eLife Assessment

This important work employed a recent, functional muscle network analysis for evaluating rehabilitation outcomes in post-stroke patients. While the research direction is relevant and suggests the need for further investigation, the strength of evidence supporting the claims is incomplete. Muscle interactions can serve as biomarkers, but improvements in function are not directly demonstrated, and the method's robustness is not benchmarked against existing approaches.

Reviewer #1 (Public review):

Summary:

This study addresses an important clinical challenge by proposing muscle network analysis as a tool to evaluate rehabilitation outcomes. The research direction is relevant, and the findings suggest further research. The strength of evidence supporting the claims is, however, limited: the improvements in function are not directly demonstrated, the robustness of the method is not benchmarked against already published approaches, and key terminology is not clearly defined, which reduces the clarity and impact of the work.

Comments:

There are several aspects of the current work that require clarification and improvement, both from a methodological and a conceptual standpoint.

First, the actual improvements associated with the rehabilitation protocol remain unclear. While the authors report certain quantitative metrics, the study lacks more direct evidence of functional gains. Typically, rehabilitation interventions are strengthened by complementary material (e.g., videos or case examples) that clearly demonstrate improvements in activities of daily living. Including such evidence would make the findings more compelling.

Second, the claim that the proposed muscle network analysis is robust is not sufficiently substantiated. The method is introduced without adequate reference to, or comparison with, the extensive literature that has proposed alternative metrics. It is also not evident whether a simpler analysis (e.g., EMG amplitude) might produce similar results. To highlight the added value of the proposed method, it would be important to benchmark it against established approaches. This would help clarify its specific advantages and potential applications. Moreover, several studies have shown very good outcomes when using AI and latent manifold analyses in patients with neural lesions. Interpreting the latent space appears even easier than interpreting muscle networks, as the manifolds provide a simple encoding-decoding representation of what the patient can still perform and what they can no longer do.

Third, the terminology used throughout the manuscript is sometimes ambiguous. A key example is the distinction made between "functional" and "redundant" synergies. The abstract states: "Notably, we identified a shift from redundancy to synergy in muscle coordination as a hallmark of effective rehabilitation-a transformation supported by a more precise quantification of treatment outcomes."

However, in motor control research, redundancy is not typically seen as maladaptive. Rather, it is a fundamental property of the CNS, allowing the same motor task to be achieved through different patterns of muscle activity (e.g., alternative motor unit recruitment strategies). This redundancy provides flexibility and robustness, particularly under fatiguing conditions, where new synergies often emerge. Several studies have emphasized this adaptive role of redundancy. Thus, if the authors intend to use "redundancy" differently, it is essential to define the term explicitly and justify its use to avoid misinterpretation.

Reviewer #2 (Public review):

Summary:

This study analyzes muscle interactions in post-stroke patients undergoing rehabilitation, using information-theoretic and network analysis tools applied to sEMG signals with task performance measurements. The authors identified patterns of muscle interaction that correlate well with therapeutic measures and could potentially be used to stratify patients and better evaluate the effectiveness of rehabilitation.

However, I found that the Methods and Materials section, as it stands, lacks sufficient detail and clarity for me to fully understand and evaluate the quality of the method. Below, I outline my main points of concern, which I hope the authors will address in a revision to improve the quality of the Methods section. I would also like to note that the methods appear to be largely based on a previous paper by the authors (O'Reilly & Delis, 2024), but I was unable to resolve my questions after consulting that work.

I understand the general procedure of the method to be: (1) defining a connectivity matrix, (2) refining that matrix using network analysis methods, and (3) applying a lower-dimensional decomposition to the refined matrix, which defines the sub-component of muscle interaction. However, there are a few steps not fully explained in the text.

(1) The muscle network is defined as the connectivity matrix A. Is each entry in A defined by the co-information? Is this quantity estimated for each time point of the sEMG signal and task variable? Given that there are only 10 repetitions of the measurement for each task, I do not fully understand how this is sufficient for estimating a quantity involving mutual information.

In the previous paper (O'Reilly & Delis, 2024), the authors initially defined the co-information (Equation 1.3) but then referred to mutual information (MI) in the subsequent text, which I found confusing. In addition, while the matrix A is symmetrical, it should not be orthogonal (the authors wrote AᵀA = I) unless some additional constraint was imposed?

(2) The authors should clarify what the following statement means: "Where a muscle interaction was determined to be net redundant/synergistic, their corresponding network edge in the other muscle network was set to zero."

(3) It should be clarified what the 'm' values are in Equation 1.1. Are these the co-information values after the sparsification and applying the Louvain algorithm to the matrix 'A'? Furthermore, since each task will yield a different co-information value, how is the information from different tasks (r) being combined here?

(4) In general, I recommend improving the clarity of the Methods section, particularly by being more precise in defining the quantities that are being calculated. For example, the adjacency matrix should be defined clearly using co-information at the beginning, and explain how it is changed/used throughout the rest of the section.

(5) In the previous paper (O'Reilly & Delis, 2024), the authors applied a tensor decomposition to the interaction matrix and extracted both the spatial and temporal factors. In the current work, the authors simply concatenated the temporal signals and only chose to extract the spatial mode instead. The authors should clarify this choice.

eLife Assessment

The authors collected time-course RNA-seq data from four tree species in natural environments and analyzed seasonal patterns of gene expression. This fundamental study substantially advances our understanding of how seasonal environments shape gene expression. The evolutionary effects of seasonal environments on gene expression are rarely studied at this scale and the dataset is extensive. The evidence supporting the conclusions is compelling, with caveats and limitations clearly described. The work will be of broad interest to colleagues studying evolution and gene expression.

Reviewer #2 (Public review):

This study investigates how seasonal environments shape the evolution of gene expression by analyzing two-year time-series transcriptomes from leaves and buds of four Fagaceae tree species. The revised manuscript incorporates additional data and analyses that directly address earlier concerns about sampling design and environmental variation, thereby strengthening the robustness of the conclusions.

The major strengths of this work are the scale and quality of the dataset, the integration of genome assemblies with time-series transcriptomics, and the careful analyses showing that winter bud expression is strongly conserved across species. The additional samples and re-analyses demonstrate convincingly that these results are not artifacts of sampling period or site differences. The study also links gene expression dynamics to phenological observations and frames its findings in relation to broader evolutionary concepts such as phenological synchrony and the developmental hourglass model.

Remaining limitations include the absence of direct mechanistic analyses of cis-regulatory and chromatin-level processes, the relatively coarse resolution of phenological trait measurements, and the weak association between seasonal expression divergence and sequence divergence. Importantly, these limitations are now explicitly acknowledged in the revised Discussion and framed as directions for future research.

Overall, the authors have substantially achieved their aims. This revised version represents a robust and convincing contribution that provides valuable data resources and conceptual insights into how seasonal environments constrain and shape gene expression. It will be of interest not only to evolutionary biologists and plant scientists, but also to researchers considering the broader role of environmental cycles in gene regulatory evolution.

Author response:

The following is the authors’ response to the original reviews

Public Reviews

Reviewer #1 (Public review):

Summary:

The authors performed genome assemblies for two Fagaceae species and collected transcriptome data from four natural tree species every month over two years. They identified seasonal gene expression patterns and further analyzed species-specific differences.

Strengths:

The study of gene expression patterns in natural environments, as opposed to controlled chambers, is gaining increasing attention. The authors collected RNA-seq data monthly for two years from four tree species and analyzed seasonal expression patterns. The data are novel. The authors could revise the manuscript to emphasize seasonal expression patterns in three species (with one additional species having more limited data). Furthermore, the chromosome-scale genome assemblies for the two Fagaceae species represent valuable resources, although the authors did not cite existing assemblies from closely related species.

Thank you for your careful assessment of our manuscript.

Weaknesses:

Comment; The study design has a fundamental flaw regarding the evaluation of genetic or evolutionary effects. As a basic principle in biology, phenotypes, including gene expression levels, are influenced by genetics, environmental factors, and their interaction. This principle is well-established in quantitative genetics.

In this study, the four species were sampled from three different sites (see Materials and Methods, lines 543-546), and additionally, two species were sampled from 2019-2021, while the other two were sampled from 2021-2023 (see Figure S2). This critical detail should be clearly described in the Results and Materials and Methods. Due to these variations in sampling sites and periods, environmental conditions are not uniform across species.

Even in studies conducted in natural environments, there are ways to design experiments that allow genetic effects to be evaluated. For example, by studying co-occurring species, or through transplant experiments, or in common gardens. To illustrate the issue, imagine an experiment where clones of a single species were sampled from three sites and two time periods, similar to the current design. RNA-seq analysis would likely detect differences that could qualitatively resemble those reported in this manuscript.

One example is in line 197, where genus-specific expression patterns are mentioned. While it may be true that the authors' conclusions (e.g., winter synchronization, phylogenetic constraints) reflect real biological trends, these conclusions are also predictable even without empirical data, and the current dataset does not provide quantitative support.

If the authors can present a valid method to disentangle genetic and environmental effects from their dataset, that would significantly strengthen the manuscript. However, I do not believe the current study design is suitable for this purpose.

Unless these issues are addressed, the use of the term "evolution" is inappropriate in this context. The title should be revised, and the result sections starting from "Peak months distribution..." should be either removed or fundamentally revised. The entire Discussion section, which is based on evolutionary interpretation, should be deleted in its current form.

If the authors still wish to explore genetic or evolutionary analyses, the pair of L. edulis and L. glaber, which were sampled at the same site and over the same period, might be used to analyze "seasonal gene expression divergence in relation to sequence divergence." Nevertheless, the manuscript would benefit from focusing on seasonal expression patterns without framing the study in evolutionary terms.

We sincerely thank the reviewer for the detailed and thoughtful comments. We fully recognize the importance of carefully distinguishing genetic and environmental contributions in transcriptomic studies, particularly when addressing evolutionary questions. The reviewer identified two major concerns regarding our study design: (1) the use of different monitoring periods across species, and (2) the use of samples collected from different study sites. We addressed both concerns with additional analyses using 112 new samples and now present new evidence that supports the robustness of our conclusions.

(1) Monitoring period variation does not bias our conclusions<br /> To address concerns about the differing monitoring periods, we added new RNA-seq data (42 samples each for bud and leaf samples for L. glaber and 14 samples each for bud and leaf samples for _L. eduli_s) collected from November 2021 to November 2022, enabling direct comparison across species within a consistent timeframe. Hierarchical clustering of this expanded dataset (Fig. S6) yielded results consistent with our original findings: winter-collected samples cluster together regardless of species identity. This strongly supports our conclusion that the seasonal synchrony observed in winter is not an artifact of the monitoring period and demonstrates the robustness of our conclusions across datasets.

(2) Site variation is limited and does not confound our findings<br /> Although the study included three sites, two of them (Imajuku and Ito Campus) are only 7.3 km apart, share nearly identical temperature profiles (see Fig. S2), and are located at the edge of similar evergreen broadleaf forests. Only Q. acuta was sampled from a higher-altitude, cooler site. To assess whether the higher elevation site of Q. acuta introduced confounding environmental effects, we reanalyzed the data after excluding this species. Hierarchical clustering still revealed that winter bud samples formed a distinct cluster regardless of species identity (Fig. S7), consistent with our original finding.

Furthermore, we recalculated the molecular phenology divergence index D (Fig. 4C) and the interspecific Pearson’s correlation coefficients (Fig. 5A) without including Q. acuta. These analyses produced results that were similar to those obtained from the full dataset (Fig. S12; Fig. S14), indicating that the observed patterns are not driven by environmental differences associated with elevation.

(3) Justification for our approach in natural systems<br /> We agree with the reviewer that experimental approaches such as common gardens, reciprocal transplants, and the use of co-occurring species are valuable for disentangling genetic and environmental effects. In fact, we have previously implemented such designs in studies using the perennial herb Arabidopsis halleri (Komoto et al., 2022, https://doi.org/10.1111/pce.14716) and clonal Someiyoshino cherry trees (Miyawaki-Kuwakado et al., 2024, https://doi.org/10.1002/ppp3.10548) to examine environmental effects on gene expression. However, extending these approaches to long-lived tree species in diverse natural ecosystems poses significant logistical and biological challenges. In this study, we addressed this limitation by including three co-occurring species at the same site, which allowed us to evaluate interspecific differences under comparable environmental conditions. Importantly, even when we limited our analyses to these co-occurring species, the results remained consistent, indicating that the observed variation in transcriptomic profiles cannot be attributed to environmental factors alone and likely reflects underlying genetic influences.

Accordingly, we added four new figures (Fig. S6, Fig. S7, Fig. S12 and Fig. S14) and revised the manuscript to clarify the limitations and strengths of our design, to tone down the evolutionary claims where appropriate, and to more explicitly define the scope of our conclusions in light of the data. We hope that these efforts sufficiently address the reviewer’s concerns and strengthen the manuscript.

To better support the seasonal expression analysis, the early RNA-seq analysis sections should be strengthened. There is little discussion of biological replicate variation or variation among branches of the same individual. These could be important factors to analyze. In line 137, the mapping rate for two species is mentioned, but the rates for each species should be clearly reported. One RNA-seq dataset is based on a species different from the reference genome, so a lower mapping rate is expected. While this likely does not hinder downstream analysis, quantification is important.

We thank the reviewer 1 for the helpful comment. To evaluate the variation among biological replicates, we compared the expression level of each gene across different individuals. We observed high correlation between each pair of individuals (Q. glauca (n=3): an average correlation coefficient r = 0.947; Q. acuta (n=3): r = 0.948; L. glaber (n=3): r = 0.948)). This result suggests that the seasonal gene expression pattern is highly synchronized across individuals within the same species. We mentioned this point in the Result section in the revised manuscript. We also calculated the mean mapping rates for each species. As the reviewer expected, the mapping rate was slightly lower in Q. acuta (88.6 ± 2.3%) and L. glaber (84.3 ± 5.4%), whose RNA-Seq data were mapped to reference genomes of related but different species, compared to that in Q. glauca (92.6 ± 2.2%) and L. edulis (89.3 ± 2.7%). However, we minimized the impact of these differences on downstream analysis. These details have been included in the revised main text.

In Figures 2A and 2B, clustering is used to support several points discussed in the Results section (e.g., lines 175-177). However, clustering is primarily a visualization method or a hypothesis-generating tool; it cannot serve as a statistical test. Stronger conclusions would require further statistical testing.

We thank the reviewer for the helpful comment. As noted, we acknowledge that hierarchical clustering (Fig. 2A) is primarily a visualization and hypothesis-generating method. To assess the biological relevance of the clusters identified, we conducted a Mann-Whitney U test or the Steel-Dwass test to evaluate whether the environmental temperatures at the time of sample collection differed significantly among the clusters. This analysis (Fig. 2B) revealed statistically significant differences in temperature in the cluster B3 (p < 0.01), indicating that the gene expression clusters are associated with seasonal thermal variation. These results support the interpretation that the clusters reflect coordinated transcriptional responses to environmental temperature. We revised the Results section to clarify this point.

The quality of the genome assemblies appears adequate, but related assemblies should be cited and discussed. Several assemblies of Fagaceae species already exist, including Quercus mongolica (Ai et al., Mol Ecol Res, 2022), Q. gilva (Front Plant Sci, 2022), and Fagus sylvatica (GigaScience, 2018), among others. Is there any novelty here? Can you compare your results with these existing assemblies?

We agree that genome assemblies of Fagaceae species are becoming increasing available. However, our study does not aim to emphasize the novelty of the genome assemblies per se. Rather, with the increasing availability of chromosome-level genomes, we regard genome assembly as a necessary foundation for more advanced analyses. The main objective of our study is to investigate how each gene is expressed in response to seasonal environmental changes, and to link genome information with seasonal transcriptomic dynamics. To address the reviewer’s comment in line with this objective, we added a discussion on the syntenic structure of eight genome assemblies spanning four genera within the Fagaceae, including a species from the genus Fagus (Ikezaki et al. 2025, https://doi.org/10.1101/2025.07.31.667835). This addition helps to position our work more clearly within the context of existing genomic resources.

Most importantly, Figure 1B-D shows synteny between the two genera but also indicates homology between different chromosomes. Does this suggest paleopolyploidy or another novel feature? These chromosome connections should be interpreted in the main text-even if they could be methodological artifacts.

A previous study on genome size variation in Fagaceae suggested that, given the consistent ploidy level across the family, genome expansion likely occurred through relatively small segmental duplications rather than whole-genome duplications. Because Figure 1B-D supports this view, we cited the following reference in the revised version of the manuscript. Chen et al. (2014) https://doi.org/10.1007/s11295-014-0736-y

In both the Results and Materials and Methods sections, descriptions of genome and RNA-seq data are unclear. In line 128, a paragraph on genome assembly suddenly introduces expression levels. RNA-seq data should be described before this. Similarly, in line 238, the sentence "we assembled high-quality reference genomes" seems disconnected from the surrounding discussion of expression studies. In line 632, Illumina short-read DNA sequencing is mentioned, but it's unclear how these data were used.

We relocated the explanation regarding the expression levels of single-copy and multi-copy genes to the section titled “Seasonal gene expression dynamics.” Additionally, we clarified in the Materials and Methods section that short-read sequencing data were used for both genome size estimation and phylogenetic reconstruction.

Reviewer #2 (Public review):

Summary:

This study explores how gene expression evolves in response to seasonal environments, using four evergreen Fagaceae species growing in similar habitats in Japan. By combining chromosome-scale genome assemblies with a two-year RNA-seq time series in leaves and buds, the authors identify seasonal rhythms in gene expression and examine both conserved and divergent patterns. A central result is that winter bud expression is highly conserved across species, likely due to shared physiological demands under cold conditions. One of the intriguing implications of this study is that seasonal cycles might play a role similar to ontogenetic stages in animals. The authors touch on this by comparing their findings to the developmental hourglass model, and indeed, the recurrence of phenological states such as winter dormancy may act as a cyclic form of developmental canalization, shaping expression evolution in a way analogous to embryogenesis in animals.

Strengths:

(1) The evolutionary effects of seasonal environments on gene expression are rarely studied at this scale. This paper fills that gap.

(2) The dataset is extensive, covering two years, two tissues, and four tree species, and is well suited to the questions being asked.

(3) Transcriptome clustering across species (Figure 2) shows strong grouping by season and tissue rather than species, suggesting that the authors effectively controlled for technical confounders such as batch effects and mapping bias.

(4) The idea that winter imposes a shared constraint on gene expression, especially in buds, is well argued and supported by the data.

(5) The discussion links the findings to known concepts like phenological synchrony and the developmental hourglass model, which helps frame the results.

We are grateful for the reviewer for the detailed and thoughtful review of our manuscript.

Weaknesses:

(1) While the hierarchical clustering shown in Figure 2A largely supports separation by tissue type and season, one issue worth noting is that some leaf samples appear to cluster closely with bud samples. The authors do not comment on this pattern, which raises questions about possible biological overlap between tissues during certain seasonal transitions or technical artifacts such as sample contamination. Clarifying this point would improve confidence in the interpretation of tissue-specific seasonal expression patterns.

Leaf samples clustered into the bud are newly flushed leaves collected in April for Q. glauca, May for Q. acuta, May and June for L. edulis, and August and September for L. glaber. To clarify this point, we highlighted these newly flushed leaf samples as asterisk in the revised figure (Fig. 2A).

(2) While the study provides compelling evidence of conserved and divergent seasonal gene expression, it does not directly examine the role of cis-regulatory elements or chromatin-level regulatory architecture. Including regulatory genomic or epigenomic data would considerably strengthen the mechanistic understanding of expression divergence.

We thank the reviewer for this insightful comment. As noted in the Discussion section, we hypothesize that such genome-wide seasonal expression patterns—and their divergence across species—are likely mediated by cis-regulatory elements and chromatin-level mechanisms. While a direct investigation of regulatory architecture was beyond the scope of the present study, we fully agree that incorporating regulatory genomic and epigenomic data would significantly deepen the mechanistic understanding of expression divergence. In this regard, we are currently working to identify putative cis-regulatory elements in non-coding regions and are collecting epigenetic data from the same tree species using ChIP-seq. We believe the current study provide a foundation for these future investigations into the regulatory basis of seasonal transcriptome variation. We made a minor revision to the Discussion to note that an important future direction is to investigate the evolution of non-coding sequences that regulate gene expression in response to seasonal environmental changes.

(3) The manuscript includes a thoughtful analysis of flowering-related genes and seasonal GO enrichment (e.g., Figure 3C-D), providing an initial link between gene expression timing and phenological functions. However, the analysis remains largely gene-centric, and the study does not incorporate direct measurements of phenological traits (e.g., flowering or bud break dates). As a result, the connection between molecular divergence and phenotypic variation, while suggestive, remains indirect.

We would like to note that phenological traits have been observed in the field on a monthly basis throughout the sampling period and the phenological data were plotted together with molecular phenology (e.g. Fig. 2A, C; Fig. 3C, D). Although the temporal resolution is limited, these observations captured species-specific differences in key phenological events such as leaf flushing and flowering times. We revised the manuscript to clarify this point.

(4) Although species were sampled from similar habitats, one species (Q. acuta) was collected at a higher elevation, and factors such as microclimate or local photoperiod conditions could influence expression patterns. These potential confounding variables are not fully accounted for, and their effects should be more thoroughly discussed or controlled in future analyses.

We fully agree with the reviewer that local environmental conditions, including microclimate and photoperiod differences, could potentially influence gene expression patterns. To assess whether the higher elevation site of Q. acuta introduced confounding environmental effects, we reanalyzed the data after excluding this species. Hierarchical clustering still revealed that winter bud samples formed a distinct cluster regardless of species identity (Fig. S7), consistent with our original finding.

Furthermore, we recalculated the molecular phenology divergence index D (Fig. 4C) and the interspecific Pearson’s correlation coefficients (Fig. 5A) without including Q. acuta. These analyses produced results that were qualitatively similar to those obtained from the full dataset (Fig. S12; Fig. S14), indicating that the observed patterns are not driven by environmental differences associated with elevation.

We believe these additional analyses help to decouple the effects of environment and genetics, and support our conclusion that both seasonal synchrony and phylogenetic constraints play key roles in shaping transcriptome dynamics. We added four new figures (Fig. S6, Fig. S7, Fig. S12 and Fig. S14) and revised the text accordingly to clarify this point and to acknowledge the potential impact of site-specific environmental variation.

(5) Statistical and Interpretive Concerns Regarding Δφ and dN/dS Correlation (Figures 5E and 5F):

a) Statistical Inappropriateness: Δφ is a discrete ordinal variable (likely 1-11), making it unsuitable for Pearson correlation, which assumes continuous, normally distributed variables. This undermines the statistical validity of the analysis.

We thank the reviewer for the insightful comment. We would like to clarify that the analysis presented in Figures 5E and 5F was based on linear regression, not Pearson’s correlation. Although Δ_φ_ is a discrete variable, it takes values from 0 to 6 in 0.5 increments, resulting in 13 levels. We treated it as a quasi-continuous variable for the purposes of linear regression analysis. This approach is commonly adopted in practice when a discrete variable has sufficient resolution and ordering to approximate continuity. To enhance clarity, we revised the manuscript to explicitly state that linear regression was used, and we now reported the regression coefficient and associated p-value to support the interpretation of the observed trend.

b) Biological Interpretability: Even with the substantial statistical power afforded by genome-wide analysis, the observed correlations are extremely weak. This suggests that the relationship, if any, between temporal divergence in expression and protein-coding evolution is negligible.

Taken together, these issues weaken the case for any biologically meaningful association between Δφ and dN/dS. I recommend either omitting these panels or clearly reframing them as exploratory and statistically limited observations.

We agree with the reviewer’s comment. While we retained the original panels, we reframed our interpretation to emphasize that, despite statistical significance, the observed correlation is very weak—suggesting that coding region variation is unlikely to be the primary driver of seasonal gene expression patterns. Accordingly, we revised the “Relating seasonal gene expression divergence to sequence divergence” section in the Results, as well as the relevant part of the Discussion.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Sentences around lines 250-251 are incomplete and need revision.

We thank the reviewer for pointing this out. We revised the sentences in the subsection “Peak month distribution of rhythmic genes and intra-genus and inter-genera comparison” in the Results section to ensure clarity and completeness. In addition, to improve the interpretability of the peak month distribution, we added arrows to indicate the major peaks in the circular histograms shown in Fig. 3C and 3D.

Reviewer #2 (Recommendations for the authors):

(1) In Figure 1E-G, the term Copy number or Copy number variation could be misleading, as it is commonly associated with inter-individual gene copy number variation in a population. Since the analysis here refers to orthology relationships rather than population-level variation, a more precise term, such as orthogroup classification, may be preferable.

We thank the reviewer for this helpful suggestion. We agree that the term “copy number” could be misleading in this context. Accordingly, we updated the labeling in Fig. 1 to reflect the more precise term “orthogroup classification.”

(2) In Figure 3A, the x-axis label Period (month) may be misleading, as it could be mistaken for calendar months rather than referring to the periodicity of gene expression cycles. A more explicit label, such as Expression periodicity (months), might improve clarity for the reader.

We thank the reviewer for this valuable suggestion. In the original version of Fig. 3A, we used the label “Period (month),” which could indeed be misinterpreted as referring to calendar months. To clarify that this axis represents the length of gene expression cycles, we revised the label to “Period length (months).” This change also aligns with the terminology used throughout the manuscript, where “Period” refers specifically to cycle length, and “Periodicity” denotes the presence or absence of rhythmic expression.

Other minor revisions

We also made minor revisions for the reference list and the grant number details, and included the accession numbers for all DNA and RNA sequence data deposited in the DNA Data Bank of Japan (DDBJ) in the Data deposition and code availability section, in addition to the BioProject ID.

eLife Assessment

The authors used comprehensive approaches to identify Gyc76C as an ITPa receptor in Drosophila. They revealed that ITPa acts via Gyc76C in the renal tubules and fat body to modulate osmotic and metabolic homeostasis. The designed experiments, data, and analyses convincingly support the main claims. The findings are important to help us better understand how ITP signals contributes to systemic homeostasis regulation.

Reviewer #1 (Public review):

Summary:

In Drosophila melanogaster, ITP has functions in feeding, drinking, metabolism, excretion, and circadian rhythm. In the current study, the authors characterized and compared the expression of all three ITP isoforms (ITPa and ITPL1&2) in the CNS and peripheral tissues of Drosophila. An important finding is that they functionally characterized and identified Gyc76C as an ITPa receptor in Drosophila using both in vitro and in vivo approaches. In vitro, the authors nicely confirmed that the inhibitory function of recombinant Drosophila ITPa on MT secretion is Gyc76C-dependent (knockdown of Gyc76C specifically in two types of cells abolished the anti-diuretic action of Drosophila ITPa on renal tubules). They also confirmed that ITPa activates Gyc76C in a heterologous system. The authors used a combination of multiple approaches to investigate the roles of ITPa and Gyc76C on osmotic and metabolic homeostasis modulation in vivo. They revealed that ITPa signaling to renal tubules and fat body modulates osmotic and metabolic homeostasis via Gyc76C.

Furthermore, they tried to identify the upstream and downstream of ITP neurons in the nervous system by using connectomics and single-cell transcriptomic analysis. I found this interesting manuscript to be well-written and described. The findings in this study are valuable to help understand how ITP signals work on systemic homeostasis regulation. Both anatomical and single-cell transcriptome analysis here should be useful to many in the field.

Strengths:

The question (what receptors of ITPa in Drosophila) that this study tries to address is important. The authors ruled out the Bombyx ITPa receptor orthologs as potential candidates. They identified a novel ITP receptor by using phylogenetic, anatomical analysis, and both in vitro and in vivo approaches.

The authors exhibited detailed anatomical data of both ITP isoforms and Gyc76C (in the main and supplementary figures), which helped audiences understand the expression of the neurons studied in the manuscript.

They also performed connectomes and single-cell transcriptomics analyses to study the synaptic and peptidergic connectivity of ITP-expressing neurons. This provided more information for better understanding and further study of systemic homeostasis modulation.

Comments on revisions:

In the revised manuscript, the authors addressed all my concerns.

There is one more suggestion: The scale bar for fly and ovary images should be included in Figures 9, 10, and 12.

Reviewer #2 (Public review):

The physiology and behaviour of animals are regulated by a huge variety of neuropeptide signalling systems. In this paper, the authors focus on the neuropeptide ion transport peptide (ITP), which was first identified and named on account of its effects on the locust hindgut (Audsley et al. 1992). Using Drosophila as an experimental model, the authors have mapped the expression of three different isoforms of ITP, all of which are encoded by the same gene.

The authors then investigated candidate receptors for isoforms of ITP. Firstly, Drosophila orthologs of G-protein coupled receptors (GPCRs) that have been reported to act as receptors for ITPa or ITPL in the insect Bombyx mori were investigated. Importantly, the authors report that ITPa does not act as a ligand for the GPCRs TkR99D and PK2-R1. Therefore, the authors investigated other putative receptors for ITPs. Informed by a previously reported finding that ITP-type peptides cause an increase in cGMP levels in cells/tissues (Dircksen, 2009, Nagai et al., 2014), the authors investigated guanylyl cyclases as candidate receptors for ITPs. In particular, the authors suggest that Gyc76C may act as an ITP receptor in Drosophila. Evidence that Gyc76C may be involved in mediating effects of ITP in Bombyx was first reported by Nagai et al. (2014) and here the authors present further evidence, based on a proposed concordance in the phylogenetic distribution ITP-type neuropeptides and Gyc76C and experimental demonstration that ITPa causes dose-dependent stimulation of cGMP production in HEK cells expressing Gyc76C. Having performed detailed mapping of the expression of Gyc76C in Drosophila, the authors then investigated if Gyc76C knockdown affects the bioactivity of ITPa in Drosophila. The inhibitory effect of ITPa on leucokinin- and diuretic hormone-31-stimulated fluid secretion from Malpighian tubules was found to be abolished when expression of Gyc76C was knocked down in stellate cells and principal cells, respectively.

Having investigated the proposed mechanism of ITPa signalling in Drosophila, the authors then investigate its physiological roles at a systemic level. The authors present evidence that ITPa is released during desiccation and accordingly overexpression of ITPa increases survival when animals are subjected to desiccation. Furthermore, knockdown of Gyc76C in stellate or principal cells of Malphigian tubules decreases survival when animals are subject to desiccation. Furthermore, the relevance of the phenotypes observed to potential in vivo actions of ITPa is also explored and publicly available connectomic data and single-cell transcriptomic data are analysed to identify putative inputs and outputs of ITPa expressing neurons.

Strengths of this paper.

(1) The main strengths of this paper are:

i) the detailed analysis of the expression and actions of ITP and the phenotypic consequences of over-expression of ITPa in Drosophila.

ii). the detailed analysis of the expression of Gyc76C and the phenotypic consequences of knockdown of Gyc76C expression in Drosophila.

iii). the experimental demonstration that ITPa causes dose-dependent stimulation of cGMP production in HEK cells expressing Gyc76C, providing biochemical evidence that the effects of ITPa in Drosophila are, at least in part, mediated by Gyc76C.

(2) Furthermore, the paper is generally well written and the figures are of good quality.

Weaknesses of this paper.

A weakness of this paper is the phylogenetic analysis to investigate if there is correspondence in the phylogenetic distribution of ITP-type and Gyc76C-type genes/proteins. Unfortunately, the evidence presented is rather limited in scope. Essentially, the authors report that they only found ITP-type and Gyc76C-type genes/proteins in protostomes, but not in deuterostomes. What is needed is a more fine-grained analysis at the species level within the protostomes. However, I recognise that such a detailed analysis may extend beyond the scope of this paper, which is already rich in data.

Reviewer #3 (Public review):

Summary:

The goal of this paper is to characterize an anti-diuretic signaling system in insects using Drosophila melanogaster as a model. Specifically, the authors wished to characterize a role for ion transport peptide (ITP) and its isoforms in regulating diverse aspects of physiology and metabolism. The authors combined genetic and comparative genomic approaches with classical physiological techniques and biochemical assays to provide a comprehensive analysis of ITP and its role in regulating fluid balance and metabolic homeostasis in Drosophila. The authors further characterized a previously unrecognized role for Gyc76C as a receptor for ITPa, an amidated isoform of ITP, and in mediating the effects of ITPa on fluid balance and metabolism. The evidence presented in favor of this model is very strong as it combines multiple approaches and employs ideal controls. Taken together, these findings represent an important contribution to the field of insect neuropeptides and neurohormones and has strong relevance for other animals. The authors have addressed all weaknesses raised in my previous review.

Author Response:

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

Reviewer #1 (Public review):

The scale bar for fly and ovary images should be included in Figures 9, 10, and 12.

We agree with this comment and apologize for the oversight. We have now modified Figures 9, 10, and 12 to include the scale bars for the ovary images. The fly images were acquired using a stereo microscope where scale bar calculation was not possible. However, all images were acquired at the same magnification for consistency.

Reviewer #2 (Public review):

A weakness of this paper is the phylogenetic analysis to investigate if there is correspondence in the phylogenetic distribution of ITP-type and Gyc76C-type genes/proteins. Unfortunately, the evidence presented is rather limited in scope. Essentially, the authors report that they only found ITP-type and Gyc76C-type genes/proteins in protostomes, but not in deuterostomes. What is needed is a more fine-grained analysis at the species level within the protostomes. However, I recognise that such a detailed analysis may extend beyond the scope of this paper, which is already rich in data.

We thank the reviewer for their comment and the suggestion to perform a fine-grained species level comparison of ITP and Gyc76C genes across protostomes. We are unsure of the utility of this analysis for the present study given that we have now shown that ITPa can activate Gyc76C using both an ex vivo and a heterologous assay, the latter being the gold standard in GPCR and guanylate cyclase discovery (see Huang et al 2025 https://doi.org/10.1073/pnas.2420966122; Beets et al 2023 https://doi.org/10.1016/j.celrep.2023.113058); Chang et al 2009 https://doi.org/10.1073/pnas.0812593106.

Additionally, absence of a gene in a genome/proteome is hard to prove especially when many/most of the protostomian datasets are not as high-quality as those of model systems (e.g. Drosophila melanogaster and Caenorhabditis elegans). Secondly, based on previous findings in Bombyx mori (Nagai et al. 2014 https://doi.org/10.1074/jbc.m114.590646 and Nagai et al. 2016 https://doi.org/10.1371/journal.pone.0156501) and Drosophila (Xu et al. 2023 https://doi.org/10.1038/s41586-023-06833-8 and our study) it is evident that different products of the ITP gene (ITPa and ITPL) could signal via different receptor types depending on the species. Hence, we would need to explore the presence of several genes (ITP, tachykinin, pyrokinin, tachykinin receptor, pyrokinin receptor, CG30340 orphan receptor and Gyc76C) to fully understand which components of these diverse signaling systems are present in a given species to decipher the potential for cross-talk.

While this species-level comparison will certainly be useful in the context of ITP-Gyc76C evolution, it will not alter the conclusions of the present study – ITPa acts via Gyc76C in Drosophila. We therefore agree with the reviewer that these analyses are beyond the scope of this paper.

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

Reviewer #1 (Public Review):  

Summary:  

In Drosophila melanogaster, ITP has functions on feeding, drinking, metabolism, excretion, and circadian rhythm. In the current study, the authors characterized and compared the expression of all three ITP isoforms (ITPa and ITPL1&2) in the CNS and peripheral tissues of Drosophila. An important finding is that they functionally characterized and identified Gyc76C as an ITPa receptor in Drosophila using both in vitro and in vivo approaches. In vitro, the authors nicely confirmed that the inhibitory function of recombinant Drosophila ITPa on MT secretion is Gyc76C-dependent (knockdown Gyc76C specifically in two types of cells abolished the anti-diuretic action of Drosophila ITPa on renal tubules). They also used a combination of multiple approaches to investigate the roles of ITPa and Gyc76C on osmotic and metabolic homeostasis modulation in vivo. They revealed that ITPa signaling to renal tubules and fat body modulates osmotic and metabolic homeostasis via Gyc76C.  

Furthermore, they tried to identify the upstream and downstream of ITP neurons in the nervous system by using connectomics and single-cell transcriptomic analysis. I found this interesting manuscript to be well-written and described. The findings in this study are valuable to help understand how ITP signals work on systemic homeostasis regulation. Both anatomical and single-cell transcriptome analysis here should be useful to many in the field. 

We thank this reviewer for the positive and thorough assessment of our manuscript.  

Strengths:  

The question (what receptors of ITPa in Drosophila) that this study tries to address is important. The authors ruled out the Bombyx ITPa receptor orthologs as potential candidates. They identified a novel ITP receptor by using phylogenetic, anatomical analysis, and both in vitro and in vivo approaches. 

The authors exhibited detailed anatomical data of both ITP isoforms and Gyc76C (in the main and supplementary figures), which helped audiences understand the expression of the neurons studied in the manuscript.  

They also performed connectomes and single-cell transcriptomics analysis to study the synaptic and peptidergic connectivity of ITP-expressing neurons. This provided more information for better understanding and further study on systemic homeostasis modulation.  

Weaknesses:  

In the discussion section, the authors raised the limitations of the current study, which I mostly agree with, such as the lack of verification of direct binding between ITPa and Gyc76C, even though they provided different data to support that ITPa-Gyc76C signaling pathway regulates systemic homeostasis in adult flies. 

We now provide evidence of Gyc76C activation by ITPa in a heterologous system (new Figure 7 and Figure 7 Supplement 1).

Reviewer #2 (Public Review):  

Summary:  

The physiology and behaviour of animals are regulated by a huge variety of neuropeptide signalling systems. In this paper, the authors focus on the neuropeptide ion transport peptide (ITP), which was first identified and named on account of its effects on the locust hindgut (Audsley et al. 1992). Using Drosophila as an experimental model, the authors have mapped the expression of three different isoforms of ITP (Figures 1, S1, and S2), all of which are encoded by the same gene.  

The authors then investigated candidate receptors for isoforms of ITP. Firstly, Drosophila orthologs of G-protein coupled receptors (GPCRs) that have been reported to act as receptors for ITPa or ITPL in the insect Bombyx mori were investigated. Importantly, the authors report that ITPa does not act as a ligand for the GPCRs TkR99D and PK2-R1 (Figure S3). Therefore, the authors investigated other putative receptors for ITPs. Informed by a previously reported finding that ITP-type peptides cause an increase in cGMP levels in cells/tissues (Dircksen, 2009, Nagai et al., 2014), the authors investigated guanylyl cyclases as candidate receptors for ITPs. In particular, the authors suggest that Gyc76C may act as an ITP receptor in Drosophila.  

Evidence that Gyc76C may be involved in mediating effects of ITP in Bombyx was first reported by Nagai et al. (2014) and here the authors present further evidence, based on a proposed concordance in the phylogenetic distribution ITP-type neuropeptides and Gyc76C (Figure 2). Having performed detailed mapping of the expression of Gyc76C in Drosophila (Figures 3, S4, S5, S6), the authors then investigated if Gyc76C knockdown affects the bioactivity of ITPa in Drosophila. The inhibitory effect of ITPa on leucokinin- and diuretic hormone-31-stimulated fluid secretion from Malpighian tubules was found to be abolished when expression of Gyc76C was knocked down in stellate cells and principal cells, respectively (Figure 4). However, as discussed below, this does not provide proof that Gyc76C directly mediates the effect of ITPa by acting as its receptor. The effect of Gyc76C knockdown on the action of ITPa could be an indirect consequence of an alteration in cGMP signalling.  

Having investigated the proposed mechanism of ITPa in Drosophila, the authors then investigated its physiological roles at a systemic level. In Figure 5 the authors present evidence that ITPa is released during desiccation and accordingly, overexpression of ITPa increases survival when animals are subjected to desiccation. Furthermore, knockdown of Gyc76C in stellate or principal cells of Malphigian tubules decreases survival when animals are subject to desiccation. However, whilst this is correlative, it does not prove that Gyc76C mediates the effects of ITPa. The authors investigated the effects of knockdown of Gyc76C in stellate or principal cells of Malphigian tubules on i). survival when animals are subject to salt stress and ii). time taken to recover from of chill coma. It is not clear, however, why animals overexpressing ITPa were also not tested for its effect on i). survival when animals are subject to salt stress and ii). time taken to recover from of chill coma. In Figures 6 and S8, the authors show the effects of Gyc76C knockdown in the female fat body on metabolism, feeding-associated behaviours and locomotor activity, which are interesting. Furthermore, the relevance of the phenotypes observed to potential in vivo actions of ITPa is explored in Figure 7. The authors conclude that "increased ITPa signaling results in phenotypes that largely mirror those seen following Gyc76C knockdown in the fat body, providing further support that ITPa mediates its effects via Gyc76C." Use of the term "largely mirror" seems inappropriate here because there are opposing effects- e.g. decreased starvation resistance in Figure 6A versus increased starvation resistance in Figure 7A. Furthermore, as discussed above, the results of these experiments do not prove that the effects of ITPa are mediated by Gyc76C because the effects reported here could be correlative, rather than causative. 

We thank this reviewer for an extremely thorough and fair assessment of our manuscript. 

We have now performed salt stress tolerance and chill coma recovery assays using flies over-expressing ITPa (new Figure 10 Supplement 1).

We agree that the use of the term “largely mirrors” to describe the effects of ITPa overexpression and Gyc76C knockdown is not appropriate and have changed this sentence. We also agree that the experiments did not provide direct evidence that the effects of ITPa are mediated by Gyc76C. To address this, we now provide evidence of Gyc76C activation by ITPa in a heterologous system (new Figure 7 and Figure 7 Supplement 1).

Lastly, in Figures 8, S9, and S10 the authors analyse publicly available connectomic data and single-cell transcriptomic data to identify putative inputs and outputs of ITPa-expressing neurons. These data are a valuable addition to our knowledge ITPa expressing neurons; but they do not address the core hypothesis of this paper - namely that Gyc76C acts as an ITPa receptor.  

The goal of our study was to comprehensively characterize an anti-diuretic system in Drosophila. Hence, in addition to identifying the receptor via which ITPa exerts its effects, we also wanted to understand how ITPa-producing neurons are regulated. Connectomic and single-cell transcriptomic analyses are highly appropriate for this purpose. We have now updated the connectomic analyses using an improved connectome dataset that was released during the revision of this manuscript. Our new analysis shows that lNSC^ITP are connected to other endocrine cells that produce other homeostatic hormones (new Figure 13F). We also identify a pathway through which other ITP-producing neurons (LNd^ITP) receive hygrosensory inputs to regulate water seeking behavior (new Figure 13E). Moreover, we now include results which showcase that ITPa-producing neurons (l-NSC^ITP) are active (new Figure 8A and B) and release ITPa under desiccation. Together with other analyses, these data provide a comprehensive outlook on the when, what and how ITPa regulates systemic homeostasis.  

Strengths:  

(1) The main strengths of this paper are i) the detailed analysis of the expression and actions of ITP and the phenotypic consequences of overexpression of ITPa in Drosophila. ii). the detailed analysis of the expression of Gyc76C and the phenotypic consequences of knockdown of Gyc76C expression in Drosophila.  

(2) Furthermore, the paper is generally well-written and the figures are of good quality. 

We thank this reviewer for highlighting the strengths of this manuscript.

Weaknesses:  

(1) The main weakness of this paper is that the data obtained do not prove that Gyc76C acts as a receptor for ITPa. Therefore, the following statement in the abstract is premature: "Using a phylogenetic-driven approach and the ex vivo secretion assay, we identified and functionally characterized Gyc76C, a membrane guanylate cyclase, as an elusive Drosophila ITPa receptor." Further experimental studies are needed to determine if Gyc76C acts as a receptor for ITPa. In the section of the paper headed "Limitations of the study", the authors recognise this weakness. They state "While our phylogenetic analysis, anatomical mapping, and ex vivo and in vivo functional studies all indicate that Gyc76C functions as an ITPa receptor in Drosophila, we were unable to verify that ITPa directly binds to Gyc76C. This was largely due to the lack of a robust and sensitive reporter system to monitor mGC activation." It is not clear what the authors mean by "the lack of a robust and sensitive reporter system to monitor mGC activation". The discovery of mGCs as receptors for ANP in mammals was dependent on the use of assays that measure GC activity in cells (e.g. by measuring cGMP levels in cells). Furthermore, more recently cGMP reporters have been developed. The use of such assays is needed here to investigate directly whether Gyc76C acts as a receptor for ITPa. In summary, insufficient evidence has been obtained to conclude that Gyc76C acts as a receptor for ITPa. Therefore, I think there are two ways forward, either:  

(a) The authors obtain additional biochemical evidence that ITPa is a ligand for Gyc76C.  

or  

(b) The authors substantially revise the conclusions of the paper (in the title, abstract, and throughout the paper) to state that Gyc76C MAY act as a receptor for ITPa, but that additional experiments are needed to prove this. 

We thank the reviewer for this comment and agree with the two options they propose. We had previously tried different a cGMP reporter (Promega GloSensor cGMP assay) to monitor activation of Gyc76C by ITPa in a heterologous system. Unfortunately, we were not successful in monitoring Gyc76C activation by ITPa. We now utilized another cGMP sensor, Green cGull, to show that ITPa can indeed activate Gyc76C heterologously expressed in HEK cells (new Figure 7 and Figure 7 Supplement 1). However, we still cannot rule out the possibility that ITPa can act on additional receptors in vivo. This is based on our ex vivo Malpighian tubule assays (new Figure 6E and F). ITPa inhibits DH31- and LK-stimulated secretion and we show that this effect is abolished in Gyc76C knockdown specifically in principal and stellate cells, respectively. Interestingly, application of ITPa alone can stimulate secretion when Gyc76C is knocked down in principal cells (new Figure 6E). This could be explained by: 1) presence of another receptor for ITPa which results in diuretic actions and/or 2) low Gyc76C signaling activity (RNAi based knockdown lowers signaling but does not abolish it completely) could alter other intracellular messenger pathways that promote secretion. We have added text to indicate the possibility of other ITPa receptors. Nonetheless, our conclusions are supported by the heterologous assay results which indicate that ITPa can activate Gyc76C. Therefore, we do not alter the title. 

(2) The authors state in the abstract that a phylogenetic-driven approach led to their identification of Gyc76C as a candidate receptor for ITPa. However, there are weaknesses in this claim. Firstly, because the hypothesis that Gyc76C may be involved in mediating effects of ITPa was first proposed ten years ago by Nagai et al. 2014, so this surely was the primary basis for investigating this protein. Nevertheless, investigating if there is correspondence in the phylogenetic distribution of ITP-type and Gyc76C-type genes/proteins is a valuable approach to addressing this issue. Unfortunately, the evidence presented is rather limited in scope. Essentially, the authors report that they only found ITP-type and Gyc76C-type genes/proteins in protostomes, but not in deuterostomes. What is needed is a more fine-grained analysis at the species level within the protostomes. Thus, are there protostome species in which both ITP-type and Gyc76C-type genes/proteins have been lost? Furthermore, are there any protostome species in which an ITP-type gene is present but an Gyc76C-type gene is absent, or vice versa? If there are protostome species in which an ITP-type gene is present but a Gyc76C-type gene is absent or vice versa, this would argue against Gyc76C being a receptor for ITPa. In this regard, it is noteworthy that in Figure 2A there are two ITP-type precursors in C. elegans, but there are no Gyc76Ctype proteins shown in the tree in Figure 2B. Thus, what is needed is a more detailed analysis of protostomes to investigate if there really is correspondence in the phylogenetic distribution of Gyc76C-type and ITP-type genes at the species level. 

We thank the reviewer for this comment. While the previous study by Nagai et al had implicated Gyc76C in the ITP signaling pathway, how they narrowed down Gyc76C as a candidate was not reported. Therefore, our unbiased phylogenetic approach was necessary to ensure that we identified all suitable candidate receptors. Indeed, our phylogenetic analysis also identified Gyc32E as another candidate ITP receptor. However, we did not pursue this receptor further as our expression data (new Figure 4 Supplement 2) indicated that Gyc32E is not expressed in osmoregulatory tissues and therefore likely does not mediate the osmotic effects of ITPa. 

We also appreciate the suggestion to perform a more detailed phylogenetic analysis for the peptide and receptor. We did not include C. elegans receptors in the phylogenetic analysis because they tend to be highly evolved and routinely cause long-branch attraction (see: Guerra and Zandawala 2024: https://doi.org/10.1093/gbe/evad108). We (specifically the senior author) have previously excluded C. elegans receptors in the phylogenetic analysis of GnRH and Corazonin receptors for similar reasons (see: Tian and Zandawala et al. 2016: 10.1038/srep28788). 

Unfortunately, absence of a gene in a genome is hard to prove especially when they are not as high-quality as the genomes of model systems (e.g. Drosophila and mice). Moreover, given the concern of this reviewer that our physiological and behavioral data on ITPa and Gyc76C only provide correlative evidence, we decided against performing additional phylogenetic analysis which also provides correlative evidence. Our only goal with this analysis was to identify a candidate ITPa receptor. Since we have now functionally characterized this receptor using a heterologous system, we feel that the current phylogenetic analysis was able to successfully serve its purpose.  

(3) The manuscript would benefit from a more comprehensive overview and discussion of published literature on Gyc76C in Drosophila, both as a basis for this study and for interpretation of the findings of this study.  

We thank the reviewer for this comment. We have now included a broader discussion of Gyc76C based on published literature.  

Reviewer #3 (Public Review):  

Summary:  

The goal of this paper is to characterize an anti-diuretic signaling system in insects using Drosophila melanogaster as a model. Specifically, the authors wished to characterize a role of ion transport peptide (ITP) and its isoforms in regulating diverse aspects of physiology and metabolism. The authors combined genetic and comparative genomic approaches with classical physiological techniques and biochemical assays to provide a comprehensive analysis of ITP and its role in regulating fluid balance and metabolic homeostasis in Drosophila. The authors further characterized a previously unrecognized role for Gyc76C as a receptor for ITPa, an amidated isoform of ITP, and in mediating the effects of ITPa on fluid balance and metabolism. The evidence presented in favor of this model is very strong as it combines multiple approaches and employs ideal controls. Taken together, these findings represent an important contribution to the field of insect neuropeptides and neurohormones and have strong relevance for other animals. 

We thank this reviewer for the positive and thorough assessment of our manuscript.

Strengths:  

Many approaches are used to support their model. Experiments were wellcontrolled, used appropriate statistical analyses, and were interpreted properly and without exaggeration.  

Weaknesses:  

No major weaknesses were identified by this reviewer. More evidence to support their model would be gained by using a loss-of-function approach with ITPa, and by providing more direct evidence that Gyc76C is the receptor that mediates the effects of ITPa on fat metabolism. However, these weaknesses do not detract from the overall quality of the evidence presented in this manuscript, which is very strong.  

We agree with this reviewer regarding the need to provide additional evidence using a loss-of-function approach with ITPa. We now characterize the phenotypes following knockdown of ITP in ITP-producing cells (new Figure 9). Our results are in agreement with phenotypes observed following Gyc76C knockdown, lending further support that ITPa mediates its effects via Gyc76C. Unfortunately, we are not able to provide evidence that ITPa acts on Gyc76C in the fat body using the assay suggested by this reviewer (explained in detail below). Instead, we now provide direct evidence of Gyc76C activation by ITPa in a heterologous system (new Figure 7 and Figure 7 Supplement 1).

Reviewer #1 (Recommendations For The Authors):  

Here, I have several extra concerns about the work as below:  

(1) The authors confirmed the function of ITPa in regulating both osmotic and metabolic homeostasis by specifically overexpressing ITPa driven by ITP-RCGal4 in adult flies (Figures. 5 and 7). Have authors ever tried to knock down ITP in ITP-RC-Gal4 neurons? What was the phenotype? Especially regarding the impact on metabolic homeostasis, does knocking down ITP in ITP neurons mimic the phenotypes of Gyc76C fat body knockdown flies? 

We thank the reviewer for this suggestion. We now characterize the phenotypes following knockdown of ITP using ITP-RC-Gal4 (new Figure 9). Our results are in agreement with phenotypes observed following Gyc76C knockdown, lending further support that ITPa mediates its effects via Gyc76C.

The authors mentioned that the existing ITP RNAi lines target all three isoforms. It would be interesting if the authors could overexpress ITPa in ITPRC-Gal4>ITP-RNAi flies and confirm whether any phenotypes induced by ITP knockdown could be rescued. It will further confirm the role of ITPa in homeostasis regulation.  

We thank the reviewer for this suggestion. Unfortunately, this experiment is not straightforward because knockdown with ITP RNAi does not completely abolish ITP expression (see Figure 9A). Hence, the rescue experiment needs to be ideally performed in an ITP mutant background. However, ITP mutation leads to developmental lethality (unpublished observation) so we cannot generate all the flies necessary for this experiment. Therefore, we cannot perform the rescue experiments at this time. In future studies, we hope to perform knockdown of specific ITP isoforms using the transgenes generated here (Xu et al 2023: 10.1038/s41586-023-06833-8).   

(2) In Figures 5A and B, the authors nicely show the increased release of ITPa under desiccation by quantifying the ITPa immunolabelling intensity in different neuronal populations. It may be induced by the increased neuronal activity of ITPa neurons under the desiccated condition. Have the authors confirmed whether the activity of ITPa-expressing neurons is impacted by desiccation?  

The TRIC system may be able to detect the different activity of those neurons before and after desiccation. This may further explain the reduced ITPa peptide levels during desiccation.  

We thank the reviewer for this suggestion. We have now monitored the activity of ITPa-expressing neurons using the CaLexA system (Masuyama et al 2012: 10.3109/01677063.2011.642910). Our results indicate that ITPa neurons are indeed active under desiccation (new Figure 8A and B). These results are also in agreement with ITPa immunolabelling showing increased peptide release during desiccation (new Figure 8C and D). Together, these results show that ITPa neurons are activated and release ITPa under desiccation.  

(3) What about the intensity of ITPa immunolabelling in other ITPa-positive neurons (e.g., VNC) under desiccation? If there is no change in other ITPa neurons, it will be a good control. 

We thank the reviewer for this suggestion. Unfortunately, ITPa immunostaining in VNC neurons is extremely weak preventing accurate quantification of ITPa levels under different conditions. We did hypothesize that ITPa immunolabelling in clock neurons (5^th-LN_v and LN<Sub>d</sub>^ITP) would not change depending on the osmotic state of the animal. However, our results (Figure 8C and D) indicate that ITPa from these neurons is also released under desiccation. Interestingly, LNd^ITP, which also coexpress Neuropeptide F (NPF) have recently been implicated in water seeking during thirst (Ramirez et al, 2025: 10.1101/2025.07.03.662850). Our new connectomic-driven analysis shows that these neurons can receive thermo/hygrosensory inputs (new Figure 13E). Hence, it is conceivable that other ITPa-expressing neurons also release ITPa during thirst/desiccation.

(4) The adult stage, specifically overexpression of ITPa in ITP neurons, does show significant phenotypes compared to controls in both osmotic and metabolic homeostasis-related assays. It would be helpful if authors could show how much ITPa mRNA levels are increased in the fly heads with ITPa overexpression (under desiccation & starvation or not). 

We thank the reviewer for this suggestion. We have now included immunohistochemical evidence showing increase in ITPa peptide levels in flies with ITPa overexpression (new Figure 10A). We feel that this is a better indicator of ITPa signaling level instead of ITPa mRNA levels.   

(5) Another question concerns the bloated abdomens of ITPa-overexpressing flies. Are the bloated abdomens of ITPa OE female flies (Figure 5E) due to increased ovary size (Figure 7G)? Have the authors also detected similar bloated abdomens in male flies with ITPa overexpression? Since both male and female flies show more release of ITPa during the desiccation.  

We thank the reviewer for this comment. The bloated abdomen phenotype seen in females can be attributed to increased water content since we see a similar phenotype in males (see Author response image 1 below).

Author response image 1.

Reviewer #2 (Recommendations For The Authors):  

(1) Page 1 - change "Homeostasis is obtained by" to "Homeostasis is achieved by".  

Changed

(2) Page 1 - change "Physiological responses" to "Physiological processes". 

Changed

(3) Page 2 - Change "Recently, ITPL2 was also shown to mediate anti-diuretic effects via the tachykinin receptor" to "Recently, ITPL2 was also shown to exert anti-diuretic effects via the tachykinin receptor". 

Changed

(4) Page 9 - "(C) Adult-specific overexpression of ITPa using ITP- RC-GAL4TS (ITP-RC-T2A-GAL4 combined with temperature-sensitive tubulinGAL80) increases desiccation" Unless I am misunderstanding Fig 5C, I think what is shown is that overexpression of ITPa prolongs survival during a period of desiccation. I am not sure what the authors mean by "increases desiccation". In the text (page 9) the authors state "ITPa overexpression improves desiccation tolerance, which is a much clearer statement than what is in the figure legend. 

We thank the reviewer for identifying this oversight. We have now changed the caption to “increases desiccation tolerance”.  

(5) Page 11 - The authors conclude that "increased ITPa signaling results in phenotypes that largely mirror those seen following Gyc76C knockdown in the fat body, providing further support that ITPa mediates its effects via Gyc76C." Use of the term "largely mirror" seems inappropriate here because there are opposing effects- e.g. decreased starvation resistance in Figure 6A versus increased starvation resistance in Figure 7A.  

Perhaps there is a misunderstanding of what is meant by "mirroring" - it means the same, not the opposite. 

We thank the reviewer for this comment. We agree that the use of the term “largely mirrors” to describe the effects of ITPa overexpression and Gyc76C knockdown is not appropriate and have changed this sentence as follows: “Taken together, the phenotypes seen following Gyc76C knockdown in the fat body largely mirror those seen following ITP knockdown in ITP-RC neurons, providing further support that ITPa mediates its effects via Gyc76C.”

(6) Page 12 - There appear to be words missing between "neurons during desiccation, as well as their downstream" and "the recently completed FlyWire adult brain connectome" 

We thank the reviewer for highlighting this mistake. We have changed the sentence as following: “Having characterized the functions of ITP signaling to the renal tubules and the fat body, we wanted to identify the factors and mechanisms regulating the activity of ITP neurons during desiccation, as well as their downstream neuronal pathways. To address this, we took advantage of the recently completed FlyWire adult brain connectome (Dorkenwald et al., 2024, Schlegel et al., 2024) to identify pre- and post-synaptic partners of ITP neurons.”

(7) Page 15 - "can release up to a staggering 8 neuropeptides" - I suggest that the word "staggering" is removed. The notion that individual neurons release many neuropeptides is now widely recognised (both in vertebrates and invertebrates) based on analysis of single-cell transcriptomic data. 

Removed staggering.

(8) Page 16 - "(Farwa and Jean-Paul, 2024)" - this citation needs to be added to the reference list and I think it needs to be changed to "Sajadi and Paluzzi, 2024". 

We thank the reviewer for highlighting this oversight. The correct citation has now been added.

(9) It is noteworthy that, based on a PubMed search, there are at least thirteen published papers that report on Gyc76C in Drosophila (PMIDs: 34988396, 32063902, 27642749, 26440503, 24284209, 23862019, 23213443,  21893139, 21350862, 16341244, 15485853, 15282266, 7706258). However, none of these papers are discussed/cited by the authors. This is surprising because the authors' hypothesis that Gyc76C acts as a receptor for ITPa surely needs to be evaluated and discussed with reference to all the published insights into the developmental/physiological roles of this protein. 

We thank the reviewer for this comment. Some of the references mentioned above (21350862, 16341244, 15485853) mainly report on soluble guanylyl cyclases and not membrane guanylyl cyclase like Gyc76C. Based on other studies on Gyc76C and its role in immunity and development, we have now expanded the discussion on additional roles of ITPa.

Reviewer #3 (Recommendations For The Authors):  

I have only a few comments that will help the authors strengthen a couple of aspects of their model.  

(1) The case for Gyc76C as a receptor for ITPa in regulating fluid homeostasis is clear, given the experiments the authors carried out where they applied ITPa to tubules and showed that the effects of ITPa on tubule secretion were blocked if Gyc76C was absent in tubules. This approach, or something similar, should be used to provide conclusive proof that ITPa's metabolic effects on the fat body go through Gyc76C.  

At present (unless I missed it) the authors only show that gain of ITPa has the opposite phenotype to fat body-specific loss of Gyc76C. While this would be the expected result if ITPa/Gyc76C is a ligand-receptor pair, it is not quite sufficient to conclusively demonstrate that Gyc76C is definitely the fat body receptor. Ex vivo experiments such as soaking the adult fat body carcasses with and without Gyc76C in ITPa and monitoring fat content via Nile Red could be one way to address this lack of direct evidence. The authors could also make text changes to explicitly mention this lack of conclusive evidence and suggest it as a future direction.

We thank the reviewer for this comment. We have now conclusively demonstrated that Gyc76C is activated by ITPa in a heterologous assay (new Figure 7 and Figure 7 Supplement 1). With this evidence, we can confidently claim that ITPa can mediate its actions via Gyc76C in various tissues including the Malpighian tubules and fat body. Nonetheless, we liked the suggestion by this reviewer to perform the ex vivo assay and test the effect of ITPa on the fat body. Unfortunately, it is challenging to do this because increased ITPa signaling (chronically using ITPa overexpression) results in increased lipid accumulation in the fat body in vivo. Therefore, we would likely not see the effect of ITPa addition in an ex vivo fat body preparation since lipogenesis will not occur in the absence of glucose. However, ITPa could counteract the effects of other lipolytic factors such as adipokinetic hormone (AKH). To test this hypothesis, we monitored fat content in the fat body incubated with and without AKH (see Author response image 2 below showing representative images from this experiment). Since we did not observe any differences in fat levels between these two conditions, we were unable to test the effects of ITPa on AKH-activity using this assay.

Author response image 2.

(2) I did not see any loss of function data for ITPa - is this possible? If so this would strengthen the case for a 1:1 relationship between loss of ligand and loss of receptor. Alternatively, the authors could suggest this as an important future direction. 

We agree with this reviewer regarding the need to provide additional evidence using a loss-of-function approach with ITPa. We have now characterized the phenotypes following knockdown of ITP in ITP-producing cells (new Figure 9). Our results are in agreement with phenotypes observed following Gyc76C knockdown, lending further support that ITPa mediates its effects via Gyc76C.

(3) For clarity, please include the sex of all animals in the figure legend. Even though the methods say 'females used unless otherwise indicated' it is still better for the reader to know within the figure legend what sex is displayed. 

