eLife assessment

This valuable study advances our understanding of the below-ground resource acquisition strategies of diverse tree species, integrating the roles of both roots and their associated microbes. The support for the conclusions is incomplete owing to the uncertainties or shortcomings associated with the design and statistical analyses. Regardless of these technical issues, this study can be of broad interest for plant and microbial ecologists.

Reviewer #1 (Public Review):

Summary:<br /> In this study, Wu et al. investigated the microbiome in the rhizosphere and roots of plant species along an elevational gradient. They found that: (i) plants with higher root nitrogen ("fast" strategy) were more likely to be associated with saprotrophic fungi, plant pathogenic fungi, and AM fungi, but plants with lower root nitrogen ("slow" strategy) were more likely to be associated with ectomycorrhizal fungi; (ii) bacterial functional guilds were associated with root-zone pH but not root traits.

Strengths:<br /> This study is novel in the sense that it revealed the associations between microbiome and trait dimensions of plants. This has been rarely explored even though we acknowledge the importance of plant-microbe interactions.

Weaknesses:<br /> The authors tried to include the relative abundances of bacterial and fungal guilds into the root economics framework, which I disagree with because they are just associated with the root economics framework. The title also states that the authors' aim is to link microbial functional guilds to root economics. Therefore, I would suggest that the analyses should be redone to elaborate on the relationships between microbiome and root functional traits.

Below I provide some critiques and comments that outline my concerns and provide recommendations to hopefully improve the current manuscript.

-Figures 2 and 3: The authors included soil properties, relative abundances of bacterial or fungal guilds, and root traits in the root economics spectrum. However, soil properties and relative abundances of bacterial or fungal guilds are not root traits, they are just associated with root traits. These bacterial or fungal guilds are the consequence of root traits. Also, the authors did not elaborate on the root trait dimensions of the plants. The only trait dimension they discussed is the "fast-slow" axis. Therefore, I would suggest the authors first analyze the trait dimensions of plants by only using the root traits (PCA), and then explore how the soil properties and relative abundances of bacterial or fungal guilds are associated with the trait dimensions (e.g., envfit in the vegan package).

-When exploring the associations between microbial functional guilds and root traits, it is unnecessary to analyze the bacterial and fungal functional guilds separately. The bacterial and fungal functional guilds can be included in the same models, and their relative importance and patterns can be compared.

-For fungi, the authors used FUNGuild to infer functional guilds from taxonomy. qPCR was also performed to validate the results of AMF. This is fantastic. For bacteria, the authors used FAPROTAX to infer functional guilds from taxonomy. However, archaea are also considered in some functions in FAPROTAX. For example, both bacteria (ammonia-oxidizing bacteria) and archaea (ammonia-oxidizing archaea) play critical roles in nitrification. I would assume the authors have removed archaea from the dataset because they stated that the functions of bacteria are inferred from FAPROTAX. Therefore, the importance of nitrification might be underestimated.

-Key methodological details are missing. First, maps of the sampling site and plots are missing. It would be great if the authors provided maps showing the location of the sampling site and the spatial distribution of the 11 plots. Second, in lines 304-306 the authors claimed that they sampled the most common species in the plots, but they did not provide the coverage or relative abundances of plant species in the plots.

Reviewer #2 (Public Review):

Summary:<br /> The authors aimed to determine to what extent root morphology, chemistry, and soil characteristics explained the relative abundance of functional groups of bacteria and fungi associated with roots. To do so, they sample roots and rhizhospheric soil of trees along an elevation gradient. This type of work is common in the field of microbial ecology. The main novelties I see are two: a) a focus on the functional groups of bacteria and fungi rather than just taxonomic abundance. I think this approach is valuable because it provides information about the potential functions of these microorganisms; b) using the root economic spectrum to frame the findings. The root economic spectrum reflects a gradient along which plant roots can be allocated from 'short-lived that provide fast investment return' to 'long-lived that provide a slow investment return'. It is logical to expect (as the authors did) that variation along this gradient will be an important factor in explaining the variation in functional groups.

Strengths:<br /> The main strength is using the root economic spectrum as a framework to interpret the data. There are countless studies addressing variation in the relative abundance of microbial communities along environmental gradients which tend to be more descriptive. I think using this framework advances the field by suggesting that while the root economic spectrum exists it is not a very important explanatory variable to predict changes in functional diversity. I also think the authors use state-of-the art methods to collect and process the sample (i.e. to obtain the data).

Weaknesses:<br /> The main weakness is with the presentation of statistical methods as it currently stands. The authors use distance-based redundancy analysis as the main statistical method. However, my understanding is that this method is not advised for a relative abundance of communities. At least not with Euclidean distances which is the default option of the functions dbrda in vegan. The use of this distance would group together communities with no species in common as close to each other (which is an incorrect interpretation). I think the authors should specify what distance they use. My guess is that they actually used bray-curtis in which case this weakness does not apply. However, as it stands it is not specified what metric they use and if they indeed use Euclidean distances it may lead to inaccurate conclusions. In addition, they also mention they use PCA on the relative abundance of functional groups. By definition, PCA is also based on Euclidean distances, which gives a similar problem as dbrda. Thus, I encourage the authors to use bray-curtis distance and specify it in the text.

Reviewer #3 (Public Review):

Summary:<br /> In this study, the authors collected a large set of data on root traits and root-associated microbes in the root endosphere and rhizosphere in order to integrate these important organisms in the root economics spectrum. By sampling a relatively large set of species from the subtropics along an elevation gradient, they tested whether microbial functions covary with root traits and root trait axes and if so, aimed to discuss what this could tell us about the (belowground) functioning of trees and forests.

Strengths:<br /> The strengths of this study lie mostly in the impressive dataset set the authors compiled: they sampled belowground properties of a relatively large number of tree species from an understudied region: i.e., the subtropics, where species-level root data are notoriously scarce. Secondly, their extensive sampling of associated microbes to integrate them in the root economics space is an important quality, because of the strong associations between roots and fungi and bacteria: soil microbes are directly related to root form (e.g., mycorrhizal fungi and root diameter and SRL), and function (e.g., taking up soil nutrients from various sources). Thirdly, the PCA figures (Figures 2 and 3) look very nice and intuitive and the paper is very well written.

Weaknesses:<br /> That said, this study also has several methodological weaknesses that make the results, and therefore the impact of this study difficult to evaluate and interpret.

(1) Design: The design of this study needs further explanation and justification in the Introduction and Methods sections in order to understand the ecological meaning of the results. Root traits and microbial community composition differ with their environment, and therefore (likely) also with elevation. Elevation is included in the redundancy analysis as a main effect, but without further environmental information, its impact is not ecologically meaningful. What is the rationale for including an elevation gradient in the design and as a main effect in the analyses? Do environmental conditions vary across altitudes and how, and if so, how would this impact the data?

What is the rationale behind sampling endosphere and rhizosphere microbial communities - why do both? And why also include pathogens - what are their expected roles in the RES? What do we know about this already? The introduction needs a more extensive literature review of these additional variables that are included in the analyses.

(2) Units of replication and analysis in the model: What are the units of replication and analyses, e.g., how many trees were sampled per species, how many species or trees per elevation, and how many plots per elevation? Were all 11 plots at different elevations and if so, which ones? The level of analysis for the redundancy analyses is not entirely clear: L. 404 mentions that the analyses were done 'across the rhizosphere and root tissue samples', but is that then at the individual-tree level? If so, it seems that these analyses should then also account for dependencies between trees from the same species and phylogeny (as (nested) covariates or random factors). With the information provided, I cannot tell whether there was sufficient replication for statistical interpretations.

(3) PCA: The results of the parallel analyses are not described: which components were retained? Because the authors aim to integrate microbial functions in a root economics space, I recommend first demonstrating the existence of a root economics space across the 52 subtropical species before running a PCA that includes the microbial traits. The PCA shown in this study does not exactly match the RES and this could be because traits of these species covary differently, but may also simply result from including additional traits to the PCA.

Also, the PCA's shown are carried out at the individual-tree level. I would recommend, however, including the species-level PCA's in the main text, because the individual-level PCA may not only reflect species-inherent ecological strategies (that e.g., the RES by Bergmann et al. 2020 describe) but also plasticity (Figures 2 and 3 both show an elevation effect that may be partly due to plasticity). While the results here are rather similar, intraspecific differences in root traits may follow different ecological principles and therefore not always be appropriate to compare with an interspecific RES (see for example Weemstra & Valverde-Barrantes, 2022, Annals of Botany).

I could not deduce whether tree species in the "fungal PCA" (Figure 2) were assigned as AM or EcM based on Table 1, or based on their observed fungal community composition. In the former case, the fungal functional guild gradient (from EcM to saprotrophs and AM) is partially an artificial one, because EcM tree species are not AM species (according to Table 1) and therefore, by definition, constitute a tradeoff or autocorrelation. And, as the authors also discuss, AM tree species may host EcM fungal species. Before I can evaluate the ecological meaning of PC1, and whether or not it really represents a mineral/organic nutrient gradient, information is needed on which data are used here.

I do not agree with the term 'gradient of bacterial guilds' (i.e., PC1 in Figure 3). All but 1 bacterial 'function' positively loaded on PC1 and 'fermentation' was only weakly negatively correlated with PC1. I do not think this constitutes a 'bacterial gradient'.

(4) Soil samples: Were they collected from the surrounding soil of each tree (L. 341), or from the root zone (L. 110). The former seems to refer to bulk soil samples, but the latter could be interpreted as rhizosphere soils. It is therefore not entirely clear whether these are the same soil samples, and if so, where they were sampled exactly.

Aims:<br /> The authors aimed to integrate endospheric and rhizospheric microbial and fungal community composition in the root economics space. Owing to statistical concerns (i.e., lacking parallel analysis results and the makeup of the PCs (AM versus EcM classification), I am not sure the authors succeeded in this. Besides that, the interpretation of the axes seems rather oversimplified and needs some consideration.

Root N is discussed as an important driver of fungal functional composition. Indeed, it was one of the significant variables in the redundancy models predicting microbial community composition, but its contribution to community composition was small (2 - 3 %), and the mechanistic interpretation was rather speculative. Specifically, the role of root N in root (and tree) functioning remains highly uncertain: the link with respiration and exudation is increasingly demonstrated but its actual meaning for nutrient uptake is not well understood (Freschet et al. 2021. New Phytologist). If and how root economics (represented by root N) and the fungal-driven nutrient economy (EcM versus AM, saprotrophs) can indeed be integrated into a unified framework (L. 223 - 224) seems a relevant question that is worth pursuing based on this paper, but in my opinion, this study does not clearly answer it, because the statistical analyses might need further work (or explanation) and underlying mechanisms are not well explained and supported by evidence.

In addition, the root morphology axis was indeed independent of the "fungal gradient", but this is in itself not an interesting finding. What is interesting, but not discussed is that, generally, AM species are expected to have thicker roots than EcM tree species (Gu et al. 2014 Tree Physiology; Kong et al. 2014 New Phytologist). I am therefore curious to see why this is not the case here? Did the few EcM species sampled just happen to have very thick roots? Or is there a phylogenetic effect that influences both mycorrhizal type and root thickness that is not accounted for here (Baylis, 1975; Guo et al., 2008 New Phytologist; Kubisch et al., 2015 Frontiers in Plant Science; Valverde-Barrantes et al., 2015 Functional Ecology; 2016 Plant and Soil)?

I also do not agree with the conclusion that this integrated framework 'explained' tree distributions along the elevation gradient. First of all, it is difficult to interpret because the elevation gradient is not well explained (e.g., in terms of environmental variation). Secondly, the framework might coincide with the framework, but the framework does not explain it: an environmental gradient probably underlies the elevation gradient that may be selected for species with certain root traits or mycorrhizal types, but this is not tested nor clearly demonstrated by the data. It thus remains rather speculative, and it should be more thoroughly explained based on the data observed. Similarly, I do not understand from this study how root traits like root N can influence the abundance of EcM and pathogenic fungi (L. 242 - 243). Which data show this causality? It seems a strong statement, but not well supported (or explained).

Impact:<br /> The data collected for this study are timely, valuable, and relevant. Soilborne microbes (fungi and bacteria; symbionts and pathogens) play important roles in root trait expressions (e.g., root diameter) and below-ground functioning (e.g., resource acquisition). They should therefore not be excluded from studies into the belowground functioning of forests, but they mostly are. This dataset therefore has the potential to improve our understanding of this subject. Making these data publicly available in large-scale datasets that have recently been initiated (e.g., FRED) will also allow further study in comparative (with other biomes) or global (across biomes) studies.

Technically, the methodology seems sound, although I lack the expertise to judge the Molecular Methods (L. 349 - 397). However, owing to some statistical uncertainties mentioned above (that the authors might well clarify or improve) and the oversimplified discussion, I am hesitant to determine the impact of the contents of this work. Statistical improvements and/or clearer explanation/justification of statistical choices made can make this manuscript highly interesting and impact, however.

Context:<br /> As motivated above, I am not sure to what extent the EcM - AM/saprotroph presents a true ecological tradeoff. However, if it does, this work would fit very well in the context of the mycorrhizal-associated nutrient economy (Phillips et al. 2013 New Phytology). This theory postulates that EcM trees generally produce low-quality litter (associated with 'slow traits') that can be more readily accessed by EcM but not AM fungi, thereby slowing down nutrient cycling rates at their competitive advantage, and vice versa for AM tree species. This study did not aim to test the MANE, so it was beyond its scope to study litter quality, and the number of EcM and AM species was unbalanced (8 EcM versus 44 AM species): nonetheless, the denser roots of EcM species and higher root N of AM species indicates that the MANE may also apply to this subtropical forest and may be an interesting impetus for future work on this topic. It might also offer one way to bridge the root economics space and the MANE.

What I also found interesting is the sparse observations of EcM fungal taxa in the root endosphere of species typically identified as AM hosts (L. 212 - 214). While their functionality remains to be tested (fungal structures in the endosphere were not studied here), this observation might call for renewed attention to classifying species as AM, EcM, or both.

Reviewer #4 (Public Review):

Summary:<br /> Recent progress in root economics has revealed global-scale axes of covaried root traits that reflect various root resource acquisition strategies. These covariance patterns are powerful tools for understanding root functional diversity. However, roots do not function in isolation for below-ground resource acquisition. Rather, symbiotic fungi and rhizosphere microorganisms often collaborate with plant roots, forming a root-microbial-soil continuum. This study seeks to provide novel insights into this continuum by extending the existing framework of root economics to include the structures of root-associated microorganisms. I find this topic highly relevant. Considering the role of soil microorganisms is undoubtedly crucial for a more comprehensive understanding of below-ground resource strategies.

Major comments:<br /> A key finding of this study is a relationship between root N and the tendency for roots to associate with particular types of mycorrhizal associations (Line 27, Fig. 2). The authors concluded that this indicates "a linkage from simple root traits to fungal-mediated carbon nutrient cycling" (line 27) and integrates "microbial functions into the root economics framework," (line 32). If substantiated, this correlation could represent a significant discovery about the connection between root functional traits and root-associated fungi. It suggests that low root N, indicative of low metabolic activity within the root economics framework, is linked with forming EcM associations. However, I am not fully convinced this is the case based on the current data presentation and interpretation.

First, there is no biological interpretation of this relationship between root N and mycorrhizal type. It merely noted that root N is indicative of root metabolic activity, and thus by relating root N to fungal composition, "the trait-related root economics and fungal-driven nutrient economics may be integrated into a unified framework" (lines 221-224). Why would roots with low N and low metabolic activity tend to favor EcM associations? What are the potential mechanisms? Biological interpretation is essential for understanding whether a statistical correlation reflects a causal and meaningful relationship or is coincidental.

I am also concerned that this relationship may be spurious, especially when it lacks biological interpretation. EcM is underrepresented in this study (8 EcM species, of which more than half are conifers and oaks vs. 44 AM) and seems to cluster at higher elevations (line 231). Thus, the tree species/individual data points are not independent, but phylogenetically and geographically clustered. The unique properties at higher elevations (e.g., distinct plant community structures, low levels of mineral N) may drive both the lower root N and the prevalence of EcM associations. This scenario aligns with the observation that at higher elevations, AM roots also exhibited low root N (Line 231). In this case, root N may not directly relate to mycorrhizal type but is characteristic of certain locations (or closely related species), and it would be misleading to suggest that low root N/metabolic activity, a proxy in fast-slow root economics, is directly linked to the preference for a particular mycorrhizal type (lines 27-28, 220 - 224). In summary, because the studied tree species appear to be clustered both phylogenetically and geographically, these factors need to be carefully taken into account in the statistical analysis and data interpretation to understand the underlying causes of the apparent relationship and prevent overinterpretation. I also recommend, if possible, providing a visual presentation of the geographical and phylogenetic distribution of the studied tree species.

That being said, this dataset is undoubtedly valuable in revealing the shifts in the compositional structures of root-associated soil microorganisms. However, integrating the traits of microbial composition to root trait economics would require more caution and careful examination of the potential driving causes.

eLife assessment

This study divided structural brain aging into two groups, revealing that one group is more vulnerable to aging and brain-related diseases compared to the other group. This study is valuable as such subtyping could be utilized in predicting and diagnosing cognitive decline and neurodegenerative brain disorders in the future. However, the authors' claims remain incomplete, as there appears to be a lack of connection between this and the authors' claims.

Reviewer #1 (Public Review):

Summary:<br /> Duan et al analyzed brain imaging data in UKBK and found a pattern in brain structure changes by aging. They identified two patterns and found links that can be differentiated by the categorization.

Strengths:<br /> This discovery harbors a substantial impact on aging and brain structure and function.

Weaknesses:<br /> Therefore, the study requires more validation efforts. Most importantly, data underlying the stratification of the two groups are not obvious and lack further details. Can they also stratified by different methods? i.e. PCA?

Are there any external data that can be used for validation?

Other previous discoveries or claims supporting the results of the study should be explored to support the conclusion.

Sex was merely used as a covariate. Were there sex differences during brain aging? What was the sex ratio difference in groups 1 and 2?

Although statistically significant, Figure 3 shows minimal differences. LTL and phenoAge are displayed in adjusted values but what are the actual values that differ between patterns 1 and 2?

It is not intuitive to link gene expression results shown in Figure 8 and brain structure and functional differences between patterns 1 and 2. Any overlap of genes identified from analyses shown in Figure 6 (GWAS) and 8 (gene expression)?

Reviewer #2 (Public Review):

Summary:<br /> The authors aimed to understand the heterogeneity of brain aging by analyzing brain imaging data. Based on the concept of structural brain aging, they divided participants into two groups based on the volume and rate of decrease of gray matter volume (GMV). The group with rapid brain aging showed accelerated biological aging and cognitive decline and was found to be vulnerable to certain neuropsychiatric disorders. Furthermore, the authors claimed the existence of a "last in, first out" mirroring pattern between brain aging and brain development, which they argued is more pronounced in the group with rapid brain aging. Lastly, the authors identified genetic differences between the two groups and speculated that the cause of rapid brain aging may lie in genetic differences.

Strengths:<br /> The authors supported their claims by analyzing a large amount of data using various statistical techniques. There seems to be no doubt about the quality and quantity of the data. Additionally, they demonstrated their strength in integrating diverse data through various analysis techniques to conclude.

Weaknesses:<br /> There appears to be a lack of connection between the analysis results and their claims. Readers lacking sufficient background knowledge of the brain may find it difficult to understand the paper. It would be beneficial to modify the figures and writing to make the authors' claims clearer to readers. Furthermore, the paper gives an overall impression of being less polished in terms of abbreviations, figure numbering, etc. These aspects should be revised to make the paper easier for readers to understand.

Author Response

Reviewer #1 (Public Review):

Summary:

This manuscript from Mukherjee et al examines potential connections between telomere length and tumor immune responses. This examination is based on the premise that telomeres and tumor immunity have each been shown to play separate, but important, roles in cancer progression and prognosis as well as prior correlative findings between telomere length and immunity. In keeping with a potential connection between telomere length and tumor immunity, the authors find that long telomere length is associated with reduced expression of the cytokine receptor IL1R1. Long telomere length is also associated with reduced TRF2 occupancy at the putative IL1R1 promoter. These observations lead the authors towards a model in which reduced telomere occupancy of TRF2 - due to telomere shortening - promotes IL1R1 transcription via recruitment of the p300 histone acetyltransferase. This model is based on earlier studies from this group (i.e. Mukherjee et al., 2019) which first proposed that telomere length can influence gene expression by enabling TRF2 binding and gene transactivation at telomere-distal sites. Further mechanistic work suggests that G-quadruplexes are important for TRF2 binding to IL1R1 promoter and that TRF2 acetylation is necessary for p300 recruitment. Complementary studies in human triple-negative breast cancer cells add potential clinical relevance but do not possess a direct connection to the proposed model. Overall, the article presents several interesting observations, but disconnection across central elements of the model and the marginal degree of the data leave open significant uncertainty regarding the conclusions.

Strengths:

Many of the key results are examined across multiple cell models.

The authors propose a highly innovative model to explain their results.

Weaknesses:

Although the authors attempt to replicate most key results across multiple models, the results are often marginal or appear to lack statistical significance. For example, the reduction in IL1R1 protein levels observed in HT1080 cells that possess long telomeres relative to HT1080 short telomere cells appears to be modest (Supplementary Figure 1I). Associated changes in IL1R1 mRNA levels are similarly modest.

Related to the point above, a lack of strong functional studies leaves an open question as to whether observed changes in IL1R1 expression across telomere short/long cancer cells are biologically meaningful.

Statistical significance is described sporadically throughout the paper. Most major trends hold, but the statistical significance of the results is often unclear. For example, Figure 1A uses a statistical test to show statistically significant increases in TRF2 occupancy at the IL1R1 promoter in short telomere HT1080 relative to long telomere HT1080. However, similar experiments (i.e. Figure 2B, Figure 4A - D) lack statistical tests.

TRF2 overexpression resulted in ~ 5-fold or more change in IL1R1 expression. Compared to this, telomere length-dependent alterations in IL1R1 expression, although about 2-fold, appear modest (~ 50% reduction in cells with long telomeres across different model systems used). Notably, this was consistent and significant across cell-based model systems and xenograft tumors (see Figure 1). Unlike TRF2 induction, telomere elongation or shortening vary within the permissible physiological limits of cells. This is likely to result in the observed variation in IL1R1 levels. For biological relevance, we further demonstrated that IL1 signalling in TNBC tissue and tumor organoids, and M2 macrophage infiltration, was significantly dependent on telomere length. Details of tests of significance were included in the individual figure legends. Based on the comment here we will expand on it in a dedicated paragraph in the methods section to make the information clearer for readers. We noticed that the stars (*) denoting statistical significance were omitted in some ChIP-experiment figures. This was likely an error during figure assembly for PDF conversion. We thank the reviewer for bringing this up; necessary changes will be made in the revised manuscript.

Reviewer #2 (Public Review):

This study highlights the role of telomeres in modulating IL-1 signaling and tumor immunity. The authors demonstrate a strong correlation between telomere length and IL-1 signaling by analyzing TNBC patient samples and tumor-derived organoids. Mechanistic insights revealed non-telomeric TRF2 binding at the IL-1R1. The observed effects on NF-kB signaling and subsequent alterations in cytokine expression contribute significantly to our understanding of the complex interplay between telomeres and the tumor microenvironment. Furthermore, the study reports that the length of telomeres and IL-1R1 expression is associated with TAM enrichment. However, the manuscript lacks in-depth mechanistic insights into how telomere length affects IL-1R1 expression. Overall, this work broadens our understanding of telomere biology.

The mechanism of how telomere length affects IL1R1 expression involves sequestration and reallocation of TRF2 between telomeres and gene promoters (in this case, the IL1R1 promoter). We have previously shown this across multiple genomic sites (Mukherjee et al, 2018; reviewed in J. Biol. Chem. 2020, Trends in Genetics 2023). We have described this in the manuscript along with references citing the previous works. A scheme explaining the model was provided as Additional Supplementary Figure 1, along with a description of the mechanistic model.

Figure 1-4 in main figures describe the molecular mechanism of telomere-dependent IL1R1 activation. This includes ChIP data for TRF2 on the IL1R1 promoter in long/short telomeres, as well as TRF2-mediated histone/p300 recruitment and IL1R1 gene expression. We further show how specific acetylation on TRF2 is crucial for TRF2-mediated IL1R1 regulation (Figure 5).

Reviewer #3 (Public Review):

Summary:

In this manuscript, entitled "Telomere length sensitive regulation of Interleukin Receptor 1 type 1 (IL1R1) by the shelterin protein TRF2 modulates immune signalling in the tumour microenvironment", Dr. Mukherjee and colleagues pointed out clarifying the extra-telomeric role of TRF2 in regulating IL1R1 expression with consequent impact on TAMs tumor-infiltration.

Strengths:

Upon careful manuscript evaluation, I feel that the presented story is undoubtedly well conceived. At the technical level, experiments have been properly performed and the obtained results support the authors' conclusions.

Weaknesses:

Unfortunately, the covered topic is not particularly novel. In detail, the TRF2 capability of binding extratelomeric foci in cells with short telomeres has been well demonstrated in a previous work published by the same research group. The capability of TRF2 to regulate gene expression is well-known, the capability of TRF2 to interact with p300 has been already demonstrated and, finally, the capability of TRF2 to regulate TAMs infiltration (that is the effective novelty of the manuscript) appears as an obvious consequence of IL1R1 modulation (this is probably due to the current manuscript organization).

Here we studied the TRF2-IL1R1 regulatory axis (not reported earlier by us or others) as a case of the telomere sequestration model that we described earlier (Mukherjee et al., 2018; reviewed in J. Biol. Chem. 2020, Trends in Genetics 2023). This manuscript demonstrates the effect of the TRF2-IL1R1 regulation on telomere-sensitive tumor macrophage recruitment. To the best of our knowledge, no previous study connects telomeres of tumor cells mechanistically to the tumor immune microenvironment. Here we focused on the IL1R1 promoter and provided mechanistic evidence for acetylated-TRF2 engaging the HAT p300 for epigenetically altering the promoter. This mechanism of TRF2 mediated activation has not been previously reported. Further, the function of a specific post translational modification (acetylation of the lysine residue 293K) of TRF2 in IL1R1 regulation is described for the first time. Additional experiments showed that TRF2-acetylation mutants, when targeted to the IL1R1 promoter, significantly alter the transcriptional state of the IL1R1 promoter. To our knowledge, the function of any TRF2 residue in transcriptional activation had not been previously described. Taken together, these demonstrate novel insights into the mechanism of TRF2-mediated gene regulation, that is telomere-sensitive, and affects the tumor-immune microenvironment. We are considering the suggestion to reorganize the manuscript to highlight the novel aspects of our work more convincingly.

Reviewer #3 (Public Review):

Summary:<br /> In this manuscript, entitled "Telomere length sensitive regulation of Interleukin Receptor 1 type 1 (IL1R1) by the shelterin protein TRF2 modulates immune signalling in the tumour microenvironment", Dr. Mukherjee and colleagues pointed out clarifying the extra-telomeric role of TRF2 in regulating IL1R1 expression with consequent impact on TAMs tumor-infiltration.

Strengths:<br /> Upon careful manuscript evaluation, I feel that the presented story is undoubtedly well conceived. At the technical level, experiments have been properly performed and the obtained results support the authors' conclusions.

Weaknesses:<br /> Unfortunately, the covered topic is not particularly novel. In detail, the TRF2 capability of binding extratelomeric foci in cells with short telomeres has been well demonstrated in a previous work published by the same research group. The capability of TRF2 to regulate gene expression is well-known, the capability of TRF2 to interact with p300 has been already demonstrated and, finally, the capability of TRF2 to regulate TAMs infiltration (that is the effective novelty of the manuscript) appears as an obvious consequence of IL1R1 modulation (this is probably due to the current manuscript organization).

eLife assessment

This study presents an important finding on the role of telomeres in modulating interleukin-1 signaling and tumor immunity in TNBC. The evidence supporting these findings is solid, presented through comprehensive analyses including TNBC clinical samples, tumor-derived organoids, cancer cells, and xenografts. The work will be of broad interest to cell and medical biologists focusing on TNBC.

Reviewer #1 (Public Review):

Summary:<br /> This manuscript from Mukherjee et al examines potential connections between telomere length and tumor immune responses. This examination is based on the premise that telomeres and tumor immunity have each been shown to play separate, but important, roles in cancer progression and prognosis as well as prior correlative findings between telomere length and immunity. In keeping with a potential connection between telomere length and tumor immunity, the authors find that long telomere length is associated with reduced expression of the cytokine receptor IL1R1. Long telomere length is also associated with reduced TRF2 occupancy at the putative IL1R1 promoter. These observations lead the authors towards a model in which reduced telomere occupancy of TRF2 - due to telomere shortening - promotes IL1R1 transcription via recruitment of the p300 histone acetyltransferase. This model is based on earlier studies from this group (i.e. Mukherjee et al., 2019) which first proposed that telomere length can influence gene expression by enabling TRF2 binding and gene transactivation at telomere-distal sites. Further mechanistic work suggests that G-quadruplexes are important for TRF2 binding to IL1R1 promoter and that TRF2 acetylation is necessary for p300 recruitment. Complementary studies in human triple-negative breast cancer cells add potential clinical relevance but do not possess a direct connection to the proposed model. Overall, the article presents several interesting observations, but disconnection across central elements of the model and the marginal degree of the data leave open significant uncertainty regarding the conclusions.

Strengths:<br /> Many of the key results are examined across multiple cell models.

The authors propose a highly innovative model to explain their results.

Weaknesses:<br /> Although the authors attempt to replicate most key results across multiple models, the results are often marginal or appear to lack statistical significance. For example, the reduction in IL1R1 protein levels observed in HT1080 cells that possess long telomeres relative to HT1080 short telomere cells appears to be modest (Supplementary Figure 1I). Associated changes in IL1R1 mRNA levels are similarly modest.

Related to the point above, a lack of strong functional studies leaves an open question as to whether observed changes in IL1R1 expression across telomere short/long cancer cells are biologically meaningful.

Statistical significance is described sporadically throughout the paper. Most major trends hold, but the statistical significance of the results is often unclear. For example, Figure 1A uses a statistical test to show statistically significant increases in TRF2 occupancy at the IL1R1 promoter in short telomere HT1080 relative to long telomere HT1080. However, similar experiments (i.e. Figure 2B, Figure 4A - D) lack statistical tests.

Reviewer #2 (Public Review):

This study highlights the role of telomeres in modulating IL-1 signaling and tumor immunity. The authors demonstrate a strong correlation between telomere length and IL-1 signaling by analyzing TNBC patient samples and tumor-derived organoids. Mechanistic insights revealed non-telomeric TRF2 binding at the IL-1R1. The observed effects on NF-kB signaling and subsequent alterations in cytokine expression contribute significantly to our understanding of the complex interplay between telomeres and the tumor microenvironment. Furthermore, the study reports that the length of telomeres and IL-1R1 expression is associated with TAM enrichment. However, the manuscript lacks in-depth mechanistic insights into how telomere length affects IL-1R1 expression. Overall, this work broadens our understanding of telomere biology.

Reviewer #2 (Public Review):

In this study, the authors address discrepancies in determining the local bacterial burden in osteomyelitis between that determined by culture and enumeration by DNA-directed assay. Discrepancies between culture and other means of bacterial enumeration are long established and highlighted by Staley and Konopka's classic, "The great plate count anomaly" (1985). Here, the authors first present data demonstrating the emergence of discrepancies between CFU counts and genome copy numbers detected by PCR in S. aureus strains infecting osteocyte-like cells. They go on to demonstrate PCR evidence that S. aureus can be detected in bone samples from sites meeting a widely accepted clinicopathological definition of osteomyelitis. They conclude their approach offers advantages in quantifying intracellular bacterial load in their in vitro "co-culture" system.

Weaknesses<br /> - My main concern here is the significance of these results outside the model osteocyte system used by this group. Although they carefully avoid over-interpreting their results, there is a strong undercurrent suggesting their approach could enhance aetiologic diagnosis in osteomyelitis and that enumeration of the infecting pathogen might have clinical value. In the first place, molecular diagnostics such as 16S rDNA-directed PCR are well established in identifying pathogens that don't grow. Secondly, it is hard to see how enumeration could have value beyond in vitro and animal model studies since serial samples will rarely be available from clinical cases.

- I have further concerns regarding the interpretation of the combined bacterial and host cell-directed PCRs against the CFU results. Significance is attached to the relatively sustained genome counts against CFU declines. On the one hand, it must be clearly recognised that the detection of bacterial genomes does not equate to viable bacterial cells with the potential for further replication or production of pathogenic factors. Of equal importance is the potential contribution of extracellular DNA from lysed bacteria and host cells to these results. The authors must clarify what steps, if any, they have taken to eliminate such contributions for both bacteria and host cells. Even the treatment with lysotaphin may have coated their osteocyte cultures with bacterial DNA, contributing downstream to the ddPCR results presented.

Strengths<br /> - On the positive side, the authors provide clear evidence for the value of the direct buffer extraction system they used as well as confirming the utility of ddPCR for quantification. In addition, the successful application of MinION technology to sequence the EF-Tu amplicons from clinical samples is of interest.

- Moreover, the phenomenology of the infection studies indicating greater DNA than CFU persistence and differences between the strains and the different MOI inoculations are interesting and well-described, although I have concerns regarding interpretation.

eLife assessment

This useful study addresses discrepancies in determining bacterial burden in osteomyelitis as determined by culture and enumeration using DNA. The authors present compelling data demonstrating the emergence of discrepancies between CFU counts and genome copy numbers detected by PCR in Staphylococcus aureus strains infecting osteocyte-like cells. Whilst the observations may represent a substantial addition to the field of musculoskeletal infection, the broad applicability and clinical benefit are unclear.

Reviewer #1 (Public Review):

Summary:<br /> This work shows, based on basic laboratory investigations of in-vitro-grown bacteria as well as human bone samples, that conventional bacterial culture can substantially underrepresent the quantity of bacteria in infected tissues. This has often been mentioned in the literature, however, relatively limited data has been provided to date. This manuscript compares culture to a digital droplet PCR approach, which consistently showed greater levels of bacteria across the experiments (and for two different strains).

Strengths:<br /> Consistency of findings across in vitro experiments and clinical biopsies. There are real-world clinical implications for the findings of this study.

Weaknesses:<br /> No major weaknesses. Only three human samples were analyzed, although the results are compelling.

Author Response

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

Reviewer #1 (Public Review):

• A summary of what the authors were trying to achieve.

The authors cultured pre- and Post-vaccine PBMCs with overlapping peptides encoding S protein in the presence of IL-2, IL-7, and IL-15 for 10 days, and extensively analyzed the T cells expanded during the culture; by including scRNAseq, scTCRseq, and examination of reporter cell lines expressing the dominant TCRs. They were able to identify 78 S epitopes with HLA restrictions (by itself represents a major achievement) together with their subset, based on their transcriptional profiling. By comparing T cell clonotypes between pre- and post-vaccination samples, they showed that a majority of pre-existing S-reactive CD4+ T cell clones did not expand by vaccinations. Thus, the authors concluded that highly-responding S-reactive T cells were established by vaccination from rare clonotypes.

• An account of the major strengths and weaknesses of the methods and results.

Strengths

• Selection of 4 "Ab sustainers" and 4 "Ab decliners" from 43 subjects who received two shots of mRNA vaccinations.

• Identification of S epitopes of T cells together with their transcriptional profiling. This allowed the authors to compare the dominant subsets between sustainers and decliners.

Weaknesses

• Fig. 3 provides the epitopes, and the type of T cells, yet the composition of subsets per subject was not provided. It is possible that only one subject out of 4 sustainers expressed many Tfh clonotypes and explained the majority of Tfh clonotypes in the sustainer group. To exclude this possibility, the data on the composition of the T cell subset per subject (all 8 subjects) should be provided.

In accordance with the reviewer’s suggestion, we provided the composition of the T cell subset per subject (all 8 subjects) in the revised manuscript (shown below).

Author response image 1.

• S-specific T cells were obtained after a 10-day culture with peptides in the presence of multiple cytokines. This strategy tends to increase a background unrelated to S protein. Another shortcoming of this strategy is the selection of only T cells amenable to cell proliferation. This strategy will miss anergic or less-responsive T cells and thus create a bias in the assessment of S-reactive T cell subsets. This limitation should be described in the Discussion.

We thank the reviewer for raising the question related to our experimental strategy. We chose this method because a background unrelated to S protein was lower than widely used AIM methods, which is verified by reconstituting many TCRs and testing the responses in vitro. One more reason is this method can identify S-reactive functional (proliferative) T cell clonotypes than anergic or less-responsive T cells as the reviewer mentioned, which is our objective in this study. In accordance with the reviewer’s suggestion, we have carefully described our limitation and rationale of our experimental strategy in the revised manuscript.

• Fig. 5 shows the epitopes and the type of T cells present at baseline. Do they react to HCoV-derived peptides? I guess not, as it is not clearly described. If the authors have the data, it should be provided.

As the reviewer mentioned, the pre-existing highly expanded clonotypes that we analyzed did not react to HCoV-derived peptides. After we determined the epitopes of the clonotypes, the S peptide sequences were analyzed for homology in HCoVs. The only two clonotypes whose epitope sequences were relatively conserved in HCoV strains (clonotypes #8-pre_9 and #8-pre_10) were tested for their reactivity to the similar HCoV epitope counterparts, but no activation was observed (shown below). We added these data in the revised manuscript.

Author response image 2.

• As the authors discussed (L172), pre-existing S-reactive T cells were of low affinity. The raw flow data, as shown in Fig. S3, for pre-existing T cells may help discuss this aspect.

As the reviewer mentioned, some pre-existing S-reactive T cells might appear to react with S peptides judging from the NFAT-GFP expression of their reporter cell lines. However, the percentage of GFP-expressing cells is affected by many factors such as TCR expression level and HLA molecule expression level. Thus, the affinity of pre-existing S-reactive T cells was not fully deduced from the activation of reporter cell lines as shown in Fig. S3 in the present manuscript. We thank the reviewer for this constructive suggestion, but we therefore decided not to use these data quantitatively to evaluate affinity in this manuscript.

Reviewer #2 (Public Review):

Summary:

A short-term comparison of durability of S antibody levels after 2-dose vaccination, showing that better or more poorly sustained responses correlate with the presence of Tfh cells.

Strengths:

Novelty of approach in expanding, sequencing and expressing TCRs for functional studies from the implicated populations.

Weaknesses:

Somewhat outdated question, short timeline, small numbers, over-interpretation of sequence homology data

Reviewer #2 (Recommendations For The Authors):

In line with my above comments, it might be useful for the authors to look at moderating some of the assertions in what is a rather small-scale descriptive account of correlates of some quite nuanced, short-term, S antibody response differences

We clearly described that some homologous microbe-derived peptides were indeed recognized by S-reactive T cells. Also, we have removed our overstatement from the revised manuscript.

Reviewer #3 (Public Review):

Summary:

The paper aims to investigate the relationship between anti-S protein antibody titers with the phenotypes&clonotypes of S-protein-specific T cells, in people who receive SARS-CoV2 mRNA vaccines. To do this, the paper recruited a cohort of Covid-19 naive individuals who received the SARS-CoV2 mRNA vaccines and collected sera and PBMCs samples at different timepoints. Then they mainly generate three sets of data: 1). Anti-S protein antibody titers on all timepoints. 2) Single-cell RNAseq/TCRseq dataset for divided T cells after stimulation by S-protein for 10 days. 3) Corresponding epitopes for each expanded TCR clones. After analyzing these results, the paper reports two major findings & claims: A) Individuals having sustained anti-S protein antibody response also have more so-called Tfh cells in their single-cell dataset, which suggests Tfh-polarization of S-specific T cells can be a marker to predict the longevity of anti-S antibody. B). S-reactive T cells do exist before the vaccination, but they seem to be unable to respond to Covid-19 vaccination properly.

The paper's strength is it uses a very systemic and thorough strategy trying to dissect the relationship between antibody titers, T cell phenotypes, TCR clonotypes and corresponding epitopes, and indeed it reports several interesting findings about the relationship of Tfh/sustained antibody and about the S-reactive clones that exist before the vaccination. However, the main weakness is these interesting claims are not sufficiently supported by the evidence presented in this paper. I have the following major concerns:

(1) The biggest claim of the paper, which is the acquisition of S-specific Tfh clonotypes is associated with the longevity of anti-S antibodies, should be based on proper statistical analysis rather than just a UMAP as in Fig2 C, E, F. The paper only shows the pooled result, but it looks like most of the so-called Tfh cells come from a single donor #27. If separating each of the 4 decliners and sustainers and presenting their Tfh% in total CD4+ T cells respectively, will it statistically have a significant difference between those decliners and sustainers? I want to emphasize that solid scientific conclusions need to be drawn based on proper sample size and statistical analysis.

In accordance with the reviewer’s request, we have also analyzed the T cells separately (shown below). We observed the average frequency was much lower in decliners than sustainers, while the difference did not reach statistical significance partly because of the large deviation due to one sustainer (#27) who possessed quite a high Tfh%. We modified our description in the revised manuscript.

Author response image 3.

(2) The paper does not provide any information to justify its cell annotation as presented in Fig 2B, 4A. Moreover, in my opinion, it is strange to see that there are two clusters of cells sit on both the left and right side of UMAP in Fig2B but both are annotated as CD4 Tcm and Tem. Also Tfh and Treg belong to a same cluster in Fig 2B but they should have very distinct transcriptomes and should be separated nicely. Therefore I believe the paper can be more convincing if it can present more information and discussion about the basis for its cell annotation.

We agree with the reviewer’s concern. Since antigen stimulation only induced the proliferation of antigen-specific T cells, the multiple clusters were mostly due to the fluctuation of cell cyclerelated genes. We therefore carefully and manually annotated these clusters by selecting the cell type-related genes (Kaech et al, Nat. Rev. Immunol., 2002; Sallusto et al, Annu Rev Immunol., 2004) and determined their subsets regardless of the automatic clustering based on the whole transcriptome. Indeed, antigen-responded Tfh and Treg are close, as ICOS and PDCD1 are expressed. We mainly used IL21 and FOXP3 to distinguish the Tfh and Treg populations, respectively. We thank the reviewer for pointing out this important process that we carefully addressed. We added the description of annotation methods to the revised manuscript.

(3) Line 103-104, the paper claims that the Tfh cluster likely comes from cTfh cells. However considering the cells have been cultured/stimulated for 10 days, cTfh cells might lose all Tfh features after such culture. To my best knowledge there is no literature to support the notion that cTfh cells after stimulated in vitro for 10 days (also in the presence of IL2, IL7 and IL15), can still retain a Tfh phenotype after 10 days. It is possible that what actually happens is, instead of having more S-specific cTfh cells before the cell culture, the sustainers' PBMC can create an environment that favors the Tfh cell differentiation (such as express more pro-Tfh cytokines/co-stimulations). Thus after 10-days culture, there are more Tfh-like cells detected in the sustainers. The paper may need to include more evidence to support cTfh cells can retain Tfh features after 10-days' culture.

We thank the reviewer for raising this important issue. As the reviewer pointed out, culturing T cells for 10 days indeed changed the repertoire and features, so the Tfh clonotypes we detected after the expansion may not correspond to the cTfh clonotypes in vivo. Because our observation and analysis were mostly based on the dominant T cell clonotypes expanded in vitro, we modified our description and conclusion accordingly in the revised manuscript.

(4) It is in my opinion inaccurate to use cell number in Fig4B to determine whether such clone expands or not, given that the cell number can be affected by many factors like the input number, the stimulation quality and the PBMC sample quality. A more proper analysis should be considered by calculating the relative abundance of each TCR clone in total CD4 T cells in each timepoint.

We thank the reviewer for pointing out our inaccuracy. As the reviewer suggested, we used percentages to demonstrate the relative abundance of each clonotype in Fig. 4B of the revised manuscript.

(5) It is well-appreciated to express each TCR in cell line and to determine the epitopes. However, the author needs to make very sure that this analysis is performed correctly because a large body of conclusions of the paper are based on such epitope analysis. However, I notice something strange (maybe I am wrong) but for example, Table 4 donor #8 clonotype post_6 and _7, these two clonotypes have exactly the same TRAV5 and TRAJ5 usage. Because alpha chain don't have a D region, in theory these clonotypes, if have the same VJ usage, they should have the same alpha chain CDR3 sequences, however, in the table they have very different CDR3α aa sequences. I wish the author could double check their analysis and I apologize in advance if I raise such questions based on wrong knowledge.

We thank the reviewer for carefully reading our manuscript. Although the two clonotypes, donor #8 clonotype post_6 and _7, have the exactly same TRAV5 and TRAJ5 usage, they have different CDR3a aa sequences due to random nucleotide addition in the rearrangement. Likewise, donor #27 clonotype post_1 and donor #13 clonotype post_15 had the same TRAV9-2 and TRAJ17 usage but different CDR3a.

Reviewer #3 (Recommendations For The Authors):

(1) Related to my public review 1. To make a solid conclusion, I think the author can include more sustainers and decliners if possible, can just stimulate their PBMCs for 10 days and check the Tfh features in proliferated CD4 T cells (e.g. IL21 secretion, PD-1 expression etc). And then compare these values in sustainers vs decliners

We thank the reviewer for the suggestion. Unfortunately, additional PBMCs from more sustainers and decliners are not available to us. Instead, we carefully described the current observation in the revised manuscript.

(2) Related to my public review 3. The author can attempt to sort CXCR5+ cTfh and CXCR5- non cTfh, stimulate in vitro for 10 days and compare whether the stimulated cTfh still have more Tfh-related features such as increased IL- 21 secretion.

As the reviewer recommended, sorting and culturing the cTfh and non cTfh separately will clarify this issue. Due to the limitation of the samples, we could not perform these experiments.

(3) I couldn't find information about the availability of data and code to analyze the single cell RNA-seq dataset in the manuscript

We clarified the availability of data and added the codes for the single cell RNA-seq dataset in the revised manuscript.

eLife assessment

This study presents an important finding on the key factors of T cell responses associated with durable antibody responses following COVID-19 mRNA vaccinations. Though the sample size is small, and in-vitro stimulated T cells were used, the analysis and approaches were extensive, and the collected data were mostly solid. The results may greatly impact future COVID-19 vaccine design.

Reviewer #1 (Public Review):

• A summary of what the authors were trying to achieve.

The authors cultured pre- and Post-vaccine PBMCs with overlapping peptides encoding S protein in the presence of IL-2, IL-7, and IL-15 for 10 days, and extensively analyzed the T cells expanded during the culture; by including scRNAseq, scTCRseq, and examination of reporter cell lines expressing the dominant TCRs. They were able to identify 78 S epitopes with HLA restrictions (by itself represents a major achievement) together with their subset, based on their transcriptional profiling. By comparing T cell clonotypes between pre- and post-vaccination samples, they showed that a majority of pre-existing S-reactive CD4+ T cell clones did not expand by vaccinations. Thus, the authors concluded that highly-responding S-reactive T cells were established by vaccination from rare clonotypes.

• An account of the major strengths and weaknesses of the methods and results.

Strengths:

• Selection of 4 "Ab sustainers" and 4 "Ab decliners" from 43 subjects who received two shots of mRNA vaccinations.<br /> • Identification of S epitopes of T cells together with their transcriptional profiling. This allowed the authors to compare the dominant subsets between sustainers and decliners.

Weaknesses were properly addressed in the revised manuscript, and I do not have any additional concerns.

Reviewer #3 (Public Review):

Summary: The paper aims to investigate the relationship between anti-S protein antibody titers with the phenotypes&clonotypes of S-protein-specific T cells, in people who receive SARS-CoV2 mRNA vaccines. To do this, the paper recruited a cohort of Covid-19 naive individuals that receives the SARS-CoV2 mRNA vaccines and collect sera and PBMCs samples on different timepoints. Then they mainly generate three sets of data: 1). Anti-S protein antibody titers on all timepoints. 2) Single-cell RNAseq/TCRseq dataset for divided T cells after stimulation by S-protein for 10 days. 3) Corresponding epitopes for each expanded TCR clones. After analyzing these result, the paper reports two major findings&claims: A) Individuals having sustained anti-S protein antibody response also have more so-called Tfh cells in their single-cell dataset. B). S-reactive T cells do exist before the vaccination, but they seems to be unable to response to Covid-19 vaccination properly.

The paper's strength is it uses a very systemic and thorough strategy trying to dissect the relationship between antibody titers, T cell phenotypes, TCR clonotypes and corresponding epitopes, and indeed it reports several interesting findings about the relationship of Tfh clonotypes/sustained antibody and about the S-reactive clones that exist before the vaccination. The conclusion is solid in general but some claims are overstated. My suggestion is the authors should further limit their claims in abstract, for example,

"Even before vaccination, S-reactive CD4+ T cell clonotypes did exist, most of which (MAY) cross-reacted with environmental or symbiotic bacteria" -- The paper don't have experimental evidence to show these TCR clones respond to these epitopes.

"These results suggest that de novo acquisition of memory Tfh-like cells upon vaccination (LIKELY) contributes to the longevity of anti-S antibody titers." --Given the small sample size and the statistical analysis was not significant, this claim was overstated.

"S-reactive T cell clonotypes detected immediately after 2nd vaccination polarized to follicular helper T (Tfh)-like cells (UNDER IN VITRO CULTURE)". -- the conclusion was based on vitro cultured cells, which had limitation.

Author Response

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

Comment 1: The authors showed increased plasma IL-22 and its expression in the intestine. Are intestinal ILC3s the main source of plasma IL-22?

Reply: ILC3s are the main source of IL-22 as reported previously (PMID: 30700914). In the small intestine, ILC3s account for about 62% of IL22+ cells. Other IL22+ cells include γδ T, Foxp3+T and CD4+T cells.

Comment 2: The authors transplanted intestinal ILC3s from NCD mice to DIO mice and showed significant metabolic improvements. However, in Fig. 1, intermittent fasting increased IL-22positive ILC3s proportion rather than changing the total number. Please clarify whether this transplantation is due to increasing ILC3s number or introducing more IL-22 positive ILC3s (which are decreased in DIO). Are these transplanted ILC3s by default homing to the intestine rather than to other tissues?

Reply: We believe that the transplantation increases ILC3s number, leading to the increment in IL22 levels. The transplanted ILC3s by default are homing to the intestine rather than to other tissues because ILC3s express several homing receptors such as CCR7, CCR9, and α4β7, which modulate their capacity to migrate to the gut (PMID: 26141583; PMID: 26708278; PMID: 25575242; PMID: 34625492). Our observation that ILC3s in adipose tissue remained unchanged by ILC3 cell transplantation (Supplementary Figure 5F) also supports this concept.

Comment 3: Thermogenesis in this acute cold challenge is mainly by brown adipose tissue. Beiging is a chronic and adaptive response. Based on the data in WAT, there is a beiging phenotype, but the core body temperature in acute cold challenge is not an accurate readout. It would be a missed opportunity by not evaluating thermogenic activity in BAT. More browning genes should be included to strengthen the beiging phenotype of WAT. Moreover, inflammation in WAT can be examined to provide a whole picture of adipose tissue remodeling through this pathway.

Reply: Per suggestion, we performed additional experiments to measure levels of inflammation genes such as Il4, Il1b, Il6, Il22, Il23, Il17a. As shown in supplemental figure 2D, these inflammation relevant genes were not altered.

Comment 4: For the SVF beige adipocyte differentiation, 100 ng/mL IL-22 was used. This is highly above the physiological concentration at ~5 pg/mL. Please justify this high concentration used.

Reply: We agree with the reviewer that the dose of IL-22 used is high. However, the efficient dose at 100 ng/ml used in our studies is consistent with the literatures. Previous reports have shown that IL-22 directly activates Stat3 in adipose tissue and primary adipocytes, and promotes the expression of genes involved in triglyceride lipolysis (Lipe and Pnpla2) and fatty-acid β-oxidation (Acox1) at the dose of 100 ng/ml (Wang X, Ota N, et al. Nature. 2014). Consistently, other studies have reported that IL-22 at 100 ng/ml significantly reversed the enhanced expression of CCL2, CCL20 and IL1B mRNAs in granulosa cells in vitro (Qi X, et al. Nat Med. 2019).

Comment 5: The authors showed increased Ucp1 and Cidea expression by IL-22 treatment in SVFs. Please be aware that these increases are likely due to boosted adipogenesis as told by the morphology. Please examine more adipogenic markers to confirm. Is this higher adipogenesis caused by the high concentration of IL-22?

Reply: Per suggestion, we examined the expression of adipogenic marker genes such as Pparγand Fabp4. We found that IL-22 did not increase the levels of these adipogenic marker genes relevant to the PBS control as shown in supplemental figure 6F.

Author response image 1.

Comment 6: In line 201, the authors drew the conclusion that IL-22 increased SVF beige differentiation. To fully support this conclusion, the authors should assure adipogenesis at the same baseline and then compare beiging, or examine the effect of IL-22 on normal adipogenesis to compare with beige differentiation.

Reply: We examined the expression of adipogenic marker genes such as Pparγ and Fabp4 and found that IL-22 did not increase the expression of these adipogenic marker genes relevant to the PBS control.

Reviewer #2:

This study aims to investigate the mediatory role of intestinal ILC3-derived IL-22 in intermittent fasting-elicited metabolic benefits.

Strengths:

The observation of induction of IL-22 production by intestinal ILC3 is significant, and the scRNAseq provides new information into intestine-resident immune cell profiling in response to repeated fasting and refeeding.

Weaknesses:

The experimental design for some studies needs to be improved to enhance the rigor of the overall study. There is a lack of direct evidence showing that the metabolically beneficial effects of IF are mediated by intestinal ILC3 and their derived IL-22. The mechanism by which IL-22 induces a thermogenic program is unknown. The browning effect induced by IF may involve constitutive activation of lipolysis, which was not considered.

Comment 1: Lack of direct evidence showing that IL-22-expressing ILC3s in intestine is the key contributor to intermittent fasting (IF)-mediated elevation of circulating IL-22 levels. The fraction of IL-22-expressing cells was increased threefold by IF but the increase in circulating IL-22 is moderate (Figs. 1J and 1K).

Reply: IL-22 in circulation is subjected to clearance, degradation, and binding with plasma proteins, et al. Thus, circulating levels of IL-22 may be much lower than the amount secreted by the intestinal IL-22 positive ILC3s.

Comment 2: The loss of fat mass by IF suggests that the active lipolysis may explain the white fat browning which was not considered. This may apply to the observations in IL-22 treated mice as well as IL-22R KO mice.

Reply: We analyzed the expression of genes relate to lipolysis in NCD and NCD-IF mice and found that IF did not alter the levels of these genes in white adipose tissues (Supplementary figure 2D). We have addressed this concerns in lines 119, page 6.

Author response image 2.

Comment 3: IL-22 administration and adoptive transfer of ILC3 had no significant effect on body weight. Not clear how IL-22 improves insulin sensitivity in this case.

Reply: Our results are consistent with previous report showing that IL-22 administration improves insulin sensitivity without change in body weight (Qi X, et al. Nat Med. 2019). In addition, previous studies have demonstrated that IL-22 can increase Akt phosphorylation in muscle, liver and adipose tissues, leading to improvement in insulin sensitivity (Wang X, et al. Nature. 2014). We have addressed this potential mechanism in lines192-195, page 9.

Comment 4: The energy expenditure data look unusual given that there was little increase in oxygen consumption during dark cycle compared to light cycle (Fig.3).

Reply: The not so obvious difference in oxygen consumption between dark cycle and light cycle may be due to the technical problem of the system.

Comment 5: The thermogenic capacity for the whole fat pad needs to consider the expression of UCP1 in certain amount of tissue and the total mass for each individual animal because the mRNA level itself does not reflect the whole tissue capacity.

Reply: We used the whole subcutaneous adipose tissue from one side for qPCR to reflect the whole tissue capacity.

Comment 6: The design of studies for the adoptive transfer of ILC3 was concerned. The PBS is not a good control for the group with ILC3 cells (Figs. 2A-2H). Similar issue applies for the co-culture study in which beige only is not an ideal control for Beige+ILC3 (Figs. 2I-2J).

Reply: We agree with the reviewer that the PBS is not a good control. Because we cannot find a similar immune cell without any effect on adipocytes, we designed this experiment based on other studies in which saline or PBS are used as ILC transfer experiment controls (Sasaki T, et al. Cell Rep. 2019; Wang H, et al. Nat Commun. 2019)

Comment 7: The induction of thermogenesis by IL-22 treatment may be related to enhanced differentiation rather than direct activation of thermogenic genes (Figs. 4G and 4H).

Reply: Our observation that IL-22 did not alter the levels of genes related to adipogenesis (Supplemental figure 6F) indicates that IL-22 may not alter the differentiation of adipocytes. We addressed this concern in Lines 211-212, page 10.

Reviewer #3:

Chen et al. investigated how intermittent fasting causes metabolic benefits in obese mice and found that intestinal ILC3 and IL-22-IL-22R signaling contribute to the beiging of white adipose tissue (WAT) and consequent metabolic benefits including improved glucose and lipid metabolism in diet-induced obese mice. They demonstrate that intermittent fasting causes increased IL22+ILC3 in small intestines of mice. Adoptive transfer of purified intestinal ILC3 or administration of exogenous IL-22 can lead to increases in UCP1 gene expression and energy expenditure as well as improved glucose metabolism. Importantly, the above metabolic benefits caused by intermittent fasting are abolished in IL-22R-/- mice. Using an in vitro experiment, the authors show that ILC3derived IL-22 may directly act on adipocytes to promote SVF beige differentiation. Finally, by performing sc-RNA-seq analysis of intestinal immune cells from mice with different treatments, the authors indicate a possible way of intestinal ILC3 being activated by intermittent fasting. Overall, this study provides a new mechanistic explanation for the metabolic benefits of intermittent fasting and reveals the role of intestinal ILC3 in the enhancement of the whole-body energy expenditure and glucose metabolism likely via IL-22-induced beige adipogenesis.

Although this study presents some interesting findings, particularly IL-22 derived from intestinal ILC3 could induce beiging of WAT by directly acting on adipocytes, the experimental data are not sufficient to support the key claims in the manuscript.

Comment 1: Only increased UCP1 expression on mRNA level is not enough to support the beiging of WAT. More methods such as western blotting and immunostaining of UCP1 in WAT are needed to confirm the enhanced beige adipogenesis.

Reply: Additional experiments have been performed to measure the UCP1 protein by Western blot. The data is included in Figure 4I and Supplementary Figure 2E.

Comment 2: IL-22 is known to modulate metabolic pathways via multiple downstream functions. The use of whole-body knockout of IL-22R could not exclude the indirect effect on the promotion of beiging of WAT. Specific deletion of IL-22R in adipose tissues is therefore needed to confirm the direct effect of IL-22 on adipocytes which is suggested by the in vitro study.

Reply: We agreed with the reviewer that specific deletion of IL-22R in adipose tissues is critical to confirm the direct effect of IL-22 on adipocytes. We will generate the AdioQ-IL-22R-/- mice to test this concept further in vivo.

Comment 3: The authors failed to show the cellular distribution of IL-22R in adipose tissues. This is important because the mechanism that explains the increased beige adipogenesis could be different based on the expression of IL-22R in adipose progenitor cells or mature adipocytes. So it is not appropriate to conclude that "IL-22 then directly activates IL-22R on adipocytes, leading to subsequent induction of beiging of white adipose tissue" in line 407. Additionally, Oil red O staining is needed for Fig 4G and Fig 5J, and protein levels of UCP1 and adipogenesis-related markers are needed to evaluate beige fat differentiation and the whole adipogenesis.

Reply: Per suggestion, we have added the expression of IL-22R in adipose progenitor cells or mature adipocytes (Supplementary Figure 6E). In addition, protein levels of UCP1 and adipogenesis-related markers to evaluate the whole adipogenesis (Figure 4I, Supplementary figure 6F) are now included. We have also addressed this issue in lines 207-215, page 10.

Comment 4: Although the authors provided some hypothesis about how intermittent fasting increases IL-22+ILC3 in small intestines by sc-RNA-seq analysis, some functional assays are needed to identify the factors, for example, how about the levels of macrophage-derived IL-23 or AHR ligands in small intestines and whether they contribute to increased percentages of intestinal IL-22+ILC3 following intermittent fasting.

Reply: We used flow cytometry sorting of macrophages combined with qPCR experiments to preliminarily demonstrate that intermittent fasting increases the expression of molecules such as Cd44 and CCl4 (Supplementary Figure 10B), which may contribute to the increase in the proportion of IL-22+ ILC3s in the intestine under intermittent fasting. Our observation that IL-23 mRNA levels were not changed indicates that this molecule may not the major contributor for the communication between macrophage and ILC3s. Other potential molecules such as AHR ligands remain to be explored.

Comment 5: What are the differences between adipose ILC3 and intestinal ILC3? Why do transferred ILC3 only migrate to the small intestine but not WAT of recipient mice? It would be better to examine or at least discuss whether other factors from intestinal ILC3 may also contribute to beiging of WAT following intermittent fasting.

Reply: Intestinal ILC3s specifically express gut homing receptors CCR7, CCR9, and α4β7 (PMID: 26141583; PMID: 26708278; PMID: 25575242; PMID: 34625492). This may explain transplantation of intestinal ILC3s can migrate mainly to the intestine instead of adipose tissue (PMID: 34625492). The proportion of ILC3s in adipose tissue of mice is very small. Their functions have not been clarified yet. We have addressed this issue in lines 156-158, page 8.

There are some other factors from intestinal ILC3 which may also contribute to beiging of WAT following intermittent fasting. By secreting IL-22, ILC3 enhanced the intestinal mucosal barrier, leading to reduction of the influx of LPS and PGN into the bloodstream under high-fat diet conditions, and subsequent increase in the beiging of white adipose tissue (Chen H, et al. Acta Pharm Sin B. 2022). We have addressed this potential mechanism in lines 344-347, page 16.

Comment 6: The sensitivity of the IL-22 ELISA kit used in the manuscript was 8.2 pg/mL, according to the information from the methods, however, in Fig. 1J and Fig. 2B, the IL-22 levels in mouse plasma were lower than 6 pg/mL, which was below the sensitivity of the ELISA kit and also the assay range. Please explain.

Reply: We have double-checked the original data and found that we have made a mistake in calculating the concentration of IL-22. We have corrected this error (Fig. 1J, Fig. 2B).

Comment 7: In Fig 7A, the significance of the Hypothesis testing should be marked. In Fig 7F and 7G, the contrast between the two groups is not apparent, other comparing ways could be used to enhance the readability.

Reply: Per suggestion, we have marked the significance of the hypothesis testing between HFD vs NCD and HFD-IF vs HFD in Fig7A. Shown in Fig 7F and 7G are the top 20 enriched interacting proteins between different cell types. The dot plot displays the average expression level and significance of protein interactions in cell types.

Comment 8: The total food intake of fasting mice fed with NCD or HFD was less than those without fasting, and the food intake rate the author showed in Fig S1 represents the value that was normalized to body weight. So the author should describe it precisely In line 114.

Reply: We have revised the statement accordingly in line 114-115.

Comment 9: Western blotting analysis has been described in methods, however, there is no corresponding experimental data in the result part.

Reply: The Western blotting results are now included.

Reviewer #3 (Public Review):

Chen et al. investigated how intermittent fasting causes metabolic benefits in obese mice and find that intestinal ILC3 and IL-22-IL-22R signaling contribute to the beiging of white adipose tissue (WAT) and consequent metabolic benefits including improved glucose and lipid metabolism in diet-induced obese mice. They demonstrate that intermittent fasting causes increased IL22+ILC3 in small intestines of mice. Adoptive transfer of purified intestinal ILC3 or administration of exogenous IL-22 can lead to increases in UCP1 gene expression and energy expenditure as well as improved glucose metabolism. Importantly, the above metabolic benefits caused by intermittent fasting are abolished in IL-22R-/- mice. Using an in vitro experiment, the authors show that ILC3-derived IL-22 may directly act on adipocytes to promote SVF beige differentiation. Finally, by performing sc-RNA-seq analysis of intestinal immune cells from mice with different treatments, the authors indicate a possible way of intestinal ILC3 being activated by intermittent fasting. Overall, this study provides a new mechanistic explanation for the metabolic benefits of intermittent fasting and reveals the role of intestinal ILC3 in the enhancement of the whole-body energy expenditure and glucose metabolism likely via IL-22-induced beige adipogenesis.

Although this study presents some interesting findings, particularly IL-22 derived from intestinal ILC3 could induce beiging of WAT by directly acting on adipocytes, the experimental data are not sufficient to support the key claims in the manuscript.

eLife assessment

This study provides valuable findings showing the production of IL-22 from intestinal ILC3 during intermittent fasting promotes beigeing of white adipose tissue. The authors provided solid data and mechanistic insight by which IL-22-derived from ILC3 directly induces beigeing.

Reviewer #1 (Public Review):

In the present study, the authors carefully evaluated the metabolic effects of intermittent fasting on normal chow and HFD fed mice and reported that intermittent fasting induces beiging of subcutaneous white adipose tissue. By employing complementary mouse models, the authors provided compelling evidence to support a mechanism through ILC3/IL-22/IL22R pathway. They further performed comprehensive single-cell sequencing analyses of intestinal immune cells from lean, obese, obese undergone intermittent fasting mice and revealed altered interactome in intestinal myeloid cells and ILC3s by intermittent fasting via activating AhR. Overall, this is a very interesting and timely study uncovering a novel connection between intestine and adipose tissue in the context of executing metabolic benefits of intermittent fasting.

(1) The authors showed increased plasma IL-22 and its expression in intestine. Are intestinal ILC3s the main source of plasma IL-22?

(2) The authors transplanted intestinal ILC3s from NCD mice to DIO mice and showed significant metabolic improvements. However, in Fig. 1, intermittent fasting increased IL-22-positive ILC3s proportion rather than changing the total number. Please clarify whether this transplantation is due to increasing ILC3s number or introducing more IL-22 positive ILC3s (which are decreased in DIO). Are these transplanted ILC3s by default homing to intestine rather than to other tissues?

(3) The authors adopted cold challenge at 4 degree for 6 hours to assess beiging in subcutaneous WAT and showed difference in core temperature. However, thermogenesis in this acute cold challenge is mainly by brown adipose tissue. Beiging is a chronic and adaptive response. Based on the data in WAT, there is a beiging phenotype, but the core body temperature in acute cold challenge is not an accurate readout. It would be a missed opportunity by not evaluating thermogenic activity in BAT.<br /> More browning genes should be included to strengthen the beiging phenotype of WAT. Moreover, inflammation in WAT can be examined to provide a whole picture of adipose tissue remodeling through this pathway.

(4) For the SVF beige adipocyte differentiation, 100 ng/mL IL-22 was used. This is highly above the physiological concentration at ~5 pg/mL. Please justify this high concentration used.

The authors showed increased Ucp1 and Cidea expression by IL-22 treatment in SVFs. Please be aware that these increases are likely due to boosted adipogenesis as told by the morphology. Please examine more adipogenic markers to confirm. Is this higher adipogenesis caused by the high concentration of IL-22?<br /> In line 201, the authors drew the conclusion that IL-22 increased SVF beige differentiation. To fully support this conclusion, the authors should assure adipogenesis at the same baseline and then compare beiging, or examine the effect of IL-22 on normal adipogenesis to compare with beige differentiation.

Reviewer #2 (Public Review):

Summary:<br /> This study aims to investigate the mediatory role of intestinal ILC3-derived IL-22 in intermittent fasting-elicited metabolic benefits.

Strengths:<br /> The observation of induction of IL-22 production by intestinal ILC3 is significant, and the scRNAseq provides new information into intestine-resident immune cell profiling in response to repeated fasting and refeeding.

Weaknesses:<br /> The experimental design for some studies needs to be improved to enhance the rigor of overall study. There is a lack of direct evidence showing that the metabolically beneficial effects of IF are mediated by intestinal ILC3 and their derived IL-22. The mechanism by which IL-22 induces thermogenic program is unknown. The browning effect induced by IF may involve constitutive activation of lipolysis, which was not considered.

Majority of weaknesses have been addressed in the revision. Based on the analysis of thermogenic genes in addition to Ucp1 (Fig. 4D and S6F), the alteration on thermogenesis induced by IL-22 is dependent on UCP1 but not other markers such as PGC1a, PPARg, and Cidea. The data need to be discussed in the Section of Discussion.

Author Response

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

We have made substantial revisions to the manuscript, incorporating new data, which led to a renumbering and relabeling of several figures: • Figure 3F now features a modified graph color.

• Figure 4I introduces a new experiment.

• What was previously labeled as Figure 4I-O is now Figure 4J-P.

• Figure 5H presents another new experiment.

• The earlier Figure 5H is now rebranded as Figure 5I.

• A fresh experiment has been incorporated into Supplement Figure 1a.

• The former Supplement Figure 1a is now Supplement Figure 1b.

• Supplement Figure 2d describes an additional new experiment.

• In accordance with the HUGO gene nomenclature committee (HGNC) recommendations, we've updated the names of genes/proteins in both figures and their accompanying legends.

Reviewer #1 (Recommendations For The Authors):

Comment #1. Standard practice would include multiple TNBC cell lines to test the author's hypotheses, but the authors rely only on one cell line in the entire paper, MDA-MB-231 cells. The authors do correlate their findings to patient data, but the inclusion of an additional TNBC cell line would strengthen their findings about the L-DOXR cells and help with the assessment as to how reproducible their original microfluidics system is.

Response: Thank you for your valuable feedback. We recognize the importance of utilizing multiple TNBC cell lines for rigorous validation and reproducibility. There are several reports highlighting the generation of L-DOXR cells in other types of breast cancer cell lines, such as MCF-7 (Fei et al., 2015), and in other cancer types like the prostate cancer cell line PC-3. These studies utilized a microfluidic device with a concentration gradient of Doxorubicin. With this existing evidence, we are confident that a variety of cancer cell types have the potential to form L-DOXR cells in a doxorubicin gradient. The cited reports support our choice of the MDA-MB-231 cell line for our current study:

“L-DOXR cells exhibit increased genomic content (4N+) as compared to WT cells. The presence of cells with increased nuclear size and increased genomic content has been demonstrated to be associated with poor clinical outcomes in several types of cancers (Alharbi et al., 2018; Amend et al., 2019; Fei et al., 2015; Imai et al., 1999; Liu et al., 2018; Lv et al., 2014; Mukherjee et al., 2022; O’connor et al., 2002; Saini et al., 2022; Trabzonlu et al., 2023). (Page 5, Line 24)”

However, we acknowledge the validity of your point regarding the strengthening of our findings with the inclusion of additional TNBC cell lines. We are considering expanding our research in future studies to further validate our findings across multiple TNBC cell lines. Thank you for bringing this to our attention, and we hope our response adequately addresses your concerns.

Comment #2. It would be helpful to comment on the frequency at which doxorubicin is used clinically to treat TNBC patients. The authors equate their resistance phenotype to all chemotherapies (in patient data and title) but only test doxorubicin. Does NUPR1 overexpression result in resistance to other chemotherapies?

Response: Thank you for raising these pertinent questions. To address your first point regarding the clinical use of doxorubicin for TNBC patients: At the Samsung Medical Center, the typical chemotherapy regimen for TNBC patients involves administering Neo. AC (Doxorubicin 34 mg + Cyclophosphamide 840 mg per session) four times, followed by Adj. D (Docetaxel 25 mg + 80 mg per session) for another four sessions. This provides insight into the clinical relevance and frequency of Doxorubicin's use in treating TNBC.

Regarding your second point about NUPR1 overexpression and its broader implications for chemotherapy resistance: Yes, NUPR1 overexpression has been documented to result in resistance to various chemotherapies. A study by Lei Jiang et al. in the Journal of Pharmacy and Pharmacology found that NUPR1 plays a role in YAP-mediated gastric cancer malignancy and drug resistance through the activation of AKT and p21 (Jiang et al., 2021, https://doi.org/10.1093/jpp/rgab010). Additionally, another study by Wang et al. in Cell Death and Disease observed that the transcriptional coregulator NUPR1 is linked to tamoxifen resistance in breast cancer cells (Wang et al., 2021, https://doi.org/10.1038/s41419-021-03442-z). In light of this, while our study primarily focused on doxorubicin, the role of NUPR1 in resistance spans across various chemotherapeutic agents, adding depth to our findings and their broader implications in cancer therapy.

Comment #3. The authors knockdown NUPR1 in L-DOXR cells, but overexpression of NUPR1 in WT TNBC cells to see if this renders the WT cells more resistant would be an important experiment.

Response: We appreciate the reviewer's suggestion, which indeed underscores an important aspect of our study. In response, we have incorporated additional experiments in the revised manuscript. Specifically, on page 7 (lines 7-8) and in Supplement Figure 2c, we present data from experiments where we overexpressed Nupr1 in WT-MDA-MB231 cells. Our findings revealed that overexpression of GST-Nupr1 not only attenuates Dox-induced cell death but also mildly enhances cell viability in WT cells even without DOX treatment. This implies that cells expressing Nupr1 exhibit resistance to the cytotoxic effects of DOX. We believe these new data further solidify our conclusions and address the valuable point you raised.

Comment #4. The similar colors/symbols chosen for the different groups in the xenograft plots are hard to easily interpret without zooming in.

Response: We modified the xenograft plots as you recommended in Figure 3F.

Comment #5. There are some grammatical errors throughout the paper. Below is an example: In the opening of the Discussion "TNBC is the most aggressive subtype of breast cancer, and chemotherapy is a mainstay of treatment. However, chemoresistance is common and contributes to the long-term survival of TNBC patients" - this sentence makes it seem like chemoresistance makes TNBC patients survive longer. The following sentence "These cells demonstrated a large phenotype with increased genomic content." is abrupt and doesn't make sense. Consider carefully re-reading the manuscript for grammatical errors.

Response: Thank you for highlighting the grammatical errors and providing specific <br /> examples. We deeply apologize for the oversight. In response to your feedback, we've carefully re-reviewed the manuscript and made the necessary corrections. Based on your example: We've revised the sentences to: “TNBC is the most aggressive subtype of breast cancer, with chemotherapy being a mainstay of treatment. However, the development of chemoresistance frequently occurs and poses significant challenges to the long-term survival prospects of TNBC patients.” “As for the cells in question, they exhibited an enlarged phenotype along with an increased genomic content.”

We appreciate your meticulous review, and we have made an effort to address and rectify other such errors throughout the manuscript.

Reviewer #2 (Recommendations for The Authors):

I recommend the authors to address the following minor issues. Below are specific comments on the manuscript.

Comments # 1. Thank you for the comment. In CDRA chip, DOXR cells and L-DOXR cells appeared in the mid-DOX region. What is the concentration of DOX in this region? Can the authors calculate the concentrations of DOX in high-, mid-, and low- regions (or ranges of concentrations)?

Response: Instead of DOX, we used FITC dye to visualize the concentration gradient over the chip as below because DOX generate very low fluorescent light.

Author response image 1.

While our method provides an estimation rather than precise measurement due to the difference in molecular weight between FITC (389.38 g/mol) and DOX (579.98 g/mol), it is still possible to approximate the distribution of DOX concentrations across different regions. We utilize a formula where the ratio of the average fluorescence intensity of FITC for each specific region to the highest recorded fluorescence intensity is multiplied by the peak DOX concentration (1.5 μM). This approach gives us an estimated average concentration of DOX in each region, acknowledging that the diffusion characteristics of FITC and DOX may vary due to their differences in molecular weight. The following formula.

With this formula we can calculate the concentration in each region. High region= 1.161 μM; Mid region = 0.554 μM; Low region = 0.098 μM

Comment #2. Is there any other phenotypic difference between DOXR cells and L-DOXR cells besides their size?

Response: "In addition to differences in cell size, L-DOXR cells exhibit several distinct phenotypic characteristics when compared to DOXR cells. These include variations in the cell cycle profile (as detailed in Fig. 2F-H), altered drug efflux capabilities (presented in Fig. 2I-J), and changes in nuclear morphology (illustrated in Fig. S3D). These phenotypic distinctions suggest that L-DOXR cells may have adapted unique mechanisms of resistance and survival, which are comprehensively depicted in the figures mentioned.

Comment #3. Please add a description of abbreviations when the abbreviation is first used in the manuscript (e.g. NUPR1, HDAC11 etc.).

Response: We corrected the mistake.

Comment # 4. Figure 2B is the schematic of the chip, not the dimension of the chip. Please add the dimension of the chip to keep the figure caption as is or change the figure caption.

Response: Thank you for the correction. We change the figure caption as Schematic of the chip.

Reviewer #3 (Recommendations for The Authors):

In this manuscript, Lim and colleagues use an innovative CDRA chip platform to derive and mechanistically elucidate the molecular wiring of doxorubicin-resistant (DOXR) MDA-MB-231 cells. Given their enlarged morphology and polyploidy, they termed these cells as Large-DOXR (L-DORX). Through comparative functional omics, they deduce the NUPR1/HDAC11 axis to be essential in imparting doxorubicin resistance and, consequently, genetic or pharmacologic inhibition of the NUPR1 to restore sensitivity to the drug. Although innovative, some deficiencies in the present manuscript slightly weaken the primary conclusions. A couple of critical issues are the use of a single cell line model (i.e., MDA-MB-231) for all the phenotypic and functional experiments and absolutely no mechanistic insights into how NUPR1 imparts resistance to doxorubicin. Some questions and comments are listed below for the authors' consideration and response:

Major:

Comment #1. The authors treated only the MDA-MB-231 cells with doxorubicin in the CDRA chip. Do other TNBC cell lines (namely, MDA-MB-436, HCC1187, or others) respond similarly to dox treatment, eventually yielding enlarged, aneuploid cells with the resistant phenotype? It is important to show that this phenotype is not confined to a single cell line, particularly given the numerous TNBC models that are commonly used.

Response: Thank you for your insightful query regarding the generalizability of our findings across different TNBC cell lines. In this initial study, we focused exclusively on MDA-MB-231 cells due to their widespread use as a model for aggressive triple-negative breast cancer and the constraints of time and resources. While we cannot definitively claim that the observed phenotypic changes upon doxorubicin treatment will be identical in other TNBC cell lines such as MDA-MB-436 or HCC1187, we hypothesize that the underlying mechanisms of chemoresistance and cellular response could be similar across various TNBC models. This hypothesis is supported by literature indicating common pathways of drug resistance in TNBC. We believe that our findings lay the groundwork for future studies to explore the response of a broader range of TNBC cell lines to doxorubicin treatment. Such studies would greatly enhance our understanding of the cellular adaptations to chemotherapeutic agents in TNBC and help to validate the potential universal application of our findings.

Comment #2: Do the L-DOXR cells permanently hold onto the enlarged and polyploid states upon prolonged culture in vitro? Does that change given the presence or withdrawal of the drug? In other words, is the physical state of the resistant cells reversible, or is it passed onto the progeny cells regardless of continued stress from the drug?

Response: Thank you for your question about the stability of the phenotypic changes in L- DOXR cells. Our observations suggest that the enlarged and polyploid states in L-DOXR cells are not permanently fixed. When cultured in vitro over an extended period without the selective pressure of doxorubicin, we have noted that some cells may revert to a non- polyploid state. However, this reversion does not seem to be a stable change as subsequent generations can present with polyploidy again, even in the absence of the drug. This indicates a potential epigenetic or microenvironmental influence on the phenotypic state of these cells, suggesting a complex interplay between the drug-induced stress and the inherent cellular response mechanisms. Further investigation is needed to fully understand the dynamics of these phenotypic changes and whether they are heritable and/or reversible under different culture conditions.

Comment #3: In Figures 2F-H, the authors perform DNA-staining-based FACS to estimate the ploidy of the cells. These estimations could be improved using 2D cell cycle analyses using EdU or BrdU co-treatment and staining. This would further allow a clear distinction between S-phase and G0/G1 and M-phase cells in the WT, DOXR, and L-DORX populations.

Response: Thank you for the suggestion to enhance the accuracy of our ploidy estimations. We appreciate the advice to implement 2D cell cycle analyses using EdU or BrdU co-treatment and staining, as this could indeed provide a clearer distinction between the various phases of the cell cycle in our WT (wild-type), DOXR (doxorubicin-resistant), and L-DOXR (large doxorubicin-resistant) cell populations. Incorporating these thymidine analogs would allow us to label newly synthesized DNA and thereby accurately delineate cells in the synthesis phase from those in the G0/G1 and M phases. This approach will likely add depth to our understanding of the cell cycle dynamics and the mechanism behind the drug resistance phenotype. We will consider incorporating these techniques in our future experiments to validate and extend the findings reported in this study.

Comment #4. In Figure 3H, the authors quantitate the number of enlarged cells detected in human specimens of TNBC or normal breast tissues. How were these cells detected simply using the H&E staining, particularly when assessing the genomic content? Were certain size and nuclear staining intensity thresholds used for these categorizations? If so, these should be mentioned in the paper.

Response: In our study, we identified enlarged cells within human TNBC and normal breast tissue specimens using H&E staining, and their quantitation was carried out using the Colour Deconvolution 2 plugin (Landini G et al., 2020) within the ImageJ software. This method allowed us to analyze the staining intensity and cell size systematically. To ascertain that we were indeed observing cells with increased genomic content, we established specific size and nuclear staining intensity thresholds. Cells exceeding these predetermined thresholds were categorized as 'enlarged'. Additionally, we used continuous serial slides for the human TNBC tissues microarray (BR1301, US Biomax) for more accurate comparisons in Figures 3H, I, and 5H. To strengthen our findings, we verified that NUPR1 expression, which is associated with the observed cell enlargements, was indeed elevated in these same cells from the patient samples. We have detailed these methodological aspects and the criteria for cell categorization in the 'Tissue Microarray and Immunohistochemistry' section of our Materials and Methods to ensure clarity and reproducibility of our results.

Comment #5: In Figure 3I, the authors label the enlarged cells in the patient tissues as L-DOXR cells. Were these assessments done in dox-treated tumors? Even if that is the case, it'll be unfair to call them resistant to doxorubicin. The axis label "% enlarged cells" might be more accurate.

Response: We appreciate the reviewer's attention to detail and agree that the terminology used in Figure 3I was inaccurate. The cells identified in patient tissues were labeled based on their morphological resemblance to L-DOXR cells observed in vitro; however, these patient tissue samples were not confirmed to be treated with doxorubicin, nor were the cells confirmed to be resistant. Therefore, we have amended the figure legend to reflect this and now refer to these cells simply as 'enlarged cells’.

Comment #6: The authors uncovered that NUPR1 expression is dramatically increased in the L-DOXR cells vs the wild-type cells. How does the NUPR1 gene expression and activity compare between L-DOXR and DOXR MDA-MB-231 cells?

Response: Thank you for the valuable comment. The data are included in figure supplement 3 and we revise the manuscript as below. “While DOXR cells exhibited a marked increase in Nupr1 expression compared to the WT cells, this expression was substantially less than that observed in L-DOXR cells, as detailed in figure supplement 3.”(Page 7, Line 3).

Comment #7: Following from above, the authors show that NUPR1 activity is not necessary for cell survival in the absence of doxorubicin (Fig. 4H). But, does it control the cellular size and polyploid states of the L-DOXR cells? In other words, is there any association between increased size and genomic content of the cells to their sensitivity to doxorubicin? Are cells resistant to other chemotherapeutics as well? Or is the resistant phenotype specific to doxorubicin? The authors causally implicate NUPR1 in driving the dox-resistant phenotype in MDA-MB-231 cells. To fully substantiate this claim, the authors should perform gain-of-function studies, in at least 2-3 TNBC cell lines, to show that over-expression of NUPR1 alone is sufficient to impart doxorubicin resistance. Also, the most critical information missing from the study is how NUPR1 drives resistance to doxorubicin. What is the function of NUPR1 in L-DOXR cells and what gene expression program does it activate to impart the resistant phenotype?

