually responsive neurons, there was a significant reduction in EV during gray screen compared to visual stimulus presentation" -> perfectly expected. But the report-worthy result here is how much is left, not whether EV is decreased!

We have changed the wording on the results to highlight the sustained predictability (lines 211-212). It is important to note that, although the reduction in EV during gray screen may be expected, this observation does not hold for all neurons. In fact, there are some neurons for which the EV during visual presentation is comparable to that during gray screen (Figure 5B,C,E: neurons that lie on the diagonal line).

R1.29 "Similar to the conclusions drawn from the mouse data, the predictability of neuronal activity was higher in response to stimulus presentation than to gray screen presentations" -> Really? Conditioned on stimulus, or explainable by the well-known fact that both V1 and V4 are visually driven?

As discussed in R1.28, in mice, there are many neurons where the EV during gray screen is comparable to that during stimulus presentation. In monkeys, most sites were visually driven. As the reviewer points out, we expected that EV during stimulus presentation would be higher than during gray screen; this observation is a reasonable sanity check. The difference between unshuffled trials and shuffled trials (Figure 7, Supplementary Figure 11) provides an estimate of the interactions that are not purely explained by visual inputs alone in monkeys.

R1.30 "Unlike the mouse, macaque correlation of visual predictability between stimulus presentation and spontaneous activity was high across all types of spontaneous conditions" -> Why? Is this simply explainable by a lower mean response in the spontaneous condition in the mouse? Are these mouse and monkey experiments truly comparable? Isn't it surprising that spontaneous activity in the monkey visual cortex compared to evoked activity is higher than in the mouse?

With respect to the question of whether spontaneous activity (or stimulus-evoked activity) in monkeys is higher than in the mouse, it is difficult to make these comparisons. We emphasize in the text the multiple differences between the experiments in both species. Our goal is not to perform any quantitative comparison across species (see R1.4). We changed the wording to remove any inference of comparison between species (lines 248-250).

R1.31 Occasionally imprecise presentation. Ex "To further examine the non-stimulus driven component, we reasoned that if the shared information between areas were strictly driven by the visual stimulus, then using the activity of a stimulus presentation repeat to one specific image could be used to predict the responses to any other stimulus repeat of the same image. On the other hand, if the shared activity does not have any stimulus-response information, then the prediction model would not work when considering responses across repeated presentations of identical stimuli in different trials. To test these two opposing ideas, we compared the inter-areal prediction EV fractions using unshuffled versus shuffled trials." -> Sets up two extreme strawmen (100% driven by stimulus vs 0% driven by stimulus). What does "model would not work" mean? EV=0? Hypotheses not ideas.

Our intent was to set up two extreme hypotheses, not to claim that neurons must fall exclusively into one or the other. The two extremes help better interpret the results.

The reviewer indicates that these are straw-man hypotheses. This may well be the case. But note the responses to R1.12, R1.27, R1.28, and R1.29. The reviewer seems to assume that all or most neurons in the visual cortex should be mostly or exclusively driven by visual stimuli.

We also replaced “ideas” with “hypotheses”, as suggested. We have expanded the discussion of these points in the manuscript (lines 480-493). Many neurons occupy intermediate positions between these two extreme hypotheses. We clarified that “model would not work” refers to prediction accuracy approaching chance (EV ≈ 0).

R1.32 "In both species and in both directions, inter-areal prediction EV fraction persisted (𝑝 < 0.001," Doesn't persist mean EV is unchanged? But the test is EV>0 or not in both cases.

We meant that EV values remained significantly above chance, not that they were unchanged. The statistical test was indeed whether EV > 0 as the reviewer indicated. We have revised the text accordingly (lines 375-380).

R1.33 "In mice, neurons showed a bimodal distribution in terms of their response predictability in shuffled and unshuffled trials" -> I don't see any bimodality in the figure, nor is there a statistical test provided for bimodality.

In Figure 7C, a group of neurons lay essentially along the horizontal axis, whereas the other group is dispersed closer to the diagonal line. Specifically, the neurons that lay on the horizontal axis are also the ones whose responses are best predicted during gray screen activity. We have changed the text to clarify this point (lines 380-382).

R1.34 "In the macaque V4 → V1 direction, there was a large proportion of neurons with peak EV when considering 25 ms to 50 ms offsets in the positive direction (i.e., V4 after V1, Figure 7I, right)." -> So what does this mean? Is this compatible with anything we know? This is the anti-causal direction so some kind of explanation would be warranted.