We thank the reviewer for this suggestion and have now included sex of the animals in the figure legends.  

(4) Please state whether females are mated or not, as this is relevant for taste preferences and food intake. 

We apologize for this oversight. We used mated females for all experiments. This has now been included in the methods.  

(5) More discussion on the previous study on metabolic effects of ITP in this study compared with past studies would help readers appreciate any similarities and/or differences between this study and past work (Galikova 2018, 2022) 

We thank the reviewer for this suggestion. Unfortunately, it is difficult to directly compare our phenotypes with the metabolic effects of ITP reported in Galikova and Klepsatel 2022 because the previous study used a ubiquitous driver (Da-GAL4) to manipulate ITP levels. Ectopically overexpressing ITPa in non-ITP producing cells can result in non-physiological phenotypes. This is evident in their metabolic measurements where both global overexpression and knockdown of ITP results in reduced glycogen and fat levels, and starvation tolerance. Moreover, ITP-RC-GAL4 used in our study to overexpress and knockdown ITPa is more specific than the Da-GAL4 used previously. Da-GAL4 would include other ITP cells (e.g. ITP-RD producing cells). Since ITP is broadly expressed across the animal, it is difficult to parse out the phenotypes of ITPa and other isoforms using manipulations performed with Da-GAL4. We have mentioned this limitation in the results for ITP knockdown as follows: “A previous study employing ubiquitous ITP knockdown and overexpression suggests that Drosophila ITP also regulates feeding and metabolic homeostasis (Galikova and Klepsatel, 2022) in addition to osmotic homeostais (Galikova et al., 2018). However, given the nature of the genetic manipulations (ectopic ITPa overexpression and knockdown of ITP in all tissues) utilized in those studies, it is difficult to parse the effects of ITP signaling from ITPa-producing neurons.”

eLife Assessment

This study provides convincing evidence that homologous recombination can occur in telophase-arrested cells, independently of cohesin subunits Smc 1-3. These findings are valuable as they point to investigate the role of cohesins re-association with chromatin in the allelic inter-sister repair by homologous recombination.

Reviewer #1 (Public review):

Summary

The cohesin complex is essential for maintaining sister chromatid cohesion from S phase until anaphase. Beyond this canonical role, it is also recruited to double-strand breaks (DSBs), supporting both local and global post-replicative cohesion, a phenomenon first reported in 2004. In a previous study, Ayra-Plasencia et al. demonstrated that in telophase, DSBs can be repaired by homologous recombination (HR) through re-coalescence of sister chromatids (Ayra-Plasencia & Machín, 2019). In the present work, the authors provide further insights into DSB repair in late mitosis, showing that:

Scc1 is reloaded and reconstituted on chromatin together with Smc1.

HR occurs with high efficiency.

HR-driven MAT switching can occur in an Smc3-independent manner.

Strengths

The authors take full advantage of the yeast model system, employing the HO endonuclease to generate a single, site-specific DSB at the MAT locus on chromosome III. Combined with careful cell synchronization, this setup allows them to monitor HR-mediated repair events specifically in G2/M and late mitosis. Their demonstration that full-length Scc1 can be recovered upon DSB induction is compelling. Most importantly, the finding that efficient HR can take place during M phase is significant, as HR has long been thought to be largely inhibited at this stage of the cell cycle.

Weaknesses

While the authors provide evidence for Scc1 recovery and efficient HR in late mitosis, some critical points need to be clarified to improve the impact and interpretability of the study.

Reviewer #2 (Public review):

Cohesin drive inter-sister repair of DNA breaks by homologous recombination (HR) in G2/M. Cohesion is lost at the metaphase to anaphase transition upon digestion of the Scc1 subunit of cohesin by Esp1, raising the question as to whether and how break repair by HR could occur in late mitosis (late-M).

Here the author investigate the behavior of cohesin in cells arrested in telophase and experiencing a DNA break at the mating-type locus on chr. III (a specialized recombination process required for mating-type switching) or upon random DNA break formation with the drug phleomycin.

The revised version of the manuscript now convincingly establishes three facts:

- The cohesin subunit Scc1 can re-associate with chromatin and the other Smc1-3 subunits upon formation of an unrepairable DSB at MAT in telophase.<br /> - HR can occur in telophase-arrested cells<br /> - Cohesin (an a fortiori cohesin that reassociated with chromatin) plays no role in non-allelic HR in telophase in the specific context of MAT switching.

Unfortunately, the role of cohesin re-association with chromatin for the allelic inter-sister repair by HR is not addressed. In the absence of such evidence, the main claims of the paper making up the title (cohesin re-association and HR repair) appear disconnected. Even if the very last sentence of the abstract corrects the false sense from the title and the rest of the abstract that cohesin reconstitution has somehow something to do with efficient HR in late mitosis, I think a general rewriting of the abstract and a different title would better lift any ambiguity about the conclusions of the paper.

Author response:

The following is the authors’ response to the original reviews

We would like to thank the reviewers for taking the time to thoroughly revise our work. We have considered their suggestions carefully and tried our best to respond to them point by point. Based on their recommendations, two major issues came forward: (1) the strength of our claims about the involvement of cohesin in HR-driven repair in late mitosis; and (2) the underlying mechanism that reconstitutes cohesin in late mitosis after DNA damage. In this revision, we focused on the former and left the latter out (yet it is discussed). We considered that the question of how cohesin returns in late mitosis after DNA damage is important and worthy of further research, but it is beyond the scope of this study (as it is the putative role of condensin). Thus, we have focused on buttressing our main claims, as otherwise pointed out by the reviewers. What have we done to strengthen the role of cohesin in late mitotic DSB repair?

(1) We have biologically replicated and quantified the reappearance of Scc1 after DSB generation (new Figure 1e). We have also quantified changes for the other core subunits (new Figure 1c-e).

(2) We now show that the newly synthetized Scc1 serves to assemble back the cohesin complex (new Figure 2a and S1).

(3) We have performed chromatin fractionation and show that cohesin binding to chromatin increases after the HO-induced DSB (new Figure 2b and S2).

(4) We have performed ChIP assays and show that, despite the increase in the chromatin-bound fraction, the HOcs DSB does not recruit new cohesin to the locus (new Figure 2c and S3).

(5) A key assertion in the preprint version was that depleting cohesin using the auxin degron system impairs HR-driven MAT switching. This claim was based on a direct comparison of cultures treated or not with auxin (-/+ IAA). However, during the revision process, we realized that auxin treatment itself could interfere with MAT switching. Firstly, we noticed a diminished HOcs cutting efficiency by HO in +IAA cultures (Figure S6). Secondly, the apparently dramatic delay in gene conversion to MAT_α could actually be related to other undesirable effects of IAA downstream in the repair process. Thus, we decided to repeat this experiment with strains that differ in their response to auxin, so that we could compare all strains in the presence of auxin. We compared four isogenic strains: _SMC3; SMC3-aid*; SMC3 + OsTIR1; and SMC3-aid* + OsTIR1. As a result, we can now show that cohesin depletion does not affect MAT switching (see new Figure 4b-d).

(6) We recently reported a negative chemical interaction between auxin and phleomycin. Auxin appears to diminish the ability of phleomycin to generate DSBs (Comm Biol 2025, doi: 10.1038/s42003-025-08416-x; see Figures S14 and S15 in that paper). While the underlying nature of this interaction is unknown to us (we are working on it), this leads us to omit the coalescence assay included in the preprint version (old Figure 4c), as the diminished coalescence upon IAA addition is actually due to this effect rather than cohesin depletion. This is also in agreement with the new data we include in the revised version, in which we observed only minor changes in cohesin reconstitution and chromatin binding after phleomycin (Figure 2a,b; S1 and S2).  

(7) In addition to addressing these reviewers’ requests, we have better characterized the MAT switching in late mitosis by incorporating the kinetics of _rad9_Δ (deficient in the DNA damage checkpoint), _yku70_Δ (deficient in non-homologous end joining) and _mre11_Δ (deficient in DSB end tethering). The effect of _rad52_Δ (deficient in HR) has been described elsewhere (our iScience 2024, 10.1016/j.isci.2024.110250).

As a result of these new experiments, new figure panels have been added in the main figures and as supplementary figures. To make room for the these panels in the main figures and keep the short report format, the following changes have been made: (i) old figures and new panels have been combined into four main figures, (ii) some panels from the old figures have been moved to supplementary figures, and (iii) some panels have been reordered for the sake of simplicity and fluidity in the main text. 

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The cohesin complex maintains sister chromatid cohesion from S phase to anaphase. Beyond that, DSBs trigger cohesin recruitment and post-replication cohesion at both damage sites and globally, which was originally reported in 2004. In their recent study, Ayra-Plasencia et al reported in telophase, DSBs are repaired via HR with re-coalesced sister chromatids (Ayra-Plasencia & Machín, 2019). In this study, they show that HR occurs in a Smc3-dependent way in late mitosis.

Strengths:

The authors take great advantage of the yeast system, they check the DSB processing and repair of a single DSB generated by HO endonuclease, which cuts the MAT locus in chromosome III. In combination with cell synchronization, they detect the HR repair during G2/M or late mitosis. and the cohesin subunit SMC3 is critical for this repair. Beyond that, full-length Scc1 protein can be recovered upon DSBs.

Weaknesses:

These new results basically support their proposal although with a very limited molecular mechanistic progression, especially compared with their recent work.

Reviewer #2 (Public Review):

Summary:

The manuscript "Cohesin still drives homologous recombination repair of DNA double-strand breaks in late mitosis" by Ayra-Plasencia et al. investigates regulations of HR repair in conditional cdc15 mutants, which arrests the cell cycle in late anaphase/telophase. Using a non-competitive MAT switching system of S. cerevisiae, they show that a DSB in telophase-arrested cells elicits a delayed DNA damage checkpoint response and resection. Using a degron allele of SMC3 they show that MATa-to-alpha switching requires cohesin in this context. The presence of a DSB in telophase-arrested cells leads to an increase in the kleisin subunit Scc1 and a partial rejoining of sister chromatids after they have separated in a subset of cells.

Strengths:

The experiments presented are well-controlled. The induction systems are clean and well thought-out.

Weaknesses:

The manuscript is very preliminary, and I have reservations about its physiological relevance. I also have reservations regarding the usage of MAT to make the point that inter-sister repair can occur in late mitosis.

Regarding these two weaknesses:

- Physiological relevance: This is something we already addressed in our previous research work (Nat Commun. 2019; 10(1):2862. doi: 10.1038/s41467-019-10742-8), and which was further discussed in a follow-up theoretical paper (Bioessays. 2020 ;42(7):e2000021. doi: 10.1002/bies.202000021). In summary, this is physiologically relevant because a DSB in anaphase activates a late-mitotic checkpoint so the DSB can be repaired before cytokinesis. The fact that anaphase is quick and only a minor fraction of cells get a DSB in this cell cycle stage in an asynchronous population does not preclude its importance since it is enough a single mis-repaired DSB in hundreds of cells to mutate a population in an health- or evolution-relevant way.

- MAT system in late mitosis: It was not our intention to use the MAT switching assay to state that inter-sister repair can occur in late-M. The purpose was to address whether HR was fully functional in this non-G2/M non-G1 stage. Having said that, it is very challenging to design a strategy based on sequence-specific DSB to tackle the inter-sister repair in late-M. Any endonuclease-generated DSB is going to cut in both sisters. This is something we also deeply discussed in our previous works (Nat Commun & Bioessays).    

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major points:

(1) Smc3 degradation affects Rad53 activation upon DSBs, and this may directly lead to HR repair deficiency. Smc3 also could be phosphorylated by ATM and functions in DNA damage checkpoint activation, these alternative possibilities should also be tested before addressing the bona fide role of Smc3 in this context.

Our previous data already suggested that Rad53 hyperphosphorylation still occurs after Smc3 degradation (Figure S6). Regardless, the question of whether the DNA damage checkpoint (DDC) may play a distinct role in the MAT switching has been addressed in this revision by comparing RAD9 versus rad9_Δ. Rad9 is a mediator in the DDC required for the activation of Rad53. We have seen that MAT switching in _rad9_Δ is as efficient as in _RAD9 (new Figure S5d-f).

On the other hand, our new results, in which we have compared four different strains with all auxin system combinations in the presence of auxin, show that cohesin depletion does not affect MAT switching. Previously, we compared minus versus plus auxin and noticed diminished HO cutting efficiency. Thus, we repeated this experiment with four isogenic strains (SMC3; SMC3-aid*; SMC3 + OsTIR1; and SMC3-aid* + OsTIR1) that differ in their response to auxin and ability to degrade cohesin, so that we could compare all strains in the presence of auxin. As a result, we can now affirm that cohesin depletion does not affect MAT switching (see new Figure 4b-d). Therefore, HR appears efficient after cohesin depletion.

(2) The requirement of cohesin subunit Smc3 and "coincidently" recovery of Scc1 are not sufficient to claim they act as a cohesin complex in this scenario. CoIP in the chromatin fraction after DSBs to prove the cohesin complex formation is recommended. If they act as a complex, are cohesin loader Scc2/4 required?

We have constructed a SMC3-HA SCC1-myc strain. We have purified the chromatin-bound fraction as well as performing the co-IP. We have found Smc1-acSmc3-Scc1 forms a complex after Scc1 returns, and that at least a fraction of this complex binds to the chromatin in our HO model of DSBs in late anaphase (the cdc15-2 arrest). This is now shown in the new Figures 2a,b and S1,S2.

As for the requirement of Scc2/4, we consider that the mechanisms underlying how Scc1 comes back, how a new cohesin complex is reassembled, and how it can partly bind to the chromatin in late anaphase are beyond the scope of this study and worth pursuing in a follow-up story.

(3) Figure 3b. acetylated SMC3 was prominently detected in the absence of DSBs. During the cohesion cycle, the cohesin was released from chromatin in a separase-dependent manner at the anaphase onset. Released Smc3 was deacetylated by Hos1 subsequently. In principle, the acSMC3 level could be very low in late mitosis.

In that figure (now renumbered as Fig S6), we did detect acetylated Smc3 for the remnant Smc3 still found in late mitosis, however, a direct comparison between the acetylated versus non-acetylated pools was not performed, and would require more sophisticated approaches. Note that blots are distinctly exposed until the band is detected, and that signal intensity is antibody-specific. The presence of an acSmc3 pool in the cdc15-2 arrest is now further confirmed by the new blots in Figures 2a, S1 and S2b.

On the other hand, previous time course experiments from G1 and G2/M releases point out that Smc3 deacetylation is incomplete in anaphase, with up to 30% of acetylated Smc3 remaining (Beckouët et al, 2010 doi:10.1016/j.molcel.2010.08.008). This is consistent with the presence of acSmc3 in the cdc15-2 arrest.   

(4) Did the author examine the acSMC3 levels returning after DSB, as Scc1's levels? If so, how about the Eco1's protein level? Chromatin fractionation could be conducted to check the chromatin-bound SMC3, acSMC3/Eco1, SCC1, SCC1 phosphorylation, and SMC1. These results will tell us whether cohesin functions in DSB repair in late M in a cohesion state.

As stated above, we have now determined that cohesin depletion does not affect HR-driven MAT switching. As for the other questions, yes, we have performed both an assessment of acSmc3 in the pull down and chromatin fractionation, before and after DSBs (new Figures 2a, S1 and S2b). Interestingly, we have noticed a difference between the HO-generated and the phle-generated DSBs. It appears that the former leads to a better reconstituted Smc1-acSmc3-Scc1 complex and more chromatin-bound cohesin. The overall acSmc3 levels do not appear to significantly change in the whole cell extracts, although there could be further posttranslational modifications in telophase (see the changes in intensity between the two acSmc3 bands in Figure S1).

The role of Eco1 has not been directly addressed but is discussed. The main point here is that Eco1 levels may be low after G2/M (e.g., Lyons and Morgan, 2011), but there is still a significant acSmc3 pool in anaphase as Hof1 does not deacetylate all Smc3 (Beckouët et al., 2010). 

(5) Figure 4a, the return of full-length Scc1 is based on a single experiment. What's the mechanism? Inhibition of cleavage or re-expression? How about its mRNA levels?

We have repeated the full-length Scc1 experiment two more times. Now, an expression graph is included as a new Figure 1e. The two other subunits, Smc1 and Smc3, have been assessed as well, with no major changes in abundance (new Figure 1c and d).

We feel that the exact molecular mechanism of how Scc1 returns is beyond the scope of this study, but we discuss that the DDC may either inactivate separase or protect Scc1 against it. Indeed, there is literature that supports both mechanisms (e.g., Heidinger-Pauli et al., 2008 doi:10.1016/j.molcel.2008.06.005; Yam et al., 2020 doi:10.1093/nar/gkaa355).   

Minor points:

(6) FACS data should be shown for all cell synchronization experiments.

From our previous own works, FACS profiles add little to late-M experiments. To properly confirm late-M, microscopy is a must. FACS cannot differentiate between G2/M (metaphase-like), anaphase, telophase and the ensuing G1 (as cdc15-2 cells do not immediately split apart after re-entering G1). In all experiments, Tel samples (late-M cdc15-2 arrest) were characterized by >95% large budded binucleated cells.

(7) Figure 1d, A loading control of Rad53-P in is missing. The "Arrest" samples should be loaded again on the right to confirm the shift of Rad53, but not due to "smiling gels".

It is true that the blot on the right has a right-handed smile; however, it is very clear the presence of the Rad53/Rad53-P partner. Because there is not a full shift from Rad53 to Rad53-P, the concern of misidentifying Rad53-P as a result of a blot smile is unfounded.

(8) Figure 1c, After the HO cut, the resected DNA at the 726 bp site reaches to platform at about 4 hrs, while it still increases at the 5.6 kb site. Thus, it is difficult to conclude that "The time to reach half of the maximum possible resection (t1/2) was ~1 h at 0.7 Kb and ~2.5 h at 5.7 Kb from the DSB, respectively".

We assumed that both loci reach the plateau at 0.8 (which is consistent with other studies), so the t1/2 was calculated when the resected intersected 0.4.

(9) Figure 2b and 2c are wrongly labeled.

We have fixed this (now Fig. 3d and e).

(10) Figure 2d, Double check and make sure the quantitative data reflects the representative result. E.g. in Figure 2b (in fact should be 2c). For instance, in Figure 2b, the MATα signals seem to remain stable from 60' to 180', but they keep increasing in Figure 2d. In Yamaguchi & James E. Haber's paper, the signals and changes of MATa and MATα over time are way stronger compared to this study.

We have double checked this. It is true that the sum of MATα, MATalpha and cut HOcs bands throughout the assay does not have the intensity seen for MATa before the HO induction (Tel), but MATalpha and HOcs signals cannot be established based on the equimolarity of the reaction as all band signals are probe-specific (the best indication of this can be seen in the signal comparison between MAT_α and _MAT distal at Tel). Alternatively, some resected HOcs may remain unrepaired.

As for the referred example (now Figure 3e), note that they are double normalized to ACT1 and MAT_α (Tel), and the _ACT1 band gets fainter after 60’. This explains the increase in the MATalpha quantification in spite of what is apparently seen in the blot.

(11) Typos and fonts: e.g. lines 111-112; line 76 "his link".

We have fixed this. Thanks.

Reviewer #2 (Recommendations For The Authors):

Major concerns:

(1) Physiological relevance. The authors show that HR can happen in the anaphase to telophase interval, yet does it outside of an hours-long artificial arrest upon inactivation of Cdc15? It is this reviewer's understanding that the duration of the anaphase to telophase transition is short, in the order of minutes. In fact, break signaling and resection are delayed by ~1 hour (Fig. 1), which suggests that cells avoid dealing with the damage and engaging in HR in the anaphase-telophase interval. Is there any described physiological context or checkpoint that blocks this transition for extended periods, that would make any of the findings in this paper relevant?

This concern about the physiological relevance was addressed in our previous study (Nat Commun. 2019; 10(1):2862. doi: 10.1038/s41467-019-10742-8). In that paper’s Figure 1, we showed that G1 re-entry after a cdc15-2 release was delayed by several hours when DSBs had been previously generated at the cdc15-2 arrest. We also showed that such a delay depended on Rad9 (i.e., the DNA damage checkpoint). In addition, synchronized (not arrested) cells transiting through anaphase responded to DSB generation by slowing anaphase transition while partly regressing chromosome segregation (Figure S7 in that paper).

(2) Methodological caveats. It is unclear why the authors chose to study DSB-repair in the context of MATa-to-alpha switching (which uses an ectopic donor on the other chromosome arm) as a model for inter-sister repair. It creates a disconnect in the claims of the paper, which means to study inter-sister repair. Studying the kinetics of DSB repair by cytology following low-dose irradiation or radiomimetic drugs would have been a better option. Phleomycin is used in Fig. 4, but the repair kinetics (e.g. Rad52 foci) is not studied.

The MAT switching assay was used here to address how much HR was functional in late-M compared to G2/M (metaphase-like). Then, it was employed to check how cohesin depletion hampers HR in late-M. Even though this is something we already deeply discussed previously (Nat Commun. 2019; 10(1):2862. doi: 10.1038/s41467-019-10742-8; Bioessays. 2020 ;42(7):e2000021. doi: 10.1002/bies.202000021), it is worth recapitulating the methodological challenges that the study of inter-sister repair has in late-M: (i) endonuclease-based DSBs are going to generate two DSBs, one per sister chromatid; (ii) the use of a homologous chromosome without the cutting site as a template is pointless because a sister of the homolog is always going to co-segregate with the broken chromatid, and the same caveat applies for any other ectopic sequence. In this context, the MATa with the HML ectopic intrachromosomal sequence is as valid as any other option, with the advantage that it is a very well-known system.

On the other hand, most of the reviewer’s concerns about the inter-sister repair by cytology and the role of Rad52 was addressed in our previous paper (Nat Commun). Note that our new results about the cohesin role on MAT switching show that this HR-mediated DSB repair does not depend on cohesin (new Figure 4b-d).

(3) Preliminary work. The requirement of cohesin for MAT switching in cdc15 mutants would have warranted several additional experiments. Indeed, Cohesin has been shown to regulate homology search in multiple ways upon DNA damage checkpoint-induced metaphase-arrest (see Piazza et al. Nat Cell Biol 2021 (10.1038/s41556-021-00783-x), not cited in the current manuscript). Consequently, is the effect of cohesin observed in the MAT system specific to telophase or is it true in other cell-cycle phases? What is the mechanism behind this requirement (one may expect it not to depend on the sister since the HML donor is available within the damaged chromatid)? Does cohesin re-accumulate around the DSB site or genome-wide? How does the Esp1 activity decay from anaphase onset? Is cohesin required for the horseshoe folding of chr. III involved in MATa-to-alpha switching? Furthermore, condensin is involved in MATa-specific switching (Li et al. PLoS Genet 2019, 10.1371/journal.pgen.1008339), and condensin remains active on chromatin in cdc15 arrested cells, as shown on chr. XII (Lazar-Stefanita et al. EMBO J. 2017 10.15252/embj.201797342), which calls for determining the impact contribution of condensin in the recoil of the right ch.XII arm (Fig 4c) and on MAT switching.

There are several points here:

- Is the effect of cohesin observed in the MAT system specific to telophase or is it true in other cell-cycle phases?

Our new results show that cohesin depletion does not affect MAT switching when four different strains with all auxin system combinations are compared in the presence of auxin. Previously, when we compared minus versus plus auxin, we noticed diminished HO cutting efficiency. Therefore, we repeated the experiment using four isogenic strains (SMC3, SMC3-aid*, SMC3 + OsTIR1, and SMC3-aid* + OsTIR1), which differ in their response to auxin and ability to degrade cohesin. This allowed us to compare all strains in the presence of auxin. As a result, we can now confirm that cohesin depletion does not affect MAT switching (see the new Figures 4b–d). Therefore, HR appears efficient after cohesin depletion. In agreement, the new ChIPs we have performed do not detect an increment in local cohesin after the HO DSB in telophase (but it does in cells arrested in G2/M).

- What is the mechanism behind this requirement (one may expect it not to depend on the sister since the HML donor is available within the damaged chromatid)?

As just said, we have changed our previous conclusion on cohesin and MAT switching. It was an effect of auxin addition rather than cohesin depletion.

- Does cohesin re-accumulate around the DSB site or genome-wide?

We have performed ChIP around the HOcs. We have found that it does accumulate in G2/M after HO induction, but it does not in telophase (new Figures 2c and S3). As for the global binding of cohesin, our chromatin fractionation data suggest there is ~2-fold increase in Smc1-Smc3, which also binds to the newly formed Scc1, rendering an overall increase in the chromatin-bound canonical complex (new Figures 2b and S2). Altogether, this suggests a genome-wide binding but with little role in the repair of HO DSBs.

- How does the Esp1 activity decay from anaphase onset?

We have not checked this here but it is an interesting question for a follow-up story.

- Is cohesin required for the horseshoe folding of chr. III involved in MATa-to-alpha switching?

Probably not in view of our new data in Figures 2c and 4b-d. The Piazza papers are cited and discussed.

- Contribution of condensin in the recoil of the right ch.XII arm (Fig 4c) and on MAT switching.

The role of condensin, which overtakes some cohesin function in late-M as the reviewer reminds, is worth studying indeed. However, we feel this deserves a separate and focus-on study. We does discuss, though, that condensin loading onto the arms in anaphase may prevent Smc1-Smc3 from loading after DSBs.

Other points:

(4) Is the retrograde behavior in Fig. 4c dependent on recombination?

No, this is something we addressed in our previous paper (see Figure 4 in Nat Commun. 2019; 10(1):2862. doi: 10.1038/s41467-019-10742-8).

(5) Fig 3c: add a scheme of the system.

A scheme was already shown in the old Figure 2a (note that the old Fig 3c is now Fig S6).

(6) Fig 3b: annotate as in Fig 2b.

We have fixed this (now the referred figures are S6a and 3d, respectively).

(7) Authors used IAA concentrations 4- to 8-fold higher than commonly used. Given the solubility of IAA in DMSO (the most commonly used solvent), it is likely that authors treated their cells with >2% DMSO. This is expected to have broad transcriptional and physiological effects on yeast. A comparison of +IAA samples with a mock (DMSO) treatment would be more appropriate than a lack of treatment.

The IAA stock solution was 500 mM in DMSO, so the final DMSO concentration for an 8 mM IAA solution was 1.6% (v/v). Although the stock concentration was high and some precipitation was observed during preparation, we always heated, sonicated, and vigorously vortexed the stock tube before adding IAA to the cultures. Thus, we kept the uncertainty in the final IAA concentration to a minimum.

eLife Assessment

This important study by Zheng et al characterizes a novel Legionella pneumophila effector, Llfat1 (Lpg1387), which binds actin through a newly identified actin-binding domain. Data is convincing; structural analysis of the Llfat1 ABD-F-actin complex enabled the development of this domain as a probe for F-actin. Additionally, the authors show that Llfat1 functions as a lysine fatty acyltransferase targeting small GTPases, highlighting its importance in both bacterial pathogenesis and cytoskeletal biology.

Reviewer #1 (Public review):

The manuscript by Zeng et al. describes the discovery of an F-actin-binding Legionella pneumophila effector, which they term Lfat1. Lfat1 contains a putative fatty acyltransferase domain that structurally resembles the Rho-GTPase Inactivation (RID) domain toxin from Vibrio vulnificus, which targets small G-proteins. Additionally, Lfat1 contains a coiled-coil (CC) domain.

The authors identified Lfat1 as an actin-associated protein by screening more than 300 Legionella effectors, expressed as GFP-fusion proteins, for their co-localization with actin in HeLa cells. Actin binding is mediated by the CC domain, which specifically binds to F-actin in a 1:1 stoichiometry. Using cryo-EM, the authors determined a high-quality structure of F-actin filaments bound to the actin-binding domain (ABD) of Lfat1. The structure reveals that actin binding is mediated through a hydrophobic helical hairpin within the ABD (residues 213-279). A Y240A mutation within this region increases the apparent dissociation constant by two orders of magnitude, indicating a critical role for this residue in actin interaction.

The ABD alone was also shown to strongly associate with F-actin upon overexpression in cells. The authors used a truncated version of the Lfat1 ABD to engineer an F-actin-binding probe, which can be used in a split form. Finally, they demonstrate that full-length Lfat1, when overexpressed in cells, fatty acylates host small G-proteins, likely on lysine residues.

Comments on revisions:

Since LFAT1 cannot be produced in E. coli, it may be worth considering immunoprecipitating the protein from mammalian cells to see if it has activity in vitro. Presumably, actin will co-IP but the actin binding mutant can also be used. These are just suggestions to improve an already solid manuscript. Otherwise, I am happy with the paper.

Reviewer #2 (Public review):

Summary:

The manuscript by Zheng et al reports the structural and biochemical study of a novel effectors from the bacterial pathogen Legionella pneumophila. The authors continued from results from their earlier screening for L. pneumophila proteins that that affect host F-actin dynamics to show that Llfat1 (Lpg1387) interacts with actin via a novel actin-binding domain (ABD). The authors also determined the structure of the Lfat1 ABD-F-actin complex, which allowed them to develop this ABD as probe for F-actin. Finally, the authors demonstrated that Llfat1 is a lysine fatty acyltransferase that targets several small GTPases in host cells. Overall, this is a very exciting study and should be of great interest to scientists in both bacterial pathogenesis and actin cytoskeleton of eukaryotic cells.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

(1) Legionella effectors are often activated by binding to eukaryote-specific host factors, including actin. The authors should test the following: a) whether Lfat1 can fatty acylate small G-proteins in vitro; b) whether this activity is dependent on actin binding; and c) whether expression of the Y240A mutant in mammalian cells affects the fatty acylation of Rac3 (Figure 6B), or other small G-proteins.

We were not able to express and purify the full-length recombinant Lfat1 to perform fatty acylation of small GTPases in vitro. However, In cellulo overexpression of the Y240A mutant still retained ability to fatty acylate Rac3 and another small GTPase RheB (see Figure 6-figure supplement 2). We postulate that under infection conditions, actin-binding might be required to fatty acylate certain GTPases due to the small amount of effector proteins that secreted into the host cell.

(2) It should be demonstrated that lysine residues on small G-proteins are indeed targeted by Lfat1. Ideally, the functional consequences of these modifications should also be investigated. For example, does fatty acylation of G-proteins affect GTPase activity or binding to downstream effectors?

We have mutated K178 on RheB and showed that this mutation abolished its fatty acylation by Lfat1 (see Author response image 1 below). We were not able to test if fatty acylation by Lfat1 affect downstream effector binding.

Author response image 1.

(3) Line 138: Can the authors clarify whether the Lfat1 ABD induces bundling of F-actin filaments or promotes actin oligomerization? Does the Lfat1 ABD form multimers that bring multiple filaments together? If Lfat1 induces actin oligomerization, this effect should be experimentally tested and reported. Additionally, the impact of Lfat1 binding on actin filament stability should be assessed. This is particularly important given the proposed use of the ABD as an actin probe.

The ABD domain does not form oligomer as evidenced by gel filtration profile of the ABD domain. However, we do see F-actin bundling in our in vitro -F-actin polymerization experiment when both actin and ABD are in high concentration (data not shown). Under low concentration of ABD, there is not aggregation/bundling effect of F-actin.

(4) Line 180: I think it's too premature to refer to the interaction as having "high specificity and affinity." We really don't know what else it's binding to.

We have revised the text and reworded the sentence by removing "high specificity and affinity."

(5) The authors should reconsider the color scheme used in the structural figures, particularly in Figures 2D and S4.

Not sure the comments on the color scheme of the structure figures.

(6) In Figure 3E, the WT curve fits the data poorly, possibly because the actin concentration exceeds the Kd of the interaction. It might fit better to a quadratic.

We have performed quadratic fitting and replaced Figure 3E.

(7) The authors propose that the individual helices of the Lfat1 ABD could be expressed on separate proteins and used to target multi-component biological complexes to F-actin by genetically fusing each component to a split alpha-helix. This is an intriguing idea, but it should be tested as a proof of concept to support its feasibility and potential utility.

It is a good suggestion. We plan to thoroughly test the feasibility of this idea as one of our future directions.

(8) The plot in Figure S2D appears cropped on the X-axis or was generated from a ~2× binned map rather than the deposited one (pixel size ~0.83 Å, plot suggests ~1.6 Å). The reported pixel size is inconsistent between the Methods and Table 1-please clarify whether 0.83 Å refers to super-resolution.

Yes, 0.83 Å is super-resolution.  We have updated in the cryoEM table

Reviewer #2:

Weaknesses:

(1) The authors should use biochemical reactions to analyze the KFAT of Llfat1 on one or two small GTPases shown to be modified by this effector in cellulo. Such reactions may allow them to determine the role of actin binding in its biochemical activity. This notion is particularly relevant in light of recent studies that actin is a co-factor for the activity of LnaB and Ceg14 (PMID: 39009586; PMID: 38776962; PMID: 40394005). In addition, the study should be discussed in the context of these recent findings on the role of actin in the activity of L. pneumophila effectors.

We have new data showed that Actin binding does not affect Lfat1 enzymatic activity. (see response to Reviewer #1). We have added this new data as Figure S7 to the paper. Accordingly, we also revised the discussion by adding the following paragraph.

“The discovery of Lfat1 as an F-actin–binding lysine fatty acyl transferase raised the intriguing question of whether its enzymatic activity depends on F-actin binding. Recent studies have shown that other Legionella effectors, such as LnaB and Ceg14, use actin as a co-factor to regulate their activities. For instance, LnaB binds monomeric G-actin to enhance its phosphoryl-AMPylase activity toward phosphorylated residues, resulting in unique ADPylation modifications in host proteins  (Fu et al, 2024; Wang et al, 2024). Similarly, Ceg14 is activated by host actin to convert ATP and dATP into adenosine and deoxyadenosine monophosphate, thereby modulating ATP levels in L. pneumophila–infected cells (He et al, 2025). However, this does not appear to be the case for Lfat1. We found that Lfat1 mutants defective in F-actin binding retained the ability to modify host small GTPases when expressed in cells (Figure S7). These findings suggest that, rather than serving as a co-factor, F-actin may serve to localize Lfat1 via its actin-binding domain (ABD), thereby confining its activity to regions enriched in F-actin and enabling spatial specificity in the modification of host targets.”

(2) The development of the ABD domain of Llfat1 as an F-actin domain is a nice extension of the biochemical and structural experiments. The authors need to compare the new probe to those currently commonly used ones, such as Lifeact, in labeling of the actin cytoskeleton structure.

We fully agree with the reviewer’s insightful suggestion. However, a direct comparison of the Lfat1 ABD domain with commonly used actin probes such as Lifeact, as well as evaluation of the split α-helix probe (as suggested by Reviewer #1), would require extensive and technically demanding experiments. These are important directions that we plan to pursue in future studies.

For all other minors, we have made corrections/changes in our revised text and figures.

eLife Assessment

This study provides important insights into bacterial genome evolution by analyzing single-cell genome sequences of cyanobacteria from Yellowstone hot springs. Using compelling evidence, the authors demonstrate that both homologous recombination within species and frequent hybridization across species are major drivers of genome diversification. Despite the challenges that are inherent to sparse and fragmented single-cell data, the analyses are thorough, carefully controlled, and supported by multiple complementary approaches, making the conclusions highly robust. This work represents a significant advance in our understanding of microbial evolution in natural environments.

Reviewer #1 (Public review):

Summary:

What are the overarching principles by which prokaryotic genomes evolve? This fundamental question motivates the investigations in this excellent piece of work. While it is still very common in this field to simply assume that prokaryotic genome evolution can be described by a standard model from mathematical population genetics, and fit the genomic data to such a model, a smaller group of researchers rightly insists that we should not have such preconceived ideas and instead try to carefully look at what the genomic data tell us about how prokaryotic genomes evolve. This is the approach taken by the authors of this work. Lacking a tight theoretical framework, the challenge of such approaches is to device analysis methods that are robust to all our uncertainties about what the underlying evolutionary dynamics might be.

The authors here focus on a collection of ~300 single-cell genomes from a relatively well-isolated habitat with a relatively simple species composition, i.e. cyanobacteria living in hot springs in Yellowstone National Park. They convincingly demonstrate that the relative simplicity of this habitat increases our ability to interpret what the genomic data tells us about the evolutionary dynamics.

Using a very thorough and multi-faceted analysis of these data, the authors convincingly show that there are three main species of Synechococcus cyanobacteria living in this habitat, and that apart from very frequent recombination within each species (which is in line with insights from other recent studies) there is also a remarkably frequent occurrence of hybridization events between the different species, and with as of yet unindentified other genomes. Moreover, these hybridization events drive much of the diversity within each species. The authors also show convincing evidence that many of these hybridization events are not neutral but are driven by natural selection.

Strengths:

The great strength of this paper is that, by not making any preconceived assumptions about what the evolutionary dynamics is expected to look like, but instead devicing careful analysis methods to tease apart what the data tells us about what has happened in the evolution in these genomes, highly novel and unexpected results are obtained, i.e. the major role of hybridization across the 3 main species living in this habitat.

The analysis is very thorough and reading the detailed descriptions in the appendices it is clear that these authors took a lot of care in using these methods and avoiding the pitfalls that unfortunately affect many other studies in this research area.

The picture of the evolutionary dynamics of these three Synechococcus species that emerges from this analysis is quite novel and surprising. I think this study is a major stepping stone toward development of more realistic quantitative theories of genome evolution in prokaryotes.

The analysis methods that the authors employ are also partially quite novel and will no doubt by very valuable for analysis of many other datasets.

Weaknesses:

The main text is tight and concise, but this sort of hides the very large amount of careful complementary analyses that went into the conclusions presented in the main text. The appendices are quite well written but they are substantial, so that really understanding the paper is not an easy read. However, I do not really think the authors can be faulted for this. The topic is complex and a lot of care is required to make sure conclusions are valid.

A very interesting observation is that a lot of hybridization events (i.e. about half) originate from species other than the alpha, beta, and gamma Synechococcus species from which the genomes that are analyzed here derive. For this to occur, these other species must presumably also be living in the same habitat and must be relatively abundant. But if they are, why are they not being captured by the sampling? I did not see a clear explanation for this very common occurrence of hybridization events from outside of these Synechococcus species. The authors raise the possibility that these other species used to live in these hot springs but are now extinct or that the occur in other pools. I guess this is possible but I still find it puzzling and wonder if these donors could have been filtered out at some step of the experimental and/or analysis procedures.

Reviewer #2 (Public review):

Summary.

Birzu et al. describe two sympatric hotspring cyanobacterial species ("alpha" and "beta") and infer recombination across the genome, including inter-species recombination events (hybridization) based on single-cell genome sequencing. The evidence for hybridization is strong and the authors took care to control for artefacts such as contamination during sequencing library preparation. Despite hybridization, the species remain genetically distinct from each other. The authors also present evidence for selective sweeps of genes across both species - a phenomenon which is widely observed for antibiotic resistance genes in pathogens, but rarely documented in environmental bacteria.

Strengths.

This manuscript describes some of the most thorough and convincing evidence to date of recombination happening within and between co-habitating bacteria in nature. Their single-cell sequencing approach allows them to sample the genetic diversity from two dominant species. Although single-cell genome sequences are incomplete, they contain much more information about genetic linkage than typical short-read shotgun metagenomes, enabling a reliable analysis of recombination. The authors also go to great lengths to quality-filter the single-cell sequencing data and to exclude contamination and read mismapping as major drivers of the signal of recombination. This is a fascinating dataset with intricate analyses showing the great extent of between-species hybridization that is possible in nature.

Weaknesses.

This revised version is much improved, with a much clearer flow and organisation within both the main text and supplement. The remaining weaknesses that I note below are certainly not critical, but are simply useful context for the reader to keep in mind.

My main concern is that the evidence for selection on the hybridized genes is incomplete and statements about the 'overwhelming evidence for the crucial role played by selection' (lines 334-5) are a bit overstated. What fraction of the hybridization events were driven by positive selection? The breakdown of hard (15%) vs soft (85%) sweeps is given, out of 153 (as sidenote, it is not clear if this is 153 genes or events, troughs, etc.). But how many of the hybridization events (or genes) have evidence for a selective sweep relative to those that do not? I recognize that this may be a hard question to answer, because it may be statistically easier to identify a hybridization event that rises to high frequency due to positive selection from a neutral event that remains rare. Even a rough estimate would be useful; would it be something like 153 out of the number of core genes tested (~700)?

Regardless, I think that Figure 6 (A and B) could benefit from comparison to a neutral model, including hybridization but no selection to see if a similar pattern (notably, higher synonymous diversity in alpha troughs compared to the backbone) could arise due to hybridization alone without selection.

An implicit assumption in microbiology is often that cross-species recombination events are driven by selection. The authors recognize that "diversity troughs resulted from selective sweeps [...] likely overcame mechanistic barriers to recombination, genetic incompatibilities, and ecological differences" (lines 335-7) and thus would not be retained unless they had some strong adaptive value to offset these costs. There are surprisingly few tests of the hypothesis that cross-species recombination events tend to be driven by selection. An analysis of Streptococcus spp. genomes showed that between-species recombination events tended to be accompanied by positive selection, whereas most within-species events were not (Shapiro et al. Trends in Microbiology 2009; reanalysis of data from Lefebure & Stanhope, Genome Biology 2007). There are probably other examples out there, but the authors could highlight that they provide rare data to support a common expectation.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

What are the overarching principles by which prokaryotic genomes evolve? This fundamental question motivates the investigations in this excellent piece of work. While it is still very common in this field to simply assume that prokaryotic genome evolution can be described by a standard model from mathematical population genetics, and fit the genomic data to such a model, a smaller group of researchers rightly insists that we should not have such preconceived ideas and instead try to carefully look at what the genomic data tell us about how prokaryotic genomes evolve. This is the approach taken by the authors of this work. Lacking a tight theoretical framework, the challenge of such approaches is to devise analysis methods that are robust to all our uncertainties about what the underlying evolutionary dynamics might be.

The authors here focus on a collection of ~300 single-cell genomes from a relatively well-isolated habitat with relatively simple species composition, i.e. cyanobacteria living in hotsprings in Yellowstone National Park, and convincingly demonstrate that the relative simplicity of this habitat increases our ability to interpret what the genomic data tells us about the evolutionary dynamics.

Using a very thorough and multi-faceted analysis of these data, the authors convincingly show that there are three main species of Synechococcus cyanobacteria living in this habitat, and that apart from very frequent recombination within each species (which is in line with insights from other recent studies) there is also a remarkably frequent occurrence of hybridization events between the different species, and with as of yet unidentified other genomes. Moreover, these hybridization events drive much of the diversity within each species. The authors also show convincing evidence that these hybridization events are not neutral but are driven by selected by natural selection.

Strengths:

The great strength of this paper is that, by not making any preconceived assumptions about what the evolutionary dynamics is expected to look like, but instead devising careful analysis methods to tease apart what the data tells us about what has happened in the evolution in these genomes, highly novel and unexpected results are obtained, i.e. the major role of hybridization across the 3 main species living in this habitat.

The analysis is very thorough and reading the detailed supplementary material it is clear that these authors took a lot of care in devising these methods and avoiding the pitfalls that unfortunately affect many other studies in this research area.

The picture of the evolutionary dynamics of these three Synechococcus species that emerge from this analysis is highly novel and surprising. I think this study is a major stepping stone toward the development of more realistic quantitative theories of genome evolution in prokaryotes.

The analysis methods that the authors employ are also partially novel and will no doubt be very valuable for analysis of many other datasets.

We thank the reviewer for their appreciation of our work.

Weaknesses:

I feel the main weakness of this paper is that the presentation is structured such that it is extremely difficult to read. I feel readers have essentially no chance to understand the main text without first fully reading the 50-page supplement with methods and 31 supplementary materials. I think this will unfortunately strongly narrow the audience for this paper and below in the recommendations for the authors I make some suggestions as to how this might be improved.<br /> A very interesting observation is that a lot of hybridization events (i.e. about half) originate from species other than the alpha, beta, and gamma Synechococcus species from which the genomes that are analyzed here derive. For this to occur, these other species must presumably also be living in the same habitat and must be relatively abundant. But if they are, why are they not being captured by the sampling? I did not see a clear explanation for this very common occurrence of hybridization events from outside of these Synechococcus species. The authors raise the possibility that these other species used to live in these hot springs but are now extinct. I'm not sure how plausible this is and wonder if there would be some way to find support for this in the data (e.g that one does not observe recent events of import from one of these unknown other species). This was one major finding that I believe went without a clear interpretation.

We agree with the reviewer that the extent of hybridization with other species is surprising. While we do feel that our metagenome data provide convincing evidence that “X” species are not present in MS or OS, we cannot currently rule out the presence of X in other springs. In the revision we explicitly mention the alternative hypothesis (Lines 239-242).

The core entities in the paper are groups of orthologous genes that show clear evidence of hybridization. It is thus very frustating that exactly the methods for identifying and classifying these hybridization events were really difficult to understand (sections I and V of the supplement). Even after several readings, I was unsure of exactly how orthogroups were classified, i.e. what the difference between M and X clusters is, what a `simple hybrid' corresponds to (as opposed to complex hybrids?), what precisely the definitions of singlet and non-singlet hybrids are, etcetera. It also seems that some numbers reported in the main text do not match what is shown in the supplement. For example, the main text talks about "around 80 genes with more than three clusters (SM, Sec. V; fig. S17).", but there is no group with around 80 genes shown in Fig S17! And similarly, it says "We found several dozen (100 in α and 84 in β) simple hybrid loci" and I also cannot match those numbers to what is shown in the supplement. I am convinced that what the authors did probably made sense. But as a reader, it is frustrating that when one tries to understand the results in detail, it is very difficult to understand what exactly is going on. I mention this example in detail because the hybrid classification is the core of this paper, but I had similar problems in other sections.

We thank the reviewer for pointing out these issues with our original presentation. In the revision, we have redone most of the analysis to simplify the methods and check the consistency of the results. We did not find any qualitative differences in our results after reanalysis, but some of the numbers for different hybridization patterns have changed. The most notable difference is an increase in the number of alpha-gamma simple hybrids and a corresponding decrease in mixed-species clusters (now labeled mosaic hybrids). These transfers are difficult to assign because we only have access to a single gamma genome. We have added a short explanation of this point in Lines 219-222.

To improve the presentation, we significantly expanded the “Results” section to better explain our analysis and the different steps we take. We included two additional figures (Figs. 3 and 4) that illustrate the different types of hybrids and the heterogeneity in the diversity of alpha which is discussed in the main text and is important for interpreting our results. We also included two additional figures (Figs. 2 and 6) that were previously in the Appendix but were mentioned in the main text. We believe these changes should address most of the issues raised by the reviewer and hopefully make the manuscript easier to read.

Although I generally was quite convinced by the methods and it was clear that the authors were doing a very thorough job, there were some instances where I did not understand the analysis. For example, the way orthogroups were built is very much along the lines used by many in the field (i.e. orthoMCL on the graph of pairwise matchings, building phylogenies of connected components of the graph, splitting the phylogenies along long branches). But then to subdivide orthogroups into clusters of different species, the authors did not use the phylogenetic tree already built but instead used an ad hoc pairwise hierarchical average linkage clustering algorithm.

The reviewer is correct that there is an unexplained discrepancy between the clustering methods we used at different steps in our pipeline. We followed previous work by using phylogenetic distances for the initial clustering of orthogroups. On these scales we expect hybridization to play a minor role and phylogenetic distances to correlate reasonably well with evolutionary divergence. However, because of the extensive hybridization we observed, the use of phylogenetic models for species clustering is more difficult to justify. We therefore chose to simply use pairwise nucleotide distances, which make fewer assumptions about the underlying evolutionary processes and should be more robust. We have briefly explained our reasoning and the details of our clustering method in the revision (Lines 182-190).

Reviewer #2 (Public Review):

Summary:

Birzu et al. describe two sympatric hotspring cyanobacterial species ("alpha" and "beta") and infer recombination across the genome, including inter-species recombination events (hybridization) based on single-cell genome sequencing. The evidence for hybridization is strong and the authors took care to control for artefacts such as contamination during sequencing library preparation. Despite hybridization, the species remain genetically distinct from each other. The authors also present evidence for selective sweeps of genes across both species - a phenomenon which is widely observed for antibiotic resistance genes in pathogens, but rarely documented in environmental bacteria.

Strengths:

This manuscript describes some of the most thorough and convincing evidence to date of recombination happening within and between cohabitating bacteria in nature. Their single-cell sequencing approach allows them to sample the genetic diversity from two dominant species. Although single-cell genome sequences are incomplete, they contain much more information about genetic linkage than typical short-read shotgun metagenomes, enabling a reliable analysis of recombination. The authors also go to great lengths to quality-filter the single-cell sequencing data and to exclude contamination and read mismapping as major drivers of the signal of recombination.

We thank the reviewer for their appreciation of our work.

Weaknesses:

Despite the very thorough and extensive analyses, many of the methods are bespoke and rely on reasonable but often arbitrary cutoffs (e.g. for defining gene sequence clusters etc.). Much of this is warranted, given the unique challenges of working with single-cell genome sequences, which are often quite fragmented and incomplete (30-70% of the genome covered). I think the challenges of working with this single-cell data should be addressed up-front in the main text, which would help justify the choices made for the analysis.

We have significantly expanded the “Results” section to better justify and explain the choices we made during our analysis. We hope these changes address the reviewer’s concerns and make the manuscript more accessible to readers.

The conclusions could also be strengthened by an analysis restricted to only a subset of the highest quality (>70% complete) genomes. Even if this results in a much smaller sample size, it could enable more standard phylogenetic methods to be applied, which could give meaningful support to the conclusions even if applied to just ~10 genomes or so from each species. By building phylogenetic trees, recombination events could be supported using bootstraps, which would add confidence to the gene sequence clustering-based analyses which rely on arbitrary cutoffs without explicit measures of support.

It seems to us that the reviewer’s suggestion presupposes that the recombination events we find can be described as discrete events on an asexual phylogeny, similar to how rare mutations are treated in standard phylogenetic inference. Popular tools, such as ClonalFrame and its offshoots, have attempted to identify individual recombination events starting from these assumptions. But the main conclusion of both our linkage and SNP block analysis is that the ClonalFrame assumptions do not hold for our data. Under a clonal frame, the SNP blocks we observe should be perfectly linked, similar to mutations on an asexual tree. But our results in Fig. 7D show the opposite. Part of the issue may have been that in our original presentation, we only briefly discuss the results of our linkage analysis and refer readers to the Appendix for more details. To fix this issue we have added an extra figure (Fig. 2), showing rapid linkage decrease in both species and that at long distances the linkage values are essentially identical to the unlinked case, similar to sexual populations. We hope that this change will help clarify this point.

The manuscript closes without a cartoon (Figure 4) which outlines the broad evolutionary scenario supported by the data and analysis. I agree with the overall picture, but I do think that some of the temporal ordering of events, especially the timing of recombination events could be better supported by data. In particular, is there evidence that inter-species recombination events are increasing or decreasing over time? Are they currently at steady-state? This would help clarify whether a newly arrived species into the caldera experiences an initial burst of accepting DNA from already-present species (perhaps involving locally adaptive alleles), or whether recombination events are relatively constant over time.

The reviewer raises some very interesting questions about the dynamics of recombination in the population, which we hope to pursue in future work. We have added this as an open question in the Discussion (Lines 365-382).

These questions could be answered by counting recombination events that occur deeper or more recently in a phylogenetic tree.

The reviewer here seems to presuppose that recombination is rare enough that a phylogenetic tree can reliably be inferred, which is contrary to our linkage analysis (see the response to an earlier comment). Perhaps the reviewer missed this point in our original manuscript since it was discussed primarily in the Appendix. See also our response to a previous comment by the reviewer.

The cartoon also shows a 'purple' species that is initially present, then donates some DNA to the 'blue' species before going extinct. In this model, 'purple' DNA should also be donated to the more recently arrived 'orange' species, in proportion to its frequency in the 'blue' genome. This is a relatively subtle detail, but it could be tested in the real data, and this may actually help discern the order of the inferred recombination events.

We have included an extra figure in the main text (Fig. 6) that addresses the question of timing of events. A quantitative test of our cartoon model along the lines the reviewer suggested would certainly be worthwhile and we hope to do that in future work.  

The abstract also makes a bold claim that is not well-supported by the data: "This widespread mixing is contrary to the prevailing view that ecological barriers can maintain cohesive bacterial species..." In fact, the two species are cohesive in the sense that they are identifiable based on clustering of genome-wide genetic diversity (as shown in Fig 1A). I agree that the mixing is 'widespread' in the sense that it occurs across the genome (as shown in Figure 2A) but it is clearly not sufficient to erode species boundaries. So I believe the data is consistent with a Biological Species Concept (sensu Bobay & Ochman, Genome Biology & Evolution 2017) that remains 'fuzzy' - such that there are still inter-species recombination events, just not sufficient to erode the cohesion of genomic clusters. Therefore, I think the data supports the emerging picture of most bacteria abiding by some version of a BSC, and is not particularly 'contrary' to the prevailing view.

We have revised the phrase mentioned by the reviewer to “prevent genetic mixture between bacterial species,” which more accurately represents our conclusions. 

The final Results paragraph begins by posing a question about epistatic interactions, but fails to provide a definitive answer to the extent of epistasis in these genomes. Quantifying epistatic effects in bacterial genomes is certainly of interest, but might be beyond the scope of this paper. This could be a Discussion point rather than an underdeveloped section of the Results.

We agree with the reviewer that an exhaustive analysis of epistasis in the population is beyond the scope of the manuscript. Our original intention was to answer whether SNP blocks we discovered showed evidence of strong linkage, as might be expected if only a small number of strains are present in the population. In light of the previous comments by the reviewer regarding the consistency with the clonal frame hypothesis, we believe this is especially relevant for our results. Moreover, the results we found‑especially for the beta population‑were quite conclusive: SNP block linkages in beta are indistinguishable from an unlinked model. To avoid misdirecting the reader about the significance of our results, we have revised the relevant paragraph (Lines 316-319).

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

Although I am entirely convinced of the validity of the results, methodology, and interpretations presented in this work, I must say I found the paper very hard to read. And I think I am really quite familiar with these kinds of approaches. I fear that for people other than experts on these kinds of comparative genomic analyses, this paper will be almost impossible to read. With the aim of expanding the audience for this compelling work, I think the authors might want to consider ways to improve the presentation.

At the end of a long project, the obtained results typically form a web of mutual interconnections and dependencies and one of the key challenges in presenting the results in a paper is having to untangle this web of connected results and analysis into a linear ordered narrative so that, at any point in the narrative, understanding the next point only depends on previous points in the narrative. I frankly feel that this paper fails at this.

The paper reads to me as if one author put together the supplement by essentially writing a report of all the analyses that were done together with supplementary figures summarizing all those analyses, and that another author then wrote the main text by using the materials in the supplement almost in the way a cook uses ingredients for a dish. Almost every other sentence in the main text refers to results in the (31!) supplementary figures and can only be understood by reading the appropriate corresponding sections in the supplementary materials. I found it essentially impossible to read the main text without having first read the entire 50-page supplement.

I think the paper could be hugely improved by trying to restructure the presentation so as to make it more linear. The main text can be expanded to include a summary of the crucial methods and analysis results from the supplement needed to understand the narrative in the main text. For example, as it currently stands it is really challenging to understand what is shown in figures 2 and 3 of the main text without having to first read a very substantial part of the supplement. Figure 3, even after having read the relevant sections in the supplement, took me quite a while to understand and almost felt like a puzzle to decypher. Rethinking which parts of the supplement are really necessary would also help. Finally, it would also help if the terminology was kept as simple, transparent, and consistent as possible.

I understand that my suggestion to thoroughly reorganize the presentation may feel like a big hassle, but I am afraid that in its current form, these important results are essentially rendered inaccessible to all but a small group of experts in this area. This paper deserves a wider readership.

We thank the reviewer for these valuable suggestions. In the revision, we have significantly expanded and restructured the “Results” section to make the presentation more linear, as the reviewer suggested (see our reply to the public comment by the reviewer for details). We hope these changes will make the manuscript easier to read.

Reviewer #2 (Recommendations For The Authors):

I found this paper challenging to follow since the main text was so condensed and the supplementary material so extensive. Given that eLife does not impose strong limits on the length of the main text, I suggest moving some key sections from the supplement into the main text to make it easier for the reader to follow rather than flipping back and forth. Adding to the confusion, supplementary figures were referenced out of order in the main text (e.g. S23 is referenced before S1). Please check the numbering and ensure figures are mentioned in the main text in the correct order.

We thank the reviewer for their feedback on the presentation of the results. In response to similar comments from Reviewer #1, we have significantly expanded and restructured the “Results” section to make it easier to read (see also our responses to Reviewer #1).

Page 2: The term 'coevolution' is typically reserved for two species that mutually impose selective pressures on one another (e.g. predator-prey interactions; see Janzen, Evolution 1980). In the context of these two cyanobacterial species, it's not clear that this is the case so I would simply refer to them 'cohabitating' or being sympatric in the same environment.

It is true that the term "coevolution” has become associated with predator-prey interactions, as the reviewer said. However, we feel that in our case “coevolution” fairly accurately describes the continual hybridization over long time scales we observe. We have therefore chosen to keep the term.

Page 3: The authors mention that the gamma SAG is ~70% complete, which turns out to be quite high. It would be useful to mention early in the Results the mean/median completeness across SAGs, and how this leads to some challenges in analysing the data. Some of the material from the Supplement could be moved into the Results here.

We have added a short note on the completeness in the Results (Lines 153-154). We have also added an extra figure in Appendix 1 with the completeness of all the SAGs for interested readers.

I was left puzzled by the sentence: "Alternatively, high rates of recombination could generate different genotypes within each genome cluster that are adapted to different temperatures, with the relative frequencies of each cluster being only a correlated and not a causal driver of temperature adaptation." This is suggesting that individual genes or alleles, rather than entire genomes, could be adapted to temperature. But figure 1B seems to imply that the entire genome is adapted to different temperatures. Anyway, this does not seem to be a key point and could probably be removed (or clarified if the authors deem this an important point, which I failed to understand).

We have revised this section to clarify the alternative hypothesis mentioned by the reviewer (Lines 100-103).

Page 4. 'Several dozen' hybrid genes were found, but please also specify how many genes were tested. In general, it would be good to briefly outline the sample size (SAGs or genes) considered for each analysis.

We have added the total numbers of genes we analyzed at each step of our analysis.

'Mosaic hybrid loci' are mentioned alongside the issue of poor alignment. Presumably, the mosaic hybrid loci are first filtered to remove the poor alignments? This should be specified, and please mention how many loci are retained before/after this filter.

We thank the reviewer for highlighting this important point. In the revision, we have implemented a more aggressive filtering of genes with poor alignments. We have added an extra paragraph to Appendix 1 (step 5 in the pipeline analysis) briefly explaining the issue.

Page 5. "By contrast, the diversity of mosaic loci was typical of other loci within beta, suggesting most of the beta genome has undergone hybridization." Please point to the data (figure) to support this statement.

We have restructured our discussion of the different hybrid loci so this comment is no longer relevant. In case the reviewer is interested, the synonymous diversity within beta was 0.047, while in mosaic hybrids it was 0.064.

Page 6. "The largest diversity trough contained 28 genes." Since this trough is discussed in detail and seems to be of interest, it would be nice to illustrate it, perhaps as an inset in Figure 2 or as a separate figure. If I understood correctly, this trough includes genes (in a nitrogen-fixation pathway) that are present in all genomes, but are exchanged by homologous recombination. So I don't think it's correct to say that the "ancestors acquired the ability to fix nitrogen." Rather, the different alleles of these same genes were present in the ancestor. So perhaps there was a selective sweep involving alleles in this region that provided adaptation to local nitrogen sources or concentrations, but not a gain of new genes. Perhaps I misunderstood, in which case clarification would be appreciated.

The reviewer raises an interesting possibility. We agree that it is in principle possible that the ancestor contained the nitrogen fixation genes and the selective sweep simply replaced the ancestral alleles. In this particular case, there is additional evidence that the entire pathway was acquired around roughly the same time from gene order. The gene order between alpha and beta is almost entirely different, with only a few segments containing more than 2-3 genes in the same order, as shown by Bhaya et al. 2007 and confirmed by additional unpublished analysis of the SAGs. One of the few exceptions is the nitrogen fixation pathway, which has essentially the same gene order over more than 20 kbp. Thus, if the ancestor of both alpha and beta contained the nitrogen-fixation pathway, we would expect these genes to be scatter across the genome. We have revised the sentences in question to clarify this point (Lines 260-271).

Page 6. Last paragraph on epistasis references Fig 3C, but I believe it should be Fig 3D.

Fixed.

Page 7. Figure 3 legend. "Note that alpha-2 is identical to gamma here." I believe it should be beta, not gamma.

The reviewer is correct. We have fixed this error.

Page 8. What is the evidence for "at least six independent colonizers"? I could not find the data supporting this claim.

The statement mentioned by the reviewer was based on the maximum number of species clusters we identified in different core genes. However, during the revision, we found that only a handful of genes contained five or more clusters. We did find several tens of genes with four clusters. In addition, Rosen et al. (2018) also found additional 16S clusters at low frequency in the same springs. Based on these results we conservatively estimate that at least four independent strains colonized the caldera, but the number could be much greater. We have revised the text in question accordingly (Lines 336-339) and added Fig. 2 in Appendix 1 to support the conclusion.

Page 9. Line 200: "acting to homogenize the population." It should be specified that the population is only homogenized at these introgressed loci, not genome-wide. Otherwise, the genome-wide species clusters seen in Fig 1 would not be maintained.

It is true that the selective sweeps that lead to diversity throughs only homogenize the introgressed loci. But other hybrid segments could also rise to high frequency in the population during the sweep through hitchhiking. The fact that we observe SNP blocks generated through secondary recombination events of introgressed segments throughout the genome supports this view. While we do not fully understand the dynamics of this process currently, we do feel that the current evidence supports the statement that mixing is occurring throughout the genome and not just at a few loci so we have kept the original statement.