Response: During the experimental process either the loss of function or gain of function of Nupr1 in the L-DOXR cells, we have not noticed any specific changes in the cellular size and polyploid states of L-DOXR cells. Although we cannot rule out the possibility that not only by DOX treatment, phenotypically larger cell might arise in response to other chemotherapeutics, in the current study, we found that high level of Nupr1 expression is correlated with sensitivity to doxorubicin in L-DOX cells. Moreover, as followed by the reviewer’s suggestion we performed gain-of-function study to determine whether over-expression of NUPR1 alone is sufficient to impart doxorubicin resistance in TNBC cells. Overexpression of GST-NUPR1 attenuates DOX-induced cell death while slightly increased cell viability of WT (MDA-MB231) cells in the condition of vehicle -treatment, indicating that NUPR1 expressing cells are resistant to the cytotoxic effect of DOX. We have also demonstrated that Nupr1 upregulation in L-DOXR cells are due to suppressed expression of HDAC11 in these cells as we found that HDAC11 triggers promoter acetylation of Nupr1 in L-DOXR cells. Thus, it is conceivable that increased expression of Nupr1 upon HDAC11 suppression in L-DOXR cells is at least responsible for doxorubicin resistance.

Comment #8: Do the authors speculate the dox-resistant phenotype to be restricted to basal TNBC tumors or even NUPR1-high ER+ breast cancer cells (MCF7 or T47D) would likely be resistant to doxorubicin or other chemotherapeutics?

Response: Yes, NUPR1-high ER+ breast cancer cells (MCF7 or T47D) would likely be resistant to doxorubicin or other chemotherapeutics as reported elsewhere; Wang, L., Sun, J., Yin, Y. et al. Transcriptional coregualtor NUPR1 maintains tamoxifen resistance in breast cancer cells. Cell Death Dis 12, 149 (2021). https://doi.org/10.1038/s41419-021-03442-z

Comment #9: The authors suggest that HDAC11 continuously deacetylates the NUPR1 promoter to suppress its expression. Consequently, does the inactivation of HDAC11 in wild-type TNBC cells lead to NUPR1 up-regulation? Is this increase in NUPR1 expression reverted upon inhibition of the HAT machinery (say P300/CBP) in HDAC11-deficient TNBC cells?

Response: In the revised manuscript (pg 8, lines 14-16 and Fig 5H) consistent with our observation that while overexpression of HDAC11 suppresses the expression of Nupr1 in the both WT and L-DOXR cells, HDAC11 inhibitor treatment enhances Nupr1 expression in WT cells, inversely mirroring an unusual low expression of HDAC11 and high level of Nupr1 in L-DOXR cells. Conceivably, the increased Nupr1 expression reflects reverting of promoter acetylation.

Minor:

Comment #10: In Figure 4L, how many animals or tumors were in each of the treatment arms? Were the weights of all the tumors recorded as well? It would be meaningful to add this data, if available. The authors keep changing gene nomenclature throughout the manuscript, listing the gene names in either capital letters or the small-case. This can be made consistent.

Response: We have used 6 mice per group and one tumor for one mouse due to the tumor <br /> size of L-DORX with the vehicle group. We also added new data showing the weights of the tumors in Figure supplement 2D. We apologize for the unmatched gene names. Following the reviewer’s suggestion, the names of genes/proteins have been changed in figures and legends to the recommendations of the HUGO gene nomenclature committee (HGNC).

Reviewer #2 (Public Review):

Summary:

In this paper, the authors induced large doxorubicin-resistant (L-DOXR) cells by generating DOX gradients using their Cancer Drug Resistance Accelerator (CDRA) chip. The L-DOXR cells showed enhanced proliferation rates, migration capacity, and carcinogenesis. Then the authors identified that the chemoresistance of L-DOXR cells is caused by failed epigenetic control of NUPR1/HDAC11 axis.

Strengths:

- Chemoresistant cancer cells were generated using a novel technique and their oncogenic properties were clearly demonstrated using both in vivo and in vitro analysis.<br /> - The mechanisms of chemoresistance of the L-DOXR cells could be elucidated using in vivo chemoresistant xenograft models, an unbiased genome-wide transcriptome analysis, and a patient data/tissue analysis.<br /> - This technique has great capability to be used for understanding the chemoresistant mechanisms of tumor cells.

eLife assessment

This study based on the use of Cancer Drug Resistance Accelerator (CDRA) chip is valuable as a platform technology to assess chemoresistance mechanisms. The strength is convincing from the technological point of view. However, the use of a single cell line model is a limitation. However we acknowledge the authors' plan to further validate their current findings across multiple TNBC cell lines.

Reviewer #1 (Public Review):

Lim W et al. investigated the mechanisms underlying doxorubicin resistance in triple negative breast cancer cells (TNBC). They use a new multifluidic cell culture chamber to grow MB-231 TNBC cells in the presence of doxorubicin and identify a cell population of large, resistant MB-231 cells they term L-DOXR cells. These cells maintain resistance when grown as a xenograft model, and patient tissues also display evidence for having cells with large nuclei and extra genomic content. RNA-seq analysis comparing L-DOXR cells to WT MB-231 cells revealed upregulation of NUPR1. Inhibition or knockdown of NUPR1 resulted in increased sensitivity to doxorubicin. NUPR1 expression was determined to be regulated via HDAC11 via promoter acetylation. The data presented could be used as a platform to understand resistance mechanisms to a variety of cancer therapeutics.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Lim and colleagues use an innovative CDRA chip platform to derive and mechanistically elucidate the molecular wiring of doxorubicin-resistant (DOXR) MDA-MB-231 cells. Given their enlarged morphology and polyploidy, they termed these cells as Large-DOXR (L-DORX). Through comparative functional omics, they deduce the NUPR1/HDAC11 axis to be essential in imparting doxorubicin resistance and, consequently, genetic or pharmacologic inhibition of the NUPR1 to restore sensitivity to the drug.

Strengths:

The study focuses on a major clinical problem of the eventual onset of resistance to chemotherapeutics in patients with triple-negative breast cancer (TNBC). They use an innovative chip-based platform to establish as well as molecularly characterize TNBC cells showing resistance to doxorubicin and uncover NUPR1 as a novel targetable driver of the resistant phenotype.

Weaknesses:

Critical weaknesses are the use of a single cell line model (i.e., MDA-MB-231) for all the phenotypic and functional experiments and absolutely no mechanistic insights into how NUPR1 functionally imparts resistance to doxorubicin. It is imperative that the authors demonstrate the broader relevance of NUPR1 in driving dox resistance using independent disease models.

Author Response

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

Recommendations for the authors

Reviewer #1 (Recommendations For The Authors):

(1) Please expand methods with additional details related to cell co-culture, such as cell numbers and duration.

We thank the reviewer for the careful reading and constructive suggestions and we are sorry to make you confused. We have added the experimental details (manuscript line 551-553) related to co-culture in the revised manuscript.

(2) Please unify the writing of the abbreviation of small extracellular vesicles in the text, figure, and caption.

Thank you for your comments. We have unified the abbreviation of extracellular vesicles to sEVs in the revised manuscript.

(3) The effects of components other than sEVs in mechanically stimulated osteocyte CM on the proliferation of NSCLC cells should be evaluated.

We evaluated the effects of SF, lEVs and sEVs in osteocyte CM on NSCLC cell proliferation under mechanical stimulation, and found that sEVs had the most obvious inhibition on NSCLC cell proliferation, as shown in the revised Supplemental Figure 4c, d.

(4) In addition to osteocytes and osteoblasts, the effects of other types of cells on the proliferation of NSCLC cells should be detected. It is recommended to add at least one type of cell from an infrequent metastatic site of NSCLC as a negative control.

We thank the reviewer for the suggestion. We added NCM460 cell line (derived from intestinal epithelium) as a negative control and found that NCM460 had no significant effect on NSCLC cell proliferation, as shown in Figure 1d. These experiments were conducted before our last submission.

(5) The bone microenvironment is complex. It is recommended to evaluate the effect of bone marrow-derived sEVs on NSCLC to validate whether the tumor suppressive effect of osteocyte sEVs is unique.

We thank the reviewer for the suggestion. We agree with the reviewer’s comments that the bone microenvironment is complex. We explored the effect of bone marrow-derived sEVs on NSCLC cell proliferation and found that bone marrow-derived sEVs promoted NSCLC cell proliferation, as shown in Supplemental Figure 2g, h in the revised manuscript.

(6) The description of exercise preconditioning is not clear enough. It is recommended to supplement the pattern diagram to improve readability. Exercise preconditioning should be further discussed by the Authors.

Thank you for your comments and we are sorry to make you confused. We have added the pattern diagram of the exercise preconditioning in Supplemental Figure 6a.

Reviewer #2 (Recommendations For The Authors):

(1) The histological images are analyzed in a qualitative manner, with no description of the methodology used. A quantitative assessment of the distance and level of Ki-67+ NSCLC cells needs to be performed in human and murine tissues. Because in bone metastases cancer cells are frequently mixed with bone marrow cells, the inclusion of a cell marker to identify NSCLC cells is needed for proper interpretation of the imaging data.

We thank the reviewer for the careful reading and constructive suggestions. We conducted the suggested quantitative assessment and descripted the methodology in the revised manuscript. The results showed that Ki-67 was lower in tumor cells adjacent to bone tissue than in the surrounding tumor cells (Figure 1a, b).

In order to effectively identify NSCLC cells in bone metastases, GFP-expressing NSCLC cells were used in the animal model. We have added the immunofluorescence analysis of GFP and CCND3 in Supplemental Figure 4e, 4g, 5 and 6b.

(2) The authors rely on KI-67 as a marker of proliferation. Yet, it is intriguing that some osteocytes, non-proliferating cells by definition, are often positive for this marker, which questions the specificity of the staining. The authors should provide the proper immunostaining controls to check for specificity and use additional markers of proliferation to confirm these results.

We thank the reviewer for the suggestions. Ki-67 staining was wildly used to determine the dormancy of tumor cells in previous studies [1-4]. To confirm the results of Ki-67 staining, we used cyclin D3 (CCND3) as an additional marker of proliferation as suggested by the reviewer. We added the immunofluorescence analysis of CCND3 in Supplemental Figure 4e, 4g, 5 and 6b, which is consistent with the result of the quantitative immunofluorescence analysis of KI-67.

(3) The lack of proper controls in the in vivo experiments makes the interpretation of the data difficult. For instance, in the preconditioning experiment, it is likely that the bone mass increases. thus, these mice start with high bone mass than the control mice. The lack of a proper control (naive mice exposed to moderate exercise) does not allow testing if the presence of cancer cells still promotes bone loss in this group. The authors need to include naive mice or analyze the bones from the non-injected contralateral legs.

We thank the reviewer for the thoughtful comments and we are sorry to make you confused. We absolutely agree with the reviewer that the bone mass increases after exercise preconditioning. Multiple tissues and organ systems are affected by exercise, initiating diverse homeostatic responses. Although exercise preconditioning effectively suppressed bone metastasis progression of NSCLC as mentioned in the previous manuscript, we cannot immediately conclude that it is completely dependent on osteocytes to function. The mechanism of exercise preconditioning in suppressing bone metastasis progression is complex which still need further exploration. The revised manuscript has expanded the discussion on this area (manuscript line 326-328).

(4)Further, validating the in vivo work with other osteocyte-like cells or primary osteocytes would have strengthened the results.

We thank the reviewer for the suggestion. We have conducted the experiments of co-culture of MLO-A5 (another type of osteogenic cell line) and NSCLC cells as shown in Supplemental Figure 1g. Not surprisingly, MLO-A5 cells also had an inhibitory effect on proliferation of NSCLC cells.

(5) The data on miRNA99b-3p on NSCLC in Supplementary Figure 3 is not convincing. The positive cells are difficult to see and most of the osteocyte lack nuclei. Better data, in humans and the mouse model, is needed to confirm that osteocytes produce miRNA99b-3p.

We thank the reviewer for the comments and we are sorry to make you confused. In this study, we used miRCURY LNA miRNA detection probes in ISH without staining the nuclei in the tissues, which method have been used in our previous studies with others [5-7]. Detailed experimental procedures for ISH of miRNA have been added in the revised manuscript (manuscript line 461-474).

(6) The authors do not provide a piece of data supporting that osteocytes are responsible for any of the effects seen by the interventions done in the in vivo models. Osteocytes, as well as other bone cells, can respond to mechanical stimulation and thus could virtually be responsible for the protective effects of mechanical loading or moderate exercise. In vivo experiments demonstrating a direct role of osteocytes-produced miRNA99b-3p are needed to support the notion that osteocytes maintain tumor dormancy in NSCLC bone metastasis.

We thank the reviewer for the thoughtful comments and suggestion. We constructed in vivo model by injecting with antagomir-NC and antagomir-99b-3p with mechanical loading [8]. The results showed that the injection of antagomiR-99b-3p could partially and effectively rescue the inhibitory effect on NSCLC cell proliferation (Figure 4i-k).

(7) Further, the authors solely rely on Ki-67 as a marker of dormancy. Completing this analysis with an assessment of a dormant gene expression signature or in vivo studies assessing tumor dormancy directly would be needed to confirm this notion.

We thank the reviewer for the suggestion. We conducted the suggested experiment by using CCND3 as an additional dormancy marker. We added the immunofluorescence analysis of CCND3 in Supplemental Figure 4e, 4g, 5 and 6b, which is consistent with the result of the quantitative immunofluorescence analysis of Ki-67.

References

[1] Guba M, Cernaianu G, Koehl G et al. A primary tumor promotes dormancy of solitary tumor cells before inhibiting angiogenesis. Cancer Res, 2001, 61: 5575-9.

[2] Bliss Sarah A, Sinha Garima, Sandiford Oleta A et al. Mesenchymal Stem Cell-Derived Exosomes Stimulate Cycling Quiescence and Early Breast Cancer Dormancy in Bone Marrow. Cancer Res, 2016, 76: 5832-5844.

[3] Correia Ana Luísa, Guimaraes Joao C, Auf der Maur Priska et al. Hepatic stellate cells suppress NK cell-sustained breast cancer dormancy. Nature, 2021, 594: 566-571.

[4] Hu Jing, Sánchez-Rivera Francisco J, Wang Zhenghan et al. STING inhibits the reactivation of dormant metastasis in lung adenocarcinoma. Nature, 2023, 616: 806-813.

[5] Song Qiancheng, Xu Yuanfei, Yang Cuilan et al. miR-483-5p promotes invasion and metastasis of lung adenocarcinoma by targeting RhoGDI1 and ALCAM. Cancer Res, 2014, 74: 3031-42.

[6] Carotenuto Pietro, Hedayat Somaieh, Fassan Matteo et al. Modulation of Biliary Cancer Chemo-Resistance Through MicroRNA-Mediated Rewiring of the Expansion of CD133+ Cells. Hepatology, 2020, 72: 982-996.

[7] Lv Yan, Wang Yin, Song Yu et al. LncRNA PINK1-AS promotes Gαi1-driven gastric cancer tumorigenesis by sponging microRNA-200a. Oncogene, 2021, 40: 3826-3844.

[8] Zhang Yun, Li Shuaijun, Jin Peisheng et al. Dual functions of microRNA-17 in maintaining cartilage homeostasis and protection against osteoarthritis. Nat Commun, 2022, 13: 2447.

eLife assessment

This is an important study, that adds to the field a new understanding of exercise or mechanical loading, microRNAs, and secreted extracellular vessicles in the field of lung cancer (NSCLC), which may have relevance to other osteolytic cancers. The strength of the evidence was mixed: whereas in vitro microRNA experiments were convincing, other elements were incomplete (e.g., proving the roles of osteocytes, as opposed to other mechanosensitive cells, in vivo). This work would be of broad interest to those investigating osteolytic cancers, and the role of exercise in bone cancer, preclinically.

Reviewer #1 (Public Review):

Xie and Colleagues propose here to investigate the mechanism by which exercise inhibits bone metastasis progression. The authors describe that osteocyte, sensing mechanical stimulation generated by exercise, inhibit NSCLC cell proliferation and sustain the dormancy thereof by releasing sEVs with tumor suppressor microRNAs. Furthermore, mechanical loading of the tibia inhibited the bone metastasis progression of NSCLC. Interestingly, exercise preconditioning effectively suppressed bone metastasis progression.

Reviewer #2 (Public Review):

In this manuscript, Xie and colleagues investigate the contribution of osteocytes to bone metastasis of non-small cell lung carcinoma (NSCLC) using a combination of clinical samples and in vitro and in vivo data. They find that metastatic NSCLC cells exhibit lower levels of the proliferation markers Ki-67 and CCND3 when located in areas adjacent to the bone surface in both NSCLC patients and an intraosseous animal model of NSCLC. Using in vitro approaches, they show that osteocyte-like cells inhibit the proliferation of NSCLC cells through the secretion of small extracellular vesicles (sEVs). They identify miR-99b-3p as a component of sEVs and demonstrate that miR-99b3p inhibits the proliferation of NSCLC cells by targeting the transcription factor MDM2. Interestingly, the data also shows that mechanical stimulation of osteocytes enhances the inhibitory effect of osteocytes on NSCLC cell proliferation via increasing sEVs release. By performing different in vivo studies, the authors show that tibial loading and moderate exercise (treadmill running), before and after tumor cell inoculation, suppress tumor progression in bone and protect bone mass. Intriguingly, the moderate exercise regime shows additive/synergistic effects with the co-administration of anti-resorptive therapy. These data add to the growing evidence pointing towards osteocytes as important cells of the tumor microenvironment capable of influencing the progression of tumors in bone.

The conclusions of the paper, however, are not well supported by the data, and some critical aspects of image analysis and data analysis need to be clarified and extended.

(1) In Figure 1, the authors rely on KI-67 as a marker of proliferation. Yet, it is intriguing that some osteocytes, non-proliferating cells by definition, are often positive for this marker, which questions the specificity of the staining. The data displayed in supplementary figures showing CCND3 as a marker of proliferation ,and GFP as a marker of cancer cells, is much more robust and should be moved to the main figures.

(2) Adding control groups to fully assess the impact of the in vivo interventions (tibial loading, moderate exercise, anti-resorptive therapy) on bone mass would be needed. The authors should have used naive mice or analyzed the bones from the non-injected contralateral legs.

(3) The data on miRNA99b-3p on NSCLC in Supplementary figure 3 is not convincing. The positive cells are difficult to see and most of the osteocyte lack nuclei. Better data, in humans and the mouse model, would have helped to confirm that osteocytes produce miRNA99b-3p.

(4) Some conclusions of the paper are not entirely supported by the data provided. Osteocytes, as well as other bone cells, can respond to mechanical stimulation and thus could virtually be responsible for the protective effects of mechanical loading or moderate exercise. While blocking miR-99b3p with antagomiRs rescued the decreases in proliferation, it is unclear whether this effect is mediated by osteocytes or other cells that express this miRNA. In vivo experiments demonstrating a direct role of osteocytes are needed to support the notion that osteocytes maintain tumor dormancy in NSCLC bone metastasis. In vivo, studies assessing tumor dormancy directly would be needed to confirm osteocytes promote cancer cell dormancy.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

TRIP13/Pch2 is a conserved essential regulator of meiotic recombination from yeast to humans. In this manuscript, the authors generated TRIP13 null mice and Flag-tagged TRIP13 knock-in mice to study its role in meiosis. They demonstrate that TRIP13 regulates MORMA domain proteins and is essential for meiotic completion and fertility. The main impact of this manuscript is its clarification of the in vivo function of TRIP13 during mouse meiosis and its previously unrecognized role as a dose-sensitive regulator of meiosis.

Strengths:

Two previously reported Trip13 mutations in mice are both hypomorphic alleles with distinct phenotypes, precluding a conclusion on its function. This study for the first time generated the TRIP13 null mice, definitively revealing the function of TRIP13 in meiosis. The authors also show the novel localization of TRIP13 at SC and its independence from the axial element components. The finding of dose-sensitive regulation of meiosis by TRIP13 has implications in understanding human meiosis and disease phenotypes.

Weaknesses:

This manuscript would be more impactful if more mechanistic advancements could be made. For example, the authors could follow up with one of the new interactors identified by MS to offer new insight into the molecular function of TRIP13.

We agree that it would be interesting to follow up on new candidate interactors but think that it would be more feasible to follow up on them in future studies.

Reviewer #2 (Public Review):

Summary and Strengths:

In this manuscript, Chotiner and colleagues demonstrated the localization of TRIP13 and clarified the phenotypes of Trip13-null mice in mouse meiosis. The meiotic phenotypes of Trip13 have been well characterized using the hypomorph alleles in the literature. However, the null phenotypes have not been examined, and the localization of TRIP13 was not clearly demonstrated. The study fills these important knowledge gaps in the field. The demonstration of TRIP13 localization to SC in mice provides an explanation of how HOMRA domain proteins are evicted from SC in diverse organisms. This conclusion was confirmed in both IF and TRIP13-tagged Tg mice. Further, the phenotypes of Trip13-null mice are very clear. The manuscript is well crafted, and the discussion section is well organized and comprehends the topic in the field. All in all, the manuscript will provide important knowledge in the field of meiosis.

Weaknesses:

The heterozygous phenotypes demonstrate that TRIP13 is a dosage-sensitive regulator of meiosis. In relation to this conclusion, as summarized in the discussion section, other mutants defective in meiotic recombination showed dosage-sensitive phenotypes. However, the authors did not examine meiotic recombination in the Trip13-null mice.

Meiotic recombination was extensively characterized in Trip13 severe hypomorph mutants in two previous studies: gamma-H2AX, BLM, BRCA1, ATR, RPA, RAD51, DMC1, MLH1 (Li and Schimenti, 2007; Roig et al., 2010). All the meiotic defects in our Trip13-null mice were also present in Trip13 severe hypermorph mutants: meiotic arrest, defects in chromosomal synapsis, asynapsis at chromosomal ends, and accumulation of HORMAD1/2 on the SC axis. Therefore, the defects in meiotic recombination in Trip13-null mice are expected to be similar to those in Trip13 severe hypermorph mutants and thus we did not examine the proteins involved in meiotic recombination in the Trip13-null mutant.

Reviewer #3 (Public Review):

Summary:

The authors perform a thorough examination of the phenotypes of a newly generated Trip13 null allele in mice, noting defects in chromosome synapsis and impact on localization of other key proteins (namely HORMADs) on meiotic chromosomes. The vast majority of data confirms observations of several prior studies of Trip13 alleles (moderate and severe hypomorphs). The original or primary aims of the study aren't clear, but it can be assumed that the authors wanted to better study the role of this protein in evicting HORMADs upon synapsis by studying phenotypes of mutants and better characterizing TRIP13 localization data (which they find localizes to the central element of synapsed chromosomes using a new epitope-tagged allele). Their data confirm prior reports and are consistent with localization data of the orthologous Pch2 protein in many other organisms.

Strengths:

The quality of data is high. Probably the most important data the authors find is that TRIP13 is localized along the CE of synapsed chromosomes. However, this was not unexpected because PCH2 is also similarly localized. Also, the authors use a clear null (deletion allele), whereas prior studies used hypomorphs.

Weaknesses:

There is limited new data; most are confirmatory or expected (i.e., SC localization), and thus the impact of this report is not high. The claim that TRIP13 "functions as a dosage-sensitive regulator of meiosis" is exaggerated in my opinion. Indeed, the authors make the observation that hets have a phenotype, but numerous genes have haploinsufficient phenotypes. In my opinion, it is a leap to extrapolate this to infer that TRIP13 is a "regulator" of meiosis. What is the definition of a meiosis regulator? Is it at the apex of the meiosis process, or is it a crucial cog of any aspect of meiosis?

TRIP13 is not haploinsufficient, as Trip13 heterozygotes were still viable and fertile (albeit with defects in meiosis). TRIP13 is an ATPase and changes the conformation of meiosis-specific proteins such as HORMAD proteins. TRIP13 is essential for meiosis and its mutations cause defects in both meiotic recombination and chromosomal synapsis. Reviewer 1 stated that “TRIP13/Pch2 is a conserved essential regulator of meiotic recombination from yeast to humans”. Therefore, we feel that TRIP13 can be called a regulator of meiosis.

Reviewer #1 (Recommendations For The Authors):

A schematic illustration of SC structure, the components involved, and the main finding, would be helpful for readers to better understand the advancement made by this study.

We have now added a schematic illustration in a new panel - Figure 7C.

Fig. 1B, the stage with diplotene cells should be XII.

The pachytene cells (Pac) were mis-labelled as diplotene cells. Corrected.

Fig. 1C, color mislabeled.

Corrected.

Reviewer #2 (Recommendations For The Authors):

The manuscript will provide important knowledge in the field of meiosis. I support the publication of this study. I have some suggestions to improve and polish the manuscript.

Major points:

(1) The heterozygous phenotypes demonstrate that TRIP13 is a dosage-sensitive regulator of meiosis. In relation to this conclusion, as summarized in the discussion section, other mutants defective in meiotic recombination showed dosage-sensitive phenotypes. Given the function of HORMAD1 in meiotic recombination, it would be informative if the authors could examine how major makers of meiotic recombination behave in Trip13-null meiosis.

Please see our response to Weaknesses from Reviewer #2.

(2) Relating to the above point, the complete lack of synapsis on the sex chromosomes in the Trip13-null meiosis is impressive. This result raises a question as to whether the pathway to designate XY-obligatory crossover (which can be detected with large foci of ANKRD31 and MEI4/REC114 at PAR) is affected or not. It would be interesting to examine whether the ANKRD31 and MEI4/REC114 foci are present on PAR in Trip13-null meiosis.

We have performed immunofluorescent analysis of REC114 in spermatocytes. In Trip13-null pachytene-like spermatocytes, X and Y chromosomes are not synapsed. REC114 still formed one focus each on the unsynapsed X and Y chromosomes. We have added this new data in the Results as a new supplementary figure (Figure 4 -supplement 1).

(3) Figure 4 can be improved if there are quantified data for each phenotype. These phenotypes look nearly complete, but it would be informative to show the penetrance of these phenotypes.

Because some chromosomes have unsynapsed ends, resulting in two centromere or telomere foci, the total number of centromere or telomere foci is always higher in Trip13-null pachytene-like spermatocytes than wild type pachytene spermatocytes. Therefore, we did not count the foci of centromeres and telomeres. Consistently, the centromere and telomere markers localized as expected in both wild type and Trip13-null spermatocytes.

(4) I am not fully convinced by these photos: "synapsed sister chromatids (Figure 6B)" and "Sycp2-/- spermatocytes formed short stretches of synapsis (Figure 6C)". The authors may try confocal microscopy with super-resolution deconvolution as they did for other data.

These have been previously demonstrated. The “synapsed sister chromatids (Figure 6B)” were previously demonstrated by confocal microscopy with super-resolution deconvolution (Guan et al., 2020). The short stretches of synapsis in Sycp2-/- spermatocytes was previously demonstrated by electron microscopy (Tripartite SC structure) and SYCP1 immunofluorescence (Yang et al., 2006). We have revised the text by citing the previous evidence and the publications.

Minor points:

(1) Line 19-21: "Loss of TRIP13 leads to meiotic arrest and thus sterility in both sexes. Trip13-null meiocytes exhibit abnormal persistence of HORMAD1 and HOMRAD2 on synapsed SC". These findings confirm the previously reported phenotypes of the Trip13 hypomorph alleles. This information can be added to the abstract. Otherwise, it sounds like these are totally new findings, as written.

This information is now added to the abstract: “These findings confirm the previously reported phenotypes of the Trip13 hypomorph alleles.”

(2) The introduction section seems too long and contains unnecessary information. Some molecular details that are not touched in the result section can be deleted (e.g., Line 65-73).

We would like to keep the molecular details on the two conformation states, as it provides biochemical background on TRIP13-HORMAD interactions.

(3) Introduction, Line 92. A rationale can be added as to why the authors characterized the Trip13-null allele.

a rationale has been added as follows: “To determine the effect of complete loss of TRIP13, we characterized Trip13-null mice.”

(4) Line 205: Typo "TRRIP13". Corrected.

Reviewer #3 (Recommendations For The Authors):

Just a few recommendations:

(1) In my opinion, the title is an overreach. "Regulator" invokes other concepts such as transcription factors.

Please see our explanation in response to weaknesses from Reviewer #3.

(2) The first sentence of the results deals with TRIP13 expression in only 3 tissues. The authors might look at more comprehensive RNA-seq data from mice and humans.

We examined TRIP13 protein expression in 8 mouse tissues by WB and found that TRIP13 protein was abundant in testis but present at a very low level in ovary and liver (Figure 1A). We feel that readers can easily look up the relative transcript levels of Trip13 in more tissues from mice and humans from NCBI database under “Gene”.

(3) The null allele is semi-lethal. Is body size affected? Were the mice abnormal in any other ways, given that TRIP13 has been implicated in other diseases and processes, and is expressed in other tissues (TRIP13 stands for Thyroid receptor interacting protein).

The body weight of 2-3 month-old males was not significantly different between wild type (24.3±2.8 g, n=5) and Trip13 KO mice (22.8±1.7 g, n=5, p=0.3, Student’s t-Test). We have included the body weight information in the revised manuscript. We didn’t observe abnormal somatic defects in the viable Trip13-null mice, nor did the authors report any in the Trip13 hypomorph mutants in two previous studies (Li and Schimenti, 2007; Roig et al., 2010).

(4) Line 276 : It would be nice to elaborate on the "spatial explanation."

We meant that TRIP13 localizes to SC while HORMAD proteins are removed from SC upon chromosomal synapsis, thus providing a spatial explanation. However, we have now deleted “spatial”.

eLife assessment

This important study defined the physiological function of a conserved meiosis factor during murine spermatogenesis. The genetic and cellular biological evidence supporting the conclusion is convincing. This work will be of broad interest to cell biologists, geneticists, and reproductive biologists.

Reviewer #1 (Public Review):

Summary:<br /> TRIP13/Pch2 is a conserved essential regulator of meiotic recombination from yeast to humans. In this manuscript, the authors generated TRIP13 null mice and Flag-tagged TRIP13 knock-in mice to study its role in meiosis. They demonstrate that TRIP13 regulates MORMA domain proteins and is essential for meiotic completion and fertility. The main impact of this manuscript is its clarification of the in vivo function of TRIP13 during mouse meiosis and previously unrecognized role as a dose-sensitive regulator of meiosis.

Strengths:<br /> Two previously reported Trip13 mutations in mice are both hypomorphic alleles with distinct phenotypes, precluding a conclusion on its function. This study for the first time generated the TRIP13 null mice, definitively revealed the function of TRIP13 in meiosis. The authors also show novel localization of TRIP13 at SC and its independence from the axial element components. The finding of dose-sensitive regulation of meiosis by TRIP13 has implication in understanding human meiosis and disease phenotypes.

The results support the main conclusions and advance the understand of meiosis in the germline.

Reviewer #2 (Public Review):

Summary and Strengths:<br /> In this manuscript, Chotiner and colleagues demonstrated the localization of TRIP13 and clarified the phenotypes of Trip13-null mice in mouse meiosis. The meiotic phenotypes of Trip13 have been well characterized using the hypomorph alleles in the literature. However, the null phenotypes have not been examined, and the localization of TRIP13 was not clearly demonstrated. The study fills these important knowledge gaps in the field. The demonstration of TRIP13 localization to SC in mice provides an explanation of how HOMRA domain proteins are evicted from SC in diverse organisms. This conclusion was confirmed in both IF and TRIP13-tagged Tg mice. Further, the phenotypes of Trip13-null mice are very clear. The manuscript is well crafted, and the discussion section is well organized and comprehends the topic in the field. All in all, the manuscript will provide important knowledge in the field of meiosis.

Weaknesses:<br /> The heterozygous phenotypes demonstrate that TRIP13 is a dosage-sensitive regulator of meiosis. In relation to this conclusion, as summarized in the discussion section, other mutants defective in meiotic recombination showed dosage-sensitive phenotypes. However, the authors did not examine meiotic recombination in the Trip13-null mice.

Author Response

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

Reviewer #1 (Public Review):

However, there are several concerns to be explained more in this study. In addition, some results should be revised and updated.

Thank you for your comments. The concerns were addressed by the description and experiment.

Some results were revised and updated accordingly.

Reviewer #2 (Public Review):

The minor weakness of the study is inconsistent use of terminology throughout the manuscript, occasional logic-jump in their flow, and missing detailed description in methodologies used either in the text or Materials and Methods section, which can be easily rectified.

Thank you for your review. We have revised the manuscript and corrected errors according to your comments.

Reviewer #3 (Public Review):

Importantly, besides the Miwi ubiquitination experiment which is performed in a heterologous and therefore may not be ideal for extracting conclusions, the possible involvement of ubiquitination was not shown for any other proteins that the authors found that interact with FBXO24. Could histones and transition proteins be targets of the proposed ubiquitin ligase activity of FBXO24, and in its absence, histone replacement is abrogated?

Thank you for your comments. The histones and transition proteins were not found in the immunoprecipitates of FBXO24, suggesting they are not the direct targets of FBXO24, shown in Figure S3G.

Miwi should be immunoprecipitated and Miwi ubiquitination should be detected (with WB or mass spec) in WT testis.

We agree with this suggestion. In the revision, the expression and ubiquitination of MIWI were detected in WT testis by the immunoprecipitation and ubiquitination assay, as shown in Figure 8H.

Therefore, the claim that FBXO24 is essential for piRNA biogenesis/production (lines 308, 314) is not appropriately supported.

We appreciate the comment. We have revised the description and modified the claim on page 11.

Reviewing Editor's note for revision

(1) As noted by all three reviewers, as currently written the rationale to focus on MIWI is not entirely clear. A transitional narrative to focus on MIWI needs to be provided as well as an explanation for how the absence of FBXO24 as an E3 ubiquitin ligase is responsible for the observed mRNA and protein differential expression.

We appreciate your comments. We have supplemented the transitional narrative by focusing on MIWI and explained mRNA and protein differential expression upon FBXO24 deletion, shown on Page 7 and Page 13, respectively.

(2) As it can be indirect, mass spec detection of MIWI in testis co-IP and MIWI ubiquitination should be detected (with WB or mass spec) in WT testis.

In the revision, the expression and ubiquitination of MIWI were detected in WT testis by the immunoprecipitation and ubiquitination assay, as shown in Figure 8H.

(3) Please tone down the claim that FBXO24 is essential for piRNA biogenesis/production as it requires further evidence.

We have revised the description and modified the claim on page 11.

(4) Ontology analysis of the genes with abnormally spliced mRNAs to provide an explanation for developmental defects.

In the revision, we have performed the ontology analysis and provided new data regarding the abnormally spliced genes, as shown in Figure S4D.

Reviewer #1 (Recommendations For The Authors):

Major comments

(1) The authors performed mainly with the WT (or knock-in) and Fbxo24-knockout mouse model. Do the heterozygous males and their sperm have any physiological defects like FBXO24-deficient mice?

This is a good question. We did the phenotype analysis and found that heterozygous males are all fertile, and their sperm do not have any physiological defects.

(2) Fbxo24-KO sperm carries swollen mitochondria. How do the mitochondria affect sperm function?

Thank you for raising this interesting question. Based on our data and published literature, the defective mitochondria were associated with energetic disturbances and reduced sperm motility, as shown on Page 12.

(3) TEM images show that Fbxo24-KO spermatids carry swollen mitochondria and enlarged chromatoid bodies. How the swollen mitochondria and enlarged chromatid are defective for sperm motility and flagellar development, requires more explanation. In addition, it is unclear how the enlarged diameter of the chromatoid body is critical for normal sperm development.

Thank you for your comments. The chromatoid bodies are considered to be engaged in mitochondrial sheath morphogenesis. Analysis of the chromatoid bodies' RNA content reveals enrichment of PIWI-interacting RNAs (piRNAs), further emphasizing the role of the chromatoid bodies in post-transcriptional regulation of spermatogenetic genes. We added this explanation on Page 12-13.

(4) The authors only show band images to compare the protein amounts between WT and KO sperm and round spermatids. As the blots for loading controls are not clear, the authors should quantify the protein levels and perform a statistical comparison.

We quantified the protein levels and performed a statistical comparison, as shown in Figure S3B.

(5) The authors show the defective sperm head structure from Fbxo24-KO sperm in Figure 5. However, the Fbxo24-KO sperm heads seem quite normal in Figure 3. How many sperm show defective sperm head structure? In addition, the authors observed altered histone-to-protamine conversion in sperm, but it is unclear whether the altered nuclear protein conversion causes morphological defects in the sperm head.

We appreciate the comments. In our study, we found over 80% of Fbxo24 KO sperm showed defective structure in the sperm head. Altered histone-to-protamine conversion caused the decondensed nucleus of Fbxo24 KO sperm. Notably, in many knockout mice studies, impaired chromatin condensation is frequently associated with abnormal sperm head morphology, as shown in reference 15 of Page 8.

(6) The authors compare the protein levels of RNF8, PHF7, TSSK6, which participate in nuclear protein replacement in sperm. However, considering the sperm is the endpoint for the nuclear protein conversion, it is unclear to compare the protein levels in mature sperm. The authors might want to compare the protein levels in developing germ cells.

Thank you for your comment. Yes, we actually detected the protein levels of RNF8, PHF7, and TSSK6 in the testes, not in sperm. We have corrected it in the Figure 5E. We apologize for our carelessness.

(7)This reviewer suggests describing more rationales for how the authors focus on the MIWI protein. Also, it is wondered whether MIWI is also detected from testis co-IP mass spectrometry.

We agree with this suggestion. Since MIWI was a core component of CB and also identified as an FBOX24 interacting partner from our immunoprecipitation-mass spectrometry (IP-MS) (Table S1), we focused on the examination of MIWI expression between WT and Fbxo24 KO testes. We have added this description in the revision (see lines 191-193 on page 7).

(8) The authors need to provide a more detailed explanation for how the altered piRNA production affects physiological defects in germ cell development. In addition, it will be good to describe more how the piRNAs affect a broad range of mRNA levels.

Thank you for your comments. The previously published studies have demonstrated that piRNAs could act as siRNAs to degrade specific mRNAs during male germ cell development and maturation. We have cited these studies on lines 369-372 of Page 13.

(9) The authors observed an altered splicing process in the absence of FBXO24. However, it is a little bit confusing how the altered splicing events affect developmental defects. Therefore, the authors should state which mRNAs have undergone abnormal splicing processes and provide ontology analysis for the genes.

We have performed the ontology analysis and showed the new data in Figure S4D.

Minor comments

(1) Figure 1A-C - Statistical comparison is missed. Numbers for biological replication should be described in corresponding legends.

Thank you for your careful review. We have provided the statistical comparison and the numbers for biological replication in the legends of Figure 1A-C.

(2) Figure 1E, F - Current images can't clearly resolve the nuclear localization of the FBXO24 testicular germ cells. To clarify the intracellular localization, the authors should provide images with higher resolution.

The resolution of Figure 1E, F was improved, as suggested. Thank you!

(3) Figure 1E, F - Scale bar information is missing.

The scale bars of Figure 1E, F were provided.

(4) It will be much better to show the predicted frameshift and early termination of the protein translation in Fbxo24-knockout mice.

The predicted frameshift of Fbxo24-knockout mice was added and shown in Figure S1B.

(5) It is required to provide primer information for qPCR.

The primer information for qPCR was provided, as shown in Table S7.

(6) The authors describe that Fbxo24-KO sperm show abrupt bending of the tail. However, the description is unclear and the sperm shown in Figure 3C seems quite normal. The authors should clarify the abnormal bending pattern of the tail and show quantified results.

Thank you for pointing out this issue. In Fbxo24 KO sperm, abnormal bending of the sperm tails mainly included neck bending and midpiece bending. We have shown them in Figure S3A.

(7) The authors mention that Fbxo24-KO sperm have swollen mitochondria at the midpiece, but this is also unclear. How many mitochondria are swollen in Fbxo24-KO sperm?

This is a good question. However, since it is very difficult to observe all of the mitochondria in each sperm using the electronic microscope, we could not quantify the swollen mitochondria in Fbxo24 KO sperm.

(8) Scale bar information is missed - Fig 3C insets, Fig 3D, Fig 3F insets, 4A insets, Figure 4C insets.

All the scale bars have been added.

(9) How many sperm have annulus defects? In Figure 3F, WT sperm does not have an annulus, which could be damaged during sample preparation. Is the annulus defects in Fbxo24-KO sperm consistent?

Thank you for asking these questions. Based on our results, about 30% of Fbxo24 KO sperm showed defective annulus structure. Since both TEM (Figure 3F) and SEM (Figure 3G) results clearly showed the defective annulus structure of Fbxo24 KO sperm, we believe the annulus defects are consistent and highly unlikely caused by sample preparation.

(10) A Cross-section image for the endpiece of Fbxo24-KO sperm is not suitable. There is a longitudinal column structure of the principal piece.

Thank you for your comments. It is difficult to observe a completely longitudinal structure of sperm tail under TEM. The cross-section of the endpiece and principal piece allowed us know the structure of the axoneme, ODFs and fibrous sheath (FS).

(11) The endpiece of Fbxo24-KO sperm seems to have a normal axoneme. Do all endpieces of Fbxo24KO sperm have normal axoneme? Also, the authors need to describe whether an axonemal structure is damaged and disrupted in all Fbxo24-KO sperm.

Our TEM data showed the axonemal structure was impaired in the endpiece of Fbxo24 KO sperm (See right panels of Figure 3H). Moreover, based on the ultrastructure analysis of TEM, we found over 90% of Fbxo24 sperm had a damaged axonemal structure.

(12) Reference blots in Fig 3I, 3J, 4E (left), 5C and 5E are quite faint. The authors should replace the blot images.

Thank you for pointing out this. We have rerun Western blot multiple times but could not obtain better images due to antibody sensitivity. However, we quantified the protein levels and performed a statistical comparison, as shown in Figure S3B, to establish a good readout from these images for the readers.

(13) Loading controls are required - 7D-H.

Done as suggested. Thanks!

(14) How do the authors measure the midpiece length? From where to where? This should be clarified.

Good question. We measured the midpiece length from the sperm neck to the sperm annulus by MitoTracker staining. We have clarified this on Page 16.

(15) How are the bands for Fbxo24 shifted during IP in Fig 7A?

The protein modification in the interaction may cause the band shift.

(16) There are several typos throughout the manuscript. Please check carefully and fix them.

Thank you for your careful review. We have corrected and fixed all the typos as far as we can.

Reviewer #2 (Recommendations For The Authors):

Major comments

(1) Please provide a schematic of HA-Fbxo24 knock-in construct and strategy together with knockout (Figure S2) or even separately early in Figure S1. The description of using the transgenic mouse is mentioned even earlier than the knockout but there are no citations or methods provided in the text other than that listed in Materials and Methods.

Thank you for your suggestion. As suggested, the schematic of the HA-Fbxo24 knock-in strategy has been supplemented in Figure S2A. The description of using the transgenic mouse has been added to the results, as shown on page 4 of lines 102-103.

Also, it is not clear to what extent the phenotypic and molecular characterization of HA-transgenic mice is performed. For example, Lines 134-139: The use of Fbxo24-HA labeled transgenic mice results in the rescue of spermatogenesis and fertility as shown in Figure 2F by measuring the litter size. It is not clear how this observation leads the author to state that this rescues defects in spermiogenesis. Please clarify how and what other measures are taken to support this conclusion. Is the observed infertility due to defects in spermatogenesis or spermiogenesis?

Thank you for your question. We crossed FBXO24-HATag males with FBXO24−/− females to obtain FBXO24−/−; FBXO24-HATag males. We examined the testes volume and histological morphology of FBXO24−/−; FBXO24-HATag males and found that they were similar to FBXO24+/−; FBXO24-HATag littermates, indicating that spermatogenesis was restored, as shown in Figure S2H.

(2) Line 107 vs Line 114: Please use the terminology spermatogenesis and spermiogenesis consistently throughout the text. Earlier in the introduction, the authors clearly defined that spermatogenesis involves three phases, with the third phase referred to as spermiogenesis. However, the author concludes in the first line that "FBXO24 plays a role during spermatogenesis" while summarizing at the end of the paragraph that this protein is "expressed in haploid spermatids specifically during spermiogenesis". Therefore, it is not clear whether the authors conclude that FBXO24 is important for all of spermatogenesis (line 107) or only for part of spermiogenesis (line 114). Another example is line 219 vs. 238: At this point in the manuscript, it is again unclear whether the authors want to study molecular changes during spermatogenesis or spermiogenesis upon FBXO24 depletion. Many examples of such cases throughout the text, and it is recommended to be consistent in using more restrictive terminology whenever applicable for a clear interpretation.

We thank you for your careful review. We have double-checked the terminology of spermatogenesis and spermiogenesis and made it consistent throughout the text of the revised manuscript.

(3) It is not clear how rampant/frequent the Fbxo24-knockout sperm show defects in head morphology based on Figures 3C, 3F, and 5A since it seems that there are some sperm showing relatively normallooking sperm heads. Please provide quantification.

We have performed the quantification and found that over 80% of Fbxo24 KO sperm showed defective structures in the sperm head.

(4) Figure 3B: The authors describe in the figure legend that 3 mice were analyzed in each group. The standard deviation for the WT analysis is missing, or if the author wanted to set the WT value to 100%, the bar and scale shown on the y-axis do not fit. The value for WT looks more like 95%.

We have indeed analyzed sperm motility based on the WT value set at 100% and have revised Figure 3B in the revision. We apologize for this oversight.

(5) Figure 3 B and C: It is not clear how the motility is measured. Is CASA used (not described in Methods). The conclusion about abnormal flagellar bending in KO spermatozoa cannot be drawn from the static microscopic images alone. Please provide more details of motility analysis together with videos of live cell imaging.

The sperm motility was measured manually using a hemocytometer, according to the reference.

We provided the details of sperm motility analysis in the Materials and Methods section on Page 16.

(6) Figure 3 I and J: These are one of a few figures that are not supported by statistical analysis. In particular, for 3I, GAPDH controls of WT and KO protein do not show equal loading, which could explain the lower expression of the KO protein. Please show normalized bar graphs with multiple biological replicates or at least show a representee technical replicat that shows equal loading of GAPDH to better support the conclusion.

Thank you for your suggestion. Statistical comparison of relative protein expression was supplemented, as shown in new Figure S3B.

(7) Line 184: It is not clear how the authors define a swollen mitochondrion? Are there any size criteria (roundness) that can be measured to distinguish between a swollen and a non-swollen mitochondrion? It is recommended to use another terminology as often 'swollen' implies there is a difference in osmolarity but there is no experiment to support this implication.

Thank you for your comment. We have changed the “swollen” to “vacuolar” in the revision, as shown on Page 7.

(8) Figure S4, without a bright field image, it is hard to see the purity and morphology of the isolated prep. Please provide the bright field images together or as overlaid images.

We agree with your comment. We have provided the overlaid images in new Figure S4A.

(9) There is a big logic jump in what prompts the authors to look MIWI protein level and link the observation to MIWI/piRNA pathway in both Introduction and Results while it is one of the main findings. It is recommended to provide a better rationale and logical flow in the text.

Thank you for your suggestion. We have added a sentence explaining why we wanted to focus on studying MIWI expression (see lines 190-193 on page 7).

Minor comments

(1) Please keep all the conventions of gene vs. protein nomenclature. For example, write the genes mentioned in the figures in italics with the first letter in Capital, as it is done in the main part. Proteins should be in ALL CAPITAL like FBXO24.

The names of gene and protein have been revised in the revision, as suggested.

(2) In the MM section, the name of the manufacturer and the location of the materials used are missing in several sections. Please go back through the MM section and add this information in the appropriate places.

Done as suggested. Thank you!

(3) On page 4, the authors mentioned that "Further qPCR analysis of developmental testes and purified testicular cells showed that FBXO24 mRNA was highly expressed in the round spermatids and elongating spermatids (Fig 1B-C)". Please include statistical analyses for Fig 1B-C as well as for Fig 1A to support the written statements.

Statistical comparison was supplemented, as shown in Figure 1. P-values are denoted in figures by *p < 0.05.

(4) Figure 3E: Please describe in more detail how the length of the midpiece was measured. Was it based on TEM images or based on fluorescent images using MitoTracker?

As we responded to Reviewer #1, we measured the midpiece length from the sperm neck to the sperm annulus by MitoTracker staining. We have clarified this in the Method and Material section on Page 16.

(5) Line 431: In the "Electron Microscopy" section of the MM part, the author should indicate the ascending ethanol series (%) used.

Done as suggested. Thank you!

(6) Line 432: The thickness of the sections prepared is missing, as well as an indication of the microtome used.

We have added thickness and the microtome in the Method and Material section on Page 16.

(7) Line 433: If the generated tiff files have been processed with Adobe Photoshop, this information is missing.

We have provided information on the usage of Adobe Photoshop for the generation of tiff files on Page 17.

(8) Lines 445, 452, 467: In some places in the paper, the temperature is written with a space between the number and {degree sign}C, and sometimes it is not. Please go through the paper and make it consistent. The usual spelling is 4{degree sign}C.

We have gone through the manuscript and checked all the spelling of temperature writing to make them consistent. Thank you for careful review.

(9) Line 469: The gel documentation system used is not mentioned.

Done as suggested. Thank you!

(10) Line 469: The 'TM' should be superscripted.

Done as suggested.

(11) Line 489: A space is missing between the changes and the parenthesis.

Done as suggested.

(12) Line 495-496: The authors write that the fractions enriched with round spermatids after sedimentation were collected manually. Was a determination of cell concentration - e.g., 2 x106 cells/ml -performed after collection of the cells? How were the cells stored until use? Please add the sedimentation time and used temperature.

Store the cell in the 1´ Krebs buffer on ice. The cell sediment was through a BSA density gradient for 1.5 h at 4°C. The cell concentration was determined after collection, as shown on Page 18.

(13) Line 505: spelling error. Instead of " manufacturer's procedure" it is written manufactures' instructions.

The spelling error was corrected.

(14) Line 520: Please write a short sentence on how the purification of the 16-40 nt long RNA was performed.

The length of 16–40 nt RNA was enriched by polyacrylamide gel electrophoresis. We added this information on Page 19 of line 531.

(15) Line 528: The version of the used GraphPad software is missing.

The version of GraphPad software was supplemented, as shown on Page 19.

(16) Line 677: For qPCR analyses, the number of mice analyzed (N) and a statistical evaluation are missing.

The statistical comparison and the numbers for biological replication were added, as shown on Page 26.

(17) Figure 3D: Please add a scale bar.

Done as suggested. Thanks!

(18) Line 371 and Line 377: Two times "in summary" is written. Please make one summary for the whole paper.

This sentence was revised, as shown in Page 13.

(19) Line 382: To be consistent in the whole paper, please write Figure 10 in bold letters.

Done as suggested.

(20) Please make the size and font of the references consistent with the main text.

Done as suggested. Thanks again for your careful review.

Reviewer #3 (Recommendations For The Authors):

I would like to see the description of the FBXO24 immunoprecipitation experiment performed in HEK293T cells. This somatic cell line does not normally express Miwi, so how Miwi was detected in FBXO24 mCherry IP beads? It is not mentioned if Miwi is expressed from a recombinant vector in this experiment. Similarly, I would like to see a better description of the experiment described in the same paragraph towards the end of it with the ubiquitin peptides, it is not clear.

Thank you for your comments. FBXO24-mCherry was expressed in HEK293T cells and the immunoprecipitates was incubated with the protein lysate of the testes (see lines 268-272 on Page 10). The description of the ubiquitin experiment was added as well, as shown in lines 283-286 on Page 10.

Line 263: I think the term ectopic here is not appropriate, a correction is needed.

We have changed “ectopic” to “increased” in the revision (see line 268 on Page 10).

I would like the authors to provide a tentative explanation or evidence of why FBXO24 KO males are completely sterile, even though there are still mature sperm produced with some motility. Since there are defects in nuclear condensation it will be very relevant to check DNA damage/fragmentation, which could contribute to the sterility phenotype.

This is a good suggestion. We reanalyzed the sperm DNA damage by TUNEL staining and shown the new data in Figure S3E-F.

Line 213: There have been some conflicting reports about the role of RNF8 in spermiogenesis, but a recent report has shown that RNF8 is not involved in histone PTMs that mediate histone to protamine transition (Abe et al Biol Reprod 2021 https://doi.org/10.1093%2Fbiolre%2Fioab132).

Thank you for your comment. We have cited this critical reference and discussed it in Discussion section on Page 12.

Figure 7: I would like to see zoomed-out views of the affected exons, so that flanking unaffected exons can be used as a reference for unaffected splicing. Most of the genome browser views in this image only show affected exons and it is impossible to see if these alone are affected or if the reduced RNAseq coverage in those exons is a result of overall reduced mapped reads in these genes. Also, a fixed Y axis with the same max value should be shown for these genome browser snapshots so that the expression level is comparable between the two genotypes.

Thank you for your comments. Loading control of RT-PCR and scale range of Y axis were added in new Figure 7.

Minor corrections:

Line 70: correct "..functions as protein-protein interaction..".

Thank you for your careful review. We have corrected this sentence (see line 69 on Page 3).

Line 101: correct "..qPCR analysis of developmental testis..".

We have corrected this sentence (see line 100 on Page 4). Thanks again.

Line 116: correct "..results in detective..".

Corrected.

Line 186: correct ".. explored..".

Corrected.

Line 218: correct ".. gene expressions.

Corrected.

Line 221: correct "..genes significantly differentiated expressed".

Corrected.

Line 241: FBXO24 was shown earlier in both cytoplasm and nucleus.

We have changed “FBXO24 is mainly confined to the nucleus” to “FBXO24 expressed in the nucleus”, as shown in line 247 on Page 9.

Line 501-502: correct "..reverse transcriptional".

“reverse transcriptional” was changed into “reverse transcription”, showing in Page 18.

Line 686: correct ".. deficiency male..".

Corrected.

Line 769: correct "..Western blots were adopted..".

Corrected.

Line 784: correct "..WT tesis..".

Corrected.

I cannot understand exactly what is shown in Figure 9B. Some elements marked on the X-axis are single base locations (-2K, TSS, +2K) and others are stretches of sequences so they cannot be equivalent. Why there is only an intron shown? There should be a measure of normalized expression on the Y-axis.

Thank you for your questions. The X-axis means that genome segments were scaled to the same size and were calculated the signal abundance, which was analyzed by computeMatrix. Aim to know the piRNA source, piRNA was mapped to the gene body, including introns, CDS and UTRs. The value of the Y-axis is the normalized count.

Figure 6F is not needed.

Figure 6F was used to illustrate the number of different types of mRNA splicing upon FBXO24 deletion in the round spermatids. To better understand the splicing for the reader, we decided to keep it.

The last two paragraphs of the discussion seem to be redundant.

Thank you for pointing out this. We have revised the last two paragraphs of the discussion.

eLife assessment

This important study provides insights into the role of FBXO24 in controlling spermiogenesis and male fertility in mice. The mouse models used and the data are convincing. This paper will interest biomedical researchers working on reproductive biology and fertility control.

Reviewer #1 (Public Review):

In this study, Li et al., report that FBXO24 contributes to sperm development by modulating alternative mRNA splicing and MIWI degradation during spermiogenesis. The authors demonstrated that FBXO24 deficiency impairs sperm head formation, midpiece compartmentalization, and axonemal/peri-axonemal organization in mature sperm, which causes sperm motility defects and male infertility. In addition, FBXO24 interacts with various mRNA splicing factors, which causes altered splicing events in Fbxo24-null round spermatids. Interestingly, FBXO24 also modulates MIWI levels via its polyubiquitination in round spermatids. Thus, the authors address that FBXO24 modulates global mRNA levels by regulating piRNA-mediated MIWI function and splicing events in testicular haploid germ cells.

This study is performed with various experimental approaches to explore and elucidate underlying molecular mechanisms for the FBXO24-mediated sperm defects during germ cell development. Overall, the experiments were designed properly and performed well to support the authors' observation in each part. In addition, the findings in this study are useful for understanding the physiological and developmental significance of FBXO24 in the male germ line, which can provide insight into impaired sperm development and male infertility.

In the revised manuscript, the authors address most of the concerns raised in the previous review. The following are representative remaining points.

• Quantification of the defective, vacuolar mitochondria (80%) and missing annulus (30%) was not shown in the figures or described in the results as well as in a few other figures.

Reviewer #2 (Public Review):

Spermatogenesis describes a complex sequence of differentiation events that lead to the development of genetically distinct male germ cells. The final part of spermatogenesis is called spermiogenesis, in which spermatids differentiate into mature sperm by developing an acrosome and a motile flagellum, which are required for reaching and successfully penetrating the oocyte. This process of spermatogenesis is based on a coordinated regulation of gene expressions in round spermatids. In the current study, FBXO24 was identified as a highly expressed protein in human and mouse testis. To define its biological role in vivo, the authors generated genetically engineered Fbxo24 knockout and Fbxo24-HA-labeled transgenic mouse models.

To elucidate the causes of the observed sterility in Fbxo24-KO males, the authors performed molecular and phenotypic analyses that revealed aberrant histone retention, incomplete axonemes, oversized chromatoid bodies (CB), and abnormal mitochondrial coiling along the sperm flagella. These results support the causal role of the FBXO24 gene in sperm motility.

Furthermore, the authors carefully characterized by SEM, TEM and western blot analyses that deletion of FBXO24 leads to incomplete histone-to-protamine exchange and defective chromatin interaction during spermiogenesis. In addition to increased MIWI expression, the authors show that FBXO24 interacts with SCF subunits and mediates the degradation of MIWI via K48-linked polyubiquitination.

This is a solid work demonstrating the role of FBXO24 in modulating alternative mRNA splicing, MIWI degradation and normal spermiogenesis.

Reviewer #3 (Public Review):

This work is carried out by the research group led by Shuiqiao Yuan, who has a long interest and significant contribution in the field of male germ cell development. The authors study a protein for which limited information existed prior to this work, a component of the E3 ubiquitin ligase complex, FBXO24. The authors generated the first FBXO24 KO mouse model reported in the literature using CRISPR, which they complement with HA-tagged FBXO24 transgenic model in the KO background. The authors begin their study with a very careful examination of the expression pattern of the FBXO24 gene at the level of mRNA and the HA-tagged transgene, and they provide conclusive evidence that the protein is expressed exclusively in the mouse testis and specifically in post-meiotic spermatids of stages VI to IX, which include early stages of spermatid elongation and nuclear condensation. The authors report a fully sterile phenotype for male mice, while female mice are normal. Interestingly, the testis size and the populations of spermatogenic cells in the KO mutant mice show small (but significant) reduction compared to the WT testis. Importantly, the mature sperm from KO animals show a series of defects that were very thoroughly documented in this work by scanning and transmission electron microscopy; this data constitutes a very strong point in this paper. FBXO24 KO sperm have severe defects in the mitochondrial sheath with missing mitochondria near the annulus, and missing outer dense fibers. Collectively these defects cause abnormal bending of the flagellum and severely reduced sperm motility. Moreover, defects in nuclear condensation are observed with faint nuclear staining of elongating and elongated spermatids, and reduction of protein levels of protamine 2 combined with increased levels of histones and transition protein 1. All the above are in line with the observed male sterility phenotype.

The authors also performed RNASeq in the KO animal, and found profound changes in the abundance of thousands of mRNAs; changes in mRNA splicing patterns were noted as well. This data reveals deeply affected gene expression patterns in the FBXO24 KO testis, which further supports the essential role that this factor serves in spermiogenesis. Unfortunately, a molecular explanation of what causes these changes is missing; it is still possible that they are an indirect consequence of the absence of FBXO24 and not directly caused by it.

The finding that Miwi protein levels are increased in the FBXO24 KO testis is an important point in this work, and it is in agreement with the observed increased size of the chromatoid body, where most of Miwi protein is accumulated in round spermatids. This finding is well supported with experiments performed in 293T cells showing that Miwi ubiquitination is FBXO24 dependent in this ectopic system. Moreover, the authors detect reduced ubiquitination of endogenous Miwi protein immunoprecipitated from FBXO24 KO testis. Consistent with an increase in Miwi protein levels, Miwi-sized piRNAs show increased abundance in total RNA from FBXO24 KO testis. It has been documented that Piwi proteins stabilize their piRNA cargo, so the increase in piRNA levels in 29-32 nt sizes is most likely not a result of altered biogenesis, but increased half-life of the piRNAs as a result of Miwi upregulation. piRNAs have been involved in the regulation of mRNAs in the post-meiotic spermatid, but it is unclear how increased Miwi protein and its piRNA cargo at the levels observed in this study contribute to the complete infertility phenotype of the FBXO24 KO male mice.

Therefore, a well-reasoned narrative on if and how the absence of FBXO24 as an E3 ubiquitin ligase is responsible for the observed mRNA and protein differential expression is largely absent. If FBXO24-mediated ubiquitination is required for normal protein degradation during spermiogenesis, protein level increase should be the direct consequence of genuine FBXO24 targets in the KO testis. Apart from Miwi, the possible involvement of ubiquitination was not shown for any other proteins that the authors found interact with FBXO24 such as splicing factors SRSF2, SRSF3, SRSF9, or any of the other proteins whose levels were found to be changed (reduced, thus the change in the KO is less likely due to absence of ubiquitination) such as ODF2, AKAP3, TSSK4, PHF7, TSSK6 and RNF8. Interestingly, the authors do observe increased amounts of histones and transition proteins, but reduced amounts of protamines, which directly shows that histone to protamine transition is indeed affected in the FBXO24 KO testis, consistent with the observed less condensed nuclei of spermatozoa. Could histones and transition proteins be targets of the proposed ubiquitin ligase activity of FBXO24, and in its absence, histone replacement is abrogated? Providing experimental evidence to address this possibility would greatly expand our understanding on why FBXO24 is essential during spermiogenesis.

Author Response

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, Maestri et al. use an integrative framework to study the evolutionary history of coronaviruses. They find that coronaviruses arose recently rather than having undergone ancient codivergences with their mammalian hosts. Furthermore, recent host switching has occurred extensively, but typically between closely related species. Humans have acted as an intermediate host, especially between bats and other mammal species.

Strengths:

The study draws on a range of data sources to reconstruct the history of virus-host codivergence and host switching. The analyses include various tests of robustness and evaluations through simulation.

Weaknesses:

The analyses are limited to a single genetic marker (RdRp) from coronaviruses, but using other sections of the genome might lead to different conclusions. The genetic marker also lacks resolution for recent divergences, which precludes the detailed examination of recent host switches. Careful and detailed reconstruction of the timescale would be helpful for clarifying the evolutionary history of coronaviruses alongside their hosts.

The use of a single short genetic marker (the RdRp palmprint region) from coronaviruses is indeed a limitation. However, this marker is the one that is currently used for routinely delimiting operational taxonomic units in RNA viruses and reconstructing their evolutionary history (Edgar et al. 2022, see also the Serratus project; https://serratus.io/); therefore, we took the conscious decision early on to rely on this expertise. Unfortunately, this marker cannot provide robust timescale reconstructions for coronavirus evolution (previous estimates of coronavirus origin range from around 10 thousand years ago to 293 million years ago depending on modeling assumptions). Only future genomic work across Coronaviridae that will characterize multiple genetic regions with different evolutionary rates will allow us to precisely elucidate the timescale of the evolutionary history of coronaviruses alongside their hosts. In the meantime, we show here that, while the RdRp palmprint region cannot by itself resolve the precise timescale of coronavirus evolution, it strongly suggests, when used along with cophylogenetic approaches, a recent evolutionary origin in bats.

R. C. Edgar, et al., Petabase-scale sequence alignment catalyses viral discovery. Nature 602, 142–147 (2022).

Reviewer #2 (Public Review):

Summary:

In their study titled "Recent evolutionary origin and localized diversity hotspots of mammalian coronaviruses," authors Benoît Perez-Lamarque, Renan Maestri, Anna Zhukova, and Hélène Morlon investigate the complex evolutionary history of coronaviruses, particularly those affecting mammals, including humans. The study focuses on unraveling the evolutionary trajectory of these viruses, which have shown a high propensity for causing pandemics, as evidenced by the SARS-CoV2 outbreak.

The research addresses a significant gap in our understanding of the evolutionary dynamics of coronaviruses, particularly their history, patterns of host-to-host transmission, and geographical spread. These aspects are important for predicting and managing future pandemic scenarios.

Historically, studies have employed cophylogenetic tests to explore virus-host relationships within the Coronaviridae family, often suggesting a long history of virus-host codiversification spanning millions of years. However, the team led by Perez-Lamarque proposes a novel phylogenetic framework that contrasts this traditional view. Their approach, which involves adapting gene tree-species tree reconciliation, is designed to robustly test the validity of two competing scenarios: an ancient origination and codiversification versus a more recent emergence and diversification through host switching.

Upon applying this innovative framework to the study of coronaviruses and their mammalian hosts, the authors' findings challenge the prevailing notion of a deep evolutionary history. Instead, their results strongly support a scenario where coronaviruses have a more recent origin, likely in bat populations, followed by diversification predominantly through host-switching events. This diversification, interestingly, seems to occur preferentially within mammalian orders.

A critical aspect of their findings is the identification of hotspots of coronavirus diversity, particularly in East Asia and Europe. These regions align with the proposed scenario of a relatively recent origin and subsequent localized host-switching events. The study also highlights the rarity of spillovers from bats to other species, yet underscores the relatively higher likelihood of such spillovers occurring towards humans, suggesting a significant role for humans as an intermediate host in the evolutionary journey of these viruses.

The research also points out the high rates of host-switching within mammalian orders, including between humans, domesticated animals, and non-flying wild mammals.

In conclusion, the study by Perez-Lamarque and colleagues presents an important quantitative advance in our understanding of the evolutionary history of mammalian coronaviruses. It suggests that the long-held belief in extensive virus-host codiversification may have been substantially overestimated, paving the way for a reevaluation of how we understand, predict, and potentially control the spread of these viruses.

Strengths:

The study is conceptually robust, and its conclusions are convincing.

Weaknesses:

Despite the availability of a dated host tree the authors were only able to use the "undated" model in ALE, with the dated method (which only allows time-consistent transfers) failing on their dataset (possibly due to dataset size?). Further exploration of the question would be potentially valuable.

Our intuition is that ALE in its “dated” version did not necessarily fail on our dataset due to its size (ALE ran, but provided unrealistic parameter estimates and was not able to output possible reconciliations, as mentioned in our Material and Methods section). We think it most likely did not run because there is no pattern of codiversification: the coronavirus and mammal trees are so distinct that finding a reconciliation scenario between these trees with time-consistent transfers is very difficult and ALE fails at estimating an amalgamated likelihood for such an unlikely scenario. Following a suggestion from reviewer #3, we are going to try running the dated version of ALE independently on the alpha and beta-coronaviruses, resulting in smaller datasets. This will help us elucidate whether the dated version of ALE fails due to data size or the absence of a codiversification pattern.

Reviewer #3 (Public Review):

Summary:

This work uses tools and concepts from co-phylogenetic analyses to reconstruct the evolutionary and diversification history of coronaviruses in mammals. It concludes that cross-species transmissions from bats to humans are a relatively common event (compared to bats to other species). Across all mammals, the diversification history of coronaviruses suggests that there is potential for further evolutionary diversification.

Strengths:

The article uses an interesting approach based on jointly looking at the extant network of coronaviruses-mammals interactions, and the phylogenetic history of both these organisms. The authors do an impressive job of explaining the challenges of reconstructing evolutionary dynamics for RNA viruses, and this helps readers appraise the relevance of their approach.

Weaknesses:

I remain unconvinced by the argument that sampling does not introduce substantial biases in the analyses. As the authors highlight, incomplete knowledge of the extant interactions would lead to a biased reconstruction of the diversification history. In a recent paper (Poisot et al. 2023, Patterns), we look at sampling biases in the virome of mammals and suggest that is a fairly prominent issue, that is furthermore structured by taxonomy, space, and phylogenetic position. Case in point, even for betacoronaviruses, there have been many newly confirmed hosts in recent years. For organisms that have received less intense scrutiny, I think a thorough discussion of potential gaps in data would be required (see for example Cohen et al. 2022, Nat. Comms).

I was also surprised to see little discussion of the differences between alpha and beta coronaviruses - there is evidence that they may differ in their cross-species transmission (see Caraballo et al. 2022 Micr. Spectr.), which could call into question the relevance of treating all coronaviruses as a single, homogeneous group.

Some of the discussions in this paper also echo previous work by e.g. Geoghegan et al. (see 2017, PLOS Pathogens), which I was surprised to not see discussed, as it is a much earlier investigation of the relative frequencies of co-divergence and host switches for different viral families, with a deep discussion of how this may structure future evolutionary dynamics.

We totally agree that sampling biases in the virome of mammals is a prominent issue, which is why we conducted a series of sensitivity analyses to test their effect on our main conclusions. We thoroughly tested the effect of (i) the unequal sampling effort across mammalian species that have been screened and (ii) the unequal screening of mammalian species across the mammalian tree of life by subsampling the data to correct for the unequal sampling effort (see Supporting Information Text). In both cases, we still reported low support for a scenario of codiversification, the origin in bats in East Asia, the preferential host switches within mammalian orders, and the rare spillovers from bats to humans. The robustness of our findings to sampling biases may be explained by the fact that the cophylogenetic approach we used (ALE) explicitly accounts for undersampling by assuming that all host transfers involve unsampled intermediate hosts. To address the reviewer's comment, we will better underline the importance of sampling biases in our main text and include the suggested references. We will also better highlight our sensitivity analyses by moving them from the Supporting Information Text to the main text.

We agree that distinguishing between alpha and beta coronaviruses will provide useful additional insights; we are going to run separate cophylogenetic analyses for these two sub-clades. We will report the results of these additional analyses in the revised manuscript, and put them in context with the existing literature about the two sub-clades.

We were not aware of the work of Geoghegan et al. (see 2017, PLOS Pathogens), thank you for providing this reference that we will now discuss.

Reviewer #1 (Public Review):

Summary:<br /> In this study, Maestri et al. use an integrative framework to study the evolutionary history of coronaviruses. They find that coronaviruses arose recently rather than having undergone ancient codivergences with their mammalian hosts. Furthermore, recent host switching has occurred extensively, but typically between closely related species. Humans have acted as an intermediate host, especially between bats and other mammal species.

Strengths:<br /> The study draws on a range of data sources to reconstruct the history of virus-host codivergence and host switching. The analyses include various tests of robustness and evaluations through simulation.

Weaknesses:<br /> The analyses are limited to a single genetic marker (RdRp) from coronaviruses, but using other sections of the genome might lead to different conclusions. The genetic marker also lacks resolution for recent divergences, which precludes the detailed examination of recent host switches. Careful and detailed reconstruction of the timescale would be helpful for clarifying the evolutionary history of coronaviruses alongside their hosts.

eLife assessment

Maestri et al report the absence of phylogenetic evidence supporting codiversification of mammalian coronaviruses and their hosts, leading to the important conclusion that the evolutionary history of the virus and its hosts are decoupled through frequent host switches. The evidence for frequent host switching, derived from a probabilistic model of co-evolution, appears convincing, but evidence for quantitative statements about the time of the last common ancestor of extant mammalian coronaviruses remains incomplete. The results would be strengthened by a reconstruction of the evolutionary timescale and further investigation of robustness to sampling biases and unsampled diversity.

Reviewer #2 (Public Review):

Summary:<br /> In their study titled "Recent evolutionary origin and localized diversity hotspots of mammalian coronaviruses," authors Benoît Perez-Lamarque, Renan Maestri, Anna Zhukova, and Hélène Morlon investigate the complex evolutionary history of coronaviruses, particularly those affecting mammals, including humans. The study focuses on unraveling the evolutionary trajectory of these viruses, which have shown a high propensity for causing pandemics, as evidenced by the SARS-CoV2 outbreak.

The research addresses a significant gap in our understanding of the evolutionary dynamics of coronaviruses, particularly their history, patterns of host-to-host transmission, and geographical spread. These aspects are important for predicting and managing future pandemic scenarios.

Historically, studies have employed cophylogenetic tests to explore virus-host relationships within the Coronaviridae family, often suggesting a long history of virus-host codiversification spanning millions of years. However, the team led by Perez-Lamarque proposes a novel phylogenetic framework that contrasts this traditional view. Their approach, which involves adapting gene tree-species tree reconciliation, is designed to robustly test the validity of two competing scenarios: an ancient origination and codiversification versus a more recent emergence and diversification through host switching.

Upon applying this innovative framework to the study of coronaviruses and their mammalian hosts, the authors' findings challenge the prevailing notion of a deep evolutionary history. Instead, their results strongly support a scenario where coronaviruses have a more recent origin, likely in bat populations, followed by diversification predominantly through host-switching events. This diversification, interestingly, seems to occur preferentially within mammalian orders.

A critical aspect of their findings is the identification of hotspots of coronavirus diversity, particularly in East Asia and Europe. These regions align with the proposed scenario of a relatively recent origin and subsequent localized host-switching events. The study also highlights the rarity of spillovers from bats to other species, yet underscores the relatively higher likelihood of such spillovers occurring towards humans, suggesting a significant role for humans as an intermediate host in the evolutionary journey of these viruses.

The research also points out the high rates of host-switching within mammalian orders, including between humans, domesticated animals, and non-flying wild mammals.

In conclusion, the study by Perez-Lamarque and colleagues presents an important quantitative advance in our understanding of the evolutionary history of mammalian coronaviruses. It suggests that the long-held belief in extensive virus-host codiversification may have been substantially overestimated, paving the way for a reevaluation of how we understand, predict, and potentially control the spread of these viruses.

Strengths:<br /> The study is conceptually robust, and its conclusions are convincing.

Weaknesses:<br /> Despite the availability of a dated host tree the authors were only able to use the "undated" model in ALE, with the dated method (which only allows time-consistent transfers) failing on their dataset (possibly due to dataset size?). Further exploration of the question would be potentially valuable.

Reviewer #3 (Public Review):

Summary:<br /> This work uses tools and concepts from co-phylogenetic analyses to reconstruct the evolutionary and diversification history of coronaviruses in mammals. It concludes that cross-species transmissions from bats to humans are a relatively common event (compared to bats to other species). Across all mammals, the diversification history of coronaviruses suggests that there is potential for further evolutionary diversification.

Strengths:<br /> The article uses an interesting approach based on jointly looking at the extant network of coronaviruses-mammals interactions, and the phylogenetic history of both these organisms. The authors do an impressive job of explaining the challenges of reconstructing evolutionary dynamics for RNA viruses, and this helps readers appraise the relevance of their approach.

Weaknesses:<br /> I remain unconvinced by the argument that sampling does not introduce substantial biases in the analyses. As the authors highlight, incomplete knowledge of the extant interactions would lead to a biased reconstruction of the diversification history. In a recent paper (Poisot et al. 2023, Patterns), we look at sampling biases in the virome of mammals and suggest that is a fairly prominent issue, that is furthermore structured by taxonomy, space, and phylogenetic position. Case in point, even for betacoronaviruses, there have been many newly confirmed hosts in recent years. For organisms that have received less intense scrutiny, I think a thorough discussion of potential gaps in data would be required (see for example Cohen et al. 2022, Nat. Comms).

I was also surprised to see little discussion of the differences between alpha and beta coronaviruses - there is evidence that they may differ in their cross-species transmission (see Caraballo et al. 2022 Micr. Spectr.), which could call into question the relevance of treating all coronaviruses as a single, homogeneous group.

Some of the discussions in this paper also echo previous work by e.g. Geoghegan et al. (see 2017, PLOS Pathogens), which I was surprised to not see discussed, as it is a much earlier investigation of the relative frequencies of co-divergence and host switches for different viral families, with a deep discussion of how this may structure future evolutionary dynamics.

Author Response

Reviewer #1:

This manuscript presents an extremely exciting and very timely analysis of the role that the nucleosome acidic patch plays in SWR1-catalyzed histone exchange. Intriguingly, SWR1 loses activity almost completely if any of the acidic patches are absent. To my knowledge, this makes SWR1 the first remodeler with such a unique and pronounced requirement for the acidic patch. The authors demonstrate that SWR1 affinity is dramatically reduced if at least one of the acidic patches is absent, pointing to a key role of the acidic patch in SWR1 binding to the nucleosome. The authors also pinpoint a specific subunit - Swc5 - that can bind nucleosomes, engage the acidic patch, and obtain a cryo-EM structure of Swc5 bound to a nucleosome. They also identify a conserved arginine-rich motif in this subunit that is critical for nucleosome binding and histone exchange in vitro and for SWR1 function in vivo. The authors provide evidence that suggests a direct interaction between this motif and the acidic patch.

Strengths:

The manuscript is well-written and the experimental data are of outstanding quality and importance for the field. This manuscript significantly expands our understanding of the fundamentally important and complex process of H2A.Z deposition by SWR1 and would be of great interest to a broad readership.

We thank the reviewer for their enthusiastic and positive comments on our work.

Reviewer #2:

Summary:

In this study, Baier et al. investigated the mechanism by which SWR1C recognizes nucleosomal substrates for the deposition of H2A.Z. Their data convincingly demonstrate that the nucleosome's acidic patch plays a crucial role in the substrate recognition by SWR1C. The authors presented clear evidence showing that Swc5 is a pivotal subunit involved in the interaction between SWR1C and the acidic patch. They pared down the specific region within Swc5 responsible for this interaction. However, two central assertions of the paper are less convincing. First, the data supporting the claim that the insertion of one Z-B dimer into the canonical nucleosome can stimulate SWR1C to insert the second Z-B dimer is somewhat questionable (see below). Given that this claim contradicts previous observations made by other groups, this hypothesis needs further testing to eliminate potential artifacts. Secondly, the claim that SWR1C simultaneously recognizes the acidic patch on both sides of the nucleosome also needs further investigation, as the assay used to establish this claim lacks the sensitivity necessary to distinguish any difference between nucleosomal substrates containing one or two intact acidic patches.

Strengths:

As mentioned in the summary, the authors presented clear evidence demonstrating the role of Swc5 in recognition of the nucleosome acidic patch. The identification of the specific region in Swc5 responsible for this interaction is important.

We thank the reviewer for their careful critique of our work. Below we address each major concern.

Major comments:

(1) Figure 1B: It is unclear how much of the decrease in FRET is caused by the bleaching of fluorophores. The authors should include a negative control in which Z-B dimers are omitted from the reaction. In the absence of ZB dimers, SWR1C will not exchange histones. Therefore, any decrease in FRET should represent the bleaching of fluorophores on the nucleosomal substrate, allowing normalization of the FRET signal related to A-B eviction.

In this manuscript, as well as in our two previous publications (Singh et al., 2019; Fan et al.,2022), we have presented the results of no enzyme controls, +/- ZB dimers, no ATP controls, or AMP-PNP controls for our FRET-based, H2A.Z deposition assay (see also Figure S3). We do not observe significant levels of photobleaching in this assay, either during ensemble measurements or in an smFRET experiment. To aid the reader, we have added the AMP-PNP data for the experiment shown in Figure 1B. The results show there is less than a 10% decrease in FRET over 30’, and the signal from the double acidic patch disrupted nucleosome is identical to this negative control.

(2) Figure S3: The authors use the decrease in FRET signal as a metric of histone eviction. However, Figure S3 suggests that the FRET signal decrease could be due to DNA unwrapping. Histone exchange should not occur when SWR1C is incubated with AMP-PNP, as histone exchange requires ATP hydrolysis (10.7554/eLife.77352). And since the insertion of Z-B dimer and the eviction of A-B dimer are coupled, the decrease of FRET in the presence of AMP-PNP is unlikely due to histone eviction or exchange. Instead, the FRET decrease is likely due to DNA unwrapping (10.7554/eLife.77352). The authors should explicitly state what the loss of FRET means.

We agree with the reviewer, that loss of FRET can be due to DNA unwrapping from the nucleosome. We have previously demonstrated this activity by SWR1C in our smFRET study (Fan et al., 2022). However, DNA unwrapping is highly reversible and has a time duration of only 1-3 seconds. We and others have not observed stable unwrapping of nucleosomes by SWR1C, but rather the stable loss of FRET reports on dimer eviction. We assume the reviewer is concerned about the rather large decrease in FRET signal shown in the AMP-PNP controls for Figure S3, panels A and D. For the other 7 panels, the decrease in FRET with AMP-PNP are minimal. In fact, if we average all of the AMP-PNP data points, the rate of FRET loss is not statistically different from no enzyme control reactions (nucleosome plus ZB dimers).

Data for panels A and D used a 77NO nucleosomal substrate, with Cy3 labeling the linker distal dimer. This is our standard DNA fragment, and it was used in Figure 1B. The only difference between data sets is that the data shown in Fig 1B used nucleosome reconstituted with a Cy5-labelled histone octamer, rather than the hexasome assembly method used for Fig S3. Three points are important. First, for all of these substrates, we assembled 3 independent nucleosomes, and the results are highly reproducible. Two, we performed a total of 6 experiments for the 77NO-Cy5 substrates to ensure that the rates were accurate (+/-ATP). Third, and most important, we do not see this decrease in FRET signal in the absence of SWR1C (no enzyme control). This data was included in the data source file. Thus, it appears that there is significant SWR1C-induced nucleosome instability for these two hexasome-assembled substrates. We now note this in the legend to Figure S3. Key for this work, however, is that there is a large increase in the rate of FRET loss in the presence of ATP, and this rate is faster when a ZB dimer was present at the linker proximal location. In response to the last point, we state in the first paragraph of the results: “The dimer exchange activity of SWR1C is monitored by following the decrease in the 670 nm FRET signal due to eviction of the Cy5-labeled AB-Cy5 dimer (Figure 1A).”

(3) Related to point 2. One way to distinguish nucleosomal DNA unwrapping from histone dimer eviction is that unwrapping is reversible, whereas A-B eviction is not. Therefore, if the authors remove AMP-PNP from the reaction chamber and a FRET signal reappears, then the initial loss of FRET was due to reversible DNA unwrapping. However, if the removal of AMP-PNP did not regain FRET, it means that the loss of FRET was likely due to A-B eviction. The authors should perform an AMP-PNP and/or ATP removal experiment to make sure the interpretation of the data is correct.

See response to item 2 above

(4) The nature of the error bars in Figure 1C is undefined; therefore, the statistical significance of the data is not interpretable.

We apologize for not making this more explicit for each figure. The error bars report on 95% confidence intervals from at least 3 sets of experiments. This statement has been added to the legend.

(5) The authors claim that the SWR1C requires intact acidic patches on both sides of the nucleosomes to exchange histone. This claim was based on the experiment in Figure 1C where they showed mutation of one of two acidic patches in the nucleosomal substrate is sufficient to inhibit SWR1C-mediated histone exchange activity. However, one could argue that the sensitivity of this assay is too low to distinguish any difference between nucleosomes with one (i.e., AB/AB-apm) versus two mutated acidic patches (i.e., AB-apm/AB-apm). The lack of sensitivity of the eviction assay can be seen when Figure 1B is taken into consideration. In the gel-shift assay, the AB-apm/AB-apm nucleosome exhibited a 10% SWR1C-mediated histone exchange activity compared to WT. However, in the eviction assay, the single AB/AB-apm mutant has no detectable activity. Therefore, to test their hypothesis, the authors should use the more sensitive in-gel histone exchange assay to see if the single AB/AB-apm mutant is more or equally active compared to the double AB-apm/AB-apm mutant.

Our pincher model is based on three, independent sets of data, not just Figure 1C. First, as noted by the reviewer, we find that disruption of either acidic patch cripples the dimer exchange activity of SWR1C in the FRET-based assay. Whether the defect is identical to that of the double APM mutant nucleosome does not seem pertinent to the model. In a second set of assays, we used fluorescence polarization to quantify the binding affinity of SWR1C for wildtype nucleosomes, a double APM nucleosome, or each single APM nucleosome. Consistent with the pincher model, each single APM disruption decreases binding affinity at least 10-fold (below the sensitivity of the assay). Finally, we monitored the ability of different nucleosomes to stimulate the ATPase activity of SWR1C. Consistent with the pincher model, a single APM disruption was sufficient to eliminate nucleosome stimulation.

(6) The authors claim that the AZ nucleosome is a better substrate than the AA nucleosome. This is a surprising result as previous studies showed that the two insertion steps of the two Z-B dimers are not cooperative (10.7554/eLife.77352 and 10.1016/J.CELREP.2019.12.006). The authors' claim was based on the eviction assay shown in Fig 1C. However, I am not sure how much variation in the eviction assay is contributed by different preparations of nucleosomes. The authors should use the in-gel assay to independently test this hypothesis.