In the V4→V1 panel, a positive offset means we use V4 at t+Δt to predict V1 at t (and conversely in the V1→V4 panel). Therefore, the fact that the peak EV occurs at +10–20 ms indicates that V1 leads V4 by ~10–20 ms: in other words, V1’s earlier response best predicts V4’s slightly later response. This observation is not anti-causal, but rather it is consistent with the canonical largely feed-forward V1→V4 latency (e.g., Schmolesky et al., 1998 among many others). We clarified this in text (lines 400-404).

R1.35 L. 307: "In monkeys," plural!?

While this was not correct in the original version, we have now added data from two more monkeys.

R1.36 L. 313: "we observed an approximately bimodal distribution of neuronal responses, with a large subset of neurons that do not show reliable responses to visual stimuli both in L4 and L2/3" -> where?

The bimodal distribution can be appreciated in Figure 6B (1-vs-rest r2, third panel, note neurons along the y-axis, see also R1.33) and Supplementary Figure 7B (lines 307-312). Additionally, as stated in R1.3, we have now formally quantified the bimodality of the relationship between one-vs-rest correlation and inter-laminar explained variance (EV) in mice using Hartigan’s dip test (lines 310-313); see also Supplementary Figure 7A,D. In datasets that did not show bimodality by visual inspection (macaque recordings) the same test yielded non-significant results, confirming that the statistical analysis distinguishes between bimodal and unimodal cases.

R1.37 Random subsampling to control for population size done with how many subsamples? How are they combined? Variability across subsamples interpreted how?

We performed 10 permutations and used the median distributions across permutations (line 621).

Reviewer #2 (Public Review):

R2.0: “Summary:

In this work, the authors investigated the extent of shared variability in cortical population activity in the visual cortex in mice and macaques under conditions of spontaneous activity and visual stimulation. They argue that by studying the average response to repeated presentations of sensory stimuli, investigators are discounting the contribution of variable population responses that can have a significant impact at the single trial level. They hypothesized that, because these fluctuations are to some degree shared across cortical populations depending on the sources of these fluctuations and the relative connectivity between cortical populations within a network, one should be able to predict the response in one cortical population given the response of another cortical population on a single trial, and the degree of predictability should vary with factors such as retinotopic overlap, visual stimulation, and the directionality of canonical cortical circuits.”

R2.1: To test this, the authors analyzed previously collected and publicly available datasets. These include calcium imaging of the primary visual cortex in mice and electrophysiology recordings in V1 and V4 of macaques under different conditions of visual stimulation. The strength of this data is that it includes simultaneous recordings of hundreds of neurons across cortical layers or areas. However, the weaknesses of calcium dynamics (which has lower temporal resolution and misses some non-linear dynamics in cortical activity) and multi-unit envelope activity (which reflects fluctuations in population activity rather than the variance in individual unit spike trains), underestimate the variability of individual neurons. The authors deploy a regression model that is appropriate for addressing their hypothesis, and their analytic approach appears rigorous and well-controlled.

We agree with these points, and we discuss these specific limitations in capturing the variability of individual neurons in the Discussion section (lines 500-504). We have now also added analyses based on local field potentials (LFP). LFPs do not directly reflect the activity of individual neurons either.

R2.2: From their analysis, they found that there was significant predictability of activity between layer II/III and layer IV responses in mice and V1 and V4 activity in macaques, although the specific degree of predictability varied somewhat with the condition of the comparison with some minor differences between the datasets. The authors deployed a variety of analytic controls and explored a variety of comparisons that are both appropriate and convincing that there is a significant degree of predictability in population responses at the single trial level consistent with their hypothesis. This demonstrates that a significant fraction of cortical responses to stimuli is not due solely to the feedforward response to sensory input, and if we are to understand the computations that take place in the cortex, we must also understand how sensory responses interact with other sources of activity in cortical networks. However, the source of these predictive signals and their impact on function is only explored in a limited fashion, largely due to limitations in the datasets. Overall, this work highlights that, beyond the traditionally studied average evoked responses considered in systems neuroscience, there is a significant contribution of shared variability in cortical populations that may contextualize sensory representations depending on a host of factors that may be independent of the sensory signals being studied.

We agree that these datasets do not lend themselves well to directly separating and quantifying all the different sources of the predictive signals. We expand on this point in the Discussion section (lines 509-511).

R2.3: The different recording modalities and comparisons (within vs. across cortical areas) limit the interpretability of the inter-species comparisons.

We also agree with this comment. We emphasize that our goal is not to attempt a direct quantitative comparison across species (lines 497-499).