The final sentence (lines 221-222) is vague and uninformative. On the one hand, "investigating whether hybridization plays a major role" is what the current manuscript has already done - depending on what is meant by 'major' (how much of the genome? Or whether there are ecological implications?). It is also not clear what is meant by a predictive theory and 'possible evolutionary scenarios. This should be elaborated upon, otherwise, it is not clear what the authors mean. Otherwise, this sentence could be cut.

We thank the reviewer for their feedback. One possible source of confusion could be that in this sentence we were referring to detecting hybridization in other communities. We have changed “these communities” to “other communities” to make this clearer.

Supplement.

Broadly speaking, I appreciate the thorough and careful analysis of the single cell data. On the other hand, it is hard to evaluate whether these custom analyses are doing what is intended in many cases. Would it be possible to consider an analysis using more established methods, e.g. taking a subset of genomes with 'good' completeness and using Panaroo to find the core and accessory genome, then ClonalFrameML or Gubbins to infer a phylogeny and recombination events? Such analyses could probably be applied to a subset of the sample with relatively complete genomes. I don't want to suggest an overly time-consuming analysis, but the authors could consider what would be feasible.

We have added a comparison between our analysis and that from two other methods, including ClonalFrameML mentioned by the author. One important point that we feel might have been lost in the first version is that our linkage results imply that recombination is not rare such that it can be mapped onto an asexual tree as assumed by ClonalFrameML. Note that this is not simply due to technical limitations due to incomplete coverage and is instead a consequence of the evolutionary dynamics of the population. Consistent with this, we found several inconsistencies in how recombination events were assigned by ClonalFrameML. We have summarized these conclusions in Appendix 7 of the revised manuscript.

Page 8. Line 190. What is meant by 'minimal compositional bias'?

We mean that the sample is not biased towards strains that grow in the lab. We have revised the sentence to clarify.

Page 25. Figure S14 is not referenced in the text.

We have added part of this figure to the main text since it illustrates one of our main results, namely that sites at long genomic distances are essentially unlinked.

Page 26. The 'unlinked controls' (line 530) are very useful, but it would be even more informative to see if these controls also show the same decline in linkage with distance in the genome as observed in the real data. In particular, it would be good to know if the observed rapid decline in linkage with distance in the low-diversity regions is also observed in controls. Currently, it is unclear if this observation might be due to higher uncertainty in inferring linkage in low-diversity regions, which by definition have less polymorphism to include in the linkage calculation.

We thank the reviewer for the suggestion. After further consideration, we have decided to remove the subsection on linkage decrease in the low-diversity regions. We feel such detailed quantitative analysis would be better suited for a more technical paper, which we hope to do at a later time.

Page 26. There are some sections with missing identifiers (Sec ??).

Fixed.

Page 27. The information about the typical breadth of SAG coverage (~30%) would be better to include earlier in the Supplement, and also mentioned in the main text so the reader can more easily understand the nature of the dataset.

We have added an extra figure with the SAG coverages to Appendix 1.

Page 29. Any sensitivity analysis around the S = 0.9 value? Even if arbitrary, could the authors provide justification why they think this value is reasonable?

We have significantly revised this section in response to earlier comments by one of the reviewers. We hope that this would clarify the details of our methods to interested readers. To answer the reviewer’s specific question, we chose this heuristic after examining the fraction of cells of each species in different species clusters. For the clusters assigned to alpha and beta, we found a sharp peak near one and that a cutoff of 0.9 captured most clusters while still being high enough to inconsistent with a mixed cluster.

Page 30. I could not see where Fig. S17 was mentioned in the text. Also, how are 'simple hybrid genes' defined?

We have removed this figure in the revision. The definition of the different types of hybrid genes have been added to the main text in response to a comment from the other reviewer.

Page 36. It is hard to see that divergence is 'high' relative to what reference. Would it be possible to include the expected value (from ref. 12) in the plot, or at least explicitly mentioned in the text?

We have added the mean synonymous and non-synonymous divergences between alpha and beta to the figures for reference.

Page 38. Line 770 "would be comparable to that of beta." This is not necessarily the case since beta could have a different time to its most recent common ancestor. It could have a different time to the last bottleneck or selective sweep, etc.

We thank the reviewer for pointing out this misleading statement. Our point here was that in the first scenario the TMRCA of alpha and beta would be similar since the diversity in the high-diversity alpha genes is similar to beta. We have clarified this statement in the revision.

Page 39. Line 793. The use of the term 'genomic backbone' implies the presence of a clonal frame, which is not what the data seems to support. Perhaps another term such as 'genetic diversity' would more appropriately capture the intended meaning here.

We agree with the reviewer that the low-diversity regions may not be asexual. We used “genomic backbone” to distinguish from the “clonal frame,” which is usually used to mean that the backbone is asexual. We have added a note in the revision to clarify this point.

Page 39. Lines 802-805. I found this explanation hard to follow. Could the logic be clarified?

We simply meant that although the beta distribution is unimodal, it is not consistent with a simple Poisson distribution, unlike in alpha. We have added an extra sentence to clarify this.

eLife Assessment

This valuable study uses tools of population and functional genomics to examine long non-coding RNAs (lncRNAs) in the context of human evolution. Analyses of computationally predicted human-specific lncRNAs and their genomic targets lead to the development of hypotheses regarding the potential roles of these genetic elements in human biology. The conclusions regarding evolutionary acceleration and adaptation, however, only incompletely take data and literature on human/chimpanzee genetics and functional genomics into account.

Reviewer #2 (Public review):

In this valuable manuscript, Lin et al attempt to examine the role of long non coding RNAs (lncRNAs) in human evolution, through a set of population genetics and functional genomics analyses that leverage existing datasets and tools. Although the methods are incomplete and at times inadequate, the results nonetheless point towards a possible contribution of long non coding RNAs to shaping humans, and suggest clear directions for future, more rigorous study.

Comments on revisions:

I thank the authors for their revision and changes in response to previous rounds of comments. As before, I appreciate the changes made in response to my comments, and I think everyone is approaching this in the spirit of arriving at the best possible manuscript, but we still have some deep disagreements on the nature of the relevant statistical approach and defining adequate controls. I highlight a couple of places that I think are particularly relevant, but note that given the authors disagree with my interpretation, they should feel free to not respond!

(1) On the subject of the 0.034 threshold, I had previously stated:<br /> "I do not agree with the rationale for this claim, and do not agree that it supports the cutoff of 0.034 used below."

In their reply to me, the authors state:<br /> "What we need is a gene number, which (a) indicates genes that effectively differentiate humans from chimpanzees, (b) can be used to set a DBS sequence distance cutoff. Since this study is the first to systematically examine DBSs in humans and chimpanzees, we must estimate this gene number based on studies that identify differentially expressed genes in humans and chimpanzees. We choose Song et al. 2021 (Song et al. Genetic studies of human-chimpanzee divergence using stem cell fusions. PNAS 2021), which identified 5984 differentially expressed genes, including 4377 genes whose differential expression is due to trans-acting differences between humans and chimpanzeees. To the best of our knowledge, this is the only published data on trans-acting differences between humans and chimpanzeees, and most HS lncRNAs and their DBSs/targets have trans-acting relationships (see Supplementary Table 2). Based on these numbers, we chose a DBS sequence distance cutoff of 0.034, which corresponds to 4248 genes (the top 20%), slightly fewer than 4377."

I have some notes here. First, Agoglia et al, Nature, 2021, also examined the nature of cis vs trans regulatory differences between human and chimps using a very similar set up to Song et al; their Supplementary Table 4 enables the discovery of genes with cis vs trans effects although admittedly this is less straightforward than the Song et al data. Second, I can't actually tell how the 4377 number is arrived at. From Song et al, "Of 4,671 genes with regulatory changes between human-only and chimpanzee-only iPSC lines, 44.4% (2,073 genes) were regulated primarily in cis, 31.4% (1,465 genes) were regulated primarily in trans, and the remaining 1,133 genes were regulated both in cis and in trans (Fig. 2C). This final category was further broken down into a cis+trans category (cis- and trans-regulatory changes acting in the same direction) and a cis-trans category (cis- and trans-regulatory changes acting in opposite directions)." Even when combining trans-only and cis&trans genes that gives 2,598 genes with evidence for some trans regulation. I cannot find 4,377 in the main text of the Song et al paper.

Elsewhere in their response, the authors respond to my comment that 0.034 is an arbitrary threshold by repeating the analyses using a cutoff of 0.035. I appreciate the sentiment here, but I would not expect this to make any great difference, given how similar those numbers are! A better approach, and what I had in mind when I mentioned this, would be to test multiple thresholds, ranging from, eg, 0.05 to 0.01 at some well-defined step size.

(2) The authors have introduced a new TFBS section, as a control for their lncRNAs - this is welcome, though again I would ask for caution when interpreting results. For instance, in their reply to me the authors state:<br /> "The number of HS TFs and HS lncRNAs (5 vs 66) alone lends strong evidence suggesting that HS lncRNAs have contributed more significantly to human evolution than HS TFs (note that 5 is the union of three intersections between and the three )."

But this assumes the denominator is the same! There are 35899 lncRNAs according to the current GENCOVE build; 66/35899 = 0.0018, so, 0.18% of lncRNAs are HS. The authors compare this to 5 TFs. There are 19433 protein coding genes in the current GENCOVE build, which naively (5/19433) gives a big depletion (0.026%) relative to the lnc number. However, this assumes all protein coding genes are TFs, which is not the case. A quick search suggests that ~2000 protein coding genes are TFs (see, eg, https://pubmed.ncbi.nlm.nih.gov/34755879/); which gives an enrichment (although I doubt it is a statistically significant one!) of HS TFs over HS lncRNAs (5/2000 = 0.0025). Hence my emphasis on needing to be sure the controls are robust and valid throughout!

(3) In my original review I said:<br /> line 187: "Notably, 97.81% of the 105141 strong DBSs have counterparts in chimpanzees, suggesting that these DBSs are similar to HARs in evolution and have undergone human-specific evolution." I do not see any support for the inference here. Identifying HARs and acceleration relies on a far more thorough methodology than what's being presented here. Even generously, pairwise comparison between two taxa only cannot polarise the direction of differences; inferring human-specific change requires outgroups beyond chimpanzee.

In their reply to me, the authors state:<br /> Here, we actually made an analogy but not an inference; therefore, we used such words as "suggesting" and "similar" instead of using more confirmatory words. We have revised the latter half sentence, saying "raising the possibility that these sequences have evolved considerably during human evolution".

Is the aim here to draw attention to the ~2.2% of DBS that do not have a counterpart? In that case, it would be better to rewrite the sentence to emphasise those, not the ones that are shared between the two species? I do appreciate the revised wording, though.

(4) Finally, Line 408: "Ensembl-annotated transcripts (release 79)" Release 79 is dated to March 2015, which is quite a few releases and genome builds ago. Is this a typo? Both the human and the chimpanzee genome have been significantly improved since then!

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

In this valuable manuscript, Lin et al attempt to examine the role of long non coding RNAs (lncRNAs) in human evolution, through a set of population genetics and functional genomics analyses that leverage existing datasets and tools. Although the methods are incomplete and at times inadequate, the results nonetheless point towards a possible contribution of long non coding RNAs to shaping humans, and suggest clear directions for future, more rigorous study.

Comments on revisions:

I thank the authors for their revision and changes in response to previous rounds of comments. As it had been nearly two years since I last saw the manuscript, I reread the full text to familiarise myself again with the findings presented. While I appreciate the changes made and think they have strengthened the manuscript, I still find parts of it a bit too speculative or hyperbolic. In particular, I think claims of evolutionary acceleration and adaptation require more careful integration with existing human/chimpanzee genetics and functional genomics literature.

We thank the reviewer heartfully for the great patience and valuable comments, which have helped us further improve the manuscript. Before responding to comments point by point, we provide a summary here.

(1) On parameters and cutoffs.

Parameters and cutoffs influence data analysis. The large number of Supplementary Notes, Supplementary Figures, and Supplementary Tables indicates that we paid great attention to the influence of parameters and robustness of analyses. Specifically, here we explain the DBS sequence distance cutoff of 0.034, which determines the top 20% genes that most differentiate humans from chimpanzees and influences the gene set enrichment analysis (Figure 2). As described in the revised manuscript, we estimated this cutoff based on Song et al., verified its rationality based on Prufer et al. (Song et al. 2021; Prufer et al. 2017), and measured its influence by examining slightly different cutoff values (e.g., 0.035).

(2) Analyses of HS TFs and HS TF DBSs.

It is desirable to compare the contribution of HS lncRNAs and HS TFs to human evolution. Identifying HS TFs faces the challenges that different institutions (e.g., NCBI and Ensembl) annotate orthologous genes using different criteria, and that multiple human TF lists have been published by different research groups. Recently, Kirilenko et al. identified orthologous genes in hundreds of placental mammals and birds and organized different types of genes into datasets of parewise comparison (e.g., hg38-panTro6) using humans and mice as references (Kirilenko et al. Integrating gene annotation with orthology inference at scale. Science 2023). Based on (a) the many2zero and one2zero gene lists in the “hg38-panTro6” dataset, (b) three human TF lists reported by two studies (Bahram et al. 2015; Lambert et al. 2018) and used in the SCENIC package, we identified HS TFs. The number of HS TFs and HS lncRNAs (5 vs 66) alone lends strong evidence suggesting that HS lncRNAs have contributed more significantly to human evolution than HS TFs (note that 5 is the union of three intersections between <many2zero + one2zero> and the three <human TF list>).

TF DBS (i.e., TFBS) prediction has also been challenging because they are very short (mostly about 10 bp) and TF-DNA binding involves many cofactors (Bianchi et al. Zincore, an atypical coregulator, binds zinc finger transcription factors to control gene expression. Science 2025). We used two TF DBS prediction programs to predict HS TF DBSs, including the well-established FIMO program (whose results have been incorporated into the JASPAR database) (Rauluseviciute et al. JASPAR 2024: 20th anniversary of the open-access database of transcription factor binding profiles Open Access. NAR 2023) and the recently reported CellOracle program (Kamimoto et al. Dissecting cell identity via network inference and in silico gene perturbation. Nature 2023). Then, we performed downstream analyses and obtained two major results. One is that on average (per base), fewer selection signals are detected in HS TF DBSs (anyway, caution is needed because TF DBSs are very short); the other is that HS TFs and HS lncRNAs contribute to human evolution in quite different ways (Supplementary Figs. 25 and 26).

(3) On genes with more transcripts may appear as spurious targets of HS lncRNAs.

Now, the results of HS TF DBSs allow us to address the question of whether genes with more transcripts may appear as spurious targets of HS lncRNAs. We note that (a) we predicted HS lncRNA DBSs and HS TF DBSs in the same promoter regions before the same 179128 Ensembl-annotated transcripts (release 79), (b) we used the same GTEx transcript expression matrices in the analyses of HS TF DBSs and HS lncRNA DBSs (the GTEx database includes gene expression matrices and transcript expression matrices, the latter includes multiple transcripts of a gene). Thus, the analyses of HS TF DBSs provide an effective control for examining the question of whether genes with more transcripts may appear as spurious targets of HS lncRNAs, and consequently, cause the high percentages of HS lncRNA-target transcript pairs that show correlated expression in the brain (Figure 3). We find that the percentages of HS TF-target transcript pairs that show correlated expression are also high in the brain, but the whole profile in GTEx tissues is significantly different from that of HS lncRNA DBSs (Figure 3A; Supplementary Figure 25). On the other hand, on the distribution of significantly changed DBSs in GTEx tissues, the difference between HS lncRNA DBSs and HS TF DBSs is more apparent (Figure 3B; Supplementary Figure 26). Together, these suggest that the brain-enriched distribution of co-expressed HS lncRNA-target transcript pairs must arise from HS lncRNA-mediated transcriptional regulation rather than from the transcript number difference.

(4) Additional notes on HS TFs and HS TF DBSs.

First, the “many2zero” and “one2zero” gene lists in the “hg38-panTro6” dataset of Kirilenko et al. provide the most update, but not most complete, data on human-specific genes because “hg38-panTro6” is a pairwise comparison. On the other hand, the Ensembl database also annotates orthologous genes, but lacks such pairwise comparisons as “hg38-panTro6”. Therefore, not all HS genes based on “hg38-panTro6” agree with orthologous genes in the Ensembl database. Second, if HS genes are identified based on both Ensembl and Kirilenko et al., HS TFs will be fewer.

(5) On speculative or hyperbolic claims.

First, the title “Human-specific lncRNAs contributed critically to human evolution by distinctly regulating gene expression” is now further supported by HS TF DBSs analyses. Second, we have carefully revised the entire manuscript, trying to make it more readable, accurate, logically reasonable, and biologically acceptable. Third, specifically, in the revision, we avoid speculative or hyperbolic claims in results, interpretations, and discussions as possible as we can. This includes the tone-down of statements and claims, for example, using “reshape” to replace “rewire” and using “suggest” to replace “indicate”. Since the revisions are pervasive, we do not mark all of them, except those that are directly relevant to the reviewer’s comments.

(1) Line 155: "About 5% of genes have significant sequence differences in humans and chimpanzees," This statement needs a citation, and a definition of what is meant by 'significant', especially as multiple lines below instead mention how it's not clear how many differences matter, or which of them, etc.

Different studies give different estimates, from 1.24% (Ebersberger et al. Genomewide Comparison of DNA Sequences between Humans and Chimpanzees. Am J Hum Genet. 2002) to 5% (Britten RJ. Divergence between samples of chimpanzee and human DNA sequences is 5%, counting indels. PNAS 2002). The 5% for significant gene sequence differences arises when considering a broader range of genetic variations, particularly insertions and deletions of genetic material (indels). To provide more accurate information, we have replaced this simple statement with a more comprehensive one and cited the above two papers.

(2) line 187: "Notably, 97.81% of the 105141 strong DBSs have counterparts in chimpanzees, suggesting that these DBSs are similar to HARs in evolution and have undergone human-specific evolution." I do not see any support for the inference here. Identifying HARs and acceleration relies on a far more thorough methodology than what's being presented here. Even generously, pairwise comparison between two taxa only cannot polarise the direction of differences; inferring human-specific change requires outgroups beyond chimpanzee.

Here, we actually made an analogy but not an inference; therefore, we used such words as “suggesting” and “similar” instead of using more confirmatory words. We have revised the latter half sentence, saying “raising the possibility that these sequences have evolved considerably during human evolution”.

(3) line 210: "Based on a recent study that identified 5,984 genes differentially expressed between human-only and chimpanzee-only iPSC lines (Song et al., 2021), we estimated that the top 20% (4248) genes in chimpanzees may well characterize the human-chimpanzee differences". I do not agree with the rationale for this claim, and do not agree that it supports the cutoff of 0.034 used below. I also find that my previous concerns with the very disparate numbers of results across the three archaics have not been suitably addressed.

(1) Indeed, “we estimated that the top 20% (4248) genes in chimpanzees may well characterize the human-chimpanzee differences” is an improper claim; we made this mistake due to the flawed use of English.

(2) What we need is a gene number, which (a) indicates genes that effectively differentiate humans from chimpanzees, (b) can be used to set a DBS sequence distance cutoff. Since this study is the first to systematically examine DBSs in humans and chimpanzees, we must estimate this gene number based on studies that identify differentially expressed genes in humans and chimpanzees. We choose Song et al. 2021 (Song et al. Genetic studies of human–chimpanzee divergence using stem cell fusions. PNAS 2021), which identified 5984 differentially expressed genes, including 4377 genes whose differential expression is due to trans-acting differences between humans and chimpanzeees. To the best of our knowledge, this is the only published data on trans-acting differences between humans and chimpanzeees, and most HS lncRNAs and their DBSs/targets have trans-acting relationships (see Supplementary Table 2). Based on these numbers, we chose a DBS sequence distance cutoff of 0.034, which corresponds to 4248 genes (the top 20%), slightly fewer than 4377.

(3) If we chose DBS sequence distance cutoff=0.033 or 0.035, slightly more or fewer genes would be determined, raising the question of whether they would significantly influence the downstream gene set enrichment analysis (Figure 2). We found that 91 genes have a DBS sequence distance of 0.034. Thus, if cutoff=0.035, 4248-91=4157 genes were determined, and the influence on gene set enrichment analysis was very limited.

(4) On the disparate numbers of results across the three archaics. Figure 1A is based on Figure 2 in Prufer et al. 2017. At first glance, our Figure 1A indicates that Altai Neanderthal is older than Denisovan (upon kya), making our result “identified 1256, 2514, and 134 genes in Altai Neanderthals, Denisovans, and Vindija Neanderthals” unreasonable. However, Prufer et al. (2017) reported that “It has been suggested that Denisovans received gene flow from a hominin lineage that diverged prior to the common ancestor of modern humans, Neandertals, and Denisovans……In agreement with these studies, we find that the Denisovan genome carries fewer derived alleles that are fixed in Africans, and thus tend to be older, than the Altai Neandertal genome”. This note by Prufer et al. provides an explanation for our result, which is that more genes with large DBS sequence distances were identified in Denisovans than in Altai Neanderthals. Of course, the 1256, 2514, and 134 depend on the cutoff of 0.034. If cutoff=0.035, these numbers change slightly, but their relationships remain (i.e., more genes in Denisovans). We examined multiple cutoff values and found that more genes in Denisovans have large DBS sequence distances than in Altai Neanderthals.

(4) I also think that there is still too much of a tendency to assume that adaptive evolutionary change is the only driving force behind the observed results in the results. As I've stated before, I do not doubt that lncRNAs contribute in some way to evolutionary divergence between these species, as do other gene regulatory mechanisms; the manuscript leans down on it being the sole, or primary force, however, and that requires much stronger supporting evidence. Examples include, but are not limited to:

(1) Indeed, the observed results are also caused by other genomic elements and mechanisms (but it is hardly feasible to identify and differentiate them in a single study), and we do not assume that adaptive evolutionary change is the only driving force. Careful revisions have been made to avoid leaving readers the impression that we have this tendency or hold the simple assumption.

(2) Comparing HS lncRNAs to HS TFs is critical, and we have done this.

(5) line 230: "These results reveal when and how HS lncRNA-mediated epigenetic regulation influences human evolution." This statement is too speculative.

We have toned down the statement, just saying “These results provide valuable insights into when and how HS lncRNA-mediated epigenetic regulation impacts human evolution”.

Line 268: "yet the overall results agree well with features of human evolution." What does this mean? This section is too short and unclear.

(1) First, the sentence “Selection signals in YRI may be underestimated due to fewer samples and smaller sample sizes (than CEU and CHB), yet the overall results agree well with features of human evolution” has been deleted, because CEU, CHB, and YRI samples are comparable (100, 99, and 97, respectively).

(2) Now the sentence has been changed to “These results agree well with findings reported in previous studies, including that fewer selection signals are detected in YRI (Sabeti et al., 2007; Voight et al., 2006)”.

(3) On “This section is too short and unclear” - To make the manuscript more readable, we adopt short sections instead of long ones. This section expresses that (a) our finding that more selection signals were detected in CEU and CHB than in YRI agrees with well-established findings (Voight et al. A Map of Recent Positive Selection in the Human Genome. PLoS Biology 2006; Sabeti et al. Genome-wide detection and characterization of positive selection in human populations. Nature 2007), (b) in considerable DBSs, selection signals were detected by multiple tests.

Line 325: "and form 198876 HS lncRNA-DBS pairs with target transcripts in all tissues." This has not been shown in this paper - sequence based analyses simply identify the “potential” to form pairs.

This section describes transcriptomic analysis using the GTEx data. Indeed, target transcripts of HS lncRNAs are results of sequence-based analysis, and a predicted target is not necessarily regulated by the HS lncRNA in a tissue. Here, “pair” means a pair of HS lncRNA-target transcript whose expression shows significant Pearson correlation in a GTEx tissue (by the way, we do not mean correlation equals regulation; actually, we identified HS lncRNA-mediated transcriptional regulation upon both DBS-targeting relationship and correlation relationship).

Line 423: "Our analyses of these lncRNAs, DBSs, and target genes, including their evolution and interaction, indicate that HS lncRNAs have greatly promoted human evolution by distinctly rewiring gene expression." I do not agree that this conclusion is supported by the findings presented - this would require significant additional evidence in the form of orthogonal datasets.

(1) As mentioned above, we have used “reshape” to replace “rewire” and used “suggest” to replace “indicate”. In addition, we have substantially revised the Discussion, in which this sentence is replaced by “our results suggest that HS lncRNAs have greatly reshaped (or even rewired) gene expression in humans”.

(2) Multiple citations have been added, including Voight et al. 2006 (Voight et al. A Map of Recent Positive Selection in the Human Genome. PLoS Biology 2006) and Sabeti et al. 2007 (Sabeti et al. Genome-wide detection and characterization of positive selection in human populations. Nature 2007).

(3) We have analyzed HS TF DBSs, and the obtained results also support the critical contribution of HS lncRNAs.

I also return briefly to some of my comments before, in particular on the confounding effects of gene length and transcript/isoform number. In their rebuttal the authors argued that there was no need to control for this, but this does in fact matter. A gene with 10 transcripts that differ in the 5' end has 10 times as many chances of having a DBS than a gene with only 1 transcript, or a gene with 10 transcripts but a single annotated TSS. When the analyses are then performed at the gene level, without taking into account the number of transcripts, this could introduce a bias towards genes with more annotated isoforms. Similarly, line 246 focuses on genes with "SNP numbers in CEU, CHB, YRI are 5 times larger than the average." Is this controlled for length of the DBS? All else being equal a longer DBS will have more SNPs than a shorter one. It is therefore not surprising that the same genes that were highlighted above as having 'strong' DBS, where strength is impacted by length, show up here too.

(1) In gene set enrichment analysis (Figure 2, which is a gene-level analysis), when determining genes differentiating humans from chimpanzees based on DBS sequence distance, if a gene has multiple transcripts/DBSs, we choose the DBS with the largest distance. That is, the input to g:Profiler is a non-redundant gene list.

(2) In GTEx data analysis (Figure 3, which is a transcriptome-level analysis), the analyses of HS TF DBSs using the GTEx data provide evidence suggesting that different DBS/transcript numbers of genes are unlikely to cause confounding effects. As explained above, we predicted HS TF DBSs in the same promoter regions of 179128 Ensembl-annotated transcripts (release 79), but Supplementary Figures 25 and 26 are distinctly different from Figure 3AB.

(3) In evolutionary analysis, a gene with 10 DBSs has a higher chance of having selection signals than a gene with 1 DBS. This is biologically plausible, because many conserved genes have novel transcripts whose expression is species-, tissue-, or developmental period-specific, and DBSs before these novel transcripts may differ from DBSs before conserved transcripts.

(4) “line 246 focuses on genes with "SNP numbers in CEU, CHB, YRI are 5 times larger than the average." Is this controlled for the length of the DBS?” - This is a defect. We have now computed SNP numbers per base and used the new table to replace the old Supplementary Table 8. After examining the new table, we find that the major results of SNP analysis remain.

(5) On “Is this controlled for length of the DBS? All else being equal a longer DBS will have more SNPs than a shorter one” - We do not think there are reasons to control for the length of DBSs; also, what “All else being equal” means matters. First, DBS sequences have specific features; thus, the feature of a long DBS is stronger than the feature of a short one, making a long DBS less likely to be generated by chance in the genome and less likely to be predicted wrongly than a short one. This means that longer DBSs are less likely to be false ones (note our explanation that the chance of a DBS of 147 bp, the mean length of DBSs, to be wrongly predicted is extremely low, p<8.2e-19 to 1.5e-48). Second, the difference in length suggests a difference in binding affinity, which in turn influences the regulation of the specific transcripts and influences the analysis of GTEx data. Third, it cannot be excluded that some SNPs may be selection signals (detecting selection signal is challenging, and many selection signals cannot be detected by statistical tests, see Grossman et al. A composite of multiple signals distinguishes causal variants in regions of positive selection. Science 2010).

(6) On “It is therefore not surprising that the same genes that were highlighted above as having 'strong' DBS, where strength is impacted by length” - Indeed, strength is influenced by length, see the above response.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Finally, figure 1 panels D and F are not legible - the font is tiny! There's also a typo in panel A, where "Homo Sapien" should be "Homo sapiens".

(1) “Homo sapien” is changed to “Homo sapiens”.

(2) Even if we double the font size, they are still too small. Inserting a very large panel D into Figure 1 will make Figure 1 ugly, and converting Figure 1D into an independent figure is unnecessary. Actually, panels 1D and F are illustrative figures; the full Fig.1D is Supplementary Figure 6, and the full Fig.1F is Figure 3. We have revised Fig.1’s legend to explain these.

eLife Assessment

This valuable study is a comprehensive investigation into the regulatory mechanisms and regional distribution of enteroendocrine cell subtypes in the Drosophila midgut, significantly advancing the understanding of how WNT and BMP gradients contribute to EE diversity. The methodological foundation and robust genetic evidence are solid in supporting the key roles of compartment boundary signals, particularly WNT and BMP, in specifying EE subtypes and division modes. However, there is a lack of full mechanistic insight regarding Notch pathway involvement, incomplete quantification of phenotype data, and insufficient global pattern analysis, which detracts from fully supporting some proposed models. Overall, the study provides a platform for future work but would benefit from stronger data integration and expanded mechanistic exploration.

Reviewer #1 (Public review):

This valuable study explores the regulatory mechanisms underlying the regional distribution of enteroendocrine cell subtypes in the Drosophila midgut. The regional distribution of EE cell subtypes is carefully documented, and the data convincingly show that each EE cell subtype has a unique spatial pattern. The study aims at determining how the spatial distribution of EE cell subtypes is established and maintained, and explores the roles of three pathways: Notch, WNT, and BMP. The data show evidence that Notch signaling regulates the subtype specificity, being necessary for the specification of Type II, but not Type I and III EE cell subtype specification. The immunofluorescence data in Figure 3 are convincing, but the analysis is incomplete due to a lack of quantification. How Notch signaling activity relates to the emergence of the regional EE cell patterns remains unclear.

As WNT and BMP are known as morphogens, the study explores their expression patterns and their roles in establishing and maintaining the subtype identities. The observed patterns of WNT and BMP are consistent with earlier studies. Manipulation of WNT and BMP pathway activities in intestinal stem cells is shown to have some region-specific effects on specific EE cell subtypes. The overall conclusion that both WNT and BMP have local effects on EE cell subtypes is based on solid evidence. However, the study falls short in achieving its main objective, i.e., to explain the regional subtype patterns by the action of WNT and BMP gradients. Despite displaying a large volume of phenotypic data in Figures 4-7, the study remains incomplete in providing sufficient evidence to support the models shown in Figures 7 M and N. The main challenge is that the reader is provided with a large volume of individual data fragments of selected regions (e.g., Figures 4 and 5) or images of whole midgut without proper quantification (Figure 7). There is not sufficient effort made to display the data in a way that allows observing changes in the global patterns of EE cell subtypes throughout the midgut and compare these patterns with the observed WNT and BMP gradients.

Reviewer #2 (Public review):

Summary:

By labeling the three major enteroendocrine cell markers - AstC, Tk, and CCHa2-the authors systematically investigated the distribution of distinct EE subtypes along the Drosophila midgut, as well as their emergence via symmetric and asymmetric divisions of enteroendocrine progenitor cells. Moreover, they dissected the molecular mechanisms underlying regional patterning by modulating Wnt and BMP signaling pathways, revealing that these compartment boundary signals play key roles in regulating EE subtype diversity.

Strengths:

This work establishes a solid methodological and conceptual foundation for future studies on how stem cells acquire positional identity and modulate region-specific behaviors.

Weaknesses:

Given that the transcriptional profiles of intestinal stem cells across different regions are highly similar, it is reasonable to hypothesize that the behavior of ISCs and enteroendocrine precursor cells may be regulated non-autonomously, potentially through interactions with enterocytes, which exhibit more distinct region-specific characteristics.

Reviewer #3 (Public review):

Summary:

The authors aimed to elucidate the mechanisms underlying the regional patterning of enteroendocrine cell (EE) subtypes along the Drosophila midgut. Through detailed immunohistochemical mapping and genetic perturbation of Notch, WNT, and BMP signaling pathways, they sought to determine how extrinsic morphogen gradients and intrinsic stem cell identity contribute to EE diversity.

Strengths:

A major strength of this work is the meticulous regional analysis of EE pairs and the use of multiple genetic tools to manipulate signaling pathways in a spatiotemporally controlled manner. The data robustly demonstrate that WNT and BMP signaling gradients play key roles in specifying EE subtypes and division modes across different gut regions.

Weaknesses:

However, the study does not fully explore the mechanistic basis for the region-specific dependence on Notch signaling. Additionally, while the authors propose that symmetric divisions occur in R1a and R4b, the observed heterogeneity in CCHa2 expression within AstC+ pairs in R4b suggests that asymmetric mechanisms may still be at play, possibly involving apical-basal polarity as previously reported.

Appraisal of achievements:

The authors successfully achieve their aims by providing a compelling model in which intercalated WNT and BMP gradients regulate EE subtype specification and EEP division modes. The genetic data strongly support the conclusion that these pathways are central to establishing regional EE diversity during pupal development.

Author response:

We would like to express our gratitude to all three reviewers for their time and valuable feedback on the manuscript. Below, we provide our point-by-point responses to their comments. Additionally, we summarize here the experiments we plan to conduct in accordance with the reviewers' suggestions:

Revision plan 1. To further explore the mechanisms of Notch signaling in the decision of regional EE pattern.

Our observation of EE subtype changes in Notch mutant clones revealed that Notch is required for the specification of Type II EEs, but whether it promotes the generation of Type III EEs is not quite clear. In this revision, we will complete the quantification of Type I and Type III EEs in Notch mutant clones to demonstrate whether Notch signaling participate the determination of these two EE subtypes. Further, we will attempt to combine Notch mutant with different manipulation of WNT and BMP gradients to investigate their interplays.

Revision plan 2. To supplement the global pattern of WNT and BMP gradient along the whole gut.

The levels of WNT and BMP gradients are variable in different gut regions both under normal condition and genetic manipulation, leading to different outcomes of EE subtype composition. To further support our model, we will supply the changes of WNT and BMP gradients along the whole gut after genetic manipulation, and perform semi-quantification of their levels to correlate with EE subtype compositions. Additionally, we will also test the gradient levels at different time point during pupal stage to interpret the establishment of regional identity during the development.

Revision plan 3. To investigate the involvement of apical-basal polarity in the determination of regional EE diversity.

Although we have demonstrated WNT and BMP gradients orchestrate the regional EE identity, but some observations cannot be fully explained by their roles, such as asymmetric expression of CCHa2 in EE pairs from R4b. A potential mechanism is apical-basal polarity, which has been reported to determine cell fate of ISC progenies at pupal stage. We will specifically knockdown or overexpress key genes related to apical-basal polarity in ISCs or EEs to test whether they are involved preliminarily.

Please find our detailed point-by-point responses below.

Public Reviews:

Reviewer #1 (Public review):

This valuable study explores the regulatory mechanisms underlying the regional distribution of enteroendocrine cell subtypes in the Drosophila midgut. The regional distribution of EE cell subtypes is carefully documented, and the data convincingly show that each EE cell subtype has a unique spatial pattern. The study aims at determining how the spatial distribution of EE cell subtypes is established and maintained, and explores the roles of three pathways: Notch, WNT, and BMP. The data show evidence that Notch signaling regulates the subtype specificity, being necessary for the specification of Type II, but not Type I and III EE cell subtype specification. The immunofluorescence data in Figure 3 are convincing, but the analysis is incomplete due to a lack of quantification. How Notch signaling activity relates to the emergence of the regional EE cell patterns remains unclear.

Indeed, the role of Notch signaling in regional EE determination was not fully characterized in this work. As the requirement of Notch activation for the differentiation of enterocytes, introduction of Notch or Delta mutant led to rapid accumulation of ISCs and EEs, making it being a challenge to dive into the details of how EE subtypes were generated. We will try to complete the quantification of Type I and Type III EEs in the Notch mutant clones from different gut regions to figure out whether Notch could influence the specification of these two EE subtypes. Additionally, different from WNT and BMP gradients, Notch signaling can only function locally and is not significantly changed along the whole gut, including Type II EE-enriched R1a and Type I EE-enriched R4b, which implies that function of Notch signaling may can be overridden by the impact of specific combination of WNT and BMP gradients. To test this hypothesis, we will attempt to combine Notch mutant with the activation or inhibition of WNT and BMP signaling since pupal stage, and further examine whether the regional EE identity could be altered, especially in R1a and R4b regions.

As WNT and BMP are known as morphogens, the study explores their expression patterns and their roles in establishing and maintaining the subtype identities. The observed patterns of WNT and BMP are consistent with earlier studies. Manipulation of WNT and BMP pathway activities in intestinal stem cells is shown to have some region-specific effects on specific EE cell subtypes. The overall conclusion that both WNT and BMP have local effects on EE cell subtypes is based on solid evidence. However, the study falls short in achieving its main objective, i.e., to explain the regional subtype patterns by the action of WNT and BMP gradients. Despite displaying a large volume of phenotypic data in Figures 4-7, the study remains incomplete in providing sufficient evidence to support the models shown in Figures 7 M and N. The main challenge is that the reader is provided with a large volume of individual data fragments of selected regions (e.g., Figures 4 and 5) or images of whole midgut without proper quantification (Figure 7). There is not sufficient effort made to display the data in a way that allows observing changes in the global patterns of EE cell subtypes throughout the midgut and compare these patterns with the observed WNT and BMP gradients.

As the variation of WNT and BMP gradients along the whole gut, manipulating these two pathways is not able to align their activation levels in different gut regions. This forced us to analyze the change of each region separately, making it to be a challenge to provide a comprehensive global overview. We will supplement the comprehensive profile of WNT and BMP activity under the manipulation of these two signaling pathways to correlated with the change of EE identity, and also try to perform a semi-quantitative interpretation to further support the model in Figure 7M and 7N.

Reviewer #2 (Public review):

Summary:

By labeling the three major enteroendocrine cell markers - AstC, Tk, and CCHa2-the authors systematically investigated the distribution of distinct EE subtypes along the Drosophila midgut, as well as their emergence via symmetric and asymmetric divisions of enteroendocrine progenitor cells. Moreover, they dissected the molecular mechanisms underlying regional patterning by modulating Wnt and BMP signaling pathways, revealing that these compartment boundary signals play key roles in regulating EE subtype diversity.

Strengths:

This work establishes a solid methodological and conceptual foundation for future studies on how stem cells acquire positional identity and modulate region-specific behaviors.

Weaknesses:

Given that the transcriptional profiles of intestinal stem cells across different regions are highly similar, it is reasonable to hypothesize that the behavior of ISCs and enteroendocrine precursor cells may be regulated non-autonomously, potentially through interactions with enterocytes, which exhibit more distinct region-specific characteristics.

This is a quite complicated point to discuss. Drosophila adult midgut is established by pISCs (pupal ISCs), which arise from AMPs (adult midgut progenitors) in larval midgut. AMPs are encased by PCs (peripheral cells) to be islands, scattered throughout the entire larval midgut by mid L3 stage (Mathur D. et al. Science. 2010). After pupariation, larval midgut is delaminated to become the yellow body and finally meconium in the pupal midgut. Simultaneously, PCs break down and die, allowing AMPs to give rise to the presumptive adult epithelium (generating enterocyte precursors) and the specification of ISCs in the adult midgut (Jiang H, Edgar BA. Development. 2009; Micchelli CA. et al. Gene Expr Patterns. 2011). During the pupal stage, pISCs only proliferate to generate new ISCs and EE lineages, while adult enterocytes start to appear after eclosion (Takashima S. et al. Dev Biol. 2011). This rules out the possibility that the interaction with enterocytes regulates regional ISC identity during pupal stage.

However, whether AMPs already acquire the regional identity during larval stage, and whether pISCs interact with enterocyte precursors at pupal stage, are not quite clear. Our study revealed that pISCs can be influenced by WNT and BMP gradients to acquire regional identity, and further establish regional EE diversity. The change of WNT and BMP gradients during the metamorphosis will be supplemented in revision. While WNT and BMP signaling ligands are provided by muscles and adult enterocytes, and even other surrounding tissues, to regulate regional ISC identity, which indicates that non-autonomous mechanisms indeed exist.

Reviewer #3 (Public review):

Summary:

The authors aimed to elucidate the mechanisms underlying the regional patterning of enteroendocrine cell (EE) subtypes along the Drosophila midgut. Through detailed immunohistochemical mapping and genetic perturbation of Notch, WNT, and BMP signaling pathways, they sought to determine how extrinsic morphogen gradients and intrinsic stem cell identity contribute to EE diversity.

Strengths:

A major strength of this work is the meticulous regional analysis of EE pairs and the use of multiple genetic tools to manipulate signaling pathways in a spatiotemporally controlled manner. The data robustly demonstrate that WNT and BMP signaling gradients play key roles in specifying EE subtypes and division modes across different gut regions.

Weaknesses:

However, the study does not fully explore the mechanistic basis for the region-specific dependence on Notch signaling. Additionally, while the authors propose that symmetric divisions occur in R1a and R4b, the observed heterogeneity in CCHa2 expression within AstC+ pairs in R4b suggests that asymmetric mechanisms may still be at play, possibly involving apical-basal polarity as previously reported.

As previously mentioned, we acknowledge that the role of Notch signaling in regional EE determination remains further exploration. We will supplement the quantification of Type I and Type III EEs in Figure 3 and Figure S4, and further combine Notch mutant with activation or inhibition of WNT and BMP signaling to test whether they have any interplays, especially in R1a and R4b.

Apical-basal polarity has been reported to determine the precise segregation of Pros to control ISC number and cell fate at the pupal stage (Wu S. et al. Cell Rep. 2023). During this time, generation of regional EEs are completed and may also be affected except for the influence of Notch, WNT and BMP pathways. Therefore, the apical-basal polarity is quite a potential mechanism to induce asymmetric cell division in R4b, which we will perform experiments to test.

Appraisal of achievements:

The authors successfully achieve their aims by providing a compelling model in which intercalated WNT and BMP gradients regulate EE subtype specification and EEP division modes. The genetic data strongly support the conclusion that these pathways are central to establishing regional EE diversity during pupal development.

eLife Assessment

This valuable study addresses the effects of selection on aggression on fitness and life-history trade-offs in Drosophila melanogaster. However, the evidence presented is incomplete and does not support the claims proposed in the study of increased survival of highly aggressive males at the expense of reproductive success and shorter mating duration. The main limitation of the study is the choice to use males from only one aggressive Drosophila line in combination with CantonS females, that do not allow disambiguation between nonaggression-related factors, such as hybrid vigor and aggression-related factors influencing mating and lifespan.

Reviewer #1 (Public review):

Summary:

This study asks how selection for male aggressiveness affects life-history and reproductive fitness traits in Drosophila melanogaster males.

Strengths:

Multiple comprehensive assays are used to address the question.

Weaknesses:

(1) The flies used for comparisons are inadequate. Behavioral assays compare Bully males mated to non-coevolved Cs females with Cs males mated to coevolved Cs females.

(2) Lifespan analysis is done on male progeny of Cs females mated to either genetically more distant Bully or co-evolved Cs males; the longer lifespan and performance on the former is interpreted as a trade-off with aggressiveness, rather than a simple explanation of hybrid vigor.

(3) Differences in CHCs between Bully and Cs males and Cs females mated to those males are not shown to cause differences in measured behavioral outcomes.

Reviewer #2 (Public review):

Summary:

The authors compare "Bully" lines, selected for male aggression, to Canton-S controls and find that Bully males have lower mating success, shorter mating durations, and remate sooner. Chemical analyses show Bully males have distinct cuticular hydrocarbons (CHC) signatures and transfer markedly less cVA to females, offering a plausible mechanistic link to weaker mate-guarding.

Paradoxically, Bully males live longer and remain fertile at older ages when CS males no longer mate, indicating a shift in the reproduction-survival trade-off in aggression-selected populations.

Importantly, the work sheds light on proximate mechanisms, demonstrating that shifts in CHCs and pheromone transfer co-occur with changes in fitness traits, thus offering new entry points for understanding life-history evolution.

Strengths:

The manuscript's strengths lie in its comprehensive and integrative approach framed within an evolutionary context. By combining behavioral assays, chemical profiling, and lifespan measurements, the authors reveal a coherent pattern linking aggression selection to life-history trade-offs. The direct quantification of cVA in female reproductive tracts after mating provides a particularly compelling mechanistic correlate, strengthening the link between behavior and chemical signaling. Findings on altered 5-T and 5-P levels further highlight how chemical communication shapes mating and mate-guarding strategies. Analytical approaches are largely rigorous, and the results provide valuable insights into the pleiotropic effects of selection on socially relevant traits. The study will be of interest to Drosophila biologists working on sexual selection, behavioral evolution, and aging.

Weaknesses:

The weaknesses are primarily conceptual rather than procedural. The generality of the findings is uncertain, as selection appears to be represented by only one (and a second closely related) Bully line, limiting conclusions about selection responses versus line-specific drift or founder effects. The causal link between aggression selection and increased longevity is not established: the data show a correlated shift but do not identify mechanisms underlying lifespan extension. In several places, the manuscript uses causal language (e.g., that selection 'influences' longevity or mating strategy) where association would be more accurate; this should be toned down to avoid overstatement. Ecological relevance is also not addressed, since laboratory conditions may bias the balance between costs and benefits of aggression compared with variable natural environments. Addressing these points would strengthen both the impact and clarity of the study.

Author response:

eLife Assessment

This valuable study addresses the effects of selection on aggression on fitness and life-history trade-offs in Drosophila melanogaster. However, the evidence presented is incomplete and does not support the claims proposed in the study of increased survival of highly aggressive males at the expense of reproductive success and shorter mating duration. The main limitation of the study is the choice to use males from only one aggressive Drosophila line in combination with CantonS females, that do not allow disambiguation between nonaggression-related factors, such as hybrid vigor and aggression-related factors influencing mating and lifespan.

We would like to clarify the points raised in the eLife assessment.

The report states that we relied on a single line of hyper-aggressive males tested with CantonS females, and implies that Bully and Cs have not co-evolved. This is a misunderstanding: Bully flies were derived from Cs population. Thus, Bully and Cs have co-evolved. In addition to the Bully A line presented in the main figures of the manuscript, we replicated several of our findings with a second independent selected line, Bully B. Results from courtship assays involving both Bully A and Bully B couples males and females were presented in Figure Supp1. We apologies for not having made this more explicit in the original manuscript, which we will correct. These experiments should alleviate the concerns from the reviewers; they demonstrate that our conclusions are supported by two independent hyper-aggressive lines, and these include assays with selected male and female flies.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study asks how selection for male aggressiveness affects life-history and reproductive fitness traits in Drosophila melanogaster males.

Strengths:

Multiple comprehensive assays are used to address the question.

We thank the reviewer for recognizing these strengths.

Weaknesses:

(1) The flies used for comparisons are inadequate. Behavioral assays compare Bully males mated to non-coevolved Cs females with Cs males mated to coevolved Cs females.

We thank the reviewer for this comment, which made us realize that we had not sufficiently highlighted some of our experiments. The Bully lines used in our work were derived from Canton-S flies and thus did co-evolve with Cs. As originally described by Penn et al. (2010), highly aggressive “Bully” lines were generated through selective breeding from Canton-S males that consistently won aggressive encounters. After 34–37 generations, stable Bully lines were established. Thus, Bully and Cs flies have co-evolved and 2) the selection applied was male-specific. Independent selection replicates produced distinct lines, including Bully A and Bully B. Previous studies only characterized Bully A (Penn et al., 2010; Chowdhury et al., 2017), but our work includes both Bully A and Bully B (Fig. S1).

The rationale for pairing Bully or Cs males with Cs females (with which both male types co-evolved) follows the approach used by Dierick et al. (2006), who investigated how the male-specific selection for aggression affected courtship and mating behaviors by testing them with standard Canton-S females. This design allows to isolate the effects of male genotype and behavior on courtship and mating outcomes, avoiding confounding effects from female behavioral changes.

We initially compared selected Bully pairs (Bully males × Bully females) (Fig. S1) with Cs pairs and observed similarly shortened mating durations in both Bully × Bully and Bully × Cs matings (Fig. S1, Fig. 1F and G). Thus, the reduction in mating duration arises specifically from Bully males. We therefore chose to use Cs females as a standard background to assess the consequences of male-specific selection for aggression on reproductive behaviors.

(2) Lifespan analysis is done on male progeny of Cs females mated to either genetically more distant Bully or co-evolved Cs males; the longer lifespan and performance on the former is interpreted as a trade-off with aggressiveness, rather than a simple explanation of hybrid vigor.

We appreciate this comment, which again stems from a poor explanation from our part about the origin of the Bully line in the original manuscript. The Bully flies were derived from the same original population as the Cs line. Hybrid vigor typically arises when crossing individuals from distinct populations, which is not the case here as both Bully and CS come from the same population.

To further support our conclusions, we conducted additional experiments using progeny from within-line crosses (Bully males × Bully females) and results revealed the same phenotype: the progeny of these flies also exhibited significantly longer lifespans than Cs males x Cs females progeny. This finding argues against hybrid vigor as the main explanation for the observed phenotype, since both the Bully and Cs crosses result in inbreeding, yet give longer lifespan in Bully. We will include these additional longevity data (currently not included in the manuscript) to strengthen our results and reinforce our interpretation.

(3) Differences in CHCs between Bully and Cs males and Cs females mated to those males are not shown to cause differences in measured behavioral outcomes.

We thank the reviewer for raising this important point regarding causality. One way to establish a causal link between differences in CHCs observed in Bully and Cs flies and the corresponding behavioral outcomes would be to experimentally manipulate CHC profiles. For instance, one could perfume oenocyte-less males with the compounds found in higher abundance in Bully flies, then perform behavioral assays to assess causality. We agree that such experiments would be highly informative in determining the functional roles of specific CHCs elevated in Bully males. However, this approach is technically challenging, as the perfuming technique must be optimized to transfer precise amounts of each compound. For example, this method can be used to gradually perfume flies to assess dose–response behavioral effects, whereas matching exactly the natural concentrations found in individuals, especially given inter-individual variability, remains difficult.

We considered conducting such experiments during our study but did not pursue them for these technical reasons. Nevertheless, we can include a statement in the Discussion acknowledging this as an important future direction to test the causal relationship between CHC variation and behavior.

Reviewer #2 (Public review):

Summary:

The authors compare "Bully" lines, selected for male aggression, to Canton-S controls and find that Bully males have lower mating success, shorter mating durations, and remate sooner. Chemical analyses show Bully males have distinct cuticular hydrocarbons (CHC) signatures and transfer markedly less cVA to females, offering a plausible mechanistic link to weaker mate-guarding.

Paradoxically, Bully males live longer and remain fertile at older ages when CS males no longer mate, indicating a shift in the reproduction-survival trade-off in aggression-selected populations.

Importantly, the work sheds light on proximate mechanisms, demonstrating that shifts in CHCs and pheromone transfer co-occur with changes in fitness traits, thus offering new entry points for understanding life-history evolution.

We thank the reviewer for this positive summary of our work.

Strengths:

The manuscript's strengths lie in its comprehensive and integrative approach framed within an evolutionary context. By combining behavioral assays, chemical profiling, and lifespan measurements, the authors reveal a coherent pattern linking aggression selection to life-history trade-offs. The direct quantification of cVA in female reproductive tracts after mating provides a particularly compelling mechanistic correlate, strengthening the link between behavior and chemical signaling. Findings on altered 5-T and 5-P levels further highlight how chemical communication shapes mating and mate-guarding strategies. Analytical approaches are largely rigorous, and the results provide valuable insights into the pleiotropic effects of selection on socially relevant traits. The study will be of interest to Drosophila biologists working on sexual selection, behavioral evolution, and aging.

We thank the reviewer for recognizing the integrative design and mechanistic contributions of our study.

Weaknesses:

The weaknesses are primarily conceptual rather than procedural. The generality of the findings is uncertain, as selection appears to be represented by only one (and a second closely related) Bully line, limiting conclusions about selection responses versus line-specific drift or founder effects. The causal link between aggression selection and increased longevity is not established: the data show a correlated shift but do not identify mechanisms underlying lifespan extension. In several places, the manuscript uses causal language (e.g., that selection 'influences' longevity or mating strategy) where association would be more accurate; this should be toned down to avoid overstatement. Ecological relevance is also not addressed, since laboratory conditions may bias the balance between costs and benefits of aggression compared with variable natural environments. Addressing these points would strengthen both the impact and clarity of the study.

(1) Generality of findings and potential line effects

We agree that our results presented in the main figures of the manuscript relied mainly on one Bully line (Bully A). To address potential line-specific effects, we replicated key courtship experiments with another independent line, Bully B, selected in parallel from the same Canton-S stock but through distinct selection replicates. The results obtained from Bully B closely matched those from Bully A, suggesting that the observed phenotypes are consistent consequences of aggression selection rather than random drift or founder effects.

(2) Causality versus correlation

We concur that some sentences in the manuscript could overstate causal interpretations. We will revise the text to clearly distinguish correlation from causation and to avoid implying direct causal relationships where data only support association.

(3) Ecological relevance

We appreciate this point. Our experiments were performed under controlled laboratory conditions, which may not fully capture the ecological contexts shaping the costs and benefits of aggression. We will acknowledge this limitation and expand the Discussion to consider how environmental variability could modulate the fitness trade-offs associated with aggression in natural populations.

We thank both reviewers for their constructive feedback, which will help us strengthen the rigor and clarity of the manuscript. We believe that the additional results and revisions will satisfactorily address their concerns.

eLife Assessment

This valuable study examines how mammals descend effectively and securely along vertical substrates. The conclusions from comparative analyses based on behavioral data and morphological measurements collected from 21 species across a wide range of taxa are convincing, making the work of interest to all biologists studying animal locomotion.

Reviewer #1 (Public review):

Summary:

This unique study reports original and extensive behavioral data collected by the authors on 21 living mammal taxa in zoo conditions (primates, tree shrew, rodents, carnivorans, and marsupials) on how descent along a vertical substrate can be done effectively and securely using gait variables. Ten morphological variables reflecting head size and limb proportions are examined in relationship to vertical descent strategies and then applied to reconstruct modes of vertical descent in fossil mammals.

Strengths:

This is a broad and data-rich comparative study, which requires a good understanding of the mammal groups being compared and how they are interrelated, the kinematic variables that underlie the locomotion used by the animals during vertical descent, and the morphological variables that are associated with vertical descent styles. Thankfully, the study presents data in a cogent way with clear hypotheses at the beginning, followed by results and a discussion that addresses each of those hypotheses using the relevant behavioral and morphological variables, always keeping in mind the relationships of the mammal groups under investigation. As pointed out in the study, there is a clear phylogenetic signal associated with vertical descent style. Strepsirrhine primates much prefer descending tail first, platyrrhine primates descend sideways when given a choice, whereas all other mammals (with the exception of the raccoon) descend head first. Not surprisingly, all mammals descending a vertical substrate do so in a more deliberate way, by reducing speed, and by keeping the limbs in contact for a longer period (i.e., higher duty factors).

Weaknesses:

The different gait patterns used by mammals during vertical descent are a bit more difficult to interpret. It is somewhat paradoxical that asymmetrical gaits such as bounds, half bounds, and gallops are more common during descent since they are associated with higher speeds and lower duty factors. Also, the arguments about the limb support polygons provided by DSDC vs. LSDC gaits apply for horizontal substrates, but perhaps not as much for vertical substrates.

The importance of body mass cannot be overemphasized as it affects all aspects of an animal's biology. In this case, larger mammals with larger heads avoid descending head-first. Variation in trunk/tail and limb proportions also covaries with different vertical descent strategies. For example, a lower intermembral index is associated with tail-first descent. That said, the authors are quick to acknowledge that the five lemur species of their sample are driving this correlation. There is a wide range of intermembral indices among primates, and this simple measure of forelimb over hindlimb has vital functional implications for locomotion: primates with relatively long hindlimbs tend to emphasize leaping, primates with more even limb proportions are typically pronograde quadrupeds, and primates with relatively long forelimbs tend to emphasize suspensory locomotion and brachiation. Equally important is the fact that the intermembral index has been shown to increase with body mass in many primate families as a way to keep functional equivalence for (ascending) climbing behavior (see Jungers, 1985). Therefore, the manner in which a primate descends a vertical substrate may just be a by-product of limb proportions that evolved for different locomotor purposes. Clearly, more vertical descent data within a wider array of primate intermembral indices would clarify these relationships. Similarly, vertical descent data for other primate groups with longer tails, such as arboreal cercopithecoids, and particularly atelines with very long and prehensile tails, should provide more insights into the relationship between longer tail length and tail-first descent observed in the five lemurs. The relatively longer hallux of lemurs correlates with tail-first descent, whereas the more evenly grasping autopods of platyrrhines allow for all four limbs to be used for sideways descent. In that context, the pygmy loris offers a striking contrast. Here is a small primate equipped with four pincer-like, highly grasping autopods and a tail reduced to a short stub. Interestingly, this primate is unique within the sample in showing the strongest preference for head-first descent, just like other non-primate mammals. Again, a wider sample of primates should go a long way in clarifying the morphological and behavioral relationships reported in this study.

Reconstruction of the ancient lifestyles, including preferred locomotor behaviors, is a formidable task that requires careful documentation of strong form-function relationships from extant species that can be used as analogs to infer behavior in extinct species. The fossil record offers challenges of its own, as complete and undistorted skulls and postcranial skeletons are rare occurrences. When more complete remains are available, the entire evidence should be considered to reconstruct the adaptive profile of a fossil species rather than a single ("magic") trait.

Reviewer #2 (Public review):

Summary:

This paper contains kinematic analyses of a large comparative sample of small to medium-sized arboreal mammals (n = 21 species) traveling on near-vertical arboreal supports of varying diameter. This data is paired with morphological measures from the extant sample to reconstruct potential behaviors in a selection of fossil euarchontaglires. This research is valuable to anyone working in mammal locomotion and primate evolution.

Strengths:

The experimental data collection methods align with best research practices in this field and are presented with enough detail to allow for reproducibility of the study as well as comparison with similar datasets. The four predictions in the introduction are well aligned with the design of the study to allow for hypothesis testing. Behaviors are well described and documented, and Figure 1 does an excellent job in conveying the variety of locomotor behaviors observed in this sample. I think the authors took an interesting and unique angle by considering the influence of encephalization quotient on descent and the experience of forward pitch in animals with very large heads.

Weaknesses:

The authors acknowledge the challenges that are inherent with working with captive animals in enclosures and how that might influence observed behaviors compared to these species' wild counterparts. The number of individuals per species in this sample is low; however, this is consistent with the majority of experimental papers in this area of research because of the difficulties in attaining larger sample sizes.

Figure 2 is difficult to interpret because of the large amount of information it is trying to convey.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This unique study reports original and extensive behavioral data collected by the authors on 21 living mammal taxa in zoo conditions (primates, tree shrew, rodents, carnivorans, and marsupials) on how descent along a vertical substrate can be done effectively and securely using gait variables. Ten morphological variables reflecting head size and limb proportions are examined in relationship to vertical descent strategies and then applied to reconstruct modes of vertical descent in fossil mammals.

Strengths:

This is a broad and data-rich comparative study, which requires a good understanding of the mammal groups being compared and how they are interrelated, the kinematic variables that underlie the locomotion used by the animals during vertical descent, and the morphological variables that are associated with vertical descent styles. Thankfully, the study presents data in a cogent way with clear hypotheses at the beginning, followed by results and a discussion that addresses each of those hypotheses using the relevant behavioral and morphological variables, always keeping in mind the relationships of the mammal groups under investigation. As pointed out in the study, there is a clear phylogenetic signal associated with vertical descent style. Strepsirrhine primates much prefer descending tail first, platyrrhine primates descend sideways when given a choice, whereas all other mammals (with the exception of the raccoon) descend head first. Not surprisingly, all mammals descending a vertical substrate do so in a more deliberate way, by reducing speed, and by keeping the limbs in contact for a longer period (i.e., higher duty factors).

Weaknesses:

The different gait patterns used by mammals during vertical descent are a bit more difficult to interpret. It is somewhat paradoxical that asymmetrical gaits such as bounds, half bounds, and gallops are more common during descent since they are associated with higher speeds and lower duty factors. Also, the arguments about the limb support polygons provided by DSDC vs. LSDC gaits apply for horizontal substrates, but perhaps not as much for vertical substrates.

We analyzed gait patterns using methods commonly found in the literature and discussed our results accordingly. However, the study of limbs support polygons was indeed developed specifically for studying locomotion on horizontal supports, and may not be applicable for studying vertical locomotion, which is in fact a type of locomotion shared by all arboreal species. In the future, it would be interesting to consider new methods for analyzing vertical gaits.

The importance of body mass cannot be overemphasized as it affects all aspects of an animal's biology. In this case, larger mammals with larger heads avoid descending head-first. Variation in trunk/tail and limb proportions also covaries with different vertical descent strategies. For example, a lower intermembral index is associated with tail-first descent. That said, the authors are quick to acknowledge that the five lemur species of their sample are driving this correlation. There is a wide range of intermembral indices among primates, and this simple measure of forelimb over hindlimb has vital functional implications for locomotion: primates with relatively long hindlimbs tend to emphasize leaping, primates with more even limb proportions are typically pronograde quadrupeds, and primates with relatively long forelimbs tend to emphasize suspensory locomotion and brachiation. Equally important is the fact that the intermembral index has been shown to increase with body mass in many primate families as a way to keep functional equivalence for (ascending) climbing behavior (see Jungers, 1985). Therefore, the manner in which a primate descends a vertical substrate may just be a by-product of limb proportions that evolved for different locomotor purposes. Clearly, more vertical descent data within a wider array of primate intermembral indices would clarify these relationships. Similarly, vertical descent data for other primate groups with longer tails, such as arboreal cercopithecoids, and particularly atelines with very long and prehensile tails, should provide more insights into the relationship between longer tail length and tail-first descent observed in the five lemurs. The relatively longer hallux of lemurs correlates with tail-first descent, whereas the more evenly grasping autopods of platyrrhines allow for all four limbs to be used for sideways descent. In that context, the pygmy loris offers a striking contrast. Here is a small primate equipped with four pincer-like, highly grasping autopods and a tail reduced to a short stub. Interestingly, this primate is unique within the sample in showing the strongest preference for head-first descent, just like other non-primate mammals. Again, a wider sample of primates should go a long way in clarifying the morphological and behavioral relationships reported in this study.