For all data shown in our manuscript, at least three different nucleosome preparations were used. The impact of a ZB dimer on the rates of dimer exchange was highly reproducible among different nucleosome preparations and experiments. We also see reproducible ZB stimulation for three different substrates – with ZB on the linker proximal side, the linker distal side, and on one side of a core particle. We do not believe that our data are inconsistent with previous studies. First, the previous work referenced by the reviewer performed dimer exchange reactions with a large excess of nucleosomes to SWR1C (catalytic conditions), whereas we used single turnover reactions. Secondly, our study is the first to use a homogenous, ZA heterotypic nucleosome as a substrate for SWR1C. All previous studies used a standard AA nucleosome, following the first and second rounds of dimer exchange that occur sequentially. And finally, we observe only a 20-30% increase in rate by a ZB dimer (e.g. 77N0 substrates), and such an increase was unlikely to have been detected by previous gel-based assays.

Minor comments:

(1) Abstract line 4: To say 'Numerous' studies have shown acidic patch impact chromatin remodeling enzymes activity may be too strong.

Removed

(2) Page 15, line 15: The authors claim that swc5∆ was inviable on formamide media. However, the data in Figure 8 shows cell growth in column 1 of swc5∆.

The term ‘inviable’ has been replaced with ‘poor’ or ‘slow growth’

(3) The authors should use standard yeast nomenclature when describing yeast genes and proteins. For example, for Figure 8 and legend, Swc5∆ was used to describe the yeast strain BY4741; MATa; his3Δ1; leu2Δ0; met15Δ0; ura3Δ0; YBR231c::kanMX4. Instead, the authors should describe the swc5∆ mutant strain as BY4741 MAT a his3∆1 leu2∆0 met15∆0 ura3∆0 swc5∆::kanMX4. Exogenous plasmid should also be indicated in italics and inside brackets, such as [SWC5-URA3] or [swc5(R219A)-URA3].

We apologize for missing this mistake in the Figure 8 legend. We had inadvertently copied this from the euroscarf entry and forgot to edit the entry. We decided not to add all the plasmid names to the figure, as it was too cluttered. We state in the figure legend that the panels show growth of swc5 deletion strains harboring the indicated swc5 alleles on CEN/ARS plasmids.

(4) According to Lin et al. 2017 NAR (doi: 10.1093/nar/gkx414), there is only one Swc5 subunit per SWR1C. Therefore, the pincher model proposed by the authors would suggest that there is a missing subunit that recognizes the second acidic patch. The authors should point out this fact in the discussion. However, as mentioned in Major comment 6, I am not sure if the pincer model is substantiated.

In our discussion, we had noted that the published cryoEM structure had suggested that the Swc2 subunit likely interacts with the acidic patch on the dimer that is not targeted for replacement, and we proposed that Swc5 interacts with the acidic patch on the exchanging H2A/H2B dimer. We have now made this more clear in the text.

eLife assessment

This manuscript presents an important analysis of the role that the nucleosome acidic patch plays in SWR1-catalyzed histone exchange. This manuscript contains convincing data which significantly expands our understanding of the complex process of H2A.Z deposition by SWR1 and therefore would be of interest to a broad readership. The manuscript would benefit from addressing previous models in the field, specifically regarding the insertion of the second dimer of H2A.Z/H2B; and the involvement of the acidic patch recognition by SWR1. These points should be addressed more directly with additional data.

Reviewer #1 (Public Review):

This manuscript presents an extremely exciting and very timely analysis of the role that the nucleosome acidic patch plays in SWR1-catalyzed histone exchange. Intriguingly, SWR1 loses activity almost completely if any of the acidic patches are absent. To my knowledge, this makes SWR1 the first remodeler with such a unique and pronounced requirement for the acidic patch. The authors demonstrate that SWR1 affinity is dramatically reduced if at least one of the acidic patches is absent, pointing to a key role of the acidic patch in SWR1 binding to the nucleosome. The authors also pinpoint a specific subunit - Swc5 - that can bind nucleosomes, engage the acidic patch, and obtain a cryo-EM structure of Swc5 bound to a nucleosome. They also identify a conserved arginine-rich motif in this subunit that is critical for nucleosome binding and histone exchange in vitro and for SWR1 function in vivo. The authors provide evidence that suggests a direct interaction between this motif and the acidic patch.

Strengths:<br /> The manuscript is well-written and the experimental data are of outstanding quality and importance for the field. This manuscript significantly expands our understanding of the fundamentally important and complex process of H2A.Z deposition by SWR1 and would be of great interest to a broad readership.

Reviewer #2 (Public Review):

Summary:<br /> In this study, Baier et al. investigated the mechanism by which SWR1C recognizes nucleosomal substrates for the deposition of H2A.Z. Their data convincingly demonstrate that the nucleosome's acidic patch plays a crucial role in the substrate recognition by SWR1C. The authors presented clear evidence showing that Swc5 is a pivotal subunit involved in the interaction between SWR1C and the acidic patch. They pared down the specific region within Swc5 responsible for this interaction. However, two central assertions of the paper are less convincing. First, the data supporting the claim that the insertion of one Z-B dimer into the canonical nucleosome can stimulate SWR1C to insert the second Z-B dimer is somewhat questionable (see below). Given that this claim contradicts previous observations made by other groups, this hypothesis needs further testing to eliminate potential artifacts. Secondly, the claim that SWR1C simultaneously recognizes the acidic patch on both sides of the nucleosome also needs further investigation, as the assay used to establish this claim lacks the sensitivity necessary to distinguish any difference between nucleosomal substrates containing one or two intact acidic patches.

Strengths:<br /> As mentioned in the summary, the authors presented clear evidence demonstrating the role of Swc5 in recognition of the nucleosome acidic patch. The identification of the specific region in Swc5 responsible for this interaction is important.

Weaknesses:

Major comments:

(1) Figure 1B: It is unclear how much of the decrease in FRET is caused by the bleaching of fluorophores. The authors should include a negative control in which Z-B dimers are omitted from the reaction. In the absence of ZB dimers, SWR1C will not exchange histones. Therefore, any decrease in FRET should represent the bleaching of fluorophores on the nucleosomal substrate, allowing normalization of the FRET signal related to A-B eviction.

(2) Figure S3: The authors use the decrease in FRET signal as a metric of histone eviction. However, Figure S3 suggests that the FRET signal decrease could be due to DNA unwrapping. Histone exchange should not occur when SWR1C is incubated with AMP-PNP, as histone exchange requires ATP hydrolysis (10.7554/eLife.77352). And since the insertion of Z-B dimer and the eviction of A-B dimer are coupled, the decrease of FRET in the presence of AMP-PNP is unlikely due to histone eviction or exchange. Instead, the FRET decrease is likely due to DNA unwrapping (10.7554/eLife.77352). The authors should explicitly state what the loss of FRET means.

(3) Related to point 2. One way to distinguish nucleosomal DNA unwrapping from histone dimer eviction is that unwrapping is reversible, whereas A-B eviction is not. Therefore, if the authors remove AMP-PNP from the reaction chamber and a FRET signal reappears, then the initial loss of FRET was due to reversible DNA unwrapping. However, if the removal of AMP-PNP did not regain FRET, it means that the loss of FRET was likely due to A-B eviction. The authors should perform an AMP-PNP and/or ATP removal experiment to make sure the interpretation of the data is correct.

(4) The nature of the error bars in Figure 1C is undefined; therefore, the statistical significance of the data is not interpretable.

(5) The authors claim that the SWR1C requires intact acidic patches on both sides of the nucleosomes to exchange histone. This claim was based on the experiment in Figure 1C where they showed mutation of one of two acidic patches in the nucleosomal substrate is sufficient to inhibit SWR1C-mediated histone exchange activity. However, one could argue that the sensitivity of this assay is too low to distinguish any difference between nucleosomes with one (i.e., AB/AB-apm) versus two mutated acidic patches (i.e., AB-apm/AB-apm). The lack of sensitivity of the eviction assay can be seen when Figure 1B is taken into consideration. In the gel-shift assay, the AB-apm/AB-apm nucleosome exhibited a 10% SWR1C-mediated histone exchange activity compared to WT. However, in the eviction assay, the single AB/AB-apm mutant has no detectable activity. Therefore, to test their hypothesis, the authors should use the more sensitive in-gel histone exchange assay to see if the single AB/AB-apm mutant is more or equally active compared to the double AB-apm/AB-apm mutant.

(6) The authors claim that the AZ nucleosome is a better substrate than the AA nucleosome. This is a surprising result as previous studies showed that the two insertion steps of the two Z-B dimers are not cooperative (10.7554/eLife.77352 and 10.1016/J.CELREP.2019.12.006). The authors' claim was based on the eviction assay shown in Fig 1C. However, I am not sure how much variation in the eviction assay is contributed by different preparations of nucleosomes. The authors should use the in-gel assay to independently test this hypothesis.

Minor comments:

(1) Abstract line 4: To say 'Numerous' studies have shown acidic patch impact chromatin remodeling enzymes activity may be too strong.

(2) Page 15, line 15: The authors claim that swc5∆ was inviable on formamide media. However, the data in Figure 8 shows cell growth in column 1 of swc5∆.

(3) The authors should use standard yeast nomenclature when describing yeast genes and proteins. For example, for Figure 8 and legend, Swc5∆ was used to describe the yeast strain BY4741; MATa; his3Δ1; leu2Δ0; met15Δ0; ura3Δ0; YBR231c::kanMX4. Instead, the authors should describe the swc5∆ mutant strain as BY4741 MAT a his3∆1 leu2∆0 met15∆0 ura3∆0 swc5∆::kanMX4. Exogenous plasmid should also be indicated in italics and inside brackets, such as [SWC5-URA3] or [swc5(R219A)-URA3].

(4) According to Lin et al. 2017 NAR (doi: 10.1093/nar/gkx414), there is only one Swc5 subunit per SWR1C. Therefore, the pincher model proposed by the authors would suggest that there is a missing subunit that recognizes the second acidic patch. The authors should point out this fact in the discussion. However, as mentioned in Major comment 6, I am not sure if the pincer model is substantiated.

Author Response

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

eLife assessment

This important work by Park et al. introduces an open-top two-photon light sheet microscopy (OT-TP-LSM) for lesser invasive evaluation of intraoperative 3D pathology. The authors provide convincing evidence for the effectiveness of this technique in investigating various human cancer cells. The paper needs some minor corrections and has the potential to be of broad interest to biologists and, specifically, pathologists utilizing 3D optical microscopy.

We would like to thank the editor for the positive general comment. We revised the manuscript by addressing the reviewers' comments.

Public Reviews:

Reviewer1

Summary:

A2. This manuscript presents the development of a new microscope method termed "open-top two-photon light sheet microscopy (OT-TP-LSM)". While the key aspects of the new approach (open-top LSM and Two-photon microscopy) have been demonstrated separately, this is the first system of integrating the two. The integration provides better imaging depth than a single-photon excitation OT-LSM.

Strengths:

The use of liquid prism to minimize the aberration induced by index mismatching is interesting and potentially helpful to other researchers in the field.

• The use of propidium iodide (PI) provided a deeper imaging depth.

Weaknesses:

Details are lacking on imaging time, data size, the processing time to generate large-area en face images, and inference time to generate pseudo H&E images. This makes it difficult to assess how applicable the new microscope approach might be in various pathology applications.

B2. We would like to thank the reviewer for the critical and positive comments. We agree with the reviewer that detailed information such as processing time is missing.

The imaging time and data size were estimated per 1cm2 area and they were 7 min and 318 GB (= (7 × 60) s × 400 fps × (1850 × 512 × 2) byte) for each channel, respectively. The time for processing en-face images was relatively long by taking ~1.7 s Gb−1 after loading the image dataset at ~6.8 s Gb−1 in the current setting and needs to be shortened for intraoperative application. The time for converting OT-TP-LSM images of 512 x 512 pixels into virtual H&E staining images was 160 ms. This study was to address the current limitation of 3D pathology such as imaging depth and to develop the image processing to generate virtual H&E images. Further development such as speeding up the image processing would be needed. We added missing information and included some discussion on limitations of the new system and further development for intraoperative applications.

C1-1. Revised manuscript, Discussion, pages 14-15 and lines 320-328

Although OT-TP-LSM enabled high-speed 3D imaging, the post-processing time of the OT-TP-LSM image datasets was relatively long due to the large data size, sequential processing of dual channel images, and manual stitching. The long post-processing time needs to be resolved for intraoperative applications. To speed up processing, these processing steps can be performed using field-programmable gate array (FPGA)-based data acquisition with graphics processing unit (GPU)-based computing. The processing time can be further reduced by coding the algorithm in a C++-based environment. Furthermore, ImageJ-based software such as the Bigstitcher plugin can be used for automatic 3D image processing [44].

C1-2. Revised manuscript, Materials and methods, Image acquisition and post-processing, page 17 and lines 390-398

Image acquisition and post-processing

Raw image datasets from dual sCMOS cameras were acquired and processed on a workstation with 128 Gb RAM and a 2 TB SSD drive. The imaging time and data size per 1cm2 area with 400 fps was 7 min and 318 GB (= (7 × 60) s × 400 fps × (1850 × 512 × 2) byte) for each channel, respectively. The raw image strip was sheared at 45° with respect to the sample surface, and a custom image processing algorithm was used to transform the image data in the XYZ coordinate. The processing for en-face image was conducted in MATLAB and took ~1.7 s Gb−1 after loading the image dataset at ~6.8 s Gb−1 in the current laboratory setting. Mosaic images were generated by joining the image strips manually.

C1-3. Revised manuscript, Materials and methods, Virtual H&E staining of OT-TP-LSM via deep learning network, page 18 and lines 414-418

The CycleGAN training and testing were performed using a Nvidia GeForce RTX 3090 with 24 GB RAM. The network was implemented using Python version 3.8.0 on a desktop computer with a Core i7-12700K CPU@3.61 GHz and 64 GB RAM, running Anaconda (version 22.9.0). The inference time for converting OT-TP-LSM patch image into virtual H&E patch image was measured as 160 ms.

Reviewer 2

Summary:

A2. In this manuscript, the authors developed an open-top two-photon light sheet microscopy (OT-TP-LSM) that enables high-throughput and high-depth investigation of 3D cell structures. The data presented here shows that OT-T-LSM could be a complementary technique to traditional imaging workflows of human cancer cells.

Strengths:

High-speed and high-depth imaging of human cells in an open-top configuration is the main strength of the presented study. An extended depth of field of 180 µm in 0.9 µm thickness was achieved together with an acquisition of 0.24 mm2/s. This was confirmed by 3D visualization of human cancer cells in the skin, pancreas, and prostate.

Weaknesses:

The complementary aspect of the presented technique in human pathological samples is not convincingly presented. The traditional hematoxylin and eosin (H&E) staining is a well-established and widely used technique to detect human cancer cells. What would be the benefit of 3D cell visualization in an OT-TP-LSM microscope for cancer detection in addition to H&E staining?

B2. We would like to thank the reviewer for the critical and positive comments. 3D pathology has been a long-standing research direction. The current pathology is 2D by examining H&E histology slides which were generated by thin sectioning biopsied and surgical specimens at different depths. The reliability of the pathological diagnosis suffers from under sampling of specimens. Although 3D pathology is possible by serial thin-sectioning, imaging, and then combining the images in 3D, it is not practice for clinical use due to the required labor and time.

We demonstrated the advantages of OT-TP-LSM in various human cancer tissues. The relatively high imaging depths of OT-TP-LSM enabled the nondestructive visualization of detailed 3D cell structures with high contrast and without distortion and allowed a distinction between cancer and normal cell structures as well as the detection of cancer invasiveness within tissues. We revised the manuscript to explain the benefits of 3D pathology with OT-TP-LSM.

C2-1. Revised manuscript, Results, 3D OT-TP-LSM imaging of human skin cancers, pages 8-9 and lines 176-180

Using 3D visualization, normal glandular structures in the dermis were distinguished from BCC tumor nests (Video 1). Both eccrine and sebaceous glands could appear similar to BCC nests in 2D images at certain depths. Hence, nondestructive 3D visualization of cell structures would be important for distinguishing them, serving as a complement to the traditional 2D H&E images.

C2-2. Revised manuscript, Results, 3D OT-TP-LSM imaging of human pancreatic cancers, pages 10-11 and lines 222-232

Magnified images of ROI 1 (PDAC) at two different depths showed irregularly shaped glands with sharp angles and 3D structural complexity including unstable bridging structure inside (Figure 4B). An irregular and distorted architecture amidst desmoplastic stroma is one of the important diagnostic factors for PDAC [35]. The cancer glands exhibited disorganized cancer cell arrangement with nuclear membrane distortion. Magnified images of ROI 2 showed both nonneoplastic ducts and cancer glands in different cell arrangements (Figure 4C). The nonneoplastic ducts showed single-layered epithelium with small, evenly distributed cells expressing relatively high nuclear fluorescence. Cancer glands, on the other hand, had disorganized and multilayered structure with large nuclei. OT-TP-LSM visualized the 3D invasiveness of cancer glands within tissues nondestructively, which could not be identified from limited 2D information.

C2-3. Revised manuscript, Results, 3D OT-TP-LSM imaging of human prostatic cancers, page 11 and lines 251-252

OT-TP-LSM provided histological 3D information equivalent to that of the H&E stained image without the need for sectioning.

C2-4. Revised manuscript, Discussion, page 12 and lines 274-276

OT-TP-LSM was developed for the rapid and precise nondestructive 3D pathological examination of excised tissue specimens during both biopsy and surgery, as a compliment to traditional 2D H&E pathology by visualizing 3D cell structures.

C2-5. Revised manuscript, Discussion, page 13 and lines 284-288

The relatively high imaging depths of OT-TP-LSM enabled the nondestructive visualization of detailed 3D cell structures with high contrast and without distortion and allowed a distinction between cancer and normal cell structures as well as the detection of cancer invasiveness within tissues. These have been challenging with 2D histological images.

Reviewer #2 (Recommendations For The Authors):

I would suggest the following points to the authors to enhance the readability of the manuscript and to provide a strong narrative to explain their findings:

A3. Line 54: For the non-expert readers, please provide more background information about the histopathology before introducing the hematoxylin and eosin staining.

B3. We would like to thank the reviewer for the comment. As suggested by the reviewer, we added information about the current standard method of histopathological examination and its limitations.

C3. Revised manuscript, introduction, page 4 and lines 56-64 Precise intraoperative cancer diagnosis is crucial for achieving optimal patient outcomes by enabling complete tumor removal. The standard method is the microscopic cellular examination of surgically excised specimens following various processing steps, including thin sectioning and hematoxylin and eosin (H&E) cell staining. However, this examination method is laborious and time-consuming. Furthermore, it has inherent artifacts that disturb accurate diagnosis, including tissue loss, limited two-dimensional (2D) information, and sampling error [1]. High-speed three-dimensional (3D) optical microscopy, which can visualize cellular structures without thin sectioning, holds promise for nondestructive 3D pathological examination as a complement of 2D pathology limitation [1-4].

A4. Line 66 and 71: Please briefly introduce the cited studies to give some information about the previous studies. This will help to reader to understand the innovative aspects of your study.

B4. We would like to thank the reviewer for the comment. As suggested by the reviewer, we added a brief introduction about the cited studies.

C4. Revised manuscript, introduction, pages 4-5 and lines 71-82

As a deep tissue imaging method, two-photon microscopy (TPM) has been used in both biological and optical biopsy studies [17-19]. TPM is based on nonlinear two-photon excitation of fluorophores and achieves high imaging depths down to a few hundred micrometers by using long excitation wavelengths, which reduce light scattering. Moreover, TPM provides additional intrinsic second harmonic generation (SHG) contrast for visualizing collagen fibers within the extracellular matrix (ECM). This feature proved advantageous for high-contrast imaging of cancer tissue and microenvironmental analysis [20-22]. However, TPM has low imaging speeds due to point scanning-based imaging. To address this limitation, two-photon LSM (TP-LSM) techniques were developed for high-speed imaging [23-27]. Although TP-LSM facilitated rapid 3D imaging of cancer cells and zebrafish, its applications were limited to small samples and biological studies due to geometric limitations.

A5. Line 72: Please mention the importance and benefit of having an open-top configuration. I think this is one of the key aspects that provide a high imaging depth in OT-LP-LSM.

B5. We would like to thank the reviewer for the comment. Conventional LSM techniques including TP-LSM have a configuration in which the illumination objective is oriented in the horizontal plane and imaging is performed with orthogonally arranged objectives. However, this geometry limited lateral sample size physically and it is unsuitable to image centimeter-scale large tissue. Therefore, we developed OT-TP-LSM for 3D large tissue examination. High imaging depths were achieved with long excitation wavelengths and long emission wavelengths of fluorophores. The open-top configuration does not contribute to the improvement of imaging depth. We revised the manuscript to explain the need for open-top configuration.

C5. Revised manuscript, introduction, page 5 and lines 82-86

Conventional TP-LSM had a configuration of a horizontally oriented illumination objective and a vertically oriented imaging objective. This geometry imposed limitations on the sample size, rendering it unsuitable for the examination of centimeter-scale specimens. TP-LSM with open-top configuration is needed for 3D histological examination.

A6. Line 78: It would be nice to clearly quantify the imaging depth here.

B6. We would like to thank the reviewer for the comment. Although we considered entering the quantitative imaging depth of OT-TP-LSM in the introduction section, we decided that it would be appropriate to present the quantitative imaging depth in the Results section and discuss it in the Discussion section.

A7. Line 146: Please clearly explain the reason why the upper layers are not resolved.

B7. We would like to thank the reviewer for the comment and we are sorry for the missing information. The skin epidermis has various cell layers and superficial layers are composed of less rounded and flat cells with relatively small cytoplasm. Therefore, cells in that layer could be difficult to resolve with the current system resolution because there is little space between nuclei. Additionally, strong autofluorescence signal in the stratum corneum could be the reason for preventing visualization of the cells in the superficial layer. We revised the manuscript to explain the reasons in detail.

C7. Revised manuscript, Results, 3D OT-TP-LSM imaging of human skin cancers, page 8 and lines 159-163

Keratinocytes in the basal layer were relatively large and individually resolved, while those in the upper layers were unresolved and appeared as a band. It could be attributed to the upper layers being comprised of flat cells with relatively small cytoplasm, resulting in little space between nuclei. Additionally, strong autofluorescence signal in the stratum corneum might prevent visualization of the cells in the superficial layer.

A8. Line 253: Please explain the importance of visualization of 3D cell structures in cancer pathology. I think this should be stated clearly throughout the text as it is the key component of OT-LP-LSM to complement the traditional H&E staining. Also, referring to the non-destructive manner of your technique would help to emphasize this point.

B8. We would like to thank the reviewer for the comment. As answered in A2, the current H&E histological examination has inherent limitations due to limited 2D information and sampling errors. To resolve this, OT-TP-LSM was developed for the visualization of 3D cell structures nondestructively as a complement to traditional slide-based 2D pathology. We demonstrated the advantages of OT-TP-LSM in various human cancer tissues. The relatively high imaging depths of OT-TP-LSM enabled the nondestructive visualization of detailed 3D cell structures with high contrast and without distortion and allowed a distinction between cancer and normal cell structures as well as the detection of cancer invasiveness within tissues. We revised the manuscript to explain the benefits of 3D pathology with OT-TP-LSM.

C8. Please refer to the answer in C2-1 – C2-5.

A9. Figures: Please clearly mark the cancer regions in the images as indicated in Figure 5. It will help the reader to easily compare the healthy and invaded tissue parts.

B9. We would like to thank the reviewer for the comment. We confirmed that the cancer area is not marked in Figure 4 of the pancreatic cancer tissue. We modified Figure 4 to mark the cancer region. Additionally, Figure 2 of the skin cancer tissue was also modified in this regard.

C9. Modified Figure 2 and Figure 4.

Author response image 1.

Author response image 2.

eLife assessment

This important work by Park et al. demonstrates an open-top two-photon light sheet microscopy (OT-TP-LSM) for lesser invasive evaluation of intraoperative 3D pathology. The authors provide convincing evidence for the effectiveness of this technique investigating various human cancer cells. This article will be of broad interest to biologists and, specifically, pathologists utilizing 3D optical microscopy.

Reviewer #1 (Public Review):

Summary:

This manuscript presents the development of a new microscope method termed "open-top two-photon light sheet microscopy (OT-TP-LSM)". While the key aspects of the new approach (open top LSM and Two-photon microscopy) have been demonstrated separately, this is the first system of integrating the two. The integration provides better imaging depth than a single-photon excitation OT-LSM.

Strengths:<br /> - Use of liquid prism to minimize the aberration induced by index mismatching is interesting and potentially helpful to other researchers in the field.<br /> - Use of propidium iodide (PI) provided a deeper imaging depth.

Weaknesses:<br /> -None noted.

Reviewer #2 (Public Review):

In this manuscript, the authors developed an open-top two-photon light sheet microscopy (OT-TP-LSM) that enables high-throughput and high-depth investigation of 3D cell structures. The data presented here shows that OT-T-LSM could be a complementary technique to traditional imaging workflows of human cancer cells.

High-speed and high-depth imaging of human cells in an open-top configuration is the main strength of the presented study. An extended depth of field of 180 µm in 0.9 µm thickness was achieved together with an acquisition of 0.24 mm2/s. This was confirmed by 3D visualization of human cancer cells in the skin, pancreas, and prostate.

Author Response

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

We would like to first thank the Editor as well as the two reviewers for their enthusiasm and careful evaluation of our manuscript. We also appreciate their thoughtful and constructive comments and suggestions. They did, however, have concerns regarding experimental design, data analysis, and over-interpretation of our findings. We endeavored to address these concerns through refinement of our framing, inclusion of additional new analyses, and rewriting some parts of our discussion section. We hope our response can better explain the rationale of our experimental design and data interpretation. In addition, we also acknowledge the limitations of our present study, so that it will benefit future investigations into this topic. Our detail responses are provided below.

Reviewer #1 (Public Review)

This study examines whether the human brain uses a hexagonal grid-like representation to navigate in a non-spatial space constructed by competence and trustworthiness. To test this, the authors asked human participants to learn the levels of competence and trustworthiness for six faces by associating them with specific lengths of bar graphs that indicate their levels in each trait. After learning, participants were asked to extrapolate the location from the partially observed morphing bar graphs. Using fMRI, the authors identified brain areas where activity is modulated by the angles of morphing trajectories in six-fold symmetry. The strength of this paper lies in the question it attempts to address. Specifically, the question of whether and how the human brain uses grid-like representations not only for spatial navigation but also for navigating abstract concepts, such as social space, and guiding everyday decision-making. This question is of emerging importance.

Thanks very much again for the evaluation and comments. Please find our revision plans to each comment below.

The weak points of this paper are that its findings are not sufficiently supporting their arguments, and there are several reasons for this:

(1) Does the grid-like activity reflect 'navigation over the social space' or 'navigation in sensory feature space'? The grid-like representation in this study could simply reflect the transition between stimuli (the length of bar graphs). Participants in this study associated each face with a specific length of two bars, and the 'navigation' was only guided by the morphing of a bar graph image. Moreover, any social cognition was not required to perform the task where they estimate the gridlike activity. To make social decision-making that was conducted separately, we do not know if participants needed to navigate between faces in a social space. Instead, they can recall bar graphs associated with faces and compute the decision values by comparing the length of bars. Notably, in the trust game in this study, competence and trustworthiness are not equally important to make a decision (Equation 1). The expected value is more sensitive to one over the other. This also suggests that the space might not reflect social values but perceptual differences.

The Reviewer raises an interesting point. We apologize for not being clear enough to address this possibility in our original manuscript and we will improve the clarity in our revision. To address this issue, we would like to break it into two sub-questions and answer them separately: 1) Are participants merely memorizing the values associated with each avatar or do they place the avatars on a two-dimensional map in their internal representation. 2) If so, are the two dimensions of this internal representation social dimensions relating to competence and trust or sensory dimensions relating to bar height (i.e., social space or sensory space).

For the first question, we hope our analysis of the distance effect on the reaction time in the comparison task can address this issue. Specifically, it came from the idea that distance is a measure of similarity between two avatars in the 2D social space. The closer two avatars are, the more similar they are, hence distinguishing them will be harder and result in longer reaction time. If participants are merely memorizing the avatars as six isolated instances without integrating them into a low-dimensional map, then avatars should be equidistant (as if they were lying on the vertices of a 5-simplex), and would not show a distance effect. Therefore, we interpreted the stronger distance effect as a behavioural index of having a better internal map-like representation. This approach is adopted from the work by Park et al. (2020), where they used the distance effect to demonstrate human brains map abstract relationships among entities from piecemeal learning.

For the second question of ‘social space’ vs. ‘sensory space’, our study adopted the paradigm developed by, in which they used a similar way to construct a conceptual space and found that such space can be represented with grid-like code in the entorhinal and prefrontal cortex. We stayed close to the original design by Constantinescu et al. (2016) and hoped that our work could provide, to some extent, a close replication of their result but using non-spatial social concepts instead. Indeed, this led to the limitation of our study that participants are passively traversing the artificial space rather than actively navigating in the space to make decisions/inferences. And we did not find sufficient evidence as reported in previous grid-like coding fMRI studies. This may have to do with low signal quality in the medial temporal region, we are not entirely sure. Nevertheless, we don’t think our findings contradict or disprove previous findings in any way. Here we would also like to point to the work by Park et al. (2021). Their task involves making novel inferences in a 2D social hierarchy space and found that grid-like code in the entorhinal cortex and medial prefrontal cortex support such novel inferences. Hence, we argue that results from these studies and partial evidence from our study collectively support the idea that the entorhinal is important for representing abstract knowledge (spatial and non-spatial).

(2) Does the brain have a common representation of faces in a social space? In this study, participants don't need to have a map-like representation of six faces according to their levels of social traits. Instead, they can remember the values of each trait. The evidence of neural representations of the faces in a 2-dimensional social space is lacking. The authors argued that the relationship between the reaction times and the distances between faces provides evidence of the formation of internal representations. However, this can be found without the internal representation of the relationships between faces. If the authors seek internal representations of the faces in the brain, it would be important to show that this representation is not simply driven by perceptual differences between bar graphs that participants may recall in association with each face.

Considering these caveats, it is hard for me to agree if the authors provide evidence to support their claims.

With regard to the common representation of faces, this is a potential limitation of our paradigm because our current task design didn’t include a stage of face presentation to properly test this question. With regard to the asymmetry between the two dimensions in determining expected value. We think that the prerequisite for identifying six-fold grid-like coding is to have an abstract space formed by orthogonal dimensions, i.e., competence and trustworthiness in our task are not correlated. In addition, the scanner task does not require computation of expected value. However, we do think that it is worth investigating whether the extent to which each dimension contributes to decision-making and inference will distort the grid-like representation of the map. Our prediction is that the entorhinal cortex will maintain a representation of the map invariant to this aspect so that it can support inferences in different contexts where different weights may be assigned to different dimensions. But this will be an interesting hypothesis for future studies to test. We hope that our revision plans with above considerations could address the Reviewer’s comments.

Reviewer #2 (Public Review)

Summary:

In this work, Liang et al. investigate whether an abstract social space is neurally represented by a grid-like code. They trained participants to 'navigate' around a two-dimensional space of social agents characterized by the traits of warmth and competence, then measured neural activity as participants imagined navigating through this space. The primary neural analysis consisted of three procedures: 1) identifying brain regions exhibiting the hexagonal modulation characteristic of a grid-like code, 2) estimating the orientation of each region's grid, and 3) testing whether the strength of the univariate neural signal increases when a participant is navigating in a direction aligned with the grid, compared to a direction that is misaligned with the grid.

From these analyses, the authors find the clearest evidence of a grid-like code in the prefrontal cortex and weaker evidence in the entorhinal cortex.

Strengths:

The work demonstrates the existence of a grid-like neural code for a socially-relevant task, providing evidence that such coding schemes may be relevant for a variety of two-dimensional task spaces.

Thank you very much again for your careful evaluation and thoughtful comments. Please find our response to the comments below.

Weaknesses:

In various parts of this manuscript, the authors appear to use a variety of terms to refer to the (ostensibly) same neural regions: prefrontal cortex, frontal pole, ventromedial prefrontal cortex (vmPFC), and orbitofrontal cortex (OFC). It would be useful for the authors to use more consistent terminology to avoid confusing readers.

Thanks for pointing out the use of terms, we will try to improve that in the revision of our manuscript.

Claims about a grid code in the entorhinal cortex are not well-supported by the analyses presented. The whole-brain analysis does not suggest that the entorhinal cortex exhibits hexagonal modulation; the strength of the entorhinal BOLD signal does not track the putative alignment of the grid code there; multivariate analyses do not reveal any evidence of a grid-like representational geometry.

On a conceptual level, it is not entirely clear how this work advances our understanding of gridlike encoding of two-dimensional abstract spaces, or of social cognition. The study design borrows heavily from Constantinescu et al. 2016, which is itself not an inherent weakness, but the Constantinescu et al. study already suggests that grid codes are likely to underlie two-dimensional spaces, no matter how abstract or arbitrary. If there were a hypothesis that there is something unique about how grid codes operate in the social domain, that would help motivate the search for social grid codes specifically, but no such theory is provided. The authors do note that warmth and competence likely have ecological importance as social traits, but other past studies have used slightly different social dimensions without any apparent loss of generality (e.g., Park et al. 2021). There are some (seemingly) exploratory analyses examining how individual difference measures like social anxiety and avoidance might affect the brain and behavior in this study, but a strong theoretical basis for examining these particular measures is lacking.

We acknowledge that we used very similar dimensions to the work by Park et al. (2021). While Park and colleagues (2021) took a more innovative and rigorous approach, we tried to stay close to the original design by Constantinescu et al. (2016) with the hope that our work could provide, to some extent, a close replication of their result. Our data was collected before the 2021 paper came out and as the comment points out, we did not find as complete and convincing evidence as in these previous grid-like coding fMRI papers. This may be due to low signal quality in the medial temporal region, we are not entirely sure. But we don’t think our current findings can contradict or disprove previous findings in any way.

I found it difficult to understand the analyses examining whether behavior (i.e., reaction times) and individual difference measures (i.e., social anxiety and avoidance) can be predicted by the hexagonal modulation strength in some region X, conditional on region X having a similar estimated grid alignment with some other region Y. It is possible that I have misunderstood the authors' logic and/or methodology, but I do not feel comfortable commenting on the correctness or implications of this approach given the information provided in the current version of this manuscript.

We apologize for not being clear enough in the manuscript and we will improve the clarity in our revision. This exploratory analysis aims to examine if there is any correlation between the strength of grid-like representation of social value map and behavioral indicators of map-like representation; and test if there are any correlation between the strength of grid-like representation of this social value map and participants’ social trait. For the behavioral indicator, we used the distance effect in the reaction time of the comparison task outside the scanner. The closer a pair of avatars are, the more similar they are, hence distinguishing them will be harder and results in longer reaction time when making comparison judgement. If participants are merely memorizing the avatars as six isolated instances without integrating them into a map, all avatars should be equidistant and there wouldn’t be a distance effect. We interpreted stronger grid-like activity as a neural index of better representation of the 2D social space, and we interpreted stronger distance effect as a behavioral index of having better internal map-like representation.

It was puzzling to see passing references to multivariate analyses using representational similarity analysis (RSA) in the main text, given that RSA is only used in analyses presented in the supplementary material.

We speculate if RSA in entorhinal ROI would be more sensitive than the wholebrain univariate analysis to identify grid-like code because a previous paper on grid-like code in olfactory space (Bao et al., 2019) didn’t identify grid-like representation with univariate analysis but identified it with RSA analysis. However, we failed to find evidence of grid-like code in the entorhinal ROI aligned to its own putative grid orientation with the RSA approach. We reported this result in the main text to show that we carried out a relatively thorough investigation to test the hypothesis using various approaches and decided to add references to the RSA approach in the main text as well.

Reviewer #3 (Public Review)

Liang and colleagues set out to test whether the human brain uses distance and grid-like codes in social knowledge using a design where participants had to navigate in a two-dimensional social space based on competence and warmth during an fMRI scan. They showed that participants were able to navigate the social space and found distance-based codes as well as grid-like codes in various brain regions, and the grid-like code correlated with behavior (reaction times).

On the whole, the experiment is designed appropriately for testing for distant-based and grid-like codes and is relatively well-powered for this type of study, with a large amount of behavioral training per participant. They revealed that a number of brain regions correlated positively or negatively with distance in the social space, and found grid-like codes in the frontal polar cortex and posterior medial entorhinal cortex, the latter in line with prior findings on grid-like activity in the entorhinal cortex. The current paper seems quite similar conceptually and in design to previous work, most notably by Park et al., 2021, Nature Neuroscience.

Thanks very much again for your careful evaluation and comments. Please find our response to the comments below.

Below, I raise a few issues and questions on the evidence presented here for a grid-like code as the basis of navigating abstract social space or social knowledge.

(1) The authors claim that this study provides evidence that humans use a spatial / grid code for abstract knowledge like social knowledge.

This data does specifically not add anything new to this argument. As with almost all studies that test for a grid code in a similar "conceptual" space (not only the current study), the problem is that when the space is not a uniform, square/circular space, and 2-dimensional then there is no reason the code will be perfectly grid-like, i.e., show six-fold symmetry. In real-world scenarios of social space (as well as navigation, semantic concepts), it must be higher dimensional - or at least more than two-dimensional. It is unclear if this generalizes to larger spaces where not all part of the space is relevant. Modelling work from Tim Behrens' lab (e.g., Whittington et al., 2020) and Bradley Love's lab (e.g., Mok & Love, 2019) have shown/argued this to be the case. In experimental work, like in mazes from the Mosers' labs (e.g., Derdikman et al., 2009), or trapezoid environments from the O'Keefe lab (Krupic et al., 2015), there are distortions in mEC cells, and would not pass as grid cells in terms of the six-fold symmetry criterion.

The authors briefly discuss the limitations of this at the very end but do not really say how this speaks to the goal of their study and the claim that social space or knowledge is organized as a grid code and if it is in fact used in the brain in their study and beyond. This issue deserves to be discussed in more depth, possibly referring to prior work that addressed this, and raising the issue for future work to address the problem - or if the authors think it is a problem at all.

Thanks very much for the references to the papers that we haven’t considered enough in our discussion. We will endeavour to discuss the topic in more depth in our revision. In summary, we raise this discussion point because various research groups have found gridlike representations in 2D artificial conceptual space. We think that the next step for a stronger claim would be to find the representation of more spontaneous non-spatial maps.

Data and analysis

(2) Concerning the negative correlation of distance with activation in the fusiform gyrus and visual cortex: this is a slightly puzzling but potentially interesting finding. However, could this be related to reaction times? The larger the distance, the longer the reaction times, so the original finding might reflect larger activations with smaller distances.

Thanks very much for the suggestion. However, we didn’t find a correlation between response time in the choice stage in the scanner task and the negative distance activation in the fusiform gyrus (Figures below). Meanwhile, the morph period in each trial remains the same, the negative correlation of distance with activation in the fusiform gyrus could also be interpreted as a positive correlation of morphing speed with activation in the fusiform gyrus. Indeed, stronger negative activation indicates larger activation for smaller distances, but we are uncertain what it indicates concerning the functional role of Fusiform in our current task.

Author response image 1.

(3) Concerning the correlation of grid-like activity with behavior: is the correlation with reaction time just about how long people took (rather than a task-related neural signal)? The authors have only reported correlations with reaction time. The issue here is that the duration of reaction times also relates to the starting positions of each trial and where participants will navigate to. Considering the speed-accuracy tradeoff, could performance accuracy be negatively correlated with these grid consistency metrics? Or it could be positively correlated, which would suggest the grid signal reflects a good representation of the task.

We apologize for not being clear enough in the manuscript and we will improve the clarity in our revision. The reaction time used to calculate the distance effect is from a task outside the scanner. The closer a pair of avatars are, the more similar they are, hence distinguishing them will be harder and results in longer reaction time when making comparison judgement. If participants are merely memorizing the avatars as six isolated instances without integrating them into a map, all avatars should be equidistant and there wouldn’t be a distance effect. We interpreted stronger grid-like activity as a neural index of better representation of the 2D social space, and we interpreted stronger distance effect as a behavioural index of having better internal map-like representation. This was the motivation behind this analysis.

References

Bao, X., Gjorgieva, E., Shanahan, L. K., Howard, J. D., Kahnt, T., & Gottfried, J. A. (2019). Grid-like Neural Representations Support Olfactory Navigation of a Two-Dimensional Odor Space. Neuron, 102(5), 1066-1075 e1065. https://doi.org/10.1016/j.neuron.2019.03.034

Constantinescu, A. O., O'Reilly, J. X., & Behrens, T. E. J. (2016). Organizing conceptual knowledge in humans with a gridlike code. Science,352(6292), 1464-1468. https://doi.org/10.1126/science.aaf0941

Park, S. A., Miller, D. S., & Boorman, E. D. (2021). Inferences on a multidimensional social hierarchy use a grid-like code. Nat Neurosci, 24(9), 1292-1301. https://doi.org/10.1038/s41593-02100916-3

Park, S. A., Miller, D. S., Nili, H., Ranganath, C., & Boorman, E. D. (2020). Map Making: Constructing, Combining, and Inferring on Abstract Cognitive Maps. Neuron, 107(6), 1226-1238 e1228. https://doi.org/10.1016/j.neuron.2020.06.030

eLife assessment

This study provides useful initial information on how humans represent two-dimensional abstract spaces in relation to the social traits of warmth and competence. While the study poses an interesting question, the evidence for a grid-like code at present is incomplete. This study will be of interest to researchers working in the field of spatial navigation as well as the navigation of conceptual abstract space.

Reviewer #1 (Public Review):

This study examines whether the human brain uses a hexagonal grid-like representation to navigate in a non-spatial space constructed by competence and trustworthiness. To test this, the authors asked human participants to learn the levels of competence and trustworthiness for six faces by associating them with specific lengths of bar graphs that indicate their levels in each trait. After learning, participants were asked to extrapolate the location from the partially observed morphing bar graphs. Using fMRI, the authors identified brain areas where activity is modulated by the angles of morphing trajectories in six-fold symmetry. The strength of this paper lies in the question it attempts to address. Specifically, the question of whether and how the human brain uses grid-like representations not only for spatial navigation but also for navigating abstract concepts, such as social space, and guiding everyday decision-making. This question is of emerging importance.

I acknowledge the authors' efforts to address the comments received. However, my concerns persist:

(1) The authors contend that shorter reaction times correlated with increased distances between individuals in social space imply that participants construct and utilize two-dimensional representations. This method is adapted from a previous study by Park et al. Yet, there is a fundamental distinction between the two studies. In the prior work, participants learned relationships between adjacent individuals, receiving feedback on their decisions, akin to learning spatial locations during navigation. This setup leads to two different predictions: If participants rely on memory to infer relationships, recalling more pairs would be necessary for distant individuals than for closer ones. Conversely, if participants can directly gauge distances using a cognitive map, they would estimate distances between far individuals as quickly as for closer ones. Consequently, as the authors suggest, reaction times ought to decrease with increasing decision value, which, in this context, corresponds to distances. However, the current study allowed participants to compare all possible pairs without restricting learning experiences, rendering the application of the same methodology for testing two-dimensional representations inappropriate. In this study, the results could be interpreted as participants not forming and utilizing two-dimensional representations.

(2) The confounding of visual features with the value of social decision-making complicates the interpretation of this study's results. It remains unclear whether the observed grid-like effects are due to visual features or are genuinely indicative of value-based decision-making, as argued by the authors. Contrary to the authors' argument, this issue was not present in the previous study (Constantinescu et al.). In that study, participants associated specific stimuli with the identities of hidden items, but these stimuli were not linked to decision-making values (i.e., no image was considered superior to another). The current study's paradigm is more akin to that of Bao et al., which the authors mention in the context of RSA analysis. Indeed, Bao et al. controlled the length of the bars specifically to address the problem highlighted here. Regrettably, in the current paradigm, this conflation remains inseparable.

(3) While the authors have responded to comments in the public review, my concerns noted in the Recommendation section remain unaddressed. As indicated in my recommendations, there are aspects of the authors' methodology and results that I find difficult to comprehend. Resolving these issues is imperative to facilitate an appropriate review in subsequent stages.

Considering that the issues raised in the previous comments remain unresolved, I have retained my earlier comments below for review.

The weak points of this paper are that its findings are not sufficiently supporting their arguments, and there are several reasons for this:

(1) Does the grid-like activity reflect 'navigation over the social space' or 'navigation in sensory feature space'? The grid-like representation in this study could simply reflect the transition between stimuli (the length of bar graphs). Participants in this study associated each face with a specific length of two bars, and the 'navigation' was only guided by the morphing of a bar graph image. Moreover, any social cognition was not required to perform the task where they estimate the grid-like activity. To make social decision-making that was conducted separately, we do not know if participants needed to navigate between faces in a social space. Instead, they can recall bar graphs associated with faces and compute the decision values by comparing the length of bars. Notably, in the trust game in this study, the competence and trustworthiness are not equally important to make a decision (Equation 1). The expected value is more sensitive to one over the other. This also suggests that the space might not reflect social values but the perceptual differences.

(2) Does the brain have a common representation of faces in a social space? In this study, participants don't need to have a map-like representation of six faces according to their levels of social traits. Instead, they can remember the values of each trait. The evidence of neural representations of the faces in a 2-dimensional social space is lacking. The authors argued the relationship between the reaction times and the distances between faces provides evidence of the formation of internal representations. However, this can be found without the internal representation of the relationships between faces. If the authors seek internal representations of the faces in the brain, it would be important to show that this representation is not simply driven by perceptual differences between bar graphs that participants may recall in association with each face.

Considering these caveats, it is hard for me to agree if the authors provide evidence to support their claims.

Reviewer #2 (Public Review):

Summary:<br /> In this work, Liang et al. investigate whether an abstract social space is neurally represented by a grid-like code. They trained participants to 'navigate' around a two-dimensional space of social agents characterized by the traits warmth and competence, then measured neural activity as participants imagined navigating through this space. The primary neural analysis consisted of three procedures: 1) identifying brain regions exhibiting the hexagonal modulation characteristic of a grid-like code, 2) estimating the orientation of each region's grid, and 3) testing whether the strength of the univariate neural signal increases when a participant is navigating in a direction aligned with the grid, compared to a direction that is misaligned with the grid. From these analyses, the authors find the clearest evidence of a grid-like code in the prefrontal cortex and weaker evidence in the entorhinal cortex.

Strengths:<br /> The work demonstrates the existence of a grid-like neural code for a socially-relevant task, providing evidence that such coding schemes may be relevant for a variety of two-dimensional task spaces.

Weaknesses:<br /> In the revised manuscript, the authors soften their claims about finding a grid code in the entorhinal cortex and provide additional caveats about limitations in their findings. It seems that the authors and reviewers are in agreement about the following weaknesses, which were part of my original review: Claims about a grid code in the entorhinal cortex are not well-supported by the analyses presented. The whole-brain analysis does not suggest that the entorhinal cortex exhibits hexagonal modulation; the strength of the entorhinal BOLD signal does not track the putative alignment of the grid code there; multivariate analyses do not reveal any evidence of a grid-like representational geometry.

In the authors' response to reviews, they provide additional clarification about their exploratory analyses examining whether behavior (i.e., reaction times) and individual difference measures (i.e., social anxiety and avoidance) can be predicted by the hexagonal modulation strength in some region X, conditional on region X having a similar estimated grid alignment with some other region Y. My guess is that readers would find it useful if some of this language were included in the main text, especially with regard to an explanation regarding the rationale for these exploratory studies.

Reviewer #3 (Public Review):

Liang and colleagues set out to test whether the human brain uses distance and grid-like codes in social knowledge using a design where participants had to navigate in a two-dimensional social space based on competence and warmth during an fMRI scan. They showed that participants were able to navigate the social space and found distance-based codes as well as grid-like codes in various brain regions, and the grid-like code correlated with behavior (reaction times).

On the whole, the experiment is designed appropriately for testing for distant-based and grid-like codes, and is relatively well powered for this type of study, with a large amount of behavioral training per participant. They revealed that a number of brain regions correlated positively or negatively with distance in the social space, and found grid-like codes in the frontal polar cortex and posterior medial entorhinal cortex, the latter in line with prior findings on grid-like activity in entorhinal cortex. The current paper seems quite similar conceptually and in design to previous work, most notably Park et al., 2021, Nature Neuroscience.

(1) The authors claim that this study provides evidence that humans use a spatial / grid code for abstract knowledge like social knowledge.

This data does specifically not add anything new to this argument. As with almost all studies that test for a grid code in a similar "conceptual" space (not only the current study), the problem is that, when the space is not a uniform, square/circular space, and 2-dimensional then there is no reason the code will be perfectly grid like, i.e., show six-fold symmetry. In real world scenarios of social space (as well as navigation, semantic concepts), it must be higher dimensional - or at least more than two dimensional. It is unclear if this generalizes to larger spaces where not all part of the space is relevant. Modelling work from Tim Behrens' lab (e.g., Whittington et al., 2020) and Bradley Love's lab (e.g., Mok & Love, 2019) have shown/argued this to be the case. In experimental work, like in mazes from the Mosers' labs (e.g., Derdikman et al., 2009), or trapezoid environments from the O'Keefe lab (Krupic et al., 2015), there are distortions in mEC cells, and would not pass as grid cells in terms of the six-fold symmetry criterion.

The authors briefly discuss the limitations of this at the very end but do not really say how this speaks to the goal of their study and the claim that social space or knowledge is organized as a grid code and if it is in fact used in the brain in their study and beyond. This issue deserves to be discussed in more depth, possibly referring to prior work that addressed this, and raise the issue for future work to address the problem - or if the authors think it is a problem at all.

Author Response

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

We wish to thank the reviewers for their helpful insightful comments. Their concerns were mainly related to the interpretation of the data, help in clarifying our statements and improving our discussion.

Reviewer #1 (Recommendations For The Authors):

This is a very interesting study It involves the utilization of hippocampal neuronal cultures from syntaxin 1 knock-out mice. These cultures serve as a platform for monitoring changes in synaptic transmission through electrophysiological recording of postsynaptic currents, upon lentiviral infection with various isoforms, chimeras, and point mutations of syntaxins.

The authors observe the following:

(1) Syntaxin2 restores neuronal viability and can partially rescue Ca2+-evoked release in syntaxin1 knock-out neurons that it is much slower (cumulative charge transfer differences) and with a clearly smaller RRP than when rescued with syntaxin1. In contrast, syntaxin2-mediated rescue leads to a high increase in spontaneous release (Figure 1). Convincingly, the authors conclude that syntaxin 1 is optimized for fast phasic release and for clamping of spontaneous release, in comparison with syntaxin2.

(2) The replacement of the SNARE domain (or its C-terminal part) of syntaxin1 by the SNARE domain of syntaxin2 (or its C-terminal part) rescues the fast kinetics, but not the amplitude, of Ca2+-evoked release. This is associated with a decrease in the size of the RRP and an increase in spontaneous release. The probability of vesicular release (PVR) is a little bit increased, which is intriguing because a little decrease would be expected instead according to the reduced RRP, indicating that an enhancement of Ca2-dependent fusion is occurring at the same time by unknown mechanisms as the authors properly point out. The replacement of the Analogous experiments in which the SNARE domain of syntaxin1 is replaced into syntaxin2, reveals the exitance of differential regulatory elements outside the SNARE domain.

(3) Different constructs of syntaxin 1 and syntaxin 2 display different expression levels. On the other hand, the expression levels of Munc-18 are associated with the characteristics of the transfected specific syntaxin construct. In any case, the electrophysiological phenotypes cannot be consistently explained by changes in Munc-18.

(4) Mutations in several residues of the outer surface of the C-terminal half of the syntaxin1 SNARE domain lead to alterations in the RRP and the frequency of spontaneous release, but the changes cannot attributed to a change in the net surface charge, because the alterations occur even in paired mutations in which electrical neutrality is conserved.

Comments:

(1) This is a comment regarding the interpretation of the results. In general, the decrease in the RRP size is associated with the increased frequency of spontaneous release due to unclamping. The authors claim that both phenomena seem to be independent of each other. In any case, how can the authors discard the possibility that the unclamping of spontaneous release leads to a decrease in the RRP size?

The main argument against the reduction of the RRP being caused by the observed increase in the mEPSC frequency is based on kinetics of refilling and depletion. The average time a vesicle fuses spontaneously after it becomes primed is 500 – 1000 seconds (spontaneous vesicle release rate – STX1 Figure 1, Figure 2 and Figure 3). The time it takes to refill the RRP after depletion is in the order of 3 seconds (Rosenmund and Stevens, 1996). Therefore, the refilling of the RRP is more than 100 times faster. Even when the spontaneous release would increase 5 fold, this would lead to less than 5 % of the steady state depletion of the RRP.

(2) The authors have analyzed the kinetics of mEPSCs and found differences (Fig2-Supp. Fig1; Fig2-Supp. Fig1). It would be interesting and pertinent to discuss these data in the context of potential phenotypes in the fusion pore kinetics involving syntaxin1 and syntaxin2 and their SNARE domains. Indeed, the figure will improve by including averaged traces of mEPSCs.

We thank the reviewer for the idea. Upon closer examination of the changes in mEPSC rise time and mEPSC decay time we noticed a minor slowing in the mEPSC rise time from 0.443ms (SEM0.0067) of STX1A to 0.535ms (SEM0.0151) for STX1A-2(SNARE) or 0.507ms (SEM0.01251) for STX1A-2(Cter), while the mEPSC half widths did not change significantly. It is possible that the measured change is related to the detection algorithm as mEPSC detection at elevated frequencies becomes more difficult due to increased overlap of event, and we therefore prefer to refrain from making any mechanistic claims.

Minor comments:

(1) Fig2 J; Fig 3 J. It is difficult to distinguish between different colors and implementing a legend within the graph will be very helpful.

(2) Fig3 H. Please change the color of the box plot for Stx1 A to improve the contrast with the individual data points.

(3) Page 6. Line 225. "Figure 2D and E" should be corrected to "Figure 2C and D"

(1) Colors were changed for clearer visualization. (2) Unfortunately, changing the color did not improve the contrast with the individual plots. However, the numerical data is all included in the data sheets of the corresponding figure. (3) The mistake was corrected.

Reviewer #2 (Recommendations For The Authors):

Line 135-136: Are cited numbers cited in the text mean and SEM? Please indicate.

Line 139 and Figure 1G: The difference between purple and blue was very hard to see on my hard copy.

Line 152: Reference to Figure 1L should probably be 1K.

Line 183: Reference to Figure 2C should probably be Figure 2F.

Line 225: Reference to Figure 2D and 2E should probably be 2C and 2D.

Line 239: Reference to Figure 3I should probably be 3H.

All typos were addressed and colors were changed for better visualization.

Line 210-211: Sentence ("One of the benefits..") is hard to understand.

Thank you for noticing this mistake, agreeably the the sentence did not add any important or new information and so it was deleted. Additionally, the message of the mentioned sentence was already clearly stated in lines 209-211.

Figure 4E-H misses data for STX2, for the figure to be arranged like Figure 5.

Given that STX1 is the endogenous syntaxin in hippocampal neurons, we use it at a control for all the analysis done in STX2 and STX2-chimera experimental groups, thus it is included in Figure 3 and 5.

It appears that the authors do not present or discuss the Western Blot in Fig. 4D. Are the quantitative results of the Western Blot consistent with or different from the quantification of the immunostainings (Fig. 4B-C)? A similar question for Figure 5D, which also seems not to be presented.

In terms of quantification, we have relied mainly on the ICC experiments because they test also for putative impairments in transport to the presynaptic compartment. Our WB data are overall consistent with the results, but were not used to quantitate expression of our syntaxin chimeras and mutations in the STX1-null hippocampal neuron model.

Figure 6F-G: The normalization of spontaneous vesicular release rates is not clear, because the vesicular release rates already contain a normalization (mEPSC rate divided by RRP size). Is a further normalization of the STX1A condition informative? The authors should consider presenting the release rates themselves. In any case, the normalization should be presented/explained, at least in the legends.

The reviewer is in principle correct. Due to the large number of experimental groups we had to perform recordings from multiple cultures, where not all experimental groups were present, while the WT STX1 was present as a consistent control. The reduce culture to culture variability, additional normalization to the WT control group was performed. However, we also included the raw data numerical values in the data-source sheets (Normalized and absolute), which produce a similar overall outcome.

References to Figure 7 subpanels (A, B, and C) are missing.

Thank you for the comment. We have integrated all panels into one for better representation and understanding since they are representative of one another.

Lines 330-339 and Figure 7 in Discussion: the authors discuss that adding the non-cognate STX2 SNARE-domain to syntaxin-1 might destabilize the primed state and decrease the fusion energy barrier (as indicated in Figure 7C). What is the evidence that the decrease in RRP size is not caused solely by the depletion of the pool due to the increased spontaneous fusion?

Please see the comments to major point 2 of reviewer 1.

Statistics: Missing is the number of observations (n) for all data. Even if all data points are displayed, this should be stated.

N numbers are included in the data sheets attached to each figure.

The statement (start of Discussion,) that the SNARE-domain of STX1 'plays a minimal role in the regulation for Ca2+-evoked release' is somewhat puzzling, since without the SNARE-domain in STX1 there would be no Ca2+-evoked release. I guess these statements (similar statements are found elsewhere) are due to the interesting finding that STX2 leads to a decrease in release kinetics, compared to STX1, and this is not (entirely) due to differences in the SNARE-domain. I would suggest rephrasing the finding in terms of release kinetics. Also, the statement in the last sentence of the Abstract is not clear.

Thank you for pointing this out and we agree that our experiments showed strong impact of the syntaxin isoform exchange on release kinetics and overall release output. A similar comment came also from reviewer #3 and so, we have addressed both comments as one.

Our confusing statement resulted from the order of the presented results and our summarizing remarks for each section. Our statement reflected our finding that mutating residues in the C-terminal part of the STX1 SNARE motif affected only spontaneous release and RRP size but not release efficacy. We now state (pg. 6 lines 231-233) that the data observed from the comparison of “the results obtained from the Ca2+-evoked release between STX1 and STX2 support major regulatory differences of the domains outside of the SNARE domain between isoforms”.

We have changed the abstract pg. 2 lines 55-56

We have changed the introduction pg. 3 lines 102-105 for a better contextualization.

We have changed the start of the discussion pg. 9 lines 250-252 for better contextualization.

Reviewer #3 (Recommendations For The Authors):

In this manuscript, Salazar-Lázaro et al. presented interesting data that C-terminal half of the Syx1 SNARE domain is responsible for clamping of spontaneous release, stabilizing RRP, and also Ca2+-evoked release. The authors routinely utilized the chimeric approach to replace the SNARE domain of Syx1 with its paralogue Syx2 and analyzed the neuronal activity through electrophysiology. The data are straightforward and fruitful. The conclusions are partly reasonable. One obvious drawback is that they did not explore the underlying mechanism. I think it is easy for the authors to carry out some simple assays to verify their hypothesis for the mechanism, instead of just talking about it in the discussion section. In all, I appreciate the data presented in the manuscript. If the authors could supply more data on the mechanisms, this would be important research in the field. Some critical comments are listed below:

We thank the reviewer for his/her comments and suggestions.

Major comments:

(1) In pg.3, lines 102-104, the authors stated that 'We found that the C-terminal half of the SNARE domain of STX1.. ..while it is minimally involved in the regulation of Ca2+-evoked release.' But in pg.5, lines 174-176, they wrote that 'Replacement of the full-SNARE domain (STX1A-2(SNARE)) or the C-terminal half (STX1A-2(Cter)) of the SNARE domain of STX1A with the same domain from STX2 resulted in a reduction in the EPSC amplitude (Figure 2B).' and in pg.5-6, lines 197-199, they wrote that 'Taken together our results suggest that the C-terminal half of the SNARE domain of STX1A is involved in the regulation of the efficacy of Ca2+-evoked release, the formation of the RRP and in the clamping of spontaneous release.' It puzzles me a lot as to what the authors are really trying to express for the relationship between C-half of the SNARE complex and Ca2+-evoked release (i.e., minimally involved or significantly participate in the process?). Please clarify and reorganize the contexts.

Please see our reply to the last comment of reviewer 2.

(2) Figure 1-figure supplement 1, the authors should analyze Syx1/VGlut1 level additionally. And, if possible, compare the difference between Syx1/VGlut1 and Syx2/VGlut1.

The levels of STX1/VGlut1 and STX2/VGlut1 were analyzed in detail in Figures 4 and 5.

The direct comparison between the expression levels of these two proteins is not possible since affinities of the antibodies to the target proteins are different and can induce potential biases. While this could be overcome by the use of a FLAG-tag to the syntaxin proteins, we have not utilized this approach in this publication. We in addition inferred sufficient and comparable expression of both syntaxins from their ability to rescue some of syntaxin1 loss of function phenotypes.

(3) Figure 2D only analyzed the EPSC half-width, could the author alternatively analyze the rise/decay time? Also, in Figure 3-figure supplement 1, does it refer to the kinetic parameters of Syx2-1A in Figure 3? It is very confused.

We have changed the text accordingly and each parameter is referenced to its corresponding figure for clarity. As for the decay and rise time of STX1 and STX1-chimeras, they are in Figure 2-figure supplement 1A and B.

(4) On pg.4, lines 151-152, 'Finally, no change was observed in the paired-pulse ratio (PPR) between STX1A and STX2 groups (Figure 1L).' does not contain any explanations and comments for this observation in the texts.

The small EPSC amplitudes and altered kinetics on the STX2 constricts (Figure 1 and Figure 3) have made it more difficult to quantitate paired pulse experiments. Therefore, we preferred not to overinterpret these measurements. The findings that the paired pulse data were not significantly different, fit with the vesicular release probability measurements which showed no major changes. We have made our statement on this basis.

(5) On pg.6, lines 235-236, the authors wrote that 'Additionally, we found that only STX2-1A(SNARE) and STX2-1A(Cter) could rescue the RRP to around double of what we measured from STX2 and STX2-1A(Nter) (figure 3F)'. However, in Figure 3F, the authors indicated 'n.s.' (p>0.05) for the differences between STX2 and STX2-1A(SNARE)/STX2-1A(Cter). It is perplexing how the authors interpret their data. Definitely, the p-value could not be arbitrarily used as a criterion of difference. An easier way is that indicating the exact p-values for each comparison (indicate in figure legends or list in tables).

We apologize for any confusion, and hope the modification gives more clarity in our interpretation. The calculated p-values are included in attached data source tables and hope this will provide clarity to our comparative analysis. We have changed the text in pg 7 lines 238-241 and are cautious to overinterpret these results and rely more on the data observed in STX1A-chimeras, which show significant changes in the RRP.

(6) I noticed that the authors preferred using 'xx% increase/decrease' or 'xx-fold increase/decrease' to interpret their inter-group data. I would doubt whether the interpretations are appropriate. First, it seems that most of the individual scatters from one set were not subject to Gaussian distribution; also, the authors utilized non-parameter tests to compare the differences. Second, the authors did not explicitly indicate the method to calculate the % or fold, e.g., by comparing mean value or median. I think it is a bad choice to use the median to calculate fold changes; meanwhile, the mean value would also be biased, given the fact that the data were not Gaussian-distributed. The authors should be cautious in interpreting their data.

We thank the reviewer for pointing the inaccuracy of our descriptions and have included the parameter used to calculated the percentage and fold increase/decrease in the materials and methods section. Specifically, the mean. Our intention is to plainly state the amount of change seen in a parameter based on the observed changes in the mean value. We agree with the reviewer that interpreting this could be problematic if we are speculating possible mechanisms. Further test should be conducted as to state whether similar increase/decrease changes in a parameter are due to the disturbance of the same mechanisms or different. E.g., we discussed whether the regulation of SYT1 might be or not be the mechanism affected in some of the chimeras that show an increase in the spontaneous release rate, for the release rate observed in some is massively higher than that seen in SYT1-KO (Bouazza-Arostegui et al., 2022). It is tempting to speculate that it could be due to other mechanisms based on the differences in the changes. For this reason, we have given an array of possible mechanisms affected when we manipulate the SNARE domain of STX1.

(7) The authors routinely analyzed the levels of Munc18-1 in neuronal lysates by WB and Munc18-1/VGlut1 by immunofluorescence in various Syx1 mutants. However, in my view, these assays were slightly indirect. It is evident that the SNARE domain of Syx1 participates in the binding to Munc18-1 according to the atomic structures (pdb entries: 3C98 and 7UDB). Meanwhile, Han et al. reported that K46E mutation (located in domain 1 of Munc18-1) strongly impairs Syx1 expression, Syx1-interaction, vesicle docking and secretion (Han et al., 2011, PMID: 21900502). Intriguingly, the residue K46 of Munc18-1, which is close to D231/R232 of Syx1, may have potential electrostatic contacts to D231 and R232 of Syx1. This is reminiscent of the possibility that Syx1D231/R232 and some Syx1-2 chimeras lost their normal function through their defective binding to Munc18-1.nmb, To better understand the underlying mechanism, the authors may need to carry out in vivo and/or in vitro binding analysis between syntaxin mutants/chimeras and Munc18-1. They also need to conduct more discussions about the issue.

We express our gratitude for the identification of a previously overlooked aspect in our investigation of the interplay between Munc18-1 and STX1. In response, we have incorporated additional discourse on this matter in pg11 lines 419-431.

Additionally, we appreciate the thoughtful suggestion regarding additional experiments to further explore the molecular relationship between Munc18-1 and STX1. We agree that co-immunoprecipitation experiments (either by using an antibody against Munc18-1 or STX1 and STX2) would offer greater insight into whether the binding of these proteins is affected in the isoform or the mutants. Notably, we performed immunoprecipitation experiments by using neuronal lysates of the corresponding groups and using STX1A and STX2 antibodies for the pull-downs. However, we were unable to co-IP Munc18-1 when doing so. Changing the conditions of the experiment did not yield better results and so these experiments remained inconclusive for the moment. For this reason, we included it as an open question and a potential concluding hypothesis of the molecular mechanism. However, Shi et al., 2021, have performed co-IP assays using Munc18-1-wt and a mutant form which affects the binding to the C-terminal half of the SNARE domain of STX, and STX1-wt and a STX mutants targeting some of our residues of interest and showed a decrease in the pulled-down levels of Munc18-1 using HeLa cells. We have made sure to mention the conclusion of this important publication in our discussion.

(8) The third possible mechanism (i.e., interaction with Syt1) proposed by the authors seems more reasonable. However, the discussions raised by the authors were not enough. For instance, plenty of literature has indicated that Syt1 may participate in synaptic vesicle priming through stabilizing partially or fully assembled SNARE complex (Li et al., 2017, PMID: 28860966; Bacaj et al., 2015, PMID: 26437117; Mohrmann et al., 2013, PMID: 24005294; Wang et al., 2011; PMID: 22184197; Liu et al., 2009, PMID: 19515907); complexins are also SNARE binding modules that regulate synaptic exocytosis. Lack of complexins could lead to unclasping of spontaneous fusion of synaptic vesicles, though it causes severe Ca2+-triggered release at the same time (Maximov et al., 2009, PMID: 19164751). Meanwhile, different domains of complexin may accomplish different steps of SV fusion, early research had indicated that the C-terminal sequence of complexin is selectively required for clamping of spontaneous fusion and priming but not for Ca2+-triggered release (Kaeser-Woo et al., 2012, PMID: 22357870). Likewise, if possible, the authors may need to carry out in vivo and/or in vitro binding analysis to confirm their hypothesis.

The exploration of complexin´s involvement was limited in our study primarily due to our methodological focus on comprehending molecular mechanisms concerning the sequence disparities between STX1 and STX2. Our laboratory has studied the role of Complexin extensively, and we certainly have had a possible involvement in mind. However, since the sites identified on syntaxin are either conserved between STX1 and STX2 or not close to the central or accessory helical domains of complexin, we did not perform experiments to test putative interactions, and we refrained from discussing complexin in this paper.

(9) Lastly, I would suspect that whether the defects of Syx2 and Syx1 chimeras were caused by the SNARE complex itself, from another point of view that is different from the hypothesis raised by the authors. Changing the outward residues (or we say the solvent-accessible residues) of the SNARE complex may affect the stability, assembly kinetics, and energetics (Wang and Ma, 2022, PMID: 35810329; Zorman et al., 2014, PMID: 25180101), especially for the C-terminal halves. Is this another possible mechanism through which the C-terminus of Syx1 might contribute to SV priming and clamping of spontaneous release? The authors should at least conduct some discussions about the point.

Thank you for this suggestion. We indeed assumed that since the hydrophobic layers of the SNARE domains that form the hydrophobic pocket of STX2 and STX1 are mainly conserved, that the intrinsic stability of the SNARE complex is largely unchanged. Additionally, Li et al., (2022) PMID: 35810329 examined the stability of the alfa-helix structure of the SNARE domain of SNAP25. And while they found no changes in the stability and formation of the alfa-helix when mutating outwards-facing residues for methodological purposes (bimane-tryptophan quenching), their study did not selectively explore the effect of mutations of outer-surface residues on the stability of the alfa-helix.

Zorman et al., (2014) PMID: 25180101, as noted by the reviewer, observed that changes in the sequence of the SNARE domain (by using SNARE proteins from different trafficking systems (neuron, GLUT4, yeast…) correlated with changes in the step-wise SNARE complex assembly. However, they also did not selectively mutate the outer solvent-accessible residues, hindering conclusive speculations in the contribution of said residues on the kinetics and energetics of assembly and intrinsic stability of the SNARE complex.

Upon petition of the reviewer, we have added this paragraph to discuss an additional mechanism:

“As a final remark, it is possible that the changes in the spontaneous release rate and the priming stability may stem from a reduced stability of the SNARE complex itself through putative interactions between outer surface residues. Studies of the kinetics of assembly of the SNARE complex which mutate solvent-accessible residues in the C-terminal half of the SNARE domain of SYB2 have shown reduction in the stability of the SNARE complex assembly and are correlated with impaired fusion (Jiao et al., 2018). However, STX1 mutations of outward residues were inconclusive and were always accompanied by hydrophobic layer mutations (Jiao et al., 2018), which affect the assembly kinetics and energetics of the SNARE complex (Ma et al., 2015). Single molecule optical-tweezer studies have focused on the impact of regulatory molecules on the stability of assembly such as Munc18-1 (Ma et al., 2015; Jiao et al., 2018) and complexin (Hao et al., 2023), or on the intrinsic stability of the hydrophobic layers in the step-wise assembly of the SNARE complex (Gao et al., 2012; Ma et al., 2015; Zhang et al., 2017). Although the conserved hydrophobic layers in the SNARE domains of STX1A and STX2 (Figure 1) suggest unchanged zippering and intrinsic stability of the complex, further studies addressing the contribution of surface residues on the stability of the alfa-helix structure of the SNARE domain of STX1 (Li et al., 2022) or the stability of the SNARE complex should be conducted.”

Minor comments:

(1) In pg.6, line 236, 'figure 3F', the initial 'f' should be uppercased.

(3) On pg.11, line 396, the section title 'The interaction of the C-terminus of de SNARE domain of STX1A with Munc18-1 in the stabilization of the primed pool of vesicles.' The word 'de' is confusing, please check.

(4) In pg.12, line 446, the section title, should 'though' be 'through'?

These comments have been acknowledged and changed. Thank you

(2) In pg.7, line 239, '..had an increased PVR (Figure 3G), no change in the release rate (Figure 3I)', should Figure 3I be Figure 3H? and line 240, 'and an increase in short-term depression during 10Hz train stimulation (Figure 3I)', should Figure 3I be Figure 3J? If so, Figure 3I will not be cited in the texts and lack adequate interpretations. Please check.

We apologize for the oversight in not referencing this specific subpanel of the figure and have incorporated the reference in the text. Additionally, our interpretation of this data is connected to the mechanisms that govern efficacy of Ca2+-evoked response, and its dependence on the integrity of the entire-SNARE domain. We wish to highlight the modifications made to the discussion on the regulation of the Ca2+-evoked response based on previous reviewer comment #1, and a similar comment from reviewer #2 (as stated previously).

eLife assessment

This important study presents a series of results to uncover the role of C-terminal half of the Syx1 SNARE domain. The evidence supporting the conclusions is convincing. The paper will be of broad interest to biophysicists and neurobiologists.

Reviewer #1 (Public Review):

In this systematic and elegant structure-function analysis study, the authors delve into the intricate involvement of syntaxin 1 in various pivotal stages of synaptic vesicle priming and fusion. The authors use an original and fruitful approach based on the side-by-side comparison of the specific contributions of the two isoforms syntaxin 1 and syntaxin 2, and their respective SNARE domains, in priming, spontaneous and Ca2+-dependent glutamate release. The experimental approach, mastered by the authors, offers an ideal means of unraveling the molecular roles played by syntaxins. Although it is not easy to come up with a model explaining all the observed phenotypes, the authors carefully restrict their conclusions to the role of the C-terminal half of the syntaxin1 C-terminal SNARE domain in the maintenance of the RRP and the clamping of neurotransmitter release. The study is carefully carried out, the conclusions are supported by high quality data and the manuscript is clearly written. In addition, the study clearly set new questions than open new paths for future experimental work.

Reviewer #2 (Public Review):

Summary:<br /> The manuscript by Salazar-Lázaro et al. systematically dissects out the different functional properties of the SNARE-domains of syntaxin-1 and syntaxin-2. By systematically substituting the SNARE-domain (or its C- or N-terminal half) into the non-cognate counterpart, the authors find that the C-terminal half of the SNARE-complex is especially important for maintaining RRP size and clamping spontaneous release. They also mutate single residues, to further nail down the effect. Overall, this is an interesting manuscript, which sheds light on the functionality of different co-expressed SNARES.

Strengths:<br /> The strength of the manuscript is the systematic dissection, using substitution of either SNARE-domain into the other syntaxin, together with the state-of-the art methods. The authors follow up with a substitution of single and paired residues. This is a large undertaking, which has been very well carried out.

Weaknesses:<br /> No major weaknesses. The large number of experiments paint a somewhat complicated picture because the process under study is complicated.

Reviewer #3 (Public Review):

Summary:<br /> In this manuscript, Salazar-Lázaro et al. presented interesting data that C-terminal half of the Syx1 SNARE domain is responsible for clamping of spontaneous release, stabilizing RRP, and also Ca2+-evoked release. The authors routinely utilized the chimeric approach to replace the SNARE domain of Syx1 with its paralogue Syx2 and analyzed the neuronal activity through electrophysiology. The data are straightforward and fruitful. The conclusions are reasonable.

Strengths:<br /> The electrophysiology data that illustrate the important functions of Syx1 in clamping of spontaneous release, stabilizing RRP, and also Ca2+-evoked release were clear and convincing.

Weaknesses:<br /> One weakness is that the authors did not go deep into the underlying molecular mechanisms experimentally, either because of a variety of complicated possibilities or limited space of the manuscript.

Author Response

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

Public reviews

Reviewer 1 (Public Review):

Summary:

The authors set out to clarify the molecular mechanism of endocytosis (re-uptake) of synaptic vesicle (SV) membrane in the presynaptic terminal following release. They have examined the role of presynaptic actin, and of the actin regulatory proteins diaphanous-related formins (mDia1/3), and Rho and Rac GTPases in controlling the endocytosis. They successfully show that presynaptic membrane-associated actin is required for normal SV endocytosis in the presynaptic terminal and that the rate of endocytosis is increased by activation of mDia1/3. They show that RhoA activity and Rac1 activity act in a partially redundant and synergistic fashion together with mDia1/3 to regulate the rate of SV endocytosis. The work adds substantially to our understanding of the molecular mechanisms of SV endocytosis in the presynaptic terminal.

Strengths:

The authors use state-of-the-art optical recording of presynaptic endocytosis in primary hippocampal neurons, combined with well-executed genetic and pharmacological perturbations to document effects of alteration of actin polymerization on the rate of SV endocytosis. They show that removal of the short amino-terminal portion of mDia1 that associates with the membrane interrupts the association of mDia1 with membrane actin in the presynaptic terminal. They then use a wide variety of controlled perturbations, including genetic modification of the amount of mDia1/3 by knock-down and knockout, combined with inhibition of activity of RhoA and Rac1 by pharmacological agents, to document the quantitative importance of each agent and their synergistic relationship in regulation of endocytosis.<br /> The analysis is augmented by ultrastructural analyses that demonstrate the quantitative changes in numbers of synaptic vesicles and in uncoated membrane invaginations that are predicted by the optical recordings.

The manuscript is well-written and the data are clearly explained. Statistical analysis of the data is strengthened by the very large number of data points analyzed for each experiment.

Weaknesses:

There are no major weaknesses. The optical images as first presented are small and it is recommended that the authors provide larger, higher-resolution images.

Response: We thank the referee for these highly positive remarks. In response, we now provide larger, high-resolution images as requested.

Reviewer 2 (Public Review):

Summary:

This manuscript expands on previous work from the Haucke group which demonstrated the role of formins in synaptic vesicle endocytosis. The techniques used to address the research question are state-of-the-art. As stated above there is a significant advance in knowledge, with particular respect to Rho/Rac signalling.

Strengths:

The major strength of the work was to reveal new information regarding the control of both presynaptic actin dynamics and synaptic vesicle endocytosis via Rho/Rac cascades. In addition, there was further mechanistic insight regarding the specific function of mDia1/3. The methods used were state-of-theart.

Weaknesses:

There are a number of instances where the conclusions drawn are not supported by the submitted data, or further work is required to confirm these conclusions.

Response: We thank the referee for his/ her thorough reading of the manuscript and the thoughtful comments and questions. We have conducted additional experiments and made textual change to our manuscript to address these points and to further strengthen the conclusions as detailed in our response to the recommendations for authors.

Recommendations for the authors

Reviewer 1 (Recommendations For The Authors):

Most of the figures contain images that are too small to be easily interpreted because the resolution is degraded when they are enlarged in the PDF file. The authors should redesign the figures so that the letters marking each panel are smaller, and the size of each data panel is much larger (at least twice as large with increased resolution). There is, at present, a great deal of white space in most of the figures that should be reduced to make room for larger, higher-resolution images. Larger fonts should be used for annotations of the images so that they are easier to read. The data appears to be very high quality, but it is presented at a size and resolution that don't do it justice.

Response: We thank the referee for his/ her helpful comments. In response to the referee’s comment, we have carefully re-arranged all figures and now provide larger, high-resolution images.

Reviewer 2 (Recommendations For The Authors):

Major points

(1) Figure 1 - While there is a rationale for employing a cocktail of drugs to interfere with actin dynamics, it would be highly informative to determine the effect of these modulators in isolation. This is important, since in their previous publication (Soykan et al Neuron 2017 93:854) the authors demonstrated that latrunculin had no effect, while jasplakinolide accelerated endocytosis of originating purely from Y-27362 and ROCK kinase inhibition, rather than destabilisation/stabilisation of actin. It will be key to dissect this by examining the effect on endocytosis of both 1) a cocktail of latrunculin/jasplakinolide and 2) Y-27362 alone.

Response: We thank the referee for highlighting this interesting point. We have now experimentally addressed the effect of latrunculin (L), jasplakinolide (J) and the ROCK inhibitor Y-27362 (Y) either alone or in combination on the kinetics of synaptic vesicle (SV) endocytosis(new Fig. 1-Supplement 1C,D). We now demonstrate that application of the ROCK inhibitor Y-27362 or the combination of latrunculin (L) and jasplakinolide (J) have no effect on Syph-pH endocytosis. Combined use of jasplakinolide (J) and the ROCK inhibitor Y-27362 (Y) has a small phenotype. In contrast, a mix of all three inhibitors (JYL) potently impairs endocytosis kinetics at hippocampal synapses. These data demonstrate that actin dynamics are required for SV endocytosis, while ROCK inhibition alone does not appear to impair endocytosis kinetics. We note that our data are in line with a study by Ann Saal et al (2020) who reported a lack of effect of ROCK inhibition on the kinetics of Synaptotagmin1-CypHer retrieval.

(2) Figure 1 - There are clear effects on the retrieval of pHluorin reporters and also endogenous vGAT in the presence of disruptors of actin function. However, there was no assessment of the impact of these interventions on either neurotransmitter release or SV fusion (with the exception of 1 condition with one stimulus train (Fig S1D), and the effect of Rac modulation in Fig S6F). As quoted by the authors, previous studies using knockout of beta- or gamma-actin have shown a profound effect on these parameters in hippocampal neurons, which has the potential to impact the speed and extent of compensatory endocytosis. The authors will already have this data from the use of the two reporters (pHluorn and GAT-cypHer), and it is important to include this to allow interpretation of the effect on endocytosis observed.

Response: We agree with the referee that this is an important point that we have tackled experimentally using vGAT-CypHer and synapto-pHluorin responses as measures. In the new Fig. 1-Supplement 1, Fig. 5- Supplement 1, and Fig.6 -Supplement 1 of our revised manuscript, we show that SV exocytosis is largely unaffected by any of the applied manipulations of actin function.<br /> Specifically, we have added surface normalized data as a surrogate measure for exocytosis for the following:

• JLY treatment monitored by Syph-pH (Figure 1-Supplement 1A) and vGAT-CypHer (Figure 1-Supplement 1B),

• shCTR/shmDia1 (transfected) assayed via Syph-pH (Figure 1-Supplement 1G),

• shCTR/shmDia1/shmDia1+3 assayed via vGLUT1-pH (40AP: Figure 1-Supplement 1J; 80AP: Figure 1-Supplement 1L),

• shCTR/shmDia1+3 (transduced) assayed by vGAT-CypHer (Figure 1-Supplement 1M),

• IMM treatment monitored by vGLUT1-pH (Figure 1-Supplement 1O),

• RhoA/B WT/DN overexpression monitored by Syph-pH (Figure 5-Supplement 1B),

• shCTR/shRhoA+B (transfected) monitored via Syph-pH (Figure 5-Supplement 1D),

• shCTR/shmDia1+3 +/- EHT 1864 (Rac Inhibitor) assayed by vGAT-CypHer (Figure 6-Supplement 1D),

• shCTR/shmDia1+3 +/- Rac1-CA/DN assayed by Syph-pH (Figure 6-Supplement 1F).

The lack of effect of these manipulations on exocytic SV fusion is thus distinct from the effects of complete abrogation of actin expression in beta- or gamma-actin knockout studies reported by the LingGang Wu laboratory (Neuron 2016) as the referee also noted.

(3) Figure 3H, 3K, 4C, 4F - It is unclear how the values on the Y-axis were calculated. Regardless, to confirm that there is a specific increase in presynaptic mDia1/actin, the equivalent values for Homer/mDia1 should be presented (with Basson/Homer as a negative control). Without this, it is difficult to argue for a specific enrichment of mDia1/actin at the presynapse. The CRISPR experiments help with this interpretation (Fig 4G-I), however, inclusion of the Homer/mDia1 STED data would strengthen it greatly.

Response: We apologize if the description has been unclear. We essentially have followed the same type of analysis as recently described by Bolz et al (2023). In brief, the rationale for quantifying presynaptic protein levels of interests is as follows: The presynaptic area was defined by the normalized distribution curve of Bassoon, i.e. area between 151.37 and -37.84 nm as marked by purple shading with a cutoff set where Bassoon and Homer1 distributions overlap (-37.84 nm) as shown in Figure 3Supplement 1H (pasted below). The individual synaptic line profiles, e.g. of mDia1 were integrated to yield presynaptic (between 151.37 and -37.84 nm (purple in the graph) vs. postsynaptic levels (from - 56.76 to -245.97 nm (green shaded area). new Figure 3-Supplement 1H-J

Author response image 1.

Based on this analysis postsynaptic mDia1 levels were also elevated upon Dynasore treatment (new Figure 3-Supplement 1I). In spite of this and consistent with the fact that the majority of mDia1 is localized at the presynapse, we found that postsynaptic F-actin levels were unchanged in mDia1/3depleted neurons (p = 0.0966; One sample t-test) (new Figure 4-Supplement 1E,F). new Figure 4 – Supplement 1E,F

Author response image 2.