R2.4: Strengths:

This work considers a variety of conditions that may influence the relative predictability between cortical populations, including receptive field overlap, latency that may reflect feed-forward or feedback delays, and stimulus type and sensory condition. Their analytic approach is well-designed and statistically rigorous. They acknowledge the limitations of the data and do not over-interpret their findings.

Weaknesses:

The different recording modalities and comparisons (within vs. across cortical areas) limit the interpretability of the inter-species comparisons.The mechanistic contribution of known sources or correlates of shared variability (eye movements, pupil fluctuations, locomotion, whisking behaviors) were not considered, and these could be driving or a reflection of much of the predictability observed and explain differences in spontaneous and visual activity predictions.

We have expanded on the Discussion section to explicitly state the points raised by the reviewer (lines 494-509).

In mice, we have now also analyzed a separate dataset in which behavioral measurements were available, including running speed and facial motion (FaceMap SVDs). We used these to build behavioral-only and combined models to predict neural activity. We found that behavioral variables explained a modest but consistent portion of the variance across both spontaneous and stimulus conditions (Supplementary Figure 10A,C, lines 268-273).

For the macaque data, we analyzed pupil size as the only available behavioral measure in the macaque dataset. We focused specifically on the “resting state, eyes open” condition, where both neural activity and pupil measurements were available. Using ridge regression, we assessed the extent to which pupil size predicted neural activity in V1 and V4. Pupil size alone explained only a small fraction of the variance (Supplementary Figure 10E, lines 274-276).

R2.5: Previous work has explored correlations in activity between areas on various timescales, but this work only considered a narrow scope of timescales.

Without going into specifics about the numbers, it is hard to fully address this question. As the reviewer noted in R2.1, the mouse data analyzed here do not lend themselves to evaluating predictability on scales of tens of milliseconds. In the macaque data, we have now conducted additional analyses where we binned the activity across a range of bin sizes (10 ms to 200 ms). The new analyses are shown in Supplementary Figure 4, and described in lines 140-143, 160-163.

R2.6: The observation that there is some degree of predictability is not surprising, and it is unclear whether changes in observed predictability with analysis conditions are informative of a particular mechanism or just due to differences in the variance of activity under those conditions. Some of these issues could be addressed with further analysis, but some may be due to limitations in the experimental scope of the datasets and would require new experiments to resolve.

First, we note that several of the analyses and comparisons are within conditions and not across conditions, where by “condition” we mean the presence or absence of a stimulus or different stimuli (e.g., Figures 3, 5, 6, 7, Supplementary Figures 3-4, 7–13).

Second, we note that our mouse preprocessing standardized responses by spontaneous mean and SD per neuron, controlling baseline scale across conditions (lines 535-538). Because of this standardization, spontaneous traces have unit scale (mean = 0, SD = 1).

To test whether differences in variance underlie our findings, we calculated the variance for both species. For mice, we computed variance across repeats (visual) and across timepoints (lines 286-291). For the macaque moving-bar sessions, we computed variance across the concatenated held-out samples pooling timepoints, repeats, and bar identities (lines 291-292).

The V4 population showed a higher overall variance distribution compared to the V1 population (Supplementary Figure 2I-J), and L2/3 variance was also overall higher than L4 (Supplementary Figure 2D-E). We also see a modest monotonic relationship between EV fraction and this variance (mouse visual: Spearman ρ = 0.43–0.52, p < 0.001; macaque stimulus responses: ρ = 0.50–0.56, p < 0.001; macaque gray-screen responses: ρ = 0.38, p < 0.001, Figure 6A,D), indicating variance contributes to (but is not the primary driver of) EV prediction fraction. We then adjusted for variance by fitting, within each stimulus condition, a linear regression of EV on variance (excluding shuffled-control rows) and conducted all comparisons on the resulting residual EV values, thereby isolating effects not attributable to variance (see Supplementary Figure 3E-G, lines 165-171).

Reviewer #2 (Recommendations for the authors):

R2.7 Overall I found this manuscript to be very clearly written and the results compelling, although I found myself wanting a little more. I believe these datasets also include information about eye movements, pupil diameter, and maybe locomotion and whisking in the rodent work. I think it could be informative to ask the degree to which the predictability, particularly during the spontaneous activity, is attributable to these other known sources of variance in trial-by-trial measures. My concern is that during visual stimulation, the space of cortical responses is limited to a very narrow scope (observing a visual stimulus during fixation) whereas spontaneous activity includes a broader range of possibilities (different states of arousal, eye movement).