We agree with this statement. In the future, we plan to study other species, particularly large-bodied ones with varied intermembral indexes.

Reconstruction of the ancient lifestyles, including preferred locomotor behaviors, is a formidable task that requires careful documentation of strong form-function relationships from extant species that can be used as analogs to infer behavior in extinct species. The fossil record offers challenges of its own, as complete and undistorted skulls and postcranial skeletons are rare occurrences. When more complete remains are available, the entire evidence should be considered to reconstruct the adaptive profile of a fossil species rather than a single ("magic") trait.

We completely agree with this, and we would like to emphasize that our intention here was simply to conduct a modest inference test, the purpose of which is to provide food for thought for future studies, and whose results should be considered in light of a comprehensive evolutionary model.

Reviewer #2 (Public review):

Summary:

This paper contains kinematic analyses of a large comparative sample of small to medium-sized arboreal mammals (n = 21 species) traveling on near-vertical arboreal supports of varying diameter. This data is paired with morphological measures from the extant sample to reconstruct potential behaviors in a selection of fossil euarchontaglires. This research is valuable to anyone working in mammal locomotion and primate evolution.

Strengths:

The experimental data collection methods align with best research practices in this field and are presented with enough detail to allow for reproducibility of the study as well as comparison with similar datasets. The four predictions in the introduction are well aligned with the design of the study to allow for hypothesis testing. Behaviors are well described and documented, and Figure 1 does an excellent job in conveying the variety of locomotor behaviors observed in this sample. I think the authors took an interesting and unique angle by considering the influence of encephalization quotient on descent and the experience of forward pitch in animals with very large heads.

Weaknesses:

The authors acknowledge the challenges that are inherent with working with captive animals in enclosures and how that might influence observed behaviors compared to these species' wild counterparts. The number of individuals per species in this sample is low; however, this is consistent with the majority of experimental papers in this area of research because of the difficulties in attaining larger sample sizes.

Yes, that is indeed the main cost/benefit trade-off with this type of study. Working with captive animals allows for large comparative studies, but there is a risk of variations in locomotor behavior among individuals in the natural environment, as well as few individuals per species in the dataset. That is why we plan and encourage colleagues to conduct studies in the natural environment to compare with these results. However, this type of study is very time-consuming and requires focusing on a single species at a time, which limits the comparative aspect.

Figure 2 is difficult to interpret because of the large amount of information it is trying to convey.

We agree that this figure is dense. One possible solution would be to combine species by phylogenetic groups to reduce the amount of information, as we did with Fig. 3 on the dataset relating to gaits. However, we believe that this would be unfortunate in the case of speed and duty factor because we would have to provide the complete figure in SI anyway, as the species-level information is valuable. We therefore prefer to keep this comprehensive figure here and we will enlarge the data points to improve their visibility, and provide the figure with a sufficiently high resolution to allow zooming in on the details.

eLife Assessment

This important study provides a systematic investigation of parent-of-origin (POE) effects on gene expression using large trio-based data from the Framingham Heart Study, uncovering thousands of potentially novel associations. While the findings are potentially significant, the statistical support for classifying POE eQTLs and some downstream analyses is incomplete, and more stringent re-analysis is needed. With such revisions, the work would serve as a foundation for advancing understanding of POEs and their role in gene regulation.

Reviewer #1 (Public review):

Summary:

This study presents a systematic investigation of parent-of-origin effects on gene expression using trio-based data from the Framingham Heart Study, which is notable for its relatively large number of trios. By combining whole-genome and RNA sequencing data, the authors examined the extent to which gene expression is influenced by whether genetic variants are inherited maternally or paternally.

The authors report that parent-of-origin eQTLs are widespread, identifying 15,893 eQTLs from 14,733 variants and 1,824 genes that were significant in paternal, maternal, or joint tests but not detected by traditional eQTL approaches. They further classified these associations based on the relative strength and direction of paternal and maternal effects, highlighting a subset with opposing directions. The study also highlighted eGenes linked to known imprinted genes as well as those with opposing parent-specific effects, and observed that paternal eGenes are enriched for drug targets. Finally, the work revisits previous findings in which eQTL studies were used to interpret disease-associated loci, emphasizing that conventional eQTL analyses without testing the parent-of-origin may mislead gene prioritization efforts. The study recommends that future downstream analyses, such as Mendelian randomization, take into account the provided lists of SNPs and eGenes and exclude those with strong parent-of-origin effects when linking genetic regulation to disease risk.

Strengths:

The major strength of the study lies in the scale and quality of the dataset, the trio-based design, and the systematic application of statistical tests for parent-of-origin effects. The strengths thoughtfully employed Bayes factors rather than p-values to provide stronger evidence of association, which adds rigor to their analyses. These design choices provide compelling evidence that parent-of-origin effects are widespread and that conventional eQTL analyses miss a substantial fraction of regulatory variation. The results are clearly presented and supported by robust analyses, including the identification of opposing parental effects and the enrichment of paternal eGenes for drug targets. Notably, the two examples demonstrating how these findings can reshape disease gene prioritization highlight the broader impact of the study and encourage further work in the community to incorporate parent-of-origin effects.

Weaknesses:

The main limitations of the study are threefold. First, there is a lack of replication in independent cohorts, which is understandable given the difficulty of identifying datasets with a comparable number of trios, but replication would help establish the generalizability of the findings. Second, while Bayes factors are thoughtfully used to assess evidence of association, the paper does not fully explore how the chosen thresholds translate to the expected rate of false positives. For example, a minor allele frequency cutoff of 1% was applied, which seems somewhat arbitrary, and without reporting the allele frequency distribution of the identified eQTLs, it is unclear whether rare variants disproportionately contribute to the signals, potentially affecting the reliability of discoveries. Third, the ancestry background of the study samples is not reported, which could be a confounding factor in the genetic analyses.

Reviewer #2 (Public review):

Summary:

The authors have used 1477 sequenced trios with available gene expression data in the offspring to discover eQTLs that act in a parent-of-origin specific manner. The classified associated SNPs are tested for enrichment for GWAS hits, drug target genes, etc.

Strengths:

The manuscript presents an impressive analysis of a very rich data set of parent-of-origin eQTLs. To my knowledge, it is one of the largest studies of its kind, most analyses are sound, and the results are of interest to many in the field and potentially beyond. The different ideas of follow-up analyses are useful and make sense.

Weaknesses:

While in general the analyses are well-conducted, I noticed a major issue with the POE eQTL classification, which puts into question most of the downstream analysis. In light of this problem, most of the analysis would need to be rerun, which represents a major revision of the paper, but is straightforward to repair.

The major problem with the classification of POEs is that simply having significant maternal, but insignificant paternal effect is not an indicator of POE, this happens widely for SNPs with no POE whatsoever (it can happen by chance even when both maternal and paternal effects are the same and non-zero - the authors can see it via simulations under the null [maternal=paternal effect]). In order to be able to talk about POE, first, a significant difference between maternal and paternal effects needs to be claimed. Therefore, none of the 4 sets of POE eQTLs are justified. To me, the only relevant criterion to pick POE SNPs is the P-value when comparing the maternal and paternal effects. The definitions of the 4 groups are based on somewhat ad hoc priors, BF thresholds, etc. Also, in Section 4.6, the value of theta is arbitrarily chosen (along with the threshold of 4 to declare POE). In my opinion, the clean treatment of the 4 groups would start with a significant P-value (beta_maternal vs beta_paternal). Within this set, you can then use the original criteria presented in the paper, but only among these associations where there is solid evidence of different parental effects.

Author response:

We thank the two anonymous reviewers who took the time and effort to read and evaluate our work. We look forward to submitting a revised version of the manuscript that addresses their comments.

A major concern shared between both reviewers is our use of Bayes factors instead pvalues to measure the strength of association. In revision, we will add a section in Supplementary to compare and constrast Bayes factor and p-values. Very briefly here, p-value is the tail probability under the null. Formally, it is defined as P(T > t|H₀), for a test statistic T with obvserved value t computed from data D. But our interest is P(H₀|D) and P(H₁|D), posterior probabilities of the null and alternative models, about which p-value says nothing. With FDR approach, a q-value, the minium FDR at which a null is rejected, which can be estimated from a collection of p-values, has a Bayesian interpretation as the probability that H₀ is true conditioning on rejecting that H₀. This is not quite P(H₀|D) but nevertheless a useful probabilistic statement. For FDR approach to work, however, the collection of tests need to be reasonably independent, and their effect sizes need to be mixed. Both implicit assumptions can fail for cis eQTL analysis.

On the other hand, with Bayes factors we can compute posterior probability P(H₀|D) and P(H₁|D) after specifying prior odds P(H₁)/P(H₀) (or equivalently P(H₁) since P(H₀)+ P(H₁) = 1). In our manuscript, the prior odds used to determined Bayes factor threshold is 1/1000, or about 1 cis eQTL per gene. Bayes factor also allows us to directly compare two non-nested alternative models P(paternal effect|D) and P(maternal effect|D), which is difficult to do using p-values.

It was suggested (by reviewer 2) that POE eQTL should be defined by testing H₀ : θ₀ = θ₁ against H₁ : θ₀ ̸= θ₁ where θ₀ and θ₁ are maternal and paternal effects respectively. This indeed was our initial approach, as evidenced in Table 1 (last column) and Section 4.5 in Methods. Our final approach is more stringent: H₀ : β₀ = β₁ = 0 against H₁ : β₀ = 0,β₁/= 0, to use test for paternal effect as an example (the test for maternal effect can be obtained in a similar fashion). That is, we not only require that paternal and maternal effects be the same, as suggested by reviewer, but also require that they are both 0 under the null. This is partially motivated by an example in Table 1 (Gene ZNF890P) where both β₀ > 0 and β₁ > 0, and β₀/= β₁. In other words, examples like this where both paternal and maternal effects are significant and their differences are also significant were not included in our downstream classification and further analysis.

eLife Assessment

This important study shows that retinal bipolar cell subtype-specific differences in the size of synaptic ribbon-associated vesicle pools contribute to the transient versus sustained kinetics of the responses of retinal ganglion cells. The data are extensive and compelling. This work will be of broad interest to researchers working on synaptic transmission, retinal signal processing, and sensory neurobiology.

Reviewer #1 (Public review):

Summary:

In the retina, parallel processing of cone photoreceptor output under bright light conditions dissects critical features of our visual environment, and fundamental to visual function. Cone photoreceptor signals are sampled by several types of bipolar cells and passed onto the ganglion cells. At the output of retinal processing, retinal ganglion cells send about 40 different codes of the visual scene to the brain for further processing. In this study, the authors focus on whether subtype-specific differences in the size of synaptic ribbon-associated vesicle pools of bipolar cells contribute to different retinal ganglion cell (RGC) responses.

Specifically, inputs to ON alpha RGCs producing transient versus sustained kinetics (ON-S vs. ON-T, respectively) are compared. The authors first demonstrate that ON-S vs. ON-T RGCs are readily identifiable in a whole mount preparation and respond differently to both static and to a spatially uniform, randomly fluctuating (Gaussian noise) light stimulus. Liner-nonlinear (LN) models were used to estimate the transformation between visual input and excitatory synaptic input for each RGCs; these models suggested the presence of transient versus sustained kinetics already in the excitatory inputs to ON-T and ON-S RGCs.

Indeed, the authors show that (glutamatergic) excitatory inputs to ON-S vs. ON-T RGCs are of distinct kinetics. The subtypes of bipolar cells providing input to ON-S are known (i.e., type 6 and 7), but the source of excitatory bipolar inputs to ON-T RGCs needed to be determined. In a tedious process, it is elegantly shown here that ON-T RGCs receive most of their excitatory inputs from type 5 and 6 bipolars. Interestingly, the temporal properties of light-evoked responses of type 5, 6 and 7 bipolars recorded from the somas were indistinguishable and rather sustained, suggesting that the origin of transient kinetics of excitatory inputs to ON-T RGCs suggested by the LN model might be found in the processing of visual signals at the bipolar cell axon terminal. Blocking GABA- or glycinergic inhibitory inputs did not alter the light-evoked excitatory input kinetics to ON-T and ON-S RGCs. Two-photon glutamate sensor imaging revealed significantly faster kinetics of light-evoked glutamate signals at ON-T versus ON-S RGCs, and that differences in glutamate release from presynaptic bipolar cells are retained without amacrine feedback to bipolar cells. Detailed EM analysis of bipolar cell ribbon synapses onto ON-T and ON-S RGCs revealed fewer ribbon-associated vesicles at ON-T synapses, that is consistent with stronger paired-flash depression of light-evoked excitatory currents in ON-T RGCS versus ON-S RGCs. This study suggests that bipolar subtype-specific differences in the size of synaptic ribbon-associated vesicle pools contributes to transient versus sustained kinetics in RGCs.

Strengths:

The use of multiple, state-of-the-art tools and approaches to address the kinetics of bipolar to ganglion cell synapse in an identified circuit.

Reviewer #2 (Public review):

Summary:

Goal of the study. The authors tried to pinpoint the origins of transient and sustained responses measured at retinal ganglion cells (rgcs), which is the output layer of the retina. Response characteristics of rgcs are used to group them into different types. The diversity of rgc types represents the ability of the retina to transform visual inputs into distinct output channels. They find that the physical dimensions of bipolar cell's synaptic ribbons (specialized release sites/active zones) vary across the different types of cone on-bpcs, in ways that they argue could facilitate transient or sustained release. This diversity of release output is what they argue underlies the differences in on-rgcs response characteristics, and ultimately represents a mechanism for creating parallel cone-driven channels.

Strengths:

The major strengths of the study are the anatomical approaches employed and the use of the "glutamate sniffer" to assay synaptic glutamate levels. The outline of the study is elegant and reflects the strengths of the authors.

Comments on revised version:

The authors have addressed my comments either through new experiments and/or with additional citations.

Explanation of the studies significance. I think the study provides a solid set of data, acquired through exceptional methodologies, and delivers a compelling hypothesis. This is an exceptionally talented group of systems level thinkers and experimentalists, who are now pointing to smaller scale biophysical principles of synaptic transmission.

Reviewer #3 (Public review):

Summary:

Different types of retinal ganglion cell (RGC) have different temporal properties - most prominently a distinction between sustained vs. transient responses to contrast. This has been well established in multiple species, including mouse. In general, RGCs with dendrites that stratify close to the ganglion cell layer (GCL) are sustained; whereas those that stratify near the middle of the inner plexiform layer (IPL) are transient. This difference in RGC spiking responses aligns with similar differences in excitatory synaptic currents as well as with differences in glutamate release in the respective layers - shown previously and here, with a glutamate sensor (iGluSnFR) expressed in the RGCs of interest. Differences in glutamate release were not explained by differences in the distinct presynaptic bipolar cells' voltage responses, which were quite similar to one another. Rather, the difference in transient vs. sustained responses seems to emerge at the bipolar cell axon terminals in the form of glutamate release. This difference in the temporal pattern of glutamate release was correlated with differences in the size of synaptic ribbons (larger in the bipolar cells with more sustained responses), which also correlated with a greater number of vesicles in the vicinity of the larger ribbons.

The main conclusion of the study relates to a correlation (because it is difficult to manipulate ribbon size or vesicle density experimentally): the bipolar cells with increased ribbon size/vesicle number would have a greater possibility of sustained release, which would be reflected in the postsynaptic RGC synaptic currents and RGC firing rates. This model proposes a mechanism for temporal channels that is independent of synaptic inhibition. Indeed, some experiments in the paper suggest that inhibition cannot explain the transient nature of glutamate release onto one of the RGC types. Still, it is surprising that such a diverse set of inhibitory interneurons in the retina would not play some role in diversifying the temporal properties of RGC responses.

Strengths:

(1) The study uses a systematic approach to evaluating temporal properties of retinal ganglion cell (RGC) spiking outputs, excitatory synaptic inputs, presynaptic voltage responses, and presynaptic glutamate release. The combination of these experiments demonstrates an important step in the conversion from voltage to glutamate release in shaping response dynamics in RGCs.

(2) The study uses a combination of electrophysiology, two-photon imaging and scanning block face EM to build a quantitative and coherent story about specific retinal circuits and their functional properties.

Weaknesses:

(1) There were some interesting aspects of the study that were not completely resolved, and resolving some of these issues may go beyond the current study. For example, it was interesting that different extracellular media (Ames medium vs. ACSF) generated different degrees of transient vs. sustained responses in RGCs, but it was unclear how these media might have impacted ion channels at different levels of the circuit that could explain the effects on temporal tuning.

(2) It was surprising that inhibition played such a small role in generating temporal tuning. The authors explored this further in the revision, which supported the original claim that inhibition plays a minor role in glutamate release dynamics from the bipolar cells under study.

Author response:

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

Reviewer #2 had several remaining suggestions:

In some instances, the authors face well-known limitations. For example, bath application of drugs. Blockers of Gly and Gaba receptors are likely problematic when studying a network that includes a diverse set of inhibitory interneurons. Likewise, the results derived from application of AMPAR and KAR blockers should impact HC cell fxn, and presumably inner retina interneuron networks. In the Discussion the authors are encouraged to address more of these concerns (e.g., Discussion line 709).

Rather than concluding that the bath application of drugs is without complications, they can conclude that under the experimental conditions, glutamate release from these On-bipolars continues to exhibit Transient and Sustained release. This is really the key point of their study.

This is a good suggestion.  We have added a discussion of the complications of the pharmacology starting on line 754.  

If indeed sustained release is a reflection of higher release rates, ribbon size is what point to but, there are many other possibilities, such as SV recycling, or recruitment of reserve pools of SVs, fusion machinery, Cav channel behavior. The authors could cite more literature in the Discussion.

We added a sentence to this effect in the discussion, starting on line 866.

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

Reviewer #1 (Public Review): 

Summary: 

In the retina, parallel processing of cone photoreceptor output under bright light conditions dissects critical features of our visual environment and is fundamental to visual function. Cone photoreceptor signals are sampled by several types of bipolar cells and passed onto the ganglion cells. At the output of retinal processing, retinal ganglion cells send about 40 different codes of the visual scene to the brain for further processing. In this study, the authors focus on whether subtype-specific differences in the size of synaptic ribbon-associated vesicle pools of bipolar cells contribute to different retinal ganglion cell (RGC) responses. Specifically, inputs to ON alpha RGCs producing transient versus sustained kinetics (ON-S vs. ON-T, respectively) are compared. The authors first demonstrate that ON-S vs. ON-T RGCs are readily identifiable in a whole mount preparation and respond differently to both static and to a spatially uniform, randomly fluctuating (Gaussian noise) light stimulus. Liner-nonlinear (LN) models were used to estimate the transformation between visual input and excitatory synaptic input for each RGCs; these models suggested the presence of transient versus sustained kinetics already in the excitatory inputs to ON-T and ON-S RGCs. Indeed, the authors show that (glutamatergic) excitatory inputs to ON-S vs. ON-T RGCs are of distinct kinetics. The subtypes of bipolar cells providing input to ON-S are known (i.e., type 6 and 7), but the source of excitatory bipolar inputs to ON-T RGCs needed to be determined. In a tedious process, it is elegantly shown here that ON-T RGCs receive most of their excitatory inputs from type 5 and 6 bipolars. Interestingly, the temporal properties of light-evoked responses of type 5, 6, and 7 bipolars recorded from the somas were indistinguishable and rather sustained, suggesting that the origin of transient kinetics of excitatory inputs to ON-T RGCs suggested by the LN model might be found in the processing of visual signals at the bipolar cell axon terminal. Blocking GABA- or glycinergic inhibitory inputs did not alter the light-evoked excitatory input kinetics to ON-T and ON-S RGCs. Twophoton glutamate sensor imaging revealed significantly faster kinetics of light-evoked glutamate signals at ON-T versus ON-S RGCs. Detailed EM analysis of bipolar cell ribbon synapses onto ON-T and ON-S RGCs revealed fewer ribbon-associated vesicles at ON-T synapses, which is consistent with stronger paired-flash depression of lightevoked excitatory currents in ON-T RGCS versus ON-S RGCs. This study suggests that bipolar subtype-specific differences in the size of synaptic ribbon-associated vesicle pools contribute to transient versus sustained kinetics in RGCs. 

Strengths: 

The use of multiple, state-of-the-art tools and approaches to address the kinetics of bipolar to ganglion cell synapse in an identified circuit. 

Weaknesses: 

For the most part, the data in the paper support the conclusions, and the authors were careful to try to address questions in multiple ways. Two-photon glutamate sensor imaging experiment showing that blocking GABA- and glycinergic inhibition does not change the kinetics of light-evoked glutamate signals at ON-T RGCs would strengthen the conclusion that bipolar subtype-specific differences in the size of synaptic ribbon-associated vesicle pools contribute to transient versus sustained kinetics in RGCs. 

Thank you for this suggestion. We have revised the text throughout to be careful not to imply that amacrine cells have no role in shaping EPSCs and spike output, but instead that the transience of the On-T responses persists without amacrine cells (see for example lines 91, 450-453, 514-518, 696-714). We have also added additional iGluSnFR experiments to the paper to further test this conclusion (new Figure 7). The new data shows that the transience of glutamate release from the On-T cells is retained when 1) spiking amacrine cell activity is suppressed by blocking voltage-gated Na⁺ channels with TTX or 2) all amacrine cell activity is suppressed by blocking AMPA receptors with NBQX. This does provide nice additional evidence that amacrine cells are not necessary for the sustained/transient distinction.

Reviewer #2 (Public Review): 

Summary: 

Goal of the study. The authors tried to pinpoint the origins of transient and sustained responses measured at retinal ganglion cells (rgcs), which is the output layer of the retina. Response characteristics of rgcs are used to group them into different types. The diversity of rgc types represents the ability of the retina to transform visual inputs into distinct output channels. They find that the physical dimensions of bipolar cell's synaptic ribbons (specialized release sites/active zones) vary across the different types of cone on-bpcs, in ways that they argue could facilitate transient or sustained release. This diversity of release output is what they argue underlies the differences in on-rgcs response characteristics, and ultimately represents a mechanism for creating parallel cone-driven channels. 

Strengths: 

The major strengths of the study are the anatomical approaches employed and the use of the "glutamate sniffer" to assay synaptic glutamate levels. The outline of the study is elegant and reflects the strengths of the authors. 

Weaknesses: 

The major weakness is that the ambitious outline is not matched with a complete set of results, and the set of physiological protocols is disjointed, not sufficient to bridge the systems-level question with the presynaptic release question. 

Thank you for this comment as it provides an opportunity (here and in the paper) for us to clarify our main goal. We wanted to link the well-established distinction between transient and sustained retinal responses to anatomy. This required locating where this difference arises within the circuitry – which we show to be at least largely the bipolar output synapse – and then examining the structure of this synapse in detail. While we would certainly be interested in connecting our results to a biophysical description of the synapse, that was not the primary focus of our study and was not something we could add without substantial additional work.  

Major comments on the results and suggestions. 

The ribbon model of release has been explored for decades and needs to be further adapted to systems-level work. The study under consideration by Kuo et al. takes on this task. Unfortunately, the experimental design does not permit a level of control over presynaptic/bpc behavior that is comparable to earlier studies, nor do they manipulate release in ways that test the ribbon model (i.e., paired recordings or Ribeye-ko). Furthermore, the data needs additional evaluation, and the presentation and interpretations should draw on published biophysical and molecular studies. 

As described above, our goal was to test several possible explanations for the difference between transient and sustained responses in OnT and OnS ganglion cells: (1) differences in the light responses of the bipolar cells that convey photoreceptor signals to the relevant ganglion cells; (2) shaping of bipolar transmitter release by presynaptic inhibition; (3) shaping of ganglion cell responses by postsynaptic inhibition or spike generation; (4) differences in feedforward bipolar synapses. We were surprised to find that the feedforward bipolar synapses play a central role in this difference, and your comment nicely prompts us to relate this to the large literature on biophysical studies of release from ribbon synapses. We have made substantial revisions in the text to do this. This includes anticipating the importance of feedforward synaptic properties in the abstract and introduction (lines 36-37 and 61-64), pointers in the results (lines 539-548), and several new paragraphs in the discussion (starting on lines 751, 773 and 787). By showing that the transient/sustained differences originates largely at feedforward bipolar synapses, we set the stage for future work that shows how biophysical properties of the synapse shape physiological signals that traverse it.

To build a ribbon-centric context, consider recent literature that supports the assertion that ribbons play a role in forming AZ release sites and facilitating exocytosis. Reference Ribeye-ko studies. For example, ribbonless bpcs show an 80% reduction in release (Maxeiner et al EMBO J 2016), the ribbonless retina exhibits signaling deficits at the output layer (Okawa et al ...Rieke, ..Wong Nat Comm 2019), and ribbonless rods show an 80% reduction the readily releasable pool (RRP) of SVs (Grabner Moser, elife 2021). In addition, the authors could refer to whole-cell membrane capacitance studies on mammalian rods, cones, and bpcs, because the size of the RRP of SVs scales with the dimensions and numbers of ribbons (total ribbon footprint). For comparison, bipolars see the review by Wan and Heidelberger 2011. For a comparison of mammalian rods and cones, see, rods: Grabner and Moser (2021 eLife), Mueller.. Regus Leidig et al. (2019; J Neurosci) and cones Grabner ...DeVries (Nat Comm 2023). A comparison of cell types shows that the extent of release is (1) proportional to the total size of the ribbon footprint, and (2) less release is witnessed when ribbons are deleted (also see photo ablation studies by Snellman.... And Mehta..Zenisek, Nat Neurosci and Neuron).

Thank you for these pointers into the literature.  We have included much of this work in the revised Discussion (see three paragraphs starting on line 751). The revised text focuses on the evidence that larger and more numerous ribbons lead to increased release. The direct evidence from previous work for this relationship supports our (indirect) conclusions in the current paper about the role of ribbon size and associated vesicle pools in transient vs sustained responses.  

Ribbon morphology may change in an activity-dependent manner. The rod ribbon AZ has been reported to lengthen in the dark (Dembla et al 2020), and deletion of the ribbon shortens the length of the AZ (defined by Cav1,4 or RIM2); in addition, the Ribeye-ko AZs fail to change in size with light and dark conditioning. Furthermore, EM studies on rod and cone AZs in light and dark argue that the number of SVs at the base of the ribbon increases in the dark, when PRs are depolarized (see Figure 10, Babai et al 2016 JNeurosci). Lastly, using goldfish Mb1 on-bipolars, Hull et al (2006, J Neurophysio) correlated an increase in release efficiency with an increase in ribbon numbers, which accompanied daylight. >> When release activity is high, ribbon AZ length increases (Dembla, rods), the number of docked SVs increases (Babai, rods cones), and the number of ribbons increases (Hull, diurnal Mb1s). 

We have extensively revised the discussion section to include more discussion of ribbons, particularly emphasizing evidence supporting the general argument that larger ribbons support higher release rates. We focused on studies that provided direct links between release rates and ribbon size or number of ribbon-associated vesicles.  This includes studies that pair electrophysiology and anatomy and those that measure the consequences of ablating ribbons,

The results under review, Kuo et al., were attained with SBF-SEM, which has the benefit of addressing large-volume questions as required here, yet it achieves lower spatial resolution than what is attained with TEM tomography and FIB-EM. Ideally, the EM description would include SV size, and the density of ribbon-tethered SVs that are docked at the plasma membrane, because this is where the SVs fuse (additional non-ribbon release sites may also exist? Mehta ... Singer 2014 J Neurosci). Studies by Graydon et al 2011 and 2014 (both in J Neurosci), and Jean ... Moser et al 2018 (eLife) are good examples of quantitative estimates of SVs docking sites at ribbons. SBF-SEM does not allow for an assessment of SVs within 5 nm of the PM, but if the authors can identify the number of SVs that appear within the limit of resolution (10 to 15 nm) from the PM, then this data would be useful. Also, what dimension(s) of the large ribbons make them larger? Typically, ribbons are fixed in height (at least in the outer retina, 200 to 250 nm), but their length varies and the number ribbons per terminal varies. Is the larger ribbon size observed in type 6 bpcs do to longer ribbons, or taller ribbons? A longer ribbon likely has more docked SVs. An additional possibility is that more SVs are about the ribbon-PM footprint, either more densely packed and/or expanding laterally (see definitions in Jean....Moser, elife 2018). 

We have included an additional analysis of ribbon surface area from our 3D SBFSEM reconstructions. As with the volume measurements included in the original submission, ribbon surface areas are distinct between type 5i and type 6 bipolar cells (Fig. S10A), ON-T RGCs on average receive input from ribbons with smaller surface area than ON-S RGCs (Fig. S10B), and ribbon surface area predicts the number of adjacent vesicles across bipolar cell types (Fig. S10C).  We agree that a higher resolution view of presynaptic structures would be very helpful, but the resolution of our SBF-SEM data is limited (e.g. each pixel is 40 nm on a side).  This resolution does not allow us to distinguish between vesicles at vs near the membrane. 

In our observations, both length and height of the ribbons showed variability across individual bipolar cells. And ribbons in type 6 bipolar cells tended to be either longer and/or taller compared to those in type 5 cells. We agree that a longer ribbon may accommodate more docked SVs. A more definitive analysis would benefit from higher-resolution, isotropic 3D reconstructions of ribbons, which would allow more precise shape analysis and ,together with a detailed assessment of docked SVs at the ribbons.

The ribbon literature given above makes the argument that ribbons increase exocytotic output, and morphological studies suggest that release activity enhances 1) ribbon length (Dembla) and 2) the density of SVs near the PM (Babai). These findings could lead one to propose that type 6 bpcs (inputs to On-sustained) are more active than type 5i (feed into On-transient). Here Kuo et al. show that the bpcs have similar Vm (measured from the soma) in response to light stimulation. Does Vm predict release? Not entirely as the authors acknowledge, because: Cav channel properties, SV availability, and negative feedback are all downstream of bpc Vm. The only experiment performed to test downstream factors focused on negative feedback from amacrines. The data presented in Figures 5C-F led me to conclude the opposite of what the authors concluded. My impression is that the T-ON rgc exhibits strong disinhibition when GABA-blockers are applied (the initial phase is greatly increased in amplitude and broadened with the drug), which contrasts with the S-On rgc responses that show a change in the amplitude of the initial phase but not its width (taus would be nice). Here and in many places the authors refer to changes in release kinetics, without implementing a useful description of kinetics. For instance, take the cumulative current (charge) in Figure 5C and fit the control and drug traces to arrive at taus, and their respective amplitudes, and use these values to describe kinetic phases. One final point, the summary in Figure 5D has a p: 0.06, very close to the cutoff for significance, which begs for more than an n = 5. Given that previous studies have shown that bpc output is shaped by immediate msec GABA feedback, in ways that influence kinetic phases of release (..Mb1 bipolars, see Vigh et al 2005 Neuron), more attention to this matter is needed before the authors rule out feedback inhibition in favor of ribbon size. If by chance, type 5i bpcs are under uniquely strong feedback inhibition, then ribbon size may result from less activity, not less output resulting from smaller ribbons.

The text surrounding Figure 5 led to some confusion, and we have revised that text and the figure for clarity.  First, the data in that figure is entirely from On-T cells (the upper and lower panels show block of GABA and glycine receptors separately).  Second, the observation that we make there is that block of inhibitory receptors increases the transience of the On-T excitatory input, rather than decreasing it as would be expected if the transience is created by presynaptic inhibition. We have added additional data and that increase in transience is now significant. Inhibitory block does substantially increase the amplitude of the postsynaptic response, and a likely origin of this change in response is inhibitory feedback to the bipolar synaptic terminal. We now indicate this in the text on page 13, lines 438-453. 

The key result of this figure for our purposes here is that the transience of the excitatory input to the OffT cell remains with inhibitory input blocked. We have clarified throughout the text that our results indicate that inhibitory feedback is not necessary for the difference between transient release into On-T and sustained release onto On-S. This does not mean that inhibitory feedback does not shape the responses in other ways or contribute to the transient/sustained difference - just that for the specific stimuli we use that difference is retained without presynaptic inhibition. We have also added citations to past work showing that activity of amacrine cells can modulate bipolar transmitter release. 

Whether strong feedback inhibition limits activity and therefore limits ribbon size in an activity-dependent way is an intriguing possibility. Indeed, addressing why ribbons are larger in type 6 bipolar cells vs. other bipolar types will be an interesting avenue of further study. However, it would be surprising if ribbon sizes changed during the acute pharmacological block conditions (~10-15 minutes) we employed in our study. Our point here is that there is an interesting correlation between presynaptic ribbon size and the kinetics of glutamate release. We do not think that the two possibilities stated in the last sentence (“…ribbon size may result from less activity, not less output resulting from smaller ribbons”) are mutually exclusive.

We have not further quantified the response kinetics in the experiments of Figure 5 as the large changes induced by the pharmacology (especially GABA receptor block) make it unclear how to interpret quantitative differences.  In other places we have quantified kinetics through the STA or specified that our focus was more qualitative (i.e. transient vs sustained kinetics). 

As mentioned above, the behavior of Cav channels is important here. This is difficult to address with voltage clamps from the soma, especially in the Vm range relevant to this study. Given that it has previously been modeled that the rod bpc to AII pathway adapts to prolonged depolarization of rbcs through downregulating Cav channel-mediated Ca²⁺ influx (Grimes ....Rieke 2014 Neuron), it seems important for Kou et al to test if there is a difference in Cav regulation between type 6 and 5i bpcs. Ca²⁺  imaging with a GCaMP strategy (Baden....Lagnado Current Biology, 2011) or filling the presynapse with Ca dyes (see inner hair cells: Ozcete and Moser, EMBO J 2020) would allow for the correlation of [Ca]intra with GluSnf signals (both local readouts).

This is a good suggestion but is outside the scope of our current paper. Our focus was on the circuit origin of the difference in response of the OnT and OnS responses rather than the specific biophysical mechanism.  We are of course interested in the mechanism, but the additional experiments needed to pin that down would need to be a part of future experiments. The work here represents an important step in that direction as it greatly reduces the number of possible locations and mechanisms for the sustained/transient difference and hence serves to focus any future mechanistic investigations.

Stimulation protocol and presentation of Glutamate Sniffer data in Figure 6. In all of your figures where you state steady st as a % of pk amplitude, please indicate in the figure where you estimate steady state. Alternatively, if you take the cumulative dF/F signal, then you can fit the different kinetic phases. From the appearance of the data, the Sustained Glu signals look like square waves (Figure 6B ROI1-4), without a transient at onset, which is not predicted in your ribbon model that assumes different kinetic phases (1. depletion of docked SVs, and 2. refilling and repriming). The Transient responses (Figure 6B ROI5-8) are transient and more compatible with a depressing ribbon scheme. If you take the cumulative, for all of the On-S and compare it to all of the On-T responses, my guess is the cumulative dF/F will be 10 to 20 larger for the S-On. Would you conclude that bpc inputs to On-S (type 6) release 20fold more SVs per 4 seconds on a per ribbon basis, and does the surface area of the type 6 bpcs account for this difference? From Figures 8B and D, the volume of the ribbon is ~2 fold greater for type 6 vs 5i, but the Surface Area (both faces of ribbon) is more relevant to your model that claims ribbon size is the pivotal factor. If making cumulative traces, and comparisons on an absolute scale is unfounded, then we need to know how to compare different observations. The classic ribbon models always have a conversion factor such as the capacitance of an SV or q size that is used to derive SV numbers from total dCm or Qcontent. See Kim ....et al von Gersdorff, 2023, Cell Reports. Why not use the Gaussian noise stimulus in Fig 6 as in Figure 1 and 2? 

For iGluSnFR recordings, steady-state responses were measured from the mean fluorescence over the last 1 sec of the light step (2 sec duration) response. We have included this information in the figure caption and in the Methods. 

There is a good deal of variability in the iGluSnR responses from one ROI to another, and the ROIs shown in the original submission had a less prominent transient component than many other ROIs. We have replaced this figure with another that is more representative of the average behavior across ROIs. The full range of behavior is captured in Figure 6C; it is clear across ROIs that glutamate release near ON-S dendrites shows both sustained and transient components. The new experiments in which we block amacrine cell activity also include a few more example ROIs from ON-S cells, and those also show both transient and sustained components.

Your suggestion to integrate the iGluSnFR signals to compare to our structural analysis of ribbons is interesting. However, we are hesitant to make a quantitative comparison between the two without further experiments to validate how the iGluSnFR signals we measure relate to release of single vesicles. For example, a quantitative measure of release based on the iGluSnR experiments would require accounting for possible differences in the expression of the indicator - which could differ both in overall level and/or location relative to release sites. 

This comment and one above highlight the importance of measures of ribbon surface area, which we now provide (Figure S10).

Figure 7. What is the recovery time for mammalian cones derived from ribbon-based models? There are estimates from membrane capacitance studies. Ground squirrel cones take 0.7 to 1 sec to recover the ultrafast, primed pool of SVs when probed with a paired-pulse protocol (Grabner ...DeVries 2016, Neuron). Their off-bpcs take anywhere from under 0.2 sec to a second to recover, which is a combination of many synaptic factors (Grabner ...DeVries Nat Comm 2023). Rod On bpcs take over a second (Singer Diamond 2006, reviewed Wan and Heidelberger 2011). In Figure 7B, the recovery time is ~150 ms for the responses measured at rgcs. This brief recovery time is incompatible with existing ribbon models of release. Whole-cell membrane capacitance measurements would be helpful here.

Thanks for drawing our attention to this issue. Indeed, we see a relatively rapid recovery in the paired-flash experiments. We now discuss this recovery time in the context of past measurements of recovery of responses in cones and bipolar cells (paragraph starting on line 773). There are many factors that could contribute to the relatively rapid recovery we observe - including synaptic factors such as those highlighted by Grabner et al., (2016) either at the cone-to-bipolar synapses or the bipolar-to-RGC synapses. We are certainly interested in a more detailed understanding of this issue, but the additional experiments are outside the scope of this paper.  

Experimental Suggestion: Add GABA blockers and see if type 5i bpc responds with more release (GluSniff) and prolonged [Ca2+] intra (GCaMP). Compare this to type 6 bpc behavior with GABA/gly blockers. This will rule in or out whether feedback inhibition is involved. 

Figure 7 in the revised manuscript includes two new experiments examining glutamate release (without the simultaneous measurement of bipolar cell intracellular calcium) while blocking (1) all/most amacrine cell-mediated inhibition via inclusion of NBQX in the bath solution, and (2) blocking spiking amacrine cells via inclusion of TTX in the bath solution. The transient vs sustained difference in light-evoked glutamate release around ON-T and ON-S RGC dendrites remained with amacrine activity suppressed. These new results are consistent with the anatomical and pharmacological data that were included in the initial submission of the manuscript (Fig. 5) that indicate presynaptic inhibition does not have a major role in shaping release kinetics at these synapses. 

Reviewer #3 (Public Review): 

Summary: 

Different types of retinal ganglion cell (RGC) have different temporal properties - most prominently a distinction between sustained vs. transient responses to contrast. This has been well established in multiple species, including mice. In general, RGCs with dendrites that stratify close to the ganglion cell layer (GCL) are sustained; whereas those that stratify near the middle of the inner plexiform layer (IPL) are transient. This difference in RGC spiking responses aligns with similar differences in excitatory synaptic currents as well as with differences in glutamate release in the respective layers - shown previously and here, with a glutamate sensor (iGluSnFR) expressed in the RGCs of interest. Differences in glutamate release were not explained by differences in the distinct presynaptic bipolar cells' voltage responses, which were quite similar to one another. Rather, the difference in transient vs. sustained responses seems to emerge at the bipolar cell axon terminals in the form of glutamate release. This difference in the temporal pattern of glutamate release was correlated with differences in the size of synaptic ribbons (larger in the bipolar cells with more sustained responses), which also correlated with a greater number of vesicles in the vicinity of the larger ribbons. 

The main conclusion of the study relates to a correlation (because it is difficult to manipulate ribbon size or vesicle density experimentally): the bipolar cells with increased ribbon size/vesicle number would have a greater possibility of sustained release, which would be reflected in the postsynaptic RGC synaptic currents and RGC firing rates. This model proposes a mechanism for temporal channels that is independent of synaptic inhibition. Indeed, some experiments in the paper suggest that inhibition cannot explain the transient nature of glutamate release onto one of the RGC types. Still, it is surprising that such a diverse set of inhibitory interneurons in the retina would not play some role in diversifying the temporal properties of RGC responses. 

Strengths: 

(1) The study uses a systematic approach to evaluating temporal properties of retinal ganglion cell (RGC) spiking outputs, excitatory synaptic inputs, presynaptic voltage responses, and presynaptic glutamate release. The combination of these experiments demonstrates an important step in the conversion from voltage to glutamate release in shaping response dynamics in RGCs. 

(2) The study uses a combination of electrophysiology, two-photon imaging, and scanning block-face EM to build a quantitative and coherent story about specific retinal circuits and their functional properties. 

Weaknesses: 

(1) There were some interesting aspects of the study that were not completely resolved, and resolving some of these issues may go beyond the current study. For example, it was interesting that different extracellular media (Ames medium vs. ACSF) generated different degrees of transient vs. sustained responses in RGCs, but it was unclear how these media might have impacted ion channels at different levels of the circuit that could explain the effects on temporal tuning.

We do not have an explanation for the quantitative differences in response kinetics we observed in Ames’ medium vs. ACSF. There are modest differences in calcium and magnesium concentration and a larger difference in potassium (2.5 mM in ACSF vs 3.6 mM in Ames). It would be interesting to test which of these (or other) differences accounts for the difference in response kinetics.

(2) It was surprising that inhibition played such a small role in generating temporal tuning. At the same time, there were some gaps in the investigation of inhibition (e.g., IPSCs were not measured in either of the RGC types; pharmacology was used to investigate responses only in the transient RGCs).

We were also surprised at this result. We have included additional data on inhibition in the revised manuscript. Figure S3 shows light-evoked IPSC data from both RGC types (Fig. S3) and Fig. 7 shows additional iGluSnFR measurements around both ON-T and ON-S RGC dendrites with inhibition blocked via bath application of NBQX (Fig. 7) and separately with inhibition from spiking amacrine cells blocked with TTX. These experiments provide additional evidence for the small role of inhibition. We attempted to measure the kinetics of excitatory input to ON-S cells with inhibition blocked, but we found that the excitatory input showed strong spontaneous oscillations under these conditions and the light responses were changed so drastically that we did not feel we could make a clear comparison with control conditions.

(3) There could be additional discussion and references to the literature describing several topics, including: temporal dynamics of glutamate release at different levels of the IPL; previous evidence that release sites from a single presynaptic neuron can differ in their temporal properties depending on the postsynaptic target; previous investigations of the role of inhibition in temporal tuning within retinal circuitry. 

Thanks, we have included more discussion and references to the relevant literature as you have suggested in the recommendations to authors.

Reviewer #1 (Recommendations For The Authors): 

The presented raw data of the pharmacological experiments show that SR95531 and TPMPA robustly increased both the amplitude and duration of the transient component of the light step-evoked excitatory currents, with slight, if any enhancement of the sustained component in ON-T RGCs Figure 5C. Statistical analysis of the population data (n=5) with Wilcoxon signed rank test yielded no significant difference (ln 363). However, reanalyzing the data extracted from the graph (Figure 5D) revealed that the difference between the paired observations is normally distributed (Shapiro-Wilk normality test, P=0.48) allowing parametric statistics to be used, which provides higher statistical power. Accordingly, reanalyzing the presented data with paired Student's t-test data revealed significant differences (P=0.01) in the steady-state amplitude normalized to that of the peak, recorded in the presence of SR95531 and TPMPA. In other words, based on the (rough) analysis of the presented pharmacology data GABAergic feedback inhibition significantly contributes to shaping the transient portion of the light-evoked excitatory currents in ON-T RGCs, by making it more transient. I believe a similar analysis based on the actual data is necessary, and the results should be communicated either way. However, if warranted, two-photon glutamate sensor imaging experiments showing that blocking GABA- and glycinergic inhibition does not change the kinetics of light-evoked glutamate signals at ON-T RGCs should also be performed, as these would be critical in drawing a conclusion regarding the effect of feedback inhibition on glutamate release from bipolar cells.

Thanks for this feedback. We have added another cell to the data set in Fig. 5D. With this addition, SR95531/TPMPA application significantly increases the response transience of excitatory currents measured in ON-T RGCs compared to control. This enhanced transience in GABA_A/C receptor blockers is due to an increase in the amplitude of the initial peak component of the response (control peak amplitude: -833.7±103.3 pA; SR95531+TPMPA peak amplitude: 2023±372.7pA; p=0.03, Wilcoxon signed rank test), with no change to the later sustained component (control plateau amplitude: -200.7±14.71pA; SR95531+TPMPA plateau amplitude: -290.9±43.69pA; p=0.15, Wilcoxon signed rank test).

We should clarify that this result indicates that GABAergic inhibition makes the excitatory inputs to ON-T RGCs less transient. Block of GABA receptors increased transience, thus intact GABAergic transmission appears to limit the initial peak of the response and therefore make excitatory currents more sustained. We unfortunately were not able to examine whether sustained excitatory currents in ON-S RGCs would become more transient using the same approach. In our hands, bath application of SR95531+TPMPA led to the generation of large-amplitude (>1nA) oscillatory bursts of excitatory input that developed within 5 minutes and persisted for the duration of the incubation (up to ~30 min) in drugs. Further, presentation of light steps tended to induce variable amplitude responses, likely dependent on the presence of spontaneous bursts; when large amplitude responses were evoked, these typically oscillated for several seconds after the step.

To examine a potential role for presynaptic inhibition in transient vs. sustained bipolar cell output, we therefore chose to eliminate amacrine cell-mediated inhibition by bath application of the AMPA/kainate receptor antagonist NBQX in additional iGluSnFR measurements. This manipulation should leave ON bipolar cell responses intact while eliminating most amacrine cell-mediated responses (and OFF bipolar cell driven responses). In separate experiments, we also eliminated inhibition from spiking amacrine cells by bath application of TTX. As shown in new Fig. 7, sustained and transient responses persisted in distal versus proximal RGC dendrites, respectively. Compared to SR95531/TPMPA, bath application of NBQX was not associated with spontaneous bursts of glutamate release around ON-S dendrites. These results show that amacrine cell-mediated inhibition is not required for either sustained or transient glutamate release from bipolar cells that provide input to ON-S and ON-T RGCs.

Small points: 

(1) The legend of Figure 1 (D) refers to shaded areas to show {plus minus} SEM, but no shade is visible (at least in my printout).

The SEM shading is there in Fig. 1D but is mostly obscured by the mean lines for the respective RGC types. We have added this to the figure caption.

(2) I found the reported Vrest for the ON bipolar cells somewhat depolarized. Perhaps due to the uncompensated junction potentials? 

These measurements are indeed not corrected for the liquid junction potential (which is approximately -10.8 mV between K-gluconate internal and Ames’ solution). We did not apply this correction since the appropriate value is not clear in perforated patch recordings as the intracellular chloride concentration is unknown (and can differ from that in the pipette solution). We have clarified this in the results text where we describe the Vrest values (lines 335-338).

(3) It is Wilcoxon signed rank test, not Wilcoxan. 

Thanks for catching this. This has been corrected in the revised manuscript.

Reviewer #2 (Recommendations For The Authors): 

Some amacrines express vesicular Glut-3 transporter and are reported to release glutamate (Marshak, Vis Neurosci 2016). Are Amacrine vGlut3 signals postsynaptic (within ~0.5 um) to cone bpc ribbons?

We did not characterize VgluT3-expressing amacrine cells in our SEM datasets. A recent study by Friedrichson et al. (Nat. Comm. 2024; PMID 38580652) using 3D SEM reconstructions found that Vglut3-amacrines are postsynaptic to both type 5i and type 6 bipolar cells, as well as other type 5/xbc bipolar cells (and receive >50% of their input from type 3a OFF bipolar cells).

How far apart are the postsynaptic targets from the ribbon release sites? The ribbons at type 5i bpc/On-T input appear separated from the dendrites of On-T rgcs (Figure 8C). At least further away than the type 6 bpc ribbons are from On-S rgc dendrites (Figure 8C). Distance may create a thresholding phenomenon, whereby only multivesicular bouts at the onset of depolarization are able to elevate synaptic Glu to levels needed to activate On-T GluRs. See Grabner et al Nat Comm 2023 for such scenarios in the outer retina.

This is an intriguing possibility, but we should point out that the presynaptic ribbons in Fig. 9C (former Fig. 8C) are similar distances (within the resolution of our reconstructions) from the ON-T and ON-S dendrites. We have increased the brightness of the dendrite segments for both RGC types in the resubmission figure; note that ON-T RGCs have spine-like protrusions that may not have been as apparent in the previously submitted version of our manuscript.

In Figures 1 and 2, Sustained responses look like the derivative of Transient responses, minus the negative going inflection. In addition, the sustained responses appear to have a lower threshold of activation than the transient On rgcs, because there are more bouts of action potentials (and membrane depol in V-clamp) with earlier onset in sustained than transients traces. It would be great if the GLuSniff data captured these differences. Take cumulative dF/F and see what the onset time is, or an initial tau if possible.

This is a good suggestion. However, we are reluctant to make detailed quantitative comparisons such as this without further validation of how the kinetics of the iGluSnFR signals relate to kinetics of glutamate release.  A specific concern is that differences in the location and amount of iGluSnFR expression could impact any such comparisons.

A recent study by Kim et al von Gersdorff (Cell Reports, 2023) presents interesting phases of release in response to light flashes, measured from AIIs, and complementary results from pairs of rbcs-AIIs. The findings highlight the complexity of SV pools under well-controlled experiments. Could their results be explained as variations in rbc ribbon size through development, and possibly between rbcs or within an rbc? 

This certainly seems possible and would be consistent with the dependence of release on ribbon size that our results support.  It would be interesting to see if there are clear anatomical correlates of that change in release properties.  

Figure 5 is a pivotal point in the study, but my review has identified numerous weaknesses. The feedback inhibition onto bipolar cell terminals is likely to sculpt glutamate release, and the results do not convincingly rule out this possibility. The suggestions for improvements range from the data needing to be reanalyzed with regard to statistical tests, and/or adding a few more data points (n = 5) before concluding a p: 0.06 is insignificant. 

We have added an additional recording to this data set. With n= 6 cells, there is now a statistically significant difference between ON-T RGC excitatory currents measured in control conditions versus during GABA_A/C receptor blockade. Please note that all the recordings shown in Figure 5C-F are from ON-T RGCs (the two panels show separately block of GABergic and glycinergic receptors). We did not make it sufficiently clear that the original trend (now statistically significant) is opposite of that expected if presynaptic GABAergic inhibition contributes to response transience in ON-T RGCs.  What we see is that excitatory synaptic inputs to ON-T RGCs become more transient (rather than mpre sustained) during GABA_A/C receptor blockade. We have revised the text in that section to make this point more clearly.

We have also included new data from iGluSnFR measurements showing that bath application of NBQX does not affect light step-evoked glutamate release kinetics at proximal (sustained) or distal (transient) RGC dendrites (control: steady-state amp. as % of peak amp. 13 ± 10; mean ± S.D.; n = 189 ROIs/4 FOVs for ON-T dendrites vs 40 ± 12; mean ± S.D.; n = 287 ROIs/8 FOVs for ON-S dendrites; NBQX: 6 ± 3; mean ± S.D.; n = 112 ROIs/1 FOV for ON-T dendrites vs 23 ± 9; mean ± S.D.; n = 97 ROIs/2 FOVs for ON-S dendrites; *p<0.001). By blocking glutamate receptors on amacrine cells, NBQX (AMPA/KAR antagonist) eliminates all/most amacrine cell-mediated signaling in the retina and should therefore abolish presynaptic inhibitory input to bipolar cell terminals across the IPL. Taken together, our results indicate that presynaptic inhibition does not play a critical role in establishing transient versus sustained kinetics for the stimulus conditions we employed in our study.

There is a need to cite more recent literature on bipolar cell ribbons (e.g. see Wakeham et al., Front. Cell. Neurosci., 2023), in order to support experimental design and interpretation of the results. The authors should discuss their Ribeye-KO data from Okawa et al 2019 Nat Comm, Figure 7, in the context of their new iGluSnFR results. 

Thank you for prompting us on this issue. We have expanded the discussion regarding ribbons and included more citations to the ribbon literature. That is largely in the three paragraphs starting on line 727.

One point deserves emphasis because it is central to the authors' ribbon model but not consistent with their data. The ribbon model as they put it, and as commonly stated, holds that a transient phase of release at the onset of depolarization indicates the depletion of the primed SVs, and the subsequent slower rate of release (steady state release in the authors' terms) reflects recruiting, priming, and release of new SVs. The On-transient dendrite GluSnf responses agree with this multiphasic process, but the sustained responses show only an elevation in glutamate without a pronounced initial peak, creating a square-wave-shaped response (Figure 6B). This does not agree with the simple ribbon-based release model. I would expect the signals from the T- and S-on dendrites to have a comparable initial phase, while the sustained phase should be greater in amplitude for the S-on dendrites. More discussion may clarify possible mechanisms.

Thanks for pointing this out. The example iGluSnFR traces we originally included in the manuscript were not entirely representative in that they did not show much initial transient phase. Note there is a distribution of steady-state amplitudes for proximal dendrites in Fig. 6C; the examples are from ROIs from the upper end of the distribution. In the new Figure 7, we have included some additional examples that show both a clear transient and sustained component. The summary data in Figure 6C shows the distribution of sustained/transient ratios across ROIs.  

Reviewer #3 (Recommendations For The Authors): 

(1) It would be interesting to understand the differences in IPSCs in the two RGC types. Perhaps they are small in both types, which would explain their apparent lack of impact on temporal tuning. The authors may already have these data.

We did make measurements of noise-evoked IPSCs (as well as EPSCs) in a subset of ON-T and ON-S recordings. We have now included this data as Figure S3. There are slight differences in the kinetics of inhibition between RGC types (Fig. S3C) and there is a trend towards stronger inhibition (relative to excitation) in ON-T RGCs compared to ON-S RGCs (Fig. S3E), although there is not a statistically significant difference. In both cases excitatory synaptic currents are as large or larger than inhibitory currents, and this does not include the difference in driving force near spike threshold which will favor excitatory input by a factor of 2-3.  Hence our data suggests that postsynaptic inhibition does not play a major role in generating the differential temporal spiking responses of ON-T and ON-S RGCs. However, additional experiments examining the relative contribution of excitation and inhibition to spiking output in these RGCs would be needed to reach a firm conclusion.

The pharmacological experiments in which we blocked inhibition (Fig. 5C-F, new Fig. 7) were designed to test the effect of presynaptic inhibition on bipolar cell output (voltage-clamp isolation of excitatory currents in Fig. 5; iGluSnFR measurements of glutamate release in Fig. 7). We do not mean to suggest that postsynaptic inhibition does not have any role in shaping the spiking behavior of these RGC types, but that transient vs. sustained kinetics are already present in the bipolar cell output and that presynaptic inhibition of bipolar cell terminals does not appear to account for this difference.  We have revised the text throughout to be clearer on this point.

(2) It could be convincing to show transient/sustained differences between RGC types in dim light, where the response would depend on the rod bipolar/AII circuit. In this case, any difference in temporal properties would presumably be explained by differences that localize to the cone bipolar cell axon terminals. Indeed, is that the result in Figure 1B? This seems to be a dim stimulus presented on darkness, which may be driven through the rod bipolar pathway. The authors could then discuss the interpretation of this data in terms of the rod bipolar circuit. 

Yes, Figure 1B is a dim light step (~30R*/rod/s) presented from darkness and the distinction between cells is clear down at still lower light levels that more effectively isolate signaling through the rod bipolar pathway. Thanks for making this point that observation of distinct temporal responses under scotopic conditions where signals suggests these differences must arise at and/or downstream of cone bipolar cell output. We have included additional text (lines 361-365) in the results describing bipolar cell responses that raise this point.

(3) Glutamate release was already measured across the full IPL depth by Borghuis et al. (2013) and Franke et al. (2017). It would be appropriate to better motivate the current study based on these existing measurements.

We have clarified that these important studies provided important motivation for measuring excitatory synaptic input to ON-T vs. ON-S RGCs (lines 165-169).   

(4) Line 212/213. It would be appropriate to add to the list of papers showing the different stratification of transient vs. sustained responses: Borghuis et al. (2013) and Beaudoin et al. (2019).

Thank you - these references have been added.  

(5) Line 635-638. It would be useful to discuss papers by Pottackal et al. (2020, 2021), which suggested that a single presynaptic cell (starburst) can signal with different temporal properties depending on the postsynaptic target (other starburst vs. DSGCs). The mechanism was not completely resolved (i.e., it was not explained by differences in presynaptic Ca channels at the two synapse types), but it at least shows that neurotransmitter release can show different filtering depending on the postsynaptic target from the same presynaptic neuron. (This could also be at play for the type 6 bipolar cell inputs to ON-S vs. ON-T RGCs in the present study.)

We have added a reference to Pottackal et al 2021 in this section.

(6) Line 714. Should describe the procedure for embedding the tissue in agarose. 

We have added more detail regarding agarose embedding for preparation of retinal slices in the methods.

(7) Line 775. Need a better description of the virus (not the construct), what serotype? Provide the Addgene number if available. 

This has been added to the methods.

(8) Line 808. Was the SD for the gaussian really 50%? That would cut off a lot of the distribution, i.e., it would get clipped at 0. 

Yes, the SD for Gaussian noise was 50%. This high contrast stimulus was used in part to achieve measurable signals from bipolar cells. You are correct that some of the distribution was clipped at 0 (it was also clipped at twice the mean to make sure that the distribution remained symmetrical). The clipping was accounted for during our LN analyses.

(9) The paper should discuss Swygart et al. (2024) results showing different spatial surround properties of neighboring synapses from a type 6 bipolar cell. Based on this result, it would seem very likely that amacrine cells could play a role in shaping the temporal processing of bipolar cell glutamate release as well. Indeed, spatial and temporal processing will not be completely independent in a typical experiment. For example, with the spot stimulus used in the present study, bipolar cells within the center versus the edge of the spot will have different balances of center/surround activation, which could potentially influence their temporal processing.

We have included discussion of results from Swygart et al 2024 in the section of the Discussion in which we point out differences in surround inhibition between ON-S and ON-T RGCs (lines 710-714). We agree that spatial and temporal processing are not completely independent. Our results with SR95531/TPMPA indicate ON-T RGCs receive stronger GABAergic surround inhibition than ON-S RGCs (Fig. S8). However, our results in Fig. 5C-D show GABAergic surround inhibition makes ON-T excitation more sustained rather than more transient. So even though bipolar cells presynaptic to ON-T RGCs receive stronger surround inhibition (Fig. S8), this inhibition does not establish the transient kinetics of glutamate release from these bipolar cells (in fact, it works to make release more sustained). Additional iGluSnFR experiments where we used NBQX to block all/most amacrine cell-mediated responses also suggest presynaptic inhibition does not have an important role in establishing differential glutamate release kinetics onto ON-S vs. ON-T RGC dendrites (Fig. 7).

(10) Cui et al. 2016 described ON-S Alpha as having a divisive suppression mechanism that explained the temporal properties of white-noise response better than a standard LN model. Do the authors think the divisive suppression reflects a property of the excitatory synapses independent of inhibition?

This is an interesting question, but one for which we don’t have a good answer for now. As mentioned in some of the above responses and as we have tried to clarify in the manuscript, we do not mean to imply that there is no role for presynaptic inhibition in modulating bipolar cell output, including for the divisive suppression described by Cui et al. Rather, our point is that the distinction between transient and sustained excitatory input to ON-T and ON-S RGCs does not require presynaptic inhibition and is more likely an intrinsic property of the bipolar cell synapses. 

(11) Do the authors mean to imply that the pool size at bipolar cell ribbon synapses could depend on the use of Ames vs. ACSF? 

For now, we do not have a good answer as to why there are quantitative differences in response kinetics between Ames and ACSF. We have not done any experiments to investigate whether ribbon sizes or ribbon pools are different in the different solutions.

(12) More generally, different mean luminance levels could drive different levels of baseline glutamate release, which could alter the available pool of vesicles at bipolar cell ribbon synapses. Can we explain varying degrees of transient/sustained in the same cell at different levels of mean luminance based on this mechanism (e.g., Grimes et al., 2014)?

Yes, the emergence of a transient component of excitatory input to ON-S RGCs at ~100 R*/rod/s versus at scotopic levels (0.5 R*/rod/s) in Grimes et al. (2014) could be due to differences in the number of releasable vesicles (due to different type 6 bipolar cell axon terminal membrane potentials and hence differences in spontaneous release rates) at the different light levels.

We should note that although ON-T and ON-S RGCs exhibit some changes in transient/sustained kinetics across different light levels, the relative differences between these RGC types are preserved across light levels. We have included a statement about this in the text (lines 361-367).

(13) Figure 1. Have the authors considered performing the LN analysis of the firing responses, to compare the degree of rectification between the two RGC types?

This is a good suggestions. From an LN analysis of spiking responses, we do not observe a clear difference between the static nonlinearity component of the model for ON-T and ON-S RGCs. Both RGC types are strongly rectified under our experimental conditions.  

(14) Figure 5. Do the authors have the pharmacology data for the ON-S cells? There are examples of sustained EPSCs in amacrine cells that become more transient after blocking inhibition, which at least suggests that inhibition can play some role in the transient/sustained nature of glutamate release (Park et al., 2015, Figure 3). Perhaps ON-S cells likewise become more transient with inhibition blocked. 

(The colored symbols in A were not visible in a printout. It would be useful to indicate the cell type (ON-T) in C and E). 

As described above in the response to reviewer 1’s recommendation for authors, we were not able to use SR95531/TPMPA for recordings from ON-S RGCs. Bath application of these drugs led to oscillatory bursts of excitatory input to ON-S RGCs. However, the lack of effect of bath-applied NBQX on the kinetics of glutamate release around either ON-T or ON-S RGC dendrites (new Fig. 7) suggests that presynaptic inhibition does not contribute to generating sustained excitation to ON-S RGCs (or transient excitation to ON-T RGCs).  

We have corrected Fig. 5A to include the referenced colored symbols and have also edited Fig 5C and E to clarify that measurements in Fig. 5C-F are from ON-T RGCs.