Moreover, we also conducted further analysis with respect to possible effects of Dynasore on synaptic architecture in general. Neither presynaptic Bassoon nor postsynaptic Homer1 levels were significantly altered by Dynasore treatment (new Figure 3–Supplement 1J).

(4) Figure 4J - The rescue of the pHlourin response by jasplakinolide is difficult to interpret when considering previous work from the same authors. In their 2017 publication (Soykan et al Neuron 2017 93:854), they revealed that the drug accelerated the pHluorin response, whereas now they demonstrate no effect in the control condition. If the drug does accelerate endocytosis, then it may be working via a different mechanism to restore endocytosis in mDia1/3 knockdown neurons.

Response: The referee is correct. The very mild acceleration of endocytosis in the presence of jasplakinolide can be observed using synaptophysin-pHluorin as a reporter under moderate mediumfrequency stimulation at 10Hz for 5 s (i.e. 50 APs). In the present dataset using a different pHluorin reporter (i.e. vGLUT1-pHluorin) that tends to yield faster endocytic responses (as noted before by the Ryan lab) and using a high frequency stimulus (20Hz) we fail to observe a significant effect. While this cannot be excluded, we would be reluctant to conclude that these differences indicate distinct mechanisms of jasplakinolide action. Alternatively, actin may be of particular importance under conditions of high-frequency stimulation.

In this regard, the conclusions from the pHluorin experiment would be greatly strengthened by demonstrating that jasplakinolide corrects the reduction of presynaptic actin in mDia1/3 knockdown synapses observed in figures 4E-I.

Response: As demonstrated in Figure 4-Supplement 1G and in support of a common mechanism of action, we find that application of jasplakinolide rescues reduced presynaptic actin levels in mDia1/3depleted neurons. The respective data for presynaptic actin (normalized to shCTR + DMSO set to 100) are: shCTR + DMSO = 100 ± 6.3; shmDia1+3 + DMSO = 47.7 ± 4.3; shCTR + Jasp = 150.6 ± 11.9; shmDia1+3 + Jasp = 94.3 ± 11.5. These data are now also quoted in the revised manuscript text.

Minor points

(1) There is no rationale provided regarding why different stimulation protocols are sometimes used in the pHluorin/cypHer experiments. In most cases it is 200 APs (40 Hz), however, in some cases, it is 40 APs or 80 APs. Can the authors explain why they used these different protocols?

Response: The referee noted this correctly. This in part reflects the history of the project, in which initial datasets were acquired using 200 AP trains using pHluorin reporters. To probe whether the phenotypic effects induced by actin perturbations, were robust over different stimulation paradigms and optical reporters, additional data using either 40 or 80 AP trains as well as experiments capitalizing on vGLUT1 or endogenous vGAT monitiored by pH-sensitive cypHer-labeled antibodies were conducted. We hope the referee agrees that these additional data add to the general importance of our study.

(2) Figure 2 - The reduction in SV density in mDia1/3 knockdown neurons correlates with the results in Figures 1 and 7. However, a functional consequence of this reduction (change in size of RRP or neurotransmitter release, as stated above) would have increased the impact of these experiments.

Response: We agree with the referee and will address this interesting possibility using electrophysiolgical recordings in future studies.

(3) It appears the experimental n in Figure 2 is profiles, rather than experiments. This should be clarified, especially since there is no reference to how many times the experiments in Fig2E-G were performed.

Response: This point has been clarified in the revised figure legend.

(4) Figure 6 - The authors state that inhibition of Rac function either via a dominant negative mutant or an inhibitor increases the inhibition of endocytosis via knockdown of mDia1/3. However, both interventions inhibit endocytosis themselves in the control condition. It would be informative to see the full statistical analysis of this data since there does not appear to be a significant additive effect when comparing Rac inhibition with the additional knockdown of mDia1/3.

Response: In our revised manuscript, we now provide the full statistical analysis in the revised Source Data Table for Figures 6G,H. We observe that Rac1-DN expression indeed further aggravates phenotypes elicited by depletion of mDia1+3, but not vice versa. We have modified the corresponding section in the results section of our revised manuscript accordingly.

(5) Figure 7 - The increase in endosomes in mDia1/3 knockdown neurons is consistent with previous studies examining pharmacological inhibition of formins (Soykan et al Neuron 2017 93:854). However, it is noted that these structures were absent in the images shown in Figure 2. Similar to the previous point in figure 6, a full reporting of the significance of different conditions is important here, since it appears that the only difference between EHT1864 and its co-incubation with mDia1/3 knockdown neurons is in the number of ELVs (Fig 7H).

Response: Similar to the example EM images shown in Figure 7, enlarged endocytic structures are also observed in shmDia1+3 depleted synapses shown in Figure 2. However, ELVs and membrane invaginations were not color-coded as the focus in figure 2 is on the reduction of the SV pool. To better illustrate this, we have chosen a more representative example of this phenotype in revised Figure 2.

Moreover, we now provide the full statistical analysis of EM phenotypes in the revised Source Data Table for Figure 7. We find that Rac1 inhibition indeed significantly aggravates the effects of mDia1+3 loss with respect to the accumulation of membrane invaginations, while the effect on ELVs remains insignificant. However, accumulation of ELVs in the presence of the Rac1 inhibitor EHT1864 is further aggravated upon depletion of mDia1+3. We have modified the corresponding section in the results section of our revised manuscript accordingly.

We speculate that Rac1 may thus predominantly act at the plasma membrane, whereas mDia1/3 may serve additional functions in SV reformation at the level of ELVs. Clearly, further studies would be needed to test this idea in the future.

eLife assessment

This manuscript provides convincing evidence for the involvement of membrane actin, and its regulatory proteins, mDia1/3, RhoA, and Rac1 in the mechanism of synaptic vesicle re-uptake (endocytosis). These important data fill a gap in the understanding of how the regulation of actin dynamics and endocytosis are linked. The manuscript will be of interest to all scientists working on cellular trafficking and membrane remodeling.

Reviewer 1 Public Review:

Summary:

The authors set out to clarify the molecular mechanism of endocytosis (re-uptake) of synaptic vesicle (SV) membrane in the presynaptic terminal following release. They have examined the role of presynaptic actin, and of the actin regulatory proteins diaphanous-related formins ( mDia1/3), and Rho and Rac GTPases in controlling the endocytosis. They successfully show that presynaptic membrane-associated actin is required for normal SV endocytosis in the presynaptic terminal, and that the rate of endocytosis is increased by activation of mDia1/3. They show that RhoA activity and Rac1 activity act in a partially redundant and synergistic fashion together with mDia1/3 to regulate the rate of SV endocytosis. The work adds substantially to our understanding of the molecular mechanisms of SV endocytosis in the presynaptic terminal.

Strengths:

The authors use state-of-the-art optical recording of presynaptic endocytosis in primary hippocampal neurons, combined with well-executed genetic and pharmacological perturbations to document effects of alteration of actin polymerization on the rate of SV endocytosis. They show that removal of the short amino-terminal portion of mDia1 that associates with the membrane interrupts the association of mDia1 with membrane actin in the presynaptic terminal. They then use a wide variety of controlled perturbations, including genetic modification of the amount of mDia1/3 by knock-down and knockout, combined with inhibition of activity of RhoA and Rac1 by pharmacological agents, to document the quantitative importance of each agent, and their synergistic relationship in regulation of endocytosis.

The analysis is augmented by ultrastructural analyses that demonstrate the quantitative changes in numbers of synaptic vesicles and in uncoated membrane invaginations that are predicted by the optical recordings.<br /> The manuscript is well-written and the data are clearly explained. Statistical analysis of the data is strengthened by the very large number of data points analyzed for each experiment.

Weaknesses:

There are no major weaknesses.

Reviewer 2 Public Review:

Summary:

This manuscript expands previous work from the Haucke group which demonstrated the role of formins in synaptic vesicle endocytosis. The techniques used to address the research question are state-of-the-art. As stated above there is a significant advance in knowledge, with particular respect to Rho/Rac signalling.

Strengths:

The major strength of the work was to reveal new information regarding the control of both presynaptic actin dynamics and synaptic vesicle endocytosis via Rho/Rac cascades. In addition, there was further mechanistic insight regarding the specific function of mDia1/3. The methods used were state-of-the-art.

Weaknesses:

There are no major weaknesses.

Author Response

We thank all three Reviewers and the editors for the time and effort they put in reading and critiquing the manuscript. Our revised manuscript includes new data and analyses that address the original concerns. These include, 1) a new Supplemental Figure characterizing Cre expression and cellular phenotypes in the hippocampus, 2) new tables that give a more comprehensive picture of the EEG recordings and statistical analyses, 3) addition of whole cell electrophysiology data, and 4) rewriting to ensure that we do not state that either mTORC1 or mTORC2 hyperactivation is sufficient to cause epilepsy. We discuss the issue of statistical power to detect reduction in generalized seizure rate in the responses below. These suggestions and additions have improved the paper and we hope they will raise both significance and strength of support for the conclusions.

Reviewer #1 (Public Review):

Hyperactivation of mTOR signaling causes epilepsy. It has long been assumed that this occurs through overactivation of mTORC1, since treatment with the mTORC1 inhibitor rapamycin suppresses seizures in multiple animal models. However, the recent finding that genetic inhibition of mTORC1 via Raptor deletion did not stop seizures while inhibition of mTORC2 did, challenged this view (Chen et al, Nat Med, 2019). In the present study, the authors tested whether mTORC1 or mTORC2 inhibition alone was sufficient to block the disease phenotypes in a model of somatic Pten loss-of-function (a negative regulator of mTOR). They found that inactivation of either mTORC1 or mTORC2 alone normalized brain pathology but did not prevent seizures, whereas dual inactivation of mTORC1 and mTORC2 prevented seizures. As the functions of mTORC1 versus mTORC2 in epilepsy remain unclear, this study provides important insight into the roles of mTORC1 and mTORC2 in epilepsy caused by Pten loss and adds to the emerging body of evidence supporting a role for both complexes in the disease development.

Strengths:

The animal models and the experimental design employed in this study allow for a direct comparison between the effects of mTORC1, mTORC2, and mTORC1/mTORC2 inactivation (i.e., same animal background, same strategy and timing of gene inactivation, same brain region, etc.). Additionally, the conclusions on brain epileptic activity are supported by analysis of multiple EEG parameters, including seizure frequencies, sharp wave discharges, interictal spiking, and total power analyses.

Weaknesses:

(1) The sample size of the study is small and does not allow for the assessment of whether mTORC1 or mTORC2 inactivation reduces seizure frequency or incidence. This is a limitation of the study.

We agree that this is a minor limitation of the present study, however, for several reasons we decided not to pursue this question by increasing the number of animals. First, we performed a power analysis of the existing data. This analysis showed that we would need to use 89 animals per group to detect a significant difference (0.8 Power, p= 0.05, Mann-Whitney test) in the frequency of generalized seizures in the Pten-Raptor group and 31 animals per group in the Pten-Rictor group versus Pten alone. It is simply not feasible to perform video-EEG monitoring on this many animals for a single study. Second, even if we did do enough experiments to detect a reduction in seizure frequency, it is clear that neither Rptor nor Rictor deletion provides the kind normalization in brain activity that we seek in a targeted treatment. Both Pten-Rptor and Pten-Rictor animals still have very frequent spike-wave events (Fig. 3D) and highly abnormal interictal EEGs (Fig. 4), suggesting that even if generalized seizures were reduced, epileptic brain activity persists. This is in contrast to the triple KO animals, which have no increase in SWD above control level and very normal interictal EEG.

(2) The authors describe that they inactivated mTORC1 and mTORC2 in a new model of somatic Pten loss-of-function in the cortex. This is slightly misleading since Cre expression was found both in the cortex and the underlying hippocampus, as shown in Figure 1. Throughout the manuscript, they provide supporting histological data from the cortex. However, since Pten loss-of-function in the hippocampus can lead to hippocampal overgrowth and seizures, data showing the impact of the genetic rescue in the hippocampus would further strengthen the claim that neither mTORC1 nor mTORC2 inactivation prevents seizures.

Thank you for pointing out this issue. Cre expression was observed in both the cortex and the dorsal hippocampus in most animals, and we agree that differences in cortical versus hippocampal mTOR signaling could have differential contributions to epilepsy. We initially focused our studies on the cortex because spike-and-wave discharge, the most frequent and fully penetrant EEG phenotype in our model, is associated with cortical dysfunction. In our revised submission we have included a new Figure that quantifies Cre expression in the hippocampal subfields, as well as pS6, pAkt and soma size. These new data show that the amount of Cre expression in the hippocampus is not related to the occurrence of generalized seizures. The pattern of cell size changes in hippocampal neurons is the same as observed in cortical neurons. The levels of pS6 and pAkt are not much changed in the hippocampus, likely due to the sparse Cre expression there. We interpret these findings as supporting the conclusion that the reason we do not see seizure prevention by mTORC1 or mTORC2 inactivation is not due to hippocampal-specific dysfunction.

(3)Some of the methods for the EEG seizure analysis are unclear. The authors describe that for control and Pten-Raptor-Rictor LOF animals, all 10-second epochs in which signal amplitude exceeded 400 μV at two time-points at least 1 second apart were manually reviewed, whereas, for the Pten LOF, Pten-Raptor LOF, and Pten-Rictor LOF animals, at least 100 of the highest- amplitude traces were manually reviewed. Does this mean that not all flagged epochs were reviewed? This could potentially lead to missed seizures.

We reviewed at least 48 hours of data from each animal manually. All seizures that were identified during manual review were also identified by the automated detection program. It is possible but unlikely that there are missed seizures in the remaining data. We have added these details to the Methods of the revised submission.

(4) Additionally, the inclusion of how many consecutive hours were recorded among the ~150 hours of recording per animal would help readers with the interpretation of the data.

Thank you for this recommendation. Our revised submission includes a table with more information about the EEG recordings in the revised version of the manuscript. The number of consecutive hours recorded varied because the wireless system depends on battery life, which was inconsistent, but each animal was recorded for at least 48 consecutive hours on at least two occasions.

(5) Finally, it is surprising that mTORC2 inactivation completely rescued cortical thickness since such pathological phenotypes are thought to be conserved down the mTORC1 pathway. Additional comments on these findings in the Discussion would be interesting and useful to the readers.

We agree that the relationship between mTORC2, cortical thickness, and growth in general is an interesting topic with conflicting results in the literature. We didn’t add anything to the Discussion along these lines because we are up against word limits, but comment here that soma size was increased 120% by Pten inactivation and partially normalized to a 60% increase from Controls by mTORC2 inactivation (Fig. 2C). We and others have previously shown that mTORC2 inactivation (Rictor deletion) in neurons reduces brain size, neuron soma size, and dendritic outgrowth (PMIDs: 36526374, 32125271, 23569215). In our revised submission we also include new data showing that the membrane capacitance of Pten-Ric LOF neurons is normal. Thus, we do not find it completely surprising that mTORC2 inactivation reduces the cortical thickness increase caused by Pten loss. There may still be a slight increase in cortical thickness in Pten-Rictor animals, but it is statistically indistinguishable from Controls.

Reviewer #2 (Public Review):

Summary:

The study by Cullen et al presents intriguing data regarding the contribution of mTOR complex 1 (mTORC1) versus mTORC2 or both in Pten-null-induced macrocephaly and epileptiform activity. The role of mTORC2 in mTORopathies, and in particular Pten loss-off-function (LOF)-induced pathology and seizures, is understudied and controversial. In addition, recent data provided evidence against the role of mTORC1 in PtenLOF-induced seizures. To address these controversies and the contribution of these mTOR complexes in PtenLOF-induced pathology and seizures, the authors injected a AAV9-Cre into the cortex of conditional single, double, and triple transgenic mice at postnatal day 0 to remove Pten, Pten+Raptor or Rictor, and Pten+raptor+rictor. Raptor and Rictor are essentially binding partners of mTORC1 and mTORC2, respectively. One major finding is that despite preventing mild macrocephaly and increased cell size, Raptor knockout (KO, decreased mTORC1 activity) did not prevent the occurrence of seizures and the rate of SWD event, and aggravated seizure duration. Similarly, Rictor KO (decreased mTORC2 activity) partially prevented mild macrocephaly and increased cell size but did not prevent the occurrence of seizures and did not affect seizure duration. However, Rictor KO reduced the rate of SWD events. Finally, the pathology and seizure/SWD activity were fully prevented in the double KO. These data suggest the contribution of both increased mTORC1 and mTORC2 in the pathology and epileptic activity of Pten LOF mice, emphasizing the importance of blocking both complexes for seizure treatment. Whether these data apply to other mTORopathies due to Tsc1, Tsc2, mTOR, AKT or other gene variants remains to be examined.

Strengths:

The strengths are as follows: 1) they address an important and controversial question that has clinical application, 2) the study uses a reliable and relatively easy method to KO specific genes in cortical neurons, based on AAV9 injections in pups. 2) they perform careful video-EEG analyses correlated with some aspects of cellular pathology.

Weaknesses:

The study has nevertheless a few weaknesses: 1) the conclusions are perhaps a bit overstated. The data do not show that increased mTORC1 or mTORC2 are sufficient to cause epilepsy. However the data clearly show that both increased mTORC1 and mTORC2 activity contribute to the pathology and seizure activity and as such are necessary for seizures to occur.

We agree that our findings do not directly show that either mTORC1 or mTORC2 hyperactivity are sufficient to cause seizures, as we do not individually hyperactivate each complex in the absence of any other manipulation. We interpreted our findings in this model as suggesting that either is sufficient based on the result that there is no epileptic activity when both are inactivated, and thus assume that there is not a third, mTOR-independent, mechanism that is contributing to epilepsy in Pten, Pten-Raptor, and Pten-Rictor animals. In addition, the histological data show that Raptor and Rictor loss each normalize activity through mTORC1 and mTORC2 respectively, suggesting that one in the absence of the other is sufficient. However, we agree that there could be other potential mTOR-independent pathways downstream of Pten loss that contribute to epilepsy. We have revised the manuscript to reflect this.

(2) The data related to the EEG would benefit from having more mice. Adding more mice would have helped determine whether there was a decrease in seizure activity with the Rictor or Raptor KO.

Please see response to Reviewer 1’s first Weakness.

(3) It would have been interesting to examine the impact of mTORC2 and mTORC1 overexpression related to point #1 above.

We are not sure that overexpression of individual components of mTORC1 or mTORC2 would result in their hyperactivation or lead to increases in downstream signaling. We believe that cleanly and directly hyperactivating mTORC1 or especially mTORC2 in vivo without affecting the other complex or other potential interacting pathways is a difficult task. Previous studies have used mTOR gain-of-function mutations as a means to selectively activate mTORC1 or pharmacological agents to selectively activate mTORC2, but it not clear to us that the former does not affect mTORC2 activity as well, or that the latter achieves activation of mTORC2 targets other than p-Akt 473, or that it is truly selective. We agree that these would be key experiments to further test the sufficiency hypothesis, but that the amount of work that would be required to perform them is more that what we can do in this Short Report.

Reviewer #3 (Public Review):

Summary: This study investigated the role of mTORC1 and 2 in a mouse model of developmental epilepsy which simulates epilepsy in cortical malformations. Given activation of genes such as PTEN activates TORC1, and this is considered to be excessive in cortical malformations, the authors asked whether inactivating mTORC1 and 2 would ameliorate the seizures and malformation in the mouse model. The work is highly significant because a new mouse model is used where Raptor and Rictor, which regulate mTORC1 and 2 respectively, were inactivated in one hemisphere of the cortex. The work is also significant because the deletion of both Raptor and Rictor improved the epilepsy and malformation. In the mouse model, the seizures were generalized or there were spike-wave discharges (SWD). They also examined the interictal EEG. The malformation was manifested by increased cortical thickness and soma size.

Strengths: The presentation and writing are strong. The quality of data is strong. The data support the conclusions for the most part. The results are significant: Generalized seizures and SWDs were reduced when both Torc1 and 2 were inactivated but not when one was inactivated.

Weaknesses: One of the limitations is that it is not clear whether the area of cortex where Raptor or Rictor were affected was the same in each animal.

Our revised submission includes new data showing that the area of affected cortex and hippocampus are similar across groups. (Figure 1A and Supplementary Figure 1)

Also, it is not clear which cortical cells were measured for soma size.

Soma size was measured by dividing Nissl stain images into a 10 mm2 grid. The somas of all GFP-expressing cells fully within three randomly selected grid squares in Layer II/III were manually traced. Three sections per animal at approximately Bregma -1.6, -2,1, and -2.6 were used. As Cre expression was driven by the hSyn promoter these cells include both excitatory and inhibitory cortical neurons.

Another limitation is that the hippocampus was affected as well as the cortex. One does not know the role of cortex vs. hippocampus. Any discussion about that would be good to add.

See response to Reviewer 1’s second Weakness.

It would also be useful to know if Raptor and Rictor are in glia, blood vessels, etc.

Raptor and Rictor are thought to be ubiquitously active in mammalian cells including glia and endothelial cells. Previous studies have shown that mTOR manipulation can affect astrocyte function and blood vessel organization, however, our study induced gene knockout using an AAV that expressed Cre under control of the hSyn promoter, which has previously been shown to be selective for neurons. Manual assessment of Cre expression compared with DAPI, NeuN, and GFAP stains suggested that only neurons were affected.

Recommendations for the authors: please note that you control which revisions to undertake from the public reviews and recommendations for the authors

Reviewer #1 (Recommendations For The Authors):

In addition to the comments in the public review, it is recommended that the authors provide a more representative figure for p-Akt staining in the Pten LOF condition in Figure 1 D2. The current figure is not convincing.

Thanks for the suggestion. We have replaced the images with zoomed in panels that beter demonstrate the difference.

Additionally, in the last paragraph of the discussion, there is a reference error to an incorrect paper (reference 18) that should be corrected.

Thanks, corrected.

Reviewer #2 (Recommendations For The Authors):

Major comments:

Comment 1: Some statements need clarifications or changes.

(1) Abstract: "spontaneous seizures and epileptiform activity persisted despite mTORC1 or mTORC2 inactivation alone but inactivating both mTORC1 and mTORC2 normalized pathology." Did inactivation of one only also normalized the pathology? Did inactivating both normalized the seizures? Pathology is not equal to seizures.

We have altered this statement to avoid ambiguity.

(2) Abstract: "These results suggest that hyperactivity of both mTORC1 and mTORC2 are sufficient to cause epilepsy,". Based on the abstract, it is not clear that it is sufficient. It is necessary.

We have altered this statement by removing the term “sufficient.”

(3) "Thus, there is strong evidence that hyperactivation of mTORC1 downstream of PTEN disruption causes the macrocephaly, epilepsy, early mortality, and synaptic dysregulation observed in humans and model organisms [17]" I would suggest adding that the strongest evidence is that mTOR GOF mutations lead to the same pathology and epilepsy, suggesting mTORC1 is sufficient. The other findings suggest that it is necessary.

Unless we misunderstand the Reviewer’s point, we believe this viewpoint is already encompassed by the proceeding text that “These phenotypes resemble those observed in models of mTORC1- specific hyperactivation.”

(4) Introduction (end): "suggesting that hyperactivity of either complex can lead to neuronal hyperexcitability and epilepsy".

Comment 2: I do not agree with the title based on comment 1 above. You did not provide evidence that the mTORCs cause seizures. Your data suggest that they are necessary for seizures or contribute to seizures, but there is no evidence that mTORC2 can induce seizure.

We softened the title by replacing “cause” with “mediate.”

Comment 3: Fig. 1B. Could you beter describe the affected regions. I can see other regions than just the cortex and hippocampus.

Almost all affected cell bodies were in the cortex and hippocampus. The virus in the image is cell-filling and as such projections from affected neurons throughout the brain can also be seen. We have clarified this in the figure legend.

Comment 4: I feel unease about the number of animals recorded for EEG to assess seizure frequency. There is not enough power to draw clear conclusions. So, please make sure to not oversell your findings since it is all-or-nothing data (seizure or no seizure) in this case and the seizure frequency could very well be decreased with single mTOR LOF, but it is impossible to conclude. Maybe discuss this limitation of your study.

We have addressed this in the public comments response.

Minor:

(1) Pten LOF: define the abbreviation.

Done

(2) Make sure that gene name in mice are not capitalized and italicized.

OK

(3) Fig 1C: could you specify in the results where the analysis was done.

Detail added to Methods (to keep Results concise for word limit)

(4) In the subtitle: "Concurrent mTORC1/2 inactivation, but neither alone, rescues epilepsy and interictal EEG abnormalities in focal Pten LOF". Replace "rescues" but prevents. This is not a rescue experiment since the LOF is done at the same time.

OK

(5) "GS did not appear to be correlated with mTOR pathway activity (Supplementary Figure 2)." Please can you do proper correlation analysis, by plotting all the values as a function of seizure frequency independent of the condition? There is also no correlation between pAKt and seizures.

Here are those data in Author response image 1. They are now part of Supplementary Figure 2.

Author response image 1.

Reviewer #3 (Recommendations For The Authors):

Figures 1 D, and E show images that are too small to judge. Where are the layers? Please add marks.

We replaced these images with larger zoomed in images to show group differences more clearly. The images no longer show multiple differentiable cortical layers.

If Fig 1 characterizes the model, where is the seizure data? When did they start? Where did they start? Was the focus of the cortical area affected by PTEN loss of function?

Updated figure name to reflect content. Information about the seizure phenotypes is included in Figure 3.

Figure 2 The font size for the calibration is too small. The correlations are hard to see. Colors are not easy to discriminate.

We edited the figure to correct these problems.

Figure 3 shows a clear effect on generalized seizures but the text of the Results does not reflect that.

We wanted to be cautious about interpreting these data based on the issue raised by other reviewers that they are underpowered to detect seizure reduction in the Pten-Raptor and Pten-Rictor groups. We have updated the language to atempt to strike a beter balance between over- and under-interpretation. We also performed an additional analysis of the occurrence of generalized seizures to emphasize that only Control and PtRapRic animals have significantly lower seizure occurrence that Pten LOF mice (Fig 3C).

For interictal power, was the same behavioral state chosen? Was a particular band affected?

Epochs to be analyzed were selected automatically and were agnostic to behavioral state. Band-specific effects are outlined in Figure 4B and Table [2].

There is no information about whether the model exhibits altered sleep, food intake, weight, etc.

We didn’t collect information on food intake. It would be possible to look at sleep from the EEG, but that is not something that we are prepared to do at this point. Weight at endpoint was not different between genotypes but we did not collect longitudinal data on weight.

Were the sexes different?

Included in new Table [1]

Where were EEG electrodes and were they subdural or not?

Additional detail on this has been added to Methods. The screws are placed in the skull but above the dura.

How long were continuous EEG records- the method just says 150 hr. per mouse in total.

Included in new Table [1]

The statistics don't discuss power, normality, whether variance was checked to ensure it did not differ significantly between groups, or whether data are mean +- sem or sd. For ANOVAs, were there multifactorial comparisons and what were F, df, and p values? Exact p for post hoc tests?

We have added a new table (Table [3]) that gives information on the exact test used, F, p values, and exact p for post hoc tests. Information regarding power, normality, variance, post- tests and multiple comparisons corrections have been added to Methods section “Statistical Analysis.”

Author Response

Reviewer #1 (Public Review):

Summary:

Visual Perceptual Learning (VPL) results in varying degrees of generalization to tasks or stimuli not seen during training. The question of which stimulus or task features predict whether learning will transfer to a different perceptual task has long been central in the field of perceptual learning, with numerous theories proposed to address it. This paper introduces a novel framework for understanding generalization in VPL, focusing on the form invariants of the training stimulus. Contrary to a previously proposed theory that task difficulty predicts the extent of generalization - suggesting that more challenging tasks yield less transfer to other tasks or stimuli - this paper offers an alternative perspective. It introduces the concept of task invariants and investigates how the structural stability of these invariants affects VPL and its generalization. The study finds that tasks with high-stability invariants are learned more quickly. However, training with low-stability invariants leads to greater generalization to tasks with higher stability, but not the reverse. This indicates that, at least based on the experiments in this paper, an easier training task results in less generalization, challenging previous theories that focus on task difficulty (or precision). Instead, this paper posits that the structural stability of stimulus or task invariants is the key factor in explaining VPL generalization across different tasks

Strengths:

• The paper effectively demonstrates that the difficulty of a perceptual task does not necessarily correlate with its learning generalization to other tasks, challenging previous theories in the field of Visual Perceptual Learning. Instead, it proposes a significant and novel approach, suggesting that the form invariants of training stimuli are more reliable predictors of learning generalization. The results consistently bolster this theory, underlining the role of invariant stability in forecasting the extent of VPL generalization across different tasks.

• The experiments conducted in the study are thoughtfully designed and provide robust support for the central claim about the significance of form invariants in VPL generalization.

Weaknesses:

• The paper assumes a considerable familiarity with the Erlangen program and the definitions of invariants and their structural stability, potentially alienating readers who are not versed in these concepts. This assumption may hinder the understanding of the paper's theoretical rationale and the selection of stimuli for the experiments, particularly for those unfamiliar with the Erlangen program's application in psychophysics. A brief introduction to these key concepts would greatly enhance the paper's accessibility. The justification for the chosen stimuli and the design of the three experiments could be more thoroughly articulated.

Response: We appreciate the reviewer's feedback regarding the accessibility of our paper. In response to this feedback, we plan to enhance the introduction section of our paper to provide a concise yet comprehensive overview of the key concepts of Erlangen program. Additionally, we will provide a more thorough justification for the selection of stimuli and the experimental design in our revised version, ensuring that readers understand the rationale behind our choices.

• The paper does not clearly articulate how its proposed theory can be integrated with existing observations in the field of VPL. While it acknowledges previous theories on VPL generalization, the paper falls short in explaining how its framework might apply to classical tasks and stimuli that have been widely used in the VPL literature, such as orientation or motion discrimination with Gabors, vernier acuity, etc. It also does not provide insight into the application of this framework to more naturalistic tasks or stimuli. If the stability of invariants is a key factor in predicting a task's generalization potential, the paper should elucidate how to define the stability of new stimuli or tasks. This issue ties back to the earlier mentioned weakness: namely, the absence of a clear explanation of the Erlangen program and its relevant concepts.

Response: Thanks for highlighting the need for better integration of our proposed theory with existing observations in the field of VPL. Unfortunately, the theoretical framework proposed in our study is based on the Klein’s Erlangen program and is only applicable to geometric shape stimuli. For VPL studies using stimuli and paradigms that are completely unrelated to geometric transformations (such as motion discrimination with Gabors or random dots, vernier acuity, spatial frequency discrimination, contrast detection or discrimination, etc.), our proposed theory does not apply. Some stimuli employed by VPL studies can be classified into certain geometric invariants. For instance, orientation discrimination with Gabors (Dosher & Lu, 2005) and texture discrimination task (F. Wang et al., 2016) both belong to tasks involving Euclidean invariants, and circle versus square discrimination (Kraft et al., 2010) belongs to tasks involving affine invariance. However, these studies do not simultaneously involve multiple geometric invariants of varying levels stability, and thus cannot be directly compared with our research. It is worth noting that while the Klein’s hierarchy of geometries, which our study focuses on, is rarely mentioned in the field of VPL, it does have connections with concepts such as 'global/local', 'coarse/fine', 'easy/difficulty', 'complex/simple': more stable invariants are closer to 'global', 'coarse', 'easy', 'complex', while less stable invariants are closer to 'local', 'fine', 'difficulty', 'simple'. Importantly, several VPL studies have found ‘fine-to-coarse’ or ‘local-to-global’ asymmetric transfer (Chang et al., 2014; N. Chen et al., 2016; Dosher & Lu, 2005), which seems consistent with the results of our study.

In the introduction section of our revised version and subsequent full author response, we will provide a clear explanation of the Erlangen program and elucidate how to define the stability of new stimuli or tasks. In the discussion section of our revised version, we will compare our results to other studies concerned with the generalization of perceptual learning and speculate on how our proposed theory fit with existing observations in the field of VPL.

• The paper does not convincingly establish the necessity of its introduced concept of invariant stability for interpreting the presented data. For instance, consider an alternative explanation: performing in the collinearity task requires orientation invariance. Therefore, it's straightforward that learning the collinearity task doesn't aid in performing the other two tasks (parallelism and orientation), which do require orientation estimation. Interestingly, orientation invariance is more characteristic of higher visual areas, which, consistent with the Reverse Hierarchy Theory, are engaged more rapidly in learning compared to lower visual areas. This simpler explanation, grounded in established concepts of VPL and the tuning properties of neurons across the visual cortex, can account for the observed effects, at least in one scenario. This approach has previously been used/proposed to explain VPL generalization, as seen in (Chowdhury and DeAngelis, Neuron, 2008), (Liu and Pack, Neuron, 2017), and (Bakhtiari et al., JoV, 2020). The question then is: how does the concept of invariant stability provide additional insights beyond this simpler explanation?

Response: We appreciate the alternative explanation proposed by the reviewer and agree that it presents a valid perspective grounded in established concepts of VPL and neural tuning properties. However, performing in the collinearity and parallelism tasks both require orientation invariance. While utilizing the orientation invariance, as proposed by the reviewer, can explain the lack of transfer from collinearity or parallelism to orientation task, it cannot explain why collinearity does not transfer to parallelism.

As stated in the response to the previous review, in the revised discussion section, we will compare our study with other studies (including the three papers mentioned by the reviewer), aiming to clarify the necessity of the concept of invariant stability for interpreting the observed data and understanding the mechanisms underlying VPL generalization.

• While the paper discusses the transfer of learning between tasks with varying levels of invariant stability, the mechanism of this transfer within each invariant condition remains unclear. A more detailed analysis would involve keeping the invariant's stability constant while altering a feature of the stimulus in the test condition. For example, in the VPL literature, one of the primary methods for testing generalization is examining transfer to a new stimulus location. The paper does not address the expected outcomes of location transfer in relation to the stability of the invariant. Moreover, in the affine and Euclidean conditions one could maintain consistent orientations for the distractors and targets during training, then switch them in the testing phase to assess transfer within the same level of invariant structural stability.

Response: Thanks for raising the issue regarding the mechanism of transfer within each invariant conditions. We plan to design an additional experiment that is similar in paradigm to Experiment 2, aiming to examine how VPL generalizes to a new test location within a single invariant stability level.

• In the section detailing the modeling experiment using deep neural networks (DNN), the takeaway was unclear. While it was interesting to observe that the DNN exhibited a generalization pattern across conditions similar to that seen in the human experiments, the claim made in the abstract and introduction that the model provides a 'mechanistic' explanation for the phenomenon seems overstated. The pattern of weight changes across layers, as depicted in Figure 7, does not conclusively explain the observed variability in generalizations. Furthermore, the substantial weight change observed in the first two layers during the orientation discrimination task is somewhat counterintuitive. Given that neurons in early layers typically have smaller receptive fields and narrower tunings, one would expect this to result in less transfer, not more.

Response: We appreciate the reviewer's feedback regarding the clarity of our DNN modeling experiment. We acknowledge that while DNNs have been demonstrated to serve as models for visual systems as well as VPL, the claim that the model provides a ‘mechanistic’ explanation for the phenomenon still overstated. In our revised version,

We will attempt a more detailed analysis of the DNN model while providing a more explicit explanation of the findings from the DNN modeling experiment, emphasizing its implications for understanding the observed variability in generalizations.

Additionally, the substantial weight change observed in the first two layers during the orientation discrimination task is not contradictory to the theoretical framework we proposed, instead, it aligns with our speculation regarding the neural mechanisms of VPL for geometric invariants. Specifically, it suggests that invariants with lower stability rely more on the plasticity of lower-level brain areas, thus exhibiting poorer generalization performance to new locations or stimulus features within each invariant conditions. However, it does not imply that their learning effects cannot transfer to invariants with higher stability.

Reviewer #2 (Public Review):

The strengths of this paper are clear: The authors are asking a novel question about geometric representation that would be relevant to a broad audience. Their question has a clear grounding in pre-existing mathematical concepts, that, to my knowledge, have been only minimally explored in cognitive science. Moreover, the data themselves are quite striking, such that my only concern would be that the data seem almost too clean. It is hard to know what to make of that, however. From one perspective, this is even more reason the results should be publicly available. Yet I am of the (perhaps unorthodox) opinion that reviewers should voice these gut reactions, even if it does not influence the evaluation otherwise. Below I offer some more concrete comments:

(1) The justification for the designs is not well explained. The authors simply tell the audience in a single sentence that they test projective, affine, and Euclidean geometry. But despite my familiarity with these terms -- familiarity that many readers may not have -- I still had to pause for a very long time to make sense of how these considerations led to the stimuli that were created. I think the authors must, for a point that is so central to the paper, thoroughly explain exactly why the stimuli were designed the way that they were and how these designs map onto the theoretical constructs being tested.

(2) I wondered if the design in Experiment 1 was flawed in one small but critical way. The goal of the parallelism stimuli, I gathered, was to have a set of items that is not parallel to the other set of items. But in doing that, isn't the manipulation effectively the same as the manipulation in the orientation stimuli? Both functionally involve just rotating one set by a fixed amount. (Note: This does not seem to be a problem in Experiment 2, in which the conditions are more clearly delineated.)

(3) I wondered if the results would hold up for stimuli that were more diverse. It seems that a determined experimenter could easily design an "adversarial" version of these experiments for which the results would be unlikely to replicate. For instance: In the orientation group in Experiment 1, what if the odd-one-out was rotated 90 degrees instead of 180 degrees? Intuitively, it seems like this trial type would now be much easier, and the pattern observed here would not hold up. If it did hold up, that would provide stronger support for the authors' theory.

It is not enough, in my opinion, to simply have some confirmatory evidence of this theory. One would have to have thoroughly tested many possible ways that theory could fail. I'm unsure that enough has been done here to convince me that these ideas would hold up across a more diverse set of stimuli.

Response: (1) We appreciate the reviewer’s feedback regarding the justification for our experimental designs. We recognize the importance of thoroughly explaining how our stimuli were designed and how these designs correspond to the theoretical constructs being tested. In our revised version, we will enhance the introduction of Erlangen program and provide a more detailed explanation of the rationale behind our stimulus designs, aiming to enhance the clarity and transparency of our experimental approach for readers who may not be familiar with these concepts.

(2) We appreciate the reviewer’s insight into the design of Experiment 1 and the concern regarding the potential similarity between the parallelism and orientation stimuli manipulations.

The parallelism and orientation stimuli in Experiment 1 were first used by Olson & Attneave (1970) to support line-based models of shape coding and then adapted to measure the relative salience of different geometric properties (Chen, 1986). In the parallelism stimuli, the odd quadrant differs from the rest in line slope, while in the orientation stimuli, in contrast, the odd quadrant contains exactly the same line segments as the rest but differs in direction pointed by the angles. The result, that the odd quadrant was detected much faster in the parallelism stimuli than in the orientation stimuli, can serve as evidence for line-based models of shape coding. However, according to Chen (1986, 2005), the idea of invariants over transformations suggests a new analysis of the data: in the parallelism stimuli, the fact that line segments share the same slope essentially implies that they are parallel, and the discrimination may be actually based on parallelism. Thus, the faster discrimination of the parallelism stimuli than that of the orientation stimuli may be explained in terms of relative superiority of parallelism over orientation of angles—a Euclidean property.

The group of stimuli in Experiment 1 has been employed by several studies to investigate scientific questions related to the Klein’s hierarchy of geometries (L. Chen, 2005; Meng et al., 2019; B. Wang et al., n.d.). Due to historical inheritance, we adopted this set of stimuli and corresponding paradigm, despite their imperfect design.

(3) Thanks for raising the important issue of stimulus diversity and the potential for "adversarial" versions of the experiments to challenge our findings. We acknowledge the validity of your concern and recognize the need to demonstrate the robustness of our results across a range of stimuli. We plan to design additional experiments to investigate the potential implications of varying stimulus characteristics, such as different rotation angles proposed by the reviewer, on the observed patterns of performance.

eLife assessment

This important study proposes a framework to understand and predict generalization in visual perceptual learning in humans based on form invariants. Using behavioral experiments in humans and by training deep networks, the authors offer evidence that the presence of stable invariants in a task leads to faster learning. However, this interpretation is promising but incomplete. It can be strengthened through clearer theoretical justification, additional experiments, and by rejecting alternate explanations.

Reviewer #1 (Public Review):

Summary:<br /> Visual Perceptual Learning (VPL) results in varying degrees of generalization to tasks or stimuli not seen during training. The question of which stimulus or task features predict whether learning will transfer to a different perceptual task has long been central in the field of perceptual learning, with numerous theories proposed to address it. This paper introduces a novel framework for understanding generalization in VPL, focusing on the form invariants of the training stimulus. Contrary to a previously proposed theory that task difficulty predicts the extent of generalization - suggesting that more challenging tasks yield less transfer to other tasks or stimuli - this paper offers an alternative perspective. It introduces the concept of task invariants and investigates how the structural stability of these invariants affects VPL and its generalization. The study finds that tasks with high-stability invariants are learned more quickly. However, training with low-stability invariants leads to greater generalization to tasks with higher stability, but not the reverse. This indicates that, at least based on the experiments in this paper, an easier training task results in less generalization, challenging previous theories that focus on task difficulty (or precision). Instead, this paper posits that the structural stability of stimulus or task invariants is the key factor in explaining VPL generalization across different tasks

Strengths:<br /> - The paper effectively demonstrates that the difficulty of a perceptual task does not necessarily correlate with its learning generalization to other tasks, challenging previous theories in the field of Visual Perceptual Learning. Instead, it proposes a significant and novel approach, suggesting that the form invariants of training stimuli are more reliable predictors of learning generalization. The results consistently bolster this theory, underlining the role of invariant stability in forecasting the extent of VPL generalization across different tasks.

- The experiments conducted in the study are thoughtfully designed and provide robust support for the central claim about the significance of form invariants in VPL generalization.

Weaknesses:<br /> - The paper assumes a considerable familiarity with the Erlangen program and the definitions of invariants and their structural stability, potentially alienating readers who are not versed in these concepts. This assumption may hinder the understanding of the paper's theoretical rationale and the selection of stimuli for the experiments, particularly for those unfamiliar with the Erlangen program's application in psychophysics. A brief introduction to these key concepts would greatly enhance the paper's accessibility. The justification for the chosen stimuli and the design of the three experiments could be more thoroughly articulated.

- The paper does not clearly articulate how its proposed theory can be integrated with existing observations in the field of VPL. While it acknowledges previous theories on VPL generalization, the paper falls short in explaining how its framework might apply to classical tasks and stimuli that have been widely used in the VPL literature, such as orientation or motion discrimination with Gabors, vernier acuity, etc. It also does not provide insight into the application of this framework to more naturalistic tasks or stimuli. If the stability of invariants is a key factor in predicting a task's generalization potential, the paper should elucidate how to define the stability of new stimuli or tasks. This issue ties back to the earlier mentioned weakness: namely, the absence of a clear explanation of the Erlangen program and its relevant concepts.

- The paper does not convincingly establish the necessity of its introduced concept of invariant stability for interpreting the presented data. For instance, consider an alternative explanation: performing in the collinearity task requires orientation invariance. Therefore, it's straightforward that learning the collinearity task doesn't aid in performing the other two tasks (parallelism and orientation), which do require orientation estimation. Interestingly, orientation invariance is more characteristic of higher visual areas, which, consistent with the Reverse Hierarchy Theory, are engaged more rapidly in learning compared to lower visual areas. This simpler explanation, grounded in established concepts of VPL and the tuning properties of neurons across the visual cortex, can account for the observed effects, at least in one scenario. This approach has previously been used/proposed to explain VPL generalization, as seen in (Chowdhury and DeAngelis, Neuron, 2008), (Liu and Pack, Neuron, 2017), and (Bakhtiari et al., JoV, 2020). The question then is: how does the concept of invariant stability provide additional insights beyond this simpler explanation?

- While the paper discusses the transfer of learning between tasks with varying levels of invariant stability, the mechanism of this transfer within each invariant condition remains unclear. A more detailed analysis would involve keeping the invariant's stability constant while altering a feature of the stimulus in the test condition. For example, in the VPL literature, one of the primary methods for testing generalization is examining transfer to a new stimulus location. The paper does not address the expected outcomes of location transfer in relation to the stability of the invariant. Moreover, in the affine and Euclidean conditions one could maintain consistent orientations for the distractors and targets during training, then switch them in the testing phase to assess transfer within the same level of invariant structural stability.

- In the section detailing the modeling experiment using deep neural networks (DNN), the takeaway was unclear. While it was interesting to observe that the DNN exhibited a generalization pattern across conditions similar to that seen in the human experiments, the claim made in the abstract and introduction that the model provides a 'mechanistic' explanation for the phenomenon seems overstated. The pattern of weight changes across layers, as depicted in Figure 7, does not conclusively explain the observed variability in generalizations. Furthermore, the substantial weight change observed in the first two layers during the orientation discrimination task is somewhat counterintuitive. Given that neurons in early layers typically have smaller receptive fields and narrower tunings, one would expect this to result in less transfer, not more.

Reviewer #2 (Public Review):

The strengths of this paper are clear: The authors are asking a novel question about geometric representation that would be relevant to a broad audience. Their question has a clear grounding in pre-existing mathematical concepts, that, to my knowledge, have been only minimally explored in cognitive science. Moreover, the data themselves are quite striking, such that my only concern would be that the data seem almost *too* clean. It is hard to know what to make of that, however. From one perspective, this is even more reason the results should be publicly available. Yet I am of the (perhaps unorthodox) opinion that reviewers should voice these gut reactions, even if it does not influence the evaluation otherwise. Below I offer some more concrete comments:

(1) The justification for the designs is not well explained. The authors simply tell the audience in a single sentence that they test projective, affine, and Euclidean geometry. But despite my familiarity with these terms -- familiarity that many readers may not have -- I still had to pause for a very long time to make sense of how these considerations led to the stimuli that were created. I think the authors must, for a point that is so central to the paper, thoroughly explain exactly why the stimuli were designed the way that they were and how these designs map onto the theoretical constructs being tested.

(2) I wondered if the design in Experiment 1 was flawed in one small but critical way. The goal of the parallelism stimuli, I gathered, was to have a set of items that is not parallel to the other set of items. But in doing that, isn't the manipulation effectively the same as the manipulation in the orientation stimuli? Both functionally involve just rotating one set by a fixed amount. (Note: This does not seem to be a problem in Experiment 2, in which the conditions are more clearly delineated.)

(3) I wondered if the results would hold up for stimuli that were more diverse. It seems that a determined experimenter could easily design an "adversarial" version of these experiments for which the results would be unlikely to replicate. For instance: In the orientation group in Experiment 1, what if the odd-one-out was rotated 90 degrees instead of 180 degrees? Intuitively, it seems like this trial type would now be much easier, and the pattern observed here would not hold up. If it did hold up, that would provide stronger support for the authors' theory.

It is not enough, in my opinion, to simply have some confirmatory evidence of this theory. One would have to have thoroughly tested many possible ways that theory could fail. I'm unsure that enough has been done here to convince me that these ideas would hold up across a more diverse set of stimuli.

Author Response

We would like to thank the editors and reviewers who took their valuable time to evaluate the manuscript from various perspectives. We are delighted that our technique was found appealing to biologists and imaging technologists. However, we received several comments that the principles and effectiveness of our techniques are often vague and difficult to understand. They also pointed out that the explanations and representations for several figures were not appropriate. We will revise the manuscript to address these issues and make the manuscript more clear and rigorous.

eLife assessment

The important study established a large-scale objective and integrated multiple optical microscopy systems to demonstrate their potential for long-term imaging of the developmental process. The convincing imaging data cover a wide range of biological applications, such as organoids, mouse brains, and quail embryos, but enhancing image quality can further enhance the method's effectiveness. This work will appeal to biologists and imaging technologists focused on long-term imaging of large fields.

Reviewer #1 (Public Review):

Summary:<br /> The authors are trying to develop a microscopy system that generates data output exceeding the previous systems based on huge objectives.

Strengths:<br /> They have accomplished building such a system, with a field of view of 1.5x1.0 cm2 and a resolution of up to 1.2 um. They have also demonstrated their system performance on samples such as organoids, brain sections, and embryos.

Weaknesses:<br /> To be used as a volumetric imaging technique, the authors only showcase the implementation of multi-focal confocal sectioning. On the other hand, most of the real biological samples were acquired under wide-field illumination, and processed with so-called computational sectioning. Despite the claim that it improves the contrast, sometimes I felt that the images were oversharpened and the quantitative nature of these fluorescence images may be perturbed.

Reviewer #2 (Public Review):

Summary:<br /> This manuscript introduced a volumetric trans-scale imaging system with an ultra-large field-of-view (FOV) that enables simultaneous observation of millions of cellular dynamics in centimeter-wide 3D tissues and embryos. In terms of technique, this paper is just a minor improvement of the authors' previous work, which is a fluorescence imaging system working at visible wavelength region (https://www.nature.com/articles/s41598-021-95930-7).

Strengths:<br /> In this study, the authors enhanced the system's resolution and sensitivity by increasing the numerical aperture (NA) of the lens. Furthermore, they achieved volumetric imaging by integrating optical sectioning and computational sectioning. This study encompasses a broad range of biological applications, including imaging and analysis of organoids, mouse brains, and quail embryos, respectively. Overall, this method is useful and versatile.

Weaknesses:<br /> The unique application that only can be done by this high-throughput system remains vague. Meanwhile, there are also several outstanding issues in this paper, such as the lack of technical advances, unclear method details, and non-standardized figures.

eLife assessment

This study presents a valuable characterization of the biochemical consequences of a disease-associated point mutation in a nonmuscle actin. The study uses well-characterized in vitro assays to explore function. The data are convincing and should be helpful to others.

Reviewer #2 (Public Review):

Greve et al. investigated the effects of a disease associated gamma-actin mutation (E334Q) on actin filament polymerization, association of selected actin-binding proteins, and myosin activity. Recombinant wildtype and mutant proteins expressed in sf9 cells were found to be folded and stable, and the presence of the mutation altered a number of activities. Given the location of the mutation, it is not surprising that there are changes in polymerization and interactions with actin binding proteins.

Comments on revised version:

I have nothing to add and am satisfied with the rebuttal.

Author Response

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

eLife assessment

This study presents a useful characterization of the biochemical consequences of a disease-associated point mutation in a nonmuscle actin. The study uses solid and well-characterized in vitro assays to explore function. In some cases the statistical analyses are inadequate and several important in vitro assays are not employed.

Public Reviews:

Reviewer #1 (Public Review):

Strengths:

The authors first perform several important controls to show that the expressed mutant actin is properly folded, and then show that the Arp2/3 complex behaves similarly with WT and mutant actin via a TIRF microscopy assay as well as a bulk pyrene-actin assay. A TIRF assay showed a small but significant reduction in the rate of elongation of the mutant actin suggesting only a mild polymerization defect.

Based on in silico analysis of the close location of the actin point mutation and bound cofilin, cofilin was chosen for further investigation. Faster de novo nucleation by cofilin was observed with mutant actin. In contrast, the mutant actin was more slowly severed. Both effects favor the retention of filamentous mutant actin. In solution, the effect of cofilin concentration and pH was assessed for both WT and mutant actin filaments, with a more limited repertoire of conditions in a TIRF assay that directly showed slower severing of mutant actin.

Lastly, the mutated residue in actin is predicted to interact with the cardiomyopathy loop in myosin and thus a standard in vitro motility assay with immobilized motors was used to show that non-muscle myosin 2A moved mutant actin more slowly, explained in part by a reduced affinity for the filament deduced from transient kinetic assays. By the same motility assay, myosin 5A also showed impaired interaction with the mutant filaments.

The Discussion is interesting and concludes that the mutant actin will co-exist with WT actin in filaments, and will contribute to altered actin dynamics and poor interaction with relevant myosin motors in the cellular context. While not an exhaustive list of possible defects, this is a solid start to understanding how this mutation might trigger a disease phenotype.

We thank the reviewer for the positive evaluation of our work.

Weaknesses:

• Potential assembly defects of the mutant actin could be more thoroughly investigated if the same experiment shown in Fig. 2 was repeated as a function of actin concentration, which would allow the rate of disassembly and the critical concentration to also be determined.

The polymerization rate of individual filaments observed in TIRFM experiments showed only minor changes, as did the bulk-polymerization rate of 2 µM actin in pyrene-actin based experiments. Therefore, we decided not to perform additional pyrene-actin based experiments, in which we titrate the actin concentration, as we expect only very small changes to the critical concentration. Instead, we focused on the disturbed interaction with ABPs, as we assume these defects to be more relevant in an in vivo context. Using pyrene-based bulkexperiments, we did determine the rate of dilution-induced depolymerization of mutant filaments and compare them with the values determined for wt (Figure 5A, Table 1).

• The more direct TIRF assay for cofilin severing was only performed at high cofilin concentration (100 nM). Lower concentrations of cofilin would also be informative, as well as directly examining by the TIRF assay the effect of cofilin on filaments composed of a 50:50 mixture of WT:mutant actin, the more relevant case for the cell.

The TIRF assay for cofilin severing was performed initially over the cofilin concentration range from 20 to 250 nM. The results obtained in the presence of 100 nM cofilin allow a particularly informative depiction of the differences observed with mutant and WT actin. This applies to the image series showing the changes in filament length, cofilin clusters, and filament number as well as to the graphs showing time dependent changes in the number of filaments and total actin fluorescence. We have not included the results for a 50:50 mixture of WT:mutant actin because its attenuating effect is documented in several other experiments in the manuscript.

• The more appropriate assay to determine the effect of the actin point mutation on class 5 myosin would be the inverted assay where myosin walks along single actin filaments adhered to a coverslip. This would allow an evaluation of class 5 myosin processivity on WT versus mutant actin that more closely reflects how Myo5 acts in cells, instead of the ensemble assay used appropriately for myosin 2.

Our results with Myo5A show a less productive interaction with mutant actin filaments as indicated by a 1.7-fold reduction in the average sliding velocity and an increase in the optimal Myo5A-HMM surface density from 770 to 3100 molecules per µm2. These results indicate a reduction in binding affinity and coupling efficiency, with a likely impact on processivity. We expect only a small incremental gain in knowledge about the extent of changes by performing additional experiments with an inverted assay geometry, given that under physiological conditions the motor properties of Myo5A and other cytoskeletal myosins are modulated by other factors such as the presence of tropomyosin isoforms and other actin binding proteins.

Reviewer #2 (Public Review):

Greve et al. investigated the effects of a disease-associated gamma-actin mutation (E334Q) on actin filament polymerization, association of selected actin-binding proteins, and myosin activity. Recombinant wildtype and mutant proteins expressed in sf9 cells were found to be folded and stable, and the presence of the mutation altered a number of activities. Given the location of the mutation, it is not surprising that there are changes in polymerization and interactions with actin binding proteins. Nevertheless, it is important to quantify the effects of the mutation to better understand disease etiology.

We thank the reviewer for the positive evaluation of our work.

Some weaknesses were identified in the paper as discussed below.

• Throughout the paper, the authors report average values and the standard-error-of-the-mean (SEM) for groups of three experiments. Reporting the SEM is not appropriate or useful for so few points, as it does not reflect the distribution of the data points. When only three points are available, it would be better to just show the three different points. Otherwise, plot the average and the range of the three points.

We have gone through the manuscript carefully to correct any errors in the statistics, as explained below.

Figure 1B, 5B, 5C, 5D, 8D, 9B, and 8 – figure supplement 2 all show the mean ± SD, as also correctly reported for Figure 8E and 8F in the figure legend. The statement, that these figures show the mean ± SEM was inaccurate. We corrected this mistake for all the listed figures. Furthermore, we now give the exact N for every experiment in the figure legend.

Figure 2C, 2E, 2F, 4B, 5A, 6B-E showed the mean ± SEM. As suggested by the reviewer, we corrected the figures to show the mean ± SD.

We still refer to the mean ± SEM in Figure 2B, where elongation rates for more than 100 filaments were recorded, and in Figure 8B, where sliding velocities for several thousand actin filaments were measured.

• The description and characterization of the recombinant actin is incomplete. Please show gels of purified proteins. This is especially important with this preparation since the chymotrypsin step could result in internally cleaved proteins and altered properties, as shown by Ceron et al (2022). The authors should also comment on N-terminal acetylation of actin.

We added an additional figure showing the purification strategy for the recombinant cytoskeletal γ –actin WT and p.E334Q protein with exemplary SDS-gels from different stages of purification (Figure 1 – figure supplement 1).

In a previous paper, we reported the mass spectrometric analysis of the post-translational modifications of recombinant human β- and γ-cytoskeletal actin produced in Sf-9 cells. (Müller et al., 2013, Plos One). Recombinant actin showing complete N-terminal processing resulting in cleavage of the initial methionine and acetylation of the following aspartate (β-actin) or glutamate (γ-actin) is the predominant species in the analyzed preparations (> 95 %). While the recombinant actin in the 2013 study was produced tag-free and purified by affinity chromatography using the column-immobilized actin-binding domain of gelsolin (G4-G6), we have no reason to assume that the purification strategy using the actin-thymosin-β4 changes the efficiency of the N-terminal processing in Sf-9 cells. This is supported by our, yet unpublished, mass-spectrometric studies on recombinant human α-cardiac actin purified using the actin- thymosin-β4 fusion construct, which revealed actin species with an acetylated aspartate-3. This N-terminal modification of α-cardiac actin is catalyzed by the same actinspecific acetyltransferase (NAA80) as the acetylation of asparate-2 or glutamate-2 in cytoskeletal actin isoforms (Varland et al., 2019, Trends in Biochemical Sciences). Furthermore, additional studies that used the actin-thymosin-β4 fusion construct for the production of recombinant human cytoskeletal actin isoforms in Pichia pastoris reported robust N-terminal acetylation, when the actin was co-produced with NAA80 (In contrast to Sf-9 cells, NAA80 is not endogenously expressed in Pichia pastoris) (Hatano et al., 2020, Journal of Cell Science).

We therefore, added the following statement to the manuscript:

“Purification of the fusion protein by immobilized metal affinity chromatography, followed by chymotrypsin–mediated cleavage of C–terminal linker and tag sequences, results in homogeneous protein without non–native residues and native N-terminal processing, which includes cleavage of the initial methionine and acetylation of the following glutamate. “

• The authors do not use the best technique to assess actin polymerization parameters. Although the TIRF assay is excellent for some measurements, it is not as good as the standard pyrene-actin assays that provide critical concentration, nucleation, and polymerization parameters. The authors use pyrene-actin in other parts of the paper, so it is not clear why they don't do the assays that are the standard in the actin field.

The polymerization rate of individual filaments observed in TIRFM experiments showed only minor changes, as did the bulk-polymerization rate of 2 µM actin in pyrene-actin based experiments. Therefore, we decided not to perform additional pyrene-actin based experiments, in which we titrate the actin concentration, as we expect only very small changes to the critical concentration. Instead, we focused on the disturbed interaction with ABPs, as we assume these defects to be more relevant in an in vivo context. Using pyrene-based bulkexperiments, we did determine the rate of dilution-induced depolymerization of mutant filaments and compare them with the values determined for WT (Figure 5A, Table 1).

• The authors' data suggest that, while the binding of cofilin-1 to both the WT and mutant actins remains similar, the major defect of the E334Q actin is that it is not as readily severed/disassembled by cofilin. What is missing is a direct measurement of the severing rate (number of breaks per second) as measured in TIRF.

The severing rate as measured in TIRF is dependent on a number of parameters in a nonlinear manner. Therefore, we opted to show the combination of images directly showing the progress of the reaction and graphs summarizing the concomitant changes in cofilin clusters, actin filaments, actin-related fluorescence intensity and cofilin-related fluorescence intensity.

• Figure 4 shows that the E334Q mutation increases rather than decreases the number of filaments that spontaneously assemble in the TIRF assay, but it is unclear how reduced severing would lead to increased filament numbers, rather, the opposite would be expected. A more straightforward approach would be to perform experiments where severing leads to more nuclei and therefore enhances the net bulk assembly rate.

Figure 4 shows polymerization experiments that were started from ATP-G-actin in the presence of cofilin-1. These experiments show clearly that, especially at the higher cofilin-1 concentration (100 nM), the filament number is strongly increased in experiments performed with mutant actin. Inspection of the corresponding videos of these TIRFM experiments suggest that the increased number of filaments must result from an increased number of de novo nucleation events and not primarily from a mutation-induced change in severing susceptibility. The observation of a cofilin-stimulated increase in the de novo nucleation efficiency of actin was initially described by Andrianantoandro & Pollard (2006, Molecular Cell) using TIRFMbased experiments and is thought to arise from the stabilization of thermodynamically unfavorable actin dimers and trimers by cofilin. While the exact role of this cofilin-mediated effect in vivo is not completely clear, it is thought to contribute to cofilin-meditated actin dynamics synergistically with cofilin-mediated severing. It is therefore necessary, to clearly distinguish between the two effects of cofilin in vitro: stimulation of de novo nucleation and stimulation of filament disassembly. Our data indicated that the E334Q mutation affects these two effects differentially, as we state in the abstract and in the discussion.

Abstract: “E334Q differentially affects cofilin-mediated actin dynamics by increasing the rate of cofilin-mediated de novo nucleation of actin filaments and decreasing the efficiency of cofilin-mediated filament severing.”

Discussion: “Cofilin-mediated severing and nucleation were previously proposed to synergistically contribute to global actin turnover in cells (Andrianantoandro & Pollard, 2006; Du & Frieden, 1998). Our results show that the mutation affects these different cofilin functions in actin dynamics in opposite ways. Cofilin-mediated filament nucleation is more efficient for p.E334Q monomers, while cofilin-mediated severing of filaments containing p.E334Q is significantly reduced. The interaction of both actin monomers and actin filaments with ADF/cofilin proteins involves several distinct overlapping reactions. In the case of actin filaments, cofilin binding is followed by structural modification of the filament, severing and depolymerizing the filament (De La Cruz & Sept, 2010). Cofilin binding to monomeric actin is followed by the closure of the nucleotide cleft and the formation of stabilized “long-pitch” actin dimers, which stimulate nucleation (Andrianantoandro & Pollard, 2006)”.

We interpret the reviewer's suggestion to mean that additional pyrene-actin-based bulk polymerization experiments should be performed to investigate the bulk-polymerization rate of ATP-G-actin in the presence of cofilin-1. In our understanding, these experiment would not provide additional value as 1) An observed increase of the bulk-polymerization rate cannot be directly correlated to a change of the efficiency of de novo nucleation or severing and 2) the effect of the mutation on cofilin-mediated filament disassembly was extensively analyzed in other experiments starting from preformed actin filaments. Moreover, our results are consistent with in silico modelling and normal mode analysis of the WT and mutant actin-cofilin complex.

• Figure 5 A: in the pyrene disassembly assay, where actin is diluted below its critical concentration, cofilin enhances the rate of depolymerization by generating more free ends. The E334Q mutation leads to decreased cofilin-induced severing and therefore lower depolymerization. While these data seem convincing, it would be better to present them as an XY plot and fit the data to lines for comparison of the slopes.

We now present the data as suggested by the reviewer. Furthermore, we determined the apparent second-order rate constant for cofilin-induced F-actin depolymerization (kc) to quantify the observed differences between WT, mutant and heterofilaments, as suggested by the reviewer.

The paragraph describing these results was changed accordingly:

“The observed rate constant values are linearly dependent on the concentration of cofilin–1 in the range 0–40 nM, with the slope corresponding to the apparent second– order rate constant (kC) for the cofilin-1 induced depolymerization of F–actin. In experiments performed with p.E334Q filaments, the value obtained for kC was 4.2-fold lower (0.81 × 10-4 ± 0.08 × 10-4 nM-1 s-1) compared to experiments with WT filaments (3.42 × 10-4 ± 0.22 × 10-4 nM-1 s-1). When heterofilaments were used, the effect of the mutation was reduced to a 2.2-fold difference compared to WT filaments (1.54 × 10-4 ± 0.11 × 10-4 nM-1 s-1).”

• Figure 5 B and C: the cosedimentation data do not seem to help elucidate the underlying mechanism. While the authors report statistical significance, differences are small, especially for gel densitometry measurements where the error is high, which suggests that there may be little biological significance. Importantly, example gels from these experiments should be shown, if not the complete set included in the supplement. In B, the higher cofilin concentrations would be expected to stabilize the filaments and thus the curve should be Ushaped.

We do not completely agree with the reviewer on this point. We think the co-sedimentation experiments are useful, as they show that cofilin-1 efficiently binds to mutant filaments, but is less efficient in stimulating disassembly in these endpoint-experiments. This information is not provided by the analysis of the effect of cofilin-1 on the bulk-depolymerization rate and adds to our understanding of the defect of the actin-cofilin interaction for the mutant.

While we agree with the reviewer on the point that co-sedimentation experiments must be repeated several times to produce reliable data, we cannot fully grasp the reasoning behind the statement “While the authors report statistical significance, differences are small, especially for gel densitometry measurements where the error is high, which suggests that there may be little biological significance.”. We interpret this statement as advice to be cautious when extrapolating the observed perturbances of cofilin-mediated actin dynamics in vitro to the in vivo context. We think we are cautious about this throughout the manuscript.

The author expects a U-shape curve, as high cofilin concentrations are reported to stabilize actin filaments by completely decorating the filament before severing-prone boundaries between cofilin-decorated and undecorated regions are generated. We have also performed these experiment with cytoskeletal β-actin and human cofilin-1 and never observed this U shape. This indicates that significant filament disassembly also happens at high cofilin concentrations, most likely directly after mixing of F-actin and cofilin. We cannot rule out that the incubation time plays an important role and that the U-shape only appears after longer incubation times. We also want to direct the reviewer to the publication “A Mechanism for Actin Filament Severing by Malaria Parasite Actin Depolymerizing Factor 1 via a Low Affinity Binding Interface” (Wong et al. 2013, JBC) in which comparable co-sedimentation experiments were performed (Figure 5E-G) with rabbit skeletal α-actin and human cofilin-1 and also no Ushaped curves were observed, even at higher molar excess of cofilin-1 compared to our experiments and with longer incubation times (1 hour vs. 10 minutes).

We now included an exemplary gel showing co-sedimentation experiments performed with WT, mutant actin and different concentrations of cofilin at pH 7.8 in the manuscript (Figure 5 – figure supplement 2)

• Figure 5 D: these data show that the binding of cofilin to WT and E334Q actin is approximately the same, with the mutant binding slightly more weakly. It would be clearer if the two plots were normalized to their respective plateaus since the difference in arbitrary units distracts from the conclusion of the figure. If the difference in the plateaus is meaningful, please explain.

As suggested by the reviewer, we normalized the data for a better understanding of the message conveyed.

• Figure 6: It is assumed that the authors are trying to show in this figure that cofilin binds both actins approximately the same but does not sever as readily for E334Q actin. The numerous parameters measured do not directly address what the authors are actually trying to show, which presumably is that the rate of severing is lower for E334Q than WT. It is therefore puzzling why no measurement of severing events per second per micron of actin in TIRF is made, which would give a more precise account of the underlying mechanism.

The severing rate as measured in TIRF is dependent on a number of parameters in a nonlinear manner. Therefore, we opted to show the combination of images directly showing the progress of the reaction and graphs summarizing the concomitant changes in cofilin clusters, actin filaments, actin-related fluorescence intensity and cofilin-related fluorescence intensity.

• Actin-activated steady-state ATPase data of the NM2A with mutant and WT actin would have been extremely useful and informative. The authors show the ability to make these types of measurements in the paper (NADH assay), and it is surprising that they are not included for assessing the myosin activity. It may be because of limited actin quantities. If this is the case, it should be indicated.

Indeed, the measurement of the steady-state actin-activated ATPase with recombinant cytoskeletal actin is very material-intensive and therefore costly, as a complete titration of actin is required for the generation of meaningful data. Since the vast majority of our assays involving a myosin family member were performed with NM2A-HMM, we decided to perform a full actin titration of the steady-state actin-activated ATPase of NM2A-HMM with WT and mutant filaments. The results of these experiments are now shown in Figure 8C. The panel showing the results used for determining the dissociation rate constants (k-A) for the interaction of NM2C-2R with p.E334Q or WT γ –actin in the absence of nucleotide was moved to the supplement (Figure 8 – figure supplement 2).

We added the following paragraph to the Material and Methods section concerning the Steady-State ATPase assay:

“For measurements of the basal and actin–activated NM2A–HMM ATPase, 0.5 µM MLCKtreated HMM was used. Phalloidin–stabilized WT or mutant F-actin was added over the range of 0–25 µM. The change in absorbance at 340 nm due to oxidation of NADH was recorded in a Multiskan FC Microplate Photometer (Thermo Fisher Scientific, Waltham, MA, USA). The data were fitted to the Michaelis-Menten equation to obtain values for the actin concentration at half-maximal activation of ATP-turnover (Kapp) and for the maximum ATP-turnover at saturated actin concentration (kcat).”

Furthermore, we added a description of the results of the experiments to the Results section of the manuscript:

“Using a NADH-coupled enzymatic assay, we determined the ability of p.E334Q and WT filaments to activate the ATPase of NM2A-HMM over the range of 0-25 µM F-actin (Figure 8C). While we observed no significant difference in Kapp, indicated by the actin concentration at half-maximal activation, in experiments with p.E334Q filaments (2.89 ± 0.49 µM) and WT filaments (3.20 ± 0.74 µM), we observed a 28% slower maximal ATP turnover at saturating actin concentration (kcat) with p.E334Q filaments (0.076 ± 0.005 s-1 vs. 0.097 ± 0.002 s-1).”

• (line 310) The authors state that they "noticed increased rapid dissociation and association events for E334Q filaments" in the motility assay. This observation motivates the authors to assess actin affinities of NM2A-HMM. Although differences in rigor and AM.ADP affinities are found between mutant and WT actins, the actin attachment lifetimes (many minutes) are unlikely to be related to the rapid association and dissociation event seen in the motility assay. Rather, this jiggling is more likely to be related to a lower duty ratio of the myosins, which appears to be the conclusion reached for the myosin-V data. These points should be clarified in the text.

We changed the text in accordance with the reviewer’ suggestion. It reads now: Cytoskeletal –actin filaments move with an average sliding velocity of 195.3 ± 5.0 nm s–1 on lawns of surface immobilized NM2A–HMM molecules (Figure 8A, B). For NM2A-HMM densities below about 10,000 molecules per μm2, the average sliding speed for cytoskeletal actin filaments drops steeply (Hundt et al, 2016). Filaments formed by p.E334Q actin move 5fold slower, resulting in an observed average sliding velocity of 39.1 ± 3.2 nm/s. Filaments copolymerized from a 1:1 mixture of WT and p.E334Q actin move with an average sliding velocity of 131.2 ± 10 nm s–1 (Figure 8A, B). When equal densities of surface-attached WT and mutant filaments were used, we observed that the number of rapid dissociation and association events increased markedly for p.E334Q filaments (Figure 8 – video supplement 7– 9).

Using a NADH-coupled enzymatic assay, we determined the ability of p.E334Q and WT filaments to activate the ATPase of NM2A-HMM over the range of 0-25 µM F-actin (Figure 8C). While we observed no significant difference in Kapp, indicated by the actin concentration at halfmaximal activation, in experiments with p.E334Q filaments (2.89 ± 0.49 µM) and WT filaments (3.20 ± 0.74 µM), we observed a 28% slower maximal ATP turnover at saturating actin concentration (kcat) with p.E334Q filaments (0.076 ± 0.005 s-1 vs. 0.097 ± 0.002 s-1). To investigate the impact of the mutation on actomyosin–affinity using transient–kinetic approaches, we determined the dissociation rate constants using a single–headed NM2A–2R construct (Figure 8D). …..

• (line 327) The authors report that the 1/K1 value is unchanged. There are no descriptions of this experiment in the paper. I am assuming the authors measured the ATP-induced dissociation of actomyosin and determined ATP affinity (K1) from this experiment. If this is the case, they should describe the experiment and show the data, provide a second-order rate constate for ATP binding, and report the max rate of dissociation (k2). This is a kinetic experiment done frequently by this group, so the absence of these details is surprising.

In the previous version of the manuscript, the method used to determine 1/K1 (ATP-induced dissociation of the actomyosin complex) was described in the Material and Methods paragraph “Transient kinetic analysis of the actomyosin complex” and the values obtained for 1/K1 were given in Table 1. We now included the experimental data as an additional figure in the manuscript (Figure 8 – figure supplement 3). Furthermore, we also give the maximal dissociation rate k+2 and the apparent second-order rate constant for ATP-binding (K1k+2) for the WT and mutant actomyosin complex in Table 1. Therefore, we changed the paragraph in the Results section concerning this experiment to:

“The apparent ATP–affinity (1/K1), the maximal dissociation rate of NM2A from F-actin in the presence of ATP (k+2), and the apparent second-order rate constant of ATP binding (K1k+2) showed no significant differences for complexes formed between NM2A and WT or p.E334Q filaments (Table 1, Figure 8 – figure supplement 3).”

and the section in the Material and Methods to:

“The apparent ATP–affinity of the actomyosin complex was determined by mixing the apyrase–treated, pyrene–labeled, phalloidin–stabilized actomyosin complex with increasing concentrations of ATP at the stopped–flow system. Fitting an exponential function to the individual transients yields the ATP–dependent dissociation rate of NM2A–2R from F–actin (kobs). The kobs–values were plotted against the corresponding ATP concentrations and a hyperbola was fitted to the data. The fit yields the apparent ATP–affinity (1/K1) of the actomyosin complex and the maximal dissociation rate k+2.

The apparent second–order rate constant for ATP binding (K1k+2) was determined by applying a linear fit to the data obtained at low ATP concentrations (0 – 25 µM).”

For a better understanding of the numerous rate and equilibrium constants, we have now included a figure showing the kinetic reaction scheme of the myosin ATPase cycle (Figure 8 – figure supplement 1).

Recommendations for the authors:

Reviewer #1:

• The subdomains of actin are mislabeled in Fig. 1A.

The labeling of the subdomains has been corrected.

• Additional experimental data addressing the 3 weaknesses noted in the public review would be informative but are not essential in my opinion. Examining the effect of cofilin on severing by the TIRF assay in more detail and using a processivity assay for myosin V (immobilized actin) would be the two aspects I would most value.

The TIRF assay for cofilin severing was performed initially over the cofilin concentration range from 20 to 250 nM. The results obtained in the presence of 100 nM cofilin allow a particularly informative depiction of the differences observed with mutant and WT actin. This applies to the image series showing the changes in filament length, cofilin clusters, and filament number as well as to the graphs showing time dependent changes in the number of filaments and total actin fluorescence. We have not included the results for a 50:50 mixture of WT:mutant actin because its attenuating effect is documented in several other experiments in the manuscript.

Our results with Myo5A show a less productive interaction with mutant actin filaments as indicated by a 1.7-fold reduction in the average sliding velocity and an increase in the optimal Myo5A-HMM surface density from 770 to 3100 molecules per µm2. These results indicate a reduction in binding affinity and coupling efficiency, with a likely impact on processivity. Given that Myo5A is only one of many cytoskeletal myosin motors and that the motor properties of all myosins are modulated by the presence of tropomyosin isoforms and other actin binding proteins, we expect only a small incremental gain in knowledge by performing additional experiments with an inverted assay geometry.

Reviewer #2:

• The authors should address the concerns regarding the statistical methodologies.

We have gone through the manuscript carefully to correct any errors in the statistics, as explained below.

Figure 1B, 5B, 5C, 5D, 8D, 9B, and 8 – figure supplement 2 all show the mean ± SD, as also correctly reported for Figure 8E and 8F in the figure legend. The statement, that these figures show the mean ± SEM was wrong and we corrected this mistake for all the listed figures. Furthermore, we now give the exact N for every experiment in the figure legend.

Figure 2C, 2E, 2F, 4B, 5A, 6B-E indeed showed the mean ± SEM. As the reviewer rightly points out, this is not the appropriate way to deal with such sample sizes. We therefore corrected the figures to show the mean ± SD.

We still refer to the mean ± SEM in Figure 2B, where elongation rates for more than 100 filaments were recorded, and in Figure 8B, where sliding velocities for several thousand actin filaments were measured.

• The authors should present the actin titration of the steady state ATPase activity for at least one of the myosins, or preferably all of them.

An actin titration of the steady state ATPase activity of NM-2A has been included in the revised version of the manuscript (Fig 8C).

• The authors should consider the use of pyrene-actin in measuring the assembly/disassembly of actin.

Values for the rate of actin assembly/disassembly measured with pyrene-actin are given in Table 1. Based on the small changes observed, we did not determine the critical actin concentration for the mutant construct.

Reviewer #1 (Public Review):

This paper is of importance to scientists interested in molecular mechanisms by which actin point mutations affect its function to ultimately lead to disease states. This work thoroughly characterizes the effect of the E334Q mutation in cytoplasmic gamma-actin on two binding partners: cofilin and myosin (non-muscle myosin 2 and myosin 5). Overall, the data showing effects on cofilin function and myosin binding are convincing and the experiments performed expertly using state-of-the art approaches. Additional binding partners of actin that were not examined here may also have altered function when interacting with the mutant actin.

Comments on revised version:

The authors seem to have done a pretty thorough job with the rebuttal.

Author Response

We thank both the editors and the Reviewers for their thoughtful comments and recommendations, that will certainly help us improve the manuscript. Below we address in a brief format some of the comments made, and then outline the changes to the manuscript that we plan to implement in the revision.

We see three interrelated issues in the comments of the Reviewers:

• the length and complexity of the manuscript;

• the link to previously proposed formalisms;

• the impact of adopting the proposed information-theoretic framework.

With regard to all of these issues, we would first like to highlight that the overall goal of our effort was to integrate con tributions to understanding the mechanisms underlying cognitive control across multiple different disciplines, using the information theoretic framework as a common formalism, while respecting and building on prior efforts as much as possible. Accordingly, we sought to be as explicit as possible about how we bridge from prior work using information theory, as well as neural networks and dynamical systems theory, which contributed to length of the original manuscript. While we continue to consider this an important goal, we will do our best to shorten and clarify the main exposition by reorganizing the manuscript as suggested by Reviewer #1 (i.e., in a way that is similar to what we did in our previous Nature Physics paper on multitasking). Specifically, we will move a substantially greater amount of the bridging material to the Supple mentary Information (SI), including the detailed discussion of the Stroop task, and the description of the link to Koechlin & Summerfield’s [L1] information theory formalism. We will also now include an outline of the full model at the beginning of the manuscript, that includes control and learning, and then more succinctly describe simplifications that focus on specific issues and applications in the remainder of the document.

Along similar lines, we will revise and harmonize our presentation of the formalism and notations, to make these more consistent, clearer and more concise throughout the document. Again, some of the inconsistencies in notation arose from our initial description of previous work, and in particular that of Koechlin & Summerfield[L1] that was an important inspiration for our work but that used slightly different notations. An important motivation for our introduction of new notation was that their formulation focused on the performance of a single task at a time, whereas a primary goal of our work was to extend the information theoretic treatment to simultaneous performance of multiple tasks. That is, in focusing on single tasks, Koechlin & Summerfield could refer to a task simply as a direct association between stimuli and responses, whereas we required a way of being able to refer to sets of tasks performed at once (”multitasks”), which in turn required specification of internal pathways. Moreover, they do not provide a mechanism to compute the conditional information Q(a|s) of a response/action s conditioned to a stimulus s does not provide a way to compute it explicitly. Our formalism instead provides a way to explicitly unpack this expression in terms of the efficacies –automatic (Eq. 5) or controlled (Eq. 15)– which can also account for the competition between different stimuli {s1, s2, . . . sn}. It also describes explicitly the competition between multiple tasks (Eq. 18, and Eq. 25 for multiple layers), because different ways of processing schemes for the same combinations of stimuli/responses can incur different levels of internal dependencies and thus require different control strategies.

To mitigate any confusion over terminology we will, as noted above, move a detailed discussion of Koechlin & Summer- field’s formulation, and how it maps to the one we present, to the SI, while taking care to introduce ours clearly at the beginning of the main document, and use it consistently throughout the remainder of the document. We will also make an important distinction – between informational and cognitive costs – more clearly, that we did not do adequately in the original manuscript.

Finally, to more clearly and concretely convey what we consider to be the most important contributions, we will restrict the number of examples we present to ones that relate most directly to the central points (e.g., the effect and limits of control in the presence of interference, and the differences in control strategy under limited temporal horizons). Accompanying our revision, we will also provide a full point-by-point response to the comments and questions raised by the Reviewers. We summarize some the key points we will address below.

PRELIMINARY REPLY TO THE REPORT OF REVIEWER #1

We want to thank the Reviewer for the time and effort put into reviewing our paper and constructive feedback that was provided. We also thank the Reviewer for recognizing the need for a clear computational account of how ”control” manages conflicts by scheduling tasks to be executed in parallel versus serially, and for the positive evaluation on our “efforts of the authors to give these intuitions a more concrete computational grounding.”. As noted in the general reply above, we regret the lack of clarity in several parts of the manuscript and in our introduction and use of the formalism. We consider the following to be the main points to be addressed:

• the role of task graphs and their mapping to standard neural architectures

• the description of entropy and related information-theoretic concepts;

• confusing choice of symbols in our notation between stimuli/responses and serialization/reconfiguration costs;

• missing definition of response time;

Regarding the first part point, we acknowledge that the network architectures we focus on do not draw direct inspiration from conventional machine learning models. Instead, our approach is rooted in the longstanding tradition of using (often simpler, but also more readily interpretable) neural network models to address human cognitive function and how this may be implemented in the brain [L2]; and, in particular, the mechanisms underlying cognitive control (e.g., [L3, L4]). In this context, we emphasize that, for analytical clarity, we deliberately abstract away from many biological details, in an effort to identify those principles of function that are most relevant to cognitive function. Nevertheless, our network architecture is inspired by two concepts that are central to neurobiological mechanisms of control: inhibition and gain modulation. Specifi- cally, we incorporate mutual inhibition among neural processing units, a feature represented by the parameter β. This aspect of our model is consistent with biologically inspired frameworks of neural processing, such as those discussed by Munakata et al. (2011)[L5], reflecting the competitive dynamics observed in neural circuits. Moreover, we introduce the parameter ν to represent a strictly modulatory form of control, akin to the role of neuromodulators in the brain. This modulatory control adjusts the sensitivity of a node to differences among its inputs (e.g., Servan-Schreiber, Printz, & Cohen, (1990)[L6]; Aston-Jones & Cohen (2005)[L7]). Finally, as the Reviewer notes, additional hidden layers can improve expressivity in neural networks, enabling the efficient implementation of more complex tasks, and are a universal feature of biological and artificial neural systems. We thus examined multitasking capability under the assumption that multiple hidden layers are present in a network; irrespective of whether they are needed to implement the corresponding tasks.

Regarding the second point, as noted above, we believe that the confusion arose from our review of the work by Koechlin & Summerfield. In their formalism, in which an action a is chosen (from a set of potential actions) with probability p(a), the cost of choosing that action is − log p(a). This is usually referred to as the information content or, alternatively, the localized entropy [L8]. As the Reviewer correctly observed, the canonical (Shannon) entropy is actually the expectation lEa[− log p(a)] over the localized entropies of a set of actions. In summarizing their formulation, we misleadingly stated that ”they used standard Shannon entropy formalism as a measure of the information required to select the action a.” We will now correct this to state: “[..] they used local entropy (− log p(a)) as a measure of the information required to select the action a, that can be treated as the cost of choosing that action.” We follow this formulation in our own, referring to informational cost as Ψ, and generalizing this to include cases in which more than one action may be chosen to perform at a time.

Regarding the third point, the confusion is due to our use of the letters S and R for both the stimulus and response units (in Sec. II.B) and then serialization and reconstruction costs (in eqs 31-33). We will fix this by renaming the serialization and reconstruction costs more explicitly as S er and Rec.

Finally, we realized we never explicitly stated the expression of the response time we used, but only pointed to it in the literature. In the manuscript we used the expression given in Eq. 53 of [L9], which provides response times as function of the error rates ER and the number of options .

PRELIMINARY REPLY TO THE REPORT OF REVIEWER #2

We want to thank the Reviewer for recognizing our effort to ”rigorously synthesize ideas about multi-tasking within an information-theoretic framework” and its potential. We also thank the Reviewer for the careful comments.

To our best understanding, and similarly to Reviewer #1, the main comments of the Reviewer are on:

• the length and density of the paper;

• the presentation of the Koechlin & Summerfield’s formalism, and the mismatch/lack of clarity of ours in certain points;

• the added value of the information theoretic formalism.

Regarding the first two points, which are common to Reviewer #1, we plan to move a significant part of the manuscript to the Supplementary Information, both to improve readability and make the manuscript shorter, as well as to provide one consistent and cleaner formalism (in particular with regards to the typos and errors highlighted by the Reviewer). In par- ticular, with respect to the comment on Eq. 4-5-6, we will clarify that the probability p[ fi j] is the probability that a certain input dimension (i in this case) is selected by on node j to produce its response (averaged over the individual inputs in each input dimension). We will also take care to make sure that the definition and domain of the various probabilities and probability distributions we use are clearly delineated (e.g. where the costs computed for tasks and task pathways come from).

Regarding the third point, we hope that our work offers value in at least two ways: i) it helps bring unity to ideas and descriptions about the capacity constraints associated with cognitive control that have previously been articulated in different forms (viz., neural networks, dynamical systems, and statistical mechanical accounts); and ii) doing so within an information theoretic framework not only lends rigor and precision to the formulation, but also allows us to cast the allocation of control in normative form – that is, as an optimization problem in which the agent seeks to minimize costs while maximizing gains. While we do not address specific empirical phenomena or datasets in the present treatment, we have done our best to provide examples showing that: a) our information theoretic formulation aligns with treatments using other formalisms that have been used to address empirical phenomena (e.g., with neural network models of the Stroop task); and b) our formulation can be used as a framework for providing a normative approach to widely studied empirical phenomena (e.g., the transition from control-dependent to automatic processing during skill acquisition) that, to date, have been addressed largely from a descriptive perspective; and that it can provide a formally rigorous approach to addressing such phenomena.

[L1] E. Koechlin and C. Summerfield, Trends in cognitive sciences 11, 229 (2007).

[L2] J. L. McClelland, D. E. Rumelhart, P. R. Group, et al., Explorations in the Microstructure of Cognition 2, 216 (1986).

[L3] J. D. Cohen, K. Dunbar, and J. L. McClelland, Psychological Review 97, 332 (1990).

[L4] E. K. Miller and J. D. Cohen, Annual review of neuroscience 24, 167 (2001).

[L5] Y. Munakata, S. A. Herd, C. H. Chatham, B. E. Depue, M. T. Banich, and R. C. O’Reilly, Trends in cognitive sciences 15, 453 (2011).

[L6] D. Servan-Schreiber, H. Printz, and J. D. Cohen, Science 249, 892 (1990).

[L7] G. Aston-Jones and J. D. Cohen, Annu. Rev. Neurosci. 28, 403 (2005).

[L8] T. F. Varley, Plos one 19, e0297128 (2024).

[L9] T. McMillen and P. Holmes, Journal of Mathematical Psychology 50, 30 (2006).

Author Response

Reviewer #1 (Public Review):

This study used a multi-day learning paradigm combined with fMRI to reveal neural changes reflecting the learning of new (arbitrary) shape-sound associations. In the scanner, the shapes and sounds are presented separately and together, both before and after learning. When they are presented together, they can be either consistent or inconsistent with the learned associations. The analyses focus on auditory and visual cortices, as well as the object-selective cortex (LOC) and anterior temporal lobe regions (temporal pole (TP) and perirhinal cortex (PRC)). Results revealed several learning-induced changes, particularly in the anterior temporal lobe regions. First, the LOC and PRC showed a reduced bias to shapes vs sounds (presented separately) after learning. Second, the TP responded more strongly to incongruent than congruent shape-sound pairs after learning. Third, the similarity of TP activity patterns to sounds and shapes (presented separately) was increased for non-matching shape-sound comparisons after learning. Fourth, when comparing the pattern similarity of individual features to combined shape-sound stimuli, the PRC showed a reduced bias towards visual features after learning. Finally, comparing patterns to combined shape-sound stimuli before and after learning revealed a reduced (and negative) similarity for incongruent combinations in PRC. These results are all interpreted as evidence for an explicit integrative code of newly learned multimodal objects, in which the whole is different from the sum of the parts.

The study has many strengths. It addresses a fundamental question that is of broad interest, the learning paradigm is well-designed and controlled, and the stimuli are real 3D stimuli that participants interact with. The manuscript is well written and the figures are very informative, clearly illustrating the analyses performed.

There are also some weaknesses. The sample size (N=17) is small for detecting the subtle effects of learning. Most of the statistical analyses are not corrected for multiple comparisons (ROIs), and the specificity of the key results to specific regions is also not tested. Furthermore, the evidence for an integrative representation is rather indirect, and alternative interpretations for these results are not considered.

We thank the reviewer for their careful reading and the positive comments on our manuscript. As suggested, we have conducted additional analyses of theoretically-motivated ROIs and have found that temporal pole and perirhinal cortex are the only regions to show the key experience-dependent transformations. We are much more cautious with respect to multiple comparisons, and have removed a series of post hoc across-ROI comparisons that were irrelevant to the key questions of the present manuscript. The revised manuscript now includes much more discussion about alternative interpretations as suggested by the reviewer (and also by the other reviewers).

Additionally, we looked into scanning more participants, but our scanner has since had a full upgrade and the sequence used in the current study is no longer supported by our scanner. However, we note that while most analyses contain 17 participants, we employed a within-subject learning design that is not typically used in fMRI experiments and increases our power to detect an effect. This is supported by the robust effect size of the behavioural data, whereby 17 out of 18 participants revealed a learning effect (Cohen’s D = 1.28) and which was replicated in a follow-up experiment with a larger sample size.

We address the other reviewer comments point-by-point in the below.

Reviewer #2 (Public Review):

Li et al. used a four-day fMRI design to investigate how unimodal feature information is combined, integrated, or abstracted to form a multimodal object representation. The experimental question is of great interest and understanding how the human brain combines featural information to form complex representations is relevant for a wide range of researchers in neuroscience, cognitive science, and AI. While most fMRI research on object representations is limited to visual information, the authors examined how visual and auditory information is integrated to form a multimodal object representation. The experimental design is elegant and clever. Three visual shapes and three auditory sounds were used as the unimodal features; the visual shapes were used to create 3D-printed objects. On Day 1, the participants interacted with the 3D objects to learn the visual features, but the objects were not paired with the auditory features, which were played separately. On Day 2, participants were scanned with fMRI while they were exposed to the unimodal visual and auditory features as well as pairs of visual-auditory cues. On Day 3, participants again interacted with the 3D objects but now each was paired with one of the three sounds that played from an internal speaker. On Day 4, participants completed the same fMRI scanning runs they completed on Day 2, except now some visual-auditory feature pairs corresponded with Congruent (learned) objects, and some with Incongruent (unlearned) objects. Using the same fMRI design on Days 2 and 4 enables a well-controlled comparison between feature- and object-evoked neural representations before and after learning. The notable results corresponded to findings in the perirhinal cortex and temporal pole. The authors report (1) that a visual bias on Day 2 for unimodal features in the perirhinal cortex was attenuated after learning on Day 4, (2) a decreased univariate response to congruent vs. incongruent visual-auditory objects in the temporal pole on Day 4, (3) decreased pattern similarity between congruent vs. incongruent pairs of visual and auditory unimodal features in the temporal pole on Day 4, (4) in the perirhinal cortex, visual unimodal features on Day 2 do not correlate with their respective visual-auditory objects on Day 4, and (5) in the perirhinal cortex, multimodal object representations across Days 2 and 4 are uncorrelated for congruent objects and anticorrelated for incongruent. The authors claim that each of these results supports the theory that multimodal objects are represented in an "explicit integrative" code separate from feature representations. While these data are valuable and the results are interesting, the authors' claims are not well supported by their findings.

We thank the reviewer for the careful reading of our manuscript and positive comments. Overall, we now stay closer to the data when describing the results and provide our interpretation of these results in the discussion section while remaining open to alternative interpretations (as also suggested by Reviewer 1).

(1) In the introduction, the authors contrast two theories: (a) multimodal objects are represented in the co-activation of unimodal features, and (b) multimodal objects are represented in an explicit integrative code such that the whole is different than the sum of its parts. However, the distinction between these two theories is not straightforward. An explanation of what is precisely meant by "explicit" and "integrative" would clarify the authors' theoretical stance. Perhaps we can assume that an "explicit" representation is a new representation that is created to represent a multimodal object. What is meant by "integrative" is more ambiguous-unimodal features could be integrated within a representation in a manner that preserves the decodability of the unimodal features, or alternatively the multimodal representation could be completely abstracted away from the constituent features such that the features are no longer decodable. Even if the object representation is "explicit" and distinct from the unimodal feature representations, it can in theory still contain featural information, though perhaps warped or transformed. The authors do not clearly commit to a degree of featural abstraction in their theory of "explicit integrative" multimodal object representations which makes it difficult to assess the validity of their claims.

Due to its ambiguity, we removed the term “explicit” and now make it clear that our central question was whether crossmodal object representations require only unimodal feature-level representations (e.g., frogs are created from only the combination of shape and sound) or whether crossmodal object representations also rely on an integrative code distinct from the unimodal features (e.g., there is something more to “frog” than its original shape and sound). We now clarify this in the revised manuscript.

“One theoretical view from the cognitive sciences suggests that crossmodal objects are built from component unimodal features represented across distributed sensory regions.8 Under this view, when a child thinks about “frog”, the visual cortex represents the appearance of the shape of the frog whereas the auditory cortex represents the croaking sound. Alternatively, other theoretical views predict that multisensory objects are not only built from their component unimodal sensory features, but that there is also a crossmodal integrative code that is different from the sum of these parts.9,10,11,12,13 These latter views propose that anterior temporal lobe structures can act as a polymodal “hub” that combines separate features into integrated wholes.9,11,14,15” – pg. 4

For this reason, we designed our paradigm to equate the unimodal representations, such that neural differences between the congruent and incongruent conditions provide evidence for a crossmodal integrative code different from the unimodal features (because the unimodal features are equated by default in the design).

“Critically, our four-day learning task allowed us to isolate any neural activity associated with integrative coding in anterior temporal lobe structures that emerges with experience and differs from the neural patterns recorded at baseline. The learned and non-learned crossmodal objects were constructed from the same set of three validated shape and sound features, ensuring that factors such as familiarity with the unimodal features, subjective similarity, and feature identity were tightly controlled (Figure 2). If the mind represented crossmodal objects entirely as the reactivation of unimodal shapes and sounds (i.e., objects are constructed from their parts), then there should be no difference between the learned and non-learned objects (because they were created from the same three shapes and sounds). By contrast, if the mind represented crossmodal objects as something over and above their component features (i.e., representations for crossmodal objects rely on integrative coding that is different from the sum of their parts), then there should be behavioral and neural differences between learned and non-learned crossmodal objects (because the only difference across the objects is the learned relationship between the parts). Furthermore, this design allowed us to determine the relationship between the object representation acquired after crossmodal learning and the unimodal feature representations acquired before crossmodal learning. That is, we could examine whether learning led to abstraction of the object representations such that it no longer resembled the unimodal feature representations.” – pg. 5

Furthermore, we agree with the reviewer that our definition and methodological design does not directly capture the structure of the integrative code. With experience, the unimodal feature representations may be completely abstracted away, warped, or changed in a nonlinear transformation. We suggest that crossmodal learning forms an integrative code that is different from the original unimodal representations in the anterior temporal lobes, however, we agree that future work is needed to more directly capture the structure of the integrative code that emerges with experience.

“In our task, participants had to differentiate congruent and incongruent objects constructed from the same three shape and sound features (Figure 2). An efficient way to solve this task would be to form distinct object-level outputs from the overlapping unimodal feature-level inputs such that congruent objects are made to be orthogonal from the representations before learning (i.e., measured as pattern similarity equal to 0 in the perirhinal cortex; Figure 5b, 6, Supplemental Figure S5), whereas non-learned incongruent objects could be made to be dissimilar from the representations before learning (i.e., anticorrelation, measured as patten similarity less than 0 in the perirhinal cortex; Figure 6). Because our paradigm could decouple neural responses to the learned object representations (on Day 4) from the original component unimodal features at baseline (on Day 2), these results could be taken as evidence of pattern separation in the human perirhinal cortex.11,12 However, our pattern of results could also be explained by other types of crossmodal integrative coding. For example, incongruent object representations may be less stable than congruent object representations, such that incongruent objects representation are warped to a greater extent than congruent objects (Figure 6).” – pg. 18

“As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation.” – pg. 18

(2) After participants learned the multimodal objects, the authors report a decreased univariate response to congruent visual-auditory objects relative to incongruent objects in the temporal pole. This is claimed to support the existence of an explicit, integrative code for multimodal objects. Given the number of alternative explanations for this finding, this claim seems unwarranted. A simpler interpretation of these results is that the temporal pole is responding to the novelty of the incongruent visual-auditory objects. If there is in fact an explicit, integrative multimodal object representation in the temporal pole, it is unclear why this would manifest in a decreased univariate response.

We thank the reviewer for identifying this issue. Our behavioural design controls unimodal feature-level novelty but allows object-level novelty to differ. Thus, neural differences between the congruent and incongruent conditions reflects sensitivity to the object-level differences between the combination of shape and sound. However, we agree that there are multiple interpretations regarding the nature of how the integrative code is structured in the temporal pole and perirhinal cortex. We have removed the interpretation highlighted by the reviewer from the results. Instead, we now provide our preferred interpretation in the discussion, while acknowledging the other possibilities that the reviewer mentions.

As one possibility, these results in temporal pole may reflect “conceptual combination”. “hummingbird” – a congruent pairing – may require less neural resources than an incongruent pairing such as “bark-frog”.

“Furthermore, these distinct anterior temporal lobe structures may be involved with integrative coding in different ways. For example, the crossmodal object representations measured after learning were found to be related to the component unimodal feature representations measured before learning in the temporal pole but not the perirhinal cortex (Figure 5, 6, Supplemental Figure S5). Moreover, pattern similarity for congruent shape-sound pairs were lower than the pattern similarity for incongruent shape-sound pairs after crossmodal learning in the temporal pole but not the perirhinal cortex (Figure 4b, Supplemental Figure S3a). As one interpretation of this pattern of results, the temporal pole may represent new crossmodal objects by combining previously learned knowledge. 8,9,10,11,13,14,15,33 Specifically, research into conceptual combination has linked the anterior temporal lobes to compound object concepts such as “hummingbird”.34,35,36 For example, participants during our task may have represented the sound-based “humming” concept and visually-based “bird” concept on Day 1, forming the crossmodal “hummingbird” concept on Day 3; Figure 1, 2, which may recruit less activity in temporal pole than an incongruent pairing such as “barking-frog”. For these reasons, the temporal pole may form a crossmodal object code based on pre-existing knowledge, resulting in reduced neural activity (Figure 3d) and pattern similarity towards features associated with learned objects (Figure 4b).”– pg. 18

(3) The authors ran a neural pattern similarity analysis on the unimodal features before and after multimodal object learning. They found that the similarity between visual and auditory features that composed congruent objects decreased in the temporal pole after multimodal object learning. This was interpreted to reflect an explicit integrative code for multimodal objects, though it is not clear why. First, behavioral data show that participants reported increased similarity between the visual and auditory unimodal features within congruent objects after learning, the opposite of what was found in the temporal pole. Second, it is unclear why an analysis of the unimodal features would be interpreted to reflect the nature of the multimodal object representations. Since the same features corresponded with both congruent and incongruent objects, the nature of the feature representations cannot be interpreted to reflect the nature of the object representations per se. Third, using unimodal feature representations to make claims about object representations seems to contradict the theoretical claim that explicit, integrative object representations are distinct from unimodal features. If the learned multimodal object representation exists separately from the unimodal feature representations, there is no reason why the unimodal features themselves would be influenced by the formation of the object representation. Instead, these results seem to more strongly support the theory that multimodal object learning results in a transformation or warping of feature space.

We apologize for the lack of clarity. We have now overhauled this aspect of our manuscript in an attempt to better highlight key aspects of our experimental design. In particular, because the unimodal features composing the congruent and incongruent objects were equated, neural differences between these conditions would provide evidence for an experience-dependent crossmodal integrative code that is different from its component unimodal features.

Related to the second and third points, we were looking at the extent to which the original unimodal representations change with crossmodal learning. Before crossmodal learning, we found that the perirhinal cortex tracked the similarity between the individual visual shape features and the crossmodal objects that were composed of those visual shapes – however, there was no evidence that perirhinal cortex was tracking the unimodal sound features on those crossmodal objects. After crossmodal learning, we see that this visual shape bias in perirhinal cortex was no longer present – that is, the representation in perirhinal cortex started to look less like the visual features that comprise the objects. Thus, crossmodal learning transformed the perirhinal representations so that they were no longer predominantly grounded in a single visual modality, which may be a mechanism by which object concepts gain their abstraction. We have now tried to be clearer about this interpretation throughout the paper.

Notably, we suggest that experience may change both the crossmodal object representations, as well as the unimodal feature representations. For example, we have previously shown that unimodal visual features are influenced by experience in parallel with the representation of the conjunction (e.g., Liang et al., 2020; Cerebral Cortex). Nevertheless, we remain open to the myriad possible structures of the integrative code that might emerge with experience.

We now clarify these points throughout the manuscript. For example:

“We then examined whether the original representations would change after participants learned how the features were paired together to make specific crossmodal objects, conducting the same analysis described above after crossmodal learning had taken place (Figure 5b). With this analysis, we sought to measure the relationship between the representation for the learned crossmodal object and the original baseline representation for the unimodal features. More specifically, the voxel-wise activity for unimodal feature runs before crossmodal learning was correlated to the voxel-wise activity for crossmodal object runs after crossmodal learning (Figure 5b). Another linear mixed model which included modality as a fixed factor within each ROI revealed that the perirhinal cortex was no longer biased towards visual shape after crossmodal learning (F1,32 = 0.12, p = 0.73), whereas the temporal pole, LOC, V1, and A1 remained biased towards either visual shape or sound (F1,30-32 between 16.20 and 73.42, all p < 0.001, η2 between 0.35 and 0.70).” – pg. 14

“To investigate this effect in perirhinal cortex more specifically, we conducted a linear mixed model to directly compare the change in the visual bias of perirhinal representations from before crossmodal learning to after crossmodal learning (green regions in Figure 5a vs. 5b). Specifically, the linear mixed model included learning day (before vs. after crossmodal learning) and modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object). Results revealed a significant interaction between learning day and modality in the perirhinal cortex (F1,775 = 5.56, p = 0.019, η2 = 0.071), meaning that the baseline visual shape bias observed in perirhinal cortex (green region of Figure 5a) was significantly attenuated with experience (green region of Figure 5b). After crossmodal learning, a given shape no longer invoked significant pattern similarity between objects that had the same shape but differed in terms of what they sounded like. Taken together, these results suggest that prior to learning the crossmodal objects, the perirhinal cortex had a default bias toward representing the visual shape information and was not representing sound information of the crossmodal objects. After crossmodal learning, however, the visual shape bias in perirhinal cortex was no longer present. That is, with crossmodal learning, the representations within perirhinal cortex started to look less like the visual features that comprised the crossmodal objects, providing evidence that the perirhinal representations were no longer predominantly grounded in the visual modality.” – pg. 13

“Importantly, the initial visual shape bias observed in the perirhinal cortex was attenuated by experience (Figure 5, Supplemental Figure S5), suggesting that the perirhinal representations had become abstracted and were no longer predominantly grounded in a single modality after crossmodal learning. One possibility may be that the perirhinal cortex is by default visually driven as an extension to the ventral visual stream,10,11,12 but can act as a polymodal “hub” region for additional crossmodal input following learning.” – pg. 19

(4) The most compelling evidence the authors provide for their theoretical claims is the finding that, in the perirhinal cortex, the unimodal feature representations on Day 2 do not correlate with the multimodal objects they comprise on Day 4. This suggests that the learned multimodal object representations are not combinations of their unimodal features. If unimodal features are not decodable within the congruent object representations, this would support the authors' explicit integrative hypothesis. However, the analyses provided do not go all the way in convincing the reader of this claim. First, the analyses reported do not differentiate between congruent and incongruent objects. If this result in the perirhinal cortex reflects the formation of new multimodal object representations, it should only be true for congruent objects but not incongruent objects. Since the analyses combine congruent and incongruent objects it is not possible to know whether this was the case. Second, just because feature representations on Day 2 do not correlate with multimodal object patterns on Day 4 does not mean that the object representations on Day 4 do not contain featural information. This could be directly tested by correlating feature representations on Day 4 with congruent vs. incongruent object representations on Day 4. It could be that representations in the perirhinal cortex are not stable over time and all representations-including unimodal feature representations-shift between sessions, which could explain these results yet not entail the existence of abstracted object representations.

We thank the reviewer for this suggestion and have conducted the two additional analyses. Specifically, we split the congruent and incongruent conditions and also investigated correlations between unimodal representations on Day 4 with crossmodal object representations on Day 4. There was no significant interaction between modality and congruency in any ROI across or within learning days. One possible explanation for these findings is that both congruent and incongruent crossmodal objects are represented differently from their underlying unimodal features, and all of these representations can transform with experience.

However, the new analyses also revealed that perirhinal cortex was the only region without a modality-specific bias after crossmodal learning (e.g., Day 4 Unimodal Feature runs x Day 4 Crossmodal Object runs; now shown in Supplemental Figure S5). Overall, these results are consistent with the notion of a crossmodal integrative code in perirhinal cortex that has changed with experience and is different from the component unimodal features. Nevertheless, we explore alternative interpretations for how the crossmodal code emerges with experience in the discussion.

“To examine whether these results differed by congruency (i.e., whether any modality-specific biases differed as a function of whether the object was congruent or incongruent), we conducted exploratory linear mixed models for each of the five a priori ROIs across learning days. More specifically, we correlated: 1) the voxel-wise activity for Unimodal Feature Runs before crossmodal learning to the voxel-wise activity for Crossmodal Object Runs before crossmodal learning (Day 2 vs. Day 2), 2) the voxel-wise activity for Unimodal Feature Runs before crossmodal learning to the voxel-wise activity for Crossmodal Object Runs after crossmodal learning (Day 2 vs Day 4), and 3) the voxel-wise activity for Unimodal Feature Runs after crossmodal learning to the voxel-wise activity for Crossmodal Object Runs after crossmodal learning (Day 4 vs Day 4). For each of the three analyses described, we then conducted separate linear mixed models which included modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object) and congruency (congruent vs. incongruent)….There was no significant relationship between modality and congruency in any ROI between Day 2 and Day 2 (F1,346-368 between 0.00 and 1.06, p between 0.30 and 0.99), between Day 2 and Day 4 (F1,346-368 between 0.021 and 0.91, p between 0.34 and 0.89), or between Day 4 and Day 4 (F1,346-368 between 0.01 and 3.05, p between 0.082 and 0.93). However, exploratory analyses revealed that perirhinal cortex was the only region without a modality-specific bias and where the unimodal feature runs were not significantly correlated to the crossmodal object runs after crossmodal learning (Supplemental Figure S5).” – pg. 14

“Taken together, the overall pattern of results suggests that representations of the crossmodal objects in perirhinal cortex were heavily influenced by their consistent visual features before crossmodal learning. However, the crossmodal object representations were no longer influenced by the component visual features after crossmodal learning (Figure 5, Supplemental Figure S5). Additional exploratory analyses did not find evidence of experience-dependent changes in the hippocampus or inferior parietal lobes (Supplemental Figure S4c-e).” – pg. 14

“The voxel-wise matrix for Unimodal Feature runs on Day 4 were correlated to the voxel-wise matrix for Crossmodal Object runs on Day 4 (see Figure 5 in the main text for an example). We compared the average pattern similarity (z-transformed Pearson correlation) between shape (blue) and sound (orange) features specifically after crossmodal learning. Consistent with Figure 5b, perirhinal cortex was the only region without a modality-specific bias. Furthermore, perirhinal cortex was the only region where the representations of both the visual and sound features were not significantly correlated to the crossmodal objects. By contrast, every other region maintained a modality-specific bias for either the visual or sound features. These results suggest that perirhinal cortex representations were transformed with experience, such that the initial visual shape representations (Figure 5a) were no longer grounded in a single modality after crossmodal learning. Furthermore, these results suggest that crossmodal learning formed an integrative code different from the unimodal features in perirhinal cortex, as the visual and sound features were not significantly correlated with the crossmodal objects. * p < 0.05, ** p < 0.01, *** p < 0.001. Horizontal lines within brain regions indicate a significant main effect of modality. Vertical asterisks denote pattern similarity comparisons relative to 0.” – Supplemental Figure S5

“We found that the temporal pole and perirhinal cortex – two anterior temporal lobe structures – came to represent new crossmodal object concepts with learning, such that the acquired crossmodal object representations were different from the representation of the constituent unimodal features (Figure 5, 6). Intriguingly, the perirhinal cortex was by default biased towards visual shape, but that this initial visual bias was attenuated with experience (Figure 3c, 5, Supplemental Figure S5). Within the perirhinal cortex, the acquired crossmodal object concepts (measured after crossmodal learning) became less similar to their original component unimodal features (measured at baseline before crossmodal learning); Figure 5, 6, Supplemental Figure S5. This is consistent with the idea that object representations in perirhinal cortex integrate the component sensory features into a whole that is different from the sum of the component parts, which might be a mechanism by which object concepts obtain their abstraction…. As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation.” – pg. 18

In sum, the authors have collected a fantastic dataset that has the potential to answer questions about the formation of multimodal object representations in the brain. A more precise delineation of different theoretical accounts and additional analyses are needed to provide convincing support for the theory that “explicit integrative” multimodal object representations are formed during learning.

We thank the reviewer for the positive comments and helpful feedback. We hope that our changes to our wording and clarifications to our methodology now more clearly supports the central goal of our study: to find evidence of crossmodal integrative coding different from the original unimodal feature parts in anterior temporal lobe structures. We furthermore agree that future research is needed to delineate the structure of the integrative code that emerges with experience in the anterior temporal lobes.

Reviewer #3 (Public Review):

This paper uses behavior and functional brain imaging to understand how neural and cognitive representations of visual and auditory stimuli change as participants learn associations among them. Prior work suggests that areas in the anterior temporal (ATL) and perirhinal cortex play an important role in learning/representing cross-modal associations, but the hypothesis has not been directly tested by evaluating behavior and functional imaging before and after learning cross- modal associations. The results show that such learning changes both the perceived similarities amongst stimuli and the neural responses generated within ATL and perirhinal regions, providing novel support for the view that cross-modal learning leads to a representational change in these regions.

This work has several strengths. It tackles an important question for current theories of object representation in the mind and brain in a novel and quite direct fashion, by studying how these representations change with cross-modal learning. As the authors note, little work has directly assessed representational change in ATL following such learning, despite the widespread view that ATL is critical for such representation. Indeed, such direct assessment poses several methodological challenges, which the authors have met with an ingenious experimental design. The experiment allows the authors to maintain tight control over both the familiarity and the perceived similarities amongst the shapes and sounds that comprise their stimuli so that the observed changes across sessions must reflect learned cross-modal associations among these. I especially appreciated the creation of physical objects that participants can explore and the approach to learning in which shapes and sounds are initially experienced independently and later in an associated fashion. In using multi-echo MRI to resolve signals in ventral ATL, the authors have minimized a key challenge facing much work in this area (namely the poor SNR yielded by standard acquisition sequences in ventral ATL). The use of both univariate and multivariate techniques was well-motivated and helpful in testing the central questions. The manuscript is, for the most part, clearly written, and nicely connects the current work to important questions in two literatures, specifically (1) the hypothesized role of the perirhinal cortex in representing/learning complex conjunctions of features and (2) the tension between purely embodied approaches to semantic representation vs the view that ATL regions encode important amodal/crossmodal structure.

There are some places in the manuscript that would benefit from further explanation and methodological detail. I also had some questions about the results themselves and what they signify about the roles of ATL and the perirhinal cortex in object representation.

We thank the reviewer for their positive feedback and address the comments in the below point-by-point responses.

(A) I found the terms "features" and "objects" to be confusing as used throughout the manuscript, and sometimes inconsistent. I think by "features" the authors mean the shape and sound stimuli in their experiment. I think by "object" the authors usually mean the conjunction of a shape with a sound---for instance, when a shape and sound are simultaneously experienced in the scanner, or when the participant presses a button on the shape and hears the sound. The confusion comes partly because shapes are often described as being composed of features, not features in and of themselves. (The same is sometimes true of sounds). So when reading "features" I kept thinking the paper referred to the elements that went together to comprise a shape. It also comes from ambiguous use of the word object, which might refer to (a) the 3D- printed item that people play with, which is an object, or (b) a visually-presented shape (for instance, the localizer involved comparing an "object" to a "phase-scrambled" stimulus---here I assume "object" refers to an intact visual stimulus and not the joint presentation of visual and auditory items). I think the design, stimuli, and results would be easier for a naive reader to follow if the authors used the terms "unimodal representation" to refer to cases where only visual or auditory input is presented, and "cross-modal" or "conjoint" representation when both are present.

We thank the reviewer for this suggestion and agree. We have replaced the terms “features” and “objects” with “unimodal” and “crossmodal” in the title, text, and figures throughout the manuscript for consistency (i.e., “crossmodal binding problem”). To simplify the terminology, we have also removed the localizer results.

(B) There are a few places where I wasn't sure what exactly was done, and where the methods lacked sufficient detail for another scientist to replicate what was done. Specifically:

(1) The behavioral study assessing perceptual similarity between visual and auditory stimuli was unclear. The procedure, stimuli, number of trials, etc, should be explained in sufficient detail in methods to allow replication. The results of the study should also minimally be reported in the supplementary information. Without an understanding of how these studies were carried out, it was very difficult to understand the observed pattern of behavioral change. For instance, I initially thought separate behavioral blocks were carried out for visual versus auditory stimuli, each presented in isolation; however, the effects contrast congruent and incongruent stimuli, which suggests these decisions must have been made for the conjoint presentation of both modalities. I'm still not sure how this worked. Additionally, the manuscript makes a brief mention that similarity judgments were made in the context of "all stimuli," but I didn't understand what that meant. Similarity ratings are hugely sensitive to the contrast set with which items appear, so clarity on these points is pretty important. A strength of the design is the contention that shape and sound stimuli were psychophysically matched, so it is important to show the reader how this was done and what the results were.

We agree and apologize for the lack of sufficient detail in the original manuscript. We now include much more detail about the similarity rating task. The methodology and results of the behavioral rating experiments are now shown in Supplemental Figure S1. In Figure S1a, the similarity ratings are visualized on a multidimensional scaling plot. The triangular geometry for shape (blue) and sound (red) indicate that the subjective similarity was equated within each unimodal feature across individual participants. Quantitatively, there was no difference in similarity between the congruent and incongruent pairings in Figure S1b and Figure S1c prior to crossmodal learning. In addition to providing more information on these methods in the Supplemental Information, we also now provide a more detailed description of the task in the manuscript itself. For convenience, we reproduce these sections below.

“Pairwise Similarity Task. Using the same task as the stimulus validation procedure (Supplemental Figure S1a), participants provided similarity ratings for all combinations of the 3 validated shapes and 3 validated sounds (each of the six features were rated in the context of every other feature in the set, with 4 repeats of the same feature, for a total of 72 trials). More specifically, three stimuli were displayed on each trial, with one at the top and two at the bottom of the screen in the same procedure as we have used previously27. The 3D shapes were visually displayed as a photo, whereas sounds were displayed on screen in a box that could be played over headphones when clicked with the mouse. The participant made an initial judgment by selecting the more similar stimulus on the bottom relative to the stimulus on the top. Afterwards, the participant made a similarity rating between each bottom stimulus with the top stimulus from 0 being no similarity to 5 being identical. This procedure ensured that ratings were made relative to all other stimuli in the set.”– pg. 28

“Pairwise similarity task and results. In the initial stimulus validation experiment, participants provided pairwise ratings for 5 sounds and 3 shapes. The shapes were equated in their subjective similarity that had been selected from a well-characterized perceptually uniform stimulus space27 and the pairwise ratings followed the same procedure as described in ref 27. Based on this initial experiment, we then selected the 3 sounds from the that were most closely equated in their subjective similarity. (a) 3D-printed shapes were displayed as images, whereas sounds were displayed in a box that could be played when clicked by the participant. Ratings were averaged to produce a similarity matrix for each participant, and then averaged to produce a group-level similarity matrix. Shown as triangular representational geometries recovered from multidimensional scaling in the above, shapes (blue) and sounds (orange) were approximately equated in their subjective similarity. These features were then used in the four-day crossmodal learning task. (b) Behavioral results from the four-day crossmodal learning task paired with multi-echo fMRI described in the main text. Before crossmodal learning, there was no difference in similarity between shape and sound features associated with congruent objects compared to incongruent objects – indicating that similarity was controlled at the unimodal feature-level. After crossmodal learning, we observed a robust shift in the magnitude of similarity. The shape and sound features associated with congruent objects were now significantly more similar than the same shape and sound features associated with incongruent objects (p < 0.001), evidence that crossmodal learning changed how participants experienced the unimodal features (observed in 17/18 participants). (c) We replicated this learning-related shift in pattern similarity with a larger sample size (n = 44; observed in 38/44 participants). *** denotes p < 0.001. Horizontal lines denote the comparison of congruent vs. incongruent conditions. – Supplemental Figure S1

(2) The experiences through which participants learned/experienced the shapes and sounds were unclear. The methods mention that they had one minute to explore/palpate each shape and that these experiences were interleaved with other tasks, but it is not clear what the other tasks were, how many such exploration experiences occurred, or how long the total learning time was. The manuscript also mentions that participants learn the shape-sound associations with 100% accuracy but it isn't clear how that was assessed. These details are important partly b/c it seems like very minimal experience to change neural representations in the cortex.

We apologize for the lack of detail and agree with the reviewer’s suggestions – we now include much more information in the methods section. Each behavioral day required about 1 hour of total time to complete, and indeed, participants rapidly learned their associations with minimal experience. For example:

“Behavioral Tasks. On each behavioral day (Day 1 and Day 3; Figure 2), participants completed the following tasks, in this order: Exploration Phase, one Unimodal Feature 1-back run (26 trials), Exploration Phase, one Crossmodal 1-back run (26 trials), Exploration Phase, Pairwise Similarity Task (24 trials), Exploration Phase, Pairwise Similarity Task (24 trials), Exploration Phase, Pairwise Similarity Task (24 trials), and finally, Exploration Phase. To verify learning on Day 3, participants also additionally completed a Learning Verification Task at the end of the session. – pg. 27

“The overall procedure ensured that participants extensively explored the unimodal features on Day 1 and the crossmodal objects on Day 3. The Unimodal Feature and the Crossmodal Object 1-back runs administered on Day 1 and Day 3 served as practice for the neuroimaging sessions on Day 2 and Day 4, during which these 1-back tasks were completed. Each behavioral session required less than 1 hour of total time to complete.” – pg. 27

“Learning Verification Task (Day 3 only). As the final task on Day 3, participants completed a task to ensure that participants successfully formed their crossmodal pairing. All three shapes and sounds were randomly displayed in 6 boxes on a display. Photos of the 3D shapes were shown, and sounds were played by clicking the box with the mouse cursor. The participant was cued with either a shape or sound, and then selected the corresponding paired feature. At the end of Day 3, we found that all participants reached 100% accuracy on this task (10 trials).” – pg. 29

(3) I didn't understand the similarity metric used in the multivariate imaging analyses. The manuscript mentions Z-scored Pearson's r, but I didn't know if this meant (a) many Pearson coefficients were computed and these were then Z-scored, so that 0 indicates a value equal to the mean Pearson correlation and 1 is equal to the standard deviation of the correlations, or (b) whether a Fisher Z transform was applied to each r (so that 0 means r was also around 0). From the interpretation of some results, I think the latter is the approach taken, but in general, it would be helpful to see, in Methods or Supplementary information, exactly how similarity scores were computed, and why that approach was adopted. This is particularly important since it is hard to understand the direction of some key effects.

The reviewer is correct that the Fisher Z transform was applied to each individual r before averaging the correlations. This approach is generally recommended when averaging correlations (see Corey, Dunlap, & Burke, 1998). We are now clearer on this point in the manuscript:

“The z-transformed Pearson’s correlation coefficient was used as the distance metric for all pattern similarity analyses. More specifically, each individual Pearson correlation was Fisher z-transformed and then averaged (see 61).” – pg. 32

(C) From Figure 3D, the temporal pole mask appears to exclude the anterior fusiform cortex (or the ventral surface of the ATL generally). If so, this is a shame, since that appears to be the locus most important to cross-modal integration in the "hub and spokes" model of semantic representation in the brain. The observation in the paper that the perirhinal cortex seems initially biased toward visual structure while more superior ATL is biased toward auditory structure appears generally consistent with the "graded hub" view expressed, for instance, in our group's 2017 review paper (Lambon Ralph et al., Nature Reviews Neuroscience). The balance of visual- versus auditory-sensitivity in that work appears balanced in the anterior fusiform, just a little lateral to the anterior perirhinal cortex. It would be helpful to know if the same pattern is observed for this area specifically in the current dataset.

We thank the reviewer for this suggestion. After close inspection of Lambon Ralph et al. (2017), we believe that our perirhinal cortex mask appears to be overlapping with the ventral ATL/anterior fusiform region that the reviewer mentions. See Author response image 1 for a visual comparison:

Author response image 1.

The top four figures are sampled from Lambon Ralph et al (2017), whereas the bottom two figures visualize our perirhinal cortex mask (white) and temporal pole mask (dark green) relative to the fusiform cortex. The ROIs visualized were defined from the Harvard-Oxford atlas.

We now mention this area of overlap in our manuscript and link it to the hub and spokes model:

“Notably, our perirhinal cortex mask overlaps with a key region of the ventral anterior temporal lobe thought to be the central locus of crossmodal integration in the “hub and spokes” model of semantic representations.9,50 – pg. 20

(D) While most effects seem robust from the information presented, I'm not so sure about the analysis of the perirhinal cortex shown in Figure 5. This compares (I think) the neural similarity evoked by a unimodal stimulus ("feature") to that evoked by the same stimulus when paired with its congruent stimulus in the other modality ("object"). These similarities show an interaction with modality prior to cross-modal association, but no interaction afterward, leading the authors to suggest that the perirhinal cortex has become less biased toward visual structure following learning. But the plots in Figures 4a and b are shown against different scales on the y-axes, obscuring the fact that all of the similarities are smaller in the after-learning comparison. Since the perirhinal interaction was already the smallest effect in the pre-learning analysis, it isn't really surprising that it drops below significance when all the effects diminish in the second comparison. A more rigorous test would assess the reliability of the interaction of comparison (pre- or post-learning) with modality. The possibility that perirhinal representations become less "visual" following cross-modal learning is potentially important so a post hoc contrast of that kind would be helpful.

We apologize for the lack of clarity. We conducted a linear mixed model to assess the interaction between modality and crossmodal learning day (before and after crossmodal learning) in the perirhinal cortex as described by the reviewer. The critical interaction was significant, which is now clarified in the text as well as in the rescaled figure plots.

“To investigate this effect in perirhinal cortex more specifically, we conducted a linear mixed model to directly compare the change in the visual bias of perirhinal representations from before crossmodal learning to after crossmodal learning (green regions in Figure 5a vs. 5b). Specifically, the linear mixed model included learning day (before vs. after crossmodal learning) and modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object). Results revealed a significant interaction between learning day and modality in the perirhinal cortex (F1,775 = 5.56, p = 0.019, η2 = 0.071), meaning that the baseline visual shape bias observed in perirhinal cortex (green region of Figure 5a) was significantly attenuated with experience (green region of Figure 5b). After crossmodal learning, a given shape no longer invoked significant pattern similarity between objects that had the same shape but differed in terms of what they sounded like. Taken together, these results suggest that prior to learning the crossmodal objects, the perirhinal cortex had a default bias toward representing the visual shape information and was not representing sound information of the crossmodal objects. After crossmodal learning, however, the visual shape bias in perirhinal cortex was no longer present. That is, with crossmodal learning, the representations within perirhinal cortex started to look less like the visual features that comprised the crossmodal objects, providing evidence that the perirhinal representations were no longer predominantly grounded in the visual modality.” – pg. 13

We note that not all effects drop in Figure 5b (even in regions with a similar numerical pattern similarity to PRC, like the hippocampus – also see Supplemental Figure S5 for a comparison for patterns only on Day 4), suggesting that the change in visual bias in PRC is not simply due to noise.

“Importantly, the change in pattern similarity in the perirhinal cortex across learning days (Figure 5) is unlikely to be driven by noise, poor alignment of patterns across sessions, or generally reduced responses. Other regions with numerically similar pattern similarity to perirhinal cortex did not change across learning days (e.g., visual features x crossmodal objects in A1 in Figure 5; the exploratory ROI hippocampus with numerically similar pattern similarity to perirhinal cortex also did not change in Supplemental Figure S4c-d).” – pg. 14

(E) Is there a reason the authors did not look at representation and change in the hippocampus? As a rapid-learning, widely-connected feature-binding mechanism, and given the fairly minimal amount of learning experience, it seems like the hippocampus would be a key area of potential import for the cross-modal association. It also looks as though the hippocampus is implicated in the localizer scan (Figure 3c).

We thank the reviewer for this suggestion and now include additional analyses for the hippocampus. We found no evidence of crossmodal integrative coding different from the unimodal features. Rather, the hippocampus seems to represent the convergence of unimodal features, as evidenced by …[can you give some pithy description for what is meant by “convergence” vs “integration”?]. We provide these results in the Supplemental Information and describe them in the main text:

“Analyses for the hippocampus (HPC) and inferior parietal lobe (IPL). (a) In the visual vs. auditory univariate analysis, there was no visual or sound bias in HPC, but there was a bias towards sounds that increased numerically after crossmodal learning in the IPL. (b) Pattern similarity analyses between unimodal features associated with congruent objects and incongruent objects. Similar to Supplemental Figure S3, there was no main effect of congruency in either region. (c) When we looked at the pattern similarity between Unimodal Feature runs on Day 2 to Crossmodal Object runs on Day 2, we found that there was significant pattern similarity when there was a match between the unimodal feature and the crossmodal object (e.g., pattern similarity > 0). This pattern of results held when (d) correlating the Unimodal Feature runs on Day 2 to Crossmodal Object runs on Day 4, and (e) correlating the Unimodal Feature runs on Day 4 to Crossmodal Object runs on Day 4. Finally, (f) there was no significant pattern similarity between Crossmodal Object runs before learning correlated to Crossmodal Object after learning in HPC, but there was significant pattern similarity in IPL (p < 0.001). Taken together, these results suggest that both HPC and IPL are sensitive to visual and sound content, as the (c, d, e) unimodal feature-level representations were correlated to the crossmodal object representations irrespective of learning day. However, there was no difference between congruent and incongruent pairings in any analysis, suggesting that HPC and IPL did not represent crossmodal objects differently from the component unimodal features. For these reasons, HPC and IPL may represent the convergence of unimodal feature representations (i.e., because HPC and IPL were sensitive to both visual and sound features), but our results do not seem to support these regions in forming crossmodal integrative coding distinct from the unimodal features (i.e., because representations in HPC and IPL did not differentiate the congruent and incongruent conditions and did not change with experience). * p < 0.05, ** p < 0.01, *** p < 0.001. Asterisks above or below bars indicate a significant difference from zero. Horizontal lines within brain regions in (a) reflect an interaction between modality and learning day, whereas horizontal lines within brain regions in reflect main effects of (b) learning day, (c-e) modality, or (f) congruency.” – Supplemental Figure S4.

“Notably, our perirhinal cortex mask overlaps with a key region of the ventral anterior temporal lobe thought to be the central locus of crossmodal integration in the “hub and spokes” model of semantic representations.9,50 However, additional work has also linked other brain regions to the convergence of unimodal representations, such as the hippocampus51,52,53 and inferior parietal lobes.54,55 This past work on the hippocampus and inferior parietal lobe does not necessarily address the crossmodal binding problem that was the main focus of our present study, as previous findings often do not differentiate between crossmodal integrative coding and the convergence of unimodal feature representations per se. Furthermore, previous studies in the literature typically do not control for stimulus-based factors such as experience with unimodal features, subjective similarity, or feature identity that may complicate the interpretation of results when determining regions important for crossmodal integration. Indeed, we found evidence consistent with the convergence of unimodal feature-based representations in both the hippocampus and inferior parietal lobes (Supplemental Figure S4), but no evidence of crossmodal integrative coding different from the unimodal features. The hippocampus and inferior parietal lobes were both sensitive to visual and sound features before and after crossmodal learning (see Supplemental Figure S4c-e). Yet the hippocampus and inferior parietal lobes did not differentiate between the congruent and incongruent conditions or change with experience (see Supplemental Figure S4).” – pg. 20

(F) The direction of the neural effects was difficult to track and understand. I think the key observation is that TP and PRh both show changes related to cross-modal congruency - but still it would be helpful if the authors could articulate, perhaps via a schematic illustration, how they think representations in each key area are changing with the cross-modal association. Why does the temporal pole come to activate less for congruent than incongruent stimuli (Figure 3)? And why do TP responses grow less similar to one another for congruent relative to incongruent stimuli after learning (Figure 4)? Why are incongruent stimulus similarities anticorrelated in their perirhinal responses following cross-modal learning (Figure 6)?

We thank the author for identifying this issue, which was also raised by the other reviewers. The reviewer is correct that the key observation is that the TP and PRC both show changes related to crossmodal congruency (given that the unimodal features were equated in the methodological design). However, the structure of the integrative code is less clear, which we now emphasize in the main text. Our findings provide evidence of a crossmodal integrative code that is different from the unimodal features, and future studies are needed to better understand the structure of how such a code might emerge. We now more clearly highlight this distinction throughout the paper:

“By contrast, perirhinal cortex may be involved in pattern separation following crossmodal experience. In our task, participants had to differentiate congruent and incongruent objects constructed from the same three shape and sound features (Figure 2). An efficient way to solve this task would be to form distinct object-level outputs from the overlapping unimodal feature-level inputs such that congruent objects are made to be orthogonal from the representations before learning (i.e., measured as pattern similarity equal to 0 in the perirhinal cortex; Figure 5b, 6, Supplemental Figure S5), whereas non-learned incongruent objects could be made to be dissimilar from the representations before learning (i.e., anticorrelation, measured as patten similarity less than 0 in the perirhinal cortex; Figure 6). Because our paradigm could decouple neural responses to the learned object representations (on Day 4) from the original component unimodal features at baseline (on Day 2), these results could be taken as evidence of pattern separation in the human perirhinal cortex.11,12 However, our pattern of results could also be explained by other types of crossmodal integrative coding. For example, incongruent object representations may be less stable than congruent object representations, such that incongruent objects representation are warped to a greater extent than congruent objects (Figure 6).” – pg. 18

“As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation. Furthermore, these anterior temporal lobe structures may be involved with integrative coding in different ways. For example, the crossmodal object representations measured after learning were found to be related to the component unimodal feature representations measured before learning in the temporal pole but not the perirhinal cortex (Figure 5, 6, Supplemental Figure S5). Moreover, pattern similarity for congruent shape-sound pairs were lower than the pattern similarity for incongruent shape-sound pairs after crossmodal learning in the temporal pole but not the perirhinal cortex (Figure 4b, Supplemental Figure S3a). As one interpretation of this pattern of results, the temporal pole may represent new crossmodal objects by combining previously learned knowledge. 8,9,10,11,13,14,15,33 Specifically, research into conceptual combination has linked the anterior temporal lobes to compound object concepts such as “hummingbird”.34,35,36 For example, participants during our task may have represented the sound-based “humming” concept and visually-based “bird” concept on Day 1, forming the crossmodal “hummingbird” concept on Day 3; Figure 1, 2, which may recruit less activity in temporal pole than an incongruent pairing such as “barking-frog”. For these reasons, the temporal pole may form a crossmodal object code based on pre-existing knowledge, resulting in reduced neural activity (Figure 3d) and pattern similarity towards features associated with learned objects (Figure 4b).” – pg. 18

This work represents a key step in our advancing understanding of object representations in the brain. The experimental design provides a useful template for studying neural change related to the cross-modal association that may prove useful to others in the field. Given the broad variety of open questions and potential alternative analyses, an open dataset from this study would also likely be a considerable contribution to the field.

eLife assessment

The fMRI study is important because it investigates fundamental questions about the neural basis of multimodal binding using an innovative multi-day learning approach. The results provide solid evidence for learning-related changes in the anterior temporal lobe, however, the interpretation of these changes is not straightforward, and the study does not (yet) provide direct evidence for an integrative code. This paper is of potential interest to a broad audience of neuroscientists.

Reviewer #1 (Public Review):

This study used a multi-day learning paradigm combined with fMRI to reveal neural changes reflecting the learning of new (arbitrary) shape-sound associations. In the scanner, the shapes and sounds are presented separately and together, both before and after learning. When they are presented together, they can be either consistent or inconsistent with the learned associations. The analyses focus on auditory and visual cortices, as well as the object-selective cortex (LOC) and anterior temporal lobe regions (temporal pole (TP) and perirhinal cortex (PRC)). Results revealed several learning-induced changes, particularly in the anterior temporal lobe regions. First, the LOC and PRC showed a reduced bias to shapes vs sounds (presented separately) after learning. Second, the TP responded more strongly to incongruent than congruent shape-sound pairs after learning. Third, the similarity of TP activity patterns to sounds and shapes (presented separately) was increased for non-matching shape-sound comparisons after learning. Fourth, when comparing the pattern similarity of individual features to combined shape-sound stimuli, the PRC showed a reduced bias towards visual features after learning. Finally, comparing patterns to combined shape-sound stimuli before and after learning revealed a reduced (and negative) similarity for incongruent combinations in PRC. These results are all interpreted as evidence for an explicit integrative code of newly learned multimodal objects, in which the whole is different from the sum of the parts.

The study has many strengths. It addresses a fundamental question that is of broad interest, the learning paradigm is well-designed and controlled, and the stimuli are real 3D stimuli that participants interact with. The manuscript is well written and the figures are very informative, clearly illustrating the analyses performed.

There are also some weaknesses. The sample size (N=17) is small for detecting the subtle effects of learning. Most of the statistical analyses are not corrected for multiple comparisons (ROIs), and the specificity of the key results to specific regions is also not tested. Furthermore, the evidence for an integrative representation is rather indirect, and alternative interpretations for these results are not considered.

Reviewer #2 (Public Review):

Li et al. used a four-day fMRI design to investigate how unimodal feature information is combined, integrated, or abstracted to form a multimodal object representation. The experimental question is of great interest and understanding how the human brain combines featural information to form complex representations is relevant for a wide range of researchers in neuroscience, cognitive science, and AI. While most fMRI research on object representations is limited to visual information, the authors examined how visual and auditory information is integrated to form a multimodal object representation. The experimental design is elegant and clever. Three visual shapes and three auditory sounds were used as the unimodal features; the visual shapes were used to create 3D-printed objects. On Day 1, the participants interacted with the 3D objects to learn the visual features, but the objects were not paired with the auditory features, which were played separately. On Day 2, participants were scanned with fMRI while they were exposed to the unimodal visual and auditory features as well as pairs of visual-auditory cues. On Day 3, participants again interacted with the 3D objects but now each was paired with one of the three sounds that played from an internal speaker. On Day 4, participants completed the same fMRI scanning runs they completed on Day 2, except now some visual-auditory feature pairs corresponded with Congruent (learned) objects, and some with Incongruent (unlearned) objects. Using the same fMRI design on Days 2 and 4 enables a well-controlled comparison between feature- and object-evoked neural representations before and after learning. The notable results corresponded to findings in the perirhinal cortex and temporal pole. The authors report (1) that a visual bias on Day 2 for unimodal features in the perirhinal cortex was attenuated after learning on Day 4, (2) a decreased univariate response to congruent vs. incongruent visual-auditory objects in the temporal pole on Day 4, (3) decreased pattern similarity between congruent vs. incongruent pairs of visual and auditory unimodal features in the temporal pole on Day 4, (4) in the perirhinal cortex, visual unimodal features on Day 2 do not correlate with their respective visual-auditory objects on Day 4, and (5) in the perirhinal cortex, multimodal object representations across Days 2 and 4 are uncorrelated for congruent objects and anticorrelated for incongruent. The authors claim that each of these results supports the theory that multimodal objects are represented in an "explicit integrative" code separate from feature representations. While these data are valuable and the results are interesting, the authors' claims are not well supported by their findings.

(1) In the introduction, the authors contrast two theories: (a) multimodal objects are represented in the co-activation of unimodal features, and (b) multimodal objects are represented in an explicit integrative code such that the whole is different than the sum of its parts. However, the distinction between these two theories is not straightforward. An explanation of what is precisely meant by "explicit" and "integrative" would clarify the authors' theoretical stance. Perhaps we can assume that an "explicit" representation is a new representation that is created to represent a multimodal object. What is meant by "integrative" is more ambiguous-unimodal features could be integrated within a representation in a manner that preserves the decodability of the unimodal features, or alternatively the multimodal representation could be completely abstracted away from the constituent features such that the features are no longer decodable. Even if the object representation is "explicit" and distinct from the unimodal feature representations, it can in theory still contain featural information, though perhaps warped or transformed. The authors do not clearly commit to a degree of featural abstraction in their theory of "explicit integrative" multimodal object representations which makes it difficult to assess the validity of their claims.

(2) After participants learned the multimodal objects, the authors report a decreased univariate response to congruent visual-auditory objects relative to incongruent objects in the temporal pole. This is claimed to support the existence of an explicit, integrative code for multimodal objects. Given the number of alternative explanations for this finding, this claim seems unwarranted. A simpler interpretation of these results is that the temporal pole is responding to the novelty of the incongruent visual-auditory objects. If there is in fact an explicit, integrative multimodal object representation in the temporal pole, it is unclear why this would manifest in a decreased univariate response.

(3) The authors ran a neural pattern similarity analysis on the unimodal features before and after multimodal object learning. They found that the similarity between visual and auditory features that composed congruent objects decreased in the temporal pole after multimodal object learning. This was interpreted to reflect an explicit integrative code for multimodal objects, though it is not clear why. First, behavioral data show that participants reported increased similarity between the visual and auditory unimodal features within congruent objects after learning, the opposite of what was found in the temporal pole. Second, it is unclear why an analysis of the unimodal features would be interpreted to reflect the nature of the multimodal object representations. Since the same features corresponded with both congruent and incongruent objects, the nature of the feature representations cannot be interpreted to reflect the nature of the object representations per se. Third, using unimodal feature representations to make claims about object representations seems to contradict the theoretical claim that explicit, integrative object representations are distinct from unimodal features. If the learned multimodal object representation exists separately from the unimodal feature representations, there is no reason why the unimodal features themselves would be influenced by the formation of the object representation. Instead, these results seem to more strongly support the theory that multimodal object learning results in a transformation or warping of feature space.

(4) The most compelling evidence the authors provide for their theoretical claims is the finding that, in the perirhinal cortex, the unimodal feature representations on Day 2 do not correlate with the multimodal objects they comprise on Day 4. This suggests that the learned multimodal object representations are not combinations of their unimodal features. If unimodal features are not decodable within the congruent object representations, this would support the authors' explicit integrative hypothesis. However, the analyses provided do not go all the way in convincing the reader of this claim. First, the analyses reported do not differentiate between congruent and incongruent objects. If this result in the perirhinal cortex reflects the formation of new multimodal object representations, it should only be true for congruent objects but not incongruent objects. Since the analyses combine congruent and incongruent objects it is not possible to know whether this was the case. Second, just because feature representations on Day 2 do not correlate with multimodal object patterns on Day 4 does not mean that the object representations on Day 4 do not contain featural information. This could be directly tested by correlating feature representations on Day 4 with congruent vs. incongruent object representations on Day 4. It could be that representations in the perirhinal cortex are not stable over time and all representations-including unimodal feature representations-shift between sessions, which could explain these results yet not entail the existence of abstracted object representations.

In sum, the authors have collected a fantastic dataset that has the potential to answer questions about the formation of multimodal object representations in the brain. A more precise delineation of different theoretical accounts and additional analyses are needed to provide convincing support for the theory that "explicit integrative" multimodal object representations are formed during learning.

Reviewer #3 (Public Review):

This paper uses behavior and functional brain imaging to understand how neural and cognitive representations of visual and auditory stimuli change as participants learn associations among them. Prior work suggests that areas in the anterior temporal (ATL) and perirhinal cortex play an important role in learning/representing cross-modal associations, but the hypothesis has not been directly tested by evaluating behavior and functional imaging before and after learning cross-modal associations. The results show that such learning changes both the perceived similarities amongst stimuli and the neural responses generated within ATL and perirhinal regions, providing novel support for the view that cross-modal learning leads to a representational change in these regions.

This work has several strengths. It tackles an important question for current theories of object representation in the mind and brain in a novel and quite direct fashion, by studying how these representations change with cross-modal learning. As the authors note, little work has directly assessed representational change in ATL following such learning, despite the widespread view that ATL is critical for such representation. Indeed, such direct assessment poses several methodological challenges, which the authors have met with an ingenious experimental design. The experiment allows the authors to maintain tight control over both the familiarity and the perceived similarities amongst the shapes and sounds that comprise their stimuli so that the observed changes across sessions must reflect learned cross-modal associations among these. I especially appreciated the creation of physical objects that participants can explore and the approach to learning in which shapes and sounds are initially experienced independently and later in an associated fashion. In using multi-echo MRI to resolve signals in ventral ATL, the authors have minimized a key challenge facing much work in this area (namely the poor SNR yielded by standard acquisition sequences in ventral ATL). The use of both univariate and multivariate techniques was well-motivated and helpful in testing the central questions. The manuscript is, for the most part, clearly written, and nicely connects the current work to important questions in two literatures, specifically (1) the hypothesized role of the perirhinal cortex in representing/learning complex conjunctions of features and (2) the tension between purely embodied approaches to semantic representation vs the view that ATL regions encode important amodal/crossmodal structure.

There are some places in the manuscript that would benefit from further explanation and methodological detail. I also had some questions about the results themselves and what they signify about the roles of ATL and the perirhinal cortex in object representation.

A) I found the terms "features" and "objects" to be confusing as used throughout the manuscript, and sometimes inconsistent. I think by "features" the authors mean the shape and sound stimuli in their experiment. I think by "object" the authors usually mean the conjunction of a shape with a sound---for instance, when a shape and sound are simultaneously experienced in the scanner, or when the participant presses a button on the shape and hears the sound. The confusion comes partly because shapes are often described as being composed of features, not features in and of themselves. (The same is sometimes true of sounds). So when reading "features" I kept thinking the paper referred to the elements that went together to comprise a shape. It also comes from ambiguous use of the word object, which might refer to (a) the 3D-printed item that people play with, which is an object, or (b) a visually-presented shape (for instance, the localizer involved comparing an "object" to a "phase-scrambled" stimulus---here I assume "object" refers to an intact visual stimulus and not the joint presentation of visual and auditory items). I think the design, stimuli, and results would be easier for a naive reader to follow if the authors used the terms "unimodal representation" to refer to cases where only visual or auditory input is presented, and "cross-modal" or "conjoint" representation when both are present.

B) There are a few places where I wasn't sure what exactly was done, and where the methods lacked sufficient detail for another scientist to replicate what was done. Specifically:

(1) The behavioral study assessing perceptual similarity between visual and auditory stimuli was unclear. The procedure, stimuli, number of trials, etc, should be explained in sufficient detail in methods to allow replication. The results of the study should also minimally be reported in the supplementary information. Without an understanding of how these studies were carried out, it was very difficult to understand the observed pattern of behavioral change. For instance, I initially thought separate behavioral blocks were carried out for visual versus auditory stimuli, each presented in isolation; however, the effects contrast congruent and incongruent stimuli, which suggests these decisions must have been made for the conjoint presentation of both modalities. I'm still not sure how this worked. Additionally, the manuscript makes a brief mention that similarity judgments were made in the context of "all stimuli," but I didn't understand what that meant. Similarity ratings are hugely sensitive to the contrast set with which items appear, so clarity on these points is pretty important. A strength of the design is the contention that shape and sound stimuli were psychophysically matched, so it is important to show the reader how this was done and what the results were.

(2) The experiences through which participants learned/experienced the shapes and sounds were unclear. The methods mention that they had one minute to explore/palpate each shape and that these experiences were interleaved with other tasks, but it is not clear what the other tasks were, how many such exploration experiences occurred, or how long the total learning time was. The manuscript also mentions that participants learn the shape-sound associations with 100% accuracy but it isn't clear how that was assessed. These details are important partly b/c it seems like very minimal experience to change neural representations in the cortex.

(3) I didn't understand the similarity metric used in the multivariate imaging analyses. The manuscript mentions Z-scored Pearson's r, but I didn't know if this meant (a) many Pearson coefficients were computed and these were then Z-scored, so that 0 indicates a value equal to the mean Pearson correlation and 1 is equal to the standard deviation of the correlations, or (b) whether a Fisher Z transform was applied to each r (so that 0 means r was also around 0). From the interpretation of some results, I think the latter is the approach taken, but in general, it would be helpful to see, in Methods or Supplementary information, exactly how similarity scores were computed, and why that approach was adopted. This is particularly important since it is hard to understand the direction of some key effects.

C) From Figure 3D, the temporal pole mask appears to exclude the anterior fusiform cortex (or the ventral surface of the ATL generally). If so, this is a shame, since that appears to be the locus most important to cross-modal integration in the "hub and spokes" model of semantic representation in the brain. The observation in the paper that the perirhinal cortex seems initially biased toward visual structure while more superior ATL is biased toward auditory structure appears generally consistent with the "graded hub" view expressed, for instance, in our group's 2017 review paper (Lambon Ralph et al., Nature Reviews Neuroscience). The balance of visual- versus auditory-sensitivity in that work appears balanced in the anterior fusiform, just a little lateral to the anterior perirhinal cortex. It would be helpful to know if the same pattern is observed for this area specifically in the current dataset.

D) While most effects seem robust from the information presented, I'm not so sure about the analysis of the perirhinal cortex shown in Figure 5. This compares (I think) the neural similarity evoked by a unimodal stimulus ("feature") to that evoked by the same stimulus when paired with its congruent stimulus in the other modality ("object"). These similarities show an interaction with modality prior to cross-modal association, but no interaction afterward, leading the authors to suggest that the perirhinal cortex has become less biased toward visual structure following learning. But the plots in Figures 4a and b are shown against different scales on the y-axes, obscuring the fact that all of the similarities are smaller in the after-learning comparison. Since the perirhinal interaction was already the smallest effect in the pre-learning analysis, it isn't really surprising that it drops below significance when all the effects diminish in the second comparison. A more rigorous test would assess the reliability of the interaction of comparison (pre- or post-learning) with modality. The possibility that perirhinal representations become less "visual" following cross-modal learning is potentially important so a post hoc contrast of that kind would be helpful.

E) Is there a reason the authors did not look at representation and change in the hippocampus? As a rapid-learning, widely-connected feature-binding mechanism, and given the fairly minimal amount of learning experience, it seems like the hippocampus would be a key area of potential import for the cross-modal association. It also looks as though the hippocampus is implicated in the localizer scan (Figure 3c).

F) The direction of the neural effects was difficult to track and understand. I think the key observation is that TP and PRh both show changes related to cross-modal congruency - but still it would be helpful if the authors could articulate, perhaps via a schematic illustration, how they think representations in each key area are changing with the cross-modal association. Why does the temporal pole come to activate *less* for congruent than incongruent stimuli (Figure 3)? And why do TP responses grow less similar to one another for congruent relative to incongruent stimuli after learning (Figure 4)? Why are incongruent stimulus similarities *anticorrelated* in their perirhinal responses following cross-modal learning (Figure 6)?

This work represents a key step in our advancing understanding of object representations in the brain. The experimental design provides a useful template for studying neural change related to the cross-modal association that may prove useful to others in the field. Given the broad variety of open questions and potential alternative analyses, an open dataset from this study would also likely be a considerable contribution to the field.

Author Response

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

Reviewer 1

Comment 1.1: “Did the UKB or HCHS datasets have information on accurate markers of insulin resistance, such as HbA1c or HOMA-IR (if fasting glucose was not available)? Looking at that data would allow us to determine the contribution of insulin resistance to the observed cortical phenotype.”

Reply 1.1: We appreciate the insightful suggestion from the reviewer. In response, we incorporated the HbA1c into our analysis, enhancing its sensitivity to potential effects of insulin resistance. Subsequently, our analysis was reperformed, integrating HbA1c alongside non-fasting blood glucose in the PLS. This addition did not alter our main results, i.e., that of the PLS, virtual histology, and network contextualization analysis. Notably, as a result of the inclusion of HbA1c, the second latent variable now accounted for a greater shared variance (22.13%), with HbA1c showing the highest loading among MetS component variables. The manuscript has been thoroughly revised to incorporate these results.

Comments 1.2: “(Results, p.13, 291-292) "A correlation matrix relating all considered MetS component measures is displayed in supplementary figure S12. Please clarify in this figure labels whether this was non-fasting glucose. If this is non-fasting glucose, it is not a MetS-related risk factor. The reader might be misled into thinking that fasting-glucose has a weak correlation, while its contribution (and the effect of insulin resistance) was not studied here.”

“Table S8 and Table S9: Is the glucose metric here measured following fasting? If not, this should not be listed as a metabolic syndrome criterion. Or it should be specified that it isn't fasted glucose, otherwise, it sounds misleading.”

Reply 1.2: We thank the reviewer for bringing this ambiguity to our attention. The initial analysis included only non-fasting plasma glucose in the PLS, as fasting plasma glucose data was unavailable for UKB and HCHS participants. Following your suggestion in reply 1.1, we have now incorporated HbA1c, a more indicative marker of insulin resistance. We retained non-fasting blood glucose in our analysis, recognizing its relevance as a diagnostic variable for type 2 diabetes mellitus, although it is less informative than fasting plasma glucose, HbA1c, or HOMA-IR. This decision is substantiated by the significant correlation found between non-fasting plasma glucose and HbA1c in our sample (r=.49).

To enhance clarity, we have revised the methods section to explicitly mention that the study investigates non-fasting blood glucose. The revised sentence reads: “Here, we related regional cortical thickness and subcortical volumes to clinical measurements of MetS components, i.e., obesity (waist circumference, hip circumference, waist-hip ratio, body mass index), arterial hypertension (systolic blood pressure, diastolic blood pressure), dyslipidemia (high density lipoprotein, low density lipoprotein, total cholesterol, triglycerides) and insulin resistance (HbA1c, non-fasting blood glucose).”

Additionally, we have updated the caption of supplementary figure S13 (formerly supplementary figure S12) to clearly indicate the investigation of non-fasting plasma glucose. The table detailing diagnostic MetS criteria (supplementary table S2) has also been amended to clarify the absence of fasting plasma glucose data in our study and to indicate that only data on antidiabetic therapy and diagnosis of type 2 diabetes mellitus were used as criteria for insulin resistance in the case-control analysis.

Comment 1.3: “I do not understand how the authors can claim there is a deterministic relationship there if all the results are only correlational or comparative. Can the differences in functional connectivity and white matter fiber tracts observed not be caused by the changes in cortices they relate to? How can the authors be sure the network organisation is shaping the cortical effects and not the opposite (the cortical changes influence the network organisation)? This should be further discussed or explained.”

Reply 1.3: We agree with the reviewer's comment on the non-causative nature of our data and have accordingly revised the discussion section to reflect a more cautious interpretation of our findings. We have carefully reframed our language to avoid any implications of causality, ensuring the narrative aligns with the correlational nature of our data. Nevertheless, we believe that exploring causal interpretations can offer valuable clinical insights. Therefore, while moderating our language, we have maintained certain speculative discussions regarding potential causative pathomechanistic pathways.

Comment 1.4: “The hippocampus is also an area where changes have consistently been observed. Why did the authors limit their analysis to the cortex.”

Reply 1.4: We appreciate this reviewer comment. In response, we have added volumes of Melbourne Subcortical Atlas parcels (including the hippocampus) to the analysis. Corresponding results are now shown in figure 2. The subcortical bootstrap ratios indicated that higher MetS severity was related to lower volumes across all investigated subcortical structures.

Comment 1.5: “Which field ID of the UK biobank are the measures referring to? If possible, please specify the Field ID for each of the UKB metrics used in the study.”

Reply 1.5: We thank the reviewer for the recommendation. The Field IDs used in our study are now listed in supplementary figure S1.

Comment 1.6: “Several Figures were wrongly annotated, making it hard to follow the text.”

Reply 1.6: Thank you for bringing the annotation issues to our awareness. We have thoroughly edited all annotations which should now correctly reference the figure content.

Reviewer 2

Comment 2.1: “Do the authors have the chance to see how the pattern relates to changes in cognitive function in the UKBB and possibly HCHS? This could help to provide some evidence about the directionality of the effect.” Reply 2.1: Thank you for your suggestion. We acknowledge the potential value of investigating gray matter morphometric data alongside longitudinal information on cognitive function. Although we concur with the significance of this approach, we are constrained by the ongoing processing of the UKB's imaging follow-up data and the pending release of the HCHS follow-up data. Consequently, our current analysis cannot incorporate this aspect for now. We plan to explore the relationship between MetS, cognition and brain morphology using longitudinal data as soon as it becomes available.

Comment 2.2: “Also, you could project new data onto the component and establish a link with cognition in a third sample which would be even more convincing. I can offer LIFE-Adult study for this aim.”

Reply 2.2: We are grateful for your recommendation to enhance our study's robustness by including a third sample to establish a cognitive link. While we recognize the merit of such a sensitivity analysis, we believe that our current dataset, derived from two large, independent cohorts, is sufficiently comprehensive for the scope of our current analysis. However, we are open to considering this approach in future studies and appreciate your offer of the LIFE-Adult study. We would welcome further conversation with you regarding future joint projects.

Comment 2.3: “The sentences (p.17, ll.435 ff) seem to repeat: "Interestingly, we also observed a positive relationship between cortical thickness and MetS in the superior frontal, parietal and occipital lobe. Interpretation of this result is, however, less intuitive. We also noted a positive MetS-cortical thickness association in superior frontal, parietal and occipital lobes, a less intuitive finding that has been previously reported [60,61].”

Reply 2.3: Thank you for making us aware of this duplication. We have deleted the first part of the section. It now reads “We also noted a positive MetS-cortical thickness association in superior frontal, parietal and occipital lobes, a less intuitive finding that has been previously reported.”

Comment 2.4: “I would highly appreciate empirical evidence for the claim in ll. 442 "In support of this hypothesis, the determined cortical thickness abnormality pattern is consistent with the atrophy pattern found in vascular mild cognitive impairment and vascular dementia" Considering the previous reports about the co-localization of obesity-associated atrophy and AD neurodegeneration (Morys et al. 2023, DOI: 10.3233/JAD-220535), that most dementias are mixed and that MetS probably increases dementia risk through both AD and vascular mechanisms, I feel such "binary" claims on VaD/AD-related atrophy patterns should be backed up empirically.”

Reply 2.4: Thank you for highlighting the need for clarity in differentiating between vascular and Alzheimer's dementia. We recognize the intricate overlap in dementia pathologies. Acknowledging the prevalence of mixed dementia and the influence of MetS on both AD and vascular mechanisms, we realize our original statement might have implied a specificity to vascular dementia, which was not intended.

To address your concern, we have revised our statement to avoid an exclusive focus on vascular pathology, ensuring a more balanced representation of dementia types. Additionally, we have included Morys et al. 2023 as a reference. The section now reads: “In support of this hypothesis, the determined brain morphological abnormality pattern is consistent with the atrophy pattern found in vascular mild cognitive impairment, vascular dementia and Alzheimer’s dementia.”

Comment 2.5: “I wonder how specific the cell-type results are to this covariance pattern. Maybe patterns of CT (independent of MetS) show similar associations with one or more of the reported celltypes? Would it be possible to additionally show the association of the first three components of general cortical thickness variation with the cell type densities?”

Reply 2.5: Thank you for your query regarding the specificity of the cell-type results to the observed covariance pattern. To address this, we have conducted a virtual histology analysis of the first three latent variables of the main analysis PLS. The findings of this extended analysis have been detailed in the supplementary Figure S21. The imaging covariance profile of latent variable 2 was significantly associated with the density of excitatory neurons of subtype 3. The imaging covariance profile linked to latent variable 3 showed no significant association of cell type densities. Possibly, latent variable 3 represents only a noise component as it explained only 2.12% of shared variance. We hope this addition provides a clearer understanding of the specificity of our main results.

Comment 2.6: “I agree that this multivariate approach can contribute to a more holistic understanding, yet I would like to see the discussion expanded on how to move on from here. Should we target the MetS more comprehensively or would it be best to focus on obesity (being the strongest contributor and risk factor for other "downstream" conditions such as T2DM)? A holistic approach is somewhat at odds with the in-depth investigation of specific mechanisms.”

Reply 2.6: We value your suggestion to elaborate on the implications of our findings. Our study indicates that obesity may have the most pronounced impact on brain morphology among MetS components, suggesting it as a key contributor to the clinical-anatomical covariance pattern observed in our analysis. This highlights obesity as a primary target for future research and preventive strategies. However, we believe that our results warrant further validation, ideally through longitudinal studies, before drawing definitive clinical conclusions.

Additionally, our study endorses a comprehensive approach to MetS, highlighting the importance of considering the syndrome as a whole to gain broader insights. We want to clarify, however, that such an approach is meant to complement, rather than replace, the study of individual cardiometabolic risk factors. The broad perspective our study adopts is facilitated by its epidemiological nature, which may not be as applicable in experimental settings that are vital for deriving mechanistic disease insights.

To reflect these points, we have expanded the discussion in our manuscript to include a more detailed consideration of these implications and future research directions.

Comment 2.7: “Please report the number of missing variables.”

Reply 2.7: Thank you for your request to report the number of missing variables. We would like to direct your attention to table 1, where we have listed the number of available values for each variable in parentheses. To determine the number of missing variables, one can subtract these numbers from the total sample size.

Comment 2.8: “Was the pattern similar in pre-clinical (pre-diabetes, pre-hypertension) vs. clinical conditions?“

Reply 2.8: Thank you for your interest in the applicability of our findings across different MetS severity levels. Our analysis employs a continuous framework to encompass the entire range of vascular and cardiometabolic risks, including those only mildly affected by MetS. The linear relationship we observed between MetS severity and gray matter morphology patterns, as illustrated in Figure 2d, supports the interpretation that our findings apply to the entire spectrum of MetS severities.

Comment 2.9: “How did you deal with medication (anti-hypertensive, anti-diabetic, statins..)?”

Reply 2.9: Information on medication was considered for defining MetS for the case-control sensitivity analysis but was not included in the PLS. Detailed information can be found in table 1.

Comment 2.10: “It would be really interesting to determine the genetic variations associated with the latent component. Have you considered doing a GWAS on this, potentially in the CHARGE consortium or with UKBB as discovery and HCHS as replication sample?”

Reply 2.10: Thank you for your valuable suggestion regarding the implementation of a GWAS. We agree that incorporating a GWAS would provide significant insights, but we also recognize that it extends beyond the scope of our current analysis. However, we are actively planning a follow-up analysis. This subsequent analysis will encompass a comprehensive examination of both genetic variation and imaging findings in the context of MetS.

Comment 2.11: “Please provide more information on which data fields from UKBB were used exactly (e.g. in github repository).”

Reply 2.11: We appreciate your recommendation. The details regarding the Field IDs used in our study have been included as supplementary table S1.

Reviewer 3

Comments 3.1: “After a thorough review of the methods and results sections, I found no direct or strong evidence supporting the authors' claim that the identified latent variables were related to more severe MetS to worse cognitive performance. While a sub-group comparison was conducted, it did not adequately account for confounding factors such as educational level.”

“Page 18-19 lines 431-446: the fifth paragraph in the discussion section. - As previously mentioned in the "Weaknesses" section, this study did not conduct a direct association analysis between MetS and cognitive levels without considering subgroup comparisons. Hence, I recommend the content of this paragraph warrants careful reconsideration.”

Reply 3.1: We acknowledge the reviewer's constructive feedback regarding our analysis of cognitive data. We have performed a mediation analysis relating the subject-specific clinical PLS score of latent variable 1 representing MetS severity and cognitive test performances and testing for mediating effects of the imaging PLS score capturing the MetS-related brain morphological abnormalities. The imaging score was found to statistically mediate the relationship between the clinical PLS score and executive function and processing speed, memory, and reasoning test performance. These findings highlight brain structural differences as a relevant pathomechanistic correlate in the relationship of MetS and cognition. Corresponding information can now be found in figure 3, methods section 2.6.2, result section 3.3 and discussion section 4.2.

Moreover, we would like to apologize for any confusion caused by previous unclear presentation. Our study further incorporates association analyses between MetS, brain structure, and cognition using MetS components, regional brain morphological measures, and cognitive performance data in a PLS to investigate whether cognitive measures contribute to the latent variable. These analyses were separately performed on the UK Biobank and HCHS datasets, due to their distinct cognitive assessments. We adjusted for age, sex, and education in the subgroup analyses by removing their effects from the input variables. These relationships are detailed in supplementary figures S16b and S17b, with loadings close to zero for age, sex, and education, confirming effective deconfounding.

In sum, we greatly appreciate the suggestion to conduct a mediation analysis, which has substantially enhanced the strength and relevance of our analysis.

Comment 3.2: “I would suggest the authors provide a more comprehensive description of the metrics used to assess each MetS component, such as obesity (incorporating parameters like waist circumference, hip circumference, waist-hip ratio, and body mass index) and arterial hypertension (detailing metrics like systolic and diastolic blood pressure), etc.”

Reply 3.2: Thank you for your suggestion regarding a more detailed description of the metrics for assessing each component of MetS. We would like to point out that the specific metrics used, including those for obesity (such as waist circumference, hip circumference, waist-hip ratio, and body mass index) and arterial hypertension (including systolic and diastolic blood pressure), are comprehensively detailed in table 1 of our manuscript. We hope this table provides the clarity and specificity you are seeking regarding the MetS assessment metrics in our study.

Comment 3.3: “I recommend the inclusion of an additional, detailed flowchart to further illustrate the procedure of virtual histology analysis. This would enhance the clarity of the methodological approach and assist readers in better comprehending the analysis method.”

Reply 3.3: Thank you for your suggestion. Recognizing the challenges in visually representing many of our analysis steps, we have instead supplemented our manuscript with additional references. These references provide a clearer understanding of our virtual histology approach, particularly focusing on the processing of regional microarray expression data.

The corresponding sentence reads: “Further details on the processing steps covered by ABAnnotate can be found elsewhere (https://osf.io/gcxun) [42]”

Comment 3.4: “Why were both brain hemispheres used instead of solely utilizing the left hemisphere as the atlas, especially considering that the Allen Human Brain Atlas (AHBA) only includes gene data for the right hemisphere for two subjects?”

Reply 3.4: Thank you for your query regarding our decision to use both brain hemispheres instead of solely the left hemisphere, especially considering the Allen Human Brain Atlas (AHBA) predominantly featuring gene data from the left hemisphere. Given the AHBA's limited spatial coverage of expression data in the right hemisphere, our approach involved mirroring the existing tissue samples across the left-right hemisphere boundary using the abagen toolbox,1 a practice supported by findings that suggest minimal lateralization of microarray expression.2,3 Further details are provided in previous work employing ABAnnotate.4 These studies are now referenced in our methods section.

Comment 3.5: “The second latent variable was not further discussed. If this result is deemed significant, it warrants a more detailed discussion. "

Reply 3.5: Thank you for the suggestion. We have added a paragraph to the discussion that discusses the second latent variable in greater detail. It reads: “The second latent variable accounted for 22.33% of shared variance and linked higher insulin resistance and lower dyslipidemia to lower thickness and volume in lateral frontal, posterior temporal, parietal and occipital regions. The distinct covariance profile of this latent variable, compared to the first, likely indicates a separate pathomechanistic connection between MetS components and brain morphology. Given that HbA1c and blood glucose were the most significant contributors to this variable, insulin resistance might drive the observed clinicalanatomical relationship.”

Comment 3.6: “I suggest appending positive MetS effects after "..., insular, cingulate and temporal cortices;" for two reasons: a). The "positive MetS effects" might represent crucial findings that should not be omitted. b). Including both negative and positive effects ensures that subsequent references to "this pattern" are more precise.”

Reply 3.6: We concur with the notion that the positive MetS effects should be highlighted as well. We modified the first discussion paragraph now mentioning them.

Comment 3.7: “I would appreciate further clarification on this sentence and the use of the term "uniform" in this context. Does this suggest that despite the heterogeneity in the physiological and pathological characteristics of the various MetS components (e.g., obesity, hypertension), their impacts on cortical thickness manifest similarly? How is it that these diverse components lead to "uniform" effects on cortical thickness? Does this observation align with or deviate from previous findings in the literature?”

Reply 3.7: Thank you for highlighting the ambiguity in our previous explanation. We agree that the complexity of the relationship between MetS components and brain morphology requires clearer articulation. To address this, we have revised the relevant sentence for better clarity. It now reads: „This finding indicates a relatively uniform connection between MetS and brain morphology, implying that the associative effects of various MetS components on brain structure are comparatively similar, despite the distinct pathomechanisms each component entails.“

Comment 3.8: “Figure 1 does not have the labels "c)" and "d)". ”

Reply 3.8: Thank you. We have modified figure 1 and made sure that the caption correctly references its content.

Comment 3.10: “Incorrect figure/table citation:

• Page 18 line 418: "(figure 2b and 1c)" à (figure 2b and 2c).

• Page 18 line 419: "(supplementary figures S8 and S12-13)" à (supplementary figures S11 and S1516).

• In the supplementary material, "Text S5 - Case-control analysis" section contains several figure or table citation errors. Please take a moment to review and correct them.”

Reply 3.10: Thank you for bringing this to our attention. We have corrected the figure and table citation errors.

Comment 3.11: “Page 8 line 184: The more commonly used term is "insulin resistance" rather than "insuline resistance.”

Reply 3.11: We now use “insulin resistance” throughout the manuscript.

Comment 3.12: “Nevertheless, variations in gene sets may introduce a degree of heterogeneity in the results (Seidlitz, et al., 2020; Martins et al., 2021). Consequently, further validation or exploratory analyses utilizing different gene sets can yield more compelling results and conclusions.”

Reply 3.12: Thank you for your insightful comment regarding the potential heterogeneity introduced by variations in gene sets. We agree that exploring different gene sets could indeed enhance the robustness and generalizability of our findings. However, we think conducting a comprehensive methodological analysis of the available cell-type specific gene sets is a substantial effort and warrants its own investigation to thoroughly implement it and assess its implications. We also like to highlight that we are adhering to previous practices in our analysis setup.4,5

References

(1) Markello RD, Arnatkeviciute A, Poline JB, Fulcher BD, Fornito A, Misic B. Standardizing workflows in imaging transcriptomics with the abagen toolbox. Jbabdi S, Makin TR, Jbabdi S, Burt J, Hawrylycz MJ, eds. eLife. 2021;10:e72129. doi:10.7554/eLife.72129

(2) Hawrylycz MJ, Lein ES, Guillozet-Bongaarts AL, et al. An anatomically comprehensive atlas of the adult human brain transcriptome. Nature. 2012;489(7416):391-399. doi:10.1038/nature11405

(3) Hawrylycz M, Miller JA, Menon V, et al. Canonical genetic signatures of the adult human brain. Nat Neurosci. 2015;18(12):1832-1844. doi:10.1038/nn.4171

(4) Lotter LD, Saberi A, Hansen JY, et al. Human cortex development is shaped by molecular and cellular brain systems. Published online May 5, 2023:2023.05.05.539537. doi:10.1101/2023.05.05.539537

(5) Lotter LD, Kohl SH, Gerloff C, et al. Revealing the neurobiology underlying interpersonal neural synchronization with multimodal data fusion. Neuroscience & Biobehavioral Reviews. 2023;146:105042. doi:10.1016/j.neubiorev.2023.105042

eLife assessment

This important work contributes to our understanding of the combined effects of metabolic syndrome on fronto-temporal gray matter morphology from two large-scale datasets. The evidence based on state-of-the art multivariate imaging analysis and detailed micro- and macrostructural contextualization analyses is convincing and provides an understanding of the neurological correlates of metabolic syndrome, although the study would have benefitted from the inclusion of longitudinal data.