(15) Figure 6 legend. Should be Kcng4-Cre, not KCNG-Cre. Also, it should make clear that this is cre-dependent expression of iGluSnFR. For C, were the statistics based on the number of FOVs? 

Thanks for catching this, we have corrected Figure 6 legend. The methods section includes a description of how we achieved iGluSnFR expression on alpha RGC dendrites via a cre-dependent viral strategy in Kcng4-Cre mice.  We have also clarified that the statistics are based on ROIs in Figure 6C.

(16) Figure 7, Flashes were apparently 400% contrast on a dim background. What was the background? Is there a rod component to the response in this case? 

In Figure 7 (now Figure 8), the same background (~3300 R*/rod/s; 2000 P*/Scone/s) was used as in the Gaussian noise and step response experiments. At this light level, the response should be primarily be mediated by cones.

(17) Figure S1. The colors here differ from those in previous figures (Here, ON-T, magenta; ON-S, cyan). Is something mislabeled? 

Thanks for catching this. We mistakenly swapped the labels in the legend for Fig. S1. The figure colors were correct, but we have corrected the legend in the revised manuscript.

(18) Figure S2. For the LN model for RGC synaptic currents, the ON-S are more rectified than some previous recordings (Cui et al., 2016). Is this perhaps explained by different light levels?

We aren’t sure why ON-S excitatory currents are more strongly rectified in our recordings compared to Cui et al., 2016. Cui et al. used an ~20-fold higher background light intensity (~40,000 P*/cone/s vs. ~2000 P*/cone/s in our study), so different light levels may be a factor (although we should point out that rectification increases in these RGCs between scotopic to low photopic light levels (see Grimes et al., 2014 and Kuo et al., 2016).

(19) The study is apparently comparing PV1 and PV2 described in Farrow et al. (2013; see Supplementary information for stratification analysis), which should be cited.

Thanks, we have corrected this oversight in the revised manuscript. We now cite Farrow et al and mention the connection to PV1 and PV2 in the first paragraph of Results (lines 104-108).

eLife Assessment

This important work provides a new method to extract cfDNA from residual plasma from heparin separators for molecular testing. The evidence supporting the authors' claims is convincing, although some further metrics should also be evaluated. This finding will be interesting to people working in epigenomics and infectious disease diagnostics.

Reviewer #1 (Public review):

Summary:

The manuscript "Adapting Clinical Chemistry Plasma as a Source for Liquid Biopsies" addresses a timely and practical question: whether residual plasma from heparin separator tubes can serve as a source of cfDNA for molecular profiling. This idea is attractive, since such samples are routinely generated in clinical chemistry labs and would represent a vast and accessible resource for liquid biopsy applications. The preliminary results are encouraging, but in its current form, the study feels incomplete and requires additional work.

My major concerns/suggestions are as follows:

(1) Context and literature

The introduction provides only limited background on prior attempts to use heparinized plasma for cfDNA work. It is well known that heparin can inhibit PCR and sequencing library preparation, which has historically discouraged its use. The authors should summarize the relevant literature more comprehensively and explain clearly why this approach has not been widely adopted until now, and how their work differs from or overcomes these earlier challenges.

(2) Genome-wide coverage

The analyses focus on correlations in methylation patterns and fragmentation metrics, but there is no evaluation of sequencing coverage across the genome. For both WGS and WMS, it would be important to demonstrate whether cfDNA from heparin plasma provides unbiased coverage, or whether certain genomic regions are systematically under-represented. A comparison against coverage profiles from cell-derived DNA (e.g., PBMC genomic DNA) would help to put the results in context and assess whether the material is suitable for whole-genome applications.

(3) Viral detection sensitivity

The study shows strong concordance in viral detection between EDTA and heparin samples, but the sensitivity analysis is lacking. For clinical relevance, it is critical to demonstrate how well heparin-derived plasma performs in low viral load cases. A quantitative comparison of viral read counts and genome coverage across tube types would strengthen the conclusions.

Reviewer #2 (Public review):

Summary:

The authors propose that leftover heparin plasma can serve as a source for cfDNA extraction, which could then be used for downstream genomic analyses such as methylation profiling, CNV detection, metagenomics, and fragmentomics. While the study is potentially of interest, several major limitations reduce its impact; for example, the study does not adequately address key methodological concerns, particularly cfDNA degradation, sequencing depth limitations, statistical rigor, and the breadth of relevant applications.

Strengths:

The paper provides a cheap method to extract cfDNA, which has broad application if the method is solid.

Weaknesses:

(1) The introduction lacks a sufficient review of prior work. The authors do not adequately summarize existing studies on cfDNA extraction, particularly those comparing heparin plasma and EDTA plasma. This omission weakens the rationale for their study and overlooks important context.

(2) The evaluation of cfDNA degradation from heparin plasma is incomplete. The authors did not compare cfDNA integrity with that extracted from EDTA plasma under realistic sample handling conditions. Their analysis (lines 90-93) focuses only on immediate extraction, which is not representative of clinical workflows where delays are common. This is in direct conflict with findings from Barra et al. (2025, LabMed), who showed that cfDNA from heparin plasma is substantially more degraded than that from EDTA plasma. A systematic comparison of cfDNA yields and fragment sizes under delayed extraction conditions would be necessary to validate the feasibility of their proposed approach.

(3) The comparison of methylation profiles suffers from the same limitation. The authors do not account for cfDNA degradation and the resulting reduced input material, which in turn affects sequencing depth and data quality. As shown by Barra et al., quantifying cfDNA yield and displaying these data in a figure would strengthen the analysis. Moreover, the statistical method applied is inappropriate: the authors use Pearson correlation when Spearman correlation would be more robust to outliers and thus more suitable for methylation and other genomic comparisons.

(4) The CNV analysis also raises concerns. With low-coverage WGS (~5X) from heparin-derived cfDNA, only large CNVs (>100 kb) are reliably detectable. The authors used a 500 kb bin size for CNV calling, but they did not acknowledge this as a limitation. Evaluating CNV detection at multiple bin sizes (e.g., 1 kb, 10 kb, 50 kb, 100 kb, 250 kb) would provide a more complete picture. In addition, Figure 3 presents CNV results from only one sample, which risks bias. Similar bias would exist for illustrations of CNVs from other samples in the supplementary figures provided by the authors. Again, Spearman correlation should be applied in Figure 3c, where clear outliers are visible.

(5) It is important to point out that depth-based CNV calling is just one of the CNV calling methods. Other CNV calling software using SNVs, pair-reads, split-reads, and coverage depth for calling CNV, such as the software Conserting, would be severely affected by the low-quality WGS data. The authors need to evaluate at least two different software with specific algorithms for CNV calling based on current WGS data.

(6) The authors omit an important application of cfDNA: somatic mutation detection. Degraded cfDNA and reduced sequencing depth could substantially impact SNV calling accuracy in terms of both recall and precision. Assessing this aspect with their current dataset would provide a more comprehensive evaluation of heparin plasma-derived cfDNA for genomic analyses.

Author response:

Reviewer #1 (Public review):

Summary:

The manuscript "Adapting Clinical Chemistry Plasma as a Source for Liquid Biopsies" addresses a timely and practical question: whether residual plasma from heparin separator tubes can serve as a source of cfDNA for molecular profiling. This idea is attractive, since such samples are routinely generated in clinical chemistry labs and would represent a vast and accessible resource for liquid biopsy applications. The preliminary results are encouraging, but in its current form, the study feels incomplete and requires additional work.

We thank the reviewer for the encouragement and for recognizing the potential of clinical chemistry plasma as an accessible source for cfDNA-based analyses. We look forward to addressing the gaps described below.

My major concerns/suggestions are as follows:

(1) Context and literature

The introduction provides only limited background on prior attempts to use heparinized plasma for cfDNA work. It is well known that heparin can inhibit PCR and sequencing library preparation, which has historically discouraged its use. The authors should summarize the relevant literature more comprehensively and explain clearly why this approach has not been widely adopted until now, and how their work differs from or overcomes these earlier challenges.

We thank the reviewer for their valuable comments and agree that the review of prior work needs to be more thorough, with the gaps clearly identified. In the revised manuscript, we will expand the introduction to include a more comprehensive summary of prior studies. Some of the material was in the Discussion, but we will move it to the introduction in the revision. In general, we will comment briefly here about the novelty of this work and the previous gap in the literature:

(1) Previous pre-analytical studies use DNA fluorometry and qPCR, which cannot distinguish between genomic DNA contamination (from cells) and cfDNA. In contrast, our study uses adapter-based NGS with DNA spike-ins, which can exclude genomic DNA contamination and enable precise quantification of cfDNA input and measurement of their lengths. In Figure 5b-c, we demonstrate that we were able to match our paired sample results only under the measurements of our NGS study, not in previous attempts. Note the current Fig. 5 captions b&c should be swapped and will be corrected in the revision.

(2) As the reviewer has astutely mentioned, heparin is a well-recognized inhibitor of PCR, and heparinized specimens are historically contraindicated for molecular testing. However, most modern cfDNA assays now use NGS, which includes multiple purification steps before PCR amplification, minimizing the impact of heparin interference.

(3) Previous clinical chemistry tests used serum tubes, which are known to generate background gDNA during clotting and are therefore unsuitable for cfDNA-based analyses. In recent years, modern hospital chemistry laboratories, especially those supporting emergency departments, have gradually transitioned to heparin separator tubes for faster turnaround. Hence, residual plasma from heparin separator tubes is a more recent option, one that was not widely available when key pre-analytical studies on cfDNA were performed.

(2) Genome-wide coverage

The analyses focus on correlations in methylation patterns and fragmentation metrics, but there is no evaluation of sequencing coverage across the genome. For both WGS and WMS, it would be important to demonstrate whether cfDNA from heparin plasma provides unbiased coverage, or whether certain genomic regions are systematically under-represented. A comparison against coverage profiles from cell-derived DNA (e.g., PBMC genomic DNA) would help to put the results in context and assess whether the material is suitable for whole-genome applications.

Thank you for the insightful comment. We agree that evaluating sequencing coverage across the genome is important for assessing the suitability of cfDNA from heparin separators. In response, we are performing additional, in-depth runs to compare genome-wide coverage profiles in the Hospital Cohort. The results of these analyses will be included in the revised version of the manuscript.

(3) Viral detection sensitivity

The study shows strong concordance in viral detection between EDTA and heparin samples, but the sensitivity analysis is lacking. For clinical relevance, it is critical to demonstrate how well heparin-derived plasma performs in low viral load cases. A quantitative comparison of viral read counts and genome coverage across tube types would strengthen the conclusions.

We agree that evaluating analytical sensitivity in cases with low viral loads is important for understanding clinical performance. To address this point, we plan to include additional paired cases with viral loads below 1,000 IU/mL and examine the correlation of viral read counts between EDTA and heparin separators in this subset.

Reviewer #2 (Public review):

Summary:

The authors propose that leftover heparin plasma can serve as a source for cfDNA extraction, which could then be used for downstream genomic analyses such as methylation profiling, CNV detection, metagenomics, and fragmentomics. While the study is potentially of interest, several major limitations reduce its impact; for example, the study does not adequately address key methodological concerns, particularly cfDNA degradation, sequencing depth limitations, statistical rigor, and the breadth of relevant applications.

We thank the reviewer for the insightful comments and will work to clarify and address the mentioned issues. We do not find the residual plasma from the heparin separator to be a replacement for gold standard methods. Instead, we take it as a practical and complementary resource that may help broaden the accessibility of samples. Comparable cfDNA metrics highlight its potential to serve as an additional source for biobanking and research applications.

Strengths:

The paper provides a cheap method to extract cfDNA, which has broad application if the method is solid.

We thank the reviewer for the encouraging comment. While cost-effectiveness is a practical advantage, we believe the greater strength of this approach lies in the accessibility of sampling. Residual plasma from routine clinical tests offers an opportunity to include patients or time points that would otherwise be difficult to capture, such as those with severe illness or those sampled before treatment.

Weaknesses:

(1) The introduction lacks a sufficient review of prior work. The authors do not adequately summarize existing studies on cfDNA extraction, particularly those comparing heparin plasma and EDTA plasma. This omission weakens the rationale for their study and overlooks important context.

We thank both reviewers for this comment. See above under Reviewer 1’s responses for our provisional perspective on the background literature and gap. We will expand the Introduction to provide a more comprehensive summary of prior studies.

(2) The evaluation of cfDNA degradation from heparin plasma is incomplete. The authors did not compare cfDNA integrity with that extracted from EDTA plasma under realistic sample handling conditions. Their analysis (lines 90-93) focuses only on immediate extraction, which is not representative of clinical workflows where delays are common. This is in direct conflict with findings from Barra et al. (2025, LabMed), who showed that cfDNA from heparin plasma is substantially more degraded than that from EDTA plasma. A systematic comparison of cfDNA yields and fragment sizes under delayed extraction conditions would be necessary to validate the feasibility of their proposed approach.

We appreciate this thoughtful comment, which highlights reasonable concerns about cfDNA degradation in heparin. We would like to clarify that the Hospital Cohort, which only used leftover plasma in the clinical lab, was designed to reflect real-world clinical workflows, where unavoidable delays before plasma processing are already incorporated. In the Healthy Cohort, a subset of samples is also processed after controlled delays, as shown in Supplementary Figure 2.

Regarding the differing results in Barra et al. (2025, LabMed), where heparin tubes showed 85% cfDNA degradation, it is important to note that samples were incubated at 37 °C for 24 hours. We anticipate that endogenous nuclease would be active under 37 °C and would cause cfDNA degradation. However, this condition differs markedly from the relevant clinical workflows we describe here. In the routine hospital settings, blood samples are typically kept at room temperature for up to 60 minutes during transport and waiting. The outpatient setting can be more variable, but samples here are supposed to be refrigerated during transportation. They are then processed in high-throughput, fully automated systems that comply with nationally standardized quality regulations in the United States (CLIA). The resultant plasma will be physically separated from cellular components because of the gel in the heparin separators. The processed tubes are subsequently transferred to refrigerated storage at 4 °C. Under these conditions, samples do not experience prolonged exposure to elevated temperatures such as 37 °C, and refrigeration usually occurs within two hours of collection. We will incorporate these details in the revised manuscript.

Also, as we mentioned in our reply to Reviewer 1, Barra et al. used qPCR like most cfDNA pre-analytical studies, but qPCR is not a perfect DNA quantification method for NGS-based downstream analyses because it measures both cfDNA and contaminating genomic DNA. The latter can be excluded by most NGS assays. By using constant spike-in internal controls, our approach directly quantifies the amount of sequenceable cfDNA, providing a more accurate estimate of input DNA (Figure 5c). In one possible future experiment, the same sample in the Healthy Cohort can be delayed by 1-2 hours prior to processing (centrifugation and refrigeration) and kept at room temperature rather than 4 °C to mimic real-world delays. Outputs would be cfDNA yields and fragment sizes, and we would use constant spike-ins to quantify the amount of sequenceable DNA.

(3) The comparison of methylation profiles suffers from the same limitation. The authors do not account for cfDNA degradation and the resulting reduced input material, which in turn affects sequencing depth and data quality. As shown by Barra et al., quantifying cfDNA yield and displaying these data in a figure would strengthen the analysis. Moreover, the statistical method applied is inappropriate: the authors use Pearson correlation when Spearman correlation would be more robust to outliers and thus more suitable for methylation and other genomic comparisons.

We appreciate the reasonable concerns regarding cfDNA degradation and agree that the methylation profile is not an adequate metric for degradation. To evaluate for degradation, we will focus on NGS-derived length profiles (WGS data) and constant spike-in DNA. We appreciate the reviewer’s suggestion to use the Spearman correlation, and this will be incorporated.

(4) The CNV analysis also raises concerns. With low-coverage WGS (~5X) from heparin-derived cfDNA, only large CNVs (>100 kb) are reliably detectable. The authors used a 500 kb bin size for CNV calling, but they did not acknowledge this as a limitation. Evaluating CNV detection at multiple bin sizes (e.g., 1 kb, 10 kb, 50 kb, 100 kb, 250 kb) would provide a more complete picture. In addition, Figure 3 presents CNV results from only one sample, which risks bias. Similar bias would exist for illustrations of CNVs from other samples in the supplementary figures provided by the authors. Again, Spearman correlation should be applied in Figure 3c, where clear outliers are visible.

We appreciate the reviewer’s constructive comments regarding the CNV analysis. We agree that the use of low-coverage WGS (~5×) limits the reliable detection of small CNVs, and we will acknowledge this as a limitation in the revised manuscript. To address this point, we will perform additional analyses using 50kb as bin sizes. To reduce potential bias from single-sample representation, we will show the aggregated CNV plots for all CNA-positive cases along with their log₂ copy ratio correlations, and Spearman’s correlation will be applied as suggested.

(5) It is important to point out that depth-based CNV calling is just one of the CNV calling methods. Other CNV calling software using SNVs, pair-reads, split-reads, and coverage depth for calling CNV, such as the software Conserting, would be severely affected by the low-quality WGS data. The authors need to evaluate at least two different software with specific algorithms for CNV calling based on current WGS data.

Thank you for this suggestion. We will evaluate CNV profiles using alternative informatics methods.

(6) The authors omit an important application of cfDNA: somatic mutation detection. Degraded cfDNA and reduced sequencing depth could substantially impact SNV calling accuracy in terms of both recall and precision. Assessing this aspect with their current dataset would provide a more comprehensive evaluation of heparin plasma-derived cfDNA for genomic analyses.

We thank the reviewer for emphasizing SNVs as an important application of cfDNA. We agree that the limited volume of residual plasma is a constraint. Routine chemistry tests leave ~1–2 mL of plasma, and this limited volume places an upper limit on performing SNV analysis. We will expand the discussion of this limitation in the paper. Our approach is not intended to replace specialized tubes for large-volume cfDNA collection but rather to complement them by enabling the use of residual material.

eLife Assessment

The characterization of a dissociable Mediator subunit implicated in cellular pathways, particularly lung alveolar function and HIV latency, would be conceptually interesting. The authors have preliminary evidence for a stable Med16 subcomplex that may regulate specific genes. This work is useful in that it points to interactions between Med16 and UBP1, but the evidence is preliminary and incomplete.

Reviewer #1 (Public Review):

Summary:

Characterization of a dissociable Mediator subunit implicated in cellular pathways, particularly lung alveolar function, and HIV latency is conceptually interesting.

Strengths:

The strengths of this study are:

(1) Demonstration of MED16 dissociation from the core Mediator complex and formation of a subcomplex containing MED16, upstream-binding protein 1 (UBP1), and transcription factor cellular promoter 2 (TFCP2) by elegant biochemical fractionation and immunoblotting analysis.

(2) Defining nine N-terminal WD-40 repeats (WDRs) of MED16 as a Mediator-incorporating module and the C-terminal ⍺β-domain (157 amino acids) important for interaction with the UBP1-TFCP2 heterodimeric complex.

(3) Illustration of a weak hydrophobic interaction between MED16 and the Mediator core that could be disrupted by 1,6-hexanediol, but not by its 2,5-hexanediol isomer nor by high salt (500 mM NaCl) disruption.

(4) Classification of UBP1-upregulated cellular genes typically containing binding sites flanking the transcription start site (TSS) in contrast to UBP1-downregulated genes often containing a TSS-overlapping UBP1-binding site

(5) Presenting evidence for Mediator complex-dissociated free MED16-repressed HIV promoter activity through functional association with UBP1 and showing bromodomain-containing protein 4 (BRD4) inhibitor JQ1 that potentially disrupts BRD4-inhibited HIV-1 transcription elongation could lead to reversal of HIV-1 latency.

Weaknesses:

Nevertheless, foreseeable weaknesses include:

(1) No clear demonstration of MED16-UBP1-TFCP2 indeed forming a trimeric core subcomplex in regulating cellular gene transcription and HIV-1 promoter inhibition

(2) No validation of transcriptomic datasets and pathways identified.

(3) Use of mostly artificial reporter gene constructs and non-HIV host cells (e.g., human 293T embryonic kidney cells, human HeLa cervical cancer cells, and mouse HT pancreatic cancer cells) for examining MED16/UBP1-regulated HIV transcription.

(4) Inconsistent use of 293T and HeLa cells in the characterization of dissociated MED16 interaction with UBP1 and TFCP2.

(5) In vitro transcription using immobilized DNA templates was not performed to a high standard, thus failing to convincingly show MED16/UBP1-inhibited HIV-1 transcription preinitiation complex formation.

Reviewer #2 (Public Review):

Summary:

The article from Zheng et al. proposes an interesting hypothesis that the Med16 subunit of Mediator detaches from the complex, associates with transcription factor UBP1, and this complex activates or represses specific sets of genes in human cells. Despite my excitement upon reading the abstract, I was concerned by the lack of rigor in the experimental design. The only statement in the abstract that has some experimental support is the finding that Med16 dissociates from the Mediator and forms a subcomplex, but the data shown remain incomplete.

Strengths:

The authors have preliminary evidence that a stable Med16 complex may exist and that it may regulate specific sets of genes.

Weaknesses:

The experiments are poorly designed and can only infer possible roles for Med16 or UBP1 at this point. Furthermore, the data are often of poor quality and lack replication and quantitation. In other cases, key data such as MS results aren't even shown. Instead, we are given a curated list of only about 6 proteins (Figure S1), a subset of which the authors chose to pursue with follow-up experiments. This is not the expected level of scientific process.

(1) The data supporting the Med16 dissociation and co-association with UBP1 are incomplete and not convincing at this stage. According to the Methods and text, the gel filtration column was run with "un-dialyzed HeLa cell nuclear extract" and eluted in 300mM KCl buffer. The extracts were generated with the Dignam/Roeder method according to the text. Undialyzed, that means the extract would be between 0.4 - 0.5M NaCl. Under these high salt conditions (not physiological), it's possible and even plausible that Mediator subunits could separate over time. This caveat is not mentioned or controlled for by the authors. Because a putative Med16 subcomplex is a foundational point of the article, this is concerning.

The data are incomplete because a potential Med16 complex is not defined biochemically. The current state suggests a smaller Med16-containing complex that may also contain UBP1 and other factors, but its composition is not determined. This is important because if you're going to conclude a new and biologically relevant Med16 complex, which is a point of the article, then readers will expect you to do that.

Equally concerning are the IP-western results shown in Figure 1. In my opinion, these experiments do nothing to support the claims of the authors. The authors use hexanediols at 5% or 10% in an effort to disrupt the Mediator complex. Assuming this was weight/volume, that means ~400 to 800mM hexanediol solution, which is fairly high and can be expected to disrupt protein complexes, but the effects haven't been carefully assessed as far as I'm aware. The 2,5 HD (Figure 1B) experiments appear to simply contain greater protein loading, and this may contribute to the apparent differential results. In fact, in looking at the data, it seems that all MED subunits probed show the same trend as Med16. They are all reduced in the 1,6HD experiment relative to the 2,5 HD experiment. But it's hard to know, because replicates weren't completed and quantitation was not done. There aren't even loading controls. Other concerns about the IP-Western experiments are outlined in point 2.

(2) At no point do the authors apply rigorous methods to test their hypothesis. Instead, methods are applied that have been largely discredited over time and can only serve as preliminary data for pilot studies, and cannot be used to draw definitive conclusions about protein function.

a) IP-westerns are fraught with caveats, especially the way they were performed here, in which the beads were washed at relatively low salt and then eluted by boiling the beads in loading buffer. This will "elute" bound proteins, but also proteins that non-specifically interact with or precipitate on the beads. And because Westerns are so sensitive, it is easy to generate positive results. It's just not a rigorous experiment.

b) Many conclusions relied on transient transfection experiments, which are problematic because they require long timeframes, during which secondary/indirect effects from expression/overexpression will result. This is especially true if the proteins being artificially expressed/overexpressed are major transcription regulators, which is the case here. It is simply impossible to separate direct from indirect effects with these types of experiments. Another concern is that there was no effort to assess whether the induced protein levels were near physiological levels. Protein overexpression, especially if the protein is a known regulator of pol2 transcription (e.g., UBP1 or Med16), will create many unintended consequences.

c) Many conclusions were made based upon shRNA knockdown experiments, which are problematic because they require long timeframes (see above point), which makes it nearly impossible to identify effects that are direct vs. indirect/secondary/tertiary effects. Also, shRNA experiments will have off-target effects, which have been widely reported for well over a decade. An advantage of shRNA knockdowns is that they prevent genetic adaptation (a caveat with KO cell lines). A minimal test would be to show phenotypic rescue of the knockdown by expressing a knockdown-resistant Med16 (for example), but these types of experiments were not done.

d) Many experiments used reporter assays, which involved artificial, non-native promoters. Reporters are good for pilot studies, but they aren't a rigorous test of direct regulatory roles for Med16 or other proteins. Reporters don't even measure transcription directly. In fact, no experiment in this study directly measures transcription. An RNA-seq experiment was done with overexpressed or Med16 knockdown cells, but these required long timeframes and RNA-seq measures steady-state mRNA, which doesn't test the potential direct effects of these proteins on nascent transcription.

e) The MS experiments show promise, but the data were not shown, so it's hard to judge. The reader cannot compare/contrast the experiments, and we have no indication of the statistical confidence of the proteins identified. How many biological replicate MS experiments were performed?

(3) The data are over-interpreted, and alternative (and more plausible) hypotheses are ignored. Many examples of this, some of which are alluded to in the points above. For example, Med16 loss or overexpression will cause compensatory responses in cells. An expected result is that Mediator composition will be disrupted, since Med16 directly interacts with several other subunits. Also in yeast, the Robert, Gross, and Morse labs showed that loss of Med16/Sin4 causes loss of other tail module subunits, and this would be expected to cause major changes in the transcriptome. The authors also mention that yeast Med16/Sin4 "alters chromatin accessibility globally" and this would be expected to cause major changes in the transcriptome, leading to unintended consequences that will make data analysis and identification of direct Med16 effects impossible. The unintended consequences will be magnified with prolonged disruption of MED16 levels in cells (e.g., longer than 4h). These unintended consequences are hard to predict or define, and are likely to be widespread given the pivotal role of Mediator in gene expression. One unintended consequence appears to be loss of pol2 upon Med16 over-expression, as suggested by the western blot in Figure 8B. I point this out as just one example of the caveats/pitfalls associated with long-term knockdowns or over-expression.

Reviewer #3 (Public Review):

Summary:

There are two major flaws that fundamentally undermine the value of the study. First, nearly all the central conclusions drawn here rely on the unfounded assumption that the effects observed are direct. No rigorous cause-and-effect relationships are established to support the claims. Second, the quality of the experimental data is substandard. Collectively, these concerns significantly limit any advances that might be gained in our understanding of the UBP1 pathway or Mediator function.

Weaknesses:

(1) The decrease in 1,6-hexanediol-treated cells of MED16 is modest, variable, not quantified, and internally inconsistent. For example, in Figure 1A, 1,6-hexanediol treatment should not have an impact on the level of the protein being directly IP. For MED12 (and CDK8 and MED1 to a lesser extent), 1,6-hexanediol treatment alters the level of the target protein in the IP. Along these lines, Figure 1A shows a no 1,6H-D dependent decrease in MED1 or MED12 levels in the CDK8 IP, whereas Figure 1B does show a decrease. Figure 1A shows no 1,6H-D dependent decrease in CDK8 levels in the MED1 IP, whereas Figure 1B shows a dramatic decrease. MED24 levels in the MED12 IP increase upon 1,6H-D in Figure 1A, but decrease in Figure 1B. Internal inconsistencies of this nature persist in the other Figures.

(2) Undermining the value of Figure 1E/F, UBP1 and TFCP2 may also associate with the small amount of MED16 in the 2MDa fractions. This is not tested, and therefore, the conclusion that they just associate with the dissociable form of MED16 is not supported.

(3) Domain mapping studies in Figure 2 are overinterpreted. Since the interactions could be indirect, it is not accurate to conclude "Therefore, the N-terminal WDR domain of MED16 is crucial for its integration into the Mediator complex, while the C-terminal αβ-domain is essential for interacting with UBP1-TFCP2. "

(4) A close examination of Figure 2C undermines confidence in the association studies. The bait protein in lanes 5-8 should be equal. Also, there is significant binding of GST to UBP1 and TFCP2, in roughly the same patterns as they bind to GST-MED16 αβ. The absence of input samples makes the results even more difficult to interpret.

(5) The domain deletion mutants are utilized throughout the manuscript as evidence of the importance of the UBP1-MED16 interaction. However, in Figure 2F lanes 7 and 8, the delta-S mutant binds MED16 as well as full-length UBP1. This undermines much of the subsequent data and conclusions about specificity.

(6) Even if the delta-S mutant were defective for MED16 binding, the result in Figure 3B does not "confirm that MED16 is required for the transcriptional activity of UBP1,". Removal of that domain may have other effects.

(7) As Mediator is critical for the activation of many genes, it is not accurate to assume that the impact of its deletion in Figure 3E/F demonstrates a direct requirement in UBP1-driven transcription. This could easily be an indirect effect.

(8) Without documenting the relative protein expression levels in Figure 3G/H, conclusions cannot be drawn about the titration experiments, nor the co-expression experiments. These findings are likely the result of squelching or some form of competition that is not directly related to the UBP1-mediated transcription. A great deal of validation would be required in order to support the model that these effects are a result of MED16 overexpression sequestering UBP1 away from holo-Mediator.

(9) The lack of any documentation of expression levels for the various ectopic proteins in the majority of Figures, renders mechanistic claims meaningless (Figures 3, 4, 5, 6, 7, S2, S3). This is particularly relevant since the model presented for many of the results invokes concentration-dependent competition.

eLife Assessment

This study offers a valuable methodological advance by introducing a gene panel selection approach that captures combinatorial specificity to define cell identity. The findings address key limitations of current single-gene marker methods. The evidence is compelling, but would be strengthened by further validation of rare cell states and unexpected marker categories.

Joint Public Review:

In this study, the authors introduce CellCover, a gene panel selection algorithm that leverages a minimal covering approach to identify compact sets of genes with high combinatorial specificity for defining cell identities and states. This framework addresses a key limitation in existing marker selection strategies, which often emphasize individually strong markers while neglecting the informative power of gene combinations. The authors demonstrate the utility of CellCover through benchmarking analyses and biological applications, particularly in uncovering previously unresolved cell states and lineage transitions during neocorticogenesis.

The major strengths of the work include the conceptual shift toward combinatorial marker selection, a clear mathematical formulation of the minimal covering strategy, and biologically relevant applications that underscore the method's power to resolve subtle cell-type differences. The authors' analysis of the Telley et al. dataset highlights intriguing cases of ribosomal, mitochondrial, and tRNA gene usage in specific cortical cell types, suggesting previously underappreciated molecular signatures in neurodevelopment. Additionally, the observation that outer radial glia markers emerge prior to gliogenic progenitors in primates offers novel insights into the temporal dynamics of cortical lineage specification.

However, several aspects of the study would benefit from further elaboration. First, the interpretability of gene panels containing individually lowly expressed genes but high combinatorial specificity could be improved by providing clearer guidelines or illustrative examples. Second, the utility of CellCover in identifying rare or transient cell states should be more thoroughly quantified, especially under noisy conditions typical of single-cell datasets. Third, while the findings on unexpected gene categories are provocative, they require further validation - either through independent transcriptomic datasets or orthogonal methods such as immunostaining or single-molecule FISH-to confirm their cell-type-specific expression patterns.

Specifically, the manuscript would benefit from further clarification and additional validation in the following areas:

• A more in-depth explanation of marker panel applications is needed. Specifically, how should users interpret gene panels where individual genes show only moderate or low expression levels, but the combination provides high specificity? Providing a concrete example, along with guidelines for interpreting such combinatorial signatures, would enhance the practical utility of the method.

• Further quantification of CellCover's sensitivity in detecting rare cell subtypes or states would strengthen the evaluation of its performance. Additionally, it would be helpful to assess how CellCover performs under noisy conditions, such as low cell numbers or read depths, which are common challenges in scRNA-seq datasets.

• It is intriguing and novel that CellCover analysis of the dataset from Telley et al. suggests cell-type-specific expression of ribosomal, mitochondrial, or tRNA genes. These findings would be significantly strengthened by additional validation. For example, the reported radial glia-specific expression of Rps18-ps3 and Rps10-ps1, as well as the postmitotic neuron-specific expression of mt-Tv and mt-Nd4l, should be corroborated using independent scRNA-seq or spatial transcriptomic datasets of the developing neocortex. Alternatively, these expression patterns could be directly examined through immunostaining or single-molecule FISH analysis.

• The observation that outer radial glia (oRG) markers are expressed in neural progenitors before the emergence of gliogenic progenitors in primates and humans is compelling. This could be further supported by examining the temporal and spatial expression patterns of early oRG-specific markers versus gliogenic progenitor markers in recent human spatial transcriptomic datasets - such as the one published by Xuyu et al. (PMID: 40369074) or Wang et al. (PMID: 39779846).

Summary:

Overall, this work provides a conceptually innovative and practically useful method for cell type classification that will be valuable to the single-cell and developmental biology communities. Its impact will likely grow as more researchers seek scalable, interpretable, and biologically informed gene panels for multimodal assays, diagnostics, and perturbation studies.

eLife Assessment

This important study systematically investigates repeat expansion in the plant Arabidopsis thaliana using a new k-mer-based method, expanding on smaller studies to more comprehensively identify cis- and trans-acting loci associated with repeat dynamics. The approach is methodologically sound and broadly applicable to large-scale short-read datasets for assessing copy number variation and genomic repeat content. While convincing in its scope and novelty, the findings would be further strengthened with exploratory analyses of datasets from other species with more or fewer repeats in their genomes.

Reviewer #1 (Public review):

Summary:

Overall, this study is an excellent and systematic investigation of the expansion of repeat sequences in Arabidopsis thaliana, and the genetic mechanisms underlying these expansions. Many of the key findings here confirm smaller studies of both repeat sequence variation and the individual genes associated with the expansion of various repeat classes. The authors present a highly effective and practical approach that requires datasets that are far more readily available than the multiple reference genomes used to annotate repeat variation in recent works. Therefore, they provide an approach that shows significant promise in non-model systems in which far less is known of repeat variation and its underlying drivers.

Strengths:

This is a very methodologically sound study that extends the relatively well-studied Arabidopsis thaliana repeat landscape with more systematic sampling, highlights the loci associated with repeat expansions (many of which were previously identified in a piecemeal manner), and provides some evolutionary inference on these.

Weaknesses:

Regarding cis-QTLs: I foresee at least two causes of these associations: non-repetitive cis-acting sequences that promote or permit the expansion of local repeats, and variation in repeat sequences themselves that directly tag the expanding sequence itself. It's arguable whether these are truly two distinct classes, but an attempt to discriminate between them may provide some insight as to the local factors that allow for repeat expansion, beyond the mere presence of a repeat sequence. One way to discriminate these could be to map the ~1300 12-mer frequency profiles on the reference genome, and filter any SNPs with elevated 12-mer frequency from the GWAS (or to categorize them independently).

I also have a question regarding the choice of k=12 in kmer profile analyses. Did the authors perform any GWAS with other values of K? If so, how did the results change? I would expect that as K is increased, the associations would become more specific to individual repeat families, possibly to the point where only cis-acting loci are detected. The authors show convincing evidence that k=12 is appropriate; however, I would be interested to see if/how GWAS results vary among e.g. k=10, 12, 15, 18.

Reviewer #2 (Public review):

Summary:

The authors introduce a K-mer-based method for profiling repeat content within a species, applied here to 1,142 A. thaliana genomes sequenced with short reads. This approach allowed them to bypass the challenges of genome assembly, particularly for repetitive regions, while still quantifying copy number variation. Their analysis identified >50 trans-acting loci regulating repeat abundance, enriched for genes involved in DNA repair, replication, and methylation. They also speculate on the role of selection in shaping genome repeat content, arguing that purifying selection tends to suppress alleles that promote repeat expansion.

The work presents a scalable way to extract meaningful insights from the large quantities of short-read datasets available. However, I have several concerns regarding the methodology, scope of claims, and interpretation of results.

Strengths:

The authors leverage a large dataset, >1100 samples, of A. thaliana. The scale of the study is impressive and clearly bolsters their findings. Additionally, this provides a framework for future, large-scale studies and offers a solid foundation for hypothesis generation. The k-mer-based method is generally practical for large-scale analysis and should be transferable to other datasets. Finally, the authors are commendably upfront about many of the project's limitations.

Weaknesses:

The decision to use k=12 is loosely justified. While the authors performed a sweep of k-mer lengths (from 5-20) and noted computational constraints, the choice is highly dataset-specific. Benchmarking across different k values with additional datasets (especially including other species) would strengthen confidence in the robustness of the method.

All analyses rely exclusively on the TAIR10 reference genome, which is incomplete and known to collapse certain repetitive regions. This dependence raises concerns that some repeats (especially recently expanded or highly variable ones) are systematically undercounted. With improved A. thaliana assemblies now available, testing the method against a more complete reference would alleviate these concerns.

The manuscript's conclusions are framed in very broad terms (e.g., "shaping genome evolution in plants"). However, the study is restricted to a single species, A. thaliana, which may not represent other plants. While the findings may suggest general principles, the claims in the abstract and conclusion should be moderated to reflect the study system more accurately.

The identification of >50 trans-acting loci enriched for DNA repair and replication genes is compelling, but the conclusions remain correlational.

eLife Assessment

This work introduces FunC-ESMs, a proteome-scale framework to classify loss-of-function missense variants into distinct mechanistic groups by combining two complementary state-of-the-art machine learning models. The strength of evidence is convincing, supported by solid benchmarking, integration with experimental datasets, and careful methodological design. The significance of the findings is valuable, providing a resource of clear interest to researchers and diagnostic laboratories working on variant interpretation.

Reviewer #1 (Public review):

Summary:

In this work, the authors aim to improve upon their previous iterations of frameworks and models that try to decouple variant effects of protein stability from direct effects on function. This is motivated by the utility of understanding the specific molecular mechanisms underlying loss-of-function disease to assist in developing potential treatment approaches, which differ based on the causal mechanisms. The authors demonstrably achieve this goal, with FunC-ESMs presenting an elegant approach, utilizing pre-trained ESM-1b and ESM-IF models, which freed them from model training or running computationally intensive Rosetta predictions. While the performance improvements over their previous model are not unambiguous, in some of the examples, FunC-ESMs allowed them to scale up their analysis to the proteome level, deriving variant classifications of stable-but-inactive and total-loss across 20,144 human proteins, and further allowing them to identify functionally and structurally critical sites. However, the strength of the manuscript could be improved by clarifying or rewording some terminology concerning the molecular effects and what other underlying molecular mechanisms could also reside in the stable-but-inactive group, given the stated motivation of setting up a mechanistic starting point for therapeutic development and clinical applications.

Strengths:

Overall, the manuscript is very well framed and written, with clear motivations and objectives. The previous works are explained well and set up a clear methodological comparison with the new framework. FunC-ESMs is solidly designed to minimize data circularity, and the methodology to derive optimal thresholds is well reasoned. The authors make an effort to provide all the data and code very accessible.

Weaknesses:

(1) Considering how loss-of-function mechanisms dominate the known missense disease variant landscape, it is understandable that the scope of the work focuses on loss of function. However, variants exceeding the established ESM-1b threshold in the manuscript are often generalized as loss-of-function variants (e.g., lines 176, 304; line 285, for instance, uses much more neutral language), which can be misleading due to the guaranteed presence of deleterious variants that manifest through other mechanisms, such as gain-of-function.

While relatively not as well predicted, gain-of-function variants would still likely demonstrate inflated ESM-1b scores and end up in the SBI class. Given the emphasis on the potential utility of the framework for tailoring therapeutic approaches, it seems pertinent to highlight gain-of-function and dominant-negative mechanisms in the manuscript, as they would require considerably different therapeutics than loss-of-function variants.

A short disclaimer explaining the other mechanisms and the potential limitations of the framework in picking them out would improve the clarity of the manuscript. As an additional step, it would be interesting to explore where clinically validated gain-of-function and dominant-negative variant examples fall within the framework's classification.

(2) Given the clinical angle, it would be useful to see the predicted label distribution in population datasets like gnomAD, for instance, focusing on dominant Mendelian disease genes to minimize the impact of non-penetrant or heterozygous disease variants. The performance demonstration using (likely) benign ClinVar variants is not as informative of the real-world utility cases that the method would be used in by clinicians or researchers.

Reviewer #2 (Public review):

Summary:

The paper by Cagiada et al builds on their previously published work, but now uses two independent and complementary machine learning models to predict the deleteriousness of every missense change in the human proteome. The authors were able to separate all missense variants into three classes - wild-type like, total loss (important for stability), or stable-but-inactive (important for function), showing that the predictions correlated well with intuition in terms of clustering and location in folded versus intrinsically disordered regions. Evaluation of known pathogenic and benign variants from ClinVar suggested that around half of all pathogenic missense variants cause disease by disrupting protein stability. These results could be valuable for researchers and genomic diagnostics laboratories performing variant interpretation.

Strengths:

The method uses data from two independent state-of-the-art ML models, which were developed and published by other groups. The predictions were provided for every missense variant in the entire human proteome, and have been validated against a small previously published experimental dataset, as well as using known pathogenic and benign variants from ClinVar. Results are clearly stated and well illustrated with useful figures.

Weaknesses:

Both the description and the analysis could benefit from some additional work around the thresholds used for both ML models (ESM-1b and ESM-IF). The thresholds were selected based on an ROC analysis using published MAVE data, which has various limitations, including the small number of proteins for which MAVE data are available. Moreover, the correlation between the predictions from the two ML models was not evaluated, and there was no discussion of the limitations of the models or where they might predict different things, which was avoided by using two independent thresholds. The threshold approach needs further explanation, and a sensitivity analysis of how the results would change using different thresholds or by defining thresholds in an alternative way would be informative. In addition, the ClinVar pathogenic variants are all treated equally, when in fact it is known that some act via a gain versus a loss of function mechanism. It would be useful to know if these known patho-mechanisms correlate with predictions of variants that affect stability versus function.

eLife Assessment

This work reveals metabolic pathways and molecular events mechanistically linked to B cell activation. Using an unbiased, comprehensive proteome profiling method and various functional validation approaches, this study generated convincing evidence suggesting a role for amino acid uptake, cholesterol accumulation, and protein prenylation in the proliferation, survival, and biogenesis of B cells stimulated with LPS and other activating stimuli. The significance of the findings is considered to be fundamental, in that they will advance our understanding of cell metabolism during B cell activation.

Reviewer #1 (Public review):

The work presented by Cheung et al. used a quantitative proteomics method to capture molecular changes in B cells exposed to LPS and IL-4, a combination of stimuli activating naive B cells. Amino acid transporters, cholesterol biosynthetic enzymes, ribosomal components, and other proteins involved in cell proliferation were found to increase in stimulated B cells. Experiments involving genetic loss-of-function (SLC7A5), pharmacological inhibition (HMGCR, SQLE, prenylation), and functional rescue by metabolites (mevalonate, GGPP) validated the proteomics data and revealed that amino acid uptake, cholesterol/mevalonate biosynthesis, and cholesterol uptake played a crucial role in B cell proliferation, survival, biogenesis, and immunoglobulin class switching. Experiments involving cholesterol-free medium showed that both biosynthesis and LDLR-mediated uptake catered to the cholesterol demand of LPS/IL-4-stimulated B cells. A role for protein prenylation in LDLR-mediated cholesterol uptake was postulated and backed by divergent effects of GGPP rescue in the presence and absence of cholesterol in culture medium.

Strengths:

The discovery was made by proteome-wide profiling and unbiased computational analysis. The discovered proteins were functionally validated using appropriate tools and approaches. The metabolic processes identified and prioritized from this comprehensive survey and systematic validation are highly likely to represent mechanisms of high importance and influence. Analysis of immune cell metabolism at the protein level is relatively compared to transcriptomic and metabolomic analysis.

The conclusions from functional validation experiments were supported by clear data and based on rational interpretations. This was enabled by well-established readouts/analytical methods used to analyze cell proliferation, viability, size, cholesterol content, and transporter/enzyme function. The data generated from these experiments strongly support the conclusions.

This work reveals a complex, yet intriguing, relationship between cholesterol metabolism and protein prenylation as they serve to promote B cell activation. The effects of pharmacological inhibition and metabolite replenishment on the cholesterol content and activation of B cells were precisely determined and logically interpreted.

Weaknesses:

The findings of this study were obtained almost exclusively from ex vivo B cell stimulation experiments. Their contribution to B cell state and B-cell-mediated immune responses in vivo was not explored. Without in vivo data, the study still provides valuable mechanistic information and insights, but it remains unknown, and there is no discussion about how the identified mechanisms may play out in B cell immunity.

The role of HMGCR, SQLE, and prenylation in B cell activation was assessed using pharmacological inhibitors. Evidence from other loss-of-function approaches, which could strengthen the conclusions, does not exist. This is a moderate weakness.

Reviewer #2 (Public review):

This study uses mass spectrometry to quantify how LPS and IL-4 modify the mouse B cell proteome as naïve cells undergo blastogenesis and enter the cell cycle. This analysis revealed changes in key proteins involved in amino acid transport and cholesterol biosynthesis. Genetic and pharmacological experiments indicated important roles for these metabolic processes in B cell proliferation.

This work provides new information about the regulation of TI B cell responses by changes in cell metabolism and also a comprehensive mass spectrometry dataset, which will be an important general resource for future studies. The experiments are thorough and carefully carried out. The majority of conclusions are backed up by data that is shown to be highly significant statistically.

The study would be strengthened by additional experiments to determine whether the detected changes are unique to stimulation with LPS + IL-4 or more generic responses of resting B cells to mitogenic agonists.

Author response:

Reviewer #1:

We agree with the reviewer that a limitation of our study is its focus on cell-based assays rather than in vivo experiments. We did consider evaluating the effects of statins on B cell responses in vivo; however, this approach is complicated by findings that statins can influence antigen presentation by dendritic cells, thereby impacting antibody responses (Xia et al, 2018). One possible solution would be to use B cell-specific conditional knockout models to study the roles of the identified proteins in an in vivo context. However, we currently do not have access to these models and were therefore unable to include such experiments within a feasible timeframe. We will revise the discussion section to acknowledge these points.

The reviewer also noted that our study assessed the roles of HMGCR, SQLE, and prenylation in B cell activation using pharmacological inhibitors and genetic knockdown/out approaches. Loss-of-function techniques such as RNAi, siRNA, and CRISPR can be challenging to apply to primary B cells, but we are exploring their feasibility for future revisions. While we acknowledge the limitations of using pharmacological inhibitors, we have taken several steps to mitigate these, including targeting multiple steps in the cholesterol biosynthetic pathway using structurally distinct inhibitors and conducting rescue experiments by supplementing downstream metabolites. To further investigate potential off-target effects of statins, we have recently performed proteomic analysis of B cells treated with and without fluvastatin. The data suggest that fluvastatin primarily affects cholesterol metabolism and does not cause widespread off-target effects. We will include this new data in the revised manuscript.

Reviewer #2:

The reviewer suggested that the study would be strengthened by determining whether the observed changes are specific to LPS + IL-4 stimulation or represent a more general B cell response to mitogenic signals.

A complementary study by James et al. (James et al, 2024) investigated murine B cells stimulated via the B cell receptor (BCR) and CD40, using anti-IgM and anti-CD40 antibodies alongside IL-4. Their proteomic analysis showed that such co-stimulation induces a fivefold increase in total cellular protein mass within 24 hours, mirroring our findings with LPS + IL-4. They also reported upregulation of proteins associated with cell cycle progression, ribosome biogenesis, and amino acid transport. Furthermore, by using SLC7A5 knockout mice, they demonstrated that this transporter is required for B cell activation. We will expand our discussion to include and these findings.  We will also expand on the final figure in our paper showing that the effects of statins are not limited to LPS.

References:

James O, Sinclair LV, Lefter N, Salerno F, Brenes A & Howden AJM (2024) A proteomic map of B cell activation and its shaping by mTORC1, MYC and iron. bioRxiv 2024.12.19.629506 doi:10.1101/2024.12.19.629506 [PREPRINT]

Xia Y, Xie Y, Yu Z, Xiao H, Jiang G, Zhou X, Yang Y, Li X, Zhao M, Li L, et al (2018) The Mevalonate Pathway Is a Druggable Target for Vaccine Adjuvant Discovery. Cell 175: 1059-1073.e21

eLife Assessment

This important study advances our understanding of how cellular quality control machinery influences cystic fibrosis (CF) drug responsiveness by systematically analyzing the effects of the chaperone calnexin on more than two hundreds of CFTR (cystic fibrosis transmembrane regulator) variants. The evidence supporting the conclusions is convincing, with a comprehensive deep mutational scanning methodology and rigorous quantitative analysis. The findings reveal that calnexin is critical for both CFTR protein expression and corrector drug efficacy in a variant-specific manner, providing invaluable insights that could guide the development of personalized CF therapies. This work will be of significant interest to researchers in protein folding, CF drug development, and genetic disease therapeutics.

Reviewer #1 (Public review):

Summary:

This research investigates how the cellular protein quality control machinery influences the effectiveness of cystic fibrosis (CF) treatments across different genetic variants. CF is caused by mutations in the CFTR gene, with over 1,700 known disease-causing variants that primarily work through protein misfolding mechanisms. While corrector drugs like those in Trikafta therapy can stabilize some misfolded CFTR proteins, the reasons why certain variants respond to treatment while others don't remain unclear. The authors hypothesized that the cellular proteostasis network-the machinery that manages protein folding and quality control-plays a crucial role in determining drug responsiveness across different CFTR variants. The researchers focused on calnexin (CANX), a key chaperone protein that recognizes misfolded glycosylated proteins. Using CRISPR-Cas9 gene editing combined with deep mutational scanning, they systematically analyzed how CANX affects the expression and corrector drug response of 234 clinically relevant CF variants in HEK293 cells.

In terms of findings, this study revealed that CANX is generally required for robust plasma membrane expression of CFTR proteins, and CANX disproportionately affects variants with mutations in the C-terminal domains of CFTR and modulates later stages of protein assembly. Without CANX, many variants that would normally respond to corrector drugs lose their therapeutic responsiveness. Furthermore, loss of CANX caused broad changes in how CF variants interact with other cellular proteins, though these effects were largely separate from changes in CFTR channel activity.

This study has some limitations: the research was conducted in HEK293 cells rather than lung epithelial cells, which may not fully reflect the physiological context of CF. Additionally, the study only examined known disease-causing variants and used methodological approaches that could potentially introduce bias in the data analysis.

How cellular quality control mechanisms influence the therapeutic landscape of genetic diseases is an emerging field. Overall, this work provides important cellular context for understanding CF mutation severity and suggests that the proteostasis network significantly shapes how different CFTR variants respond to corrector therapies. The findings could pave the way for more personalized CF treatments tailored to patients' specific genetic variants and cellular contexts.

Strengths:

(1) This work makes an important contribution to the field of variant effect prediction by advancing our understanding of how genetic variants impact protein function.

(2) The study provides valuable cellular context for CFTR mutation severity, which may pave the way for improved CFTR therapies that are customized to patient-specific cellular contexts.

(3) The research provides further insight into the biological mechanisms underlying approved CFTR therapies, enhancing our understanding of how these treatments work.

(4) The authors conducted a comprehensive and quantitative analysis, and they made their raw and processed data as well as analysis scripts publicly available, enabling closer examination and validation by the broader scientific community.

Comments on revisions:

The authors have addressed my concerns. If Document S1 is part of the final published version, this will address one of my previous concerns about potential skew and bias in the read data (Weakness 3, Methodological Choices).

Reviewer #2 (Public review):

In this work, the authors use deep mutational scanning (DMS) to examine the effect of the endogenous chaperone calnexin (CANX) on the plasma membrane expression (PME) and potential pharmacological stabilization cystic fibrosis disease variants. This is important because there are over 1,700 loss-of-function mutations that can lead to the disease Cystic Fibrosis (CF), and some of these variants can be pharmacologically rescued by small-molecule "correctors," which stabilize the CFTR protein and prevent its degradation. This study expands on previous work to specifically identify which mutations affect sensitivity to CFTR modulators, and further develops the work by examining the effect of a known CFTR interactor-CANX-on PME and corrector response.

Overall, this approach provides a useful atlas of CF variants and their downstream effects, both at a basal level as well as in the context of a perturbed proteostasis. Knockout of CANX leads to an overall reduced plasma membrane expression of CFTR with CF variants located at the C-terminal domains of CFTR, which seem to be more affected than the others. This study then repeats their DMS approach, using PME as a readout, to probe the effect of either VX-445 or VX-455 + VX-661-which are two clinically relevant CFTR pharmacological modulators. I found this section particularly interesting for the community because the exact molecular features that confer drug resistance/sensitivity are not clear. When CANX is knocked out, cells that normally respond to VX-445 are no longer able to be rescued, and the DMS data show that these non-responders are CF variants that lie in the VX-445 binding site. Based on computational data, the authors speculate that NBD2 assembly is compromised, but that remains to be experimentally examined. Cells lacking CANX were also resistant to combinatorial treatment of VX-445 + VX-661, showing that these two correctors were unable to compensate for the lack of this critical chaperone.

One major strength of this manuscript is the mass spectrometry data, in which 4 CF variants were profiled in parental and CANX KO cells. This analysis provides some explanatory power to the observation that the delF508 variant is resistant to correctors in CANX KO cells, which is because correctors were found not to affect protein degradation interactions in this context. Findings such as this provide potential insights into intriguing new hypothesis, such as whether addition of an additional proteostasis regulators, such as a proteosome inhibitor, would facilitate a successful rescue. Taken together, the data provided can be generative to researchers in the field and may be useful in rationalizing some of the observed phenotypes conferred by the various CF variants, as well as the impact of CANX on those effects.

To complete their analysis of CF variants in CANX KO cells, the research also attempted to relate their data, primarily based on PME, to functional relevance. They observed that, although CANX KO results in a large reduction in PME (~30% reduction), changes in the actual activation of CFTR (and resultant quenching of their hYFP sensor) were "quite modest." This is an important experiment and caveat to the PME data presented above since changes in CFTR activity does not strictly require changes in PME. In addition, small molecule correctors also do not drastically alter CFTR function in the context of CANX KO. The authors reason that this difference is due to a sort of compensatory mechanism in which the functionally active CFTR molecules that are successfully assembled in an unbalanced proteostasis system (CANX KO) are more active than those that are assembled with the assistance of CANX. While I generally agree with this statement, it is not directly tested and would be challenging to actually test.

The selected model for all the above experiments was HEK293T cells. The authors then demonstrate some of their major findings in Fischer rat thyroid cell monolayers. Specifically, cells lacking CANX are less sensitive to rescue by CFTR modulators than the WT. This highlights the importance of CANX in supporting the maturation of CFTR and the dependence of chemical correctors on the chaperone. Although this is demonstrated specifically for CANX in this manuscript, I imagine a more general claim can be made that chemical correctors depend on a functional/balanced proteostasis system, which is supported by the manuscript data. I am surprised by the discordance between HEK293T PME levels compared to the CTFR activity. The authors offer a reasonable explanation about the increase in specific activity of the mature CFTR protein following CANX loss.

For the conclusions and claims relevant to CANX and CF variant surveying of PME/function, I find the manuscript to provide solid evidence to achieve this aim. The manuscript generates a rich portrait of the influence of CF mutations both in WT and CANX KO cells. While the focus of this study is a specific chaperone, CANX, this manuscript has the potential to impact many researchers in the broad field of proteostasis.

Comments on revisions:

The authors address my concerns. I appreciate seeing that the UPR probably isn't activated, ruling out that less PME is simply due to less CF protein.

Author response:

The following is the authors’ response to the original reviews

Reviewer 1 (Public review):

This research investigates how the cellular protein quality control machinery influences the effectiveness of cystic fibrosis (CF) treatments across different genetic variants. CF is caused by mutations in the CFTR gene, with over 1,700 known disease-causing variants that primarily work through protein misfolding mechanisms. While corrector drugs like those in Trikafta therapy can stabilize some misfolded CFTR proteins, the reasons why certain variants respond to treatment while others don't remain unclear. The authors hypothesized that the cellular proteostasis network-the machinery that manages protein folding and quality control-plays a crucial role in determining drug responsiveness across different CFTR variants. The researchers focused on calnexin (CANX), a key chaperone protein that recognizes misfolded glycosylated proteins. Using CRISPR-Cas9 gene editing combined with deep mutational scanning, they systematically analyzed how CANX affects the expression and corrector drug response of 234 clinically relevant CF variants in HEK293 cells. 

In terms of findings, this study revealed that CANX is generally required for robust plasma membrane expression of CFTR proteins, and CANX disproportionately affects variants with mutations in the C-terminal domains of CFTR and modulates later stages of protein assembly. Without CANX, many variants that would normally respond to corrector drugs lose their therapeutic responsiveness. Furthermore, loss of CANX caused broad changes in how CF variants interact with other cellular proteins, though these effects were largely separate from changes in CFTR channel activity. 

This study has some limitations: the research was conducted in HEK293 cells rather than lung epithelial cells, which may not fully reflect the physiological context of CF. Additionally, the study only examined known diseasecausing variants and used methodological approaches that could potentially introduce bias in the data analysis. 

We agree that the approaches employed here are not fully physiological, though we would remind the reviewer that we previously benchmarked the results generated by this experimental platform against a variety of other published datasets (PMID: 37253358). Regarding the issue of bias, we outline several pieces of evidence suggesting we retain robust and near-uniform sampling of these variants across these experimental conditions. We hope our comments below address all of these concerns. Overall, we believe deep mutational scanning is actually remarkably unbiased relative to other approaches due to the fact that all measurements are taken from a single dish of cells that is processed in parallel. Moreover, we show the trends are highly reproducible across replicates and users (see Figure S1). 

How cellular quality control mechanisms influence the therapeutic landscape of genetic diseases is an emerging field. Overall, this work provides important cellular context for understanding CF mutation severity and suggests that the proteostasis network significantly shapes how different CFTR variants respond to corrector therapies. The findings could pave the way for more personalized CF treatments tailored to patients' specific genetic variants and cellular contexts. 

Strengths: 

(1) This work makes an important contribution to the field of variant effect prediction by advancing our understanding of how genetic variants impact protein function. 

(2) The study provides valuable cellular context for CFTR mutation severity, which may pave the way for improved CFTR therapies that are customized to patient-specific cellular contexts. 

(3) The research provides further insight into the biological mechanisms underlying approved CFTR therapies, enhancing our understanding of how these treatments work. 

(4) The authors conducted a comprehensive and quantitative analysis, and they made their raw and processed data as well as analysis scripts publicly available, enabling closer examination and validation by the broader scientific community. 

We are grateful for this broad perspective on the general relevance of this work.

Weaknesses: 

(1) The study only considers known disease-causing variants, which limits the scope of findings and may miss important insights from variants of uncertain significance. 

We agree with this caveat. A more comprehensive library of CFTR variants will undoubtedly be useful for assigning variants of uncertain significance, though we note that such a large library would involve trade-offs in depth/ coverage that will compromise the sensitivity/ precision of the measurements. This will, in turn, make it challenging to compare the effects of CFTR modulators across the spectrum of clinical variants. For this reason, we believe the current library will remain a useful tool for CF variant theratyping.

(2) The cellular context of HEK293 cells is quite removed from lung epithelia, the primary tissue affected in cystic fibrosis, potentially limiting the clinical relevance of the findings. 

We concede this limitation, but note that we did carry out functional measurements in FRT monolayers, which are a prevailing model that closely mimics pharmacological outcomes in the clinic (see Fig. 6). 

(3) Methodological choices, such as the expansion of sorted cell populations before genetic analysis, may introduce possible skew or bias in the data that could affect interpretation. 

We respectfully disagree with this point. The recombination system we employ in these studies generates millions of recombinant cells per transfection, which corresponds to tens of thousands of clones per variant. Moreover, our sequencing data contain exhaustive coverage of every variant characterized herein within each of the final data sets. Generally, we do not see any evidence to suggest certain variants are lost from the population. We note that, while HEK293T cells are not the most physiological relevant system, they are robust to uniformly express these variants in a manner that provides a precise comparison of their effects and/ or response to CFTR modulators. To address this concern, we added Document S1 to the revised draft, which shows the total number of reads for each variant within each fraction and each experiment.

(4) While the impact on surface trafficking is convincingly demonstrated, how cellular proteostasis affects CFTR function requires further study, likely within a lung-specific cellular context to be more clinically relevant.

We agree with this caveat.

Reviewer 1 (Recommendations for the authors):

Major Issues

Cell Growth Bias? After sorting cell populations into quartiles, cells were expanded before genetic analysis - if CFTR variants affect cell doubling time (e.g., severely misfolded variants causing cellular stress), this could skew variant abundance within sorted quartiles and bias results.

Based on several observations, we do not believe this to be a significant issue. First, we note that we previously benchmarked the quantitative outputs of these experiments against a variety of other investigations and found very good agreement with previous variant classifications and expression levels (PMID: 37253358). If there were significant bias, we believe this would have come up in our efforts to benchmark the assay. Second, we note that we typically create recombinant cell lines that express WT or ΔF508 CFTR only alongside each recombinant cellular library. Importantly, we have never observed any difference in the growth rate of cultures expressing different CFTR variants. Third, even if cells expressing certain variants grow slower, it seems likely this slow growth would consistently occur in the context of each sorted subpopulation. Given that scores are derived from the relative amount of identifications across each subpopulation, we do not suspect this should impact the scoring. Overall, we believe the robustness of this cell line is a key feature that allows us to avoid any such issues related to proteostatic toxicity.

(1) Please add methodological detail. The data analysis pipeline lacks adequate description beyond referencing prior studies - essential details about what the Plasma Membrane Expression (PME) values represent (fold enrichment vs input library) and calculation methods must be provided.