Reviewer #1 (Public Review):

Summary:

In their study, Petersen et al. investigated the relationship between parameters of metabolic syndrome (MetS) and cortical thickness using partial least-squares correlation analysis (PLS) and performed subsequently a group comparison (sensitivity analysis). To do this, they utilized data from two large-scale population-based cohorts: the UK BioBank (UKB) and the Hamburg City Health Study (HCHS). They identified a latent variable that explained 77% of the shared variance, driven by several measures related to MetS, with obesity-related measures having the strongest contribution. Their results highlighted that higher cortical thickness in the orbitofrontal, lateral prefrontal, insular, anterior cingulate, and temporal areas is associated with lower MetS severity. Conversely, the opposite pattern was observed in the superior frontal, parietal, and occipital regions. A similar pattern was then observed in the sensitivity analysis when comparing two groups (MetS vs. matched controls) separately.

Interestingly, after including HbA1c (a blood glycemic marker, which reflects insulin resistance much better than non-fasting glucose) in their revision, the authors identified a second latent variable accounting for 22% of shared variance mostly driven by HbA1c and blood glucose. The authors conclude that the distinct covariance profile of this variable likely indicates a separate pathological mechanistic connection between MetS components and brain morphology.

They then mapped local cellular and network topological attributes to the observed cortical changes associated with MetS. This was achieved using cell-type-specific gene expressions from the Allen Human Brain Atlas and the group consensus functional and structural connectomes of the Human Connectome Project (HCP), respectively. This contextualization analysis allowed them to identify potential cellular contributions in these structures driven by endothelial cells, microglial cells, and excitatory neurons. It also indicated functional and structural interconnectedness of areas experiencing similar MetS effects.

Strengths:

The effects of metabolic syndrome on the brain are still incompletely understood, and such multi-scale analyses are important for the field. Despite the study's sole 'correlation-based' nature, it yields valuable results, including several scales of brain parameters (cortical thickness, cellular, and network-based). The results are robust and benefit from two 'large-scale' datasets, resulting in highly powered statistics

Weaknesses:

The weakness of this study lies mostly on the non-causative approach used here. Nevertheless, the authors are aware of the limitations of the study and carefully frame their language accordingly.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Petersen et al. aimed for a comprehensive assessment of the relationship between cardiometabolic risk factors and cortical thickness. They found that a latent variable reflecting higher obesity, hypertension, LDL cholesterol, triglyerides, non-fasting glucose, HbA1c and lower HDL cholesterol was associated with lower cortical thickness in orbitofrontal, lateral prefrontal, insular, anterior cingulate and temporal areas as well as lower subcortical volumes. In sensitivity analyses they showed that this pattern replicated across cohorts and was also consistent with a clinical definition of the metabolic syndrome.

Further, when including cognition into the multivariate analysis, the pattern remained unchanged and mediation analyses showed that the relationship between the first latent variable and worse cognitive performance across several tests was mediated by the brain morphological differences.

The authors investigated the cell types implicated in the regions associated with cardiometabolic risk using the Allen Brain Atlas and found that the density of excitatory neurons type 8, endothelial cells and microglia reliably co-located with the pattern of cortical thickness. Furthermore, they showed that cortial regions more strongly associated with MetS were more closely structurally & functionally connected than others.

Strengths:

This study performed a comprehensive assessment of the combined association of cardiometabolic risk factors and brain structure and investigated micro-and macroscopic underpinnings. A major strength of the study is the methodological approach of partial least squares which allows one to not single out risk factors but to take them into account simultaneously. The large sample size from two cohorts allowed for different sensitivity analyses and convincing evidence for the stability of the first latent variable. The authors demonstrated that the component was also reliably related to cognitive performance and that the association of the individual cardiometabolic risk on cognition was mediated by brain morphological differences, replicating multiple previous studies which evidenced associations of different components of the MetS with worse cognitive performance.

The novel contribution of the study lies in the virtual histology and brain topology investigation of the cortical pattern related to MetS. The virtual histology provided convincing evidence of the co-localization of endothelial, glial and excitatory neuronal cells with the regions of MetS-associated cortical thinning while the brain topology analysis highlighted the disproportionate structural and functional connectivity between associated regions. This analysis provides insights into the role of inflammatory processes and the intricate link between gray matter morphology and microvasculature, both locally and in relation to long-range connectivity. This information is valuable to inform future mechanistic studies.

Weaknesses:

The study is exclusively cross-sectional which does not allow disentangling potential causes from consequences. While studies indicate that most of the differences seen in middle age are probably consequences of the MetS on the vasculature, blood-brain barrier or inflammatory processes, differences in cortical morphology might also represent a risk factor for weight gain.<br /> The study is exploratory in nature and for the contextualization analyses it is difficult to judge whether those were selected from a larger pool of analyses.

Author Response

Reviewer #1 (Public Review):

(1.1) The work by Porciello and colleagues provides scientific evidence that the acidic content of the stomach covaries with the experienced level of disgust and fear evoked by disgusting videos. The working of the inside of the gut during cognitive or emotional processes have remained elusive due to the invasiveness of the methods to study it. The major strength of the paper is the use of the non-invasive smart pill technology, which senses changes in Ph, pressure and temperature as it travels through the gut, allowing authors to investigate how different emotions induced with validated video clips modulate the state of the gut. The experimental paradigm used to evoke distinct emotions was also successful, as participants reported the expected emotions after each emotion block. While the reported evidence is correlational in nature, I believe these results open up new avenues for studying brain-body interactions during emotions in cognitive neuroscience, and future causal manipulations will shed more insight on this phenomena. Indeed, this is the first study to provide evidence for a link between gastric acidity and emotional experience beyond single patient studies, and it has major implications for the advancement of our understanding of disorders with psycho-somatic influences, such as stress and it's influence of gastritis.

1.1 First of all, we want to thank Reviewer#1 for his cogent comments and for highlighting that our findings may inspire future research on brain-body interactions. We took into the highest consideration all the remarks and changed the manuscripts accordingly.

(1.2) As for the limitations, little insight is provided on the mechanisms, time scales, and inter-individual variability of the link between gastric Ph and emotional induction. Since this is a novel phenomena, it would be important to further validate and characterize this finding. On this line, one of the most well known influences of disgust on the gut is tachygastria, the acceleration of the gastric rhythm. It would be important to understand how acid secretion by disgusting film is related to tachygastria, but authors only examine the influence of disgusting film on the normogastric frequency range.

1.2 We are aware that at the moment our data are mainly descriptive and do not provide a clear picture of the causal mechanisms. However, to deal with this outstanding issue we added a new series of analysis.

Most of the data on gastric activity come from analysis of the normogastric band. However, information about the EGG tachygastric rhythm in humans is of potential great importance. To deal with the reviewer’s comment and considering the previously published literature, we re-examined the EGG data focusing on the tachygastric rhythm. The methodology remained consistent with the process described for normogastric peak extraction but this time, we extracted the peak in the tachygastric band, specifically 0.067 to 0.167 Hz (i.e., 4–10 cpm). The ANOVA performed over the tachygastric cycle revealed a significant main effect of the type of video clip (F(4, 112) = 2.907, p = 0.025, Eta2 (partial) = 0.09). However, the Bonferroni corrected post hoc tests did not show any significant difference between the different type of emotional video clips and the neutral condition. The sole significant comparison was observed between participants viewing happy and fearful video clips, indicating that participants’ tachygastric cycles were faster when exposed to happy rather than fearful video clips (p = 0.038). For a visual representation of the outcomes, please see Fig S6.

We revised the main text (Page 17, lines: 472-482) to include this analysis. The revised text now reads as follows:

“Finally, we explored whether normogastric and/or tachygastric cycle changed in response to specific emotional experience. After checking that normogastric and tachygastric peak frequencies were normally distributed (all ps > 0.05), we ran two separate ANOVAs on the individual peak frequencies in the normogastric and tachygastric range. Each analysis had the type of video clip as within-subjects factor. The ANOVA performed on the normogastric rhythm was not significant (F(4, 44) = 1.037, p = 0.399) suggesting that the gastric rhythm did not change while participants observed the different emotional video clips. In contrast, the ANOVA performed on the tachygastric rhythm did show a significant main effect (F(4, 112) = 2.907, p = 0.025, Eta2 (partial) = 0.09). However, the only comparison that survived the Bonferroni correction was the one between happy and fearful video clips, namely participants’ tachygastric cycle was faster when they observed happy vs fearful video clips (p = 0.038) see Fig. S6 for a graphical representation of the results.”

To deal with the Reviewer’s comment, we also correlated the average pH value with the corresponding frequency of the tachygastric cycle recorded in the disgusting, happy and the fearful video clips, namely the emotions associated to changes in pH. The only significant correlation was the one found during the disgusting video clips (r= 0.435; p= 0.023, all the other rs ≤ 0.351, all the other ps ≥ 0.073). Differently from what we expected, we found a positive correlation suggesting that when participants were exposed to disgusting video clips the less acidic was the pH the higher was the frequency of the tachygastric cycle. Instead, we know from our pill data that disgusting video clips are associated to more acid values, and from literature (not replicated by us) to a faster gastric rhythm. Since we did not find strong support in the EGG analysis suggesting a relationship between the gastric rhythm and the emotional experience, we believe that additional evidence will help to clarify the relationship between pH and gastric rhythm.

(1.3) Additionally, only one channel of the electrogastrogram (EGG) was used to measure the gastric rhythm, and no information is provided on the quality of the recordings. With only one channel of EGG, it is often impossible to identify the gastric rhythm as the position of the stomach varies from person to person, yielding inaccurate estimates of the frequency of the gastric rhythm.

1.3 We agree with Reviewer 1 on this point. We acknowledge the potential limitation associated with one-channel EGG recording in our study. To deal with this remark, in a separate (ongoing) study (N# participants= 25) we recorded the electrogastrogram following the methodology outlined by Wolpert et al., 2020 published on Psychophysiology. Thus, in order to study the EGG in association to the emotional experience, we used a bipolar 4-channels montage while participants observed the same emotional video clips used in our current study (see picture below for the montage set-up).

Author response image 1 shows the 4-channels EGG bipolar recording montage reproducing the one proposed by Wolpert et al., 2020.

Author response image 1.

Then, we extracted the gastric cycle in both the normogastric and the tachygastric bands.

After checking that data were normally distributed (Kolmogorov-Smirnov ds > 0.10; ps> .20), in the case of the gastric cycle extracted in the normogastric band, we ran a repeated measures ANOVA with the type of video clip as the only within-subjects factor measured on the 5 levels (i.e. the five types of video clip: Disgusting, Fearful, Happy, Neutral, and Sad). The ANOVA shows that the gastric cycle recorded during the different video clips did not differ (F (4,96) = 0.39; p= 0.81), see the plot on Author response image 2.

Author response image 2.

Gastric cycle (normogastric band) recorded via multiple-channels electrogastrogram (EGG) during the emotional experience. The plot shows the gastric cycle extracted in the normogastric band while participants were observing the five categories of the video clips (i.e. those inducing disgust, fear, happiness, sadness and, as control, a neutral state).

We also extracted the gastric cycle in the tachygastric band, the distribution of the data was not normal in one condition (Kolmogorov-Smirnov ds > 0.27; p < 0.05), therefore we ran a Friedman ANOVA to compare the gastric cycle during the different emotional experiences. The Friedman ANOVA was not statistically significant (χ2 (4) = 2.88; p = 0.58), suggesting that, similarly to the gastric cycle extracted in the normogastric band, also the one extracted in the tachygastric band was not clearly associated to the investigated emotional states, see Author response image 3.

Author response image 3.

Gastric cycle (tachygastric band) recorded via multiple-channels electrogastrogram (EGG) during the emotional experience. The plot above shows the gastric cycle extracted in the tachygastric band while participants were observing the five categories of the video clips (i.e. those inducing disgust, fear, happiness, sadness and as control a neutral state).

Results from this control study seem to suggest that the non-significant effect of the gastric cycle was probably not due to the fact that we use a one-channel egg montage, at least for what concerns the gastric cycle extracted from the normogastric band.

For what concerns the tachygastric frequency associated to the emotional experience these results from a multi-channel EGG recording seem to go in the same direction of the normogastric one, namely no frequency of the gastric cycles recorded during the emotional video clips was different from the control condition.

The only significant difference that we found in our 1-channel EGG study was the one between the happy and the fearful video clips (see Fig. S6 contained in the supplementary materials and above). Specifically, we found that happy video clips were associated to higher gastric frequency compared to the fearful ones. However, we did not replicate these findings in our multi-channels EGG study.

Although suggestive, this evidence is not conclusive. Indeed, we are aware that a final word on the results of our multi-channel study can be said only when a larger sample is obtained.

(1.4) Finally, I believe that the results do not show evidence in favor of the discrete nature of emotions theory as they claim in the discussion. Authors chose to use stimuli inducing discrete emotions, and only asked subjective reports of these same discrete emotions, so these results shed no light on whether emotions are represented discretely vs continuously in the brain.

We revised the discussion in order to better describe our results and toned down the interpretation that the present findings directly support the discrete nature of emotions, as suggested by this Reviewer.

Now page 21&22 lines 622-631 reads as follow:

“Overall, and in line with theoretical and empirical evidence (Damasio, 1999; Harrison et al., 2010; James, 1994, Lettieri et al., 2019; Stephens et al., 2010), our findings may suggest that specific patterns of subjective, behavioural, and physiological measures are linked to unique emotional states...We acknowledge that our results, although novel, are restricted to a sample of male participants, and more importantly they need to be replicated. We also acknowledge that future studies should better investigate the mechanisms underlying the role of the pH in the emergence of specific emotion. For instance, pharmacologically manipulating stomach pH during emotional induction, not only for basic emotions but also for exploring complex emotions such as moral disgust (Rozin et al., 2009), would enable researchers to generalize these findings and examine the directionality of this relationship.”

Reviewer #2 (Public Review):

To measure the role of gastric state in emotion, the authors used an ingestible smart pill to measure pH, pressure, and temperature in the gastrointestinal tract (stomach, small bowel, large bowel) while participants watched videos that induced disgust, fear, happiness, sadness, or a control (neutral). The study has a number of strengths, including the novelty of the measurement (very few studies have ever measured these gut properties during emotion processing) and the apparent robustness of their main finding (that during disgusting video clips, participants who experienced more feelings of disgust (and to a lesser degree which might not survive more stringent multiple comparison correction, fear) had more acidic stomach measurements, while participants who experienced more happiness during the disgusting video clips had a less acidic (more basic) stomach pH. Although the study is correlational (which all discussion should carefully reflect) and is restricted to a moderately-sized, homogenous sample, the results support their general conclusion that stomach pH is related to emotion experience during disgust induction. There may be additional analyses to conduct in order for the authors to claim this effect is specific to the stomach. Nevertheless, this work is likely to have a large impact on the field, which currently tends to rely on noninvasive measures of gastric activity such as electrogastrography (which the authors also collect for comparison); the authors' minimally-invasive approach yields new and useful measurements of gastric state. These new measures could have relevance beyond emotion processing in understanding the role of gut pH (and perhaps temperature and pressure) in cognitive processes (e.g. interoception) as well as mental and physical health.

We are very grateful to Reviewer#2 for skilfully managing the paper and highlighting its strengths, particularly the innovative measurement approach and the potential implications these findings might offer for future research into the impact of gastric signals on emotional experiences and potentially on many other higher-order cognitive functions. Additionally, we would like to thank her for the highly valuable feedback. We have incorporated all the comments into the revised manuscript, aiming to enhance its quality.

Reviewer #3 (Public Review):

This study used novel ingestible pills to measure pH and other gastric signals, and related these measures to self-report ratings of emotions induced by video clips. The main finding was that when participants viewed videos of disgust, there was an association between gastric pH and feelings of disgust and fear, and (in the opposite direction) happiness. These findings may be the first to relate objective measures of gastric physiology to emotional experience. The methods open up many new questions that can be addressed by future studies and are thus likely to have an impact on the field.

We thank very much also Reviewer#3 for the accurate reading of our manuscript; for highlighting the strengths of our study; and for providing valuable feedback. Below, a point-by-point response to all the comments raised by this Reviewer. We have incorporated their comments, and we hope they are satisfied by the new version of the manuscript.

(3.1) My main concern is with the reliability of the results. The study associates many measures (pH, temperature, pressure, EGG) in stomach, small bowel, and large bowel with multiple emotion ratings. This amounts to many statistical tests. Only one of these measures (pH in the stomach) shows a significant effect. Furthermore, the key findings, as displayed in Figure 4 do not look particularly convincing. Perhaps this is a display issue, but the relations between stomach pH and Vas ratings of disgust, fear, and happiness were not apparent from the scatter plot and may be influenced by outliers (e.g., happiness).

3.1 We thank Reviewer#3 for raising this issue which was also raised by Reviewer#1 and #2, se replies above. As reported above we worked on the data analysis in order to provide more evidence supporting our claim, i.e. that pH plays a role in the emotional experience of disgust, happiness and fear. We modified Figure 4 (now 5) as also requested by Reviewer 1 and 2, and we now hope that it is clearer. We included a new analysis, in which we used all the datapoints recorded from the ingestible device and we performed a mixed models analysis with pH as dependent variable, type of video clips and number of datapoints (‘Time’) as fixed factors, and the by-subject intercepts as random effects. This analysis not only supported the results of the original one but provided evidence for a causal role of the emotional induction on the pH of the stomach. Results of this analysis are described in point 1.7 in the response to Reviewer#1 and results of the new analysis and the revised version of the main figure can be found in track change in the manuscript (Page 15&16, lines: 408-439) in the main text and copied and pasted below.

“To explore how the emotional induction could modulate the pH of the stomach and how the length of the exposure to that specific emotional induction could also play a role in modulating pH variations, we ran an additional model, Model 2. This model included all the pH datapoints registered using the Smartpill as dependent variable, the type of video clip and the number of the datapoints (“Time”) as fixed effects, and the by-subject intercepts as random effects (see Supplementary information for a detailed description of the model). Model 2 had a marginal R2 = 0.014 and a conditional R2 = 0.79. Visual inspection of the plots did reveal some small deviations from homoscedasticity, visual inspection of the residuals did not show important deviations from normality. As for collinearity (tested by means of vif function of car package), all independent variables had a GVIF^(1/(2*Df)))^2 < 10.

Type III analysis of variance of Model 2 showed a statistically significant main effect of the Time (F = 20.237, p < 0.001, Eta2 < 0.01) suggesting that independently from the type of video clip observed, the stomach pH significantly decreased as a function of the time of exposure to the induction. A significant main effect of the type of video clip was also found (F = 22.242, p < 0.001, Eta2 = 0.01) suggesting that pH of the stomach changes when participants experienced different types of emotions. In particular, post hoc analysis revealed that pH was more acidic when participants observed disgusting compared to fearful (t= -11.417; p < 0.001), happy (t= -15.510; p < 0.001) and neutral (t= -3.598; p = 0.003) video clips.

Also, pH was more acidic when participants observed fearful compared to happy (t= -4.064; p < 0.001), and less acidic compared to neutral (t= 7.835; p < 0.001) and sad scenarios (t= 9.743; p < 0.001). Finally, pH was less acidic when participants observed happy compared to neutral (t= 11.923; p < 0.001). and sad videoclips (t= 13.806; p < 0.001), see Fig.6, left panel. Interestingly, also the double interaction Time X Type of video clip was significant (F = 3.250, p = 0.0113, Eta2 < 0.01) suggesting that the time of the exposure to the induction differentially influenced the pH of the stomach depending on to the type of the observed video clip. Simple slope analysis showed that while pH did not change over time when observing disgusting (t= -1.2691; p = 0.2045) and happy (t= 0.4466; p = 0.6552) clips, it did significantly decrease over time when observing fearful (t= -4.4212; p < 0.001), sad (t= -2.0487; p = 0.0405) and neutral video clips (t= -2.7956; p = 0.0052), see Fig.6, right panel."

We believe that the new evidence reported provides support of our claims and we hope that the reviewer agrees with us. However, as we also mentioned in the paper, we are aware that replications are needed and we are already working on this.

eLife assessment

This important study used a novel method to relate gastric acidity to subjective ratings of emotions induced by video clips. The findings are solid but could be strengthened by additional analyses and/or visualization. The findings have broad implications for the field of emotion research and opens new avenues of research for understanding psychosomatic disorders.

Reviewer #1 (Public Review):

The work by Porciello and colleagues provides scientific evidence that the acidic content of the stomach covaries with the experienced level of disgust and fear evoked by disgusting videos. The working of the inside of the gut during cognitive or emotional processes have remained elusive due to the invasiveness of the methods to study it. The major strength of the paper is the use of the non-invasive smart pill technology, which senses changes in Ph, pressure and temperature as it travels through the gut, allowing authors to investigate how different emotions induced with validated video clips modulate the state of the gut. The experimental paradigm used to evoke distinct emotions was also successful, as participants reported the expected emotions after each emotion block. While the reported evidence is correlational in nature, I believe these results open up new avenues for studying brain-body interactions during emotions in cognitive neuroscience, and future causal manipulations will shed more insight on this phenomena. Indeed, this is the first study to provide evidence for a link between gastric acidity and emotional experience beyond single patient studies, and it has major implications for the advancement of our understanding of disorders with psycho-somatic influences, such as stress and it's influence of gastritis.

As for the limitations, little insight is provided on the mechanisms, time scales, and inter-individual variability of the link between gastric Ph and emotional induction. Since this is a novel phenomena, it would be important to further validate and characterize this finding. On this line, one of the most well known influences of disgust on the gut is tachygastria, the acceleration of the gastric rhythm. It would be important to understand how acid secretion by disgusting film is related to tachygastria, but authors only examine the influence of disgusting film on the normogastric frequency range. Additionally, only one channel of the electrogastrogram (EGG) was used to measure the gastric rhythm, and no information is provided on the quality of the recordings. With only one channel of EGG, it is often impossible to identify the gastric rhythm as the position of the stomach varies from person to person, yielding inaccurate estimates of the frequency of the gastric rhythm. Finally, I believe that the results do not show evidence in favor of the discrete nature of emotions theory as they claim in the discussion. Authors chose to use stimuli inducing discrete emotions, and only asked subjective reports of these same discrete emotions, so these results shed no light on whether emotions are represented discretely vs continuously in the brain.

Reviewer #2 (Public Review):

To measure the role of gastric state in emotion, the authors used an ingestible smart pill to measure pH, pressure, and temperature in the gastrointestinal tract (stomach, small bowel, large bowel) while participants watched videos that induced disgust, fear, happiness, sadness, or a control (neutral). The study has a number of strengths, including the novelty of the measurement (very few studies have ever measured these gut properties during emotion processing) and the apparent robustness of their main finding (that during disgusting video clips, participants who experienced more feelings of disgust (and to a lesser degree which might not survive more stringent multiple comparison correction, fear) had more acidic stomach measurements, while participants who experienced more happiness during the disgusting video clips had a less acidic (more basic) stomach pH. Although the study is correlational (which all discussion should carefully reflect) and is restricted to a moderately-sized, homogenous sample, the results support their general conclusion that stomach pH is related to emotion experience during disgust induction. There may be additional analyses to conduct in order for the authors to claim this effect is specific to the stomach. Nevertheless, this work is likely to have a large impact on the field, which currently tends to rely on noninvasive measures of gastric activity such as electrogastrography (which the authors also collect for comparison); the authors' minimally-invasive approach yields new and useful measurements of gastric state. These new measures could have relevance beyond emotion processing in understanding the role of gut pH (and perhaps temperature and pressure) in cognitive processes (e.g. interoception) as well as mental and physical health.

Reviewer #3 (Public Review):

This study used novel ingestible pills to measure pH and other gastric signals, and related these measures to self-report ratings of emotions induced by video clips. The main finding was that when participants viewed videos of disgust, there was an association between gastric pH and feelings of disgust and fear, and (in the opposite direction) happiness. These findings may be the first to relate objective measures of gastric physiology to emotional experience. The methods open up many new questions that can be addressed by future studies and are thus likely to have an impact on the field.

My main concern is with the reliability of the results. The study associates many measures (pH, temperature, pressure, EGG) in stomach, small bowel, and large bowel with multiple emotion ratings. This amounts to many statistical tests. Only one of these measures (pH in the stomach) shows a significant effect. Furthermore, the key findings, as displayed in Figure 4 do not look particularly convincing. Perhaps this is a display issue, but the relations between stomach pH and Vas ratings of disgust, fear, and happiness were not apparent from the scatter plot and may be influenced by outliers (e.g., happiness).

Author Response

Reviewer #2 (Public Review):

This study aims to test the role of awake replay in short-term memory, a type of memory that operates on the timescale of seconds and minutes. Replay refers to a time-compressed burst of neuronal population activity during a particular oscillatory local field potential event in the hippocampus, called the sharp-wave ripple (SWR). SWRs are found during sleep and in the awake state and are always associated with the animal being quiescent. The paper compares results from three different behavioral tasks ranging in memory requirements and memory timescales. First, rats were trained on either a spatial match-to-sample task (MTS), a non-match-to-sample task (NMTS), or a task requiring the memorization of sequences (maze arms to be visited in a specific temporal order). In this initial training phase, the animals were allowed to learn the maze structure and the rules governing these tasks for all these behavioral paradigms. Then, awake sharp-SWRs were disrupted as the animal performed these tasks (both during instruction and test phases) via an online detection system combined with closed-loop electrical stimulation of the ventral hippocampal commissure. Notably, this manipulation appeared not to affect performance in all three tasks, as determined using various behavioral parameters. Trials with no stimulation or delayed stimulation serve as controls. Thus, the authors conclude that awake SWRs are not involved in these short-term memory-guided behaviors. I do have a few comments that the authors should discuss or address:

(1) This study adds to a large number of studies investigating the role of awake SWRs in spatial learning and memory tasks. The results of these previous studies are quite contradictory and range from awake SWRs are not crucial in guiding decisions at all to SWRs are only essential during task rule learning to SWRs do guide behavior. Could the authors comment on these seemingly contradictory results? Why are these experiments now the right ones?

The reviewer is correct that there is a large body of literature investigating awake SWRs. Most commonly, interpretations about the role of SWRs and associated replay are made based on correlations of their occurrence with behavior. These correlations do, however, not necessarily indicate that SWRs contribute to a particular cognitive process. That is why interventional studies like ours are important to clarify the contribution of SWRs.

The acquisition of a novel task involves a number of cognitive processes, including short- and long-term memory, building a map of the environment, exploration of the solution space and incorporating (non-)rewarding feedback. Based on available evidence, SWRs could contribute to many of these processes. Our experiments were designed to exclude the long-term memory aspect and focus on the memorization of locations on a short time-scale which as we now demonstrate is not dependent on SWRs. Since the use of short-term spatial memory is one of the possible explanations for the learning deficit seen by Jadhav et al. (2012) following SWR disruption in an alternation task, our results may also narrow down the exact contribution of SWR in these studies.

(2) None of the experiments presented here test the role of replay. I suggest making this distinction in the paper and the title clear. As the results are presented now, is it possible that the SWR content is not affected sufficiently to have a behavioral effect or that there is a bias towards detecting specific SWRs, e.g., longer SWRs?

The reviewer is right that our experiments do not say anything about replay directly. We adapted the text to make this distinction clear.

We address the possibility that SWR content may not be disrupted sufficiently to cause a behavioral effect in response to recommendation 1.

Reviewer #3 (Public Review):

In this manuscript, the authors seek to shed light on the role of awake hippocampal replay during memory tasks that are claimed to be short-term memory. For this, they make use of a real-time detection and disruption system of awake hippocampal ripples, which are used as a proxy for awake neuronal replay. The manuscript describes extensively the tasks as well as the disruption system and controls used during the experiments. The authors present numerous and solid analyses of the behavioral data acquired during the tasks. Nonetheless, the current version of the manuscript is lacking a more complete discussion in which the results are contrasted to previous similar findings, as well as mentioning the role of the awake ripple in the stabilization of hippocampal maps. Some extra analyses are also suggested below. The manuscript would also be enriched if the authors suggested alternative mechanisms for memory rehearsal. Finally, some claims of "we are first" seem inappropriate when compared to the previous literature.

Major comments:

How does one define short-term memory (STM) in rodents? The examples and papers cited in the first paragraphs refer mostly to human working memory tasks, from which it is known that a non- rehearsed STM lasts typically 20-30 seconds. Could the authors mention how this concept is translated to rodents? Could you clarify until what point memory is considered STM and what is the criteria to consider it has turned into long-term memory or when is it simply working memory or habit/skill?

We agree with the reviewer that the definition of short-term memory is fluid and may differ between researchers and model systems. To avoid confusion, we reframed our study in a different context and hope that this makes the timeframes we are talking about clearer.

Further, why should these tasks be classified as testing STM while Jadhav et al. tasks are working memory or as they now mention in this article rule learning?

Note that short-term memory and working memory are closely related, but not identical, concepts. Whereas short-term memory refers to the retaining of information for a short period of time, working memory is generally considered to also include some manipulation of that information. Unfortunately, in the rodent literature, (spatial) working memory and short-term memory are often used interchangeably.

Many (animal) spatial memory tasks do not test a single cognitive faculty, but likely involve a combination of short-term memory, working memory, and rule learning (among other abilities) to acquire or solve the task. As such, an unequivocal classification of behavioral tasks is not generally possible. For example, in the continuous version of the spatial alternation task used in Jadhav et al., animals may learn the rule “if I in the center arm and I came from the left goal arm, then I will next find reward in the right goal arm”. The execution of this rule would require maintaining in (short-term) memory the most recent visited goal arm. Alternatively, animals may learn the rule to turn left twice and right twice to successfully perform the task.

One of our goals in our study was to attempt to isolate rule learning components and short-term memory components in our tasks (to be clear: we are not claiming that our tasks are pure short- term memory tasks).

We have rewritten the introduction to reframe our study, which hopefully clarifies the points above.

In humans, the retention of memory after a certain time is achieved by retrieving a long-term memory. How do we know if the considerable training the rats received has not allowed the use of a long-term memory strategy which allows the rats to perform well even in the absence of rehearsal (replay)? These are conceptual explanations that would help understand the key concept of STM in greater detail.

Our experiments aimed to distinguish between the process of learning general task rules through training and the need to retain information specific to each trial or session. For example, in the NMTS task, the animals may have a long-term memory of the overall task design, but they cannot anticipate or recall in advance which specific arms will be baited in the instruction phase since they vary from one trial to another. Therefore, to complete a trial successfully, the animals must have formed some type of (short-term) memory of the instruction arms and/or of the arms that still need to be visited in the test phase. Although extended training may have resulted in a more optimized and less demanding strategy to memorize the necessary information, evidence in the literature indicates that even then (for this particular task), a functional hippocampus is required (Sasaki 2021). The question we address in our experiments is whether hippocampal SWRs (and by association, replay) are instrumental in the formation or maintenance of this memory, whether through rehearsal or other mechanisms. The rewritten introduction explains these concepts more clearly.

Further, claims of "first" should be adjusted, since I do not see a large difference between the w (m) maze of Jadhav and these tasks. The main difference between the two projects would rather be that Jadhav tests when animals are still newer to the task while here overtrained animals are used. In Jadhav, it's unlikely that just rule learning is affected since the inbound component is not affected by disruption, which also tests rule learning. Therefore, it is still likely that the effect seen in Jadhav et al is a deficit in working memory/short-term memory. And here it is more likely, that no effect was seen since with overtrained animals other strategies (cortical, striatal, etc) were used. The authors should compare in more detail how overtrained animals were in these different projects as well as in the articles they cite for replay analysis.

The training of the animals on the general task rules prior to SWR disruption manipulations is by design, as it better isolates the short-term memory demands required to solve the task in each trial/session. In our tasks, the rats are required to memorize a randomly chosen combination of goal arms on each day (MTS & SEQ task) or in every trial (NMTS task). Unlike the continuous alternation paradigm used by Jadhav et al. (2012), our tasks can not be solved using a stereotypical or habitual (striatal) strategy that is acquired through extended training. We can not exclude that the rats acquired an optimized and less cognitively demanding strategy that is mainly dependent on cortical structures outside the hippocampus, however evidence in the literature still indicates the requirement for a functional hippocampus (Sasaki, 2021; Okaichi and Oshima 1990; Blokland, Honig, and Raaijmakers, 1992).

The reviewer is correct that the inbound component of the continuous alternation task in Jadhav et al. (2012) can be considered rule learning and was not affected by SWR disruption. However, we do not believe that this should be generalized to all rule learning and it is very well conceivable that SWRs contribute to the learning of more complex rules that also feature ambiguity (such as the outbound component in the continuous alternation task). We elaborate on these points in the discussion (lines 425-455).

The main conclusion of the authors is that hippocampal replay is not the rehearsal mechanism expected in STM given that its disruption doesn't lead to behavioral changes. Could the authors hypothesize in their discussion what other neural mechanisms different from hippocampal replay may be involved in this rehearsal?

Thank you for this suggestion. We added an extra paragraph speculating on this aspect (lines 499- 518).

The discussion also lacks closure with respect to how the findings fit in the study of STM in human memory. This would make the article more interesting to a larger audience and highlight its translational aspect.

We agree with the reviewer and added our insight to the discussion.

The results describe deeply the behavioral performance of the rats and the validation of the ripple detection/disruption system. However, one important aspect missing is how the hippocampal activity and its encoding of space may be affected by the awake ripple disruption. The authors don't cite the work by Roux et al., Nature Neuroscience. 2017 where optogenetic stimulation of hippocampal neurons provided evidence that neuronal activity associated with awake hippocampal ripples during goal-directed behavior is required for both stabilizing and refining hippocampal place fields, while memory performance was not affected during ripple-locked stimulations compared to a ripple-delayed stimulation control (See supplementary Figure 7 of the mentioned article). I would like the authors to comment on their own findings and contrast them with those of Roux et al.

We agree that it is interesting to include the results of Roux et al. in our discussion (lines 470 and 463-466).

Line 64: Could the authors clarify what they mean by "indirect" causal evidence when discussing the contribution of papers by Jadhav, Igata, and Fernandez? Is it the fact that rodents' learning speed changed instead of showing a complete absence of learning? Or is it the fact that the disruption/prolongation is done on the hippocampal ripple and not strictly in the replay sequence?

We apologize for the confusion and rewrote large parts of the introduction to clarify the contributions of the papers by Jadhav, Igata, and Fernandez and the difference with what our manipulations contribute. In the process, we removed the phrase ‘indirect causal evidence’.

I would also highlight this latter difference, given that the above-mentioned authors describe their methodological approaches in terms of ripples and not in terms of replay content. For example, the use of "replay" instead of "ripple" in Line 61 results in methodological inaccurate terms such as replay disruption and replay prolongation.

Thank you for pointing this out. We adapted the manuscript to always use ‘ripple’ or ‘sharp-wave ripple’ (SWR) when describing our results.

Despite its apparent lack of statistical significance, the reported mean ripple detection rate during the trial and non-trial periods tend to be always higher in the disruption condition of all tasks by observing the median of the boxplots in Figure 1J, Figure 2H, and Figure 3J. It is worth investigating this further using the same linear regression method as Girardeau et al. Journal of Neuroscience, 2014 which may reduce the variability and allow comparing slopes of a cumulative number of ripples over time. This may reveal a compensatory homeostatic-like increase in the rate of ripples during the disrupted sessions, which may suggest a need for the ripple/replay occurrence in spite of it not having an effect on the rats' performance during the task.

The reviewer makes an interesting observation and we appreciate the suggestion for further investigation. However, note that a clear trend for higher ripple rates in disruption trials/sessions is not present when comparing to non-stimulated control trials/session. Part of the variability in the observed ripple rates is likely due to the variability in the animals’ behavioral state (e.g., moving, pausing but alert, grooming, consuming reward) and the corresponding varying propensity for SWRs to occur. The behavioral variability makes application of the linear regression approach of Girardeau et al. (2014) not straightforward (note that Girardeau et al. looked at SWRs during sleep). For these reasons, we have decided to not further look into the potential disruption-induced increase of the SWR rate.

In line 425, the authors report a median relative delay of 52.9 of their disruption system. Such a value would indicate that only around 47% of the ripple is being blocked. Is there any data from the authors or others that could reassure the reader that the 52.9% of the ripple that "leaks" is not enough for the replay phenomenon to occur? Considering the findings of Fernandez-Ruiz et al. 2019 on large-duration ripples, could the authors report the relative delay for both short and long ripples (>100 ms) separately?

The reviewer is correct that the initial part (~35 ms) of SWRs remains intact, which is inherent to the online detection and disruption approach. In relative terms, a larger fraction of long SWRs is disrupted. As requested, we have adapted figure 4c to separately show the distribution of relative detection delays for long (duration >100ms) and short SWRs.

As we and others have shown, the electrical stimulation temporarily suppresses spiking activity in CA1 and thus abruptly interferes with any ongoing replay, but any beginning of replay sequences before the stimulation will not be affected. Previous studies that use the same methodology to disrupt SWRs reported a behavioral performance deficit despite the detection delays (Michon et al. 2019; Girardeau et al. 2009; Jadhav et al. 2012). This suggests that the initial part of SWRs (and replay) is not sufficient to support the behavior. The delays in the current study are quantitatively similar to what we have reported before in Michon et al. (2019) and thus we are confident that we should have been able to observe a behavioral effect if present. We now elaborate on this topic in the Discussion (lines 489-498) .

Line 494: The authors define long ripples as (>120 ms) but this doesn't coincide with the 100ms threshold from Fernandez Ruiz et al. 2019.

Thank you for pointing this out, it is corrected in the text both in the Results (line 389) and Discussion (line 486).

The online ripple detector used filtered the traces in the 135-255 Hz range. This is a narrower frequency range compared to online detectors used by Jadhav et al. 2012 (100-400 Hz) and Fernandez-Ruiz et al. 2019 (80-300 Hz). What motivated the use of this narrow range? Would the omittance of ripples below 135 Hz have implications in the results? Could the authors add to the supplement a figure similar to Figure 4B (FDR vs TPR) using a wider frequency range similar to the authors above in the offline detection of ripples?

The frequency of hippocampal ripple oscillation in rat generally lies in the range of 160-225 Hz (Buzsaki, 1992). We have added a power spectrum in Figure 1d that confirms this frequency range in our experiments. Filters that include frequencies below this range (as in the studies referenced by the reviewer) likely also pass through high-frequency gamma oscillations, and filters that include frequencies above this range likely also pass through multi-unit spiking activity. The challenge for a real-time ripple detection system is to design a filter that has an acceptable trade-off between filtering in a specific (narrow) frequency range and introducing a long delay. In our study, we specifically designed a filter that is specific to the ripple frequency band and still has an acceptable low delay.

It is unclear what criterion was used to train the rats in the NMTS task. Line 216 specifies a learning criterion of 80% fully correct trials in one session for three days in a row, while the methods in line 852 mention an average performance below 50% for at least three days in a row.

Thank you for pointing this out. We corrected the learning criterium description in the results section (lines 108-110) to match the description in the Methods section.

In the methods section, it is not mentioned if there was a specific region in the cortex where the tetrode was placed (Line 908).

The detections in this tetrode were used to mark events as "false positives". The authors should be careful in line 933 when they make the statement "ripples are not present in the cortex". There have been recent publications that challenge this affirmation. See Khodagholy, Science. 2017, Nitzan, Nature Comm. 2020.

Thank you for pointing this out. We have added the cortical region in the methods (line 882) and clarified that, as far as we know, no ripples in that part of the cortex (parietal associate cortex) have been described that are synchronous with hippocampal ripples.

eLife assessment

This manuscript presents the lack of effect of closed-loop SWR disruption in guiding behavior and remembering the recent past in short-term memory tasks in rats. These negative results may have important theoretical and practical implications in the field of memory and learning. However, while SWR detection methods are carefully validated, the strength of evidence is incomplete and some additional controls are required.

Reviewer #1 (Public Review):

This manuscript describes the results of closed-loop SWR disruption in rats experiencing a short-term memory task that they previously acquired successfully. The authors aim to show that SWRs are dispensable for STM tasks requiring multiple match-to-sample trial rules, single-trial non-match-to-sample rules, and spatial sequence memory. In all cases, the analysis and intervention were performed at the higher standards, providing a clear proof-of-principle of appropriate detection and the necessary control. I found the experiments well executed and analyzed. Results may help to advance our understanding of the role of awake SWRs in STM. However, since the results consist of a lack of evidence there is a need for some additional positive controls to fully support the main claim of the study.

Reviewer #2 (Public Review):

This study aims to test the role of awake replay in short-term memory, a type of memory that operates on the timescale of seconds and minutes. Replay refers to a time-compressed burst of neuronal population activity during a particular oscillatory local field potential event in the hippocampus, called the sharp-wave ripple (SWR). SWRs are found during sleep and in the awake state and are always associated with the animal being quiescent. The paper compares results from three different behavioral tasks ranging in memory requirements and memory timescales. First, rats were trained on either a spatial match-to-sample task (MTS), a non-match-to-sample task (NMTS), or a task requiring the memorization of sequences (maze arms to be visited in a specific temporal order). In this initial training phase, the animals were allowed to learn the maze structure and the rules governing these tasks for all these behavioral paradigms. Then, awake sharp-SWRs were disrupted as the animal performed these tasks (both during instruction and test phases) via an online detection system combined with closed-loop electrical stimulation of the ventral hippocampal commissure. Notably, this manipulation appeared not to affect performance in all three tasks, as determined using various behavioral parameters. Trials with no stimulation or delayed stimulation serve as controls. Thus, the authors conclude that awake SWRs are not involved in these short-term memory-guided behaviors. I do have a few comments that the authors should discuss or address:

(1) This study adds to a large number of studies investigating the role of awake SWRs in spatial learning and memory tasks. The results of these previous studies are quite contradictory and range from awake SWRs are not crucial in guiding decisions at all to SWRs are only essential during task rule learning to SWRs do guide behavior. Could the authors comment on these seemingly contradictory results? Why are these experiments now the right ones?<br /> (2) None of the experiments presented here test the role of replay. I suggest making this distinction in the paper and the title clear. As the results are presented now, is it possible that the SWR content is not affected sufficiently to have a behavioral effect or that there is a bias towards detecting specific SWRs, e.g., longer SWRs?

Reviewer #3 (Public Review):

In this manuscript, the authors seek to shed light on the role of awake hippocampal replay during memory tasks that are claimed to be short-term memory. For this, they make use of a real-time detection and disruption system of awake hippocampal ripples, which are used as a proxy for awake neuronal replay. The manuscript describes extensively the tasks as well as the disruption system and controls used during the experiments. The authors present numerous and solid analyses of the behavioral data acquired during the tasks. Nonetheless, the current version of the manuscript is lacking a more complete discussion in which the results are contrasted to previous similar findings, as well as mentioning the role of the awake ripple in the stabilization of hippocampal maps. Some extra analyses are also suggested below. The manuscript would also be enriched if the authors suggested alternative mechanisms for memory rehearsal. Finally, some claims of "we are first" seem inappropriate when compared to the previous literature.

Major comments:

How does one define short-term memory (STM) in rodents? The examples and papers cited in the first paragraphs refer mostly to human working memory tasks, from which it is known that a non-rehearsed STM lasts typically 20-30 seconds. Could the authors mention how this concept is translated to rodents? Could you clarify until what point memory is considered STM and what is the criteria to consider it has turned into long-term memory or when is it simply working memory or habit/skill? Further, why should these tasks be classified as testing STM while Jadhav et al. tasks are working memory or as they now mention in this article rule learning? In humans, the retention of memory after a certain time is achieved by retrieving a long-term memory. How do we know if the considerable training the rats received has not allowed the use of a long-term memory strategy which allows the rats to perform well even in the absence of rehearsal (replay)? These are conceptual explanations that would help understand the key concept of STM in greater detail.

Further, claims of "first" should be adjusted, since I do not see a large difference between the w (m) maze of Jadhav and these tasks. The main difference between the two projects would rather be that Jadhav tests when animals are still newer to the task while here overtrained animals are used. In Jadhav, it's unlikely that just rule learning is affected since the inbound component is not affected by disruption, which also tests rule learning. Therefore, it is still likely that the effect seen in Jadhav et al is a deficit in working memory/short-term memory. And here it is more likely, that no effect was seen since with overtrained animals other strategies (cortical, striatal, etc) were used. The authors should compare in more detail how overtrained animals were in these different projects as well as in the articles they cite for replay analysis.

The main conclusion of the authors is that hippocampal replay is not the rehearsal mechanism expected in STM given that its disruption doesn't lead to behavioral changes. Could the authors hypothesize in their discussion what other neural mechanisms different from hippocampal replay may be involved in this rehearsal? The discussion also lacks closure with respect to how the findings fit in the study of STM in human memory. This would make the article more interesting to a larger audience and highlight its translational aspect.

The results describe deeply the behavioral performance of the rats and the validation of the ripple detection/disruption system. However, one important aspect missing is how the hippocampal activity and its encoding of space may be affected by the awake ripple disruption. The authors don't cite the work by Roux et al., Nature Neuroscience. 2017 where optogenetic stimulation of hippocampal neurons provided evidence that neuronal activity associated with awake hippocampal ripples during goal-directed behavior is required for both stabilizing and refining hippocampal place fields, while memory performance was not affected during ripple-locked stimulations compared to a ripple-delayed stimulation control (See supplementary Figure 7 of the mentioned article). I would like the authors to comment on their own findings and contrast them with those of Roux et al.

Line 64: Could the authors clarify what they mean by "indirect" causal evidence when discussing the contribution of papers by Jadhav, Igata, and Fernandez? Is it the fact that rodents' learning speed changed instead of showing a complete absence of learning? Or is it the fact that the disruption/prolongation is done on the hippocampal ripple and not strictly in the replay sequence? I would also highlight this latter difference, given that the above-mentioned authors describe their methodological approaches in terms of ripples and not in terms of replay content. For example, the use of "replay" instead of "ripple" in Line 61 results in methodological inaccurate terms such as replay disruption and replay prolongation.

Despite its apparent lack of statistical significance, the reported mean ripple detection rate during the trial and non-trial periods tend to be always higher in the disruption condition of all tasks by observing the median of the boxplots in Figure 1J, Figure 2H, and Figure 3J. It is worth investigating this further using the same linear regression method as Girardeau et al. Journal of Neuroscience, 2014 which may reduce the variability and allow comparing slopes of a cumulative number of ripples over time. This may reveal a compensatory homeostatic-like increase in the rate of ripples during the disrupted sessions, which may suggest a need for the ripple/replay occurrence in spite of it not having an effect on the rats' performance during the task.

In line 425, the authors report a median relative delay of 52.9 of their disruption system. Such a value would indicate that only around 47% of the ripple is being blocked. Is there any data from the authors or others that could reassure the reader that the 52.9% of the ripple that "leaks" is not enough for the replay phenomenon to occur? Considering the findings of Fernandez-Ruiz et al. 2019 on large-duration ripples, could the authors report the relative delay for both short and long ripples (>100 ms) separately? Line 494: The authors define long ripples as (>120 ms) but this doesn't coincide with the 100ms threshold from Fernandez Ruiz et al. 2019.

The online ripple detector used filtered the traces in the 135-255 Hz range. This is a narrower frequency range compared to online detectors used by Jadhav et al. 2012 (100-400 Hz) and Fernandez-Ruiz et al. 2019 (80-300 Hz). What motivated the use of this narrow range? Would the omittance of ripples below 135 Hz have implications in the results? Could the authors add to the supplement a figure similar to Figure 4B (FDR vs TPR) using a wider frequency range similar to the authors above in the offline detection of ripples?

It is unclear what criterion was used to train the rats in the NMTS task. Line 216 specifies a learning criterion of 80% fully correct trials in one session for three days in a row, while the methods in line 852 mention an average performance below 50% for at least three days in a row.

In the methods section, it is not mentioned if there was a specific region in the cortex where the tetrode was placed (Line 908). The detections in this tetrode were used to mark events as "false positives". The authors should be careful in line 933 when they make the statement "ripples are not present in the cortex". There have been recent publications that challenge this affirmation. See Khodagholy, Science. 2017, Nitzan, Nature Comm. 2020.

eLife assessment

This valuable work explores death coding data to understand the impact of COVID-19 on cancer mortality. The work provides solid evidence that deaths with cancer as a contributing cause were not above what would be expected during pandemic waves, suggesting that cancer did not strongly increase the risk of dying of COVID-19. These results are an interesting exploration into the coding of causes of death that can be used to make sense of how deaths are coded during a pandemic in the presence of other underlying diseases, such as cancer.

Reviewer #2 (Public Review):

The article is very well written, and the approach is quite novel. I have two major methodological comments, that if addressed will add to the robustness of the results.

(1) Model for estimating expected mortality. There is a large literature using a different model to predict expected mortality during the pandemic. Different models come with different caveats, see the example of the WHO estimates in Germany and the performance of splines (Msemburi et al Nature 2023 and Ferenci BMC Medical Research Methodology 2023). In addition, it is a common practice to include covariates to help the predictions (e.g., temperature and national holidays, see Kontis et al Nature Medicine 2020). Last, fitting the model-independent for each region, neglects potential correlation patterns in the neighbouring regions, see Blangiardo et al 2020 PlosONE.

Based on the above:<br /> a. I believe that the authors need to run a cross-validation to justify model performance. I would suggest training the data leaving out the last year for which they have mortality and assessing how the model predicts forward. Important metrics for the prediction performance include mean square error and coverage probability, see Konstantinoudis et al Nature Communications 2023. The authors need to provide metrics for all regions and health outcomes.

b. In the context of validating the estimates, I think the authors need to carefully address the Alzheimer case, see Figure 2. It seems that the long-term trends pick an inverse U-shape relationship which could be an overfit. In general, polynomials tend to overfit (in this case the authors use a polynomial of second degree). It would be interesting to see how the results change if they also include a cubic term in a sensitivity analysis.

c. The authors can help with the predictions using temperature and national holidays, but if they show in the cross-validation that the model performs adequately, this would be fine.

d. It would be nice to see a model across the US, accounting for geography and spatial correlation. If the authors don't want to fit conditional autoregressive models in the Bayesian framework, they could just use a random intercept per region.

(2) I think the demographic model needs further elaboration. It would be nice to show more details, the mathematical formula of this model in the supplement, and explain the assumptions.

eLife assessment

This work by Shin et al. demonstrated that a different form of PTH (R25C PTH) generated a comparable anabolic signal to rhPTH 1-34 using a large animal model. This valuable finding may have therapeutic potential in promoting bone formation or the healing process, and the methods seem solid.

Reviewer #1 (Public Review):

Summary:

This study, titled "Enhancing Bone Regeneration and Osseointegration using rhPTH(1-34) and Dimeric R25CPTH(1-34) in an Osteoporotic Beagle Model," provides valuable insights into the therapeutic effects of two parathyroid hormone (PTH) analogs on bone regeneration and osseointegration. The research is methodologically sound, employing a robust animal model and a comprehensive array of analytical techniques, including micro-CT, histological/histomorphometric analyses, and serum biochemical analysis.

Strengths:

The use of a large animal model, which closely mimics postmenopausal osteoporosis in humans, enhances the study's relevance to clinical applications. The study is well-structured, with clear objectives, detailed methods, and a logical flow from introduction to conclusion. The findings are significant, demonstrating the potential of rhPTH(1-34) and dimeric R25CPTH(1-34) in enhancing bone regeneration, particularly in the context of osteoporosis.

Weaknesses:

There are no major weaknesses.

Reviewer #2 (Public Review):

Summary:

This article explores the regenerative effects of recombinant PTH analogues on osteogenesis.

Strengths:

Although PTH has known to induce the activity of osteoclasts, accelerating bone resorption, paradoxically its intermittent use has become a common treatment for osteoporosis. Previous studies successfully demonstrated this phenomenon in vivo, but most of them used rodent animal models, inevitably having a limitation. In this article, the authors tried to address this, using a beagle model, and assessed the osseointegrative effect of recombinant PTH analogues. As a result, the authors clearly observed the regenerative effects of PTH analogues, and compared the efficacy, using histologic, biochemical, and radiologic measurement for surgical-endocrinal combined large animal models. The data seem to be solid, and has potential clinical implications.

Weaknesses:

As PTH's mechanism has already been widely accepted, and the main focus of this article was to compare the preclinical efficacy of PTH analogues, the lack of detail biologic mechanism could be allowed. However, there are some suggestions to enhance the readability of the article:

First, the authors should clarify why they compared the effects of rhPTH(1-34) and of dimeric R25C2 PTH(1-34)? In most of the parameters, rhPTH(1-34) seems to be superior to dimeric R25C2 PTH(1-34). Why did the authors insist that the anabolic effects of dimer were prominent? Even though implication of dimeric R25C2 PTH(1-34) was drawn from genetic mutation studies, the authors should describe more clearly in the discussion the potential clinical benefits of the dimeric R25C2 PTH(1-34) compared to rhPTH(1-34), especially if dimeric R25C2 PTH(1-34) has just partial agonistic effect in pharmacodynamics.

Second, please describe the intermittent and continuous application of PTH analogues. Many of the readers may misunderstand that the authors' daily injection of PTHs were actually to mimic the clinical intermittent application or continuous one. Incorporation of the author's intention for experimental design would be more helpful for readers.

Third, please unify the nomenclature. Ensure consistency in the nomenclature throughout the article. Unify the naming conventions for PTH analogues, such as rhPTH(1-34) vs teriparatide and (Cys25)PTH(1-84) vs R25CPTH(1-34) vs R25CPTH(1-34) vs (1-84). Choose one nomenclature for each analogue and use it consistently throughout the article.

Overall, this paper is well-written, but these suggestions aim to improve clarity and consistency for a broader readership.

Reviewer #3 (Public Review):

Summary:

The work submitted by Dr. Jeong-Oh Shin and co-workers aims to investigate the therapeutic efficacy of rhPTH(1-34) and R25CPTH(1-34) on bone regeneration and osseointegration of titanium implants using a postmenopausal osteoporosis animal model.<br /> In my opinion the findings presented are not strongly supported by the provided data since the methods utilized do not allow to significantly support the primary claims.

Strengths:

Strengths include certain good technologies utilized to perform histological sections (i.e. the EXAKT system).

Weaknesses:

Certain weaknesses significantly lower the enthusiasm for this work. Most important: the limited number of samples/group. In fact, as presented, the work has an n=4 for each treatment group. This limited number of samples/group significantly impairs the statistical power of the study. In addition, the implants were surgically inserted following a "conventional implant surgery", implying that no precise/guided insertion was utilized. This weakness is, in my opinion, particularly significant since the amount of bone osteointegration may greatly depend on the bucco-lingual positioning of each implant at the time of the surgical insertion (which should, therefore, be precisely standardized across all animals and for all surgical procedures).<br /> On a minor note: not sure why the authors present a methodology to evaluate the dynamic bone formation (line 272) but do not present results (i.e. by means of histomorphometrical analyses) utilizing this methodology.

Reviewer #2 (Public Review):

Summary:<br /> This is a very well-written manuscript by Saenz de Meira and colleagues on a careful study reporting on the key role of glutamate transporter vGlut2 expression in the neurons of the ventral perimammillary nucleus (PMv) of the hypothalamus expressing the leptin receptor LepRb in energy homeostasis, puberty, and estrous cyclicity. The authors first show using cre-dependent chemogenetic viral tools that the selective activation of the PMv LepRb induces luteinizing hormone (LH) release. Then the authors demonstrate that the selective invalidation of vGlut2 in LepRb-expressing cells in the all body induces obesity and mild alteration of sexual maturation in both sexes and blunted estrous cyclicity in females. Finally, the authors knock out vGlut2 in PMv neurons in which they reintroduce LepRb expression in an otherwise LepRb-null background using an AAV Cre approach. This latter very elegant experiment shows that while the sole re-expression of LepRb in PMv neurons in LepRb-null mice was shown before to restore puberty onset, deleting vGlut2 in LepRb-expressing PMv neurons blunts this effect.

Strengths:<br /> The authors employ state-of-the-art methods and their conclusions are robustly supported by the results.

Weaknesses:<br /> None identified. Only minor comments have been formulated.

eLife assessment

This important study reports a potential mechanism by which glutamate transmission from the LepRb PMv neurons influences the neuroendocrine reproductive axis. The genetic method to simultaneously remove glutamate signaling and restore the leptin receptor in LepRb PMv neurons is compelling, and most of the data are solid. The impact of the study would be enhanced if the authors could address the concerns raised by the three reviewers. This study will be of interest to biomedical researchers working on reproduction, endocrinology, and metabolism.

Reviewer #1 (Public Review):

Summary:<br /> In previous work, the Elias group has shown that leptin-sensing PMv neurons make connections with the neuroendocrine reproductive axis and are involved in reproductive function/s. Sáenz de Miera et al. build on this body of work to investigate the sufficiency of leptin sensing PMv neurons to evoke the release of luteinizing hormone. The team further investigates how glutamate signaling from leptin-sensing neurons can influence pubertal timing in females, along with mature estrous cycles. Genetic ablation of Slc17a6 (Vglut2) from LepRb-expressing cells resulted in a delay of the first estrus cycle post-pubertal transition, along with a significantly lengthened estrous cycle in mature females. However, this deficit did not lengthen the latency to the birth of the first litter in experimental dams. Restoration of leptin signaling in LepRb PMv neurons was previously shown to induce puberty and instate reproductive function in LepRb knock-out female mice (Mahany et al., 2018). Here, Sáenz de Miera et al. use a combined genetic and viral strategy to demonstrate that glutamate signaling in LepRb PMv neurons is required for sexual maturation in LepRb knock-out female mice.

Strengths:<br /> Most of the experiments performed in this manuscript are well-justified and rigorously tested. The genetic method to simultaneously remove glutamate signaling and restore the leptin receptor in LepRb PMv neurons was well executed and showed that glutamate signaling in LepRb PMv neurons is necessary for leptin-dependent fertility.

Weaknesses:<br /> Analysis of experimentally induced luteinizing hormone release could be confounded by spontaneous pulses of luteinizing hormone that are independent of LepRb PMv neurons.

Reviewer #3 (Public Review):

Summary:<br /> The authors examined the effects of glutamate release from PMv LepR neurons in the regulation of puberty and reproduction in female mice.

Strengths:<br /> Multiple genetic mouse models were utilized to either manipulate PMv LepR neuron activities, or to delete glutamate vesicle transporters from LepR neurons. The authors have been quite rigorous in validating these models and exploring potential contaminations. Most of the data presented are solid and convincing and support the conclusion.

Weaknesses:<br /> Some results are hard to interpret.

Reviewer #3 (Public Review):

Summary:<br /> The manuscript by Yujiro Umezaki and colleagues aims to describe how taste stimuli influence temperature preference in Drosophila. Under starvation flies display a strong preference for cooler temperatures than under fed conditions that can be reversed by refeeding, demonstrating the strong impact of metabolism on temperature preference. In their present study, Umezaki and colleagues observed that such changes in temperature preference are not solely triggered by the metabolic state of the animal but that gustatory circuits and peptidergic signalling play a pivotal role in gustation-evoked alteration in temperature preference.

The study of Umezaki is definitively interesting and the findings in this manuscript will be of interest to a broad readership.

Strengths:<br /> The authors demonstrate interesting new data on how taste input can influence temperature preference during starvation. They propose how gustatory pathways may work together with thermosensitive neurons, peptidergic neurons and finally try to bridge the gap between these neurons and clock genes. The study is very interesting and the data for each experiment alone are very convincing.

Weaknesses:<br /> In my opinion, the authors have opened many new questions but did not fully answer the initial question - how do taste-sensing neurons influence temperature preferences? What are the mechanisms underlying this observation? Instead of jumping from gustatory neurons to thermosensitive neurons to peptidergic neurons to clock genes, the authors should have stayed within the one question they were asking at the beginning. How does sugar sensing influence the physiology of thermos-sensation in order to change temperature preference? Before addressing all the following questions of the manuscript the authors should first directly decipher the neuronal interplay between these two types of neurons.

eLife assessment

This paper presents valuable findings that gustation and nutrition might independently influence the preferred environmental temperature in flies. While some of the evidence is solid, support for other claims appears incomplete at this stage but can be addressed with some further experimentation. The finding that flies might thus exhibit a cephalic phase response similar to mammals will be of value for future investigations.

Reviewer #1 (Public Review):

Summary:<br /> This paper presents valuable findings that gustation and feeding state influence the preferred environmental temperature preference in flies. Interestingly, the authors showed that by refeeding starved animals with the non-nutritive sugar sucralose, they are able to tune their preference towards a higher temperature in addition to nutrient-dependent warm preference. The authors show that temperature-sensing and sweet-sensing gustatory neurons (SGNs) are involved in the former but not the latter. In addition, their data indicate that peptidergic signals involved in internal state and clock genes are required for taste-dependent warm preference behavior.

The authors made an analogy of their results to the cephalic phase response (CPR) in mammals where the thought, sight, and taste of food prepare the animal for the consumption of food and nutrients. They further linked this behavior to core regulatory genes and peptides controlling hunger and sleep in flies having homologues in mammals. These valuable behavioral results can be further investigated in flies with the advantage of being able to dissect the neural circuitry underlying CPR and nutrient homeostasis.

Strengths:<br /> (1) The authors convincingly showed that tasting is sufficient to drive warm temperature preference behavior in starved flies and that it is independent of nutrient-driven warm preference.

(2) By using the genetic manipulation of key internal sensors and genes controlling internal feeding and sleep states such as DH44 neurons and the per genes for example, the authors linked gustation and temperature preference behavior control to the internal state of the animal.

Weaknesses:<br /> (1) The title is somewhat misleading, as the term homeostatic temperature control linked to gustation only applies to starved flies.

(2) The authors used a temperature preference assay and refeeding for 5 minutes, 10 minutes, and 1 hour. Experimentally, it makes a difference if the flies are tested immediately after 10 minutes or at the same time point as flies allowed to feed for 1 hour. Is 10 minutes enough to change the internal state in a nutrition-dependent manner? Some of the authors' data hint at it (e.g. refeeding with fly food for 10 minutes), but it might be relevant to feed for 5/10 minutes and wait for 55/50min to do the assays at comparable time points.

(3) A figure depicting the temperature preference assay in Figure 1 would help illustrate the experimental approach. It is also not clear why Figure 1E is shown instead of full statistics on the individual panels shown above (the data is the same).

(4) The authors state that feeding rate and amount were not changed with sucralose and glucose. However, the FLIC assay they employed does not measure consumption, so this statement is not correct, and it is unclear if the intake of sucralose and glucose is indeed comparable. This limits some of the conclusions.

(5) The authors make a distinction between taste-induced and nutrient-induced warm preference. Yet the statistics in most figures only show the significance between the starved and refed flies, not the fed controls. As the recovery is in many cases incomplete and used as a distinction of nutritive vs non-nutritive signals (see Figure 1E) it will be important to also show these additional statistics to allow conclusions about how complete the recovery is.

(6) The starvation period used is ranging from 1 to 3 days, as in some cases no effect was seen upon 1 day of starvation (e.g. with clock genes or temperature sensing neurons). While the authors do provide a comparison between 18-21 and 26-29 hours old flies in Figure S1, a comparison for 42-49 and 66-69 hours of starvation is missing. This also limits the conclusion as the "state" of the animal is likely quite different after 1 day vs. 3 days of starvation and, as stated by the authors, many flies die under these conditions.

(7) In Figure 2, glucose-induced refeeding was not tested in Gr mutants or silenced animals, which would hint at post-ingestive recovery mechanisms related to nutritional intake. This is only shown later (in Figure S3) but I think it would be more fitting to address this point here. The data presented in Figure S3 regarding the taste-evoked vs nutrient-dependent warm preference is quite important while in some parts preliminary. It would nonetheless be justified to put this data in the main figures. However, some of the conclusions here are not fully supported, in part due to different and low n numbers, which due to the inherent variability of the behavior do not allow statistically sound conclusions. The authors claim that sweet GRNs are only involved in taste-induced warm preference, however, glucose is also nutritive but, in several cases, does not rescue warm preference at all upon removal of GRN function (see Figures S3A-C). This indicates that the Gal4 lines and also the involved GRs are potentially expressed in tissues/neurons required for internal nutrient sensing.

(8) In Figure 4, fly food and glucose refeeding do not fully recover temperature preference after refeeding. With the statistical comparison to the fed control missing, this result is not consistent with the statement made in line 252. I feel this is an important point to distinguish between state-dependent and taste/nutrition-dependent changes.

(9) The conclusion that clock genes are required for taste-evoked warm preference is limited by the observation that they ingest less sucralose. In addition, the FLIC assay does not allow conclusions about the feeding amount, only the number of food interactions. Therefore, I think these results do not allow clear-cut conclusions about the impact of clock genes in this assay.

(10) CPR is known to be influenced by taste, thought, smell, and sight of food. As the discussion focused extensively on the CPR link to flies it would be interesting to find out whether the smell and sight of food also influence temperature preference behavior in animals with different feeding states.

(11) In the discussion in line 410ff the authors claim that "internal state is more likely to be associated with taste-evoked warm preference than nutrient-induced warm preference." This statement is not clear to me, as neuropeptides are involved in mediating internal state signals, both in the brain itself as well as from gut to brain. Thus, neuropeptidergic signals are also involved in nutrient-dependent state changes, the authors might just not have identified the peptides involved here. The global and developmental removal of these signals also limits the conclusions that can be drawn from the experiments, as many of these signals affect different states, circuits, and developmental progression.

Reviewer #2 (Public Review):

Animals constantly adjust their behavior and physiology based on internal states. Hungry animals, desperate for food, exhibit physiological changes immediately upon sensing, smelling, or chewing food, known as the cephalic phase response (CPR), involving processes like increased saliva and gastrointestinal secretions. While starvation lowers body temperature, the mechanisms underlying how the sensation of food without nutrients induces behavioral responses remain unclear. Hunger stress induces changes in both behavior and physiological responses, which in flies (or at least in Drosophila melanogaster) leads to a preference for lower temperatures, analogous to the hunger-driven lower body temperature observed in mammals. In this manuscript, the authors have used Drosophila melanogaster to investigate the issue of whether taste cues can robustly trigger behavioral recovery of temperature preference in starving animals. The authors find that food detection triggers a warm preference in flies. Starved flies recover their temperature preference after food intake, with a distinction between partial and full recovery based on the duration of refeeding. Sucralose, an artificial sweetener, induces a warm preference, suggesting the importance of food-sensing cues. The paper compares the effects of sucralose and glucose refeeding, indicating that both taste cues and nutrients contribute to temperature preference recovery. The authors show that sweet gustatory receptors (Grs) and sweet GRNs (Gustatory Receptor Neurons) play a crucial role in taste-evoked warm preference. Optogenetic experiments with CsChrimson support the idea that the excitation of sweet GRNs leads to a warm preference. The authors then examine the internal state's influence on taste-evoked warm preference, focusing on neuropeptide F (NPF) and small neuropeptide F (sNPF), analogous to mammalian neuropeptide Y. Mutations in NPF and sNPF result in a failure to exhibit taste-evoked warm preference, emphasizing their role in this process. However, these neuropeptides appear not to be critical for nutrient-induced warm preference, as indicated by increased temperature preference during glucose and fly food refeeding in mutant flies. The authors also explore the role of hunger-related factors in regulating taste-evoked warm preference. Hunger signals, including diuretic hormone (DH44) and adipokinetic hormone (AKH) neurons, are found to be essential for taste-evoked warm preference but not for nutrient-induced warm preference. Additionally, insulin-like peptides 6 (Ilp6) and Unpaired3 (Upd3), related to nutritional stress, are identified as crucial for taste-evoked warm preference. The investigation then extends into circadian rhythms, revealing that taste-evoked warm preference does not align with the feeding rhythm. While flies exhibit a rhythmic feeding pattern, taste-evoked warm preference occurs consistently, suggesting a lack of parallel coordination. Clock genes, crucial for circadian rhythms, are found to be necessary for taste-evoked warm preference but not for nutrient-induced warm preference.

Strengths:<br /> A well-written and interesting study, investigating an intriguing issue. The claims, none of which to the best of my knowledge controversial, are backed by a substantial number of experiments.

Weakness:<br /> The experimental setup used and the procedures for assessing the temperature preferences of flies are rather sparingly described. Additional details and data presentation would enhance the clarity and replicability of the study. I kindly request the authors to consider the following points: i) A schematic drawing or diagram illustrating the experimental setup for the temperature preference assay would greatly aid readers in understanding the spatial arrangement of the apparatus, temperature points, and the positioning of flies during the assay. The drawing should also be accompanied by specific details about the setup (dimensions, material, etc). ii) It would be beneficial to include a visual representation of the distribution of flies within the temperature gradient on the apparatus. A graphical representation, such as a heatmaps or histograms, showing the percentage of flies within each one-degree temperature bin, would offer insights into the preferences and behaviors of the flies during the assay. In addition to the detailed description of the assay and data analysis, the inclusion of actual data plots, especially for key findings or representative trials, would provide readers with a more direct visualization of the experimental outcomes. These additions will not only enhance the clarity of the presented information but also provide the reader with a more comprehensive understanding of the experimental setup and results. I appreciate the authors' attention to these points and look forward to the potential inclusion of these elements in the revised manuscript.

eLife assessment

This useful study reports that a water-soluble analog of heliomycin, 4-dmH, induces protein degradation of not only SirT1 but also tNOX, unlike heliomycin, which induces degradation of SirT1 but not tNOX, a difference that could in principle explain why 4-dmH induces apoptosis while heliomycin induces autophagy. The presented data provide solid support for the authors' conclusions.

eLife assessment

This study presents a valuable finding on the roles and mechanisms of FYN and KDM4 in TNBC tumor cell resistance. The evidence supporting the claims of the authors is somewhat incomplete and the refinement of certain experiments would have strengthened the study. Noteworthy, FYN has been implied in drug resistance previously and this should be carefully discussed in the manuscript. The work will be of interest to scientists working on breast cancer.

Reviewer #1 (Public Review):

Summary:<br /> The authors employed a combinatorial CRISPR-Cas9 knockout screen to uncover synthetically lethal kinase genes that could play a role in drug resistance to kinase inhibitors in triple-negative breast cancer. The study successfully reveals FYN as a mediator of resistance to depletion and inhibition of various tyrosine kinases, notably EGFR, IGF-1R, and ABL, in triple-negative breast cancer cells and xenografts. Mechanistically, they demonstrate that KDM4 contributes to the upregulation of FYN and thereby is an important mediator of drug resistance. All together, these findings suggest FYN and KDM4A as potential targets for combination therapy with kinase inhibitors in triple-negative breast cancer. Moreover, the study may also have important implications for other cancer types and other inhibitors, as the authors suggest that FYN could be a general feature of drug-tolerant persister cells.

Strengths:<br /> (1) The authors used a large combination matrix of druggable tyrosine kinase gene knockouts, enabling studying of co-dependence of kinase genes. This approach mitigates off-target effects typically associated with kinase inhibitors, enhancing the precision of the findings.

(2) The authors demonstrate the importance of FYN in drug resistance in multiple ways. They demonstrate synergistic interactions using both knockouts and inhibitors, while also revealing its transcriptional upregulation upon treatment, strengthening the conclusion that FYN plays a role in the resistance.

(3) The study extends its impact by demonstrating the potent in vivo efficacy of certain combination treatments, underscoring the clinical relevance of the identified strategies.

Weaknesses:<br /> (1) The methods and figure legends are incomplete, posing a barrier to the reproducibility of the study and hindering a comprehensive understanding and accurate interpretation of the results.

(2) The authors make use of a large quantity of public data (Fig. 2D/E, Fig. 3F/L/M, Fig 4C, Fig 5B/H/I), whereas it would have strengthened the paper to perform these experiments themselves. While some of this data would be hard to generate (e.g. patient data) other data could have been generated by the authors. The disadvantage of the use of public data is that it merely comprises associations, but does not have causal/functional results (e.g. FYN inhibition in the different cancer models with various drugs). Moreover, by cherry-picking the data from public sources, the context of these sources is not clear to the reader, and thus harder to interpret correctly. For example, it is not directly clear whether the upregulation of FYN in these models is a very selective event or whether it is part of a very large epigenetic re-programming, where other genes may be more critical. While some of the used data are from well-known curated databases, others are from individual papers that the reader should assess critically in order to interpret the data. Sometimes the public data was redundant, as the authors did do the experiments themselves (e.g. lung cancer drug-tolerant persisters), in this case, the public data could also be left out.

More importantly, the original sources are not properly cited. While the GEO accession numbers are shown in a supplementary table, the articles corresponding to this data should be cited in the main text, and preferably also in the figure legend, to clarify that this data is from public sources, which is now not always the case (e.g. line 224-226). If these original papers do already mention the upregulation of FYN, and the findings from the authors are thus not original, these findings should be discussed in the Discussion section instead of shown in the Results.

(3) The claim in the abstract (and discussion) that the study "highlights FYN as broadly applicable mediator of therapy resistance and persistence", is not sufficiently supported by the results. The current study only shows functional evidence for this for an EGFR, IGF1R, and Abl inhibitor in TNBC cells. Further, it demonstrates (to a limited extent) the role of FYN in gefitinib and osimertinib resistance (also EGFR inhibitors) in lung cancer cells. Thus, the causal evidence provided is only limited to a select subset of tyrosine kinase inhibitors in two cancer types. While the authors show associations between FYN and drug resistance in other cancer types and after other treatments, these associations are not solid evidence for a causal connection as mentioned in this statement. Epigenetic reprogramming causing drug resistance can be accompanied by altered gene expression of many genes, and the upregulation of FYN may be a consequence, but not a cause of the drug resistance. Therefore, the authors should be more cautious in making such statements about the broad applicability of FYN as a mediator of therapy resistance.

(4) The rationale for picking and validating FYN as the main candidate gene over other genes such as FGFR2, FRK2, and TEK is not clear.<br /> a. While gene pairs containing FGFR2 knockouts seemed to be equally effective as FYN gene pairs in the primary screening, these could not be validated in the validation experiment. It is unclear whether multiple individual or a pool of gRNAs were used for this validation, or whether only 1 gRNA sequence was picked per gene for this validation. If only 1 gRNA per gene was used, this likely would have resulted in variable knockout efficiencies. Moreover, the T7 endonuclease assay may not have been the best method to check knockout efficiency, as it only implies endonuclease activity around a gene (but not to the extent of indels that can cause frameshifts, such as by TIDE analysis, or extent of reduction in protein levels by western blot).<br /> b. Moreover, FRK2 and TEK, also demonstrated many synergistic gene pairs in the primary screen. However, many of these gene pairs were not included in the validation screening. The selection criteria of candidate gene pairs for validation screening is not clear. Still, TEK-ABL2 was also validated as a strong hit in the validation screen. The authors should better explain the choice of FYN over other hits, and/or mention that TEK and FRK2 may also be important targets for combination treatment that can be further elucidated.

(5) On several occasions, the right controls (individual treatments, performed in parallel) are not included in the figures. The authors should include the responses to each of the single treatments, and/or better explain the normalization that might explain why the controls are not shown.<br /> a. Figure 2G: The effect of PP2 treatment, without combined treatment, is not shown.<br /> b. Figure 2H/3G: The effect of the knockouts on growth alone, compared to sgGFP, is not demonstrated. It is unclear whether the viability of knockouts is normalized to sgGFP, or to each untreated knockout.<br /> c. Figure 2L: The effect of SB203580 as a single treatment is not shown.

(6) The study examines the effects at a single, relatively late time point after treatment with inhibitors, without confirming the sequential impact on KDM4A and FYN. The proposed sequence of transcriptional upregulation of KDM4A followed by epigenetic modifications leading to FYN upregulation would be more compellingly supported by demonstrating a consecutive, rather than simultaneous, occurrence of these events. Furthermore, the protein level assessment at 48 hours (for RNA levels not clearly described), raises concerns about potential confounding factors. At this late time point, reduced cell viability due to the combination treatment could contribute to observed effects such as altered FYN expression and P38 MAPK phosphorylation, making it challenging to attribute these changes solely to the specific and selective reduction of FYN expression by KDM4A.

(7) The cut-off for considering interactions "synergistic" is quite low. The manual of the used "SynergyFinder" tool itself recommends values above >10 as synergistic and between -10 and 10 as additive (https://synergyfinder.fimm.fi/synergy/synfin_docs/). Here, values between 5-10 are also considered synergistic. Caution should be taken when discussing those results. Showing the actual dose response (including responses to each single treatment) may be required to enable the reader to critically assess the synergy, along with its standard deviation.

(8) As the effect size on Western blots is quite limited and sometimes accompanied by differences in loading control, these data should be further supported by quantifications of signal intensities of at least 3 biological replicates (e.g. especially Figure 3A/5A). The figure legends should also state how many independent experiments the blots are representative of.

(9) While the article provides mechanistic insights into the likely upregulation of FYN by KDM4A, this constitutes only a fragment of the broader mechanism underlying drug resistance associated with FYN. The study falls short in investigating the causes of KDM4A upregulation and fails to explore the downstream effects (except for p38 MAPK phosphorylation, which may not be complete) of FYN upregulation that could potentially drive sustained cell proliferation and survival. These omissions limit the comprehensive understanding of the complete molecular pathway, and the discussion section does not address potential implications or pathways beyond the identified KDM4A-FYN axis. A more thorough exploration of these aspects would enhance the study's contribution to the field.

(10) FYN has been implied in drug resistance previously, and other mechanisms of its upregulation, as well as downstream consequences, have been described previously. These were not evaluated in this paper, and are also not discussed in the discussion section. Moreover, the authors did not investigate whether any of the many other mechanisms of drug resistance to EGFR, IGF1R, and Abl inhibitors that have been described, could be related to FYN as well. A more comprehensive examination of existing literature and consideration of alternative or parallel mechanisms in the discussion would enhance the paper's contribution to understanding FYN's involvement in drug resistance.

Reviewer #2 (Public Review):

Summary:<br /> Kim et al. conducted a study in which they selected 76 tyrosine kinases and performed CRISPR/Cas9 combinatorial screening to target 3003 genes in Triple-negative breast cancer (TNBC) cells. Their investigation revealed a significant correlation between the FYN gene and the proliferation and death of breast cancer cells. The authors demonstrated that depleting FYN and using FYN inhibitors, in combination with TKIs, synergistically suppressed the growth of breast cancer tumor cells. They observed that TKIs upregulate the levels of FYN and the histone demethylase family, particularly KDM4, promoting FYN expression. The authors further showed that KDM4 weakens the H3K9me3 mark in the FYN enhancer region, and the inhibitor QC6352 effectively inhibits this process, leading to a synergistic induction of apoptosis in breast cancer cells along with TKIs. Additionally, the authors discovered that FYN is upregulated in various drug-resistant cancer cells, and inhibitors targeting FYN, such as PP2, sensitize drug-resistant cells to EGFR inhibitors.

Strengths:<br /> This study provides new insights into the roles and mechanisms of FYN and KDM4 in tumor cell resistance.

Weaknesses:<br /> It is important to note that previous studies have also implicated FYN as a potential key factor in drug resistance of tumor cells, including breast cancer cells. While the current study is comprehensive and provides a rich dataset, certain experiments could be refined, and the logical structure could be more rigorous. For instance, the rationale behind selecting FYN, KDM4, and KDM4A as the focus of the study could be more thoroughly justified.

eLife assessment

This potentially useful study reports a new method for restoring sperm motility. Strengths are in the methodology being developed, but the conclusions require additional experimental support. The authors provide inadequate evidence for the success of the method or its mechanism.

Reviewer #1 (Public Review):

The authors assess the effectiveness of electroporating mRNA into male germ cells to rescue the expression of proteins required for spermatogenesis progression in individuals where these proteins are mutated or depleted. To set up the methodology, they first evaluated the expression of reporter proteins in wild-type mice, which showed expression in germ cells for over two weeks. Then, they attempted to recover fertility in a model of late spermatogenesis arrest that produces immotile sperm. By electroporating the mutated protein, the authors recovered the motility of ~5% of the sperm, although the sperm regenerated was not able to produce offspring using IVF.

This is a comprehensive evaluation of the mRNA methodology with multiple strengths. First, the authors show that naked synthetic RNA, purchased from a commercial source or generated in the laboratory with simple methods, is enough to express exogenous proteins in testicular germ cells. The authors compared RNA to DNA electroporation and found that germ cells are efficiently electroporated with RNA, but not DNA. The differences between these constructs were evaluated using in vivo imaging to track the reporter signal in individual animals through time. To understand how the reporter proteins affect the results of the experiments, the authors used different reporters: two fluorescent (eGFP and mCherry) and one bioluminescent (Luciferase). Although they observed differences among reporters, in every case expression lasted for at least two weeks.

The authors used a relevant system to study the therapeutic potential of RNA electroporation. The ARMC2-deficient animals have impaired sperm motility phenotype that affects only the later stages of spermatogenesis. The authors showed that sperm motility was recovered to ~5%, which is remarkable due to the small fraction of germ cells electroporated with RNA with the current protocol. The 3D reconstruction of an electroporated testis using state-of-the-art methods to show the electroporated regions is compelling.

The main weakness of the manuscript is that although the authors manage to recover motility in a small fraction of the sperm population, it is unclear whether the increased sperm quality is substantial to improve assisted reproduction outcomes. The quality of the sperm was not systematically evaluated in the manuscript, with the endpoints being sperm morphology and sperm mobility.

Some key results, such as the 3D reconstruction of the testis and the recovery of sperm motility, are qualitative given the low replicate numbers or the small magnitude of the effects. The presentation of the sperm motility data could have been clearer as well. For example, on day 21 after Armc2-mRNA electroporation, only one animal out of the three tested showed increased sperm motility. However, it is unclear from Figure 11A what the percentage of sperm motility for this animal is since the graph shows a value of >5% and the reported aggregate motility is 4.5%. It would have been helpful to show all individual data points in Figure 11A.

The expression of the reporter genes is unambiguous; however, better figures could have been presented to show cell type specificity. The DAPI staining is diffused, and it is challenging to understand where the basement membranes of the tubules are. For example, in Figures 7B3 and 7E3, the spermatogonia seems to be in the middle of the seminiferous tubule. The imaging was better for Figure 8. Suboptimal staining appears to lead to mislabeling of some germ cell populations. For example, in Supplementary Figure 4A3, the round spermatid label appears to be labeling spermatocytes. Also, in some instances, the authors seem to be confusing, elongating spermatids with spermatozoa, such as in the case of Supplementary Figures 4D3 and D4.

The characterization of Armc2 expression could have been improved as well. The authors show a convincing expression of ARMC2 in a few spermatids/sperm using a combination of an anti-ARMC2 antibody and tubules derived from ARMC2 KO animals. At the minimum, one would have liked to see at least one whole tubule of a relevant stage.

Overall, the authors show that electroporating mRNA can improve spermatogenesis as demonstrated by the generation of motile sperm in the ARMC2 KO mouse model.

Reviewer #2 (Public Review):

Summary:

Here, the authors inject naked mRNAs and plasmids into the rete testes of mice to express exogenous proteins - GFP and later ARMC2. This approach has been taken before, as noted in the Discussion to rescue Dmc1 KO infertility. While the concept is exciting, multiple concerns reduce reviewer enthusiasm.

Strengths:

The approach, while not necessarily novel, is timely and interesting.

Weaknesses:

Overall, the writing and text can be improved and standardized - as an example, in some places in vivo is italicized, in others it's not; gene names are italicized in some places, others not; some places have spaces between a number and the units, others not. This lack of attention to detail in the preparation of the manuscript is a significant concern to this reviewer - the presentation of the experimental details does cast some reasonable concern with how the experiments might have been done. While this may be unfair, it is all the reviewers have to judge. Multiple typographical and grammatical errors are present, and vague or misleading statements.