We thank the reviewer for this helpful comment. We have added the text below to the revised manuscript in order to provide more detail to the reader:

“Briefly, low quality reads that likely contain more than one error were first removed from the demultiplexed sequencing data. Unique molecular identifier sequences within the remaining reads were then counted within each sample to track the relative abundance of each variant. To compare read counts across fractions, the collection of reads within each population were then randomly down-sampled to ensure a consistent total read count across each sub-population. The surface immunostaining of each variant was then estimated by calculating the the weighted-average immunostaining intensity for each variant using the following equation:

where ⟨I⟩_variant is the weighted-average fluorescence intensity of a given variant, ⟨F⟩_i is the mean fluorescence intensity associated with cells from the ith FACS quartile, and Ni is the number of variant reads in the i^th FACS quartile. Variant intensities from each replicate were normalized relative to one another using the mean surface immunostaining intensity of the entire recombinant cell population for each experiment to account for small variations in laser power and/ or detector voltage. Finally, to filter out any noisy scores arising from insufficient sampling, we repeated the down-sampling and scoring process then rejected any variant measurements that exhibit more than X% variation in their intensity scores across the two replicate analyses. The reported intensity values represent the average normalized intensity values from two independent down-sampling iterations across three biologicals replicates.”

(3) Add detail on library composition. The distribution of CFTR variants within the parental HEK293T library after landing pad insertion needs documentation, including any variant dropout or overrepresentation issues.

As noted in our previous work (PMID: 37253358), our CF variant library is quite uniform, with each mutant contributing on average, 0.43% of the library with a standard deviation of +/- 0.16%. This corresponds to an average read depth of over 40K reads per variant, per experimental condition in the final analyses. Indeed, the most abundant variant in the pool was ΔF508 (1.67% of total reads). In contrast, the least sampled variant was S549R (1647T>G) was still sampled an average of 3,688 times per replicate, which corresponds to 0.09% of the total reads. See Doc S1.

(4) Documentation of CFTR variant overlap between parental and CANX KO HEK293T libraries is needed, including whether every variant was present at equivalent input abundance in both libraries.

We thank the reviewer for this suggestion. Though there are small deviations in the composition of recombinant parental and knockout cell lines, the relative abundances of individual variants within the recombinant populations only differs by an average of 18.5% between the parental and knockout lines. There are no cases in which we observe a single variant increasing by more than 50% in the knockout line relative to the parent. However, there is a single variant, Y563N, that exhibits a 96% decrease in its abundance in the context of the knockout cell line. Nevertheless, even this variant was sampled over 1,000 times, and it’s final score passed all quality control metrics. In the revised draft, we have provided a complete table containing the total number of reads and percent of total reads for each variant for each cell line and condition (see Doc. S1).

(5) The section reporting CANX impact on functional rescue of CF variants requires clearer logic flow - the conclusion about higher specific activity of CFTR assembled without CANX appears misleading, given later discussion about CANX allowing suboptimally folded CFTR to traffic to the surface.

We apologize for any confusion. We invoked the term “specific activity” in the enzymological sense, which is to say the proportion of active enzyme (i.e. channel) at the plasma membrane differs in the knockout line. The logic is quite simple- if protein levels are lower while ion conductance remains the same in the knockout cells, then a higher proportion of the mature channels must be inactive in the parental cell line. Thus, we suspect fewer of the channels at the plasma membrane are active in the context of the parental cell line containing CANX. We considered modifications to the text in the discussion, but ultimately feel the current text strikes a reasonable balance between nuance and simplicity.

(6) In your discussion, consider that HEK293T cellular context differs significantly from lung epithelia, and the hYFP quenching assay may have insufficient dynamic range or high noise for detecting relevant functional differences.

We modified the following sentence in the discussion to introduce this possibility:

“While these discrepancies could stem from differences in the dynamic range of the functional assays, they may also suggest the stringency of QC is more finely tuned to ion channel biosynthesis in epithelial monolayers.”

Minor Issues

(1) Include immunostaining quartiles as a supplementary figure overlaid on Figure 1A, and clarify whether quartiles were consistent across experiments or adjusted for each sort.

We added a new figure to demonstrate the gating approach in the revised manuscript (see Fig. S10). We have also added the following text to the Methods section:

“Sorting gates for surface immunostaining were independently set for each biological replicate and in each condition to ensure that the population was evenly divided into four equal subpopulations.”

(2) Figure 2C improvements. Flip the figure 180 degrees to position MSD1 and NBD1 on the left, replace the blue-to-red color scale with yellow-to-blue or monochromatic scaling for better intermediate value differentiation.

Respectfully, we prefer not to do this so that our figures can be easily compared across our previous and forthcoming publications. We chose this rendering because this view depicts certain trends in variant response more clearly. 

(3) Indicate the location of ECL4 on the protein structure shown in Figure 2C for better reference.

We appreciate the suggestion. However, most of ECL4 is missing from the experimental cryo-EM models of CFTR due to a lack of density. For this reason, we did not modify the figure. 

Reviewer 2 (Public review):

In this work, the authors use deep mutational scanning (DMS) to examine the effect of the endogenous chaperone calnexin (CANX) on the plasma membrane expression (PME) and potential pharmacological stabilization cystic fibrosis disease variants. This is important because there are over 1,700 loss-of-function mutations that can lead to the disease Cystic Fibrosis (CF), and some of these variants can be pharmacologically rescued by small-molecule "correctors," which stabilize the CFTR protein and prevent its degradation. This study expands on previous work to specifically identify which mutations affect sensitivity to CFTR modulators, and further develops the work by examining the effect of a known CFTR interactor-CANX-on PME and corrector response. 

Overall, this approach provides a useful atlas of CF variants and their downstream effects, both at a basal level as well as in the context of a perturbed proteostasis. Knockout of CANX leads to an overall reduced plasma membrane expression of CFTR with CF variants located at the C-terminal domains of CFTR, which seem to be more affected than the others. This study then repeats their DMS approach, using PME as a readout, to probe the effect of either VX-445 or VX-455 + VX-661-which are two clinically relevant CFTR pharmacological modulators. I found this section particularly interesting for the community because the exact molecular features that confer drug resistance/sensitivity are not clear. When CANX is knocked out, cells that normally respond to VX-445 are no longer able to be rescued, and the DMS data show that these non-responders are CF variants that lie in the VX-445 binding site. Based on computational data, the authors speculate that NBD2 assembly is compromised, but that remains to be experimentally examined. Cells lacking CANX were also resistant to combinatorial treatment of VX-445 + VX-661, showing that these two correctors were unable to compensate for the lack of this critical chaperone. 

One major strength of this manuscript is the mass spectrometry data, in which 4 CF variants were profiled in parental and CANX KO cells. This analysis provides some explanatory power to the observation that the delF508 variant is resistant to correctors in CANX KO cells, which is because correctors were found not to affect protein degradation interactions in this context. Findings such as this provide potential insights into intriguing new hypothesis, such as whether addition of an additional proteostasis regulators, such as a proteosome inhibitor, would facilitate a successful rescue. Taken together, the data provided can be generative to researchers in the field and may be useful in rationalizing some of the observed phenotypes conferred by the various CF variants, as well as the impact of CANX on those effects. 

To complete their analysis of CF variants in CANX KO cells, the research also attempted to relate their data, primarily based on PME, to functional relevance. They observed that, although CANX KO results in a large reduction in PME (~30% reduction), changes in the actual activation of CFTR (and resultant quenching of their hYFP sensor) were "quite modest." This is an important experiment and caveat to the PME data presented above since changes in CFTR activity does not strictly require changes in PME. In addition, small molecule correctors also do not drastically alter CFTR function in the context of CANX KO. The authors reason that this difference is due to a sort of compensatory mechanism in which the functionally active CFTR molecules that are successfully assembled in an unbalanced proteostasis system (CANX KO) are more active than those that are assembled with the assistance of CANX. While I generally agree with this statement, it is not directly tested and would be challenging to actually test. 

The selected model for all the above experiments was HEK293T cells. The authors then demonstrate some of their major findings in Fischer rat thyroid cell monolayers. Specifically, cells lacking CANX are less sensitive to rescue by CFTR modulators than the WT. This highlights the importance of CANX in supporting the maturation of CFTR and the dependence of chemical correctors on the chaperone. Although this is demonstrated specifically for CANX in this manuscript, I imagine a more general claim can be made that chemical correctors depend on a functional/balanced proteostasis system, which is supported by the manuscript data. I am surprised by the discordance between HEK293T PME levels compared to the CTFR activity. The authors offer a reasonable explanation about the increase in specific activity of the mature CFTR protein following CANX loss. 

For the conclusions and claims relevant to CANX and CF variant surveying of PME/function, I find the manuscript to provide solid evidence to achieve this aim. The manuscript generates a rich portrait of the influence of CF mutations both in WT and CANX KO cells. While the focus of this study is a specific chaperone, CANX, this manuscript has the potential to impact many researchers in the broad field of proteostasis.

We thank the reviewer for their thoughtful and comprehensive perspectives on the scope and relevance of this work.

Reviewer 2 (Recommendations for the authors):

While I did not identify any major weaknesses in this manuscript, I offer some suggestions below, as well as some conclusions to consider:

(1) Missing period at the end of line 51.

We thank the reviewer for catching this grammatical error and have added proper punctuation.

(2)Figure S1 "repre-sent"??

We have corrected this punctuation error.

(3) Figure S2 missing parentheses A)

We have corrected the punctuation error.

(4) Figure S5, "B) The total ΔRMSD of the active conformation of NBD2 is shown for variants bound to VX-445. Red bars show increasing deviations from the native NBD2 conformation in the mutant models, and blue bars show how much VX-445 suppresses these conformational defects in NBD2."

VX-445 should not bind/stabilize the G85E from the calculations in Figure S5A. As a confirmation, it would be nice to see the calculated hypothetical effect of VX-445 in the G85E variant as performed for L1077P and N1303K. I also want to point out that G58E is referred to as being non-responsive in S5A, but then in S5D, N103K is referred to as non-responsive, but this variant falls pretty far below the stabilized region calculated in S5A, right?

We agree that it would be insightful to examine the RMSD changes in a non-responsive variant such as G85E. We added the G85E NBD2 ∆RMSD to Supplemental Figure S5B and a G85E ∆RMSD structure map as an additional subpanel at Supplemental Figure S5C. As the reviewer expected, VX-445 fails to confer any stability to G85E as shown by a lack of significant change in NBD2 ∆RMSD or any visible ∆RMSD throughout the structure.  Finally, we acknowledge that N1303K falls below the stabilized region as calculated in S5A. However, we note that the binding energy only suggests it is likely to interact with the protein- this does not to necessarily mean that binding will allosterically suppress conformational defects in NBD2. Moreover, this is simply an in silico calculation, that does not necessarily capture all of the nuanced interactions in the cell (or lack thereof). We have corrected this in the Figure S5 caption, which reads as follows:

“Maps of the change in RMSD between N1303K modeled with and without VX-445 shows that few structural regions are stabilized by VX-445 for N1303K, which responds poorly to VX-445 in vitro.”

(5) "stan-dard" standard?

We have corrected this punctuation error.

(6) Line 270, "these variants" is written twice

We have corrected this typographical error.

(7) Figure 6 B. What is being compared? The text writes "there are prominent differences in the activity of these variants [those with CANX] (two-way ANOVA, p = 3.8 x 10-27." Does this mean WT vs. delF508, P5L, V232D, T1036N, and I1366N combined? I have not seen a set of 5 variables compared to a single variable. Usually, it would be WT vs. DelF508, WT vs. P5L, WT vs. V232D...right? Maybe this is normal in this specific field. The same goes for the CANX knockout comparison "(two-way ANOVA, p = 0.06).".

In this instance, the two-way ANOVA test is evaluating whether there are differences in the half-lives of individual variants and/ or systematic differences across the variant measurements in the knockout line relative to the parental cells. The test gives independent p-values for these two variables (variant and cell line). We chose this test because it makes it clear that, when you consider the trends together, one variable has a significant effect while the other does not.

(8) Why don't the CFTR modulators rescue CFTR activity in the WT FRT monolayers?

We thank the reviewer for this inquiry. Please note that compared to DMSO, VX-661 does significantly enhance the forskolin-mediated response of WT-CFTR (red asterisk). Treatments with VX-445 alone, VX-661+VX-445, or VX-661+VX-445+VX-770 showed no significant forskolin stimulation of WT-CFTR. These observations could be attributable to the brief period in which WT-CFTR cDNA is transiently transfected. However, it is not necessarily anticipated that modulators would enhance WT-CFTR function. Correctors and potentiators are designed to rescue processing and gating abnormalities, respectively. WT-CFTR channels do not exhibit such defects.

In both constitutive overexpression systems and primary human airway epithelia, published literature demonstrates that prolonged exposure to CFTR modulators has resulted in variable consequences on WT-CFTR activity. For example, forskolin-mediated responsiveness of WT-CFTR is not altered by chronic application of VX-445 (PMID: 34615919) nor VX-770 (PMID: 28575328, 27402691, 37014818). In contrast, short-circuit current measurements show that forskolin stimulation of WT-CFTR is augmented by chronic treatment with VX-809 (PMID: 28575328), an analog of VX-661. Thus, our findings are congruent with observations reported by other groups.

(9) General comment: As someone not familiar with the field, it would be nice to see the structures of VX-445 and VX-661 somewhere in the figures or at least in the SI.

We appreciate this suggestion, but do not feel that we include enough structural analyses to justify a stand-alone figure for these purposes. The structures of these compounds are easily referenced on a variety of internetbased resources.

(10) Weakness: As an ensemble, the data points CANX as required for plasma membrane expression, particularly those that lie in the C-terminal domain, but when considering individual CF variants, there is no clear trend. Similarly, when looking at the effect of the pharmacological correctors on PME, no variant strays from the linear trend.

We generally agree that the predominant trend is a uniform decrease in CFTR PME across all variants and that individual variant effects are hard to generalize. Indeed, this latter point has been widely appreciated in the CF community for several decades. Our approach exposes this variability in detail, but we concede that we cannot yet fully interpret the full complexity of the trends.

(11) Something to consider: Knockout of calnexin, a central ER chaperone, is going to set off the UPR, which in turn will activate the ISR and attenuate translation. From what I can tell, in general, all CF variant PME is decreased. Is this simply because less CF protein is being synthesized?

The reviewer raises an excellent point. However, to investigate this possibility further, we compared whole-cell proteomic data for the parental and knockout cell lines. Our analysis suggests there is no significant upregulation of proteins associated with UPR activation, as is shown in the graphic to the right. In fact, only proteins associated with the PERK branch of the UPR exhibit any statistically significant changes between these two cell lines across three biological replicates. Based on this consideration, we suspect any wider changes in ER proteostasis must be relatively subtle. 

Author response image 1.

eLife Assessment

This important study uses data from OpenAlex on more than 50 million journal articles in over 50,000 research journals to examine the dynamics of interdisciplinarity and international collaboration in research journals. The data analytics used to quantify disciplinary and national diversity are convincing, and support the claims that journals have become more diverse in both aspects. The revisions made by the authors have addressed the small number of concerns the reviewers had about the original version.

Reviewer #1 (Public review):

(1) Summary

The authors aim to explore how interdisciplinarity and internationalization-two increasingly prominent characteristics of scientific publishing-have evolved over the past century. By constructing entropy-based indices from a large-scale bibliometric dataset (OpenAlex), they examine both long-term trends and recent dynamics in these two dimensions across a selection of leading disciplinary and multidisciplinary journals. Their goal is to identify field-specific patterns and structural shifts that can inform our understanding of how science has become more globally collaborative and intellectually integrated.

(2) Strengths

The primary strengths of the paper remain its comprehensive temporal scope and use of a rich, openly available dataset covering over 56 million articles. The interdisciplinary and internationalization indices are well-founded and allow meaningful comparisons across fields and time. The revised manuscript has substantially improved in several aspects. In particular, the authors have clarified the methodology of trend estimation with a concrete example and justification of the 5-year window, making their approach much more transparent. They have also expanded the discussion of potential disparities in data coverage across disciplines and time, acknowledging limitations and implementing safeguards in their analysis. Furthermore, the manuscript has been carefully revised for grammar, clarity, and style, which improves its overall polish. While a sensitivity analysis might still further strengthen the robustness of findings, the revisions satisfactorily address the main methodological concerns raised in the initial review.

(3) Evaluation of Findings

The findings, such as the sharp rise in internationalization in fields like Physics and Biology, and the divergence in interdisciplinarity trends across disciplines, are clearly presented and better substantiated in the revised version. The authors now provide more discipline-specific discussion (e.g., medicine, biology, social sciences), which adds valuable nuance to the interpretation of internationalization dynamics. The improved methodological clarity and acknowledgment of data limitations enhance the credibility of the results and their generalizability.

(4) Impact and Relevance

This study continues to make a timely and meaningful contribution to scientometrics, sociology of science, and science policy. Its combination of scale, historical depth, and field-level comparison offers a useful framework for understanding changes in scientific publishing practices. The entropy-based indicators remain a simple yet flexible tool, and the expanded discussion of their appropriateness strengthens the methodological foundation. The use of open bibliometric data enhances reproducibility and accessibility for future research. Policymakers, journal editors, and researchers interested in publication dynamics will likely find this work informative, and its methods could be applied or extended to other structural dimensions of scholarly communication.

Reviewer #2 (Public review):

Summary:

This paper uses large-scale publication data to examine the dynamics of interdisciplinarity and international collaborations in research journals. The main finding is that interdisciplinarity and internationalism have been increasing over the past decades, especially in prestigious general science journals.

Strengths:

The paper uses a state-of-the-art large-scale publication database to examine the dynamics of interdisciplinarity and internationalism. The analyses span over a century and in major scientific fields in natural sciences, engineering, and social sciences. The study is well designed and has provided a range of robustness tests to enhance the main findings. The writing is clear and well organized.

Author response:

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

Reviewer #1 (Public review):

However, some methodological choices, such as the use of a 5-year sliding window to compute trend values, are insufficiently justified and under-explained. The paper also does not fully address disparities in data coverage across disciplines and time, which may affect the reliability of historical comparisons. Finally, minor issues in grammar and clarity reduce the overall polish of the manuscript.

We thank the reviewer for pointing out the weakness of the manuscript. We addressed these comments in our response to Recommendations A and B. Minor grammar and clarity issues have also been addressed.

Reviewer #2 (Public review):

The first thing that comes to mind is the epistemic mechanism of the study. Why should there be a joint discussion combining internationalism and interdisciplinarity? While internationalism is the tendency to form multinational research teams to work on research projects, interdisciplinarity refers to the scope and focus of papers that draw inspiration from multiple fields. These concepts may both fall into the realm of diversity, but it remains unclear if there is any conceptual interplay that underlies the dynamics of their increase in research journals.

We thank the reviewer for pointing out the lack of clarity in our decision to conduct a joint discussion of interdisciplinarity and internationalization.

It is a well-known fact that team science has increased in importance over time. An important question then is whether teams have only grown in size and frequency or whether they have changed in other aspects. Interdisciplinarity and internationalization are two aspects in which teams could have changed.

We revised the Introduction (Lines 68–70 of the revised manuscript) to address this matter.

It is also unclear why internationalization is increasing. Although the authors have provided a few prominent examples in physics, such as CERN and LAGO, which are complex and expensive experimental facilities that demand collective efforts and investments from the global scientific community, whether some similar concerns or factors drive the growth of internationalism in other fields remains unknown. I can imagine that these concerns do not always apply in many fields, and the authors need to come up with some case studies in diverse fields with some sociological theory to support their empirical findings.

We thank the reviewer for requesting further evidence concerning why our findings may be correct. Physics is an area where the need for extraordinary resources has naturally led to large international collaborative efforts. As we discuss in line 255 of the revised manuscript, this is actually also the case for biology. The Human Genome Project and subsequent projects have also required massive investments, leading to further internationalization.

We believe that the drive toward internationalization for medicine has to do with the need for establishment of robust results that are not specific to a single country or medical system. Additionally, the impact of global epidemics — Acquired immunodeficiency Syndrome (AIDS), Severe Acute Respiratory Syndrome (SARS) — has also increased the needs to involve researchers from around the world.

The case for increased internationalization in the social sciences is, we believe, related to the desire to identify phenomena that extend beyond the Western, educated, industrialized, rich and democratic (WEIRD) societies.

We have expanded the discussion around these points in lines 274–283 of the revised manuscript.

The authors use Shannon entropy as a measure of diversity for both internationalism and interdisciplinarity. However, entropy may fail to account for the uneven correlations between fields, and the range of value chances when the number of categories changes. The science of science and scientometrics community has proposed a range of diversity indicators, such as the RaoStirling index and its derivatives. One obvious advantage of the RS index is that it explicitly accounts for the heterogeneous connections between fields, and the value ranges from 0 to 1. Using more state-of-the-art metrics to quantify interdisciplinarity may help strengthen the data analytics.

We thank the reviewer for pointing the need to provide a deeper discussion of the impact of different metrics on how disciplinary diversity is calculated. We chose Shannon’s entropy because it accounts for both richness (the number of distinct fields) and evenness (the balance of representation across fields). While measures such as the Rao-Stirling index can be very useful when considering disciplines at different levels of aggregation, since to consider only level 0 Field-of-Study (FoS) tags, that problem is not as much a concern for our analysis.

We have added a further clarification in lines 145–151 of the revised manuscript.

Reviewer #1 (Recommendations for the authors)

Ambiguity in the Trend Calculation Methodology in Figure 4 and 5

The manuscript uses a 5-year sliding window to calculate recent trends in interdisciplinarity (I_d) and internationalization (I_n), but the method is not clearly described. Could the authors clarify whether the trend is calculated by (1) performing linear regression on the index values over the past 5 years, (2) using the regression slope as the trend value, and (3) interpreting the sign and magnitude of the slope to indicate increasing, decreasing, or stable trends? Additionally, the rationale for choosing a 5-year window over other durations (e.g., 10 or 15 years) is not discussed. Given that different time windows could yield different insights, a brief justification or sensitivity check would strengthen the methodological transparency.

Thank you for pointing the lack of clarity in our description. In an attempt to increase clarity, we added a specific case study to illustrate the use of 5-year trend in the Supplementary Information: Estimation of tendency of the revised manuscript (Lines 691–704 of the revised manuscript).

Specifically, imagine we want to calculate the trend of the Interdisciplinarity Index for 2010 for Annalen der Physik. We would perform an ordinary least squares linear fit to the 6 data points for the Index in years 2005–2010.

The reason to focus on a 5-year window is two-fold. First, a longer time period would — as suggested by the data on Figure S10 — likely aggregate over multiple trends. Second, a shorter time period would result in too great an uncertainty in the estimation of the trend.

This is the reason why we did not implement a sensitivity analysis. Reasonable time windows that consider the two reasons expressed above would be too narrow to provide a worthwhile analysis.

Lack of Discussion on Temporal Coverage Disparities Across Disciplines

The study spans publications from 1900 to 2021, but the completeness and representativeness of the data-especially in earlier decades-may differ significantly across disciplines. For instance, OpenAlex has limited coverage for publications before the mid-20th century, and disciplines such as Medicine and Political Science may have adopted journal-based publishing at different historical periods compared to Physics or Chemistry. These temporal disparities could bias cross-disciplinary comparisons of long-term trends in interdisciplinarity and internationalization. I recommend that the authors briefly discuss this limitation and, if possible, report when coverage becomes reliable for each discipline. A sensitivity analysis starting from a common baseline year (e.g., 1950 or 1970) could also help assess whether the observed disciplinary differences are driven in part by unequal temporal data availability.

We thank the reviewer for the requesting further clarification on this matter. We completely agree that “completeness and representativeness of the data – especially in earlier decades-may differ significantly across disciplines”. That is exactly the reason why we made the analyses choices described in the manuscript.

Indeed, we consider only three journals for the analysis of the entire 1900–2021 period. Those 3 journals, Nature, PNAS and Science are ones that we know to be well recorded.

When conducting the disciplinary analysis, we focus on the period 1960–2021. While we know that the coverage for the social sciences is less robust until the 1990s, we address this concern by implementing several safeguards:

Manual selection of representative journals in each discipline to ensured that their publications are well represented in OpenAlex.

Decade by decade analysis of interdisciplinarity and internationalization so that changes over time can be identified and potential issues with data coverage are restricted to only some aspects of the analysis.

We also acknowledge the potential coverage disparities in earlier years of the data source (Lines 319-326 of the revised manuscript).

The authors use both interdisciplinarity and multidisciplinarity. While these concepts offer similar definitions of diversity, it may help the reader if there is some explanation to clarify their subtle differences. (Reviewer #2)

It is a well-known fact that team science has increased in importance over time. An important question then is whether teams have only grown in size and frequency or whether they have changed in other aspects. Interdisciplinarity and internationalization are two aspects in which teams could have changed.

We revised the Introduction (Lines 68–70 of the revised manuscript) to address this matter.

Minor Comments

Several sentences

(1) Line 11: The phrase “authors form multiple countries” contains a typographical error. The word “form” should be corrected to “from” so that the sentence reads: “authors from multiple countries.”

tences and phrases throughout the manuscript could be improved for grammatical accuracy, clarity, and stylistic appropriateness:

(2) Line 63: The clause “these expansion is well described by a logistic model” contains a subject-verb agreement error. “These” should be replaced by the singular demonstrative pronoun “this”, resulting in: “This expansion is well described by a logistic model.”

(3) Line 89: The phrase “were quickly overcame” misuses the verb form. “Overcame” is a past tense form and should be replaced with the past participle “overcome” to match the passive construction. Suggested revision: “were quickly overcome.”

(4) Line 106: The verb “refered” is misspelled. It should be corrected to “referred” for proper past tense. The corrected phrase should read: “we referred to...”

(5) Line 127: The phrase “sing discipline papers” contains a typographical error. “Sing” should be “single”, yielding: “single discipline papers.”

(6) Lines 238–239: The sentence “An exception to this pattern are the two mega open-access journals: PLOS One and Scientific Reports, which have internationalization indices as high the the most internationalized Physics journals.” contains multiple grammatical issues.

First, the subject “An exception” is singular, but the verb “are” is plural; this results in a subject-verb agreement error.

Second, the phrase “the the” includes a typographical repetition.

Third, the comparative construction is incomplete; “as high the the...” is ungrammatical and should use “as high as.”

Suggested revision: “An exception to this pattern is the pair of mega open-access journals— PLOS One and Scientific Reports—which have internationalization indices as high as those of the most internationalized Physics journals.”

(7) Line 254: The sentence “biological research been revolutionized...” lacks an auxiliary verb. To be grammatically correct, it should read: “biological research has been revolutionized...”

(8) Line 258: The phrase “need global spread of...” is syntactically awkward. Depending on the intended meaning, it could be revised to either “the global spread of...” or “the global need for the spread of...” for clarity.

(9) Figure S2 Caption: The term “Microsofe Academic Graph” is a typographical error and should be corrected to “Microsoft Academic Graph.”

(10) Reference [40]: The link “ttps://doi.org/10.1038/nature02168” is missing the “h” in “https.” The corrected version is: “https://doi.org/10.1038/nature02168.”

We appreciate your comments on the grammar and clarity of the manuscript. We have thoroughly reviewed and corrected these issues to improve the overall clarity of the text.

Line 11: We changed the typo “form” to “from”.

Line 63: We changed the sentence to “There has been a significant expansion in the number of countries where scientists are publishing in selective journals”.

Line 89 (Line 93 of the revised manuscript): We revised the sentence as suggested, and the revised sentence becomes “Even the significant impacts on publication rates of the two World Wars were quickly overcome, and exponential growth resumed. ”

Line 106 (Line 110 of the revised manuscript): We changed the typo “refered” to “referred”.

Line 127 (Line 131 of the revised manuscript): We changed the typo “Sing” to “single”.

Lines 238-239 (Lines 245-247 of the revised manuscript): We thank the issues pointed out by the reviewer, and we took the reviewer’s suggested version and changed the original sentence to “An exception to this pattern is the pair of mega open-access journals — PLOS One and Scientific Reports — which have internationalization indices as high as those of the most internationalized Physics journals”.

Line 254 (Line 262 of the revised manuscript): We added the auxiliary verb to the sentence, and the sentence now becomes “biological research has been revolutionized”

Line 258 (Line 266 of the revised manuscript): We changed the phrase to “the global need for the spread of”.

Figure S2 Caption: We corrected the typo of “Microsoft Academic Graph”.

Reference [40]: We corrected the URL of the reference.

Reviewer #2 (Recommendations for author):

Some typos:

(1) Page 2: On page 2, “contributions from a multiple disciplines” and ”these expansion is well described”.

(2) Page 4: “World Wars were quickly overcame”.

(3) Page 5: “to quantify the the internationalization of a journal”.

(4) Page 10: “indices as high the the most internationalized Physics journals”

(5) Page 10: The sentence “indices as high the the most internationalized Physics journals” contains multiple issues. The phrase “the the” is a typographical error, and the comparative construction is incomplete. It should be revised to: “indices as high as those of the most internationalized Physics journals.”

We revised those typographical errors on page 2, 4, 5, and 10 pointed out by the reviewer. We truly thank the reviewer’s critical examination on the syntax of the manuscript.

Page 2: We removed “a” so now the sentence reads: “contributions from multiple disciplines.”

Page 2: We changed the sentence to “There has been a significant expansion in the number of countries where scientists are publishing in selective journals”.

Page 4: We replaced “overcame” with the past participle “overcome” , resulting in: “World Wars were quickly overcome.”

Page 5: The phrase “to quantify the the internationalization of a journal” contains a typographical repetition. We changed it to: “to quantify the internationalization of a journal.”

Page 10: For the sentence “indices as high the the most internationalized Physics journals”, we removed duplicated “the” as a typographical error. We revised the sentence into: “indices as high as those of the most internationalized Physics journals.”

eLife Assessment

The authors investigated the potential role of IgG N-glycosylation in Haemorrhagic Fever with Renal Syndrome (HFRS), which may offer significant insights for understanding molecular mechanisms and for the development of therapeutic strategies for this infectious disease. The findings are thought to be valuable to the field and the strength of evidence to support the findings is solid.

Reviewer #1 (Public review):

Summary:

The authors investigated the potential role of IgG N-glycosylation in Haemorrhagic Fever with Renal Syndrome (HFRS), which may offer significant insights for understanding molecular mechanisms and for the development of therapeutic strategies for this infectious disease.

Comments on revisions:

While the majority of the issues have been addressed, a few minor points still remain unresolved.

Quality control should be conducted prior to the analysis of clinical samples. However, the coefficient of variation (CV) value was not provided for the paired acute and convalescent-phase samples from 65 confirmed HFRS patients, which were analyzed to assess inter-individual biological variability. It is important to note that biological replication should be evaluated using general samples, such as standard serum.

Reviewer #2 (Public review):

This work sought to explore antibody responses in the context of hemorrhagic fever with renal syndrome (HFRS) - a severe disease caused by Hantaan virus infection. Little is known about the characteristics or functional relevance of IgG Fc glycosylation in HFRS. To address this gap, the authors analyzed samples from 65 patients with HFRS spanning the acute and convalescent phases of disease via IgG Fc glycan analysis, scRNAseq, and flow cytometry. The authors observed changes in Fc glycosylation (increased fucosylation and decreased bisection) coinciding with a 4-fold or greater increased in Haantan virus-specific antibody titer. The study also includes exploratory analyses linking IgG glycan profiles to glycosylation-related gene expression in distinct B cell subsets, using single-cell transcriptomics. Overall, this is an interesting study that combines serological profiling with transcriptomic data to shed light on humoral immune responses in an underexplored infectious disease. The integration of Fc glycosylation data with single-cell transcriptomic data is a strength.

The authors have addressed the major concerns from the initial review. However, one point to emphasize is that the data are correlative. While the associations between Fc glycosylation changes and recovery are intriguing, the evidence does not establish causation. This is not a weakness, as correlative studies can still be highly valuable and informative. However, the manuscript would be strengthened by making this distinction clear, particularly in the title.

Author response:

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

Reviewer #1 (Public review):

(1) The authors should provide a detailed description of the pathogenesis of Haemorrhagic Fever with Renal Syndrome (HFRS) and elaborate on the crucial role of IgG proteins in the disease's progression (line 65).

As suggested, we have now provided a detailed description of the pathogenesis of HFRS and elaborated on the crucial role of IgG proteins in the disease's progression:

"Hantaviruses are tri-segmented, single-stranded, negative-sense RNA viruses, whose genomes consist of three regions: large (L), medium (M), and small (S). The glycoproteins Gn and Gc, encoded by the M segment, can infect target cells - primarily vascular endothelial cells - via β3 integrin receptors (Pizarro et al., 2019). Simultaneously, they could also infect other cell types, such as mononuclear macrophages and dendritic cells, leading to systemic viral infection. Although hantavirus replication is thought to occur primarily in the vascular endothelium without direct cytopathic effects, a plethora of innate immune cells mediate host antiviral defenses. These include natural killer cells, neutrophils, monocytes, and macrophages, together with pattern recognition receptors (PRRs), interferons (IFNs), antiviral proteins, and complement activation, e.g., via the pentraxin 3 (PTX3) pathway, which can exacerbate HFRS disease progression leading to immunopathological damage through cytokine/chemokine production, cytoskeletal rearrangements in endothelial cells, ultimately amplifying vascular dysfunction (Tariq & Kim, 2022). Rapid and effective humoral immune responses, however, such as neutralizing antibody responses targeting the glycoproteins Gn/Gc, contribute to rapid recovery from HFRS and are critical for protection from severe disease (Engdahl & Crowe, 2020; Li et al., 2020)." Please see the Introduction (Page 4, lines 65-81).

(2) An additional discussion on the significance of glycosylation, particularly IgG N-glycosylation, in viral infections should be included in the Introduction section.

Thank you for the suggestion and we have added an additional discussion on the significance of glycosylation in viral infections in the revised Introduction section.

"Immunoglobulin G (IgG) N-linked glycosylation mediates critical functions modulating antiviral immunity during viral infection. Changes in the conserved N-linked glycan Asn297 in the Fc region of IgG typically by fucosylation, galactosylation, or sialylation can alter antibody effector function. A reduction in core fucosylation decreases IgG binding to NK cell FcγRIIIa promotes antibody-dependent cellular cytotoxicity (ADCC) necessary for clearance of viruses, including SARS-CoV-2, dengue and HIV-1 whereas sialylation can attenuate immune responses resulting in immune evasion (Ash et al., 2022; Haslund-Gourley et al., 2024; Hou et al., 2021; Wang et al., 2017). Changes in IgG and other protein N-linked glycosylation profiles therefore shape virus-host interactions and disease progression." (Page 4, lines 82-91).

(3) In the abstract section, the authors state that HTNV-specific IgG antibody titers were detected and IgG N-glycosylation was analyzed. However, the analysis of plasma IgG N-glycans is described in the Methods section. Therefore, the authors should clarify the glycome analysis process. Was the specific IgG glycome profile similar to the total IgG N-glycome? Given the biological relevance of specific IgG in immunological diseases, characterizing the specific IgG N-glycome profile would be more significant than analyzing the total plasma IgG.

We are grateful to the reviewer for the comments. Previous studies on viral infections have revealed that the pattern of virus-specific IgG N-glycans may be similar to that of total IgG N-glycome, and we therefore analyzed the total plasma IgG glycosylation profiling in the HFRS patients. However, we have discussed this in the Discussion section.

"Despite establishing a well-characterized patient cohort and performing systematic IgG glycosylation profiling based on HTNV NP antibody status, this study has several noteworthy limitations. Most notably, while preliminary comparisons suggested similar patterns between virus-specific and total IgG N-glycome, our total plasma IgG analysis may have introduced confounding factors in the observed associations. This methodological constraint could potentially affect the interpretation of certain disease-specific glycosylation signatures." Please see the Discussion (Page 12, lines 274-280). 

References

(1) Mads Delbo Larsen, Erik L de Graaf, Myrthe E Sonneveld, et al. Afucosylated IgG characterizes enveloped viral responses and correlates with COVID-19 severity. Science . 2021 Feb 26;371(6532):eabc8378.

(2) Chakraborty S, Gonzalez J, Edwards K, et al. Proinflammatory IgG Fc structures in patients with severe COVID-19. Nat Immunol. 2021 Jan;22(1):67-73.

(3) Tea Petrović, Amrita Vijay, Frano Vučković, et al. IgG N-glycome changes during the course of severe COVID-19: An observational study. EBioMedicine. 2022 Jul ;81: 104101. 

(4) Hou H, Yang H, Liu P, et al. Profile of Immunoglobulin G N-Glycome in COVID-19 Patients: A Case-Control Study. Front Immunol. 2021 Sep 23;12:748566.

(4) Further details regarding the N-glycome analysis should be provided, including the quantity of IgG protein used and the methodology employed for analyzing IgG N-glycans (lines 286-287).

As suggested, we have provided further details regarding the N-glycome analysis in the Method section.

"Briefly, the diluted plasma samples were transferred onto a 96-well protein G monolithic plate (BIA Separations, Slovenia) for the isolation of IgG. The isolated IgG was eluted with 1 mL of 0.1 M formic acid and was immediately neutralized with 170 µL of 1M ammonium bicarbonate.

The released N-glycans were labelled with 2-aminobenzamide (2-AB) and were then purified from a mixture of 100% acetonitrile and ultrapure water in a 1:1 ratio (v/v). This was then analyzed by hydrophilic interaction liquid chromatography using ultra-performance liquid chromatography (HILIC-UPLC; Walters Corporation, Milford, MA) (Hou et al., 2019). As previously reported, the chromatograms were separated into 24 IgG glycan peaks (GPs) (Menni et al., 2018)." Please see the Method section (Page 15, lines 346-355).

(5) Additional statistical analyses should be performed, including multiple comparisons with p-value adjustment, false discovery rate (FDR) control, and Pearson correlation (line 291).

As suggested, we have performed additional statistical analyses and mentioned the results in the revised manuscript.

"Positive correlations were observed between the ASM subsets and both galactosylation (p=0.017, r_s=0.418) and sialylation (p=0.008, r_s=0.458) in the antibody Fc region, as well as between the PB subsets and sialylation (p=0.036, r_s=0.372) (Figure 4A-C). (Page 8, lines 180-183)"

"The Benjamini - Hochberg (BH) method was used to adjust the raw p-values from DEG analysis, controlling the false discovery rate (FDR)." Please see the Materials and Methods (Page 16, lines 369-371).

(6) Quality control should be conducted prior to the IgG N-glycome analysis. Additionally, both biological and technical replicates are essential to assess the reproducibility and robustness of the methods.

Thank you for the suggestion. We have added descriptions on the biological and technical replicates in the Method section.

"Our study incorporated both biological and technical replicates to ensure a robust glycomic profiling analysis. Specifically, we analyzed paired acute/convalescent-phase samples from 65 confirmed HFRS patients to assess inter-individual biological variability, while technical reproducibility was validated through comparison with standard chromatographic peak plots (Vučković et al., 2016). This dual-replicate strategy enabled a comprehensive evaluation of both biological heterogeneity and assay precision." (Page 15, lines 356-362).

(7) Multiple regression analysis should be conducted to evaluate the influence of genetic and environmental factors on the IgG N-glycome.

As suggested, we have conducted multiple regression analysis to evaluate the influence of genetic and environmental factors on the IgG N-glycome. These results have been provided in the revised Result section.

"Multivariate linear regression was employed to mitigate potential confounding by genetic and environmental factors in the glycomics analysis. While no significant associations were observed for most glycan models (fucosylation, p=0.526; bisecting GlcNAc, p=0.069; and sialylation, p=0.058), we discovered sex showed a potentially influential effect on galactosylation (p=0.001) (Supplementary files 5-8). These results suggest that while most glycan features appear unaffected by the examined covariates, galactosylation may be subject to sex-specific biological regulation." (Page 7, lines 153-160).

(8) Line 196. Additional discussions should be included, focusing on the underlying correlation between the differential expression of B-cell glycogenes and the dysregulated IgG N-glycome profile, as well as the potential molecular mechanisms of IgG N-glycosylation in the development of HFRS.

Thank you for your suggestions. We have added these contents in the Discussion section.

"Antibody-related glycogenes are significantly activated following Hantaan virus infection. We noted that ribophorin I and II (RPN1 and RPN2) were significantly upregulated in the ASM/IM/PB/RM subsets after Hantaan virus infection, which linked the high mannose oligosaccharides with asparagine residues found in the Asn-X-Ser/Thr consensus motif (Hwang et al., 2025). We speculate that they continuously attach the synthesized glycan chains to the constant region of antibodies during antibody synthesis. Similarly, fucosyltransferase 8 (FUT8) in the ASM subset, catalyzing the alpha1-2, alpha1-3, and alpha1-4 fucose addition (Wang & Ravetch, 2019; Yang et al., 2015), was downregulated in the mRNA translation, and the levels of fucosylated antibodies were naturally lower in the acute HFRS patients. Meanwhile, the beta-1,4-galactosyltransferase (beta4GalT) gene expression was significantly elevated in the ASM subpopulation during the acute phase, which also correlated with increased levels of galactosylated antibodies in serum (Wang & Ravetch, 2019). However, we did not observe significant upward changes in sialyltransferase mRNA expression in the acute HFRS patients, similar with the finding from severe COVID-19 cohorts (Haslund-Gourley et al., 2024). The neuraminidase 1 (NEU1) gene is strikingly upregulated and may potentially explain the decreased sialylation on the secreted HTNV-specific IgG antibodies during convalescence. Overall, the glycosylation of immunoglobulin G is regulated by a large network of B-cell glycogenes during HTNV infection." Please see the Discussion (Page 11, lines 254-273).

Reviewer #2 (Public review):

(1) While it is great to reference prior publications in the Materials and Methods section, the current level of detail is insufficient to clearly understand the study design and experimental procedures performed. Readers should not be expected to consult multiple previous papers to grasp the core methodological aspects of the present paper. For instance, the categorization of HFRS patients into different clinical subtypes/ courses, and the methods for measuring Fc glycosylation should be explicitly described in the Materials and Methods section of this manuscript. 

Many thanks for your comments. We have added more details regarding the study design and experimental procedures in the Materials and Methods section. "Clinical specimens were collected from HFRS patients who were hospitalized in Baoji Central Hospital between October 2019 and January 2022. Patients were categorized into four clinical subtypes (mild, moderate, severe, and critical) based on the diagnostic criteria for HFRS issued by the Ministry of Health (Ma et al., 2015). This study was approved by the ethics committee of the Shandong First Medical University & Shandong Academy of Medical Sciences (R201937). Written informed consent was obtained from each participant or their guardians.

The clinical course of HFRS is grouped into acute (febrile, hypotensive, and oliguric stages) and convalescent (diuretic and convalescent stages) phases. The acute phase was defined as within 12 days of illness onset, and the convalescent phase was defined as a period of illness lasting 13 days or longer (Tang et al., 2019; Zhang et al., 2022). The earliest sample was selected if there were multiple blood samples available in the acute phase and the last available sample before discharge was selected if there were multiple blood samples in the convalescent phase.

Briefly, the diluted plasma samples were transferred onto a 96-well protein G monolithic plate (BIA Separations, Slovenia) for the isolation of IgG. The isolated IgG was eluted with 1 mL of 0.1 M formic acid and was immediately neutralized with 170 µL of 1M ammonium bicarbonate.

The released N-glycans were labelled with 2-aminobenzamide (2-AB) and were then purified from a mixture of 100% acetonitrile and ultrapure water in a 1:1 ratio (v/v). This was then analyzed by hydrophilic interaction liquid chromatography using ultra-performance liquid chromatography (HILIC-UPLC; Walters Corporation, Milford, MA) (Hou et al., 2019). As previously reported, the chromatograms were separated into 24 IgG glycan peaks (GPs) (Menni et al., 2018)." Please see the Materials and Methods (Page 13, lines 290-303, and Page 15, lines 346-355).

(2) The authors should explain the nature of their cohort in a bit more detail. While it appears that HFRS cases were identified based on IgM ELISA and/or PCR, these are indicators of the Haantan virus infection. My understanding is that not all Haantan virus infections progress to HFRS. Thus, it is unclear whether all patients in the HFRS group actually had hemorrhagic fever. This distinction is critical for interpreting how the results observed relate to disease severity.

We are sincerely grateful for this valuable suggestion. We have carefully revised Figure 1 and the texts (Page 5, lines 104-107) in the revised manuscript.

"To characterize the humoral immune profiles in HFRS patients, we enrolled 166 suspected HTNV-infected patients who were admitted to Baoji Central Hospital in Shaanxi Province, China, between October 2019 and January 2022. Among them, 65 met the inclusion criteria and were included in the study (Figure 1)."

(3) The authors state that: "A 4-fold or greater increase in HTNV-NP-specific antibody titers usually indicates a protective humoral immune response during the acute phase", but they do not cite any references or provide any context that supports this claim. Given that in their own words, one of the most significant findings in the study is changes in glycosylation coinciding with this 4-fold increase, it is important to ground this claim in evidence. Without this, the use of a 4-fold threshold appears arbitrary and weakens the rationale for using this immune state as a proxy for protective immunity.

Thank you for the suggestion and we have provided relevant references in the Results section (Page 8, lines 171-173).

According to the Expert Consensus on Prevention and Treatment of Hemorrhagic  Fever with Renal Syndrome (HFRS) (https://ts-cms.jundaodsj.com/file/163823638693909.pdf), a confirmed diagnosis requires, based on a suspected or clinical diagnosis, one of the following: positive serum-specific IgM antibodies, detection of Hantavirus RNA in patient specimens, a four-fold or greater rise in titer of serum-specific IgG antibodies in the convalescent phase compared to the acute phase, or isolation of Hantavirus from patient specimens. A four-fold or greater rise in titer of convalescent serum-specific IgG antibodies compared to the acute phase not only suggests a recent Hantaan virus infection, but also the production of antibodies helping to combat the viral infection. In addition, the antibody glycosylation modifications may thus play a significant role in the antiviral immune response.

(4) The authors also claim that changes in Fc glycosylation influence recovery from HFRS - a point even emphasized in the manuscript title. However, this conclusion is not well supported by the data for two main reasons. First, the authors appear to measure bulk IgG Fc glycans, not Fc glycans of Hantaan virus-specific antibodies. While reasonable, this is something that should be communicated in the manuscript. Hantaan virus-specific antibodies are likely a very small fraction of total circulating IgG antibodies (perhaps ~1%), even during acute infection. As a result, changes in bulk Fc glycosylation may (or may not) accurately reflect the glycosylation state of Hantaan virus-specific antibodies. Second, even if the bulk Fc glycan shifts do mirror those of Hantaan virus-specific antibodies, it remains unclear whether these changes causally drive recovery or are merely a consequence of the infection being resolved. Thus, while the differences in Fc glycosylation observed are interesting - and it is tempting to speculate on their functional significance - the manuscript treats the observed correlations as causal mechanistic insight without sufficient data or justification.

Thank you for your valuable comments. This study measured bulk IgG Fc glycans, not Fc glycans of Hantaan virus-specific antibodies. We have described this limitation in the Discussion section (Page 12, lines 274-280). As reported in previous studies (references provided below), the changed pattern of virus-specific IgG N-glycans may reflect the total IgG N-glycome. Nevertheless, more studies are clearly needed to directly measure virus-specific IgGs and to clarify the causal mechanistic insights.

References

(1) Mads Delbo Larsen, Erik L de Graaf, Myrthe E Sonneveld, et al. Afucosylated IgG characterizes enveloped viral responses and correlates with COVID-19 severity. Science. 2021 Feb 26;371(6532): eabc8378.

(2) Chakraborty S, Gonzalez J, Edwards K, et al. Proinflammatory IgG Fc structures in patients with severe COVID-19. Nat Immunol. 2021 Jan;22(1):67-73.

(3) Tea Petrović, Amrita Vijay, Frano Vučković, et al. IgG N-glycome changes during the course of severe COVID-19: An observational study. EBioMedicine. 2022 Jul ;81: 104101. 

(4) Hou H, Yang H, Liu P, et al. Profile of Immunoglobulin G N-Glycome in COVID-19 Patients: A Case-Control Study. Front Immunol. 2021 Sep 23;12: 748566.

(5) Fc glycosylation is known to be influenced by covariates such as age and sex. While it is helpful that the authors stratified the patients by age group and looked for significant differences in glycosylation across them, a more robust approach would be to directly control for these covariates in the statistical analysis - such as by using a linear mixed effects model, in which disease state (e.g., acute vs. convalescent), age, and sex are treated as fixed effects, and subject ID is included as a random effect to account for repeated measures. This would allow the authors to assess whether observed differences in Fc glycosylation remain significant after accounting for potential confounders. This could be important given that some of the reported differences are quite small, for example, 94.29% vs. 94.89% fucosylation.

Thank you for your valuable suggestion. As suggested, we have conducted multiple regression analysis to evaluate the influence of genetic and environmental factors on the IgG N-glycome, and have provided these results in the revised Result section.

"Multivariate linear regression was employed to mitigate potential confounding by genetic and environmental factors in the glycomics analysis. While no significant associations were observed for most glycan models (fucosylation, p=0.526; bisecting GlcNAc, p=0.069; and sialylation, p=0.058), we discovered sex showed a potentially influential effect on galactosylation (p=0.001) (Supplementary files 5-8). These results suggest that while most glycan features appear unaffected by the examined covariates, galactosylation may be subject to sex-specific biological regulation." (Page 7, lines 153-160).

(6) The manuscript states that there are limited studies on antibody glycosylation in the context of HFRS, but does not cite any relevant literature. If prior work exists, it should be cited to contextualize the current study. If no prior studies have been conducted/reported, to the author's knowledge, that should be stated explicitly to show the novelty of the work.

Thank you for your suggestion. To our knowledge, there has been no prior reports regarding the regulation of IgG glycosylation in HFRS, particularly in relation to seroconversion. We have reworded this sentence in the revised manuscript. "Importantly, there have not been prior studies specifically examining plasma IgG N-glycome profiles derived from chromatographic peak data in HFRS patients, particularly in relation to seroconversion status. This gap in our knowledge motivated our systematic investigation of both total and virus-specific IgG glycosylation dynamics during acute infection." Please see the Introduction (Page 5, lines 92-96).

Reviewer #2 (Recommendations for the authors):

Minor points:

(1) Line 47, 78: The use of the word 'However' appears to be an incorrect expression.

We have made this correction.

(2) Line 127: The term 'glycome' should be replaced with 'N-glycome,' and all relevant expressions should be corrected accordingly, such as 'N-glycosylation.

We have made this correction.

(3) Line 84-87: The sentence 'A total of 166 HFRS patients...' contains a grammatical error.

We have made tis correction (Page 5, lines 99-101).

eLife Assessment

This study addresses an important question in liver biology: how zonal hepatocytes balance survival and proliferation following injury; using spatial transcriptomics, mechanistic perturbations, and functional assays, the authors propose that a mid-zone Atf4-Chop axis to Btg2 program temporarily suppresses proliferation to promote survival during APAP-induced hepatotoxicity. The idea that distinct intrahepatic zones mount tailored stress responses is conceptually significant and has implications for regeneration and toxicology. The dataset is rich and the methodology modern, but several conclusions rely on assumptions about zonation under injury, limited injury models, and incomplete functional validation of the Atf4-Chop-Btg2 axis. With targeted revisions and additional experiments, the work has the potential to provide strong mechanistic insights into liver zonation and injury responses.

Reviewer #1 (Public review):

Summary:

The authors present evidence that during acetaminophen (APAP)-induced liver injury, mid-zone hepatocytes activate an integrated stress response (ISR) program via Atf4 and Chop, leading to induction of Btg2. This program suppresses proliferation in the early phase of injury, prioritizing hepatocyte survival before regeneration begins. The study uses spatial transcriptomics, immunohistochemistry, CUT&RUN, and AAV overexpression to support this model.

Strengths:

(1) Innovative use of spatial transcriptomics to capture zonal differences in hepatocyte stress responses.

(2) Identification of a mid-zone specific ISR signature and candidate downstream regulator Btg2.

(3) Functional experiments with Atf4-Chop-Btg2 modulation provide causal evidence linking ISR activation to proliferation inhibition.

(4) Conceptually significant model that hepatocytes actively balance survival and regeneration dynamically in a zone-specific manner.

Weaknesses:

(1) Zonation definition under injury has been shown to be sustained broadly, but is not sufficiently validated and quantified, especially considering the resolution of the 10x Visium system and the potential variation of outcomes based on how to define zones.

(2) The model is built entirely in APAP injury, which specifically targets pericentral hepatocytes. It remains unclear whether the proposed mechanism applies to other liver injuries (e.g., partial hepatectomy, CCl4).

(3) Baseline proliferation appears higher than expected in homeostasis (Figure 1B), and fold change analysis (not absolute counts) may be needed to assess zonal proliferation suppression (Figure 1D).

(4) AAV-based overexpression raises potential confounds (altered CYP activity before injury) and shows incomplete penetrance that is not quantified. (Figure 5 - Figure 6).

(5) The functional link between proliferation suppression and improved survival is inferred, but direct survival /injury readouts are limited.

Reviewer #2 (Public review):

The manuscript reports protection of midlobular hepatocytes from APAP toxicity by activation of Atf4-CHOP (Ddit3)-mediated cell cycle arrest and stress response. The authors acknowledge that their finding is unexpected because CHOP typically induces cell death. Therefore, they functionally validate several aspects of the proposed Atf4-CHOP mechanism. Along these lines, the mitigation of APAP toxicity by AAV expression of Atf4 or Btg2, the latter identified as CHOP effector, is impressive. Whether Atf4 indeed acts through CHOP and whether midlobular hepatocytes are protected because of cell cycle arrest is less clear. These and other criticisms are described in the following.

Major points:

(1) Starting with the basics, one wonders why midlobular hepatocytes manage to mount a defensive response to APAP but pericentral hepatocytes don't. Is this because midlobular hepatocytes express the relevant Cyps (2e1, but also 1a2 and 3a11) at lower levels, which mitigates toxicity and buys them time? This would be supported by F2A but not by F3B, at least not for the most important Cyp2e1. A moderate difference is shown for Cyp1a2 expression in F3D, but is that enough to explain the different fates? Or are additional post-transcriptional effects on these Cyps at work?

(2) The evidence presented in support of cell cycle arrest of midlobular hepatocytes is not fully convincing: there is no overt difference in S and G2/M gene scores in F2F; the marker genes used for S phase and G1 to S progression in F2G are unusual. Along these lines, one wonders if spatial transcriptomics confirmed the Ki67 immunostaining results in F1 also for specific zones, not only overall, as shown in F2E?

(3) The authors conclude in line 364 that halting of proliferation by Btg2 favors survival, which raises the question of whether Btg2 knockout causes death in midlobular hepatocytes in F6K. Data addressing this question, that is, the localization and extent of tissue necrosis and ALT levels after APAP, are missing. The efficiency of the knockout of Btg2 is also not given.

(4) Related to the previous question, the BTG2 immunostaining in F6F is not convincing when compared to F6D. One also wonders if it is necessary to apply APAP to find induction of BTG2 by AAV-Ddit3?

(5) Related to the previous question, the proposed Atf4-Ddit3 axis is challenged by the lack of midlobular induction of Atf4 in the APAP scRNA-seq data published by another group, presented in S4F and G. Further analysis of AAV-Atf4 samples generated for F5 could address whether it is really Atf4 that acts on Ddit3 in APAP toxicity.

(6) Related to the previous question, the ATF4 immunostaining in F5A doesn't look convincing, with many brown pigments appearing to be outside of the nucleus.

(7) It is not ruled out that AAV expression of Atf4 or Btg2 reduces hepatocyte sensitivity to APAP by affecting the expression of the Cyps needed for activation. In other words, does AAV-Atf4 or AAV-Btg2 change the expression of any of the Cyps relevant to APAP in the 3 weeks before APAP application (F5B)?

(8) It is laudable that the authors tried to extend their findings to humans by using snRNA-seq data from a published study (line 391), but it is unclear why they didn't analyze all 10 patients in that study but instead focused on 2 and stated that this small sample number prevented drawing definitive conclusions and could therefore only be mentioned in the discussion.

Reviewer #3 (Public review):

Summary:

This paper by Zhu et al explores zonal gene expression changes and stress responses in the liver after APAP injury. 3-6 hours after APAP, zone 2 hepatocytes demonstrate important gene expression changes. There is an increase in stress response/cell survival genes such as Hmox1, Hspa8, Atf3, and protein degradation/autophagy genes such as Ubb, Ubc, and Sqstm1. This is hypothesized to be a "stress adaption" which happens during the initial phases of acute liver injury. Furthermore, there is a spatial redistribution of Cyp450 expression that then establishes the Mid-zone as the primary site of APAP metabolism during early AILI. This particular finding was identified previously by other groups in several single-cell papers. Ddit3 (Chop) expression also increases in zone 2. The authors focused mostly on the Atf4-Ddit3 axis in stress adaptation. Importantly, they probe the functionality of this axis by overexpressing either ATF4 or DDIT3 using AAV tools, and they show that these manipulations block APAP-induced injury and necrosis. This is somewhat convincing evidence that these stress response proteins are probably important during injury and regeneration.

Strengths:

Overall, I think this is a useful study, showing that the Mid-lobular zone 2 hepatocytes turn on a stress-responsive gene program that suppresses proliferation, and that this is functionally important for efficient, long-term regeneration and homeostasis. This adds to the body of literature showing the importance of zone 2 cells in hepatic regeneration, and also provides an additional mechanism that tells us how they are better at surviving chemical injuries.

Weaknesses:

The main concern is that the overexpression of ATF4 and DDIT3 is causing reduced cell death and damage by APAP. This makes it harder to understand if these genes are truly increasing survival or if they are just reducing the injury caused by APAP. It may be better to perform overexpression immediately after, or at the same time as APAP delivery. Alternatively, loss-of-function experiments using AAV-shRNAs against these targets could be useful.

eLife Assessment

This study presents an important finding by identifying OPG as a novel stromal checkpoint influencing T-cell anti-tumor responses, thereby shedding new light on the complex interplay between the tumor microenvironment and immune regulation. The data are robust and the experimental approaches are sound, providing solid support for the study's conclusions; however, there are a number of additional questions raised by the data. Of particular note are the questions raised on the mechanistic effects of TRAIL versus RANKL. In addition, it would broaden the interest in this study to include more translational human data to complement the work presented.

Reviewer #1 (Public review):

Summary:

Wang et al. present a compelling study investigating a novel immunosuppressive mechanism within the tumor microenvironment (TME) mediated by a subset of cancer-associated fibroblasts (CAFs)-specifically, inflammatory CAFs (iCAFs) that secrete osteoprotegerin (OPG). Utilizing both genetic and antibody-mediated OPG inhibition in murine breast and pancreatic cancer models, the authors demonstrate that blocking OPG enhances infiltration and effector function of cytotoxic T cells, which leads to significant tumor regression. Their data further show that OPG blockade induces a population of IFN-licensed CAFs characterized by increased expression of antigen presentation genes and immunomodulatory properties that favour T cell infiltration. The manuscript proposes that OPG functions as a "stromal immune checkpoint" and could represent a promising therapeutic target to convert "cold" tumors into "hot," immunotherapy-responsive tumours.

Strengths:

(1) Novel role for OPG+ CAF as T-cell immune suppressors:<br /> This study introduces a novel role for OPG+ iCAFs as active suppressors of T cell function and highlights stromal OPG as a critical negative regulator of antitumor immunity.

(2) Methodological Rigor:<br /> The manuscript is underpinned by a thorough and systematic experimental design, combining genetic mouse models, antibody interventions, in vitro functional assays, single-cell RNA-seq, and human RAN-seq datasets analyses.

(3) Translational Relevance:<br /> By identifying OPG as a stromal immune checkpoint, the study opens exciting opportunities for developing new immunotherapeutic strategies in stromatogenic tumors.

(4) Clear and Comprehensive Data Presentation:<br /> The use of high-dimensional single-cell technologies and logical, detailed data presentation supports the study's reproducibility and transparency.

Weaknesses:

(1) The manuscript lacks definitive data identifying the cellular origin of OPG, particularly establishing iCAFs as the exclusive functional source.

(2) There is a paucity of translational evidence directly correlating OPG+ iCAFs with T cell exclusion in human tumors.

(3) The scope is limited by the reliance on two murine models, including a subcutaneous pancreatic cancer model, which may not fully recapitulate native tumor microenvironments.

(4) Long-term outcomes and durability of response following OPG blockade, including possible effects on bone homeostasis, are not addressed.

(5) Mechanistic experiments related to the blockade of TRAIL and RANKL remain incomplete, and alternative pathways are not thoroughly explored.

Reviewer #2 (Public review):

Summary:

The work identified a protein called OPD secreted by a particular subtype of cancer-associated fibroblasts and found that it regulated T cell function in the tumor microenvironment. They showed that an antibody that targeted this protein could induce infiltration of immune cells into the tumour and could convert a cold tumor lacking tumour infiltration to a hot tumour with an immune-rich tumour microenvironment. They have supported the conclusion with the data in animal work as well as human tissue data. The authors also stated that it remains unclear whether the IFN-stimulated CAF subset after antibody treatment of OPG is due to reprogramming of existing iCAFs or arises de novo from progenitor populations. Despite their preclinical data suggesting the latter, they rightly suggested that in vivo lineage tracing is needed to further prove the origin and fate of these CAF populations. Overall, this is a well-designed and important study that would benefit from further mechanistic clarification and minor revision.

Strengths:

The strength of their data is that they utilized an immunocompetent orthotopic breast cancer model using the GFP-labelled tumor cell line EO771 in C57BL/6J mice, a well-established model for interrogating the role of stromal-immune interactions in carcinogenesis and tumor growth. They also performed scRNA-seq of the sorted stromal cells of the implanted EO771 cells as well as stromal cells from human esophageal carcinoma using tumor samples and matched adjacent non-malignant tissues from patients.

Weaknesses:

The key mechanistic aspects remain unclear, in particular the relative contributions of the TRAIL versus RANKL pathways to immunosuppression. The dual inhibition of TRAIL and RANKL by OPG is proposed, but the contribution of each axis to immune suppression was not clearly dissected. It would strengthen the paper to evaluate the effects of TRAIL versus RANKL signalling (e.g., with selective ligands or antagonists), which warrants deeper mechanistic exploration. Moreover, while CD4⁺ T cell cytotoxicity was observed, its functional role was underexplored.

eLife Assessment

This useful study attempts to place an ancient maize sample from Bolivia, dated to the end of the Incan empire, in genetic and geographical context. The analyses show that this sample is most closely related to ancient Peruvian maize, but the data remain inadequate to determine the direction of dispersal and the extent of Inca influence over the genetic make up of the analyzed sample. There are additional deficiencies in the statistical analyses and selection inferences. The topic of the study would appeal to researchers studying maize dispersal and adaptation.