Reviewer #3 (Public Review):

Summary:

The authors used a novel technique to treat male infertility. In a proof-of-concept study, the authors were able to rescue the phenotype of a knockout mouse model with immotile sperm using this technique. This could also be a promising treatment option for infertile men.

Strengths:

In their proof-of-concept study, the authors were able to show that the novel technique rescues the infertility phenotype in vivo.

Weaknesses:

Some minor weaknesses, especially in the discussion section, could be addressed to further improve the quality of the manuscript.

It is very convincing that the phenotype of Armc2 KO mice could (at least in part) be rescued by injection of Armc2 RNA. However, a central question remains about which testicular cell types have been targeted by the constructs. From the pictures presented in Figures 7 and 8, this issue is hard to assess. Given the more punctate staining of the DNA construct a targeting of Sertoli cells is more likely, whereas the more broader staining of seminiferous tubules using RNA constructs is talking toward germ cells.

Further, the staining for up to 119 days (Figure 5) would point toward an integration of the DNA construct into the genome of early germ cells such as spermatogonia and/or possibly to Sertoli cells. Given the expression after RNA transfection for up to 21 days (Figure 4) and the detection of motile sperm after 21 days (Figure 11), this would point to either round spermatids or spermatocytes.

These aspects need to be discussed more carefully (discussion section: lines 549-574).

It would also be very interesting to know in which testicular cell type Armc2 is endogenously expressed (lines 575-591).

eLife assessment

This important study links the activity of polymerase III to the regulation of virulence gene expression in the deadliest malaria parasite, Plasmodium falciparum. It identifies Maf1 as a Pol III inhibitor that enables the parasite to respond to external stimuli such as magnesium chloride plasma levels by downregulating Pol III-transcribed ruf6 genes and subsequently regulated var genes. While the evidence presented is generally convincing, some of the results are incomplete, and the mechanistic link between external signals and Maf1 activation remains unknown.

Reviewer #1 (Public Review):

Summary:

Asymptomatic malaria infections are frequent during the dry season and have been associated with lower cytoadherence of P. falciparum parasites and lower expression of variant surface antigens. The mechanisms underlying parasite adaptation during the low transmission season remain poorly understood. The authors previously established that members of the non-coding RNA RUF6 gene family, transcribed by RNA pol III, are required for expression of the main variant surface antigens in P. falciparum, PfEMP1, which drive parasite cytoadherence and pathogenicity. In this study, the authors investigated the contribution of RNA pol III transcription in the regulation of PfEMP1 expression in different clinical states, either symptomatic malaria cases during the wet season or asymptomatic infections during the dry season.

By reanalyzing RNAseq data from a previous study in Mali, complemented with RT-qPCR on new samples collected in The Gambia, the authors first report the down-regulation of RNA pol III genes (tRNAs, RUF6) in P. falciparum isolates collected from asymptomatic individuals during the dry season, as compared to isolates from symptomatic (wet season) individuals. They also confirm the down-regulation of var (DBLalpha) gene expression in asymptomatic infection as compared to symptomatic malaria. Plasma analysis in the two groups in the Gambian study reveals higher Magnesium levels in the dry season as compared to wet season samples, pointing at a possible role of external factors. The authors tested the effect of MgCl2 supplementation on cultured parasites, as well as three other stimuli (temperature, low glucose, Ile deprivation), and showed that Ile deprivation and MgCl2 both induce down-regulation of RNA pol III transcription but not pol I or pol II (except the active var gene). Using RNAseq, they show that MgCl2 supplementation predominantly inhibits RNA pol III-transcribed genes, including the entire RUF6 family. Conditional depletion of Maf1 leads to the up-regulation of RNA pol III gene transcription, confirming that Maf1 is a RNA pol III inhibitor in P. falciparum, as described in other organisms. Quantitative mass spectrometry shows that Maf1 interacts with RNA pol III complex in the nucleus, and with distinct proteins including two phosphatases in the cytoplasm. Using the Maf1 cKD parasites, the authors document that the down-regulation of RNA pol III by MgCl2 is dependent on Maf1. Finally, they show that MgCl2 results in decreased cytoadherence of infected erythrocytes, associated with reduced PfEMP1 expression.

Strengths:

-The work is very well performed and presented.<br /> -The study uncovers a novel regulatory mechanism relying on RNA pol III-dependent regulation of variant surface antigens in response to external signals, which could contribute to parasite adaptation during the low transmission season.<br /> -Potential regulators of Maf1 were identified by mass spectrometry, including phosphatases, paving the way for future mechanistic studies.

Weaknesses:

-The signaling pathway upstream of Maf1 remains unknown. In eukaryotes, Maf1 is a negative regulator of RNA pol III and is regulated by external signals via the TORC pathway. Since TORC components are absent in the apicomplexan lineage, one central question that remains open is how Maf1 is regulated in P. falciparum. Magnesium is probably not the sole stimulus involved, as suggested by the observation that Ile deprivation also down-regulates RNA pol III activity.<br /> -The study does not address why MgCl2 levels vary depending on the clinical state. It is unclear whether plasma magnesium is increased during asymptomatic malaria or decreased during symptomatic infection, as the study does not include control groups with non-infected individuals. Along the same line, MgCl2 supplementation in parasite cultures was done at 3mM, which is higher than the highest concentrations observed in clinical samples.<br /> -Although the study provides biochemical evidence of Maf1 accumulation in the parasite nuclear fraction upon magnesium addition, this is not fully supported by the immunofluorescence experiments.

Reviewer #2 (Public Review):

Summary:

The study by Diffendall et al. set out to establish a link between the activity of RNA polymerase III (Pol III) and its inhibitor Maf1 and the virulence of Plasmodium falciparum in vivo. Having previously found that knockdown of the ncRNA ruf6 gene family reduces var gene expression in vitro, they now present experimental evidence for the regulation of ruf6 and subsequently, var gene expression by Pol III using a commercially available inhibitor. They confirm their findings with samples from a previously published Gambian cohort study using asymptomatic dry season and mildly symptomatic wet season samples, showing that higher levels of Pol III-dependent transcripts and var transcripts as well as lower MgCl2 plasma concentrations are present in wet season samples. From this, they hypothesize that the external stimuli heat, reduced glucose and essential amino acid supply, and increased MgCl2 levels are sensed by the parasite through the only known Pol III inhibitor Maf1 and result in lower Pol III activity and fewer ruf6 transcripts, which in turn reduces var gene expression, leading to reduced cytoadherence and virulence of P. falciparum. In their in vitro experiments they focus on investigating higher MgCl2 levels and their impact on Pol III and Maf1 activity as well as var gene expression and parasites adherence to purified CD36, thereby successfully confirming their hypothesis for MgCl2. Nicely, MgCl2-induced down-regulation of Pol III activity was shown to be dependent on Maf1 using a knock-down cell line. Additionally, they show that the Maf1-KD cell line displays a slower growth rate with fewer merozoites per schizonts and Maf1 interacts with RNA pol III subunits and some kinases/phosphatases.

Strengths:

Overall, the authors were largely successful in their aims. They provide largely convincing data, and the correlation between Pol III transcription and its inhibition by Maf1 with the expression of ruf6 and var genes is highly interesting. The data provide important insights for researchers investigating the function of Pol III and its inhibitor, non-coding RNAs, and their role in gene regulation, but may also indicate that the parasite senses and responds to its environment, opening up new research directions, particularly in field research.

Weaknesses:

However, most analyses are rather preliminary as only very few (3-5) candidate genes are analyzed by qPCR instead of carrying out comprehensive analyses with a large qPCR panel or RNA-seq experiments with GO term analyses. Data presentation lacks clarity, the number of biological replicates is rather low and the statistical analyses need to be largely revised. Although the in vivo data from wet (mildly symptomatic) and dry (asymptomatic) season parasites with different expression levels of Pol III-regulated genes, var genes, and MgCl2 are interesting, the link between the in vitro data and the in vivo virulence of P. falciparum, which is made in many sections of the manuscript, should be toned down. Especially since (i) the only endothelial receptor studied is CD36, which is associated with parasite binding during mild malaria, and (ii) several studies provide contradictory data on MgCl2 levels during malaria and in different disease states, which is not further discussed, but the authors mainly focused on this external stimulus in their experiments.

Reviewer #3 (Public Review):

Summary:

This work describes a new pathway by which malaria parasites, P. falciparum, may regulate their growth and virulence (i.e. their expression of virulence-linked cytoadhesins). This is a topic of considerable interest in the field - does this important parasite sense factor(s) in its host bloodstream and regulate itself accordingly? Several fragments of evidence have come out on this topic in the past decade, showing, for example, reduced parasite growth under calorie restriction (in mice); parasite dormancy in response to amino acid starvation (in culture and in mice), and also reduced virulence in dry-season, low-parasitaemia infections in humans. The molecular mechanisms that may underlie this interesting biology remain only poorly understood.

Here, the authors show that dry-season P. falciparum parasites have reduced expression of Pol3-transcribed tRNAs and ncRNAs that positively regulate virulence gene expression. They link the level of Pol3 activity to PfMaf1, a remnant of the largely-absent nutrient-sensing TOR pathway in this parasite. They propose that in the dry season, human hosts may be calorie-restricted, leading to Maf1 moving to the nucleus and suppressing Pol3, thus downregulated growth and virulence of parasites. The evidence is intriguing and the idea is conceptually elegant.

Strengths:

The use of dry/wet-season field samples from The Gambia is a strength, showing potential real-world relevance. The generation of an inducible knockdown of Maf1 in lab-cultured parasites is also a strength, allowing this pathway to be studied somewhat in isolation.

Weaknesses:

(1) The signals upstream of Maf1 remain rather a black box. 4 are tested - heat shock and low-glucose, which seem to suppress ALL transcription; low-Isoleucine and high magnesium, which suppress Pol3. Therefore the authors use Mg supplementation throughout as a 'starvation type' stimulus. They do not discuss why they didn't use amino acid limitation, which could be more easily rationalised physiologically. It may be for experimental simplicity (no need for dropout media) but this should be discussed, and ideally, sample experiments with low-IsoLeu should be done too, to see if the responses (e.g. cytoadhesion) are all the same.

(2) The proteomics, conducted to seek partners of Maf1, is probably the weakest part. From Figure S3: the proteins highlighted in the text are clearly highly selected (as ones that might be relevant, e.g. phosphatases), but many others are more enriched. It would be good to see the whole list, and which GO terms actually came top in enrichment.

(3) Figure 3 shows the Maf1-low line has very poor growth after only 5 days but it is stated that no dead parasites are seen even after 8 cycles and the merozoites number is down only ~18 to 15... is this too small to account for such poor growth (~5-fold reduced in a single cycle, day 3-5)? It would additionally be interesting to see a cell-cycle length assessment and invasion assay, to see if Maf1-low parasites have further defects in growth.

Author Response

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

Reviewer #1 (Recommendations for The Authors):

To hopefully contribute to more strongly support the conclusions of the manuscript, I am including a series of concerns regarding the experiments, as well as some recommendations that could be followed to address these issues:

(1) The Q-nMT bundle is largely unaffected by the nocodazole treatment in most phases during its formation. However, cells were only treated with nocodazole for a very short period of time (15 min). Have the authors analyzed Q-nMT stability after longer nocodazole exposures? Is a similar treatment enough to depolymerize the mitotic spindle? This result could be further substantiated by treatment with other MT-depolymerizing agents. Furthermore, the dynamicity of the Q-nMT bundle could be ideally also assessed by other techniques, such as FRAP.

The experiments suggested by the reviewer have been published in our previous paper (Laporte et al, JCB 2013). In this previous study, we presented data demonstrating the resistance of the Q-nMT bundle to several MT poisons: TBZ, benomyl, MBC (Sup Fig 2D) and to an increasing amount of nocodazole after a 90 min treatment (Sup Fig2E). These published figures are provided below.

Author response image 1.

The nMT array contains highly stable MTS. (A) Variation Of nuclear MT length in function Of time (second) in proliferating cells. Cells express GFP•Tubl (green) and Nup2•RFP (red). Bars, 2 pm. N = l, n is indicated. (B) Variation of the nMT array length in function of time measured for BirnlGFP—expressing cells In = 161, for 6-d•old Dad2GFP—expressing cells In = 171, for Stu2GFP—expressing cells (n = 17), and 6•d-old Nuf2• GFP—expressing cells (n = 17). Examples Of corresponding time lapse are shown. Time is in minutes experiments). Bar, 2 pm. (CJ Nuf2•GFP dots detected along nMT array (arrow) are immobile. Several time lapse images of cells are shown. Time is in minutes. gar, 2 pm _ MT organizations in proliferating cells and 4-d•old quiescent cells before and after a 90-min treatment With indicated drugs. Bar, 2 pm. (E) MT organizations in Sci-old quiescent cells before and after a 90min treatment With increasing concentrations Of nocodazole.

In the same article, we showed that Q-nMT bundles resist a 3h nocodazole treatment, while all MT structures assembled in proliferating cells, including mitotic spindle, vanished (see Fig 2E below). In addition, in our previous article, FRAP experiments were provided in Fig 2D.

Author response image 2.

The nuclear array is composed of stable MTS. Variation of the length in function of time of (A) aMTs in proliferating cells, (B) nMT array in quiescent cells (7 d), and the two MT structures in early quiescent cells (4 d). White arrows point ot dynamic aMTs. In A—C, N = 2, n is indicated ID) FRAP on 7-d-old quiescent cells. White arrows point to bleach areas. Error bars are SEM. In A—D. time is in seconds. (E) nMT array is not affected by nocodazole treatment. Before and various times after carbon exhaustion (red dashed line), cells were incubated for 3 h with 22.5 pg/pL nocodozole and then imaged. The corresponding control experiment is shown in Fig I A. In all panels, cells expressing GFP-TtJbl (green) and Nup2-RFP (red) are shown; bars, 2 pm.

This previous study was mentioned in the introduction and is now re-cited at the beginning of the results section (line 107-108).

As expected from our previous study, when proliferating cells were treated with Noc (30 µg/ml) in the same conditions as in Fig1, most of the short and the long mitotic spindles vanished after a 15 min treatment as shown in the graph below.

Author response image 3.

Proliferating cells expressing NOf2=GFP and mTQZ-TUb1 (00—2) were treated or not With NOC (30vgfmI) for 15 min.% Of cells With detectable MT and representative cells are shown. Khi-teet values are indicated. Bar: 2 pm,

(2) The graph in Figure 1B is somewhat confusing. Is the X-axis really displaying the length of the MTs as stated in the legend? If so, one would expect to see a displacement of the average MT length of the population as cells progress from phase II to phase III, as previously demonstrated in Figure 1A. Likewise, no data points would be anticipated for those phases in which the MT length is 0 or close to 0. Moreover, when the length of half pre-anaphase mitotic spindle was measured as a control, how can one get MT lengths that are equal or close to 0 in these cells? The length of the pre-anaphase spindle is between 2-4 um, so MT length values should range from 1 to 2 um if half the spindle is measured.

The graph in Fig1B represents the fluorescence intensity (a proxy for the Q-nMT bundle thickness) along the Q-nMT bundle length.

Fluorescence intensity is measured along a “virtual line” that starts 0,5 µm before the extremity of the QnMT bundle that is in contact with the SPB. In other words, we aligned all intensity measurements at the fluorescence increasing onset on the SPB side. We arbitrarily set the ‘zero’ at 0,5um before the fluorescence increased onset. That is why the fluorescence intensity is zero between 0 and 0,5 µm – The X-axis represents this virtual line, the 0 being set 0,5 µm before the Q-nMT bundle extremity on the SPB side. This virtual line allows us to standardize our “thickness” measurements for all Q-nMT bundles.

Using this standardization, it is clear that the length of the Q-nMT bundles increased from phase II to III (see the red arrow). Yet, as in phase II, Q-nMT bundles are not yet stable, their lengths are shorter in phase II than in phase II after a Noc treatment (compare the end of the orange line and the end of the blue line in phase II).

Author response image 4.

This is now explained in details in the Material and Methods section (line 539-545).

This is the same for the inset of Fig 1B and in Sup Fig 1A, in which we measured fluorescence intensity along the halfmitotic spindle just as we did for MT bundle. The X-axis represent a virtual line along the mitotic spindle, starting 0,5 µm before the SBP spindle extremity.

Author response image 5.

(3) Microtubules seem to locate next to or to extend beyond the nucleus in the control cells (DMSO) in Figure 1H. Since both nuclear MTs and cytoplasmic MTs emanate from the SPBs, it would have been desirable to display the morphology of the nucleus when possible. Moreover, since the nucleus is a tridimensional structure, it would also be advisable to image different Z-sections.

Analysis demonstrating that Q-nMT bundles are located inside the nucleus have been provided in our previous paper (Laporte et al, JCB 2013). In this article most of the images are maximal projections of Z-stacks in which the nuclear envelope is visualized via Nup2-RFP (see Fig1 of Laporte et al, JCB 2013 as an example below).

Author response image 6.

MTsare organized as a nuclear array in quiescent cells. (A) MT reorganization upon quiescence entry. Cells expressing GFP-Tub1 (green) and Nup2RFP (red) are shown. Glucose exhaustion is indicated as a red dashed line. Quiescent cells dl expressing Tub I-RFP and either Spc72GFP,

In Laporte et al, JCB 2013, we also provided EM analysis both in cryo and immune-gold (Fig 1E below).

Author response image 7.

(top) or coexpr;sse8 with Tub I-RFP (bottom). Arrows point dot along the nMT array. Bars: (A—C)) 2 pm. (E) AMT arroy visualized in WT cells by EMI Yellow arrows, MTS; red arrowheads, nuclear membrane; pink arrow, SPB. Insets: nMT cut transversally. Bar, 100 nm.

(4) Movies depicting the process of Q-nMT bundle formation in live cells would have been really informative to more precisely evaluate the MT dynamics. Likewise, together with still images (Fig 1D and Supp. Fig. 1D), movies depicting the changes in the localization of Nuf2-GFP would have further facilitated the analysis of this process.

In a new Sup Fig 1E, we now provide images of Q-nMT bundle formation initiation in phase I, in which it can be observed that Nuf2-GFP accompanies the growth of MT (mTQZ-TUB1) at the onset of Q-nMT bundle formation. Unfortunately, it is technically very challenging to follow the entire process of Q-nMT bundle formation in individual cells, as it takes > 48h. Indeed, for movies longer than 24h, on both microscope pads or specific microfluidic devices (Jacquel, et al, eLife 2021), phototoxicity and oxygen availability become problematic and affect cells’ viability.

(5) Western blot images displaying the relative protein levels for mTQZ-Tub1 and of the ADH2 promoter-driven mRuby-Tub1 at the different time points should be included to more strongly support the conclusion that new tubulin molecules are introduced in the Q-nMT bundle only after phase I. It is worth noting, in this sense, that the percentage of cells with 2 colors Q-nMT bundle is analyzed only 1 hour after expression of mRuby-Tub1 was induced for phase I cells, but after 24 hours for phase II cells.<br /> We have modified Fig 1F and now provide images of cells after 3, 6 and 24h after glucose exhaustion and the corresponding percentage of cells displaying Q-nMT bundle with the two colors. We also now provide a western blot in Sup Fig 1H using specific antibodies against mTQZ (anti-GFP) and mRuby (anti-RFP).

(6) In order to demonstrate that Q-nMT formation is an active process induced by a transient signal and that the Q-nMT bundle is required for cell survival, the authors treated cells with nocodazole for 24 h (Fig 1H and Supp Fig 1K). Both events, however, could be associated with the toxic effects of the extremely prolonged nocodazole treatment leading to cell death.

We have treated 5 days old cells for 24h with 30 µg/ml Noc. We then washed the drug and transferred the cells into a glucose free medium. We then followed both cell survival, using methylene blue, and the cell’s capacity to form a colony after refeeding. In these conditions, we did not observe any toxic effect of the nocodazole. This result is now provided in Sup Fig 1L and discussed line 172-176.

(7) The "Tub1-only" mutant displays shorter but stable Q-nMT bundles in phase II, although they are thinner than in wild-type cells. What happens in the "Tub3-only" mutant, which also has beta-tubulin levels similar to wild-type cells (Supp. Fig. 2B)?

In order to measure Q-nMT bundle length and thickness, we used Tub1 fused to GFP. This cannot be done in a Tub3-only mutant. Yet, we have measured Q-nMT bundle length in Tub3-only cells using Bim1-3GFP as a MT marker (as in Laporte et al, JCB 2013). As shown in the figure below, Q-nMT bundles were shorter in Tub3-only cells than in WT cells whatever the phase.

Author response image 8.

We do not know if this effect is directly linked to the absence of Tub1 or if it is very indirect and for example due to the fact that Tub1 and Tub3 interact differently with Bim1 or other proteins that are involved in Q-nMT bundle stabilization. As we cannot give a clear interpretation for that result, we decided not to present those data in our manuscript.

(8) Why were wild-type and ndc80-1 cells imaged after a 20 min nocodazole treatment to evaluate the role of KT-MT attachments in Q-nMT bundle formation (Fig 3A)? Importantly, this experiment is also missing a control in which Q-nMT length is analyzed in both wild-type and ndc80-1 cells at 25ºC instead of 37ºC.

In this experiment, we used nocodazole to test both the formation and the stability of the Q-nMT bundle. Fig 3A shows MT length distribution in WT (grey) and ndc80-1 (violet) cells expressing mTQZTub1 (green) and Nuf2-GFP (red), shifted to 37 °C at the onset of glucose exhaustion and kept at this non-permissive temperature for 12 or 96 h then treated with Noc. The control experiment was provided in Sup Fig 3B. Indeed, this figure shows MT length in WT (grey) and ndc80-1 (violet) expressing mTQZ-Tub1 (green) and Nuf2-GFP (red) grown for 4 d (96h) at 25 °C, and treated or not with Noc. This is now indicated in the text line 216 and in the figure legend line 976

Author response image 9.

(9) As a general comment linked to the previous concern, it is striking that in many instances, Q-nMT bundle length is measured after nocodazole treatment without any evident reason to do this and without displaying the results in untreated cells as a control. If nocodazole is used, the authors should explicitly indicate it and state the reason for it.

We provide control experiments without nocodazole for all of the figures. For the sake of figure clarity, for Fig.3A the control without the drug is in Sup. Fig. 3B, for Fig. 3B it is shown in Sup. Fig. 3D, for Fig. 4B, it is shown in Sup. Fig 4A. This is now stated in the text and in the figure legend: for Fig. 3A: line 216 and in the figure legend line 976; for Fig. 3B: line 222 and figure legend line 984; for Fig. 4B: line 280 and in the figure legend line 1017.

The only figures where the untreated cells are not shown is for Fig 1D since the goal of the experiment is to make dynamic MTs shorten.

In Fig. 5C and Sup. Fig. 5D to F, we used nocodazole to get rid of dynamic cytoplasmic MTs that form upon quiescence exit in order to facilitate Q-nMT bundle measurement. This was explained in our previous study (Laporte et al, JCB 2013). We now mention it in the figure legends, see for example Fig. 5 legend line 1054.

(10) Ipl1 inactivation using the ipl1-1 thermosensitive allele impedes Q-nMT bundle formation. The inhibitor-sensitive ipl1-as1 allele could have been further used to show whether this depends on its kinase activity, also avoiding the need to increase the temperature, which affects MT dynamics. As suggested, we have used the ipl1-5as allele. We have thus modified Fig 3B and now show that is it indeed the Ipl1 kinase activity that is required for Q-nMT bundle formation initiation (line 222). In any case, it is surprising that deletion of SLI15 does not affect Q-nMT formation (in fact, MT length is even larger), despite the fact that Sli15, which localizes and activates Ipl1, is present at the Q-nMT (Fig 3C). Likewise, deletion of BIR1 has barely any effect on MT length after 4 days in quiescence (Fig 3D). Do the previous observations mean that Ipl1 role is CPC-independent? Does the lack of Sli15 or Bir1 aggravate the defect in Q-nMT formation of ipl1-1 cells at non-permissive or semi-permissive temperature?

Thanks to the Reviewer’s comments, we have re-checked our sli15Δ strain and found that it was accumulating suppressors very rapidly. To circumvent this problem, we utilized the previously described sli15-3 strain (Kim et al, JCB 1999). We found that sli15-3 was synthetic lethal with both ipl1-1, ipl1-2 (as described in Kim et al, JCB 1999) and with ipl1-as5, preventing us from addressing the CPC dependence of the Ipl1 effect asked by the Reviewer. However, using the sli15-3 strain, we now show that inactivation of Sli15 upon glucose exhaustion does prevent Q-nMT bundle formation (See new Sup Fig 3F and the text line 226-227).

(11) Lack of both Bir1 and Bim1 act in a synergistic way with regard to the defect in Q-nMT bundle formation. Although the absence of both Sli15 and Bim1 is proposed to lead to a similar defect, this is not sustained by the data provided, particularly in the absence of nocodazole treatment (Supp. Fig 3E).

Deletion of bir1 alone has only a subtle effect on Q-nMT bundle length in the absence of Noc, yet in bir1Δ cells, Q-nMT bundles are sensitive to Noc. Deletion of BIM1 (bim1Δ) aggravates this phenotype (Fig. 3D). As mentioned above, Q-nMT bundle formation is impaired in sli15-3 cells. In our hands, and as expected from (Zimnaik et al, Cur Biol 2012), this allele is synthetic lethal with bim1Δ.

On the other hand, the simultaneous lack of Bir1 and Bim1 drastically reduces the viability of cells in quiescence and this is proposed to be evidence supporting that KT-MT attachments are critical for QnMT bundle assembly (Supp Fig 3G). However, similarly to what was indicated previously for the 24 h nocodazole treatment, here again, the lack of viability could be originated by other reasons that are associated with the lack of Bir1 and Bim1 and not necessarily with problems in Q-nMT formation. In fact, the viability defect of cells lacking Bir1 and Bim1 is similar to that of cells only lacking Bir1 (Supp Fig 3G).

We have previously shown that many mutants impaired for Q-nMT bundle formation (dyn1Δ, nip100Δ etc) have a reduced viability in quiescence (Laporte et al, JCB 2013). In the current study, a very strong phenotype is observed for other mutants impaired for Q-nMT bundle formation such as bim1Δ bir1Δ cells, but also for slk19Δ bim1Δ.

Importantly, as shown in the new Sup Fig 1L, in WT cells treated with Noc upon entry into quiescence, a treatment that prevents Q-nMT formation, showed a reduced viability, while a Noc treatment that does not affect Q-nMT bundle formation, i.e. a treatment in late quiescence, has no effect on cell survival. This solid set of data point to a clear correlation between the ability of cells to assemble a Q-nMT bundle and their ability to survive in quiescence. Yet, of course, we cannot formally exclude that in all these mutants, the reduction of cell viability in quiescence is due to another reason.

(12) Both Mam1 and Spo13 are, to my knowledge, meiosis-specific proteins. It is therefore surprising that mutants in these proteins have an effect on MT bundle formation (Fig 3G-H, Supp. Fig. 3G). Are Mam1 and Spo13 also expressed during quiescence? Transcription of MAM1 or SPO13 does not seem to be induced by glucose depletion in previously published microarray experiments, but if Mam1 are Spo13 are expressed in quiescent cells, the authors should show this together with their results.<br /> Indeed, it is interesting to notice that Mam1 and Spo13 are involved in both meiosis and Q-nMT bundle formation. As suggested by the Reviewer we have performed western blots in order to address the expression of those proteins in proliferation and quiescence (4d). We tagged Spo13 with either GFP, HA or Myc but none of the fusion proteins were functional. Yet, as shown in the new Sup Fig 3I, Mam1-GFP, Csm1-GFP and Lsr4-GFP were expressed both in proliferation and quiescence.

(13) In the laser ablation experiments that demonstrate that KT-MT attachments are not needed in order to maintain Q-nMT bundles once formed, anaphase spindles of proliferating cells were cut as a control (Supp. Fig 3I). However, late anaphase cells have already segregated the chromosomes, which lie next to the SPBs (this can be evidenced by looking at Dad2-GFP localization in Supp. Fig 3I), so that only interpolar MTs are severed in these experiments. The authors should have instead used metaphase cells as a control, since chromosomes are maintained at the spindle midzone and the length and width of the metaphase spindle is more similar to that of the Q-nMT bundle.

We have tried to “cut” short metaphase spindles, but as they are < 1 µm, after the laser pulse, it is difficult to verify that spindles are indeed cut and not solely “bleached”. Furthermore, after the cut, the remaining MT structure that is detectable is very short, and we are not confident in our length measurements. Yet, this type of experiment has been done in S. pombe (Khodjakov et al, Cur Biol 2004 and Zareiesfandabadi et al, Biophys. J. 2022). In these articles the authors have demonstrated that after a cut, metaphase spindles are unstable and rapidly shrink through the action of Kinesin14 and dynein. This is now mentioned in the text line 265.

(14) In the experiment that shows that cycloheximide prevents Q-nMT disassembly after quiescence exit, and therefore that this process requires de novo protein synthesis (Fig. 5A), cells are indicated to express only Spc42-RFP and Nuf2-GFP. However, Stu2-GFP images are also shown next to the graph and, according to the figure legend, it was indeed Stu2-GFP that was used to measure individual QnMT bundles in cells treated with cycloheximide. In the graph, additionally, time t=0 represents the onset of MT bundle depolymerization, but Q-nMT bundle disassembly does not take place after cycloheximide treatment. The authors should clarify these aspects of the experiment.

Following the Reviewer’s suggestion, to clarify these aspects we have split Fig. 5A into 2 panels.

Finally, some minor issues are:

(1) The text should be checked for proper spelling and grammar.

We have done our best.

(2) In some instances, there is no indication of how many cells were imaged and analyzed.

We now provide all these details either in the figure itself or in the figure legend.

(3) Besides the Q-nMT bundle, it is sometimes noticeable an additional strong cytoplasmic fluorescent signal in cells that express mTQZ-Tub1 and/or mRuby-Tub1 (e.g., Figs 1F, 1H and, particularly, Supp Fig 1H). What is the nature of these cytoplasmic MT structures?

We did mention this observation in the material and methods section (see line 526-528). This signal is a background fluorescence signal detected with our long pass GFP filter. It is not GFP as it is “yellowish” when we view it via the microscope oculars. This background signal can also be observed in quiescent WT cells that do not express any GFP. We do not know what molecule could be at the origin of that signal but it may be derivative of an adenylic metabolite that accumulates in quiescence and could be fluorescent in the 550nm –ish wavelength, but this is pure speculation.

(4) It is remarkable that a 20-30% decrease in tubulin levels had such a strong impact on the assembly of the Q-nMT bundle (Supp. Fig. 2). Can this phenotype be recovered by increasing the amount of tubulin in the mutants impaired for tubulin folding?

Yes, this is astonishing, but we believe our data are very solid since we observed that with both tub3Δ and in all the tubulin folding mutants we have tested (See Sup. Fig. 2). To answer Reviewer’s question, we would need to increase the amount of properly folded tubulin, in a tubulin folding mutant. One way to try to do that would be to find suppressors of GIM mutations, but this is a lengthy process that we feel would not add much strength to this conclusion.

(5) The graphs displaying the length of the Q-nMT bundle in several mutants in microtubule motors throughout a time course are presented in a different manner than in previous experiments, with data points for individual cells being only shown for the most extreme values (Fig 4C, 4H). It would be advisable, for the sake of comparison, to unify the way to represent the data.

We have now unified the way we present our figures.

(6) How was the exit from quiescence established in the experiments evaluating Q-nMT disassembly? How synchronous is quiescence exit in the whole population of cells once they are transferred to a rich medium?

We set the “zero” time upon cell refeeding with new medium. In fact, quiescence exit is NOT synchronous. We have reported this in previous publications, with the best description of this phenomena being in Laporte et al, MIC 2017 . <br /> The figures below are the same data but on the left graph, the kinetic is aligned upon SPB separation onset, while on the right graph (Fig 5A), it is aligned on MT shrinking onset.

Author response image 10.

We can add this piece of data in a Sup Figure if the Reviewer believes it is important.

Reviewer #2 (Recommendations For The Authors):

General:

• In general, more precise language that accurately describes the experiments would improve the text. <br /> We have tried to do our best to improve the text.

• The authors should clearly define what they mean by an active process and provide context to support this statement regarding the Q-nMT.

We have strived to clarify this point in the text (see paragraph form line 146 to 178).

• It is reasonable to assume that structures composed of microtubules are dynamic during the assembly process. The authors should clarify what they mean by "stable by default i.e., intrinsically stable." Do they mean that when Q-nMT assembly starts, it will proceed to completion regardless of a change in condition?

We mean that in phase I the Q-nMT bundle is stabilized as it grows and that stabilization is concomitant with polymerization. By contrast, MTs polymerized during phase II are not stabilized upon elongation beyond the phase I polymer, and get stabilized later, in a separate phase (i.e. in phase III). We hope to have clarified this point in the text (see line 108-110).

• In lines 33-34, the authors claim that the Q-nMT bundle functions as a "sort of checkpoint for cell cycle resumption." This wording is imprecise, and more significantly the authors do not provide evidence supporting a direct role for Q-nMT in a quiescence checkpoint that inhibits re-entry into the cell cycle.

We have softened and clarified the text in the abstract (see line 29-30)., in the introduction (line 101104), in the result section (line 331-332) and in the discussion (line 426-430).

• Many statements are qualitative and subjective. Quantitative statements supported by the results should be used where possible, and if not possible restated or removed.

We provide statistical data analysis for all the figures.

• The number of hours after glucose exhaustion used for each phase varies between assays. This is likely a logistical issue but should be explained.

This is indeed a logistical issue and when pertinent, it is explained in the text.

• It would be interesting to address how this process occurs in diploids. Do they form a Q-nMT? How does this relate to the decision to enter meiosis?

Diploid cells enter meiosis when they are starved for nitrogen. Upon glucose exhaustion diploids do form a Q-nMT bundle. This is shown and measured in the new Sup Fig1C. In fact, in diploids, Q-nMT bundles are thicker than in haploid cells.

• It would be interesting to address how the timescale of this process compares to the types of nutrient stress yeast would be exposed to in the environment.

We have transferred proliferating yeast cells to water, to try to mimic what could happen when yeast cells face rain in the wild. As shown below, they do form a Q-nMT bundle that becomes nocodazole resistant after 30h. This data is now provided in the new Sup Fig 1D.

• It is recommended that the authors use FRAP experiments to directly measure the stability of the QnMT bundles.

This experiment was published in (Laporte et al, 2013). Please see response to Reviewer #1.

• In many cases, the description of the experimental methods lacks sufficient detail to evaluate the approach or for independent verification of results.

We have strived to provide a more detailed material and methods section, as well as more detailed figure legends and statistical informations.

Specific comments on figures:

• In Figure 1 c), what do the polygons represent? They do not contain all the points of the associated colour.

The polygon represented the area of distribution of 90% of the data points. As they did not significantly add to the data presentation they have been removed.

• In Figure 2 a), is the use of two different sets of markers to control for the effect of the markers on microtubule dynamics?

Yes, we are always concerned about the influence of GFP on our results, so very often we replicate our experiments with different fluorescent proteins or even with different proteins tagged with GFP. This is now mentioned in the text (line 184-186).

• Is it accurate to say (line 201, figure 3 a)) that no Q-nMT bundles were detected in ndc80-1 cells shifted to 37 degrees, or are they just shorter?

As shown in Fig 3A, in ndc80-1 cells, most of the MT structures that we measured are below 0,5um. This has been re-phrased in the text (line 214-215).

• Lines 265-269, figure 4 b), how can the phenotype observed in cin8∆ cells be explained given the low abundance of Cin8 that is detected in quiescent cells?

Faint fluorescence signal is not synonymous of an absence of function. As shown in Sup Fig 4B, we do detect Cin8-GFP in quiescent cells.

• Quantification is needed in Figure 4 panels c) and h).

Fig 4C and 4H have been changed and quantification are provided in the figure legend.

Reviewer #3 (Recommendations For The Authors):

A few points should be addressed for clarity:

(1) Sup. Fig. 1K: are only viable cells used for the colony-forming assay? How were these selected? If not, the assay would just measure survival (as in the viability assay).

Yes, only viable cells were selected for the colony forming assay. We used methylene blue to stain dead cells. Then, we used a micromanipulation instrument (Singer Spore Play) that is commonly used for tetrad dissection to select “non blue cells” and position them on a plate (as we do with spores). Each micromanipulated cell is then allowed to grow on the plate and we count colonies (see picture in Sup Fig 1L right panel). This was described in Laporte et al, JCB 2011. We have added that piece of information in the legend (line 1129-1130) and in the M&M section (line 580-586).

(2) Could Tub3 have a role in phase I? It is not clear why the authors conclude involvement only in phase II.

As it can be seen in Fig 2D, MT bundle length and thickness are quite similar in WT and Tub1-only cells in phase I, indicating that the absence of Tub3 as no effect in phase I. In Tub1-only cells, MT bundles are thinner in both phase II and phase III, yet, they get fully stabilized in phase III. Thus, the effect of Tub3 is largely specific to the nucleation/elongation of phase II MTs. We hope to have clarified that point in the text (line 203-207).

(3) Quantifications, statistics: for all quantifications, the authors should clearly state the number of experiments (replicates), and number of cells used in each, and what number was used for statistics. For all quantifications in cells, it seems that the values from the total number of cells across different experiments were plotted and used for statistics. This is not very useful and results in extremely small p values. I assume that the values for individual cells were obtained from multiple, independent experiments. Unless there are technical limitations that allow only a very small sample size (not the case here for most experiments), for experiments involving treatments the authors should determine values for each experiment and show statistics for comparison between experiments rather than individual cells pooled from multiple experiments.

All the experiments have been done at least in replicate. In the new Fig. 1A, we now display each independent experiment with a specific color code. For Fig 2B and 2C we now provide the data obtained for each separate experiment in Sup Fig 2C. Additional details about quantifications and statistics are provided in the M&M section or in the specific figure legends.

eLife assessment

This work presents important insights regarding the mechanism underlying the assembly, maintenance, and disassembly of a very stable microtubule-based structure, termed quiescent-cell nuclear microtubule (Q-nMT) bundle, which is formed in quiescent yeast cells to ensure cell survival and viability. This insight will help to elucidate how very stable microtubules can exist alongside very dynamic microtubules, which is still poorly understood. While the experimental support is overall solid, additional analyses using state-of-the-art methodology would further strengthen some of the claims.

Reviewer #1 (Public Review):

In their manuscript, Laporte et al. analyze the process of formation of the quiescent-cell nuclear microtubule (Q-nMT) bundle, a set of parallel MTs that emanate from the nuclear side of the spindle pole bodies (SPBs) upon the entry of Saccharomyces cerevisiae cells in quiescence. Based on their results, the authors propose that Q-nMT bundle formation is a multistep process that comprises three distinct sequential phases. The authors further evaluate the role of different factors during the growth of the Q-nMT bundle upon quiescence entry, as well as during the disassembly of this structure once the cells resume their proliferation.

The Q-nMT is an interesting cellular structure whose physiological function is still widely unknown. Hence, providing new insights into the dynamics of Q-nMT bundle formation and identifying new factors involved in this process is an interesting topic of relevance in the field. The authors made a substantial effort in order to evaluate Q-nMT bundle establishment and provide a considerable amount of data, mainly obtained from microscopy analyses. Overall, the experiments are mostly well described and properly executed, and the data in the manuscript are clearly presented. Despite the interest of the study, nonetheless, there are several issues that could affect the validity of some conclusions drawn. In this way, regarding the analysis of the dynamics of Q-nMT bundle formation, the described experimental setup raises certain concerns, which mostly derive from the use of the microtubule-depolymerizing agent nocodazole as the only approach to evaluate this process. Also, regarding the factors involved in Q-nMT formation, the differences in microtubule length with the wild type strain, despite being statistically significant, are really subtle for many of the mutants analyzed (e.g., bir1, slk19, etc.). Furthermore, it is also puzzling that an effect on Q-nMT formation is proposed for meiosis-specific factors such as Mam1, which might as well be present during quiescence, but seems to be also detected in proliferating cells. Lastly, the evidence shown are insufficient to provide a direct link between defects in cell viability and aberrant Q-nMT formation.

Reviewer #2 (Public Review):

Summary: The authors investigate the assembly of the Q-nMT, a stable microtubule structure that is assembled during quiescence. Notably, the authors show that the formation of the Q-nMT cannot be solely explained by changes in the physico-chemical properties of quiescent cells. The authors report that Q-nMT assembly occurs in three regulated steps and identify kinesin motor proteins involved in the assembly and disassembly of the structure.

Strengths: The findings provide new insight into the assembly and possible function of the Q-nMT with respect to the response of haploid budding yeast to glucose starvation.

Weaknesses: The manuscript would benefit from more precise language and requires additional clarification regarding how claims are supported by the evidence. Clear definitions are also required, for example "active process" is not defined. Some conclusions are not supported by the results, for example the claim that the Q-nMT functions as a checkpoint effector that inhibits re-entry into the cell cycle.

After reviewing the responses of the authors and the revised manuscript I am now satisfied with the study in its current form.

Author Response

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

Reviewer #1 (Public Review):

We thank reviewer #1 for identifying the major caveats of the paper, and have split them out into separate comments below to address them.

Comment 1) The caveats are that ecosystem processes beyond water availability are not investigated although they are brought into play in the title and in the paper

Author response: We disagree that water availability is the only ecosystem process investigated in this study, as herbivory, plant mortality, and the maintenance of diversity in higher trophic levels are important processes within ecosystems. We have added text to the abstract and introduction clarifying that we consider these response measures to be ecosystem processes. Further language to this effect already exists in the abstract, methods, and discussion.

Comment 2) That herbivory beyond leaf damage was not reported (there might be none, the reader needs to be shown the evidence for this)

Author response: This is typically how herbivory is assessed in ecological studies, and our focus is on folivores. There may be additional herbivory in the form of fluid-sucking insects, shoot/root herbivory, etc., but these were not assessed. It would be interesting to assess these other forms of herbivory to see if they respond similarly with additional studies.

Comment 3) That herbivore diversity is defined by leaf damage (authors need to give evidence that this is a valid inference)

Author response: We thank reviewer #1 for pointing out the lack of written support for this claim. We have modified the methods (lines 138-139; 214-217) to clarify that this is a useful proxy for insect richness in the Piper system, and have added citations demonstrating it has been found to correlate well with insect richness in tropical forests.

Comment 4) That the plots were isolated from herbivores beyond their borders

Author response: This was not an assumption of the study. We have modified the methods (line 200) to make this clearer to the reader.

Comment 5) That the effects of extreme climate events were isolated to Peru

Author response: This was not an assumption of the study, rather it is an observation. While we consider it important to include observed climate differences between sites in the interpretation of our results, it was not necessary for there to be extreme climate events at other sites as we consider manipulated water availability to represent changes in precipitation that are expected to occur at these sites with climate change.

Comment 6) That intraspecific variation in the host plants needs to be explained and interpreted in more detail

Author response: We thank reviewer #1 for identifying that our current explanations needed development. We have modified the introduction to explore potential mechanisms relating intraspecific diversity to ecosystem function based on recent studies, and have modified the discussion to bring focus to why the effects of intraspecific differ from interspecific.

Reviewer #1 (Recommendations For The Authors):

Comment 1) Pare this material down to simpler results. The most significant to me is the intraspecific variation in damage. Were this broken out and reported in some detail it could be quite interesting. I find the results to be a confusing blizzard of multiple factors that differ among sites; after reading the paper twice I could not recall the takeaway lesson beyond that drought wrecks the diversity of herbivores and sometimes even kills the host plant.

Author response: We agree that the results are complicated given the variation in effects among sites, but this variation and complexity is important – and is in itself is one of the takeaway points. Unfortunately, nature is not simple. We have made several large edits to the results section, including the removal of methodological and otherwise redundant information, to hopefully bring the major takeaways into focus.

Reviewer #2 (Public Review):

Comment 1) This is an important and large experimental study examining the effects of plant species richness, plant genotypic richness, and soil water availability on herbivory patterns on Piper species in tropical forests.

A major strength is the size of the study and the fact that it tackled so many potentially important factors simultaneously. The authors examined both interspecific plant diversity and intraspecific plant diversity. They crossed that with a water availability treatment. And they repeated the experiment across five geographically separated sites.

The authors find that both water availability and plant diversity, intraspecific and interspecific, influence herbivore diversity and herbivory, but that the effects differ in important ways across sites. I found the study to be solid and the results to be very convincing. The results will help the field grapple with the importance of environmental change and biodiversity loss and how they structure communities and alter species interactions.

Author response: We thank reviewer #2 for their kind words.

Reviewer #2 (Recommendations For The Authors):

Comment 1) I was confused about why the authors measured species diversity/richness as a proportion of the species pool. This means that the metric of richness decreases if species are added to the species pool but not the plot/experiment. I think I understand it, but I suggest the authors explain this choice.

Author response: We thank reviewer #2 for pointing out that this was confusing. We have clarified the methods (lines 228-232) to explain that this choice was made to allow easier comparison between intra- and interspecific richness.

Comment 2) One of the stronger estimated relationships was a positive effect of plant species richness on insect richness. I found it a little hard to interpret this relationship. Is this just because there are host species specialists? So, with more host species there are more herbivore species? Or does insect richness increase multiplicatively with increasing plant species richness? One way to look for this would be for the authors to examine the relationship between plant species richness and the average number of herbivore damage types per plant species.

Author response: We agree that this is important for the reader to understand and have added text to the introduction and discussion sections explaining that this is the expectation based on theory and other empirical studies. We have additionally added text to the discussion (lines 386-388) pointing out that this pattern was not observed at all sites. While we agree that it would be interesting to explore if this effect was additive or multiplicative, we do not believe this is in the scope of the paper due to the methods used to measure insect richness.

Comment 3) Unless I missed it, some important information about the models was missing. E.g., what distributions were assumed for each of the variables? Any transformations?

Author response: We thank reviewer #2 for pointing this out, this information has been added to the methods (lines 272-274)

Comment 4) Why is there no model with water addition affecting insect richness directly but not percent herbivory directly?

Author response: While we originally decided to not include this model due to lack of theoretical support and low statistical performance, we have added references to this model (now model II) in the methods and results for consistency and to make model performance clearer to the reader. We have additionally moved supplemental table S1 to the main text to make the models and hypotheses tested by each model more accessible.

Comment 5) Fig. 2. What are the percentages above the figures? Maybe PD values?

Author response: These values are now clarified in the figure caption

Comment 6) L364 "can differ dramatically" This is vague and confusing. Differ in what way? From each other? Did the authors really expect plant richness to have the same effect on herbivory and plant survival? What would it mean anyway for plant richness to have the same effect on herbivory and plant survival?

Author response: We agree that the language here is confusing and thank reviewer #1 for drawing our attention to it. We have modified the discussion (lines 363-365) to clarify that the direction of effect of intraspecific richness can vary from the direction of effect of interspecific richness, rather than the effects on different response variables varying from each other.

Comment 7) L 375 "only meaningful differences" This statement feels a little overly strong. It seems like there is a good argument for this, but there could be other things going on.

Author response: We agree that the language here was unnecessarily strong, and have modified the discussion (lines 398-403) to focus on the lack of difference between methodologies at these two sites, and the observed differences in climate and community structure at each site.

eLife assessment

This important, large experimental study examines the effects of plant species richness, plant genotypic richness, and soil water availability on herbivory patterns for Piper species in several tropical sites. The authors find solid evidence that water availability, as well as intra- and interspecific plant diversity, influence herbivory and herbivore diversity, but that the effects differ geographically.

Reviewer #1 (Public Review):

This study reports a long-term, multisite study of tropical herbivory on Piper plants. The results are clear that lack of water leads to lower plant survival and altered herbivory. The results varied substantially among sites. The caveats are that ecosystem processes beyond water availability are not investigated although they are brought into play in the title and in the paper, that herbivory beyond leaf damage was not reported (there might be none, reader needs to be shown the evidence for this), that herbivore diversity is defined by leaf damage (authors need to give evidence that this is a valid inference), that the plots were isolated from herbivores beyond their borders, that the effects of extreme climate events were isolated to Peru, that intraspecific variation in the host plants needs to be explained and interpreted in more detail, the results as reported are extremely complicated, the discussion is overly long and diffuse.

Reviewer #2 (Public Review):

This is an important and large experimental study examining the effects of plant species richness, plant genotypic richness, and soil water availability on herbivory patterns on Piper species in tropical forests.

A major strength is the size of the study and the fact that it tackled so many potentially important factors simultaneously. The authors examined both interspecific plant diversity and intraspecific plant diversity. They crossed that with a water availability treatment. And they repeated the experiment across five geographically separated sites.

The authors find that both water availability and plant diversity, intraspecific and interspecific, influence herbivore diversity and herbivory, but that the effects differ in important ways across sites. I found the study to be solid and the results to be very convincing. The results will help the field grapple with the importance of environmental change and biodiversity loss and how they structure communities and alter species interactions.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

In this study, the authors aimed to investigate how cells respond to dynamic combinations of two stresses compared to dynamic inputs of a single stress. They applied the two stresses - carbon stress and hyperosmotic stress - either in or out of phase, adding and removing glucose and sorbitol.

Both a strength and a weakness, as well as the main discovery, is that the cells' hyperosmotic response strongly requires glucose. For in-phase stress, cells are exposed to hyperosmotic shock without glucose, limiting their ability to respond with the well-studied HOG pathway; for anti-phase stress, cells do have glucose when hyperosmotically shocked, but experience a hypo-osmotic shock when both glucose and sorbitol are simultaneously removed. Responding with the HOG pathway and so amassing intracellular glycerol amplifies the impact of this hypo-osmotic shock. Counterintuitively then, it is the presence of glucose rather than the stress of its absence that is deleterious for the cells.

The bulk of the paper supports these conclusions with clean, compelling time-lapse microscopy, including extensive analysis of gene deletions in the HOG network and measurements of both division and death rates. The methodology the authors develop is powerful and widely applicable.

Some discussion of the value of applying periodic inputs would be helpful. Cells are unlikely to have previously seen such inputs, and periodic stimuli may reveal behaviours that are rarely relevant to selection.

We thank the referee for his review. To answer the reviewer’s last comment, our main objective was not to study conditions that are ecologically relevant, but rather to perturb the system in an original way to reveal new mechanisms and properties of the system. The main advantage of periodic inputs over more complex or unpredictible types of temporal fluctuations is that they can be defined with few parameters that are easy to interpret and to integrate in biophysical models. For instance, by using periodic inputs we were able to investigate how changing the phasing of two stresses impacted fitness while keeping other parameters constant (the duration of each stress was kept constant). We added two sentences at the beginning of the discussion to highlight the value of using periodic inputs.

We do not fully agree with the reviewer’s statement that periodic stimuli may reveal behaviours that are rarely relevant to selection. Indeed, many parameters of natural environments are known to vary periodically, such as light, temperature, predation, tides. Even if the periodic stimuli we use are artificial, they can still be a valuable tool to reveal new molecular processes. For instance, null mutants have been invaluable to understand biological systems despite being unlikely to reveal behaviours relevant to selection.

The authors' findings demonstrate the tight links that can exist between metabolism and the ability to respond to stress. Their study appears to have parted somewhat from their original aim because of the HOG pathway's reliance on glucose. It would be interesting to see if the cells behaviour is simpler in periodically varying sorbitol and a stress where there is little known connection to the HOG network, such as nitrogen stress.

The use of periodic nitrogen stress is a very interesting suggestion from both reviewers. However, we think it represents a large amount of work that deserves its own study. In particular, it would require first identifying a relevant period at which nitrogen fluctuations have an impact on division rate similar to what we observed for glucose fluctuations before performing experiments in AS and IPS conditions.

Nitrogen starvation is known to induce filamentous growth via activation of components of the HOG pathway (Cullen and Sprague, 2012), with potential cross-talk between filamentous growth and hyperosmotic stress response. Therefore, periodic osmotic stress and periodic nitrogen starvation may interact in a complex way.

Reviewer #2 (Public Review):

The authors have used microfluidic channels to study the response of budding yeast to variable environments. Namely, they tested the ability of the cells to divide when the medium was repeatedly switched between two different conditions at various frequencies. They first characterized the response to changes in glucose availability or in the presence of hyper-osmotic stress via the addition of sorbitol to the medium. Subsequently, the two stresses were combined by applying the alternatively or simultaneously (in-phase). Interestingly, the observed that the in-phase stress pattern allowed more divisions and low levels of cell mortality compared to the alternating stresses where cells were dividing slowly and many cells died. A number mutants in the HOG pathway were tested in these conditions to evaluate their responses. Moreover, the activation of the MAPK Hog1 and the transcriptional induction of the hyper-osmotic stress promoter STL1 were quantified by fluorescence microscopy.

Overall, the manuscript is well structured and data are presented in a clear way. The time-lapse experiments were analyzed with high precision. The experiments confirm the importance of performing dynamic analysis of signal transduction pathways. While the experiments reveal some unexpected behavior, I find that the biological insights gained on this system remain relatively modest.

In the discussion section, the authors mention two important behaviors that their data unveil: resource allocation (between glycolysis and HOG-driven adaptation) and regulation of the HOG-pathway based on the presence of glucose. These behaviors had been already observed in other reports (Sharifan et al. 2015 or Shen et al. 2023, for instance). I find that this manuscript does not provide a lot of additional insights into these processes.

We thank the referee for his review. We agree with the reviewer that the interaction between glucose availability and osmotic stress response has been investigated in previous studies. However, this interaction was investigated using experimental procedures that differed from our approach in critical ways, and therefore the behaviors observed were not the same. In Sharifian et al. (2015), the authors identified a new negative feedback loop regulating Hog1 basal activity and described underlying molecular mechanisms. This feedback loop is unlikely to explain differences of cell fitness we observed in IPS and AS conditions, because 1) differences of division rate was still observed in hog1 mutant cells and 2) differences of death rate involve glycerol synthesis, which is independent of the feedback loop described in Sharifian et al. (2015). In Shen et al. (2023), the authors observed a stronger expression of Hog-responsive genes at lower glucose concentrations, which seems contradictory with our observation of very low pSTL1-GFP expression in absence of glucose. However, they did not use fluctuating conditions and they did not report expression of stress-response genes when glucose was totally depleted (the lower glucose concentration they used was 0.02%) as we did, which may explain the different outcomes. We added three sentences in the discussion to compare our findings to those of Shen et al. (2023).

One clear evidence that is presented, however, is the link between glycerol accumulation during the sorbitol treatment and the cell death phenotype upon starvation in alternating stress condition. However, no explanations or hypothesis are formulated to explain the mechanism of resource allocation between glycolysis and HOG response that could explain the poor growth in alternating stresses or the lack of adaptation of Hog1 activity in absence of glucose.

In the revised version of the manuscript, we included a new result section and a supplementary figure (Figure 4 – figure supplement 2) where we tested three hypotheses to explain the lower division rate observed in AS condition relative to IPS condition. We found no evidence supporting these hypotheses, and the mechanisms responsible for the reduced growth in AS condition therefore remains elusive.

Another key question is to what extent the findings presented here can be extended to other types of perturbations. Would the use of alternative C-source or nitrogen starvation change the observed behaviors in dynamic stresses? If other types of stresses are used, can we expect a similar growth pattern between alternating versus in-phase stresses?

As mentioned above in our response to the other reviewer, these are very interesting questions that we think go beyond the scope of our study due to the amount of work involved.

Recommendations for the authors:

Reviewer #1

My comments are only minor.<br /> - More paragraphs would improve legibility.

To improve legibility, we split the longer section of the Results in three paragraphs (page 12, section entitled “Osmoregulation is impaired under in-phase stresses but not under alternating stresses.” However, we kept it as one section with a single title for global coherency: each section of the results corresponds to one main figure and have one main conclusion.

• I found AS and IPS confusing because what becomes important is whether sorbitol appears with glucose or not. For me, an acronym that makes that co-occurrence clear would be better or even better still no acronyms at all.

We tried several alternative names for the two conditions in previous drafts of the manuscript. Based on colleagues feedback, AS and IPS acronyms appeared as a good compromise between concision and clarity. To avoid confusion, the two acronyms are precisely defined when they are first used in the Results section. We think it is more important to emphasize the co-occurrence (or not) of the two stresses, rather than the co-occurrence of glucose and sorbitol. Indeed, standard yeast medium contains glucose but no sorbitol, and therefore we defined the two periodic conditions based on differences from standard medium. Even though we avoided using acronyms as much as possible in the manuscript, the use of these two acronyms to refer to the dual fluctuations of the environment seemed essential for concision. Indeed, IPS and AS acronyms are used many times in the results (16 occurrences on page 12 alone), figures and figure legends.

• I would consider moving some of Fig S2 to the main text: it helps clarify where Fig 2 is coming from and is referenced multiple times.

We fully agree with the reviewer and we moved panels A-D from Figure S2 to the main Figure 2.

• On page 10, "constantly facing a single stress that changes over time" is confusing. Perhaps "repetitively facing a single stress" instead?

We agree this sentence could be wrongly interpreted the way it was written. We changed it to: “cells grow more slowly when facing periodic alternation of the two stresses (AS) than when facing periodic co-occurrence of these stresses (IPS)”.

• Is there any knowledge on how cells resist hyperosmotic stress in the absence of glucose? That would help explain the IPS results.

Based on comments from both reviewers, we surveyed the literature to flesh out the discussion of hypotheses that would help explain observed differences between AS and IPS conditions. We found few studies that investigated cell responses in the absence of glucose, and because of significant differences in the experimental approaches it remains difficult to explain our results from conclusions of these previous studies. For instance, Shen et al., 2023 described and modeled the hyperosmotic stress response at various glucose concentrations. They found that Hog1p relocation to the nucleus after hyperosmotic shock lasted longer at lower glucose concentration, which is consistent with our finding in absence of glucose. However, they did not include the absence of glucose in their experiments or periodic fluctuations of glucose concentration. In addition, their model ignores the impact of cell signaling processes involved in growth arrest in response to hyperosmotic stress or glucose depletion. It is therefore difficult to relate their conclusions to our results. We have developed the discussion of our study to include these hypotheses and to clarify what is explained or not in our IPS and AS results.

There is knowledge on activation of the hyperosmotic stress pathway in response to glucose fluctuations, but not about the response to hyperosmotic stress in absence of glucose.

• On page 11, Figure 5a should be Figure 4a.

Correct.

• I would explain the components of the HOG pathway in the caption of Fig 1 or in the text when you cite Fig 1a. They are described later, but an early overview would be useful.

To give more context, we added the following sentences to the caption of Figure 1: “Yeast cells maintain osmotic equilibrium by regulating the intracellular concentration of glycerol. Glycerol synthesis is regulated by the activity of the HOG MAP kinase cascade that acts both in the cytoplasm (fast response) and on the transcription of target genes in the nucleus (long-term response). For simplicity, we only represented on the figure genes and proteins involved in this study.”

• On page 16, I wasn't sure what "redirect metabolic fluxes against glycerol synthesis" meant.

For more clarity, we modified this sentence to: “Since glucose is a metabolic precursor of glycerol, the absence of glucose may prevent glycerol synthesis and thereby fast osmoregulation."

• For Fig 2, having a dot-dash and dash-dash lines rather than both dash-dash would be better.

We made the proposed change, assuming the reviewer was referring to the gray dashed lines and not the colored ones.

• In the caption of Fig 3, 2% glucose is 20 g/L.

We thank the reviewer for catching this typo.

• In the Materials and Methods Summary, adding how you estimated death rates would be helpful: they are not often reported.

The calculation of death rates was explained in the Methods section. For more clarity, we modified the names of the parameters in the equation to make more explicit which ones refer to cell death.

Reviewer #2 (Recommendations For The Authors):

In Figure 2, it would be interesting to show individual growth rates of the perturbations at various frequencies as shown in Figures 3 c and d.

We thank the reviewer for this suggestion. We added a new supplementary figure (Figure 2 – figure supplement 2) showing the temporal dynamics of division rates at three different frequencies of osmostress and glucose depletion. We did not include high frequencies (periods below 48 minutes) because the temporal resolution of image acquisition in our experiments (1 image every 6 minutes) was too low. Very interestingly, this new analysis suggests that the positive relationship between the frequency of glucose depletion and division rate is explained by a delay between glucose removal and growth arrest rather than a delay between glucose addition and growth recovery. We therefore added the following conclusion:

“Under periodic fluctuations of 2% glucose, the division rate was lower during half-periods without glucose than during half-periods with glucose (Figure 2 – figure supplement 2d-f), as expected. However, this difference depended on the frequency of glucose fluctuations: the average division rate during half-periods without glucose was higher at high frequency (small period) than at low frequency (large period) of fluctuations (Figure 2 – figure supplement 2d-f). Therefore, the effect of the frequency of glucose availability on the division rate in 2% glucose is likely due to a delay between glucose removal and growth arrest: cell proliferation never stops when the frequency of glucose depletion is too fast.”

According to Sharifan et al. 2015, I would have expected that Hog1 would not relocate in the nucleus in 0% glucose. I wonder if this is due to the use of sorbitol as a stressor or the presence of low levels of glucose in the medium. I would suggest performing some control experiments with NaCl as hyperosmotic agent and test the addition of 2-deoxy-glucose to completely block glycolysis.

After careful reading of Sharifian et al. 2015, we fail to understand why the reviewer think Hog1 would be expected to not relocate to the nucleus after hyperosmotic stress in 0% glucose. In this previous study, the authors never combined glucose depletion with a strong hyperosmotic stress as we did in our study. They report the results of independent experiments where cells were exposed either to a single pulse of hyperosmotic stress (0.4 M NaCl) or to transient glucose starvation, but they did not combine these two stimuli. In this context, it is difficult to compare their results with ours. The fact that Sharifian et al. 2015 did not observe Hog1 nuclear relocation in 0% glucose (consistent with our result in Figure 6 – figure supplement 1a, yellow curve) is not inconsistent with our observation of Hog1 nuclear enrichment in 0% glucose + 1M sorbitol. One potential discrepancy between the two studies is the fact that they observed a small transient peak of Hog1 nuclear localization just after glucose is added back to the medium, while we failed to observe this peak in similar conditions (yellow curve in Figure 6 – figure supplement 1a). However, this could be simply explained by the temporal resolution of our experimental system: we image cells once every 6 minutes and the peak lasts less than 2 minutes in Sharifian et al. 2015. We added a sentence to discuss this minor point in the Results: “Although previous studies observed small transient (less than two minutes) peaks of Hog1-GFP nuclear localization after glucose was added back to the medium following glucose depletion (Sharifian et al., 2015, Piao et al., 2013), the temporal resolution in our experiments (one image every 6 minutes) may have been too low to detect these peaks.”.

While we agree many additional experiments would be interesting, such as testing the effects of different stress factors or the non-metabolizable glucose analog 2-deoxy-D-glucose, we think this is beyond the scope of this study because such experiments are likely to open broad perspectives and to not be conclusive in a reasonable amount of time.

When discussing Figure 7, the authors write that the HOG pathway is "overactivated" or "hyperactivated". I would refrain from using these terms because as seen in Figure 6, the Hog1 activity pattern, if anything, decreases as the number of alternative pulses increases. The high level of pSTL1mCitrine measured is mostly due to the long half-life of the fluorescent protein.

We used the formulation “hyper-activation” of the HOG pathway because Mitchell et al. 2015 used it to refer to the same phenomenon in their seminal study. This "hyper-activation" refers to the fact that both the integral activation of Hog1p (sum of areas under Hog1 nuclear peaks) and the global activation of transcriptional targets is much higher during fast periodic hyperosmotic stress than during constant hyperosmotic stress. That being said, we understand the point made by the reviewer about the decreasing size of Hog1 peaks over time during repeated pulses of osmotic stress. Therefore, we slightly modified the text to refer to hyper-activation of pSTL1-mCitrine transcription or expression instead of hyper-activation of the HOG pathway. For coherency, we replaced all instances of “overactivation” by “hyper-activation”.

Last but not least, the high level of pSTL1-mCitrine is both due to the long half-life of the protein and to the fact that pSTL1 transcription is never turned off due to high Hog1p activity under fast periodic osmostress.

Minor comments:

In the main text, I think it might be more intuitive to refer to doubling time in hours instead of division rates in 1/min which are harder to interpret.

In an early draft of the manuscript, we made figures with either division rates or with doubling times (ln(2)/division rate) and we received mixed opinions from colleagues on what measure was more intuitive to interpret. Both measures are widely used in the literature, and we decided to use division rates in the final version of the figures because it was more directly related to population growth rate and to fitness. For instance, the population growth rate shown in Figure 5 is simply calculated by subtracting the death rate from the division rate. For coherency, we therefore reported division rates instead of doubling times in figures and results. However, to address the reviewer’s comment we included the doubling times (in addition to the division rates) when mentioning the most important results. For instance, page 12: “Strikingly, cells divided about twice as fast under IPS condition (1.67 x 10-3 division/min, corresponding to an average doubling time of 415 minutes) than under AS condition (9.4 x 10-4 division/min, corresponding to an average doubling time of 737 minutes)”.

I found various capitalized version of "HOG /Hog pathway"

We corrected this incoherency and used “HOG pathway” everywhere.

Page 11. Figure 5a should refer to Figure 4a I believe.

Correct.

The methods are generally very thorough and precise. The explanation about the calculation of the division rate seems incomplete. For completeness, it would be good to mention the brand and model of valves used. In addition, it would be interesting to have an idea of the number of cells and microcolonies tracked in the various growth experiments.

We are not sure why the reviewer found the explanation of the calculation of division rate incomplete. For more clarity, we modified the names of parameters in the equations to make them more explicit. We also added a reference to Supplementary File 1 that contains all R scripts used to calculate division rates and death rates. We included the brand and model of valves used, as requested. As for the number of cells tracked in the various experiments, we mentioned in the Methods: “we selected 25 positions (25 fields of view) of the motorized stage (Prior Scientific ProScan III) that captured 10 to 50 cells in each of the 25 growth chambers of the chip and were focused slightly below the median cell plane based on cell wall contrast.” To address the reviewer’s comment, we also included the range of number of tracked cells for each experiment in corresponding figure legends.

Reviewer #2 (Public Review):

The authors have used microfluidic channels to study the response of budding yeast to variable environments. Namely, they tested the ability of the cells to divide when the medium was repeatedly switched between two different conditions at various frequencies. They first characterized the response to changes in glucose availability or in the presence of hyper-osmotic stress via the addition of sorbitol to the medium. Subsequently, the two stresses were combined by applying the alternatively or simultaneously (in-phase). Interestingly, they observed that the in-phase stress pattern allowed more divisions and low levels of cell mortality compared to the alternating stresses where cells were dividing slowly and many cells died. A number of mutants in the HOG pathway were tested in these conditions to evaluate their responses. Moreover, the activation of the MAPK Hog1 and the transcriptional induction of the hyper-osmotic stress promoter STL1 were quantified by fluorescence microscopy.

Overall, the manuscript is well structured and data are presented in a clear way. The time-lapse experiments were analyzed with high precision. The experiments confirm the importance of performing dynamic analysis of signal transduction pathways. While the experiments reveal some unexpected behavior, I find that the biological insights gained on this system remain relatively modest.

In the discussion section, the authors mention two important behaviors that their data unveil: resource allocation (between glycolysis and HOG-driven adaptation) and regulation of the HOG-pathway based on the presence of glucose. These types of behaviors had been already observed in other reports (Sharifan et al. 2015 or Shen et al. 2023, for instance). The experimental set-up used in this study provides highlights new aspects of the interplay between hyper-osmotic stress response and glucose availability.

The authors have tested various processes that could explain the slow growth observed in the alternating stress regime. Unfortunately, neither glycogen accumulation, cell-cycle arrest via Sic1 or the inhibition of protein production in starved cells could explain the observed behavior. However, one clear evidence that is presented is the link between glycerol accumulation during the sorbitol treatment and the cell death phenotype upon starvation in alternating stress condition.

One question which remains open is to what extent the findings presented here can be extended to other types of perturbations which for instance would combine Nitrogen limitation and hyper-osmotic stress.

eLife assessment

This study presents important findings on how cells sense and respond to their surroundings, in particular when two environmental signals are presented periodically, in alternation or conjunction. The compelling analyses reveal some unexpected behaviors that could not have been drawn, from simpler experimental designs, related to the dynamic interplay between the starvation and hyper-osmotic stress responses in budding yeast, exemplifying that applying complex signals can unveil new biological insights, even for well-studied systems. The work will be of broad interest to researchers interested in fungal biology, dynamic systems, cell signaling, and cell biology.

Reviewer #1 (Public Review):

In this study, the authors aimed to investigate how cells respond to dynamic combinations of two stresses compared to dynamic inputs of a single stress. They applied the two stresses - carbon stress and hyperosmotic stress - either in or out of phase, adding and removing glucose and sorbitol.

Both a strength and a weakness is that the cells' hyperosmotic response strongly requires glucose. For in-phase stress, cells are exposed to hyperosmotic shock without glucose, limiting their ability to respond with the well-studied HOG pathway; for anti-phase stress, cells do have glucose when hyperosmotically shocked, but experience a hypo-osmotic shock when both glucose and sorbitol are simultaneously removed. Responding with the HOG pathway and so amassing intracellular glycerol amplifies the impact of this hypo-osmotic shock. Counterintuitively then, it is the presence of glucose rather than the stress of its absence that is deleterious for the cells.

The bulk of the paper supports these conclusions with clean, compelling time-lapse microscopy, including extensive analysis of gene deletions in the HOG network and measurements of both division and death rates. The methodology the authors develop is powerful and widely applicable.

The authors' findings demonstrate the tight links that can exist between metabolism and the ability to respond to stress and the novel insights that can be gained using multiple dynamic inputs.

Author Response

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

eLife assessment

This study of extrachromosomal DNA (ecDNA) aims to identify genes that distinguish ecDNA+ and ecDNA- tumors. This timely study is important in addressing the genes responding to the amplification of the ecDNA. The data presented are for the most part solid, there were concerns regarding the clarity in the description of the analysis methods and whether the evidence for specific genes required to maintain the ecDNA+ state was entirely conclusive.

Public Reviews:

Reviewer #1 (Public Review):

Recently discovered extrachromosomal DNA (ecDNA) provides an alternative non-chromosomal means for oncogene amplification and a potent substrate for selective evolution of tumors. The current work aims to identify key genes whose expression distinguishes ecDNA+ and ecDNA- tumors and the associated processes to shed light on the biological mechanisms underlying ecDNA genesis and their oncogenic effects. While this is clearly an important question, the analysis and the evidence supporting the claims are weak. The specific machine learning approach seems unnecessarily convoluted, insufficiently justified and explained, and the language used by the authors conflates correlation with causality. This work points to specific GO processes associated (up and down) with ecDNA+ tumors, many of which are expected but some seem intriguing, such as association with DSB pathways. My specific comments are listed below.

Response. As some of the specific questions below address similar concerns, we have answered them briefly here. As a high level point, the reviewer is correct in that other statistical or ML approaches could potentially have been used, and that some are simpler. However, the test used here directly addresses the question: Find a collection of genes whose expression value is predictive of ecDNA status in the sample. Because the underlying method in the Boruta analysis uses random forests, it can test predictive power without relying on a linearity assumption implicit in other methods. In this revision, we also compare against a Generalized Linear Model and show that it is less suited to the specific task above. We also address the reviewer concerns about specific parameter choices by showing robustness to the specific parameter.

(A) The claim of identifying genes required to 'maintain' ecDNA+ status is not justified - predictive features are not necessarily causal.

Response. We agree with the reviewer that predictive features are correlative and not causal. In the manuscript, we identify genes whose expression (when used as a feature) is predictive of ecDNA presence or absence. Such predictive genes are consistently over-expressed or consistently under-expressed in ecDNA(+) samples relative to ecDNA(-) samples even though they are not required to be on ecDNA. To our knowledge, we did not claim that these genes are causal for ecDNA formation or maintenance, only that such genes and the underlying biological processes are worth investigating. In the beginning of the manuscript, we had written the following paragraph, but we have removed the last line (struck out here):

“In lieu of identifying genes that are highly differentially expressed between ecDNA(+) and ecDNA(-) samples but driven by a small subset of cases (e.g. gene A in Fig. S1a), we sought to identify genes (e.g. gene B) whose expression level was predictive of ecDNA presence. We assumed that genes that were persistently over-expressed or under-expressed in ecDNA(+) samples relative to ecDNA(-) samples were more likely to be involved in ecDNA biogenesis or maintenance, or in mediating the cellular response to the presence of ecDNA.”

We revised the manuscript to make sure that there are no claims that refer to causality. We revisited all phrases where the words like “maintain” were used and added appropriate disclaimers, or replaced them by the phrase, “ecDNA presence.” The remaining statements say, for example, “These results are consistent with a pan-cancer role of CorEx genes in ecDNA biogenesis and maintenance,” and do not claim causality.

(B) The methods and procedures to identify the key genes is hyper-parameterized and convoluted and casts doubt on the robustness of the findings given the size and heterogeneity of the data.

(a) In the first two paragraphs of Boruta Analysis Methods section, authors describe an iterative procedure where in each iteration, a binomial p-value is computed for each gene based on number of iterations thus far in which the gene was selected (higher GINI index than max of shadow features). But then in the third paragraph they simply perform Random Forest in 200 random 80% of samples and pick a gene if it is selected in at least 10/200. It is ultimately not clear what was done. Why 10/200? Also "the probability that a gene is a "hit" or "non-hit" in each iteration is 0.5" is unclear. That probability is of a gene achieving GINI index higher than the max of shadow features. How can it be 0.5?

Response. We believe that there is some misunderstanding about the algorithm, and we agree that the description should have been more clear. We have greatly simplified the description in the manuscript. However, we want to provide some higher-level explanation here. Boruta is a standard feature extraction algorithm (Kursa, Journal of Statistical Software September 2010, Volume 36, Issue 11), and we used a Python implementation of the method. Given a gene expression data-set with class labels on samples, Boruta extracts features (genes) that best predict the class labels using a Random Forest Classifier, as long as the features are more predictive than permuted features added in each iteration. As we are using an implementation of a published method, we have removed non-essential details, referring directly to the publication. Nevertheless, to address the reviewer’s specific critique, the number of false-features added changes in each iteration (it equals the number of accepted+uncommitted features). Therefore, the choice of 0.5 by Boruta (it is fixed in the published method and not a user-specified parameter) is a conservative approach. If a gene was no better than a randomly chosen feature, its predictive performance would exceed the most predictive randomly chosen feature by at most 0.5 (but could be lower, making the choice of 0.5 conservative).

While Boruta iteratively picks genes that are significantly better than random features, the list of genes predicted might be specific to the data-set, and might change with different data-sets. Therefore, we employed a bootstrapping strategy: we performed 200 trials each time picking 80% of the ecDNA(+) samples and 80% of the ecDNA(-) samples at random, thus generating many data-sets while maintaining class imbalance. For each of the 200 trials, we performed a Boruta analysis. Finally, we picked a gene if it was selected as a Boruta feature in at least 10 of 200 trials.

The reviewer has a reasonable critique about why 10 (of 200) specifically, and why not fewer or more. Most genes are weak predictors by themselves. For example, RAE1, which is the top ranked gene, picked in all 200 Boruta trials, can only predict ecDNA status with poor recall for any meaningful precision.

Author response image 1.

Given the weakness of an individual gene as a classifier, its repeated selection in multiple Boruta trials is already a significant event. By requiring a gene to be picked in 5% of the trials (10/200), we were selecting a small, but more robust list of genes. However, to further explore the reviewer’s concerns, we also applied 8 other selection criteria ranging from 5 (of 200 Boruta trials) to 200 of 200 Boruta trials. See Figure below. The number of CorEx genes expectedly decreases. However, of the 187 GO terms that were enriched by 262 UP-genes using 10 of 200 Boruta trials as the selection criteria, 93 terms (49.7%) were enriched for each cut-off (see Author response image 2), and 155 terms (82.9%) were enriched in at least 5 of the 8 cut-off criteria. Given that the remaining analysis works on the hierarchy of GO terms and finds 4 GO-categories (Mitotic Cell Cycle, G1/S, G2/M; cell-division; DSB DNA Damage response; and the HOX Gene cluster) enriched by UP-regulated genes, those conclusions would hold regardless of the specific cut-off.

Author response image 2.

The number of GO terms that were enriched by DOWN-regulated genes is smaller, only 73, and falls rapidly for higher cut-offs, with 25 at a cut-off of 15. Therefore we see fewer terms enriched for more stringent cut-offs. However, they all support immune processes. These results do suggest that there are fewer genes that are consistently down-regulated in ecDNA(+) cancers, and expression change in a small number of genes may be sufficient to promote conditions for ecDNA.

Finally, we note that in the final section we discuss the 65 most highly ranked genes with a harmonic mean rank <= 3. These 65 CorEx genes (or a member of their cluster) appear in each of 200 Boruta trials. Thus, their choice is also not dependent on the cut-off of 10 in 200. In summary, the conclusions of the paper do not depend upon the specific cut-off of 10 in 200 trials.

We have added the figure as a supplemental figure and have added the following text to the manuscript on pages 17 and 18.

“Any CorEx gene is either a Core gene that was selected as a feature in at least 5% of 200 Boruta trials, or be highly co-expressed with a Core gene. Because the selection criterion of 5% is arbitrary, we also tested robustness with 8 other cut-offs ranging from 5-of-200 to 200-of-200 Boruta trials. The number of CorEx genes expectedly decreases with more stringent cut-offs. However, of the 187 GO terms that were enriched by 262 CorEx UP-genes using 10 of 200 Boruta trials as the selection criteria, 93 terms (49.7%) were enriched for each cut-off (Fig. S9), and 155 terms (82.9%) were enriched in at least 5 of the 8 cut-offs. Given that our subsequent analyses utilized the hierarchy of GO terms and identified 4 GO-categories enriched by UP-regulated genes, the conclusions would hold regardless of the specific cut-off.”

(b) The approach of combining genes with clusters is arbitrary. Why not start with clusters and evaluate each cluster (using some gene set summary score) for their ability to discriminate? Ultimately, one needs additional information to disambiguate correlated genes (i.e. in a coexpression cluster) in terms of causality.

Response. In general, the approach proposed by the reviewer is reasonable. However, we did consider that possibility and found that our approach was easier to implement. For example, if we clustered first, we would have the challenge of choosing the correct set of clusters. Also, the Boruta analysis would become very difficult while dealing with clusters (e.g., how to define falsefeatures?). We tested other methods of picking genes that were suggested by other reviewers such as generalized linear models. They turned out not to be as predictive of ecDNA status, as described later in the response. Finally, we performed many experiments to ensure the validity of the clustering. Specifically, we had the following text in the paper:

“Notably, among the 354 clusters, only 2 clusters (with 14 total genes) did not contain any Core genes. As most genes do not have completely identical expression patterns, we would expect one gene to be consistently picked as a Boruta gene over another co-expressed gene. Consistent with this hypothesis, most (344/354) clusters contained only 1 or 2 Core genes (Fig. 1c). When selecting clusters that contained at least 1 Core and 1 co-expressed gene, 53 of 71 clusters contained 1 to 3 Core genes (Fig. S1b), confirming that a few genes per co-expressed cluster provide sufficient predictive value, but other co-expressed genes might still play an important functional role in maintaining ecDNA(+) status.”

These experiments suggest that the genes found by extending the Core genes through clustering do not radically change the Core genes, but only enhance the set.

(c) The cross-validation procedure is not clear at all. There is a mention of 80-20 split but exactly how/if the evaluation is done on the 20% is muddled. The way precision-recall procedure is also a bit convoluted - why not simply use the area under the PR curve?

Response. We apologize if the method was unclear. We have rewritten the methods part to make things clearer. As a high level point, there are two places where we use the same 80-20 split, and that resulted in some confusion. We start by randomly picking 80% of the ecDNA(+) and 80% of ecDNA(-) samples to create an 80-20 split of all samples. This procedure is repeated to generate 200 80-20 split data-sets. These data-sets are hereafter called 200 training and test samples.

In the first usage, we use only the ‘training’ part of the 200 samples. We apply Boruta to each training set, and this helps us select the Core genes, which are then expanded to form the CorEx set. At this point, the CorEx genes are frozen for analysis in the rest of the paper. One question that we subsequently answer is what is the predictive power of the CorEx genes in determining if the sample is ecDNA(+) or ecDNA(-)? We also compare the predictive performance of CorEx genes relative to (a) Core genes, (b) LFC genes, and (c) random genes. In the revised manuscript, we have added another list of 3,012 genes selected using a single gene generalized linear model (GLM) for feature prediction. To make these comparisons, we utilized the same 200 training and test data-sets as before. In each test, we trained a random forest classifier on the training set and predicted on the ‘test’ set, for each of the 5 gene lists. This provided a uniform and fair method for testing which of the 5 gene lists was the better predictor of ecDNA status.

The precision recall values are plotted in Fig. 2b (also included below). We note that none of the gene lists was a great predictor of ecDNA status of a sample. However, the CorEx and Core genes were significantly more predictive than GLM, LFC, and random genes. The predictive power of GLM genes was very similar to LFC, and better than random.

For each of these 200 tests, we obtained a separate area under the precision-recall curve number for each of the gene-sets. To address the reviewer’s comments regarding a single number, we reported the average of the AUPRC for each of the gene-sets in the revision. The mean AUPRC values were added to the manuscript and are described here as well: Core_408_genes: 0.495 CorEx_643_genes: 0.48 Random_643_genes: 0.36 top_lfc_643_genes: 0.429 GLM_R_3012_genes: 0.426

We also changed Figure 2b to show box-plots showing distribution of recall values for specific precision windows instead of maximum recall. For ease of checking, the figure is reproduced below.

Author response image 3.

(d) The claim is that Boruta genes are different from differentially expressed genes but the differential expression seems to be estimated without regards to cancer type, which would certainly be highly biased and misleading. Why not do a simple regression of gene expression by ecDNA status, cancer type and select the genes that show significant coefficient for ecDNA status?

Response. As requested by the reviewer, and in the more detailed questions below, we added an alternative model with a generalized linear model (GLM) analysis that controlled for tumor subtype. The method itself is described in the Methods section and pasted below. The GLM genes were tested along with the LFC, CorEx, Core genes as described in response to the previous question, and those results are now presented in Figure 2b and on pages 6 and 7 of the revised manuscript.

“We tested each of 16,309 genes independently in a separate logistic regression model using the glm() function in the R stats package (v4.2.0), and retained genes that were significant (p-value 0.01). Specifically, the model was defined as glm(𝑦 ~ 𝑔𝑗 + 𝑡𝑡, data = 𝑀, family = binomial(link = 'logit')), where y is the response vector where 𝑦𝑖=1 if sample 𝑖 ∈ {1, . . . ,870} is ecDNA(+) and 𝑦𝑖 =0 otherwise, 𝑔𝑗 is the vector of expression values for gene j ∈ {1, . . . ,16309} in samples 𝑖 ∈ {1,. . . ,870}, t is the covariate vector representing the tumor subtypes of samples 𝑖 ∈ {1, . . . ,870}, and 𝑀 is the data matrix containing values of gene expression, tumor subtype, and ecDNA status for all samples. The equation for the binomial logistic regression described above 𝑝𝑝 is formulated as where p is the probability that the dependent variable y is 1, 𝑋 are the independent variables, and 𝛽 are the coefficients of the model. In this case, k=1 represents independent variable gene j and k=2 represents the tumor subtype covariate t. Of the 16,309 genes tested independently, 3,012 genes were significant at pvalue<0.01.”

(C) After identifying key features (which the authors inappropriate imply to be causal) they perform a series of enrichment/correlative analysis.

Response. We have reviewed the document to ensure that we did not use the word ‘causal.’ If the reviewer can point to specific text, we are happy to change the phrasing.

(a) It is known that ecDNA status associates with poor survival, and so are cell cycle related signal. Then the association between Boruta genes and those processes is entirely expected. Is it not? The same goes for downregulation of immune processes.