Reviewer #1 (Public review):

Summary:

In this manuscript, authors describe a good quality ancient maize genome from 15th century Boliva and try to link the genome characteristics to Inca influence. Overall, the revised manuscript is still below the standard in the field. While dating of the sample and the authentication of ancient DNA has been evidenced robustly, the downstream genetic analyses do not support the conclusion that genomic changes can be attributed to Inca influence. There is more story telling than story testing in this manuscript, analyses are not robust and possibly of very narrow interest.

Strengths:

Technical data related to the maize sample are robust. Radiocarbon dating strongly evidenced sample age, estimated to around 1474 AD. Authentication of ancient DNA has been done robustly. Spontaneous C-to-T substations which are present in all ancient DNA are visible in reported sample with the expected pattern. Despite low fraction of C-to-T at the 1st base, this number could be consistent with cool and dry climate in which the sample was preserved. The distribution of DNA fragment sizes is consistent with expectations for sample of this age.

Weaknesses:

(1) The geographic placement of the sample based on genetic data is not robust. To make use of the method correctly, it would be necessary to validate that genetic samples in this region follow the assumption of the 'isolation-by-distance' with dense sampling, which has not been done. Without this important information, we do not know if genetic similarity is influenced by demographic events and/or selection. The analysis is not a robust evidence of sample connectivity.

(2) The conclusion that Ancient Andean maize is genetically similar to European varieties and hence share similar evolutionary history is not well supported. PCA plot in Fig. 4 merely represents sample similarity based on two components (jointly responsible for about 20% of variation explained). Contrary to authors' conclusion, the direct test of similarity using outgroup f3 statistic does not support that European varieties are particularly closely related to ancient Andean maize. These levels of shared drift could be due ancient Andean maize relationship with other related groups, such as ancient or modern Brazil. A relationship test between multiple populations would be necessary to show significant direct relationship between ancient Andean maize and European maize.

(3) The conclusion that selection detected in aBM sample is due to Inca influence has no support. Firstly, selection signature can be due to environmental or any other factors. To disentangle those, authors would need to generate the data for a large number of samples from similar cultural context and from a wide-ranging environmental context followed by a formal statistical test. Secondly, allele frequency increase can be attributed to selection or demographic processes, and alone is not a sufficient evidence for selection. Presented XP-EHH method seems unsuitable for single individual. Overall, methods used in this paper raise some concerns: i) how accurate are allele-frequency tests of selection when only single individual is used as a proxy for a whole population, ii) the significance threshold has been arbitrary fixed to an absolute number based on other studies, but the standard is to use, for example, top fifth percentile.

In sum, this manuscript presents new data that seem to be of high quality, but the analyses are frequently inappropriate and/or over-interpreted.

Reviewer #2 (Public review):

I am glad to see a revised version of the manuscript. The authors have successfully handled some of my comments, but others require additional attention. In particular, the dataset seems quite robust and valuable to publish, and the descriptive analysis of its position relative to other modern and ancient genomes is generally sound. The selection analyses remain unsupported, and should be removed from the paper. In addition, I agree with the other reviewers and reiterate my comment that the Locator analysis is not robust.

As I said in my original review, the XP-EHH method is not applicable to pseudohaploid variant calls in a single individual. This method is simply not appropriate to apply to the data at hand, as the method relies on knowledge of diploid genotypes, usually phased, and the results from this test are not robust. It is possible that the XP-EHH method could be extended to this data type or genotype likelihoods with extensive validation and conditioning on a large reference panel, but in general haplotype-based approaches have not been extensible to low-coverage pseudohaplotype datasets. At any rate, any off-the-shelf implementation is inappropriate and unsupported. I am sorry to be this negative about this analysis, but it cannot be used as presented, the results from using it in this way would be spurious by definition.

In addition, identifying GO terms without statistical assessment of enrichment is not a robust analysis, nor is selecting genes with a high proportion of rare alleles without extensive additional contextualization based on the expectations of neutrality and deviations potentially tied to selection. For this reason, the two genes linked with height traits have no support here as genuinely being targets of selection. It is a frustrating reality for us in the ancient DNA field that small numbers of highly degraded genomes offer extremely limited scope for selection analyses, but that's the unfortunate state of play, and is the situation here.

My other major critique remains the application of the Locator method. As Reviewer 1 notes, this method must be built on a densely sampled dataset with strong isolation by distance, which is not done here. The authors explained their approach with more detail in their response, but it is fundamentally inappropriate for this dataset. It does not add anything more than the f3 analysis, and creates a falsely precise inference of genetic-geographic origins that is not supported.

Per authors' response to my previous recommendation 6, it is not advisable to re-map the reads after damage masking, and doing this with a conservative hard-masking approach will lead to a high mismatch rate and significant loss of reads in BWA. This could also exacerbate reference sequence bias which is already a major challenge for ancient DNA (see Gunther et al 2019 PLoS Genet). The correct approach is to map reads, mask or rescale for damage, and then proceed with the modified alignment file. In response to Reviewer 3's comment 3, the authors also refer to a "0 mismatch alignment" strategy. This is not concordant with the damage analysis, and if they truly do not allow mismatches this would be very inadvisable, as it would allow an extreme reference sequence bias.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

In this manuscript, the authors describe a good-quality ancient maize genome from 15th-century Bolivia and try to link the genome characteristics to Inca influence. Overall, the manuscript is below the standard in the field. In particular, the geographic origin of the sample and its archaeological context is not well evidenced. While dating of the sample and the authentication of ancient DNA have been evidenced robustly, the downstream genetic analyses do not support the conclusion that genomic changes can be attributed to Inca influence. Furthermore, sections of the manuscript are written incoherently and with logical mistakes. In its current form, this paper is not robust and possibly of very narrow interest. 

Strengths: 

Technical data related to the maize sample are robust. Radiocarbon dating strongly evidenced the sample age, estimated to be around 1474 AD. Authentication of ancient DNA has been done robustly. Spontaneous C-to-T substitutions, which are present in all ancient DNA, are visible in the reported sample with the expected pattern. Despite a low fraction of C-to-T at the 1st base, this number could be consistent with the cool and dry climate in which the sample was preserved. The distribution of DNA fragment sizes is consistent with expectations for a sample of this age. 

Weaknesses: 

Thank you for all your thoughtful comments. See below for comments on each.

(1) Archaeological context for the maize sample is weakly supported by speculation about the origin and has unreasonable claims weighing on it. Perhaps those findings would be more convincing if the authors were to present evidence that supports their conclusions: i) a map of all known tombs near La Paz, ii) evidence supporting the stone tomb origins of this assemblage, and iii) evidence supporting non-Inca provenance of the tomb. 

We believe we are clear about what information we have about context.  First, the intake records from the MSU Museum from 1890 are not as detailed as we would like, but we cannot enhance them. The mummified girl and her accoutrements, including the maize, came from a stone tower or chullpa south of La Paz, in what is now Bolivia. We do not know which stone chullpa, so a map would be of limited use.  The mortuary group is identified as Inca, but as we note the accoutrements do not appear of high status, so it is possible that she is not an elite.  Mud tombs are normally attributed to the local population, and stone towers to Inca or elites. We have clarified at multiple places in the text that the maize is from the period of Inca incursion in this part of Bolivia and have modified text to reflect greater uncertainty of Inca or local origin, but that selection for environmentally favorable characteristics had taken place.  Regardless, there are three 15th c CE or AD AMS ages on the maize, a cucurbita rind, and a camelid fiber.  The maize is almost certainly mid to late 15th century CE.

(2) Dismissal of the admixture in the reported samples is not evidenced correctly. Population f3 statistic with an outgroup is indeed one of the most robust metrics for sample relatedness; however, it should not be used as a test of admixture. For an admixture test, the population f3 statistic should be used in the form: i) target population, ii) one possible parental population, iii) another possible parental population. This is typically done iteratively with all combinations of possible parental populations. Even in such a form, the population f3 statistic is not very sensitive to admixture in cases of strong genetic drift, and instead population f4 statistic (with an outgroup) is a recommended test for admixture. 

We have removed “Our admixture f3-statistics test results suggest aBM is not admixed” in our revised manuscript. Since our goal here is to identify which group(s) has(have) the highest relatedness with aBM, so population f3 statistic with an outgroup is the most robust metric to do the test and to support our conclusion here.

(3) The geographic placement of the sample based on genetic data is not robust. To make use of the method correctly, it would be necessary to validate that genetic samples in this region follow the assumption of the 'isolation-by-distance' with dense sampling, which has not been done. Additionally, the authors posit that "This suggests that aBM might not only be genetically related to the archaeological maize from ancient Peru, but also in the possible geographic location." The method used to infer the location is based on pure genetic estimation. The above conclusion is not supported by this method, and it directly contradicts the authors' suggestion that the sample comes from Bolivia.  

We understood that it is necessary to validate the assumption of the 'isolation-by-distance' with dense sampling. But we did not do it because: 1) the ancient maize age ranges from ~5000BP to ~100BP and they were found in very different countries at different times. 2) isolation-by-distance is a population genetic concept and it's often used to test whether populations that are geographically farther apart are also more genetically different. Considering we only have 17 ancient samples in total our sample size is not sufficient for a big population test.

For "It directly contradicts the authors' suggestion that the sample comes from Bolivia.”, as we described in our manuscript that “Given the provenience of the aBM and its age, it is possible the samples were local or alternatively were introduced into western highland Bolivia from the Inca core area – modern Peru.” The sample recording file did show the aBM sample was found in Bolivia, but we do not know where aBM originally came from before it was found in Bolivia. To answer this question, we used locator.py to predict the potential geographic location that aBM may have originally come from, and our results showed that the predicted location is inside of modern Peru and is also very close to archaeological Peruvian maize.  

Therefore, our conclusion that "This suggests that aBM might not only be genetically related to the archaeological maize from ancient Peru, but also in the possible geographic location” does not contradict that the sample was found Bolivia.

(4) The conclusion that Ancient Andean maize is genetically similar to European varieties and hence shares a similar evolutionary history is not well supported. The PCA plot in Figure 4 merely represents sample similarity based on two components (jointly responsible for about 20% of the variation explained), and European samples could be very distant based on other components. Indeed, the direct test using the outgroup f3 statistic does not support that European varieties are particularly closely related to ancient Andean maize. Perhaps these are more closely related to Brazil? We do not know, as this has not been measured. 

Our conclusion is “We also found that a few types of maize from Europe have a much closer distance to the archaeological maize cluster compared to other modern maize, which indicates maize from Europe might expectedly share certain traits or evolutionary characteristics with ancient maize. It is also consistent with the historical fact that maize spread to Europe after Christopher Columbus's late 15th century voyages to the Americas. But as shown, maize also has diversity inside the European maize cluster. It is possible that European farmers and merchants may have favored different phenotypic traits, and the subsequent spread of specific varieties followed the new global geopolitical maps of the Colonial era”.

We understood your concerns that two components only explain about 20% of the variation. But as you can see from the Figure 2b in Grzybowski, M.W. et al., 2023 publication, it described that “the first principal component (PC1) of variation for genetic marker data roughly corresponded to the division between domesticated maize and maize wild relatives is only 1.3%”. It shows this is quite common in maize, especially when the datasets include landraces, hybrids, and wild relatives. For our maize dataset, we have archaeological maize data ranging from ~5,000BP to ~100BP, and we also have modern maize, which makes the genetic structure of our data more complicated. Therefore, we think our two components are currently the best explanation currently possible. We also included PCA plot based on component 1 and 3 in Fig4_PCA13.pdf. It does not show that the European samples are very distant.

For “Perhaps these are more closely related to Brazil?”, thank you for this very good question, but we apologize that we cannot answer this question from our current study because our study focuses on identifying the location where aBM originally came from, establishing and explaining patterns of genetic variability of maize, with a specific focus on maize strains that are related to our current aBM. Thus, we will not explore the story between maize from Brazil and European maize in our current study.

(5) The conclusion that long branches in the phylogenetic tree are due to selection under local adaptation has no evidence. Long branches could be the result of missing data, nucleotide misincorporations, genetic drift, or simply due to the inability of phylogenetic trees to model complex population-level relationships such as admixture or incomplete lineage sorting. Additionally, captions to Figure S3, do not explain colour-coding.  

We have removed “aBM tends to have long branches compare to tropicalis maize, which can be explained by adaption for specific local environment by time.” in our revised manuscript.

We have added the color-coding information under Fig. S3 in our revised manuscript.

(6) The conclusion that selection detected in aBM sample is due to Inca influence has no support. Firstly, selection signature can be due to environmental or other factors. To disentangle those, the authors would need to generate the data for a large number of samples from similar cultural contexts and from a wide-ranging environmental context, followed by a formal statistical test. Secondly, allele frequency increase can be attributed to selection or demographic processes, and alone is not sufficient evidence for selection. The presented XP-EHH method seems more suitable. Overall, methods used in this paper raise some concerns: i) how accurate are allele-frequency tests of selection when only single individual is used as a proxy for a whole population, ii) the significance threshold has been arbitrary fixed to an absolute number based on other studies, but the standard is to use, for example, top fifth percentile. Finally, linking selection to particular GO terms is not strong evidence, as correlation does not imply causation, and links are unclear anyway. 

In sum, this manuscript presents new data that seems to be of high quality, but the analyses are frequently inappropriate and/or over-interpreted. 

Regarding your suggestion that “from similar cultural contexts and from a wide-ranging environmental context, followed by a formal statistical test”, we apologize that this cannot be done in our current study because we could not find other archaeological maize samples/datasets that are from similar cultural contexts.

For “Secondly, allele frequency increase can be attributed to selection or demographic processes, and alone is not sufficient evidence for selection.” Yes, we agree, and that’s why we said it “inferred” the conclusion instead of “indicated”. Furthermore, we revised the whole manuscript following all reviewers’ comments and reorganized and reduced the part on selection on aBM.

For “The presented XP-EHH method seems more suitable”, we do not think XP-EHH is the best method that could be used here because we only have one aBM sample, but XP-EHH is more suitable for a population analysis.

For “Finally, linking selection to particular GO terms is not strong evidence, as correlation does not imply causation, and links are unclear anyway.”, as we described in our manuscript, our results “inferred” instead of “indicated” the conclusion.

Reviewer #2 (Public review): 

Summary: 

The manuscript presents valuable new datasets from two ancient maize seeds that contribute to our growing understanding of the maize evolution and biodiversity landscape in pre-colonial South America. Some of the analyses are robust, but the selection elements are not supported. 

Strengths: 

The data collection is robust, and the data appear to be of sufficiently high quality to carry out some interesting analytical procedures. The central finding that aBM maize is closely related to maize from the core Inca region is well supported, although the directionality of dispersal is not supported. 

Weaknesses: 

Thank you for your comments and suggestions. See below for responses and explanations.

The selection results are not justified, see examples in the detailed comments below. 

(1) The manuscript mentions cultural and natural selection (line 76), but then only gives a couple of examples of selecting for culinary/use traits. There are many examples of selection to tolerate diverse environments that could be relevant for this discussion, if desired. 

We have added related examples with references supported in our revised manuscript.  

(2) I would be extremely cautious about interpreting the observations of a Spanish colonizer (lines 95-99) without very significant caveats. Indigenous agriculture and food ways would have been far more nuanced than what could be captured in this context, and the genocidal activities of the Europeans would have impacted food production activities to a degree, and any contemporaneous accounts need to be understood through that lens.  

We agree with the first part of this comment and have softened our use of this particular textual material such that it is far less central to interpretation.While of interest, we cannot evaluate the impact of colonial European activities or observational bias for purposes of this analysis.

(3) The f3 stats presented in Figure 2 are not set up to test any specific admixture scenarios, so it is unsupported to conclude that the aBM maize is not admixed on this basis (lines 201-202). The original f3 publication (Patterson et al, 2012) describes some scenarios where f3 characteristics associate with admixture, but in general, there are many caveats to this approach, and it's not the ideal tool for admixture testing, compared with e.g., f4 and D (abba-baba) statistics.  

You make an important point that f3 stats is not the ideal tool for admixture testing. Since our study goal here is to identify which group(s) has(have) the highest relatedness with aBM, the population f3 statistic with an outgroup is the most robust metrics with which to do the test and to support our conclusion here. We have removed the “Our admixture f3-statistics test results suggest aBM is not admixed” in our revised manuscript.

(4) I'm a little bit skeptical that the Locator method adds value here, given the small training sample size and the wide geographic spread and genetic diversity of the ancient samples that include Central America. The paper describing that method (Battey et al 2020 eLife) uses much larger datasets, and while the authors do not specifically advise on sample sizes, they caution about small sample size issues. We have already seen that the ancient Peruvian maize has the most shared drift with aBM maize on the basis of the f3 stats, and the Locator analysis seems to just be reiterating that. I would advise against putting any additional weight on the Locator results as far as geographic origins, and personally I would skip this analysis in this case.  

As we described in our manuscript, we have 17 archaeological samples in total. Please find more detailed information from the “geographical location prediction” section.

We cannot add more ancient samples because they are all that we could find from all previous publications. We may still want to keep this analysis because f3 stats indicates the genome similarity, but the purpose of locator.py analysis is indicating the predicted location of origin of a genetic sample by comparing it to a set of samples of known geographic origin. 

(5) The overlap in PCA should not be used to confirm that aBM is authentically ancient, because with proper data handling, PCA placement should be agnostic to modern/ancient status (see lines 224-226). It is somewhat unexpected that the ancient Tehuacan maize (with a major teosinte genomic component) falls near the ancient South American maize, but this could be an artifact of sampling throughout the PCA and the lack of teosinte samples that might attract that individual.  

We have removed “which supports the authenticity of aBM as archaeological maize” in our revised manuscript. The PCA was only applied for all maize samples, so we did not include any teosinte samples in the analysis.

(6) What has been established (lines 250-251) is genetic similarity to the Inca core area, not necessarily the directionality. Might aBM have been part of a cultural region supplying maize to the Inca core region, for example? Without a specific test of dispersal directionality, which I don't think is possible with the data at hand, this is somewhat speculative. 

We added this and re-wrote this part in our revised manuscript.

(7) Singleton SNPs are not a typical criterion for identifying selection; this method needs some citations supporting the exact approach and validation against neutral expectations (line 278). Without Datasets S2 and S3, which are not included with this submission, it is difficult to assess this result further. However, it is very unexpected that ~18,000 out of ~49,000 SNPs would be unique to the aBM lineage. This most likely reflects some data artifact (unaccounted damage, paralogs not treated for high coverage, which are extremely prevalent in maize, etc). I'm confused about unique SNPs in this context. How can they be unique to the aBM lineage if the SNPs used overlap the Grzybowski set? The GO results do not include any details of the exact method used or a statistical assessment of the results. It is not clear if the GO terms noted are statistically enriched.  

We have added references 53 and 54 in our revised manuscript, and we also uploaded the Datasets S2 and S3.

For “I'm confused about unique SNPs in this context. How can they be unique to the aBM lineage if the SNPs used overlap the Grzybowski set?”, as we described in our materials and method part that “To achieve potential unique selection on aBM, we calculated the allele frequency for each SNPs between aBM and other archaeological maize, resulting in allele frequency data for 49,896 SNPs. Of these,18,668 SNPs were unique to aBM.”  Thus, the unique SNPs for aBM came from the comparison between aBM with other archaeological maize, and we did not use any modern maize data from the Grzybowski set.

For “The GO results do not include any details of the exact method used or a statistical assessment of the results. It is not clear if the GO terms noted are statistically enriched.” We did not do GO Term enrichment, so there are no statistical assessments for the results. What we have done was we retained the GO Terms information for each gene by checking their biological process from MaizeGDB, after that, we summarized the results in Dataset S4.

(8) The use of XP-EHH with pseudo haplotype variant calls is not viable (line 293). It is not clear what exact implementation of XP-EHH was used, but this method generally relies on phased or sometimes unphased diploid genotype calls to observe shared haplotypes, and some minimum population size to derive statistical power. No implementation of XP-EHH to my knowledge is appropriate for application to this kind of dataset. 

We used the same XP-EHH as this publication “Sabeti, P.C. et al. Genome-wide detection and characterization of positive selection in human populations. Nature 449, 913-918 (2007).” Specifically in our analysis, the SNP information of modern maize was compared with ancient maize. The code is available in https://doi.org/10.5061/dryad.w6m905qtd.

XP-EHH is a statistical method used in population genetics to detect recent positive selection in one population compared to another, and it often applied in modern large maize populations in previous research. In our study, we wanted to detect recent positive selection in modern maize compared to ancient maize, thus, we applied XP-EHH here. Although the population size of ancient maize is not big, it is the best method that we can apply for our dataset here to detect recent selection on modern maize.

Reviewer #3 (Public review): 

Summary: 

The authors seek to place archaeological maize samples (2 kernels) from Bolivia into genetic and geographical context and to assess signatures of selection. The kernels were dated to the end of the Incan empire, just prior to European colonization. Genetic data and analyses were used to characterize the distance from other ancient and modern maize samples and to predict the origin of the sample, which was discovered in a tomb near La Paz, Bolivia. Given the conquest of this region by the Incan empire, it is possible that the sample could be genetically similar to populations of maize in Peru, the center of the Incan empire. Signatures of selection in the sample could help reveal various environmental variables and cultural preferences that shaped maize genetic diversity in this region at that time. 

Strengths: 

The authors have generated substantial genetic data from these archaeological samples and have assembled a data set of published archaeological and modern maize samples that should help to place these samples in context. The samples are dated to an interesting time in the history of South America during a period of expansion of the Incan empire and just prior to European colonization. Much could be learned from even this small set of samples. 

Weaknesses: 

Many thanks for your comments and suggestions.  We have addressed these below and provided further explanation.

(1) Sample preparation and sequencing: 

Details of the quality of the samples, including the percentage of endogenous DNA are missing from the methods. The low percentage of mapped reads suggests endogenous DNA was low, and this would be useful to characterize more fully. Morphological assessment of the samples and comparison to morphological data from other maize varieties is also missing. It appears that the two kernels were ground separately and that DNA was isolated separately, but data were ultimately pooled across these genetically distinct individuals for analysis. Pooling would violate assumptions of downstream analysis, which included genetic comparison to single archaeological and modern individuals. 

We did not do the morphological assessment of the samples and comparison to morphological data from other maize varieties because we only have 2 aBM kernels, and we do not have other archaeological samples that could be used to do comparison.

For “It appears that the two kernels were ground separately and that DNA was isolated separately, but data were ultimately pooled across these genetically distinct individuals for analysis”, as you can see from our Materials and Methods section that “Whole kernels were crushed in a mortar and pestle”, these two kernels were ground together before sequenced. 

While morphological assessment of the sample would be interesting, most morphological data reported for maize are from microremains (starch, phytoliths, pollen) and this is beyond the scope of our study. Most studies of macrobotanical remains do not appear to focus solely on individual kernels, but instead on (or in combination with) cob and ear shape, which were not available in the assemblage.

(2) Genetic comparison to other samples: 

The authors did not meaningfully address the varying ages of the other archaeological samples and modern maize when comparing the genetic distance of their samples. The archaeological samples were as old as >5000 BP to as young as 70 BP and therefore have experienced varying extents of genetic drift from ancestral allele frequencies. For this reason, age should explicitly be included in their analysis of genetic relatedness. 

We have changed related part in our revised manuscript.

(3) Assessment of selection in their ancient Bolivian sample: 

This analysis relied on the identification of alleles that were unique to the ancient sample and inferred selection based on a large number of unique SNPs in two genes related to internode length. This could be a technical artifact due to poor alignment of sequence data, evidence supporting pseudogenization, or within an expected range of genetic differentiation based on population structure and the age of the samples. More rigor is needed to indicate that these genetic patterns are consistent with selection. This analysis may also be affected by the pooling of the Bolivian archaeological samples.  

We do not think it is because of poor alignment of sequence data since we used BWA v0.7.17 with disabled seed (-l 1024) and 0 mismatch alignment. Therefore, there are no SNPs that could come from poor alignment. Please see our detailed methods description here “For the archaeological maize samples, adapters were removed and paired reads were merged using AdapterRemoval60 with parameters --minquality 20 --minlength 30. All 5՛ thymine and 3՛ adenine residues within 5nt of the two ends were hard-masked, where deamination was most concentrated. Reads were then mapped to soft-masked B73 v5 reference genome using BWA v0.7.17 with disabled seed (-l 1024 -o 0 -E 3) and a quality control threshold (-q 20) based on the recommended parameter61 to improve ancient DNA mapping”.

For “More rigor is needed to indicate that these genetic patterns are consistent with selection”, Could you please be more specific about which method or approach we should use here? For example, methods from specific publications that could be referenced? Or which specific tool could be used?

“This analysis may also be affected by the pooling of the Bolivian archaeological samples.” As we could not prove these two seeds came from two different individual plants, we do not think this analysis was affected by the pooling of the Bolivian archaeological samples.

(4) Evidence of selection in modern vs. ancient maize: In this analysis, samples were pooled into modern and ancient samples and compared using the XP-EHH statistic. One gene related to ovule development was identified as being targeted by selection, likely during modern improvement. Once again, ancient samples span many millennia and both South, Central, and North America. These, and the modern samples included, do not represent meaningfully cohesive populations, likely explaining the extremely small number of loci differentiating the groups. This analysis is also complicated by the pooling of the Bolivian archaeological samples. 

Yes, it is possible that ovule development might be a modern improvement. We re-wrote this part in our revised manuscript.

Reviewer #1 (Recommendations for the authors): 

My suggestion is to address the comments that outline why the methods used or results obtained are not sufficient to support your conclusions. Overall, I suggest limiting the narrative of Inca influence and framing it as speculation in the discussion section. Presenting conclusions of Inca influence in the title and abstract is not appropriate, given the very questionable evidence. 

We agree and have changed the title to “Fifteenth century CE Bolivian maize reveals genetic affinities with ancient Peruvian maize”.

Reviewer #2 (Recommendations for the authors): 

(1) Line 74: Mexicana is another subspecies of teosinte; the distinction is between ssp. mexicana and ssp. parviglumis (Balsas teosinte), not mexicana and teosinte. 

We have corrected this in our revised manuscript.

(2) Line 100-102: This is a bit confusing, it cannot have been a symbol of empire "since its first introduction", since its introduction long predates the formation of imperial politics in the region. Reference 17 only treats the late precolonial Inca context, while ref 22 (which cites maize cultivation at 2450 BC, not 3000 BC) makes no reference to ritual/feasting contexts; it simply documents early phytolith evidence for maize cultivation. As such, this statement is not supported by the references offered.

lines 100-102. This point is well taken and was poor prose on our part.  We have modified this discussion to reflect both the confusing statement and we have corrected our mistake in age for reference 22. associated prose has been modified accordingly.

We have corrected them as “Indeed, in the Andes, previous research showed that under the Inca empire, maize was fulfilled multiple contextual roles. In some cases, it operated as a sacred crop” and “…since its first introduction to the region around 2500 BC”.

(3) Line 161: IntCal is likely not the appropriate calibration curve for this region; dates should probably be calibrated using SHCal.  

We greatly appreciate this important (and correct) observation. We have completely recalibrated the maize AMS result based on the southern hemisphere calibration curve, discussed the new calibrations, and have also invoked two other AMS dates also subjected to the southern hemisphere calibration on associated material for comparison.We are confident in a 15th century AD/CE age for the maize, most likely mid- to late 15th century.  

(4) Lines 167-169: The increase of G and A residues shown in Supplementary Figure S1a is just before the 5' end of the read within the reference genome context, and is related to fragmentation bias - a different process from postmortem deamination. Deamination leads to 5' C->T and 3' G->A, resulting in increased T at 5' ends and increased A at 3' ends, and the diagnostic damage curve. The reduction of C/T just before reads begin is not a result of deamination. 

We have removed the “Both features are indicative of postmortem deamination patterns” in our revised manuscript.

(5) Lines 187-196 This section presents a lot of important external information establishing hypotheses, and needs some references.  

We have added the related references here.

(6) Line 421: This makes it sound like damage masking was done BEFORE read mapping. However, this conflicts with the previous paragraph about map Damage, and Supplementary Figure 1 still shows a slight but perceptible damage curve, which is impossible if all terminal Ts and As are hard-masked. This should be reconciled.  

The Supplementary Figure 1 shows the raw ancient maize DNA sample before damage masking. Specifically, Step1: We used map Damage to check/estimate if the damage exists, and we made the Supplementary Figure 1. Step 2: Then we used our own code hard-masked the damage bases and did read mapping.

The purpose of Supplementary Figure 1 is to show the authenticity of aBM as archaeological maize. Therefore, it should show a slight but perceptible damage curve.

(7) Line 460: PCA method is not given (just the LD pruning and the plotting).  

The merged dataset of SNPs for archaeological and modern maize was used for PCA analysis by using “plink –pca”.

(8) "tropicalis" maize is not common usage, it is not clear to me what this refers to. 

We have changed all “tropicalis maize” as “tropical maize” in our revised manuscript.

(9) The Figure 4 color palette is not accessible for colorblind/color-deficient vision.  

We have changed the color of Figure 4. Please find the new colors in our upload Figure 4.

(10) Datasets S2 and S3 are not included with this submission. 

Thank you for letting us know and your suggestion. We have included Datasets S2 and S3 here.

eLife Assessment

This study presents a meta-analysis of two independent genome-wide association studies (GWAS) that investigate the role of plasma proteins as potential biomarkers for enhancing the early detection of prostate cancer (PCa). The results provide useful confirmatory data that support existing evidence currently published. The evidence is incomplete: the study does not provide a comprehensive synthesis of all currently published work, does not explore other clinical outcomes related to prostatic disease, and its findings have not been validated through an external cohort study. These shortcomings notwithstanding, the work may be of interest to researchers studying correlates and predictors of prostate cancer risk.

Reviewer #1 (Public review):

Summary:

In Causal associations between plasma proteins and prostate cancer: a Proteome-Wide Mendelian Randomization the authors present a manuscript which seeks to identify novel markers for prostate cancer through analysis of large biobank-based datasets, and to extend this analysis to potential therapeutic targets for drugs. This is an area which is already extensively researched, but remains important, due to the high burden and mortality of prostate cancer globally.

Strengths:

The main strengths of the manuscript are the identification and use of large biobank data assets, which provide large numbers of cases and controls, essential for achieving statistical power. The databases used (deCODE, FinnGen and the UK Biobank) allow for robust numbers of cases and controls. The analytical method chosen, Mendelian Randomization, however, may not be appropriate to the problem (without extensive validation, MR can be prone to false or misleading discoveries). The manuscript also integrates multi-omic datasets, here using protein data as well as GWAS sources to integrate genomic and proteomic data.

Weaknesses:

The main weaknesses of the manuscript relate to the following areas:

(1) The failure of the study to analyse the data in the context of other closely related conditions such as benign prostatic hyperplasia (BPH) or lower urinary tract symptoms (LUTS), which have some pathways and biomarkers in common, such as inflammatory pathways (including complement) and specific markers such as KLK3. As a consequence, it is not possible for readers to know whether the findings are specific to prostate cancer, or whether they are generic to prostate dysfunction. Given the prevalence of prostate dysfunction (half of men reaching their sixth decade), the potential for false positives and overtreatment from non-specific biomarkers is a major problem, resulting in the evidence presented in this manuscript being weak. Other researchers have addressed this issue using the same data sources as presented here, for example in this paper looking at BPH in the UK Biobank population.<br /> https://www.nature.com/articles/s41467-018-06920-9

(2) There is no discussion of Gleason scores with regard to either biomarkers or therapies, and a general lack of discussion around indolent disease as compared with more aggressive variants. These are crucial issues with regard to the triage and identification of genomically aggressive localized prostate cancers. See for example the work set out in: https://doi.org/10.1038/nature20788. In the revised version of the manuscript the authors set this out as a limitation, but this does not solve the core problem, which is that without this important biological context, the findings are unlikely to be robust.

(3) An additional issue is that the field of PCa research is fast-moving. The manuscript cites ~80 references, but too few of these are from recent studies and many important and relevant papers are not included. The manuscript would be much stronger if it compared and contrasted its findings with more recent studies of PCa biomarkers and targets, especially those concerned with multi-omics and those including BPH. In the latest revised version of the manuscript, some changes have been made, but the source data are still too limited for in-depth analysis.

(4) The Methods section provides no information on how the Controls were selected. There is no Table providing cohort data to allow the reader to know whether there were differences in age, BMI, ethnic grouping, social status or deprivation, or smoking status, between the Cases and Controls. These types of data are generally recorded in Biobank data; in the latest version of the manuscript the authors state that they don't have any ability to derive matched data, which again prevents deep analysis of the data.

Assessing impact:

Because of the weaknesses of the approach identified above, without further additions to the manuscript, the likely impact of the work on the field is minimal. There is no significant utility of the methods and data to the community, because the data are pre-existing and are not newly introduced to the community in this work, and mendelian randomization is a well-described approach in common use, and therefore the assets and methods described in the manuscript are not novel. In addition, Mendelian randomization is not always appropriate, especially when analysing publicly available data, see:

Stender et al. Lipids in Health and Disease (2024) 23:286<br /> https://doi.org/10.1186/s12944-024-02284-w

With regard to the authors achieving their aims, without assessing specificity and without setting their findings in the context of the latest literature, the authors (and readers) cannot know or assess whether the biomarkers identified or the druggable targets will be useful in the clinic.

In conclusion, adding additional context and analysis to the manuscript would both help readers interpret and understand the work, and would also greatly enhance its significance. For example, the UK Biobank includes data on men with BPH / LUTS, as analysed in this paper, for example, https://doi.org/10.1038/s41467-018-06920-9. In the latest version of the manuscript and through the responses to earlier review comments, the authors explain why this has not been possible, but this naturally limits the value of the research.

Reviewer #2 (Public review):

This is potentially interesting work, but the analyses are attempted in a rather scattergun way, with little evident critical thought. The structure of the work (Results before Methods) can work in some manuscripts, but it is not ideal here. The authors discuss results before we know anything about the underlying data that the results come from. It gives the impression that the authors regard data as a resource to be exploited, without really caring where the data comes from. The methods can provide meaningful insights if correctly used, but while I don't have reasons to doubt that the analyses were conducted correctly, findings are presented with little discussion or interpretation. No follow-up analyses are performed.

This is much improved but there remain some small concerns and one large concern:

Using numbering from the previous review:

(1) This looks better, but I still don't understand the claim in the text: "We found 5 genetic risk loci contained at least one SNP passing the genome-wide significance threshold of P {less than or equal to} 5×10−8". Far more gene regions appear to cross 10^-8 in Figure 1. What am I missing?

(6) I don't understand the authors' response here. Early detection is important, but MR is not the right tool to investigate biomarkers for early detection. Biomarkers for early detection do not have to be causal biomarkers. The authors replied to this point, but the manuscript was unchanged.

(7) Again, the authors still state "193 proteins were associated with PCa risk" even though they acknowledge that their analysis does not test whether proteins associate with PCa risk or not. When an error is pointed out, and you acknowledge it, please change the manuscript to correct the text. Otherwise, what is the peer review process for?

The large concern is that these analyses, while now better explained, are still the product of a semi-automated procedure. It is a good procedure, but the manuscript essentially takes public data from different sources and uses this to create a manuscript. Overall, I think there is enough novel synthesis to justify publication, but it is not automatic.

Strengths:

The data and methods used are state-of-the-art.

Weaknesses:

The reader will have to provide their own translational insight.

Reviewer #3 (Public review):

Summary of concerns about the revised submission from the Reviewing Editor:

With respect to Originality of the work, in the last 18 months, there have been 38 publications on combined topics of: (i) UK Biobank data, (ii) Mendelian randomization, (iii) and prostate cancer. The authors should consider the literature addressing prostate cancer via Mendelian randomization--specifically those using the UK Biobank data--published from 2024 onwards. A proper and comprehensive synthesis of recent findings should be made, to allow readers to compare and contrast how the work supports (or differs) from the findings presented in these other published studies.

With respect to the significance of the findings, we feel the study data are incomplete for the strength of evidence. Given the deluge of manuscripts and publications on similar topics, the study offers incremental evidence and lacks a synthesis of all currently published findings.

Author response:

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

Reviewer #1 (Public review):

Summary:

In Causal associations between plasma proteins and prostate cancer: a Proteome-Wide Mendelian Randomization, the authors present a manuscript which seeks to identify novel markers for prostate cancer through analysis of large biobank-based datasets and to extend this analysis to potential therapeutic targets for drugs. This is an area that is already extensively researched, but remains important, due to the high burden and mortality of prostate cancer globally.

Strengths:

The main strengths of the manuscript are the identification and use of large biobank data assets, which provide large numbers of cases and controls, essential for achieving statistical power. The databases used (deCODE, FinnGen, and the UK Biobank) allow for robust numbers of cases and controls. The analytical method chosen, Mendelian Randomization, is appropriate to the problem. Another strength is the integration of multi-omic datasets, here using protein data as well as GWAS sources to integrate genomic and proteomic data.

Thank you for your positive feedback regarding the overall quality of our work and we greatly appreciate you taking time and making effort in reviewing our manuscript.

Weaknesses:

The main weaknesses of the manuscript relate to the following areas:

(1) The failure of the study to analyse the data in the context of other closely related conditions such as benign prostatic hyperplasia (BPH) or lower urinary tract symptoms (LUTS), which have some pathways and biomarkers in common, such as inflammatory pathways (including complement) and specific markers such as KLK3. As a consequence, it is not possible for readers to know whether the findings are specific to prostate cancer or whether they are generic to prostate dysfunction. Given the prevalence of prostate dysfunction (half of men reaching their sixth decade), the potential for false positives and overtreatment from non-specific biomarkers is a major problem, resulting in the evidence presented in this manuscript being weak. Other researchers have addressed this issue using the same data sources as presented here, for example, in this paper, looking at BPH in the UK Biobank population. https://www.nature.com/articles/s41467-018-06920-9

Thank you for your valuable comment. We fully agree that biomarker development must prioritize specificity to avoid overtreatment. While our study is a foundational step toward identifying potential therapeutic targets or complementary biomarkers for prostate cancer—not as a direct endorsement of these proteins for standalone clinical diagnosis. Mendelian randomization analysis strengthens causal inference by design, and we further ensured robustness through sensitivity analyses (e.g., MR-Egger regression for pleiotropy, Bonferroni correction for multiple testing). These methods distinguish true causal effects from nonspecific associations. Importantly, while PSA’s lack of specificity is widely recognized, its role in reducing PCa mortality underscores the value of biomarker-driven screening. Our findings align with the need to integrate multiple markers (e.g. combining a novel protein with PSA) to improve diagnostic precision. Translating these causal insights into clinical tools remains challenging but represents a necessary next step, and we emphasize that this work provides a rigorous starting point for future validation studies.

(2) There is no discussion of Gleason scores with regard to either biomarkers or therapies, and a general lack of discussion around indolent disease as compared with more aggressive variants. These are crucial issues with regard to the triage and identification of genomically aggressive localized prostate cancers. See, for example, the work set out in: https://doi.org/10.1038/nature20788

Thank you for pointing this out. We acknowledge that our original analysis did not directly address this critical issue due to a key data limitation: the publicly available GWAS summary statistics for PCa (from openGWAS and FinnGen) do not provide genetic associations stratified by phenotypic severity or molecular subtypes. This limitation precluded MR analysis of proteins specifically linked to aggressive disease. To partially bridge this gap, we integrate evidence from recent studies in the revised Discussion section to explore the relevance of potential biomarkers to aggressive PCa.

(3) An additional issue is that the field of PCa research is fast-moving. The manuscript cites ~80 references, but too few of these are from recent studies, and many important and relevant papers are not included. The manuscript would be much stronger if it compared and contrasted its findings with more recent studies of PCa biomarkers and targets, especially those concerned with multi-omics and those including BPH.

Thank you for your professional comments. We have rigorously updated the manuscript to include more recent publications and we systematically compare and contrast our findings with these recent studies in the revised Discussion section.

(4) The Methods section provides no information on how the Controls were selected. There is no Table providing cohort data to allow the reader to know whether there were differences in age, BMI, ethnic grouping, social status or deprivation, or smoking status, between the Cases and Controls. These types of data are generally recorded in Biobank data, so this sort of analysis should be possible, or if not, the authors' inability to construct an appropriately matched set of Controls should be discussed as a Limitation.

We thank the reviewer for raising this important methodological concern. We have expanded the Limitations section to state it.

“Lastly, our analysis relied exclusively on publicly available GWAS summary statistics from openGWAS and FinnGen, which did not provide individual-level data on covariates, resulting in no direct assessment of demographic or clinical differences between cases and controls.”

Reviewer #2 (Public review):

This is potentially interesting work, but the analyses are attempted in a rather scattergun way, with little evident critical thought. The structure of the work (Results before Methods) can work in some manuscripts, but it is not ideal here. The authors discuss results before we know anything about the underlying data that the results come from. It gives the impression that the authors regard data as a resource to be exploited, without really caring where the data comes from. The methods can provide meaningful insights if correctly used, but while I don't have reasons to doubt that the analyses were conducted correctly, findings are presented with little discussion or interpretation. No follow-up analyses are performed.

In summary, there are likely some gems here, but the whole manuscript is essentially the output from an analytic pipeline.

We thank the reviewer for the thoughtful evaluation of our work. In response to the concerns regarding manuscript structure and interpretative depth, we have restructured the manuscript to present the Methods section before Results, ensuring transparency in data sources and analytical workflows. Additionally, the Discussion section has been substantially revised to provide mechanistic explanations for key findings (e.g., associated phenotype, causal proteins, druggable targets), contextualize results within recent multi-omics studies and highlight clinical implications.  These revisions aim to transform the work from a pipeline-driven analysis to a biologically grounded investigation, offering actionable insights into prostate cancer pathogenesis and therapeutic development.

Taking the researchers aims in turn:

(1) Meta-GWAS - while combining two datasets together can provide additional insights, the contribution of this analysis above existing GWAS is not clear. The PRACTICAL consortium has already reported the GWAS of 70% of these data. What additional value does this analysis provide? (Likely some, but it's not clear from the text.) Also, the presentation of results is unclear - authors state that only 5 gene regions contained variants at p<5x10-8, but Figure 1 shows dozens of hits above 5x10-8. Also, the red line in Figure 1 (supposedly at 5x10-8) is misplaced.

Thank you very much for your feedback. Although the PRACTICAL consortium constituted the majority of PCa GWAS data, our meta-analysis integrating FinnGen data enhanced statistical power enabling robust detection of low-frequency variants with minor allele frequencies. Moreover, FinnGen's Finnish ancestry (genetic isolate) helps distinguish population-specific effects. The presentation of results showed the top 5 gene regions contained variants at p < 5×10⁻⁸. We apologize for not noticing that the red line was not displayed correctly in the original figures included in the manuscript. We have updated it in the revised manuscript.

(2) Cross-phenotype analysis. It is not really clear what this analysis is, or why it is done. What is the iCPAGdb? A database? A statistical method? Why would we want to know cross-phenotype associations? What even are these? It seems that the authors have taken data from an online resource and have written a paragraph based on this existing data with little added value.

We appreciate the opportunity to clarify this analysis. The cross-phenotype analysis was designed to systematically identify phenotypic traits that share genetic or molecular pathways with prostate cancer, thereby uncovering pleiotropic mechanisms or shared risk factors. Here, iCPAGdb (integrated Cross-Phenotype Association Genetics Database) is a curated repository that aggregates GWAS summary statistics and evaluates genetic pleiotropy using LD-proxy associations from the NHGRI-EBI GWAS Catalog. Prostate carcinogenesis involves multisystem interactions, including spanning endocrine dysregulation, immune microenvironment remodeling and metabolic reprogramming, rather than isolated molecular pathway disruptions. Therefore, it is indispensable for discriminating primary pathogenic drivers from secondary compensatory responses, ultimately informing the development of precision therapeutic strategies. 

In response to your concerns, we have revised the Results section to explicitly define the rationale and methodology of cross-phenotype analysis and restructured the Discussion to interpret phenotype-PCa associations within unified biological frameworks (e.g., metabolic dysregulation, androgen signaling), rather than presenting them as isolated findings.

(3) PW-MR. I can see the value of this work, but many details are unclear. Was this a two-sample MR using PRACTICAL + FinnGen data for the outcome? How many variants were used in key analyses? Again, the description of results is sparse and gives little added value.

We thank you for raising this issue. Two-sample MR refers to an analytical design where genetic instruments for the exposure (plasma proteins) and genetic associations with the outcome (PCa) are derived from non-overlapping populations. This ensures complete sample independence between exposure and outcome datasets to avoid confounding biases, regardless of whether the outcome data originate from single or multiple cohorts. The meta-analysis of PRACTICAL and FinnGen GWAS generates 27,210 quality-controlled variants (p < 5×10⁻⁸, MAF ≥ 1%, LD-clumped r² < 0.1) used in key analyses. Regarding the concern about sparse interpretation, we have substantially expanded the Discussion by comparing significant protein findings (e.g., MSMB, SERPINA3) with results from existing functional studies and multi-omics datasets and unravelling new insights.

(4) Colocalization - seems clear to me.

(5) Additional post-GWAS analyses (pathway + druggability) - again, the analyses seem to be performed appropriately, although little additional insight other than the reporting of output from the methods.

The post-MR druggability and pathway analyses serve two primary scientific purposes: (1) therapeutic prioritization - systematically evaluating which MR-identified proteins represent tractable drug targets (either through existing FDA-approved agents or compounds in clinical development) with direct relevance to cancer or PCa management, and (2) mechanistic hypothesis generation - mapping these candidate proteins to coherent biological pathways to guide future functional validation studies investigating their causal roles in prostate carcinogenesis. In response to your feedback, we have restructured the Discussion section under the subheading “Biological Mechanisms and Druggable Targets” to synthesize these findings, explicitly linking biological pathway to therapeutic targets.

Minor points:

(6) The stated motivation for this work is "early detection". But causality isn't necessary for early detection. If the authors are interested in early detection, other analysis approaches are more appropriate.

We appreciate your insightful feedback. Early detection is one motivation for this work, meanwhile, our goal is also to identify causally implicated proteins that may serve as intervention targets for PCa prevention or therapy.  Establishing causality is critical for distinguishing biomarkers that drive disease pathogenesis from those that are secondary to disease progression, as the former holds greater specificity for early detection and prioritization of therapeutic targets. While we acknowledge that validation for early detection may require additional methodologies, MR analysis provides a foundational step by prioritizing candidate proteins with causal links to disease. This approach ensures that downstream efforts focus on biomarkers and targets with the greatest potential to alter disease trajectories, rather than merely correlative markers.

(7) The authors state "193 proteins were associated with PCa risk", but they are looking at MR results - these analyses test for disease associations of genetically-predicted levels of proteins, not proteins themselves.

True, in MR, the exposure of interest is the lifelong effect of genetically predicted protein levels. This approach is designed to infer causality while avoiding confounding and reverse causation, as genetic variants are fixed at conception and unaffected by disease processes. When we state “193 proteins were associated with PCa risk,” we specifically refer to proteins whose genetically predicted levels (based on instrument SNPs from protein QTLs) show causal links to PCa. Importantly, MR does not measure the direct association between observed protein concentrations and disease. Instead, it estimates the lifelong causal effect of protein levels predicted by genetics. This distinction is critical for disentangling cause from consequence. For example, a protein elevated due to tumor progression would not be identified as causal in MR if its genetic predictors are unrelated to PCa risk.

We acknowledge that clinical translation requires further validation of these proteins in observational studies measuring actual protein levels. However, MR provides a robust first step by prioritizing candidates with causal roles, thereby reducing the risk of investing in biomarkers confounded by disease processes.

Reviewer #1 (Recommendations for the authors):

As outlined above, the major weakness of the manuscript is its failure to consider BPH / LUTS, and whether the markers and targets are specific to PCa or not. Specific improvements that the authors could consider might include a literature review of the features identified for their 20 high-risk proteins, and ideally also analyze whether these proteins are upregulated or downregulated in the databases they have analysed (for example it will be easy to analyze whether these proteins are dysregulated in BPH patients as these are specifically identified in the UK Biobank).

The authors may be able to gain context for this approach by looking at papers analyzing BPH and the complement cascade and other proteins from the authors' top 10 or top 20, for example: https://doi.org/10.1002/pros.24639IF: 2.6 Q2

Other sources can be identified by examining the literature for recent omics papers analysing BPH, especially those that analyse and compare BPH / PCa specifically.

Thank you for highlighting the critical need to distinguish PCa-specific biomarkers from those shared with BPH. In response, we conducted a literature review of multi-omics datasets and prospective cohort studies, systematically evaluating the specificity of prioritized proteins by comparing their expression trends in PCa and BPH or benign prostate tissues. These findings are now integrated into the revised Discussion section under the subheading " Plasma Proteins Causal Links to Prostate Cancer".

In the Discussion, the paragraph (line 288) on PSA is extremely weak. The authors state that further research is needed, and yet only reference four articles (from 2008, 2010, 2012, 2014), none of which are from the last decade. Considerable amounts of research from the last ten years have been published on PSA, for example, see this article from 2018, which specifically analyses PSA in the context of the UK Biobank. This section should be made more up-to-date with the latest literature findings. https://doi.org/10.1038/s41467-018-06920-9

Thank you very much for your feedback. We acknowledge the need to strengthen the discussion on PSA by incorporating recent literature. In the revised manuscript, we have expanded the PSA discussion to integrate contemporary research on the prognostic role of PSA in the progression of PCa and its limitations in cancer screening, ensuring that our discussion reflected the current consensus and controversies. 

Also in the Discussion, the analysis of phenotypic indicators is insufficiently comprehensive and should reference other recent research. For example, this recent UK Biobank study dealt with a wide range of conditions, including prostate cancer, and identified similar factors to those identified in this paper. The authors should compare and contrast their phenotypic findings with the existing literature. https://doi.org/10.1038/s41588-024-01898-1

Thank you for addressing the comprehensiveness of phenotypic analysis. We have learned recent large-scale phenome-wide analyses (linked in your feedback) that explore multi-omics biomarkers and their associations with a range of different diseases. We have compared and contrasted our phenotypic findings with the existing literature and revised the Discussion section to interpret phenotype-PCa associations, emphasizing both shared pathways and disease-specific signals.

Under Methods, there is too little information on how Controls were selected, whether any matching process was conducted, or whether there are fundamental differences between the cases and controls (such as smoking status, BMI, comorbidities). The authors use R, and a library such as MatchIt could be used to ensure that the Controls cohort is appropriately matched to the Cases.

As outlined above, we acknowledge that our original analysis did not directly address this critical issue due to a key data limitation. The publicly available GWAS summary statistics for PCa (from openGWAS and FinnGen) do not provide individual-level data on covariates, resulting in no direct assessment of demographic or clinical differences between cases and controls.

An important final point is that, as far as I can tell, no UK Biobank Application Number has been specified in the manuscript. This is vital to establish that there was an original hypothesis being investigated (as opposed to data dredging of open access resources), especially in light of the largely mechanistic flow of the manuscript and lack of PCa and relevant confounder-specific discussion. The authors may be aware of the work of Stender et al (2024) regarding formulaic papers using Mendelian randomization, especially that "[All] combinations of exposure and outcome results based on data available in IEU openGWAS (https://gwas.mrcieu.ac.uk/) can be browsed online on epigraphDB.org. In other words, these results are, in effect, already published. Reporting them again in a scientific paper adds nothing to what can be looked up online in minutes." The authors may wish to address this issue directly.

Stender, S., Gellert-Kristensen, H. & Smith, G.D. Reclaiming Mendelian randomization from the deluge of papers and misleading findings. Lipids Health Dis 23, 286 (2024). https://doi.org/10.1186/s12944-024-02284-w

We confirm that all data used in this study were obtained from publicly available GWAS summary statistics (e.g., PRACTICAL consortium, FinnGen) and proteomic datasets (deCODE, UKB-PPP). Our research was guided by a predefined hypothesis to investigate causal plasma protein biomarkers for prostate cancer, rather than exploratory data mining. The analytical pipelines and integrative approaches (e.g., colocalization, druggability assessment) were specifically designed to address this hypothesis, aligning with the ethical use of open-access resources.

Reviewer #2 (Recommendations for the authors):

There are several specific recommendations in the public review (e.g., clarify the contribution of the GWAS). Otherwise, there is nothing clearly incorrect, but translational insight is missing - the analyses are not clearly connected to the scientific literature. This is a limitation rather than a flaw - the manuscript will likely still be useful to readers.

We thank you for highlighting the need to strengthen translational insights and contextualize our findings within existing literature. In the revised manuscript, we have expanded the Discussion section to systematically compare our results with prior mechanistic and clinical studies, including the shared pathways of associated phenotypes, the potential of significant proteins in biomarkers and therapeutic targeting. These revisions ensure our analyses are firmly rooted in the scientific literature.

eLife Assessment

This global study compares environmental niche model outputs of avian influenza pathogen niche constructed for two distinct periods, and uses differences between those outputs to suggest that the changed case numbers and distribution relate to intensification of chicken and duck farming, and extensive cultivation. While a useful update to existing niche models of highly pathogenic avian influenza, the justification for the use of environmental niche models to explore correlative relationships between land cover change and changed case epidemiology is incomplete. Key assumptions have not been adequately clarified for the readers benefit, and in consequence the communication of the likely limitations of the work are not sufficiently clear.

Reviewer #1 (Public review):

Summary:

The authors aim to predict ecological suitability for transmission of highly pathogenic avian influenza (HPAI) using ecological niche models. This class of models identify correlations between the locations of species or disease detections and the environment. These correlations are then used to predict habitat suitability (in this work, ecological suitability for disease transmission) in locations where surveillance of the species or disease has not been conducted. The authors fit separate models for HPAI detections in wild birds and farmed birds, for two strains of HPAI (H5N1 and H5Nx) and for two time periods, pre- and post-2020. The authors also validate models fitted to disease occurrence data from pre-2020 using post-2020 occurrence data. I thank the authors for taking the time to respond to my initial review and I provide some follow-up below.

Detailed comments:

In my review, I asked the authors to clarify the meaning of "spillover" within the HPAI transmission cycle. This term is still not entirely clear: at lines 409-410, the authors use the term with reference to transmission between wild birds and farmed birds, as distinct to transmission between farmed birds. It is implied but not explicitly stated that "spillover" is relevant to the transmission cycle in farmed birds only. The sentence, "we developed separate ecological niche models for wild and domestic bird HPAI occurrences ..." could have been supported by a clear sentence describing the transmission cycle, to prime the reader for why two separate models were necessary.

I also queried the importance of (dead-end) mammalian infections to a model of the HPAI transmission risk, to which the authors responded: "While spillover events of HPAI into mammals have been documented, these detections are generally considered dead-end infections and do not currently represent sustained transmission chains. As such, they fall outside the scope of our study, which focuses on avian hosts and models ecological suitability for outbreaks in wild and domestic birds." I would argue that any infections, whether they are in dead-end or competent hosts, represent the presence of environmental conditions to support transmission so are certainly relevant to a niche model and therefore within scope. It is certainly understandable if the authors have not been able to access data of mammalian infections, but it is an oversight to dismiss these infections as irrelevant.

Correlative ecological niche models, including BRTs, learn relationships between occurrence data and covariate data to make predictions, irrespective of correlations between covariates. I am not convinced that the authors can make any "interpretation" (line 298) that the covariates that are most informative to their models have any "influence" (line 282) on their response variable. Indeed, the observation that "land-use and climatic predictors do not play an important role in the niche ecological models" (line 286), while "intensive chicken population density emerges as a significant predictor" (line 282) begs the question: from an operational perspective, is the best (e.g., most interpretable and quickest to generate) model of HPAI risk a map of poultry farming intensity?

I have more significant concerns about the authors' treatment of sampling bias: "We agree with the Reviewer's comment that poultry density could have potentially been considered to guide the sampling effort of the pseudo-absences to consider when training domestic bird models. We however prefer to keep using a human population density layer as a proxy for surveillance bias to define the relative probability to sample pseudo-absence points in the different pixels of the background area considered when training our ecological niche models. Indeed, given that poultry density is precisely one of the predictors that we aim to test, considering this environmental layer for defining the relative probability to sample pseudo-absences would introduce a certain level of circularity in our analytical procedure, e.g. by artificially increasing to influence of that particular variable in our models." The authors have elected to ignore a fundamental feature of distribution modelling with occurrence-only data: if we include a source of sampling bias as a covariate and do not include it when we sample background data, then that covariate would appear to be correlated with presence. They acknowledge this later in their response to my review: "...assuming a sampling bias correlated with poultry density would result in reducing its effect as a risk factor." In other words, the apparent predictive capacity of poultry density is a function of how the authors have constructed the sampling bias for their models. A reader of the manuscript can reasonably ask the question: to what degree are is the model a model of HPAI transmission risk, and to what degree is the model a model of the observation process? The sentence at lines 474-477 is a helpful addition, however the preceding sentence, "Another approach to sampling pseudo-absences would have been to distribute them according to the density of domestic poultry," (line 474) is included without acknowledgement of the flow-on consequence to one of the key findings of the manuscript, that "...intensive chicken population density emerges as a significant predictor..." (line 282). The additional context on the EMPRES-i dataset at line 475-476 ("the locations of outbreaks ... are often georeferenced using place name nomenclatures") is in conflict with the description of the dataset at line 407 ("precise location coordinates"). Ultimately, the choices that the authors have made are entirely defensible through a clear, concise description of model features and assumptions, and precise language to guide the reader through interpretation of results. I am not satisfied that this is provided in the revised manuscript.

The authors have slightly misunderstood my comment on "extrapolation": I referred to "environmental extrapolation" in my review without being particularly explicit about my meaning. By "environmental extrapolation", I meant to ask whether the models were predicting to environments that are outside the extent of environments included in the occurrence data used in the manuscript. The authors appear to have understood this to be a comment on geographic extrapolation, or predicting to areas outside the geographic extent included in occurrence data, e.g.: "For H5Nx post-2020, areas of high predicted ecological suitability, such as Brazil, Bolivia, the Caribbean islands, and Jilin province in China, likely result from extrapolations, as these regions reported few or no outbreaks in the training data" (lines 195-197). Is the model extrapolating in environmental space in these regions? This is unclear. I do not suggest that the authors should carry out further analysis, but the multivariate environmental similarly surface (MESS; see Elith et al., 2010: https://doi.org/10.1111/j.2041-210X.2010.00036.x) is a useful tool to visualise environmental extrapolation and aid model interpretation.

On the subject of "extrapolation", I am also concerned by the additions at lines 362-370: "...our models extrapolate environmental suitability for H5Nx in wild birds in areas where few or no outbreaks have been reported. This discrepancy may be explained by limited surveillance or underreporting in those regions." The "discrepancy" cited here is a feature of the input dataset, a function of the observation distribution that should be captured in pseudo-absence data. The authors state that Kazakhstan and Central Asia are areas of interest, and that the environments in this region are outside the extent of environments captured in the occurrence dataset, although it is unclear whether "extrapolation" is informed by a quantitative tool like a MESS or judged by some other qualitative test. The authors then cite Australia as an example of a region with some predicted suitability but no HPAI outbreaks to date, however this discussion point is not linked to the idea that the presence of environmental conditions to support transmission need not imply the occurrence of transmission (as in the addition, "...spatial isolation may imply a lower risk of actual occurrences..." at line 214). Ultimately, the authors have not added any clear comment on model uncertainty (e.g., variation between replicated BRTs) as I suggested might be helpful to support their description of model predictions.

All of my criticisms are, of course, applied with the understanding that niche modelling is imperfect for a disease like HPAI, and that data may be biased/incomplete, etc.: these caveats are common across the niche modelling literature. However, if language around the transmission cycle, the niche, and the interpretation of any of the models is imprecise, which I find it to be in the revised manuscript, it undermines all of the science that is presented in this work.

Reviewer #2 (Public review):

Summary:

The geographic range of highly pathogenic avian influenza cases changed substantially around the period 2020, and there is much interest in understanding why. Since 2020 the pathogen irrupted in the Americas and the distribution in Asia changed dramatically. This study aimed to determine which spatial factors (environmental, agronomic and socio-economic) explain the change in numbers and locations of cases reported since 2020 (2020--2023). That's a causal question which they address by applying correlative environmental niche modelling (ENM) approach to the avian influenza case data before (2015--2020) and after 2020 (2020--2023) and separately for confirmed cases in wild and domestic birds. To address their questions they compare the outputs of the respective models, and those of the first global model of the HPAI niche published by Dhingra et al 2016.

ENM is a correlative approach useful for extrapolating understandings based on sparse geographically referenced observational data over un- or under-sampled areas with similar environmental characteristics in the form of a continuous map. In this case, because the selected covariates about land cover, use, population and environment are broadly available over the entire world, modelled associations between the response and those covariates can be projected (predicted) back to space in the form of a continuous map of the HPAI niche for the entire world.

Strengths:

The authors are clear about expected bias in the detection of cases, such geographic variation in surveillance effort (testing of symptomatic or dead wildlife, testing domestic flocks) and in general more detections near areas of higher human population density (because if a tree falls in a forest and there is no-one there, etc), and take steps to ameliorate those. The authors use boosted regression trees to implement the ENM, which typically feature among the best performing models for this application (also known as habitat suitability models). They ran replicate sets of the analysis for each of their model targets (wild/domestic x pathogen variant), which can help produce stable predictions. Their code and data is provided, though I did not verify that the work was reproducible.

The paper can be read as a partial update to the first global model of H5Nx transmission by Dhingra and others published in 2016 and explicitly follows many methodological elements. Because they use the same covariate sets as used by Dhingra et al 2016 (including the comparisons of the performance of the sets in spatial cross-validation) and for both time periods of interest in the current work, comparison of model outputs is possible. The authors further facilitate those comparisons with clear graphics and supplementary analyses and presentation. The models can also be explored interactively at a weblink provided in text, though it would be good to see the model training data there too.

The authors' comparison of ENM model outputs generated from the distinct HPAI case datasets is interesting and worthwhile, though for me, only as a response to differently framed research questions.

Weaknesses:

This well-presented and technically well-executed paper has one major weakness to my mind. I don't believe that ENM models were an appropriate tool to address their stated goal, which was to identify the factors that "explain" changing HPAI epidemiology.

Here is how I understand and unpack that weakness:

(1) Because of their fundamentally correlative nature, ENMs are not a strong candidate for exploring or inferring causal relationships.