Response. We agree with the reviewer that cell cycle related signals and immune related signals are associated with low survival, and so does ecDNA. However, many cellular processes could be associated with low survival (including for example, metabolic processes, protein and DNA biosynthesis, etc.). The unexpected part is that there appear to be only 4 major processes that are upregulated in ecDNA(+) cancers relative to ecDNA(-) cancers, and only one (immune response) that is downregulated.

(b) The association with DSB specifically is interesting. Further analysis or discussion of why this should be would strengthen the work.

Response. We thank the reviewer for their comment, and agree with their perspective. Note that we devoted a fair amount of text to analysis of DSB pathways. Specifically, we parsed the 4 main pathways in Figure 3b, and found our data to suggest that many genes in the classical nonhomologous end joining repair pathway are down-regulated in ecDNA(+) samples relative to ecDNA(-) samples. In contrast, Alternative end-joining and homology directed repair pathways are upregulated. This is a surprising result because c-NHEJ is considered to be an important mechanism of DSB repair. We have some lines in the discussion that address this:

“The DNA damage genes are broadly up-regulated in ecDNA(+) samples, especially in double-strand break repair. Within this broad category of mechanisms, our analysis suggests that alternative DSB repair pathways such as Alt-EJ are preferred relative to classical NHEJ. This is consistent with previous observations of small microhomologies at breakpoint junctions, and has important implications in therapeutic selection that will need to be validated in future experimental studies. We note, however, the microhomology analyses typically study breakpoint junctions, and might ignore double-strand breaks in non-junctional sequences which could be observed, for example at replication-transcription junctions.”

We note that additional experimental work to corroborate these findings is significant effort and will be part of ongoing research in our collaborators’ laboratories.

(c) On page 15, second paragraph, when providing the up versus down CorEx genes, please also provide up versus down for non-CorEx genes as well to get a sense of magnitude.

Response. We thank the reviewer for the comment. We note that Supplementary Table S15 has the complete contingency tables as well as the Fisher Exact Test statistic for all categories. For the specific categories mentioned in the paper, the chi-square tables are reproduced below. As we are citing TableS15 (containing all numbers and the statistic p-value) in the main text, we thought it was better to leave the text as it was.

Category: Inflammation (p-value: 0.005)

CorEx: 18 (UP), 76 (DOWN)

Non-CorEx: 325 (UP), 657 (DOWN)

Category: Leukocyte migration and chemotaxis (p-value: 0.03)

CorEx: 13 (UP), 49 (DOWN)

Non-CorEx: 213 (UP), 410 (DOWN)

Category: Lymphocyte activation (p-value: 0.0075)

CorEx: 23 (UP), 75 (DOWN)

Non-CorEx: 334 (UP), 560 (DOWN)

Category: Cytokine production (p-value: 0.117)

CorEx: 6 (UP), 28 (DOWN)

Non-CorEx: 93 (UP), 208 (DOWN)

(d) The finding that Boruta genes are associated with high mutation burden is intriguing because in general mutation burden is associated with better survival and immunotherapy response. This counter-intuitive result should be scrutinized more to strengthen the work.

Response. We agree with the reviewer that it is an intriguing observation. However, we are cautious in our interpretation. This is for the following reasons (all mentioned in the text):

(1) The total mutation burden was significantly higher in ecDNA(+) samples relative to ecDNA(-) samples (Fig. 5a). However, when controlling for cancer type, only glioblastoma, low-grade gliomas, and uterine corpus endometrial carcinoma continued to show differential total mutational burden (Fig. S7b).

(2) We tested if specific genes were differentially mutated between the two classes (Fig. 5b). For deleterious/high-impact mutations, TP53 was the only gene whose mutational patterns were significantly higher in ecDNA(+) compared to ecDNA(-) (OR 2.67, Bonferroni adjusted p-value 4.22e-07). BRAF mutations, however, were more common in ecDNA(-) samples and were significant to an adjusted p-value < 0.1 (OR 0.27).

(3) In response to another reviewer’s comment, we also tested correlation with variant allele frequencies, and did not find any significant correlation except for TP53. We decided not to include that result in the paper.

These tissue specific cases might be confounding the main observation, but we have placed all of them together so that the reader can gain a better understanding. It is worth noting that the correlation between high TMB and immunotherapy response is also now controversial, and perhaps not true for all cancer types. See for example (https://www.annalsofoncology.org/article/S0923-7534(21)00123-X/fulltext), which suggests that this relationship is not true for Glioma, and in Glioma (which is ecDNA enriched), higher TMB is associated with worse immunotherapy response. Our results are consistent with that finding. We have modified the discussion paragraph to better reflect this.

“Mutation data alone does not provide as clear a picture of the genes involved in ecDNA maintenance. We did observe that the total mutation burden (TMB) was higher in ecDNA(+) samples. However, that relationship is much less clear after controlling for cancer type. High TMB has been positively correlated with sensitivity to immunotherapy52, and better patient outcomes; however, the gene expression patterns suggest that immunomodulatory genes are downregulated in ecDNA(+) samples, and patients with ecDNA(+) tumors have worse outcomes2. Notably, other results have suggested that the correlation between TMB and response to immunotherapy is not uniform, and it can vary across different tumor subtypes53. Specifically, our data is consistent with previous results which showed that Gliomas with high TMB have worse response to immunotherapy relative to gliomas with low TMB53. In general, no collection of gene mutations was predictive of ecDNA status, although mutations in TP53 were more likely in ecDNA(+) samples, and perhaps are an important driver for ecDNA formation5.”

(e) On page 17 "12 of the 47 genes not specifically enriching any known GO biological Process" is confusing. How can individual gene enrich for a GO process?

Response. We agree that the statement was incorrectly phrased. We have changed it to state that “Only 12 of the 47 genes were not included in the gene sets of any enriched GO term.”

Reviewer #2 (Public Review):

In their manuscript entitled "Transcriptional immune suppression and upregulation of double stranded DNA damage and repair repertoires in ecDNA-containing tumors" Lin et al. describe an important study on the transcriptional programs associated with the presence of extrachromosomal DNA in a cohort of 870 cancers of different origin. The authors find that compared to cancers lacking such amplifications, ecDNA+ cancers express higher levels of DNA damage repair-associated genes, but lower levels of immune-related gene programs.

This work is very timely and its findings have the potential to be very impactful, as the transcriptional context differences between ecDNA+ and ecDNA- cancers are currently largely unknown. The observation that immune programs are downregulated in ecDNA+ cancers may initiate new preclinical and translational studies that impact the way ecDNA+ cancers are treated in the future. Thus, this study has important theoretical implications that have the potential to substantially advance our understanding of ecDNA+ cancers.

Strengths

The authors provide compelling evidence for their conclusions based on large patient datasets. The methods they used and analyses are rigorous.

Weaknesses

The biological interpretation of the data remains observational. The direct implication of these genes in ecDNA(+) tumors is not tested experimentally.

Response. We agree with the reviewer that experimental tests would be ideal. Towards that, there are some challenges. The immune system genes cannot be tested in cell line models as they need a tumor microenvironment. Tests of DSB repair mechanisms and cell cycle control can be performed in cell-lines, but not with the TCGA samples which are not available. Some of our collaborators are actively working on these topics, but that extensive experimental work is beyond the scope of this paper.

Reviewer #3 (Public Review):

Summary:

Using a combination of approaches, including automated feature selection and hierarchical clustering, the author identified a set of genes persistently associated with extrachromosomal DNA (ecDNA) presence across cancer types. The authors further validated the gene set identified using gene ontology enrichment analysis and identified that upregulated genes in extrachromosomal DNA-containing tumors are enriched in biological processes like DNA damage and cell proliferation, whereas downregulated genes are enriched in immune response processes.

Major comments:

(1) The authors presented a solid comparative analysis of ecDNA-containing and ecDNA-free tumors. An established automated feature selection approach, Boruta, was used to select differentially expressed genes (DEG) in ecDNA(+) and ecDNA(-) TCGA tumor samples, and the iterative selection process and two-tier multiple hypothesis testing ensured the selection of reliable DEGs. The author showed that the DEG selected using Boruta has stronger predictive power than genes with top log-fold changes.

(2) The author performed a thorough interpretation of the findings with GO enrichment analysis of biological processes enriched in the identified DEG set, and presented interesting findings, including the enrichment in DNA damage process among the genes upregulated in ecDNA(+) tumors.

(3) Overall, the authors achieved their aims with solid data mining and analysis approaches applied to public data tumor data sets.

(4) While it may not be the scope of this study, it will be interesting to at least have some justification for choosing Boruta over other feature selection methods, such as Recursive Feature Elimination (RFE) and backward stepwise selection.

Response. We actually agree with the reviewer that some other feature selection methods could work just as well, and note that the Boruta analysis is not our creation, but a published feature selection method (Kursa, Journal of Statistical Software September 2010, Volume 36, Issue 11). We use Boruta to identify relevant genes, but the bulk of the paper is to understand the biological processes driven by that gene selection. Even if we had chosen another method that performed slightly better, it likely would not change the main conclusions. However, to address the reviewers concerns on over-reliance on one method, we added a different gene list created by a generalized linear model analysis, with the goal of checking if the expression of a gene could predict the ecDNA status of the sample after controlling for tumor subtype. Thus, we tested 5 different genelists in terms of their power in predicting ecDNA. While none of the lists is a great predictor of ecDNA status, the Core and CorEx gene lists are significantly better than the other lists. The Figure below replaces the previous Figure panels 2b and 2c.

Author response image 4.

(1) The authors showed that DESEQ-selected DEGs with top log-fold changes have less strong predictive power and speculated that this may be due to the fact that genes with top log-fold changes (LFC) are confined only to a small subset of samples. It will be interesting to select DEGs with top log-fold changes after first partitioning the tumor samples. For example, randomly partition the tumor samples, identify the DEGs with top LFC, combine the DEGs identified from each partition, then evaluate the predictive power of these DEGs against the Boruta-selected DEGs.

Response. This is a great comment. We added a generalized linear model test for selecting genes whose expression is predictive of ecDNA status. The GLM list described above uses a standard methodology (Analysis of Variance) controls for tumor type as a covariate, and its predictive performance is only slightly better than the Top-|LFC| genes, while improving over a random gene set.

(2) While the authors showed that the presence of mutations was not able to classify ecDNA(+) and (-) tumor samples, it will be interesting to see if variant allele frequencies of the genes containing these mutations have predictive power.

Response. This is a great suggestion. To address the reviewer’s question, we used allelic counts (REFs and ALTs) information from the MC3 variant callset, and calculated allele frequencies of all variants from samples where ecDNA status was available. Next, we conducted a Wilcoxon rank-sum test between VAFs of the ecDNA(+) group and VAFs of the ecDNA(-) group for every mutated gene. We found 1,073 genes with p<0.05, but among them, only TP53 passed the multiple testing correction (padj<0.05, Benjamini-Hochberg). As the results are identical to the tests based solely on presence of mutations, we decided not to include this data.

Reviewer #1 (Recommendations For The Authors):

(A) The presentation should be substantially streamlined.

(B) Preferably use a more intuitive simpler ML approach with fewer parameters to make it more credible. Because there are relatively few samples across numerous cancer types with greater variability in representation, a simpler procedure with transparent controls will be more convincing.

Response. We accept the reviewer’s criticism in that other statistical or ML approaches could potentially have been used, and that some are simpler. However, the test used here directly addresses the question: Find a collection of genes whose expression value is predictive of ecDNA status in the sample. Because the underlying method in the Boruta analysis uses random forests, it can test predictive power without relying on a linearity assumption implicit in other methods. In this revision, we also compare against a Generalized Linear Model (regression analysis) and show that it is less suited to the specific task above. We address the reviewer concerns about specific parameter choices by showing robustness to the specific parameter. All details are provided in the initial questions, and in the revised manuscript.

(C) Avoid using any term implying causality unless you can bring in direct experimental evidence (e.g. mutagenesis experiment followed by ecDNA measurement. Some places you use the word 'maintain ecDNA' and other places 'ecDNA impact'. But these are all associations. How can you distinguish causal genes from downstream effects without additional data?

Response. We note that the word causal does not appear anywhere in the manuscript, and was not intended. Additionally we have revised the manuscript and are open to specific changes requested by the reviewer or the editors.

(D) Along these lines, if Boruta genes are indeed causal, one would expect Boruta-Up genes to be amplified more than expected in the ecDNA+; converse for Boruta-down genes.

Response. We did not understand the reviewer’s question. By “amplified,” if the reviewer means “amplification of transcript level,” then that is exactly what the Boruta analysis is showing. Specifically, for each gene, we have the ability to pick a transcript level cut-off ‘t’ so that samples in which the expression is higher than t are more likely to be ecDNA(+). However, we are not claiming that there is causality, just that the transcript level is (weakly) predictive of the ecDNA status of the sample.

(E) A strawman control should be a simple regression-based gene identification that controls for ecDNA status and cancer type.

Response. We agree that this was a very good suggestion. In the revision, we have applied a GLM, which controls for tumor type. Thus, we have 5 gene-lists (including the Core and CorEx genes). As described in the revised manuscript but also in response to the main comments above, none of the lists are a great predictor. However, the CorEx and Core genes are significantly better at predicting ecDNA status of a sample.

Reviewer #2 (Recommendations For The Authors):

Comments

(1) The analysis hinges on a classification of tumors into ecDNA(+) and ecDNA(-) using AmpliconClassifier. It would be good to know how robust the outcomes are with respect to the performance of AmpliconClassifier - how many false positives and negatives will AmpliconClassifier generate on this dataset and how would this influence the CorEx genes?

Response. This is a very reasonable request. AA has been extensively tested on established cell-lines for its ability in predicting ecDNA status, and this information is published in multiple venues, including Kim, Nature genetics 2020, and shows precision 85% for recall 83%. For completeness, we have reproduced the relevant plot from that paper here, and the relevant text here, but are not including it in the manuscript.

“To evaluate the accuracy of the AmpliconArchitect predictions, we analyzed whole-genome sequencing data from a panel of 44 cancer cell lines, and examined tumor cells in metaphase. We used 35 unique fluorescence in-situ hybridization (FISH) probes in combination with matched centromeric probes (81 distinct “cell-line, probe” combinations) to determine the intranuclear location of amplicons (Supplementary Table 2). Following automated analysis >1,600 images, we observed that 85% of amplicons characterized as ‘Circular’ by whole genome sequencing profile demonstrated an extrachromosomal fluorescent signal, representing the positive predictive value. Of the amplicons corresponding to extrachromosomally located FISH probes, 83% were classified as Circular, representing the sensitivity (Extended Data Fig. 1A).”

Author response image 5.

(2) It is unclear why genes are labeled Boruta genes when they are present in 10 out of 200 runs, this seems like an unexpectedly low number. How did the authors arrive at this number? Do the authors have any ground truth to estimate how well Boruta works in this setting and implementation?

Response. This is a great question and asked by another reviewer as well. Given the weakness of an individual gene as a classifier, its repeated selection in multiple Boruta trials is already a significant event. By requiring a gene to be picked in 5% of the trials (10/200), we were selecting a small, but more robust list of genes. However, to further explore the reviewer’s concerns, we also applied 8 other selection criteria ranging from 5 (of 200 Boruta trials) to 200 of 200 Boruta trials. See Figure below. The number of CorEx genes expectedly decreases with increasing stringency. However, of the 187 GO terms that were enriched by UP-genes, 93 terms (50%) were enriched regardless of the cut-off (see Figure below), and 153 terms (82%) were enriched in at least 5 of the 8 cut-offs. Given that the remaining analysis works on the hierarchy of GO terms and finds 4 GO-categories (Mitotic Cell Cycle, G1/S, G2/M; cell-division; DSB DNA Damage response; and the HOX Gene cluster) enriched by UP-regulated genes, those conclusions would hold regardless of the specific cut-off.

Author response image 6.

The number of GO terms that were enriched by DOWN-regulated genes is smaller, only 73, and falls rapidly for higher cut-offs, with 25 at a cut-off of 15. Therefore we see fewer terms enriched for more stringent cut-offs. However, they all support immune processes. These results do suggest that there are fewer genes that are consistently down-regulated in ecDNA(+) cancers, and expression change in a small number of genes may be sufficient to promote conditions for ecDNA.

We have added the figure as a supplemental figure and have added the following text to the manuscript on pages 17 and 18.

“Any CorEx gene is either a Core gene that was selected as a feature in at least 5% of 200 Boruta trials, or be highly co-expressed with a Core gene. Because the selection criterion of 5% is arbitrary, we also tested robustness with 8 other cut-offs ranging from 5-of-200 to 200-of-200 Boruta trials. The number of CorEx genes expectedly decreases with more stringent cut-offs.

However, of the 187 GO terms that were enriched by 262 CorEx UP-genes using 10 of 200 Boruta trials as the selection criteria, 93 terms (49.7%) were enriched for each cut-off (Fig. S9), and 155 terms (82.9%) were enriched in at least 5 of the 8 cut-offs. Given that our subsequent analyses utilized the hierarchy of GO terms and identified 4 GO-categories enriched by UP-regulated genes, the conclusions would hold regardless of the specific cut-off.”

(3) Authors extend the core gene set with co-expressed genes, arguing that "gene C" would not add predictive power in addition to "gene B" and is therefore not identified as a Boruta gene. However, from its description in the manuscript (summarized: "Boruta [...] selects the highest feature importance score, s, of shadow features as a cut off, and returns features with a higher score than s."), it isn't immediately obvious to me why Boruta would not return both genes B and C. Maybe the authors could explain this better.

Response. We consider the following.

(1) Consider 100 ecDNA(+) and 100 ecDNA(-) samples. Let the expression levels of genes B and C in the data-sets be as described in the figure below; y-axis is the gene expression, and x-axis is just a listing of all samples, with green color denoting ecDNA(+) samples and orange color denoting ecDNA(-) samples.

Author response image 7.

(2) Then, if we choose gene B and a transcript level of 1.25, we have a perfect prediction of ecDNA status because all samples where gene B has a transcript level higher than 1.25 are ecDNA(+) and otherwise they are ecDNA(-). Similarly, using Gene C, we can get perfect predictions. Thus, when Boruta has to select a gene, it will pick either Gene B or Gene C, because picking both will not improve prediction. We can therefore use Boruta to pick one gene, and then co-expression clustering to pick the other gene.

As an example, cluster #3 consists of 21 genes that were up-regulated in ecDNA(+) samples and enriched in cell-cycle related biological processes (Table S3). While these genes were expressed similarly in ecDNA(+) samples, and separately, in ecDNA(-) samples, out of the 21 genes, only 9 genes were selected in at least 10 out of 200 Boruta trials (i.e., Core genes). Of the 12 remaining genes (i.e., CorEx genes), 8 genes were not selected by the Boruta method at all, 3 genes were selected in less than 5 out of 200 Boruta trials, and 1 gene was selected in 9 out of 200 Boruta trials.

Author response image 8.

(4) In Fig 2a, I would like to see the variability of the precision and recall in the main text, not only the maximum values. Authors could plot mean + standard deviation for precision and recall separately, or use S2a/b.

Response. We have replaced Figures 2b and 2c with a combined figure (Fig. 2b) that gives a box-plot describing the distribution of recall values for 5 gene lists: four from the original manuscript, and another gene list created using a Generalized Linear Model (GLM).

Author response image 9.

(5) Since the authors analyze bulk RNA, the gene expression signatures they notice could, in principle, originate from non-tumor cells as well. I do not believe this is the case, however, the paper would be strengthened by an analysis that shows that the difference in expression patterns of the Corex genes between ecDNA(+) and ecDNA(-)-samples does come from tumor cells. One way of showing this would be by using single-cell mRNA-sequencing data, and another way of showing this would be to show that Corex gene-expression correlates with tumor purity in bulk samples.

Response. The reviewer is correct. Unfortunately, our analysis requires data with whole-genome sequencing (WGS) for ecDNA prediction, as well as RNA-seq for transcriptome profiling. The TCGA data-set is the only available data-set with a significant number of samples that includes both WGS and RNA-seq. They have not made tissue samples available for scRNA analysis, to our knowledge. The reviewer raises an important question regarding purity, but testing if CorEx gene expression correlates with tumor purity would require a large range of purity values, something that scientists would avoid when collecting samples.

However, the presence of non-cancer tissue (impurity) could reduce sensitivity of ecDNA detection, and therefore, change the results. To better investigate this, we started with a publication that investigated multiple tumor purity metrics and devised a composite score (CPE; Aran et al., 2015). Using their composite tumor purity, we find that ecDNA(-) samples have slightly lower purity than ecDNA(+) samples (p-value 0.0036; Fig. S2a).

This result is not surprising because one would expect lower detection of ecDNA in less pure samples. The presence of undetected ecDNA in ecDNA(-) samples would confound the results by reducing the discriminating power of genes, but would not give false results. To test this, we measured the expression directionality in CorEx genes in all samples versus samples which had a high tumor purity (CPE 0.8). The results suggest that the p-values of directionality in the pure samples were highly correlated with the expression data from all samples (Fig. S2b).

Author response image 10.

(6) The biological interpretation of the data remains a bit too observational. Can the authors offer an interpretation of the enriched GO terms? And are any of these genes already implicated in ecDNA(+) tumors?

Response. To answer the second question first, prior to our study, the focus was on genes that were amplified on ecDNA. Indeed many oncogenes known to be amplified in cancer are in fact amplified on ecDNA (Turner, Nature 2017, Kim Nature genetics 2020). This study is unique in that it identifies genes whose expression values are predictive of ecDNA(+) status. The Figure below lists 24 genes most frequently amplified on ecDNA from Kim, Nature Genetics 2020. With the exception of EGFR and CDK4, none of these 24 genes was included in the list of the 65 genes reported by us as the most frequently selected genes in the Boruta trials (lowest harmonic rank). Thus, most persistent CorEx genes do not lie on ecDNA. However, they all play important roles in biological processes relevant to cancer pathology including Immune Response, Mitotic cell Cycle, Cell division, and DSB repair. We agree with the reviewer that the results are observational (although statistically significant in populations), and some of our collaborators are actively working to experimentally validate some of these genes. The experimental work, however, is beyond the scope of this paper.

We have added the following statement to the manuscript. “Notably, of the 24 genes most frequently expressed on ecDNA,2 only EGFR and CDK4 were included in the list of 65 genes, suggesting that the most persistent CorEx genes do not themselves appear frequently on ecDNA.”

Author response image 11.

Reviewer #3 (Recommendations For The Authors):

Minor comments:

(1) The authors performed gene ontology enrichment test but referred to it as gene set enrichment analysis. Usually gene set enrichment analysis does not refer to Fischer's exact test-based analysis but rather the one described in Subramanian et al 2005. The term correction should be made to avoid confusion.

Response. We have rephrased text in the manuscript to prevent confusion between enrichment analysis on gene sets using an one-sided Fisher’s exact test and the Gene Set Enrichment Analysis (GSEA) method that exists as a software. We have also revised the header in the methods section from “Gene set enrichment analysis” to “Gene Ontology (GO) enrichment analysis”.

(2) A couple of figures could use more detailed labels and captions. In Figure 2c, it is unclear what the numbers 100 and 54 right next to the Cliff's Delta heatmap indicate. In Figures 3a and 4a, it is not immediately clear what the barplot on top of the heatmap indicates and there is no label for the y-axis.

Response. These are good suggestions, and we have added descriptions to the figure captions.

Reviewer #3 (Public Review):

Summary:

Using a combination of approaches, including automated feature selection and hierarchical clustering, the author identified a set of genes persistently associated with extrachromosomal DNA (ecDNA) presence across cancer types. The authors further validated the gene set identified using gene ontology enrichment analysis and identified that upregulated genes in extrachromosomal DNA-containing tumors are enriched in biological processes like DNA damage and cell proliferation, whereas downregulated genes are enriched in immune response processes.

Comments for the previous version:

Major comments:

(1) The authors presented a solid comparative analysis of ecDNA-containing and ecDNA-free tumors. An established automated feature selection approach, Boruta, was used to select differentially expressed genes (DEG) in ecDNA(+) and ecDNA(-) TCGA tumor samples, and the iterative selection process and two-tier multiple hypothesis testing ensured the selection of reliable DEGs. The author showed that the DEG selected using Boruta has stronger predictive power than genes with top log-fold changes.

(2) The author performed a thorough interpretation of the findings with GO enrichment analysis of biological processes enriched in the identified DEG set and presented interesting findings, including the enrichment in DNA damage process among the genes upregulated in ecDNA(+) tumors.

(3) Overall, the authors achieved their aims with solid data mining and analysis approaches applied to public data tumor data sets.

(4) While it may not be the scope of this study, it will be interesting to at least have some justification for choosing Boruta over other feature selection methods, such as Recursive Feature Elimination (RFE) and backward stepwise selection.

(5) The authors showed that DESEQ-selected DEGs with top log-fold changes have less strong predictive power and speculated that this may be due to the fact that genes with top log-fold changes (LFC) are confined only to a small subset of samples. It will be interesting to select DEGs with top log-fold changes after first partitioning the tumor samples. For example, randomly partition the tumor samples, identify the DEGs with top LFC, combine the DEGs identified from each partition, then evaluate the predictive power of these DEGs against the Boruta-selected DEGs.

(6) While the authors showed that the presence of mutations was not able to classify ecDNA(+) and (-) tumor samples, it will be interesting to see if variant allele frequencies of the genes containing these mutations have predictive power.

Comments for the revised version:

The authors addressed the comments and recommendations with solid analysis and explanations in the revision. The added analysis using GLM is especially appreciated and provides convincing evidence for the predicting power of the Boruta-selected genes. The only comment is at this point is that it is recommended that the author provide some justification for choosing Boruta over other feature selection methods. It is not necessary to provide benchmarking results - justification based on the review of previous literature is sufficient, as it is not well explained in the paper why Boruta was chosen in the first place. Is it state-of-the-art? Has it demonstrated better performance in other settings? A few sentences answering these questions should suffice.

eLife assessment

This study of extrachromosomal DNA (ecDNA) identifies genes that distinguish ecDNA+ and ecDNA- tumors. The findings in the manuscript are important and the genomic analyses convincing. However, some of the data remain observational and the inferences would therefore be more robust with experimental validation. This manuscript could well be of relevance to biologists interested in cancer biology and gene regulation.

Reviewer #1 (Public Review):

Recently discovered extrachromosomal DNA (ecDNA) provides an alternative non-chromosomal means for oncogene amplification and a potent substrate for selective evolution of tumors. The current work aims to identify key genes whose expression distinguishes ecDNA+ and ecDNA- tumors and the associated processes to shed light on the biological mechanisms underlying ecDNA genesis and their oncogenic effects. This is clearly an important question and through detailed analysis this work points to specific GO processes associated (up and down) with ecDNA+ tumors, namely, specific DNA damage repair processes and specific oncogenic processes.

In the initial submission I had commented on lack of clarity of method, potential biases, and in some cases inappropriate interpretation. In the revised version, the authors have addressed all my comments satisfactorily and I think this is an important work furthering our understanding of mechanisms underlying ecDNA+ tumors.

Reviewer #2 (Public Review):

In their manuscript Lin et al. describe an important study on the transcriptional programs associated with the presence of extrachromosomal DNA in a cohort of 870 cancers of different origins. The authors find that compared to cancers lacking such amplifications, ecDNA+ cancers express higher levels of DNA damage repair-associated genes, but lower levels of immune-related gene programs.

This work is very timely and its findings have the potential to be very impactful, as the transcriptional context differences between ecDNA+ and ecDNA- cancers are currently largely unknown. The observation that immune programs are downregulated in ecDNA+ cancers may initiate new preclinical and translational studies that impact the way ecDNA+ cancers are treated in the future. Thus, this study has important theoretical implications that have the potential to substantially advance our understanding of ecDNA+ cancers.

Strengths:

The authors provide compelling evidence for their conclusions based on large patient datasets. The methods they used and analyses are rigorous.

Weaknesses:

The biological interpretation of the data remains observational. The direct implication of these genes in ecDNA(+) tumors is not tested experimentally.

Author Response

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

First, we would like to thank you and all the reviewers for acknowledging the meaningful contribution of our manuscript to the field. Your useful comments helped us improve the manuscript's quality. We understood the key issues of the manuscript were the quantification of inference accuracy and applicability to methylome data. We here therefore present a revised version of the manuscript addressing all major comments.

For each demographic inference we have added the root mean square error as demanded by the reviewers. These results confirm the previous interpretation of the graphs especially in recent times. We also added TMRCA inference analysis as requested by one reviewer as a proof of principle that integrating multiple markers can improve ARG inference.

The discussion was rewritten to further discuss the challenges of application to empirical methylation data. We clarify that in the case epimutations are well understood and modelled, they can be integrated into a SMC framework to improve the approaches accuracy. When epimutations are not well understood, our approach can help understand the epimutations process through generations at the evolutionary time scale along the genome. Hence, in both cases our approach can be used to unveil marker evolution processes through generations, and/or deepen our understanding of the population past history. We hope our discussion underlies better how our approach is designed and can be used.

eLife assessment

This important study advances existing approaches for demographic inference by incorporating rapidly mutating markers such as switches in methylation state. The authors provide a solid comparison of their approach to existing methods, although the work would benefit from some additional consideration of the challenges in the empirical use of methylation data. The work will be of broad interest to population geneticists, both in terms of the novel approach and the statistical inference proposed.

Public Reviews:

Reviewer #1 (Public Review):

The authors developed an extension to the pairwise sequentially Markov coalecent model that allows to simultaneously analyse multiple types of polymorphism data. In this paper, they focus on SNPs and DNA methylation data. Since methylation markers mutate at a much faster rate than SNPs, this potentially gives the method better power to infer size history in the recent past. Additionally, they explored a model where there are both local and regional epimutational processes.

Integrating additional types of heritable markers into SMC is a nice idea which I like in principle. However, a major caveat to this approach seems to be a strong dependence on knowing the epimutation rate. In Fig. 6 it is seen that, when the epimutation rate is known, inferences do indeed look better; but this is not necessarily true when the rate is not known. A roughly similar pattern emerges in Supp. Figs. 4-7; in general, results when the rates have to be estimated don't seem that much better than when focusing on SNPs alone. This carries over to the real data analysis too: the interpretation in Fig. 7 appears to hinge on whether the rates are known or estimated, and the estimated rates differ by a large amount from earlier published ones.

Overall, this is an interesting research direction, and I think the method may hold more promise as we get more and better epigenetic data, and in particular better knowledge of the epigenetic mutational process. At the same time, I would be careful about placing too much emphasis on new findings that emerge solely by switching to SNP+SMP analysis.

Answer: We thank the reviewer 1 for his positive comments and acknowledging the future promises of our method as better and more reliable data will be available in different species. We appreciate the reviewer noticing the complete set of work undertaken here to integrate local and regional effects of methylation into a model containing as much knowledge of the epigenetics mutational processes as possible. Note that in Figure 2 of the manuscript we observed a gain of accuracy even when the rates are unknown. Our results thus suggests that the accuracy gain of additional marker with unknown rates is also possible, although it is most likely be scenario and rate dependent.

At last, as noticed and highlighted by the very recent work of the Johannes lab (Yao et al. Science 2023) using phylogenetic methods, knowing the epimutation rate is essential at short time scale to avoid confounding effects of homoplasy. In our estimation of the coalescent trees, the same applies, though our model considers finite site markers. We now provide additional evidence for the potential gain of power to infer the TMRCA (Supplementary Table S7) when knowing or not the epimutation rates and revised the discussion to clarify the potential shortcomings/caveats for the analysis of real data.

Reviewer #2 (Public Review):

A limitation in using SNPs to understand recent histories of genomes is their low mutation frequency. Tellier et al. explore the possibility of adding hypermutable markers to SNP based methods for better resolution over short time frames. In particular, they hypothesize that epimutations (CG methylation and demethylation) could provide a useful marker for this purpose. Individual CGs in Arabidopsis tends to be either close to 100% methylated or close to 0%, and are inherited stably enough across generations that they can be treated as genetic markers. Small regions containing multiple CGs can also be treated as genetic markers based on their cumulative methylation level. In this manuscript, Tellier et al develop computational methods to use CG methylation as a hypermutable genetic marker and test them on theoretical and real data sets. They do this both for individual CGs and small regions. My review is limited to the simple question of whether using CG methylation for this purpose makes sense at a conceptual level, not at the level of evaluating specific details of the methods. I have a small concern in that it is not clear that CG methylation measurements are nearly as binary in other plants and other eukaryotes as they are in Arabidopsis. However, I see no reason why the concept of this work is not conceptually sound. Especially in the future as new sequencing technologies provide both base calling and methylating calling capabilities, using CG methylation in addition to SNPs could become a useful and feasible tool for population genetics in situations where SNPs are insufficient.

Answer: We thank the reviewer 2 for his positive comments. Indeed, surveys of CG methylation in other plant species show that its distribution is clearly bimodal (i.e. binary). This is not the case for non-CG methylation, such as CHG and CHH (where H=C,T,A). However, these later types of methylation contexts are also not heritable across generations and can therefore not be used as heritable molecular markers.

Reviewer #3 (Public Review):

I very much like this approach and the idea of incorporating hypervariable markers. The method is intriguing, and the ability to e.g. estimate recombination rates, the size of DMRs, etc. is a really nice plus. I am not able to comment on the details of the statistical inference, but from what I can evaluate it seems sound and reasonable. This is an exciting new avenue for thinking about inference from genomic data. I have a few concerns about the presentation and then also questions about the use of empirical methylation data sets.

I think a more detailed description of demographic accuracy is warranted. For example, in L245 MSMC2 identifies the bottleneck (albeit smoothed) and only slightly overestimates recent size. In the same analysis the authors' approach with unknown mu infers a nonexistent population increase by an order of magnitude that is not mentioned.

Answer: We thank the reviewer 3 for his positive comments and refer to our answer to reviewer 1 above. We added RMSE (Root Mean Square Error) analyses to quantify the inference accuracy. We apologize for not mentioning this last point. Thank you for pointing this out and we have now fixed it (line 245-253).

Similarly, it seems problematic that (L556) the approach requiring estimation of site and region parameters (as would presumably be needed in most empirical systems like endangered nonmodel species mentioned in the introduction) does no better than using only SNPs. Overall, I think a more objective and perhaps quantitative comparison of approaches is warranted.

Answer : See answer to reviewer 1 above, and more elaborate answers below. We provide now new RMSE analyses to quantify the accuracy of our demographic inference (Supplementary Tables 1,6,7,8,9,10). We also discuss the validity and usefulness of our approach when the epimutation rates are unknown. In short, the discussion was rewritten to further discuss the challenges of application to empirical methylation data. We clarify that in the case epimutations are well known and modelled (as much is known in A. thaliana for example), they can be integrated into a SMC framework to improve the accuracy of the method approach. When epimutations are not well understood and rates unknown, our approach can help understand the epimutational process through generations at the evolutionary time scale. Hence, whether makers are understood or not, our approach can be used to study the marker evolutionary processes through generations and/or to deepen our understanding of the population past history. We hope our discussion underlies better how our approach is designed and can be used.

The authors simulate methylated markers at 2% (and in some places up to 20%). In many plant genomes a large proportion of cytosines are methylated (e.g. 70% in maize: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8496265/). I don't know what % of these may be polymorphic, but this leads to an order of magnitude more methylated cytosines than there are SNPs. Couldn't this mean that any appreciable error in estimating methylation threatens to be of a similar order of magnitude to the SNP data? I would welcome the authors' thoughts here.

Answer : The reviewer is correct and this is an interesting question. First, studies show that heritable epimutations in plants are restricted to CG dinucleotides that are located well outside of the target regions of de novo methylation pathways in plants. Most of these CGs tend of fall within so-called gene body methylated regions. While it is true that plant species can differ substantially in their proportion of methylation at the genome-wide scale, the number of gene body methylated genes (i.e. genic CG methylation) is relatively similar, and at least well within the same order of magnitude (Takuno et al. Nature Plants 2016, review in Muyle et al. Genome Biol Evol 2022). Moreover, spontaneous CG epimutations in gene body methylated regions has been shown to be neutral (van Der Graaf et al. 2015, Vidali et al. 2016, Yao et al. 2023), which is an ideal property for phylogentic and demographic inference.

Second, CG methylation calls are sometimes affected by coverage or uncertainty. Stringent filtering for reliable SMP calls typically reduces the total proportion of CG sites that can be used as input for demographic inference. Here we only kept CG sites where the methylation information could be fully trusted after SMP calling (i.e. >99.9% posteriori certainty). Overall, this explains why the percentage of sites with methylation information is so small, and why we have decided to work on simulation with 2% of reliable methylated markers.

Nevertheless, for the sake of generality, it may be that in some species such as maize a higher percentage of polymorphic methylated sites can be used, and the number of SMPs could be higher than that of SNPs when the effective population size is very small (due to past demographic history and/or life history traits). In this case, any error in the epimutation rate and variance due to the finite site model estimation (and homoplasy) are not corrected by the lack of SNPs and can lead to mis-inference.

A few points of discussion about the biology of methylation might be worth including. For example, methylation can differ among cell types or cells within a tissue, yet sequencing approaches evaluate a pool of cells. This results in a reasonable fraction of sites having methylation rates not clearly 0 or 1. How does this variation affect the method? Similarly, while the authors cite literature about the stable inheritance of methylation, a sentence or so more about the time scale over which this occurs would be helpful.

Answer: We thank reviewer 3 for asking those very interesting questions, which we further developed below and mention in the discussion (lines 716-722).

For Arabidopsis thaliana:

Following up on our previous comment above, the majority of the CG sites that serve as input to our approach are located in body methylated genes. Previous work has shown that CG methylation in these regions shows essentially no tissue and cellular heterogeneity (e.g. Horvath et al. 2019). This means that bulk methylation measurements only show limited susceptibility to measurement error. That said, to guard against any spurious SMPs call that could arise from residual measurement variation, we applied stringent filtering of CG methylation. We have kept sites where the methylation percentage is close to either 0% or 100% (the rest being removed from the analysis). We have used similar filtering strategies in previous studies of epimutational processes in mutation accumulation lines and long-lived perennials (work of the Johannes lab). In these later studies we found that the SMP calls sufficiently accurate for inferences of phylogenetic parameters in experimental settings (Sharyhary et al. Genome Biology 2021, Yao et al. Science, 2023).

For other species:

It is true that currently, evaluating the methylation state of a site from a pool of cells may be problematic for some species for two main reasons: 1) it will add noise to the signal and SMP calling could be erroneous, and 2) the methylation state used in analysis might originate from different tissues at different location of the genome/methylome. Overall, this will lead to spurious SMPs and can render the inference inaccurate (see Sellinger et al 2021 for the effect of spurious SNPs). Hence, caution is advised when calling SMPs in other species and for different tissues.

Finally, in some species methylated cytosines have mutation rates an order of magnitude higher than other nucleotides. The authors mention they assume independence, but how would violation of this assumption affect their inference?

Answer: Indeed, we assume the mutation and epimutation process to be independent thus the probability for a SNP to occur does not depend on the local methylation state. If this was the case, the mutation rate use would indeed be wrong to a degree function of the dependency between the processes. We suggest that by ignoring this dependence, we are in the same situation as ignoring the variation of mutation rate along the genome. We have previously documented the effect of ignoring this biological feature of genomes in Strüt et al 2023 and Sellinger et al 2021. The variation in mutation rate along the genome if too extreme and not accounted for can lead to erroneous inference results. However, this problem could be easily solved (modelled) by adapting the emission matrix. To correctly model this dependency, additional knowledge is needed: either the mutation and epimutation rates must be known to quantify the dependency, or the dependency must be known to quantify the resulting rates. As far as we know, these data are at the moment not available, but could maybe be obtained using the MA lines of A. thaliana (used in Yao et al. 2023).

Recommendations for the authors:

All three reviewers liked this approach and found it a valuable contribution. I think it is important to address reviewer 1/3 concerns about quantifying the accuracy of inference (the TMRCA approach from reviewer 1 sounds pretty reasonable), and reviewer 1 also highlights an intriguing point about model accuracy being worse when the mutation rate is known. Additionally, I think some discussion is warranted about challenges dealing with empirical methylation data (points from Rev 2 and 3 as well as Rev 1's question about inferred vs published rates of epigenetic mutation).

Answer : We have added tables containing the root mean square error (RMSE) of every demographic inference in the manuscript to better quantify accuracy. We have below given the explanation on why accuracy in presence of site and region epimutations can in some cases decrease when real rates are known (because methylation state at the region level needs to be first inferred). We added evidence that accounting for methylation can improve the accuracy when recovering the TMRCA along the genome when the rates are known. We also have enhanced the discussion on the challenges of dealing with epimutations data for inference. As is suggested, we hope this study will generate an interest in tackling these challenges by applying the methods to various methylome datasets from different species.

Reviewer #1 (Recommendations For The Authors):

Major comments:

• For all of the simulated demographic inference results, only plots are presented. This allowsfor qualitative but not quantitative comparisons to be made across different methods. It is not easy to tell which result is actually better. For example, in Supp. Fig. 5, eSMC2 seems slightly better in the ancient past, and times the trough more effectively, while SMCm seems a bit better in the very recent past. For a more rigorous approach, it would be useful to have accompanying tables that measure e.g. mean-squared error (along with confidence intervals) for each of the different scenarios, similar to what is already done in Tables 1 and 2 for estimating $r$.

Answer : We understand the concern of reviewer #1 for a more quantitative approach to compare the inference results. We agree that plots are not sufficient to fully grasp a method performance. To provide better supports to quantity approaches performance, we added Sup tables 1,6,8,9 and 10 containing the RMSE (in log10 for visibility) for all Figures. The root mean-squared error is calculated as in Sellinger 2021 and a description of how the root mean-squared error is calculated and now found in the method section lines 886-893.

• 434: The discussion downplays the really odd result that inputting the true value of themutation rate, in some cases, produces much worse estimates than when they are learned from data (SFig. 6)! I can't think of any reason why this should happen other than some sort of mathematical error or software bug. I strongly encourage the authors to pin down the cause of this puzzling behaviour.

Answer : There are unfortunately no errors in this plot and those results are perfectly normal and coherent, but we understand they can be confusing at first.

As described in the method section and in the appendix, when accounting for regionlevel epimutations, our algorithm requires the regional methylation status which needs to be inferred as a first step from the data (real or simulated). Because region and single site epimutation events are occurring at similar rates in our simulated scenario, the methylation state of the region is very hard to correctly recover (e.g. there will be unmethylated site in methylated regions and methylated sites in unmethylated regions). In other words, the accuracy of the region estimation HMM procedure is decreased by the joint action of site and region epimutation processes.

When subsequently applying the HMM for inference, as described in the appendix, the probabilities of two CG site being in the same or different methylation state depends on the methlylation state of the "region". Hence the mislabelling of the region methylation state is (to some extent) equivalent to spurious SMPs (or inaccurate SMP calling).

If the true rates for site and region epimutations are given as input, the model forces the demography (and other inferred parameters) to fit the observed distribution of SMPs (given the inputted rates), resulting in the poor accuracy observed in the Figure (Now Supplementary Figure 7).

Note: The estimated rates from real data in A. thaliana suffer from the same issue as the region and site epimutation rates are independently estimated, and the existence of regions first quantified using an independent HMM method (Denkena et al. 2022).

However, when rates are freely inferred, they are inferred accordingly to the estimated methylation status of regions and SNPs. Therefore, even if the inferred rates are wrong, they are used by the SMC in a more consistent way.

Note: When methylation rates violate the infinite site assumption, such as here, we first estimate the tree sequence along the genome using SNPs (i.e. DNA mutations). The algorithm then infers the epimutations rates given the inferred coalescent times and the observed methylation diversity.

To summarise: when inputting rates to the model, if the model fails to correctly recover the region methylation status there will be conflicting information between SNPs and SMPs leading to accuracy loss. However if the rates are inferred this is realized with the help of SNPs, leading to less conflicting information and potentially smaller loss of accuracy. We apologize that the explanations were missing from the manuscript and have added them lines 449-460 and 702-716.

A further argument is that if region and site epimutations occur at rates of at least two orders of magnitude difference, the inference results are better (and accurate) when the true rates are given. The reason is that one epimutational process overrides the other (see Supplementary Table 2). In that case one epimutation process is almost negligible and we fall back to results from Figure 5 or Supplementary Figure 6.

• As noted at 580, all of the added power from integrating SMPs/DMRs should come fromimproved estimation of recent TMRCAs. So, another way to study how much improvement there is would be to look at the true vs. estimated/posterior TMRCAs. Although I agree that demographic inference is ultimately the most relevant task, comparing TMRCA inference would eliminate other sources of differences between the methods (different optimization schemes, algorithmic/numerical quirks, and so forth). This could be a useful addition, and may also give you more insight into why the augmented SMC methods do worse in some cases.

Answer : We fully agree with reviewer 1. We have added a comparison in TMRCA inference as proof of principle between using or not using methylation sites. The results are written in Supplementary Table 7 and methodology is inspired by Schiffels 2014 and described at the end of the method section (line 894-907). Those results demonstrate the potential gain in accuracy when using methylation polymorphic. However, TMRCA (or ARG) inference is a very vast and complex subject in its own right. Therefore, we are developing a complete TMRCA/ARG inference investigation and an improve methodology than the one presented in this manuscript. To do so we are currently working on a manuscript focusing on this topic specifically. We hence consider further investigations of TMRCA/ARG inference beyond the scope of this current study.

• A general remark on the derivations in Section 2 of the supplement: I checked theseformulas as best I could. But a cleaner, less tedious way of calculating these probabilities would be to express the mutation processes as continuous time Markov chains. Then all that is needed is to specify the rate matrices; computing the emission probabilities needed for the SMC methods reduces to manipulating the results of some matrix exponentials. In fact, because the processes are noninteracting, the rate matrix decomposes into a Kronecker sum of the individual rate matrices for each process, which is very easy to code up. And this structure can be exploited when computing the matrix exponential, if speed is an issue.

Answer: We thank the reviewer for this very interesting suggestion! Unfortunately, it is a bit late to re-implement the algorithm and reshape the manuscript according to this suggestion. Speed is not yet an issue but will most likely become one in the future when integrating many different rates or when using a more complex SMC model. Hence, we added reviewer #1 suggestions to the discussion (line 648) and hope to be using it in our future projects.

• Most (all?) of the SNP-only SMC methods allow for binning together consecutiveobservations to cut down on computation time. I did not see binning mentioned anywhere, did you consider it? If the method really processes every site, how long does it take to run?

Answer: This is a very good question. We do the binning exactly as described in Mailund 2013 & Terhorst 2017, and added this information in the method section (lines 801-809). However, as described in Terhorst 2017, one can only bin observation of the same "type" (to compute the Baum-Welch algorithm). Therefore, the computation time gain by binning is reduced when different markers spread along the genome in high proportion. This is the approach we used throughout the study when facing multiple markers as it had the best speed performance. As for example, when the proportion of site with methylated information is 1% or less, computation time is only slightly affected (i.e. same order of magnitude).

However, the binning method presented in Mailund 2013 can be extended to observation of different types, but parameters need to be estimated through a full likelihood approach (as presented in Figure 2). In our study this approach did not have the best speed performance. However, as our study is the first of its kind, it remains sub-optimal for now. Hence, we did not further investigate the performance of our approach in presence of many multiple different genomic marker (e.g. 5 different markers each representing ~20% of the genome each). Currently, with SMC approaches a high proportion of sites contain the information "No SNPs", making the Baum welch algorithm described in Terhorst 2017 very efficient. But when further developing our theoretical approach, we expect that most of the sites in a genome analysis will contain some "information", which could render the full likelihood approach computationally more tractable.

• 486: The assumed site and region (de)methylation rates listed here are several OOMdifferent from what your method estimated (Supp. Tables 5-6). Yet, on simulated data your method is usually correct to within an order of magnitude (Supp. Table 4). How are we to interpret this much larger difference between the published estimates and yours? If the published estimates are not reliable, doesn't that call into question your interpretation of the blue line in Fig. 7 at 533?

Answer: We thank the reviewer for asking this question. We believe answering this question is indeed the most interesting aspect of our study. Beyond demographic inference, our study has indeed unveiled a discrepancy between rates inferred through biological experiment and our study through the use of SNPs and branch length. There are several reasons which could explained the discrepancy between both approaches:

• Firstly, our underlying HMM hypotheses are certainly violated. We ignoredpopulation structure, variation of mutations and recombination rate along the genome as well as the effect of selection. Hence, the branch lengths used for methylation rate estimations are to some extent inaccurate. We note that this is especially likely for the short branches of coalescent tree originating from background selection events in the coding regions and which are especially observable when using the methylation sites with a higher mutation rate than SNPs (Yao et al. 2023) at body methylated genes.

• Secondly, calling single methylation site polymorphism is not 100 % reliable. If theerror rate is 0.1%, as the study was conducted on ~10 generations a minimum epimutation rate of 10-4 is to be expected. However, because our approach works at the evolutionary time scale, we expect that it suffers less from this bias as the proportion of diversity originating from actual epimutations, and not SMP calling error, should be greater.

• Thirdly, as mentioned above, recovering the methylation status of a region is veryhard. Hence false region status inference could affect our inference accuracy as shown in Supplementary Figure 4.

• Lastly and most importantly, the reason behind this discrepancy is the modelling ofepimutation and methylation between sites and regions. As we discuss, the current combination of rates and models is still limited to describe the observed diversity along the genome (as we intend in SMC methods). This is in contrast to the recent study by Yao et al. where very few regions of polymorphic SMPs are chosen, which implicitly avoids the influence of the methylation region effect. A study just published by Biffra et al. (Cell reports 2023) also uses a functional model of methylation modelling using a mix of region and site epimutation, albeit not tuned for evolutionary analyses. Thus we suggest, in line with functional studies, that epimutations are not independent from the local methylation context and may tend to stabilize the methylation state of a region. Therefore, the estimated methylation rates show a discrepancy to the previously measured ones. Indeed, the biological experiment would reveal a fast epimutation rate because epimutations can actually be tracked at sites which can mutate, while region mutation rate is much slower. However, because the methylation state of a region is rather stable through time it would reduce the methylation diversity over long time scale, and these rates would differ between methylated or unmethylated regions (i.e. the methylation rate is higher in methylated regions). Our results are thus in agreement with the observation by Biffra et al. that region methylation modelling is needed to explain patterns of methylation across the genome.

To solve the discrepancy, one would need to develop a theoretical region + site epimutation model capable of describing the observed diversity at the evolutionary time scale (possibly based on the Biffra et al. model within an underlying population evolution model), and then use this model to reanalyse the sequence data from the biological experiment (i.e. in de Graaf et al. 2015 & Denkena et al. 2022) to re-estimate the methylation region sizes and epimutation rates.

Minor comments:

• 189: "SMCtheo" first occurs here, but it's not mentioned until 247 that this is the newmethod being presented.

Answer : Fixed

• 199: Are the estimates in this section from a single diploid sequence? Or is it n=5 (diploid) as mentioned in the earlier section?

Answer : Yes, those results were obtained with 5 diploid individuals. We added it in the Table 1 description.

• 336: I'm confused by the wording: it sounds like the test rejects the null if there is positivecorrelation in the methylation status across sites. But then, shouldn't 339 read "if the test is significant" (not non-significant)?

Answer : We apologize for the confusion and rewrote the sentence line 339-348, the choice of word was indeed misleading .

• Fig. 6: for some reason fewer simulations were run for 10Mb (panels C nad D) than for100Mb (A and B). Since it's very difficult to tell what's happening on average in the 10Mb case, I suggest running the same number of simulations.

Answer : Yes we understand your concern. Actually, the same number of simulations were run but we plotted only the first 3 runs as it was less visually confusing. We now have added the missing lines to the plot C and D.

Typos:

• 104: "or or"

• 292: build => built

• 388: fulfil

• 683: sample => samples

Answer : Many thanks to reviewer 1 for pointing out the typos. They are all now fixed.

Reviewer #2 (Recommendations For The Authors):

The authors may find some valuable information in Pisupati et al (2023) "On the causes of gene-body methylation variation in Arabidopsis thaliana" on interpreting epimutation rates.

Answer: Many thanks for the recommended manuscript. We add it to the cited literature as it strongly supports our use of heritability or methylation. We also added the recent Biffra et al. paper.

Reviewer #3 (Recommendations For The Authors):

There are many places throughout the manuscript with minor grammatical errors. Please review these. A few noted below as I read:

L104: extra "or"

L123: built not build

L 160 "relies" instead of "do rely"

L161 "events"

L 336 "from methylation data"

L 378 "exists"

L 379 "regions are on average shorter" instead of "there are shorter"

L 338 "a regional-level"

L 349 "," instead of "but"

L 394 DMRs

Table 1 legend: parentheses not brackets?

Answer : Many thanks to reviewer #3 for finding those mistakes. They are all now fixed.

I think a paragraph in the discussion of considerations of when to use this approach might be helpful to readers. Comparison to e.g. increased sample size in MSMC2, while not necessary, might be helpful here. It may often be the case that doubling the number of haplotypes with SNP data may be easier and cheaper estimating methylation accurately.

Answer : We discuss (lines 691-698) that our approach is always useful by design, but cannot always be used for the same purpose. If the evolutionary properties of the used marker used are not understood, we suggest that our approach can be used to investigate the marker heritability process through generations. This could help to correctly design experiments aiming to study the marker heritability through lineages. And if the properties of the marker are well understood and modelled, it can be integrated into the SMC framework to improve inference accuracy.

Other minor notes:

L 486 "known" is a stretch. empirically estimated seems appropriate.

Answer : Fixed

L 573 ARG? You are not estimating the full ARG here.

Answer : We apologize for the wrong choice of word and have rephrased the sentence.

Fig. 2 is not super useful and could be supplemental.

Answer : We moved Figure 2 to the appendix (now sup fig 1)

eLife assessment

This important study extends existing sequentially Markovian coalescent approaches to include the use of hypervariable loci such as epimutations. This is an intriguing addition and the authors provide solid validation of their methods via simulation and analysis of empirical data in Arabidopsis thaliana. Given the increasing availability of such data -- and thus the potential use of this approach -- there would be additional value in more extensive consideration of when and where these methods are best used.

Reviewer #1 (Public Review):

The authors developed an extension to the pairwise sequentially Markov coalecent model that allows to simultaneously analyze multiple types of polymorphism data. In this paper, they focus on SNPs and DNA methylation data. Since methylation markers mutate at a much faster rate than SNPs, this potentially gives the method better power to infer size history in the recent past. Additionally, they explored a model where there are both local and regional epimutational processes.

Integrating additional types of heritable markers into SMC is a nice idea which I like in principle. However, a major caveat to this approach seems to be a strong dependence on knowing the epimutation rate. In Fig. 6 it is seen that, when the epimutation rate is known, inferences do indeed look better; but this is not necessarily true when the rate is not known. (See also major comment #1 below about the interpretation of these plots.) A roughly similar pattern emerges in Supp. Figs. 4-7; in general, results when the rates have to be estimated don't seem that much better than when focusing on SNPs alone. This carries over to the real data analysis too: the interpretation in Fig. 7 appears to hinge on whether the rates are known or estimated, and the estimated rates differ by a large amount from earlier published ones.

Overall, this is an interesting research direction, and I think the method may hold more promise as we get more and better epigenetic data, and in particular better knowledge of the epigenetic mutational process. At the same time, I would be careful about placing too much emphasis on new findings that emerge solely by switching to SNP+SMP analysis.

Major comments:<br /> - For all of the simulated demographic inference results, only plots are presented. This allows for qualitative but not quantitative comparisons to be made across different methods. It is not easy to tell which result is actually better. For example, in Supp. Fig. 5, eSMC2 seems slightly better in the ancient past, and times the trough more effectively, while SMCm seems a bit better in the very recent past. For a more rigorous approach, it would be useful to have accompanying tables that measure e.g. mean-squared error (along with confidence intervals) for each of the different scenarios, similar to what is already done in Tables 1 and 2 for estimating $r$.

- 434: The discussion downplays the really odd result that inputting the true value of the mutation rate, in some cases, produces much worse estimates than when they are learned from data (SFig. 6)! I can't think of any reason why this should happen other than some sort of mathematical error or software bug. I strongly encourage the authors to pin down the cause of this puzzling behaviour. (Comment addressed in revision. Still, I find the explanation added at 449ff to be somewhat puzzling -- shouldn't the results of the regional HMM scan only improve if the true mutation rate is given?)

- As noted at 580, all of the added power from integrating SMPs/DMRs should come from improved estimation of recent TMRCAs. So, another way to study how much improvement there is would be to look at the true vs. estimated/posterior TMRCAs. Although I agree that demographic inference is ultimately the most relevant task, comparing TMRCA inference would eliminate other sources of differences between the methods (different optimization schemes, algorithmic/numerical quirks, and so forth). This could be a useful addition, and may also give you more insight into why the augmented SMC methods do worse in some cases. (Comment addressed in revision via Supp. Table 7.).

- A general remark on the derivations in Section 2 of the supplement: I checked these formulas as best I could. But a cleaner, less tedious way of calculating these probabilities would be to express the mutation processes as continuous time Markov chains. Then all that is needed is to specify the rate matrices; computing the emission probabilities needed for the SMC methods reduces to manipulating the results of some matrix exponentials. In fact, because the processes are noninteracting, the rate matrix decomposes into a Kronecker sum of the individual rate matrices for each process, which is very easy to code up. And this structure can be exploited when computing the matrix exponential, if speed is an issue.

- Most (all?) of the SNP-only SMC methods allow for binning together consecutive observations to cut down on computation time. I did not see binning mentioned anywhere, did you consider it? If the method really processes every site, how long does it take to run?

- 486: The assumed site and region (de)methylation rates listed here are several OOM different from what your method estimated (Supp. Tables 5-6). Yet, on simulated data your method is usually correct to within an order of magnitude (Supp. Table 4). How are we to interpret this much larger difference between the published estimates and yours? If the published estimates are not reliable, doesn't that call into question your interpretation of the blue line in Fig. 7 at 533? (Comment addressed in revision.)

Reviewer #2 (Public Review):

A limitation in using SNPs to understand recent histories of genomes is their low mutation frequency. Tellier et al. explore the possibility of adding hypermutable markers to SNP based methods for better resolution over short time frames. In particular, they hypothesize that epimutations (CG methylation and demethylation) could provide a useful marker for this purpose. Individual CGs in Arabidopsis tends to be either close to 100% methylated or close to 0%, and are inherited stably enough across generations that they can be treated as genetic markers. Small regions containing multiple CGs can also be treated as genetic markers based on their cumulative methylation level. In this manuscript, Tellier et al develop computational methods to use CG methylation as a hypermutable genetic marker and test them on theoretical and real data sets. They do this both for individual CGs and small regions. My review is limited to the simple question of whether using CG methylation for this purpose makes sense at a conceptual level, not at the level of evaluating specific details of the methods. I have a small concern in that it is not clear that CG methylation measurements are nearly as binary in other plants and other eukaryotes as they are in Arabidopsis. However, I see no reason why the concept of this work is not conceptually sound. Especially in the future as new sequencing technologies provide both base calling and methylating calling capabilities, using CG methylation in addition to SNPs could become a useful and feasible tool for population genetics in situations where SNPs are insufficient.

Reviewer #3 (Public Review):

I very much like this approach and the idea of incorporating hypervariable markers. The method is intriguing, and the ability to e.g. estimate recombination rates, the size of DMRs, etc. is a really nice plus. I am not able to comment on the details of the statistical inference, but from what I can evaluate it seems reasonable and in principle the inclusion of highly mutable sties is a nice advance. This is an exciting new avenue for thinking about inference from genomic data. I remain a bit concerned about how well this will work in systems where much less is understood about methylation,

The authors include some good caveats about applying this approach to other systems, but I think it would be helpful to empiricists outside of thaliana or perhaps mammalian systems to be given some indication of what to watch out for. In maize, for example, there is a non-bimodal distribution of CG methlyation (35% of sites are greater than 10% and less than 90%) but this may well be due to mapping issues. The authors solve many of the issues I had concerns with by using gene body methylation, but this is only briefly mentioned on line 659. I'm assuming the authors' hope is that this method will be widely used, and I think it worth providing some guidance to workers who might do so but who are not as familiar with these kind of data.

Author Response

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

Reviewer #1 (Public Review):

Summary:

This study examines the role of host blood meal source, temperature, and photoperiod on the reproductive traits of Cx. quinquefasciatus, an important vector of numerous pathogens of medical importance. The host use pattern of Cx. quinquefasciatus is interesting in that it feeds on birds during spring and shifts to feeding on mammals towards fall. Various hypotheses have been proposed to explain the seasonal shift in host use in this species but have provided limited evidence. This study examines whether the shifting of host classes from birds to mammals towards autumn offers any reproductive advantages to Cx. quinquefasciatus in terms of enhanced fecundity, fertility, and hatchability of the offspring. The authors found no evidence of this, suggesting that alternate mechanisms may drive the seasonal shift in host use in Cx. quinquefasciatus.

Strengths:

Host blood meal source, temperature, and photoperiod were all examined together.

Weaknesses: The study was conducted in laboratory conditions with a local population of Cx. quinquefasciatus from Argentina. I'm not sure if there is any evidence for a seasonal shift in the host use pattern in Cx. quinquefasciatus populations from the southern latitudes.

We agree on the reviewers observation about the evidence on seasonal shift in the host use pattern in Cx. quinquefasciatus populations from southern latitudes. We include a paragraph in the Introduction section regarding this. Unfortunately, studies conducted in South America to understand host use by Culex mosquitoes are very limited, and there are virtually no studies on the seasonal feeding pattern. In Argentina, there is some evidence (Stein et al., 2013, Beranek, 2019) regarding the seasonal change in host use by Culex species, including Cx. quinquefasciatus, where the inclusion of mammals during the autumn has been observed. As part of a comprehensive study on characterising bridge vectors for SLE and WN viruses, our research group is currently working on the molecular identification of blood meals from engorged females to gain deeper insights into the seasonal feeding pattern of Culex mosquitoes. While the seasonal change in host use by Culex quinquefasciatus has not been reported in Argentina so far, there has been an observed increase in reported cases of SLE virus in humans between summer and fall (Spinsanti et al., 2008). It is based on this evidence that we hypothesise there is a seasonal change in host use by Cx. quinquefasciatus, similar to what occurs in the United States. This is also considering that both countries (Argentina and the United States) have regions with similar climatic conditions (temperate climates with thermal and hydrological seasonality). Since we work on the same species and in a similar temperate climate regimen, we assumed there is a seasonal shift in the host use by this mosquito species.

Reviewer #1 (Recommendations for the authors):

Abstract

Line 23: fed on two different hosts.

Accepted as suggested.

I think the concluding statement should be rewritten to say that immediate reproductive outcomes do not explain the shift in host use pattern of Cx. quinquefasciatus mosquitoes from birds to mammals towards autumn.

Accepted as suggested.

Introduction

No comments.

Materials and Methods

Please mention sample sizes in the text as well (n = ?) for each treatment.

Accepted as suggested.

Page 99: ......C. quinquefasciatus, since C. pipiens and its hybrids are present as well in Cordoba.

Accepted as suggested.

Results – Line 146: subsequently instead of posteriorly

Accepted all changes as suggested.

Line 148: were counted instead of was counted.

Accepted all changes as suggested.

Line 160: Subsequently instead of posteriorly

Accepted all changes as suggested.

Line 171: on fertility

Accepted all changes as suggested.

Line 174: there was an interaction effect on…

Accepted all changes as suggested.

Line 175: there were no differences in the number of eggs

Accepted all changes as suggested.

Discussion

I think the first paragraph in the discussion section is redundant and should be deleted.

The whole discussion was rewritten to be focused on our aims and results.

Line 282: this sentence needs to be rewritten.

Accepted as suggested.

Line 299: at 28{degree sign}C

Line 300: at 30{degree sign}C

Sorry, but we are not sure about your comment here. We checked. Temperatures are written as stated, 28°C and 30°C.

Line 363: I think the authors need to discuss more about the bigger question they were addressing. I think that the discussion section can be strengthened greatly by elaborating on whether there is evidence for a seasonal shift in host use pattern in Cx. quinquefasciatus in the southern latitudes. If yes, what alternate mechanisms they believe could be driving the seasonal change in host use in this species in the southern latitudes now that they show the 'deriving reproductive advantages' hypothesis to be not true for those populations.

Thanks for this observation. We agree and so the Discussion section was restructured to align it with our results, as suggested.

Reviewer #2 (Public Review):

Summary:

Conceptually, this study is interesting and is the first attempt to account for the potentially interactive effects of seasonality and blood source on mosquito fitness, which the authors frame as a possible explanation for previously observed host-switching of Culex quinquefasciatus from birds to mammals in the fall. The authors hypothesize that if changes in fitness by blood source change between seasons, higher fitness in birds in the summer and on mammals in the autumn could drive observed host switching. To test this, the authors fed individuals from a colony of Cx. quinquefasciatus on chickens (bird model) and mice (mammal model) and subjected each of these two groups to two different environmental conditions reflecting the high and low temperatures and photoperiod experienced in summer and autumn in Córdoba, Argentina (aka seasonality). They measured fecundity, fertility, and hatchability over two gonotrophic cycles. The authors then used a generalized linear mixed model to evaluate the impact of host species, seasonality, and gonotrophic cycle on fecundity and fertility and a null model analysis via data randomization for hatchability. The authors were trying to test their hypothesis by determining whether there was an interactive effect of season and host species on mosquito fitness. This is an interesting hypothesis; if it had been supported, it would provide support for a new mechanism driving host switching. While the authors did report an interactive impact of seasonality and host species, the directionality of the effect was the opposite of that hypothesized. While this finding is interesting and worth reporting, there are significant issues with the experimental design and the conclusions that are drawn from the results, which are described below. These issues should be addressed to make the findings trustworthy.

Strengths:

(1) Using a combination of laboratory feedings and incubators to simulate seasonal environmental conditions is a good, controlled way to assess the potentially interactive impact of host species and seasonality on the fitness of Culex quinquefasciatus in the lab.

(2) The driving hypothesis is an interesting and creative way to think about a potential driver of host switching observed in the field.

Weaknesses:

(1) There is no replication built into this study. Egg lay is a highly variable trait, even within treatments, so it is important to see replication of the effects of treatment across multiple discrete replicates. It is standard practice to replicate mosquito fitness experiments for this reason. Furthermore, the sample size was particularly small for some groups (e.g. 15 egg rafts for the second gonotrophic cycle of mice in the autumn, which was the only group for which a decrease in fecundity and fertility was detected between 1st and 2nd gonotrophic cycles). Replicates also allow investigators to change around other variables that might impact the results for unknown reasons; for example, the incubators used for fall/summer conditions can be swapped, ensuring that the observed effects are not artefacts of other differences between treatments. While most groups had robust sample sizes, I do not trust the replicability of the results without experimental replication within the study.

We agree egg lay is a variable trait and so we consider high numbers of mosquitoes and egg lay during experiments compared to our studies of the same topics. Evaluating variables such as fecundity, fertility, or other types of variables (collectively referred to as "life tables") is a challenging issue that depends on several intrinsic and extrinsic factors. Because all of this, in some experiments, sample sizes might not be very large, and in several articles, lower sample sizes could be found. For instance, in Richards et al. (2012), for Culex quinquefasciatus, during the second gonotrophic cycle, some experiments had 13 or even 6 egg rafts. For species like Aedes aegypti, the sample size for life table analysis is also usually small. As an example, Muttis et al. (2018) reported between 1 and 4 engorged females (without replicates). In addition, small sample size would be a problem if we would not have obtained any effect, which is not the case due to the fact that we were interested in finding an effect, regardless of the effect size. Because of this, we do find our sample sizes quite robust for our results.

Regarding the need to repeat the experiments in order to give more robustness to the study we also agree. However, after a review of the literature (articles cited in the original manuscript), it is apparent that similar experiments are not frequently repeated as such. Examples of this are the studies of Richards et al. (2012), Demirci et al. (2014) or Telang & Skinner (2019), which even they manipulate several cages at a time as “replicates”, they are not true replicates because they summarise and manipulate all data together, and do not repeat the experiment several times. We see these “replicates” as a way of getting a greater N.

As was stated by the reviewer, repetition is a resource and time-consuming activity that we are not able to do. Replicating the experiment poses a significant time and resources challenge. The original experiment took over three months to complete, and it is anticipated that a similar timeframe would be necessary for each replication (6 months in total considering two more replicates). Given our existing commitments and obligations, dedicating such an extensive period solely to this would impede progress on other crucial projects and responsibilities.

Given the limitations of resources and time and the infrequent use of experimental replication in this type of studies, we performed a simulation-based analysis via a Monte Carlo approach. This approach involved generating synthetic data that mimics the expected characteristics of the original experiment and subsequently subjecting it to the same analysis routine. The main goal of this simulation was to evaluate the potential spuriousness and randomness of the results that might arise due to the experimental conditions. So, evaluating the robustness and confidence of our results and data.

(2) Considering the hypothesis is driven by the host switching observed in the field, this phenomenon is discussed very little. I do not believe Cx. quinquefasciatus host switching has been observed in Argentina, only in the northern hemisphere, so it is possible that the species could have an entirely different ecology in Argentina. It would have been helpful to conduct a blood meal analysis prior to this experiment to determine whether using an Argentinian population was appropriate to assess this question. If the Argentinian populations don't experience host switching, then an Argentinian colony would not be the appropriate colony to use to assess this question. Given that this experiment has already been conducted with this population, this possibility should at least be acknowledged in the discussion. Or if a study showing host switching in Argentina has been conducted, it would be helpful to highlight this in the introduction and discussion.

Thanks for this observation. We agree. However, we conducted the experiment beside host use data from Argentina since we used the mosquito species, and the centre region of Argentina (Córdoba) has a similar temperate weather regimen that those observed in the east coast of US.

We are aware that few studies regarding host shifting in South America are available, some such that those conducted by Stein et al. (2013) and Beranek (2019) reported a moderate host switch for Culex quinquefasciatus in Argentina. We have already performed a study about seasonal host feeding patterns for this species. However, even though there are few studies regarding host shifting, our hypothesis is based mainly in the seasonality of human cases of WNV and SLEV, a pattern that has been demonstrated for our region, see for example the study of Spinsanti et al. (2008).

We include a new paragraph in the Introduction and Discussion sections. Please see answers Reviewer #1.

(3) The impacts of certain experimental design decisions are not acknowledged in the manuscript and warrant discussion. For example, the larvae were reared under the same conditions to ensure adults of similar sizes and development timing, but this also prevents mechanisms of action that could occur as a result of seasonality experienced by mothers, eggs, and larvae.

We understand the confusion that may have arisen due to a lack of further details in the methodology. If we are not mistaken, you are referring to our oversight regarding the consideration of carry-over effects of larvae rearing that could potentially impact reproductive traits. When investigating the effects of temperature or other environmental factors on reproductive traits, it is possible to acclimate either larvae or adults. This is due to the significant phenotypic plasticity that mosquitoes exhibit throughout their entire ontogenetic cycle. In our study, we followed an approach similar to that of other authors where the adults are exposed to experimental conditions (temperature and photoperiod). For a similar approach you can refer to the studies conducted by Ferguson et al. (2018) for Cx. pipiens, Garcia Garcia & Londoño Benavides (2007) for Cx. quinquefasciatus or Christiansen-Jucht et al. (2014, 2015) for Anopheles gambiae.

(4) There are aspects of the data analysis that are not fully explained and should be further clarified. For example, there is no explanation of how the levels of categorical variables were compared.

The methodology and statistical analysis were expanded for a better understanding.

(5) The results show the opposite trend as was predicted by the authors based on observed feeding switches from birds to mammals in the autumn. However, they only state this once at the end of the discussion and never address why they might have observed the opposite trend as was hypothesized.

The discussion was restructured to focus on our results and our model.

(6) Generally speaking, the discussion has information that isn't directly related to the results and/or is too detailed in certain parts. Meanwhile, it doesn't dig into the meaning of the results or the ways in which the experimental design could have influenced results.

As mentioned above, the discussion was restructured to reflect our findings. We also included the effect that our design might have influenced our results. However, as stated above we do not fully agree that the design is inadequate for our analysis, we performed standard protocols followed by other researchers and studies in this research field.

(7) Beyond the issue of lack of replication limiting trust in the conclusions in general, there is one conclusion reached at the end of the discussion that would not be supported, even if additional replicates are conducted. The results do not show that physiological changes in mosquitoes trigger the selection of new hosts. Host selection is never measured, so this claim cannot be made. The results don't even suggest that fitness might trigger selection because the results show that physiological changes are in the opposite direction as what would be hypothesized to produce observed host switches. Similarly, the last sentence of the abstract is not supported by the results.

We agree with this observation. However, we did not evaluate the impact of fitness on host selection in this study. Instead, we aimed to investigate the potential influence of seasonality on mosquito fitness as a potential trigger for a shift in host selection. We agree that we have incorrectly used the term “host selection” when we should actually be discussing “host use change”. Our results indicate a seasonal alteration in mosquito fitness in response to temperature and photoperiod changes. Building upon this observation, we re-discussed our hypothesis and theoretical model to explain this seasonal shift in host use.

(8) Throughout the manuscript, there are grammatical errors that make it difficult to understand certain sentences, especially for the results.

All English grammar and writing of the manuscript was revised and corrected to be easily understood.

This study is driven by an interesting question and has the potential to be a valuable contribution to the literature.

Reviewer #2 (Recommendations for The Authors):

I hope that the authors will consider the suggested revisions and experimental replication to improve the quality of the study and paper.

This study tests a very interesting hypothesis. I understand that additional replicates are difficult to conduct, but I do believe that fitness studies absolutely require experimental replicates. Unless you are able to replicate the observed effects, I personally would not trust the results of this study. I hope that you will consider conducting replicates so that this important question can be answered in a more robust manner. Below, I expand upon some additional points in the public review and also provide more specific suggestions. I provided some copy-editing feedback, but was not able to point out all grammatical mistakes. I suggest that you use ChatGPT to help you edit the English. For example, you can feed ChatGPT your MS and ask it to bold the grammatical errors or you can ask it to edit grammatical errors and bold the sections that were edited. I understand that writing in a second language is very difficult (from personal experience!), so I view ChatGPT as a great tool to help even the playing field for publishing. Below are line item suggestions. Apologies that wording is curt, I was trying to be efficient in writing.

20-21: I suggest that you emphasize that you are investigating the interactive effect.

Accepted as suggested.

22: they weren't "reared" (from larvae) in different conditions, they were "maintained" as adults

Accepted as suggested.

26-27: increased/decreased is a bit misleading since you did not evaluate these groups sequentially in time. It might be more accurate to describe it as less than/greater than. Also, if you say increased/decreased or less than/greater than, you should always say what you are comparing to. The same applies throughout the MS.

Accepted as suggested.

29-30: "finding the" is not correct here; could be "with the lowest..."

Accepted as suggested.

34-36: I do not think that your results suggest this, even if you were to replicate the results of this experiment. You haven't shown metabolic changes.

We understand the point. Accepted as suggested.

42-44: "one of the main responsible" should be "one of the main species responsible..."

Accepted as suggested.

48: I think that "host preference" is better than selection here; -philic denotes preference

Accepted as suggested.

50: "Moreover" isn't the correct transition word here

Accepted as suggested.

57: "could" isn't correct here; consider saying "... species sometimes feed primarily on mammal hosts, including humans, in certain situations."

Accepted as suggested.

58: Different isn't correct word here

Accepted as suggested.

60: delete "feeding"

Accepted as suggested.

66-68: I am not familiar with any blood meal analysis studies in the southern hemisphere that show host switching for Culex species between summer and autumn. If this hasn't been shown, then this critique of the host migration hypothesis doesn't make sense.

There are some studies pointing this out (Stein et al., 2013, Beranek 2019), and unpublished data from us). However, our hypothesis has supported by epidemiological data observed in human population which indicate a seasonal activity pattern. It was explained in depth in the Introduction section.

68: ensures is not the right word; I suggest "suggests"

Accepted as suggested.

68-70: this explanation isn't clear to me; please revise

It will be revised. Accepted as suggested.

70: change cares to care

Accepted as suggested.

76-77: can you explain how they were not supported by the data for the benefit of those who are not familiar with these papers please?

Accepted as suggested.

87-89: I suggest the following wording: "In the autumn, we expect a greater number of eggs (fecundity) and larvae (fertility) in mosquitoes after feeding on a mammal host compared to an avian host, and the opposite relationship in the summer."

Accepted as suggested.

99: edit for grammar

Accepted as suggested.

102: suggest: "...offered a blood meal from a restrained chicken twice a month"

Accepted as suggested.

107: powder

Accepted as suggested.

108: inbred? Is this the term you meant to use?

Changed as suggested.

109: "several" cannot be used to describe 20 generations; suggest using "over twenty generations"; also, it would be good to acknowledge in your discussion that lab adaptation could force evolution, especially since mosquitoes are kept at constant temperatures and fed with certain hosts (with easy access) in the lab. Also, it would be good to know when the experiments were conducted to know the lapse of time between the creation of the colony and the experiments.

Accepted as suggested.

110-111: Does humidity vary between summer and fall in Córdoba? If so, I suggest acknowledging in the discussion that if humidity differences are involved in a potential interaction between host species and seasonality, then this would not have been captured by your experimental design.

Several variables change during seasons. We were interested in capturing the effects of temperature and photoperiod, since humidity is a variable difficult to control.

113-116: I suggest combining into one sentence to make more concise.

Accepted as suggested.

135: You might be obscuring the true impact of seasonality by rearing the larvae under the same conditions. There may be signals that mothers/eggs/larvae receive that influence their behavior (e.g. I believe this is the case for diapause), so this limitation should also be acknowledged. I understand why you decided to do this to control for development time and size, but it is something that should be considered in the discussion.

As it was explained above, Cx. quinquefasciatus do not suffer diapause in our country. Maintaining mosquitoes from adults was an approach selected by us based on other studies.

138: edit: "with cotton pads soaked in... on plastic..."; what is plastic glass? Do you mean plastic dishes?

Accepted as suggested.

141: here and throughout paragraph, full should be "fully"

Accepted as suggested.

144: located should be "placed"

Accepted as suggested.

147: suggest editing to "at which point, they were fixed with 1 mL of 96% ethanol and the number of L1 larvae per raft was counted."

Accepted as suggested.

154-155: edit for grammar

Accepted as suggested.

157: Your GLM explanation doesn't say anything about how you made pairwise comparisons between your levels; did you use emmeans?

This revised version includes a more detailed methodology and statistical analysis. Accepted as suggested.

158-160: I don't understand why you took this approach - it seems strange to me to use this analysis, but I am not familiar with it, so it might be that I lack the knowledge to be able to adequately evaluate. Please provide more explanation so that readers can better understand this analysis. A citation for this kind of application of the analysis would be helpful.

It was changed to be in accordance with the remaining analyses.

173: replace neither with either

Accepted as suggested.

174: this applies throughout; edit to : "An interaction effect was observed..."

Accepted as suggested.

175: "it was not found" is grammatically incorrect; instead : "We did not find ..." or "no differences in... were detected", etc

Accepted as suggested.

183: "it was detected" is grammatically incorrect

Accepted as suggested.

185-186: "being this treatment... in terms of fitness": I do not understand what this means. Please rephrase

Accepted as suggested.

170-199: you should provide the effect sizes and p values in text and/or in the figure for the pairwise comparisons

Accepted as suggested.

193-196. These two sentences are confusing and I am not sure what you mean, especially in the first sentence.

It was rewritten. Accepted as suggested.

Figure 1: This figure is great and easy to read and interpret! Thank you for the comment! 218-219: it is important to state which mosquito species you are referring to here.

Accepted as suggested.

226-227: you definitely should acknowledge the small sample size here.

Considered.

227: "it was observed" should be "We observed" or "A greater hatching rate.... was observed."

Accepted as suggested.

228-229: is the result really comparable even though you took very different approaches to the analysis for these outcomes?

Changed to be comparable.

230-278: the discussion of these hypotheses is too long and detailed, especially since the comparison of mouse vs chicken wasn't your main question; you really wanted to understand this in the context of seasonality. I suggest cutting this down a lot and making room to dig into your results more, and also to discuss the potential impacts of your experimental design/limitations on the results.

Discussion was changed to focus on our results and model. Accepted as suggested.

281: Hoffman is an old citation; I suggest you cite a modern review.

Accepted as suggested. We deleted it due to the re-writing of the manuscript.

282: "It can be recognise".. I am not sure what you are trying to say here

Accepted as suggested.

1. After the first time you write a species name, you can abbreviate the genus in all future mentions unless it is at the beginning of a sentence.

Accepted as suggested.

303-305: Revise this sentence. E.g "Fewer studies are available regarding photoperiod and show mixed results; Mogi (1992) found that mid and long day lengths induced greater fecundity while Costanzo et al. (2015) did not find differences in fecundity by day length."

Accepted as suggested.

315-316: typically, unpublished data shouldn't be referenced; I'm not sure if eLife has a policy on this.

We will check this with eLife guidelines. However, since the lack of evidence on this pattern we consider important to include this unpublished data.

316: Aegypti should be lowercase

Accepted as suggested.

328-330: This sentence is redundant with the first sentence of the paragraph

Accepted as suggested.

321-336: You never reintroduced your hypothesis in your discussion. I suggest that you center your whole discussion more directly around the hypothesis that motivated the study. If you decide not to restructure your discussion, you should at least reintroduce your hypothesis here and discuss how your results do not support the hypothesis.

Accepted as suggested.

337-348: This paragraph is a bit confusing as you jump between fertility and hatchability

Accepted as suggested.

353: is viral transmission the right word to use here? I think you might mean bridge vector transmission to humans specifically?

Accepted as suggested.

357: you say "neither" but never define which traits you are referring to

Accepted as suggested.

361: I suggest "two variables previously analyzed separately..."

Accepted as suggested.

General: There is no statement about the availability of data; it is eLife policy to require all data to be publicly available. Also, it would be helpful to share your code to help understand how you conducted pairwise comparisons, etc.

In the submission it was not mentioned anything about data availability. However, all data and scripts will be uploaded with the VOR if it is required.

Recommendations for the authors:

I found your study interesting and potentially promising. However, there are some fundamental problems with the study design and the hypothesis, including:

<(1) Seasonality simulation - Seasonality is strongly associated with time, so it is unusual to simulate seasonal factors without accounting for time. The actual factors associated with seasonal change in reproductive output may be neither a difference in host blood meal nor temperature and photoperiod. It is therefore, odd to reduce seasonality to a difference in photoperiod and temperature in summer and autumn without even mentioning the time of year when the experiment was carried (except for the mention of February as the time the stock samples were collected from the wild).

The temperature and photoperiod settings are established according to a representative day in both autumn and summer. To determine these settings, we utilized climate data spanning a 3-year period (2020-2022), encompassing the most frequently occurring temperatures and day lengths. The weather conditions remained notably consistent throughout this time frame, which is why the specific year was not mentioned. Moreover, including the year in laboratory experiment details is uncommon, as evident in various papers. This practice can be corroborated by referring to multiple sources (cited in the original manuscript). We mention this in the new version.

(2) Hypothesis - While the hypothesis alludes to the 'reason' for seasonal host shift, the prediction is on the outcome of the interaction between blood meal type and season.

It might be nicer to frame your hypothesis to be consistent with the aim, which is, testing the partial contributions of blood meal type, versus photoperiod and temperature to seasonal change in the reproductive output of Culex quinquefasciatus. A hypothesis like that can be accompanied by alternative predictions according to the expected individual and interactive effects of both factors.

It was rewritten in the revised version to be consistent with our predictions and findings.

Blood meal type, temperature, and photoperiod are all components of seasonality, so the strength of the study is its potential to decouple the effect of blood meal type from that of temperature and photoperiod on the seasonal reproductive output of Culex quinquefasciatus by comparing the two blood meal types under simulated summer and winter conditions. Ideally, this should have been over a natural summer and winter because a natural time difference captures the effect of other seasonal factors other than temperature and photoperiod.

Furthermore, the hypothesis stemmed from field observations, while the study itself was conducted under laboratory conditions using a local population of Culex quinquefasciatus from Argentina. It remains uncertain whether there is supporting evidence for a seasonal shift in host usage in Culex quinquefasciatus from the stock population. Discussing the field observations within the stock population would provide valuable insights.

It was considered in the new version.