(2) Generating ENMs for a species whose distribution is undergoing broad scale range change is complicated and requires particular caution and nuance in interpretation (e.g., Elith et al, 2010, an important general assumption of environmental niche models is that the target species is at some kind of distributional equilibrium (at time scales relevant to the model application). In practice that means the species has had an opportunity to reach all suitable habitats and therefore its absence from some can be interpreted as either unfavourable environment or interactions with other species). Here data sets for the response (N5H1 or N5Hx case data in domestic or wild birds ) were divided into two periods; 2015--2020, and 2020--2023 based on the rationale that the geographic locations and host-species profile of cases detected in the latter period was suggestive of changed epidemiology. In comparing outputs from multiple ENMs for the same target from distinct time periods the authors are expertly working in, or even dancing around, what is a known grey area, and they need to make the necessary assumptions and caveats obvious to readers.

(3) To generate global prediction maps via ENM, only variables that exist at appropriate resolution over the desired area can be supplied as covariates. What processes could influence changing epidemiology of a pathogen and are their covariates that represent them? Introduction to a new geographic area (continent) with naive population, immunity in previously exposed populations, control measures to limit spread such as vaccination or destruction of vulnerable populations or flocks? Might those control measures be more or less likely depending on the country as a function of its resources and governance? There aren't globally available datasets that speak to those factors, so the question is not why were they omitted but rather was the authors decision to choose ENMs given their question justified? How valuable are insights based on patterns of correlation change when considering different temporal sets of HPAI cases in relation to a common and somewhat anachronistic set of covariates?

(4) In general the study is somewhat incoherent with respect to time. Though the case data come from different time periods, each response dataset was modelled separately using exactly the same covariate dataset that predated both sets. That decision should be understood as a strong assumption on the part of the authors that conditions the interpretation: the world (as represented by the covariate set) is immutable, so the model has to return different correlative associations between the case data and the covariates to explain the new data. While the world represented by the selected covariates *may* be relatively stable (could be statistically confirmed), what about the world not represented by the covariates (see point 3)?

References:

Dhingra et al, 2016, Global mapping of highly pathogenic avian influenza H5N1 and H5Nx clade 2.3.4.4 viruses with spatial cross-validation, eLife 5, https://doi.org/10.7554/eLife.19571

Elith, J., Kearney, M., & Phillips, S. (2010). The art of modelling range‐shifting species. Methods in Ecology and Evolution, 1(4), 330-342.

Author response:

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

Public Reviews:

We thank the Reviewers for their thorough attention to our paper and the interesting discussion about the findings. Before responding to more specific comments, here some general points we would like to clarify:

(1) Ecological niche models are indeed correlative models, and we used them to highlight environmental factors associated with HPAI outbreaks within two host groups. We will further revise the terminology that could still unintentionally suggest causal inference. The few remaining ambiguities were mainly in the Discussion section, where our intent was to interpret the results in light of the broader scientific literature. Particularly, we will change the following expressions:

-  “Which factors can explain…” to  “Which factors are associated with…” (line 75);

-  “the environmental and anthropogenic factors influencing” to “the environmental and anthropogenic factors that are correlated with” (line 273);

-  “underscoring the influence” to “underscoring the strong association” (line 282).

(2) We respectfully disagree with the suggestion that an ecological niche modelling (ENM) approach is not appropriate for this work and the research question addressed therein. Ecological niche models are specifically designed to estimate the spatial distribution of the environmental suitability of species and pathogens, making them well suited to our research questions. In our study, we have also explicitly detailed the known limitations of ecological niche models in the Discussion section, in line with prior literature, to ensure their appropriate interpretation in the context of HPAI.

(3) The environmental layers used in our models were restricted to those available at a global scale, as listed in Supplementary Information Resources S1 (https://github.com/sdellicour/h5nx_risk_mapping/blob/master/Scripts_%26_data/SI_Resource_S1.xlsx). Naturally, not all potentially relevant environmental factors could be included, but the selected layers are explicitly documented and only these were assessed for their importance. Despite this limitation, the performance metrics indicate that the models performed well, suggesting that the chosen covariates capture meaningful associations with HPAI occurrence at a global scale.

Reviewer #1 (Public review):

The authors aim to predict ecological suitability for transmission of highly pathogenic avian influenza (HPAI) using ecological niche models. This class of models identify correlations between the locations of species or disease detections and the environment. These correlations are then used to predict habitat suitability (in this work, ecological suitability for disease transmission) in locations where surveillance of the species or disease has not been conducted. The authors fit separate models for HPAI detections in wild birds and farmed birds, for two strains of HPAI (H5N1 and H5Nx) and for two time periods, pre- and post-2020. The authors also validate models fitted to disease occurrence data from pre-2020 using post-2020 occurrence data. I thank the authors for taking the time to respond to my initial review and I provide some follow-up below.

Detailed comments:

In my review, I asked the authors to clarify the meaning of "spillover" within the HPAI transmission cycle. This term is still not entirely clear: at lines 409-410, the authors use the term with reference to transmission between wild birds and farmed birds, as distinct to transmission between farmed birds. It is implied but not explicitly stated that "spillover" is relevant to the transmission cycle in farmed birds only. The sentence, "we developed separate ecological niche models for wild and domestic bird HPAI occurrences ..." could have been supported by a clear sentence describing the transmission cycle, to prime the reader for why two separate models were necessary.

We respectfully disagree that the term “spillover” is unclear in the manuscript. In both the Methods and Discussion sections (lines 387-391 and 409-414), we explicitly define “spillover” as the introduction of HPAI viruses from wild birds into domestic poultry, and we distinguish this from secondary farm-to-farm transmission. Our use of separate ecological niche models for wild and domestic outbreaks reflects not only the distinction between primary spillover and secondary transmission, but also the fundamentally different ecological processes, surveillance systems, and management implications that shape outbreaks in these two groups. We will clarify this choice in the revised manuscript when introducing the separate models. Furthermore, on line 83, we will add “as these two groups are influenced by different ecological processes, surveillance biases, and management contexts”.

I also queried the importance of (dead-end) mammalian infections to a model of the HPAI transmission risk, to which the authors responded: "While spillover events of HPAI into mammals have been documented, these detections are generally considered dead-end infections and do not currently represent sustained transmission chains. As such, they fall outside the scope of our study, which focuses on avian hosts and models ecological suitability for outbreaks in wild and domestic birds." I would argue that any infections, whether they are in dead-end or competent hosts, represent the presence of environmental conditions to support transmission so are certainly relevant to a niche model and therefore within scope. It is certainly understandable if the authors have not been able to access data of mammalian infections, but it is an oversight to dismiss these infections as irrelevant.

We understand the Reviewer’s point, but our study was designed to model HPAI occurrence in avian hosts only. We therefore restricted our analysis to wild birds and domestic poultry, which represent the primary hosts for HPAI circulation and the focus of surveillance and control measures. While mammalian detections have been reported, they are outside the scope of this work.

Correlative ecological niche models, including BRTs, learn relationships between occurrence data and covariate data to make predictions, irrespective of correlations between covariates. I am not convinced that the authors can make any "interpretation" (line 298) that the covariates that are most informative to their models have any "influence" (line 282) on their response variable. Indeed, the observation that "land-use and climatic predictors do not play an important role in the niche ecological models" (line 286), while "intensive chicken population density emerges as a significant predictor" (line 282) begs the question: from an operational perspective, is the best (e.g., most interpretable and quickest to generate) model of HPAI risk a map of poultry farming intensity?

We agree that poultry density may partly reflect reporting bias, but we also assumed it a meaningful predictor of HPAI risk. Its importance in our models is therefore expected. Importantly, our BRT framework does more than reproduce poultry distribution: it captures non-linear relationships and interactions with other covariates, allowing a more nuanced characterisation of risk than a simple poultry density map. Note also that we distinguished in our models intensive and extensive chicken poultry density and duck density. Therefore, it is not a “map of poultry farming intensity”. 

At line 282, we used the word “influence” while fully recognising that correlative models cannot establish causality. Indeed, in our analyses, “relative influence” refers to the importance metric produced by the BRT algorithm (Ridgeway, 2020), which measures correlative associations between environmental factors and outbreak occurrences. These scores are interpreted in light of the broader scientific literature, therefore our interpretations build on both our results and existing evidence, rather than on our models alone. However, in the next version of the paper, we will revise the sentence as: “underscoring the strong association of poultry farming practices with HPAI spread (Dhingra et al., 2016)”. 

I have more significant concerns about the authors' treatment of sampling bias: "We agree with the Reviewer's comment that poultry density could have potentially been considered to guide the sampling effort of the pseudo-absences to consider when training domestic bird models. We however prefer to keep using a human population density layer as a proxy for surveillance bias to define the relative probability to sample pseudo-absence points in the different pixels of the background area considered when training our ecological niche models. Indeed, given that poultry density is precisely one of the predictors that we aim to test, considering this environmental layer for defining the relative probability to sample pseudo-absences would introduce a certain level of circularity in our analytical procedure, e.g. by artificially increasing to influence of that particular variable in our models." The authors have elected to ignore a fundamental feature of distribution modelling with occurrence-only data: if we include a source of sampling bias as a covariate and do not include it when we sample background data, then that covariate would appear to be correlated with presence. They acknowledge this later in their response to my review: "...assuming a sampling bias correlated with poultry density would result in reducing its effect as a risk factor." In other words, the apparent predictive capacity of poultry density is a function of how the authors have constructed the sampling bias for their models. A reader of the manuscript can reasonably ask the question: to what degree are is the model a model of HPAI transmission risk, and to what degree is the model a model of the observation process? The sentence at lines 474-477 is a helpful addition, however the preceding sentence, "Another approach to sampling pseudo-absences would have been to distribute them according to the density of domestic poultry," (line 474) is included without acknowledgement of the flow-on consequence to one of the key findings of the manuscript, that "...intensive chicken population density emerges as a significant predictor..." (line 282). The additional context on the EMPRES-i dataset at line 475-476 ("the locations of outbreaks ... are often georeferenced using place name nomenclatures") is in conflict with the description of the dataset at line 407 ("precise location coordinates"). Ultimately, the choices that the authors have made are entirely defensible through a clear, concise description of model features and assumptions, and precise language to guide the reader through interpretation of results. I am not satisfied that this is provided in the revised manuscript.

We thank the Reviewer for this important point. To address it, we compared model predictive performance and covariate relative influences obtained when pseudo-absences were weighted by poultry density versus human population density (Author response table 1). The results show that differences between the two approaches are marginal, both in predictive performance (ΔAUC ranging from -0.013 to +0.002) and in the ranking of key predictors (see below Author response images 1 and 2). For instance, intensive chicken density consistently emerged as an important predictor regardless of the bias layer used.

Note: the comparison was conducted using a simplified BRT configuration for computational efficiency (fewer trees, fixed 5-fold random cross-validation, and standardised parameters). Therefore, absolute values of AUC and variable importance may differ slightly from those in the manuscript, but the relative ranking of predictors and the overall conclusions remain consistent.

Given these small differences, we retained the approach using human population density. We agree that poultry density partly reflects surveillance bias as well as true epidemiological risk, and we will clarify this in the revised manuscript by noting that the predictive role of poultry density reflects both biological processes and surveillance systems. Furthermore, on line 289, we will add “We note, however, that intensive poultry density may reflect both surveillance intensity and epidemiological risk, and its predictive role in our models should be interpreted in light of both processes”.

Author response table 1.

Comparison of model predictive performances (AUC) between pseudo-absence sampling were weighted by poultry density and by human population density across host groups, virus types, and time periods. Differences in AUC values are shown as the value for poultry-weighted minus human-weighted pseudo-absences.

Author response image 1.

Comparison of variable relative influence (%) between models trained with pseudo-absences weighted by poultry density (red) and human population density (blue) for domestic bird outbreaks. Results are shown for four datasets: H5N1 (<2020), H5N1 (>2020), H5Nx (<2020), and H5Nx (>2020).

Author response image 2.

Comparison of variable relative influence (%) between models trained with pseudo-absences weighted by poultry density (red) and human population density (blue) for wild bird outbreaks. Results are shown for three datasets: H5N1 (>2020), H5Nx (<2020), and H5Nx (>2020).

The authors have slightly misunderstood my comment on "extrapolation": I referred to "environmental extrapolation" in my review without being particularly explicit about my meaning. By "environmental extrapolation", I meant to ask whether the models were predicting to environments that are outside the extent of environments included in the occurrence data used in the manuscript. The authors appear to have understood this to be a comment on geographic extrapolation, or predicting to areas outside the geographic extent included in occurrence data, e.g.: "For H5Nx post-2020, areas of high predicted ecological suitability, such as Brazil, Bolivia, the Caribbean islands, and Jilin province in China, likely result from extrapolations, as these regions reported few or no outbreaks in the training data" (lines 195-197). Is the model extrapolating in environmental space in these regions? This is unclear. I do not suggest that the authors should carry out further analysis, but the multivariate environmental similarly surface (MESS; see Elith et al., 2010) is a useful tool to visualise environmental extrapolation and aid model interpretation.

On the subject of "extrapolation", I am also concerned by the additions at lines 362-370: "...our models extrapolate environmental suitability for H5Nx in wild birds in areas where few or no outbreaks have been reported. This discrepancy may be explained by limited surveillance or underreporting in those regions." The "discrepancy" cited here is a feature of the input dataset, a function of the observation distribution that should be captured in pseudo-absence data. The authors state that Kazakhstan and Central Asia are areas of interest, and that the environments in this region are outside the extent of environments captured in the occurrence dataset, although it is unclear whether "extrapolation" is informed by a quantitative tool like a MESS or judged by some other qualitative test. The authors then cite Australia as an example of a region with some predicted suitability but no HPAI outbreaks to date, however this discussion point is not linked to the idea that the presence of environmental conditions to support transmission need not imply the occurrence of transmission (as in the addition, "...spatial isolation may imply a lower risk of actual occurrences..." at line 214). Ultimately, the authors have not added any clear comment on model uncertainty (e.g., variation between replicated BRTs) as I suggested might be helpful to support their description of model predictions.

Many thanks for the clarification. Indeed, we interpreted your previous comments in terms of geographic extrapolations. We thank the Reviewer for these observations. We will adjust the wording to further clarify that predictions of ecological suitability in areas with few or no reported outbreaks (e.g., Central Asia, Australia) are not model errors but expected extrapolations, since ecological suitability does not imply confirmed transmission (for instance, on Line 362: “our models extrapolate environmental suitability” will be changed to “Interestingly, our models extrapolate geographical”). These predictions indicate potential environments favorable to circulation if the virus were introduced.

In our study, model uncertainty is formally assessed when comparing the predictive performances of our models (Fig. S3, Table S1), the relative influence (Table S3) and response curves (Fig. 2) associated with each environmental factor (Table S2). All the results confirming a good converge between these replicates. Finally, we indeed did not use a quantitative tool such as a MESS to assess extrapolation but did rely on qualitative interpretation of model outputs.

All of my criticisms are, of course, applied with the understanding that niche modelling is imperfect for a disease like HPAI, and that data may be biased/incomplete, etc.: these caveats are common across the niche modelling literature. However, if language around the transmission cycle, the niche, and the interpretation of any of the models is imprecise, which I find it to be in the revised manuscript, it undermines all of the science that is presented in this work.

We respectfully disagree with this comment. The scope of our study and the methods employed are clearly defined in the manuscript, and the limitations of ecological niche modelling in this context are explicitly acknowledged in the Discussion section. While we appreciate the Reviewer’s concern, the comment does not provide specific examples of unclear or imprecise language regarding the transmission cycle, niche, or interpretation of the models. Without such examples, it is difficult to identify further revisions that would improve clarity.

Reviewer #2 (Public review):

The geographic range of highly pathogenic avian influenza cases changed substantially around the period 2020, and there is much interest in understanding why. Since 2020 the pathogen irrupted in the Americas and the distribution in Asia changed dramatically. This study aimed to determine which spatial factors (environmental, agronomic and socio-economic) explain the change in numbers and locations of cases reported since 2020 (2020--2023). That's a causal question which they address by applying correlative environmental niche modelling (ENM) approach to the avian influenza case data before (2015--2020) and after 2020 (2020--2023) and separately for confirmed cases in wild and domestic birds. To address their questions they compare the outputs of the respective models, and those of the first global model of the HPAI niche published by Dhingra et al 2016.

We do not agree with this comment. In the manuscript, it is well established that we are quantitatively assessing factors that are associated with occurrences data before and after 2020. We do not claim to determine the causality. One sentence of the Introduction section (lines 75-76) could be confusing, so we intend to modify it in the final revision of our manuscript. 

ENM is a correlative approach useful for extrapolating understandings based on sparse geographically referenced observational data over un- or under-sampled areas with similar environmental characteristics in the form of a continuous map. In this case, because the selected covariates about land cover, use, population and environment are broadly available over the entire world, modelled associations between the response and those covariates can be projected (predicted) back to space in the form of a continuous map of the HPAI niche for the entire world.

We fully agree with this assessment of ENM approaches.

Strengths:

The authors are clear about expected bias in the detection of cases, such geographic variation in surveillance effort (testing of symptomatic or dead wildlife, testing domestic flocks) and in general more detections near areas of higher human population density (because if a tree falls in a forest and there is no-one there, etc), and take steps to ameliorate those. The authors use boosted regression trees to implement the ENM, which typically feature among the best performing models for this application (also known as habitat suitability models). They ran replicate sets of the analysis for each of their model targets (wild/domestic x pathogen variant), which can help produce stable predictions. Their code and data is provided, though I did not verify that the work was reproducible.

The paper can be read as a partial update to the first global model of H5Nx transmission by Dhingra and others published in 2016 and explicitly follows many methodological elements. Because they use the same covariate sets as used by Dhingra et al 2016 (including the comparisons of the performance of the sets in spatial cross-validation) and for both time periods of interest in the current work, comparison of model outputs is possible. The authors further facilitate those comparisons with clear graphics and supplementary analyses and presentation. The models can also be explored interactively at a weblink provided in text, though it would be good to see the model training data there too.

The authors' comparison of ENM model outputs generated from the distinct HPAI case datasets is interesting and worthwhile, though for me, only as a response to differently framed research questions.

Weaknesses:

This well-presented and technically well-executed paper has one major weakness to my mind. I don't believe that ENM models were an appropriate tool to address their stated goal, which was to identify the factors that "explain" changing HPAI epidemiology.

Here is how I understand and unpack that weakness:

(1) Because of their fundamentally correlative nature, ENMs are not a strong candidate for exploring or inferring causal relationships.

(2) Generating ENMs for a species whose distribution is undergoing broad scale range change is complicated and requires particular caution and nuance in interpretation (e.g., Elith et al, 2010, an important general assumption of environmental niche models is that the target species is at some kind of distributional equilibrium (at time scales relevant to the model application). In practice that means the species has had an opportunity to reach all suitable habitats and therefore its absence from some can be interpreted as either unfavourable environment or interactions with other species). Here data sets for the response (N5H1 or N5Hx case data in domestic or wild birds ) were divided into two periods; 2015--2020, and 2020--2023 based on the rationale that the geographic locations and host-species profile of cases detected in the latter period was suggestive of changed epidemiology. In comparing outputs from multiple ENMs for the same target from distinct time periods the authors are expertly working in, or even dancing around, what is a known grey area, and they need to make the necessary assumptions and caveats obvious to readers.

We thank the Reviewer for this observation. First, we constrained pseudo-absence sampling to countries and regions where outbreaks had been reported, reducing the risk of interpreting non-affected areas as environmentally unsuitable. Second, we deliberately split the outbreak data into two periods (2015-2020 and 2020-2023) because we do not assume a single stable equilibrium across the full study timeframe. This division reflects known epidemiological changes around 2020 and allows each period to be modeled independently. Within each period, ENM outputs are interpreted as associations between outbreaks and covariates, not as equilibrium distributions. Finally, by testing prediction across periods, we assessed both niche stability and potential niche shifts. These clarifications will be added to the manuscript to make our assumptions and limitations explicit.

Line 66, we will add: “Ecological niche model outputs for range-shifting pathogens must therefore be interpreted with caution (Elith et al., 2010). Despite this limitation, correlative ecological niche models  remain useful for identifying broad-scale associations and potential shifts in distribution. To account for this, we analysed two distinct time periods (2015-2020 and 2020-2023).”

Line 123, we will revise “These findings underscore the ability of pre-2020 models in forecasting the recent geographic distribution of ecological suitability for H5Nx and H5N1 occurrences” to “These results suggest that pre-2020 models captured broad patterns of suitability for H5Nx and H5N1 outbreaks, while post-2020 models provided a closer fit to the more recent epidemiological situation”.

(3) To generate global prediction maps via ENM, only variables that exist at appropriate resolution over the desired area can be supplied as covariates. What processes could influence changing epidemiology of a pathogen and are their covariates that represent them? Introduction to a new geographic area (continent) with naive population, immunity in previously exposed populations, control measures to limit spread such as vaccination or destruction of vulnerable populations or flocks? Might those control measures be more or less likely depending on the country as a function of its resources and governance? There aren't globally available datasets that speak to those factors, so the question is not why were they omitted but rather was the authors decision to choose ENMs given their question justified? How valuable are insights based on patterns of correlation change when considering different temporal sets of HPAI cases in relation to a common and somewhat anachronistic set of covariates?

We agree that the ecological niche models trained in our study are limited to environmental and host factors, as described in the Methods section with the selection of predictors. While such models cannot capture causality or represent processes such as immunity, control measures, or governance, they remain a useful tool for identifying broad associations between outbreak occurrence and environmental context. Our study cannot infer the full mechanisms driving changes in HPAI epidemiology, but it does provide a globally consistent framework to examine how associations with available covariates vary across time periods.

(4) In general the study is somewhat incoherent with respect to time. Though the case data come from different time periods, each response dataset was modelled separately using exactly the same covariate dataset that predated both sets. That decision should be understood as a strong assumption on the part of the authors that conditions the interpretation: the world (as represented by the covariate set) is immutable, so the model has to return different correlative associations between the case data and the covariates to explain the new data. While the world represented by the selected covariates *may* be relatively stable (could be statistically confirmed), what about the world not represented by the covariates (see point 3)?

We used the same covariate layers for both periods, which indeed assumes that these environmental and host factors are relatively stable at the global scale over the short timeframe considered. We believe this assumption is reasonable, as poultry density, land cover, and climate baselines do not change drastically between 2015 and 2023 at the resolution of our analysis. We agree, however, that unmeasured processes such as control measures, immunity, or governance may have changed during this time and are not captured by our covariates.

Recommendations for the Authors:

Reviewer #1 (Recommendations for the authors):

- Line 400-401: "over the 2003-2016 periods" has an extra "s"; "two host species" (with reference to wild and domestic birds) would be more precise as "two host groups".

- Remove comma line 404

Many thanks for these comments, we have modified the text accordingly.

Reviewer #2 (Recommendations for the authors):

Most of my work this round is encapsulated in the public part of the review.

The authors responded positively to the review efforts from the previous round, but I was underwhelmed with the changes to the text that resulted. Particularly in regard to limiting assumptions - the way that they augmented the text to refer to limitations raised in review downplayed the importance of the assumptions they've made. So they acknowledge the significance of the limitation in their rejoinder, but in the amended text merely note the limitation without giving any sense of what it means for their interpretation of the findings of this study.

The abstract and findings are essentially unchanged from the previous draft.

I still feel the near causal statements of interpretation about the covariates are concerning. These models really are not a good candidate for supporting the inference that they are making and there seem to be very strong arguments in favour of adding covariates that are not globally available.

We never claimed causal interpretation, and we have consistently framed our analyses in terms of associations rather than mechanisms. We acknowledge that one phrasing in the research questions (“Which factors can explain…”) could be misinterpreted, and we are correcting this in the revised version to read “Which factors are associated with…”. Our approach follows standard ecological niche modelling practice, which identifies statistical associations between occurrence data and covariates. As noted in the Discussion section, these associations should not be interpreted as direct causal mechanisms. Finally, all interpretive points in the manuscript are supported by published literature, and we consider this framing both appropriate and consistent with best practice in ecological niche modelling (ENM) studies.

We assessed predictor contributions using the “relative influence” metric, the terminology reported by the R package “gbm” (Ridgeway, 2020). This metric quantifies the contribution of each variable to model fit across all trees, rescaled to sum to 100%, and should be interpreted as an association rather than a causal effect.

L65-66 The general difficulty of interpreting ENM output with range-shifting species should be cited here to alert readers that they should not blithely attempt what follows at home.

I believe that their analysis is interesting and technically very well executed, so it has been a disappointment and hard work to write this assessment. My rough-cut last paragraph of a reframed intro would go something like - there are many reasons in the literature not to do what we are about to do, but here's why we think it can be instructive and informative, within certain guardrails.

To acknowledge this comment and the previous one, we revised lines 65-66 to: “However, recent outbreaks raise questions about whether earlier ecological niche models still accurately predict the current distribution of areas ecologically suitable for the local circulation of HPAI H5 viruses. Ecological niche model outputs for range-shifting pathogens must therefore be interpreted with caution (Elith et al., 2010). Despite this limitation, correlative ecological niche models  remain useful for identifying broad-scale associations and potential shifts in distribution.”

We respectfully disagree with the Reviewer’s statement that “_there are many reasons in the literature not to do what we are about to do”._ All modeling approaches, including mechanistic ones, have limitations, and the literature is clear on both the strengths and constraints of ecological niche models. Our manuscript openly acknowledges these limits and frames our findings accordingly. We therefore believe that our use of an ENM approach is justified and contributes valuable insights within these well-defined boundaries.

Reference: Ridgeway, G. (2007). Generalized Boosted Models: A guide to the gbm package. Update, 1(1), 2007.

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

Reviewer #1(Public review):

I am concerned by the authors' conceptualisation of "niche" within the manuscript. Is the "niche" we are modelling the niche of the pathogen itself? The niche of the (wild) bird host species as a group? The niche of HPAI transmission within (wild) bird host species (i.e., an intersection of pathogen and bird niches)? Or the niche of HPAI transmission in poultry? The precise niche being modelled should be clarified in the Introduction or early in the Methods of the manuscript. The first two definitions of niche listed above are relevant, but separate from the niche modelled in the manuscript - this should be acknowledged.

We acknowledge that these concepts were probably not enough clearly defined in the previous version of our manuscript, and we have now included an explicit definition in the fourth paragraph of the Introduction section: “We developed separate ecological niche models for wild and domestic bird HPAI occurrences, these models thus predicting the ecological suitability for the risk of local viral circulation leading to the detection of HPAI occurrences within each host group (rather than the niche of the virus or the host species alone).”

The authors should consider the precise transmission cycle involved in each HPAI case: "index cases" in farmed poultry, caused by "spillover" from wild birds, are relevant to the wildlife transmission cycle, while the ecological conditions coinciding with subsequent transmission in farmed poultry are likely to be fundamentally different. (For example, subsequent transmission is not conditional on the presence of wild birds.) Modelling these two separate, but linked, transmission cycles together may omit important nuances from the modelling framework.

We thank the Reviewer for highlighting the distinction between primary (wild-todomestic) and secondary (farm-to-farm) transmission cycles. Our modelling framework was designed to assess the ecological suitability of HPAI occurrences in wild and domestic birds separately. In the domestic poultry models, the response variables are the confirmed outbreaks data and do not distinguish between index cases resulting from primary or secondary infections.

One of the aims of the study is to evaluate the spatial distribution of areas ecologically suitable for local H5N1/x circulation either leading to domestic or wild bird cases, i.e. to identify environmental conditions where the virus may have persisted or spread, whether as a result of introduction by wild birds or farm-to-farm transmission. Introducing mechanistic distinctions in the response variable would not necessarily improve or affect the ecological suitability maps, since each type of transmission is likely to be associated with different covariates that are included in the models.

Also, the EMPRES-i database does not indicate whether each record corresponds to an index case or a secondary transmission event, so in practice it would not be possible to produce two different models. However, we agree that distinguishing between types of transmission is an interesting perspective for future research. This could be explored, for example, by mapping interfaces between wild and domestic bird populations or by inferring outbreak transmission trees using genomic data when available.

To avoid confusion, we now explicitly clarify this aspect in the Materials and Methods section: “It is important to note that the EMPRES-i database does not distinguish between index cases (e.g., primary spillover from wild birds) and secondary farm-to-farm transmissions. As such, our ecological niche models are trained on confirmed HPAI outbreaks in poultry that may result from different transmission dynamics — including both initial introduction events influenced by environmental factors and subsequent spread within poultry systems.”

We now also address this limitation in the Discussion section: “Finally, our models for domestic poultry do not distinguish between primary introduction events (e.g., spillover from wild birds) and secondary transmission between farms due to limitations in the available surveillance data. While environmental factors likely influence the risk of initial spillover events, secondary spread is more often driven by anthropogenic factors such as biosecurity practices and poultry trade, which are not included in our current modelling framework.”

The authors should clarify the meaning of "spillover" within the HPAI transmission cycle: if spillover transmission is from wild birds to farmed poultry, then subsequent transmission in poultry is separate from the wildlife transmission cycle. This is particularly relevant to the Discussion paragraph beginning at line 244: does "farm to farm transmission" have a distinct ecological niche to transmission between wild birds, and transmission between wild birds and farmed birds? And while there has been a spillover of HPAI to mammals, could the authors clarify that these detections are dead-end? And not represented in the dataset? Dhingra et al., 2016 comment on the contrast between models of "directly transmitted" pathogens, such as HPAI, and vector-borne diseases: for vector-borne diseases, "clear eco-climatic boundaries of vectors can be mapped", whereas "HPAI is probably not as strongly environmentally constrained". This is an important piece of nuance in their Discussion and a comment to a similar effect may be of use in this manuscript.

Following the Reviewer’s previous comment, we have now added clarifications in the Methods and Discussion sections defining spillover as the transmission of HPAI viruses from wild birds to domestic poultry (index cases), and secondary transmission as onward spread between farms. As mentioned in our answer above, we now emphasise that our models do not distinguish these dynamics, which are likely to be influenced by different drivers — ecological in the case of spillover, and often anthropogenic (e.g., poultry trade movement, biosecurity) in the case of farm-to-farm transmission.

The discussion regarding farm-to-farm transmission and spillovers is indeed an interpretation derived from the covariates analysis (see the second paragraph in the Discussion section). Specifically, we observed a stronger association between HPAI occurrences and domestic bird density after 2020, which may suggest that secondary infections (e.g., farm-to-farm transmission) became more prominent or more frequently reported. We however acknowledge that our data do not allow us to distinguish primary introductions from secondary transmission events, and we have added a sentence to explicitly clarify this: “However, this remains an interpretation, as the available data do not allow us to distinguish between index cases and secondary transmission events.”

We thank the Reviewer for raising the point of mammalian infections. While spillover events of HPAI into mammals have been documented, these detections are generally considered dead-end infections and do not currently represent sustained transmission chains. As such, they fall outside the scope of our study, which focuses on avian hosts and models ecological suitability for outbreaks in wild and domestic birds. However, we agree that future work could explore the spatial overlap between mammalian outbreak detections and ecological suitability maps for wild birds to assess whether such spillovers may be linked to localised avian transmission dynamics.

Finally, we have added a comment about the differences between pathogens strongly constrained by the environments and HPAI: “This suggests that HPAI H5Nx is not as strongly environmentally constrained as vector-borne pathogens, for which clear eco-climatic boundaries (e.g., vector borne diseases) can be mapped (Dhingra et al., 2016).” This aligns with the interpretation provided by Dhingra and colleagues (2016) and helps contextualise the predictive limitations of ecological niche models for directly transmitted pathogens like HPAI.

There are several places where some simple clarification of language could answer my questions related to ecological niches. For example, on line 74, "the ecological niche" should be followed by "of the pathogen", or "of HPAI transmission in wild birds", or some other qualifier that is most appropriate to the Authors' conceptualisation of the niche modelled in the manuscript. Similarly, in the following sentence, "areas at risk" could be followed by "of transmission in wild birds", to make the transmission cycle that is the subject of modelling clear to the reader. On line 83, it is not clear who or what is the owner of "their ecological niches": is this "poultry and wild birds", or the pathogen?

We agree with that suggestion and have now modified the related part of the text  accordingly (e.g., “areas at risk for local HPAI circulation” and “of HPAI in wild or domestic birds”).

I am concerned by the authors' treatment of sampling bias in their BRT modelling framework. If we are modelling the niche of HPAI transmission, we would expect places that are more likely to be subject to disease surveillance to be represented in the set of locations where the disease has been detected. I do not agree that pseudo-absence points are sampled "to account for the lack of virus detection in some areas" - this description is misleading and does not match the following sentence ("pseudo-absence points sampled ... to reflect the greater surveillance efforts ..."). The distribution of pseudo-absences should aim to capture the distribution of probable disease surveillance, as these data act as a stand-in for missing negative surveillance records. It is sensible that pseudo-absences for disease detection in wild birds are sampled proportionately to human population density, as the disease is detected in dead wild birds, which are more likely to be identified close to areas of human occupation (as stated on line 163). However, I do not agree that the same applies to poultry - the density of farmed poultry is likely to be a better proxy for surveillance intensity in farmed birds. Human population density and farmed poultry density may be somewhat correlated (i.e., both are low in remote areas), but poultry density is likely to be higher in rural areas, which are assumed to have relatively lower surveillance intensity under the current approach. The authors allude to this in the Discussion: "monitoring areas with high intensive chicken densities ... remains crucial for the early detection and management of HPAI outbreaks".

We agree with the Reviewer's comment that poultry density could have potentially been considered to guide the sampling effort of the pseudo-absences to consider when training domestic bird models. We however prefer to keep using a human population density layer as a proxy for surveillance bias to define the relative probability to sample pseudoabsence points in the different pixels of the background area considered when training our ecological niche models. Indeed, given that poultry density is precisely one of the predictors that we aim to test, considering this environmental layer for defining the relative probability to sample pseudo-absences would introduce a certain level of circularity in our analytical procedure, e.g. by artificially increasing to influence of that particular variable in our models.

Furthermore, it is also worth noting that, to better account for variations in surveillance intensity, we also adjusted the sampling effort by allocating pseudo-absences in proportion to the number of confirmed outbreaks per administrative unit (country or sub-national regions for Russia and China). This approach aimed to reduce bias caused by uneven reporting and surveillance efforts between regions. Additionally, we restricted model training to countries or regions with a minimum surveillance threshold (at least five confirmed outbreaks per administrative unit). Therefore, both presence and pseudo-absence points originated from areas with more consistent surveillance data.

We acknowledge in the Materials and Methods section that the approach proposed by the Reviewer could have been used: “Another approach to sampling pseudo-absences would have been to distribute them according to the density of domestic poultry.” Finally, our approach is also justified in our response to the next comment of the Reviewer.

Having written my review, including the paragraph above, I briefly scanned Dhingra et al., and found that they provide justification for the use of human population density to sample pseudoabsences in farmed birds: "the Empres-i database compiles outbreak locations data from very heterogeneous sources and in the absence of explicit GPS location data, the geo-referencing of individual cases is often through the use of place name gazetteers that will tend to force the outbreak location populated place, rather in the exact location of the farm where the disease was found, which would introduce a bias correlated with human population density." This context is entirely missing from the manuscript under review, however, I maintain the comment in the paragraph above - have the Authors trialled sampling pseudo-absences from poultry density layers?

We agree with the Reviewer’s comment and have now added this precision in the Materials and Methods section (in the third paragraph dedicated to ecological niche modelling): “However, as pointed out by Dhingra and colleagues (2016), the locations of outbreaks in the EMPRES-i database are often georeferenced using place name nomenclatures due to a lack of accurate GPS data, which could introduce a spatial bias towards populated areas.”

The authors indirectly acknowledge the role of sampling bias in model predictions at line 163, however, this point could be clearer: there is sampling bias in the set of locations where HPAI has been observed and failure to adequately replicate this sampling bias in pseudo-absence data could lead covariates that are correlated with the observation distribution to appear to be correlated with the target distribution. This point is alluded to but should be clearly acknowledged to allow the reader to appropriately interpret your results. I understand the point being made on line 163 is that surveillance of HPAI in wild birds has become more structured and less opportunistic over time - if this is the case, a statement to this effect could replace "which could influence earlier data sets", which is a little ambiguous. The Authors acknowledge the role of sampling bias in lines 241-242 - this may be a good place to remind the reader that they have attempted to incorporate sampling bias through the selection of their pseudoabsence dataset, particularly for wild bird models.

We thank the Reviewer for this comment. We have now clarified in the text that observed data on HPAI occurrence are inherently influenced by heterogeneous surveillance efforts and that failure to replicate this bias in pseudo-absence sampling could effectively lead to misleading correlations with covariates associated with surveillance effort rather than true ecological suitability. We have now rephrased the related sentence as follows: “This decline may indicate a reduced bias in observation data: typically, dead wild birds are more frequently found near human-populated areas due to opportunistic detections, whereas more recent surveillance efforts have become increasingly proactive (Giacinti et al., 2024).”

Dhingra et al. aimed to account for the effect of mass vaccination of birds in China. This does not appear to be included in the updated models - is this a relevant covariate to consider in updated models? Are the models trained on pre-2020 data predicting to post-2020 given the same presence dataset as previous models? It may be helpful to provide a comment on this if we consider the pre-2020 models in this work to be representative of pre-2020 models as a cohort. Given the framing of the manuscript as an update to Dhingra et al., it may be useful for the authors to briefly summarise any differences between the existing models and updated models. Dhingra et al., also examine spatial extrapolation, which is not addressed here. Environmental extrapolation may be a useful metric to consider: are there areas where models are extrapolating that are predicted to be at high risk of HPAI transmission? Finally, they also provide some inset panels on global maps of model predictions - something similar here may also be useful.

We thank the Reviewer for these comments. Vaccination coverage is indeed a relevant covariate for HPAI suitability in domestic birds. However, we did not include this variable in our updated models for two reasons. First, comprehensive vaccination data were only available for China, so it is not possible to include this variable in a global model. Second, available data were outdated and vaccination strategies can vary substantially over time.

We however agree with the Reviewer that the Materials and Methods section did not clarify clearly the differences with Dhingra et al. (2016), and we now detail these differences at the beginning of the Materials and Methods section: “Our approach is similar to the one implemented by Dhingra and colleagues (2016). While Dhingra et al. (2016) developed their models only for domestic birds over the 2003-2016 periods, our models were developed for two host species separately (wild and domestic birds) and for two time periods (2016-2020 and 2020-2023).”

We also detail the main difference concerning the pseudo-absences sampling:  Dhingra and colleagues (2016) used human population density to sample pseudo-absences to reflect potential surveillance bias and also account for spatial filtering (min/max distances from presence). We adopted a similar strategy but also incorporated outbreak count per country or province (in the case of China and Russia) into the pseudo-absence sampling process to further account for within-country surveillance heterogeneity. We have now added these specifications in the Materials and Methods section: “To account for heterogeneity in AIV surveillance and minimise the risk of sampling pseudo-absences in poorly monitored regions, we restricted our analysis to countries (or administrative level 1 units in China and Russia) with at least five confirmed outbreaks. Unlike Dhingra et al. (2016), who sampled pseudoabsences across a broader global extent, our sampling was limited to regions with demonstrated surveillance activity. In addition, we adjusted the density of pseudo-absence points according to the number of reported outbreaks in each country or admin-1 unit, as a proxy for surveillance effort — an approach not implemented in this previous study.”

We have now also provided a comparison between the different outputs, particularly in the Results section: “Our findings were overall consistent with those previously reported by Dhingra and colleagues (Dhingra et al., 2016), who used data from January 2004 to March 2015 for domestic poultry. However, some differences were noted: their maps identified higher ecological suitability for H5 occurrences before 2016 in North America, West Africa, eastern Europe, and Bangladesh, while our maps mainly highlight ecologically suitable regions in China, South-East Asia, and Europe (Fig. S5). In India, analyses consistently identified high ecologically suitable areas for the risk of local H5Nx and H5N1 circulation for the three time periods (pre-2016, 2016-2020, and post-2020). Similar to the results reported by Dhingra and colleagues, we observed an increase in the ecological suitability estimated for H5N1 occurrence in South America's domestic bird populations post-2020. Finally, Dhingra and colleagues identified high suitability areas for H5Nx occurrence in North America, which are predicted to be associated with a low ecological suitability in the 2016-2020 models.”

We acknowledge that some regions predicted as highly suitable correspond to areas where extrapolation likely occurs due to limited or no recorded outbreaks. We have now added these specifications when discussing the resulting suitability maps obtained for domestic birds: “For H5Nx post-2020, areas of high predicted ecological suitability, such as Brazil, Bolivia, the Caribbean islands, and Jilin province in China, likely result from extrapolations, as these regions reported few or no outbreaks in the training data”, and, for wild birds: “Some of the areas with high predicted ecological suitability reflect the result of extrapolations. This is particularly the case in coastal regions of West and North Africa, the Nile Basin, Central Asia (Kyrgyzstan, Tajikistan, Uzbekistan), Brazil (including the Amazon and coastal areas), southern Australia, and the Caribbean, where ecological conditions are similar to those in areas where outbreaks are known to occur but where records of outbreaks are still rare.”

For wild birds (H5Nx, post-2020), high ecological suitability was predicted along the West and North African coasts, the Nile basin, Central Asia (e.g., Kyrgyzstan, Tajikistan, Uzbekistan), the Brazilian coast and Amazon region, Caribbean islands, southern Australia, and parts of Southeast Asia. Ecological suitability estimated in these regions may directly result from extrapolations and should therefore be interpreted cautiously.

We also added a discussion of the extrapolation for wild birds (in the Discussion section): “Interestingly, our models extrapolate environmental suitability for H5Nx in wild birds in areas where few or no outbreaks have been reported. This discrepancy may be explained by limited surveillance or underreporting in those regions. For instance, there is significant evidence that Kazakhstan and Central Asia play a role as a centre for the transmission of avian influenza viruses through migratory birds (Amirgazin et al., 2022; FAO, 2005; Sultankulova et al., 2024). However, very few wild bird cases are reported in EMPRES-i. In contrast, Australia appears environmentally suitable in our models, yet no incursion of HPAI H5N1 2.3.4.4b has occurred despite the arrival of millions of migratory shorebirds and seabirds from Asia and North America. Extensive surveillance in 2022 and 2023 found no active infections nor evidence of prior exposure to the 2.3.4.4b lineage (Wille et al., 2024; Wille and Klaassen, 2023).”

We agree that inset panels can be helpful for visualising global patterns. However, all resulting maps are available on the MOOD platform (https://app.mood-h2020.eu/core), which provides an interactive interface allowing users to zoom in and out, identify specific locations using a background map, and explore the results in greater detail. This resource is referenced in the manuscript to guide readers to the platform.

Related to my review of the manuscript's conceptualisation above, there are several inconsistencies in terminology in the manuscript - clearing these up may help to make the methods and their justification clearer to the reader. The "signal" that the models are estimating is variously described as "susceptibility" and "risk" (lines 179-180), "HPAI H5 ecological suitability" (line 78), "likelihood of HPAI occurrences" (line 139), "risk of HPAI circulation" (line 187), "distribution of occurrence data" (line 428). Each of these quantities has slightly different meanings and it is confusing to the reader that all of these descriptors are used for model output. "Likelihood of HPAI occurrences" is particularly misleading: ecological niche models predict high suitability for a species in areas that are similar to environments where it has previously been identified, without imposing constraints on species movement. It is intuitively far more likely that there will be HPAI occurrences in areas where the disease is already established than in areas where an introduction event is required, however, the niche models in this work do not include spatial relationships in their predictions.

We agree with the Reviewer’s comments. We have now modified the text so that in the Results section we refer to ecological suitability when referring to the outputs of the models. In the context of our Discussion section, we then interpret this ecological suitability in terms of risk, as areas with high ecological suitability being more likely to support local HPAI outbreaks.

I also caution the authors in their interpretation of the results of BRTs, which are correlative models, so therefore do not tell us what causes a response variable, but rather what is correlated with it. On Line 31, "correlated with" may be more appropriate than "influenced by". On Line 82, "correlated with" is more appropriate than "driving". This is particularly true given the authors' treatment of sampling bias.

We agree with the Reviewer’s comment and have now rephrased these sentences as follows: “The spatial distribution of HPAI H5 occurrences in wild birds appears to be primarily correlated with urban areas and open water regions” and “Our results provide a better understanding of HPAI dynamics by identifying key environmental factors correlated with the increase in H5Nx and H5N1 cases in poultry and wild birds, investigating potential shifts in their ecological niches, and improving the prediction of at-risk areas.”

The following sentences in line 201 are ambiguous: "For both H5Nx and H5N1, however, isolated areas on the risk map should be interpreted with caution. These isolated areas may result from sparse data, model limitations, or local environmental conditions that may not accurately reflect true ecological suitability." By "isolated", do the authors mean remote? Or ecologically dissimilar from the set of locations where HPAI has been detected? Or ecologically dissimilar from the set of locations in the joint set of HPAI detection locations and pseudo-absences? Or ecologically similar to the set of locations where HPAI has been detected but spatially isolated? These four descriptors are each slightly different and change the meaning of the sentences. "Model limitations" are also ambiguous - could the authors clarify which specific model limitations they are referring to here? Ultimately, the point being made is probably that a model may predict high ecological suitability for HPAI transmission in areas where the disease has not yet been identified, or where a model is extrapolating in environmental space, however, uncertainty in these predictions may be greater than uncertainty in predictions in areas that are represented in surveillance data. A clear comment on model uncertainty and how it is related to the surveillance dataset and the covariate dataset is currently missing from the manuscript and would be appropriate in this paragraph.

We understand the Reviewer’s concerns regarding these potential ambiguities, and have now rephrased these sentences as follows: “For both H5Nx and H5N1, certain areas of predicted high ecological suitability appear spatially isolated, i.e. surrounded by regions of low predicted ecological suitability. These areas likely meet the environmental conditions associated with past HPAI occurrences, but their spatial isolation may imply a lower risk of actual occurrences, particularly in the absence of nearby outbreaks or relevant wild bird movements.”

I am concerned by the wording of the following sentence: "The risk maps reveal that high-risk areas have expanded after 2020" (line 203). This statement could be supported by an acknowledgement of the assumptions the models make of the HPAI niche: are we saying that the niche is unchanged in environmental space and that there are now more geographic areas accessible to the pathogen, or that the niche has shifted or expanded, and that there are now more geographic areas accessible to the pathogen? The authors should review the sentence beginning on line 117: if models trained on data from the old timepoint predicting to the new timepoint are almost as good as models trained on data from the new timepoint predicting to the new timepoint, doesn't this indicate that the niche, as the models are able to capture it, has not changed too much?

We thank the Reviewer for this comment. The statement that "high-risk areas have expanded after 2020" indeed refers to an increase in the geographic extent of areas predicted to have high ecological suitability in models trained on post-2020 data. This expansion likely reflects new outbreak data from regions that had not previously reported cases, which in turn influenced model training.

However, models trained on pre-2020 data retain reasonable predictive performance when applied to post-2020 data (see the AUC results reported in Table S1), suggesting that the models suggest an expansion in the ecological suitability, but do not provide definitive evidence of a shift in the ecological niche. We have now added a statement at the end of this paragraph to clarify this point: “However, models trained on pre-2020 data maintained reasonable predictive performance when tested on post-2020 data, suggesting that the overall ecological niche of HPAI did not drastically shift over time.”

The final two paragraphs of the Results might be more helpful to include at the beginning of the Results, as the data discussed there are inputs to the models. Is it possible that the "rise in Shannon index for sea birds" that "suggests a broadening of species diversity within this category from 2020 onwards" is caused by the increasingly structured surveillance of HPAI in wild birds alluded to earlier in the Results? Is the "prevalence" discussed in line 226 the frequency of the families Laridae and Sulidae being represented in HPAI detection data? Or the abundance of the bird species themselves? The language here is a little ambiguous. Discussion of particular values of Shannon/Simpson indices is slightly out of context as the meanings of the indices are in the Methods - perhaps a brief explanation of the uses of Shannon/Simpson indices may be helpful to the reader here. It may also be helpful to readers who are not acquainted with avian taxonomy to provide common names next to formal names (for example, in brackets) in the body of the text, as this manuscript is published in an interdisciplinary journal.

We thank the Reviewer for these comments. First, we acknowledge that the paragraphs on species diversity and Shannon/Simpson indices describe important data, but we have chosen to present them after the main modelling results in order to maintain a logical narrative flow. Our manuscript first presents the ecological niche models and their predictive performance, followed by interpretations of the observed patterns, including changes in avian host diversity. Diversity indices were used primarily to support and contextualise the patterns observed in the modelling results.

For clarity, we have revised the relevant paragraphs in the Results (i) to briefly remind readers of the interpretation of the Shannon and Simpson indices (“Note that these indices reflect the diversity of bird species detected in outbreak records, not necessarily their abundance in the wild”) and (ii) to clarify that “prevalence” refers to the frequency of HPAI detection in wild bird species of the Laridae (gulls) and Sulidae (boobies and gannets) families, and not their total abundance. Family of birds includes several species, so the “common name” of a family can sometimes refer to species from other families. We have now added the common names for each family in the manuscript (even if we indeed acknowledge that “penguins” can be ambiguous).

In the Methods, it is stated: "To address the heterogeneity of AIV surveillance efforts and to avoid misclassifying low-surveillance areas as unsuitable for virus circulation, we trained the ecological niche models only considering countries in which five or more cases have been confirmed." However, it is not clear how this processing step prevents low-surveillance areas from being misclassified. If pseudo-absences are appropriately sampled, low-surveillance areas should be less represented in the pseudo-absence dataset, which should lead the models to be uncertain in their predictions of these areas. Perhaps "To address the heterogeneity of AIV surveillance efforts and to avoid sampling pseudo-absence data in realistically low-surveillance areas" is a more accurate introduction to the paragraph. I am not entirely convinced that it is appropriate to remove detection data where the national number of cases is low. This may introduce further sampling bias into the dataset.

We take the opportunity of the Reviewer’s comment to further clarify this important step aiming to mitigate bias associated with countries with substantial uncertainty in reporting and/or potentially insufficient HPAI surveillance data. While we indeed acknowledge that this procedure may exclude countries that had effective surveillance but low virus detection, we argue that it constitutes a relevant conservative approach to minimising the risk of sampling a significant number of pseudo-absence points in areas associated with relatively high yet undetected local HPAI circulation due to insufficient surveillance. Furthermore, given that five cases over two decades is a relatively low threshold — particularly for a highly transmissible virus such as AIV — non-detection or non-reporting remains a more plausible explanation than true absence.

To improve clarity, we have now revised the related sentence as follows: “To account for heterogeneity in AIV surveillance and minimise the risk of sampling pseudo-absences in poorly monitored regions, we restricted our analysis to countries (or administrative level 1 units in China and Russia) with at least five confirmed outbreaks.”

The reporting of spatial and temporal resolution of data in the manuscript could be significantly clearer. Is there a reason why human population density is downscaled to 5 arcminutes (~10km at the equator) while environmental covariate data has a resolution of 1km? The projection used is not reported. The authors should clarify the time period/resolution of the covariate data assigned to the occurrence dataset, for example, does "day LST annual mean" represent a particular year pre- or post-2020? Or an average over a number of years? Given that disease detections are associated with observation and reporting dates, and that there may be seasonal patterns in HPAI occurrence, it would be helpful to the reader to include this information when the eco-climatic indices are described. It would also be helpful to the reader to summarise the source, spatial and temporal resolution of all covariates in a table, as in Dhingra et al. Could the Authors clarify whether the duck density layer is farmed ducks or wild ducks?

The projection is WGS 84 (EPSG:4326) and the resolution of the output maps is around 0.0833 x 0.0833 decimal degrees (i.e. 5 arcmin, or approximately 10 km at the equator). We have now added these specifications in the text: “All maps are in a WGS84 projection with a spatial resolution of 0.0833 decimal degrees (i.e. 5 arcmin, or approximately 10 km at the equator).” In addition, we have now specified in the text that duck refers to domestic duck for clarity. 

Environmental variables retrieved for our analyses were here available as values averaged over distinct periods of time (for further detail see Supplementary Information Resources S1 — description and source of each environmental variable included in the original sets of variables — available at https://github.com/sdellicour/h5nx_risk_mapping). In future works, this would indeed be interesting to associate the occurrences to a specific season with the variables accordingly, specially for viruses such as HPAI which have been found correlated with seasons. However, we did not conduct this type of analysis in the present study, occurrences being here associated with averaged values of environmental data only.

In line 407, the authors state a number of pseudo-absence points used in modelling, relative to the number of presence points, without clear justification. Note that relative weights can be assigned to occurrence data in most ECN software (e.g., R package gbm), to allow many pseudo-absence points to be sampled to represent the full extent of probable surveillance effort and subsequently down-weighted.

We thank the Reviewer for this suggestion. We acknowledge that alternative approaches such as down-weighting pseudo-absence points could offer a certain degree of flexibility in representing surveillance effort. However, we opted for a fixed 1:3 ratio of pseudoabsences to presence points within each administrative unit to ensure a consistent and conservative sampling distribution. This approach aimed to limit overrepresentation of pseudoabsences in areas with sparse presence data, while still reflecting areas of likely surveillance.

There are a number of typographical errors and phrasing issues in the manuscript. A nonexhaustive list is provided below.

- Line 21: "its" should be "their" - Line 25: "HPAI cases"

Modifications have been done.

- Line 63: sentence beginning "However" is somewhat out of context - what is it (briefly) about recent outbreaks that challenge existing models?

We have now edited that sentence as follows: “However, recent outbreaks raise questions about whether earlier ecological niche models still accurately predict the current distribution of areas ecologically suitable for the local circulation of HPAI H5 viruses.”

- Lines 71 and 390: "AIV" is not defined in the text - Line 73: "do" ("are" and "what" are not capitalised)

Modifications have been done.

- Line 115: "predictability" should be "predictive capacity"

We have now replaced “predictability” by “predictive performance”.

- Line 180: omit "pinpointing"

- Line 192 sentence beginning "In India," should be re-worded: is the point that there are detections of HPAI here and the model predicts high ecological suitability?

- Line 195 sentence beginning "Finally," phrasing could be clearer: Dhingra et al. find high suitability areas for H5Nx in North America which are predicted to be low suitability in the new model.

- Line 237: omit "the" in "with the those"

- Line 374: missing "."

- Line 375: "and" should be "to" (the same goes for line 421)

- Line 448: Rephrase "Simpson index goes" to "The Simpson index ranges"

Modifications have been done.

Reviewer #2 (Public Review):

What is the justification for separating the dataset at 2020? Is it just the gap in-between the avian influenza outbreaks?

We chose 2020 as a cut-off based on a well-documented shift in HPAI epidemiology, notably the emergence and global spread of clade 2.3.4.4b, which may affect host dynamics and geographic patterns. We have now added this precision in the Materials and Methods section: “We selected 2020 as a cut-off point to reflect a well-documented shift in HPAI epidemiology, notably the emergence and global spread of clade 2.3.4.4b. This event marked a turning point in viral dynamics, influencing both the range of susceptible hosts and the geographical distribution of outbreaks.”

If the analysis aims to look at changing case numbers and distribution over time, surely the covariate datasets should be contemporaneous with the response?

Thank you for raising this important point. While we acknowledge that, ideally, covariates should match the response temporally, such high-resolution spatiotemporal environmental data were not available for most environmental factors considered in our ecological niche modelling analyses. While we used predictors (e.g., land-use variables, poultry density) that reflect long-term ecological suitability, we acknowledge that rather considering short-term seasonal variation could be an interesting perspective in future works, which is now explicitly stated in the Discussion section: “In addition, aligning outbreak occurrences with seasonally matched environmental variables could further refine predictions of HPAI risk linked to migratory dynamics.”

I would expect quite different immunity dynamics between domestic and wild birds as a function of lifespan and birth rates - though no obvious sign of that in the raw data. A statement on assumptions in that respect would be good.

Thank you for the comment. We agree that domestic and wild birds likely exhibit different immunity dynamics due to differences in lifespan, turnover rates, and exposure. However, our analyses did not explicitly model immunity processes, and the data did not show a clear signal of these differences.

Decisions and analytical tactics from Dhingra et al are adopted here in a way that doesn't quite convey the rationale, or justify its use here.

We thank the Reviewer for this observation. However, we do not agree with the notion that the rationale for using Dhingra et al.’s analytical framework is insufficiently conveyed. We adapted key components of their ecological niche modelling approach — such as the use of a boosted regression tree methodology and pseudo-absences sampling procedure — to ensure comparability with their previous findings, while also extending the analysis to additional time periods and host categories (wild vs. domestic birds). This framework aligns with the main objective of our study, which is to assess shifts in ecological suitability for HPAI over time and across host species, in light of changing viral dynamics.  

Please go over the manuscript and harmonise the language about the model target - it is usually referred to as cases, but sometimes the pathogen, and others the wild and domestic birds where the cases were discovered.

We agree and we have now modified the text to only use the “cases” or “occurrences” terminology when referring to the model inputs.

Is the reporting of your BRT implementation correct? The text suggests that only 10 trees were run per replicate (of which there were 10 per response (domestic/wild x H5N1 / H5Nx) x distinct covariate set), but this would suggest that the authors were scarcely benefiting from the 'boosting' part of the BRTs that allow them to accurately estimate curvilinear functions. As additional trees are added, they should still be improving the loss function, and dramatically so in the early stages. The authors seem heavily guided by Elith et al's excellent paper[1] explaining BRTs and the companion tutorial piece, but in that work, the recommended approach is to run an initial model with a relatively quick learning rate that achieves the best fit to the held-out data at somewhere over 1000 trees, and then to refine the model to that number of trees with a slower learning rate. If the authors did indeed run only 10 trees I think that should be explained.

For each model, we used the “gbm.step” function to fit boosted regression trees, initiating the process with 10 trees and allowing up to 10,000 trees in steps of 5. The optimal number of trees was automatically determined by minimising the cross-validated deviance, following the recommended approach of Elith and colleagues (2008, J. Anim. Ecol.). This setup allows the boosting algorithm to iteratively improve model performance while avoiding overfitting. These aspects are now further clarified in the Materials and Methods section: “All BRT analyses were run and averaged over 10 cross-validated replicates, with a tree complexity of 4, a learning rate of 0.01, a tolerance parameter of 0.001, and while considering 5 spatial folds. Each model was initiated with 10 trees, and additional trees were incrementally added (in steps of 5) up to a maximum of 10,000, with the optimal number selected based on cross-validation tests.”

I'm uncomfortable with the strong interpretation of changes in indices such as those for diversity in the case of bird species with detected cases of avian influenza, and the relative influence of covariates in the environmental niche models. In the former case, if surveillance effort is increasing it might be expected that more species will be found to be infected. In the latter, I'm just not convinced that these fundamentally correlative models can support the interpretation of changing epidemiology as asserted by authors. This strikes me as particularly problematic in light of static and in some cases anachronistic predictor sets.

We thank the Reviewer for drawing attention to how changes in surveillance intensity might influence our diversity estimates. We have now integrated a new analysis to evaluate the increase in the number of wild birds tested and discussed the potential impact of this increase on the comparison of the bird species diversity metrics presented in our study, which is now interpreted with more caution: “To evaluate whether the post-2020 increase in species diversity estimated for infected wild birds could result from an increase in the number of tests performed on wild birds, we compared European annual surveillance test counts (EFSA et al., 2025, 2019) before and after 2020 using a Wilcoxon rank-sum test. We relied on European data because it was readily accessible and offered standardised and systematically collected metrics across multiple years, making it suitable for a comparative analysis. Although borderline significant (p-value = 0.063), the Wilcoxon rank-sum test indeed highlighted a recent increase in the number of wild bird tests (on average >11,000/year pre-2020 and >22,000 post-2020), which indicates that the comparison of bird species diversity metrics should be interpreted with caution. However, such an increase in the number of tests conducted in the context of a passive surveillance framework would thus also be in line with an increase in the number of wild birds found dead and thus tested. Therefore, while the increase in the number of tests could indeed impact species diversity metrics such as the Shannon index, it can also reflect an absolute higher wild bird mortality in line with a broadened range of infected bird species.”

eLife Assessment

This study presents valuable findings regarding the basic molecular pathways leading to the cystogenesis of Autosomal Dominant Polycystic Kidney Disease, suggesting BICC1 functions as both a minor causative gene for PKD and a modifier of PKD severity. Solid data were supplied to show the functional and structural interactions between BICC-1 and PKD2 and their relevance to the pathogenesis of ADPKD, although the characterization of such interactions remains to be developed further and the clinical relevance is currently unclear.

Reviewer #1 (Public review):

In this manuscript, Tran et al. investigate the interaction between BICC1 and ADPKD genes in renal cystogenesis. Using biochemical approaches, they reveal a physical association between Bicc1 and PC1 or PC2 and identify the motifs in each protein required for binding. Through genetic analyses, they demonstrate that Bicc1 inactivation synergizes with Pkd1 or Pkd2 inactivation to exacerbate PKD-associated phenotypes in Xenopus embryos and potentially in mouse models. Furthermore, by analyzing a large cohort of PKD patients, the authors identify compound BICC1 variants alongside PKD1 or PKD2 variants in trans, as well as homozygous BICC1 variants in patients with early-onset and severe disease presentation. They also show that these BICC1 variants repress PC2 expression in cultured cells.

Overall, the concept that BICC1 variants modify PKD severity is plausible, the data are robust, and the conclusions are largely supported.

Comments on revision:

My comments have been mostly addressed.

Reviewer #2 (Public review):

Tran and colleagues report evidence supporting the expected yet undemonstrated interaction between the Pkd1 and Pkd2 gene products Pc1 and Pc2 and the Bicc1 protein in vitro, in mice, and collaterally, in Xenopus and HEK293T cells. The authors go on to convincingly identify two large and non-overlapping regions of the Bicc1 protein important for each interaction and to perform gene dosage experiments in mice that suggest that Bicc1 loss of function may compound with Pkd1 and Pkd2 decreased function, resulting in PKD-like renal phenotypes of different severity. These results led to examining a cohort of very early onset PKD patients to find three instances of co-existing mutations in PKD1 (or PKD2) and BICC1. Finally, preliminary transcriptomics of edited lines gave variable and subtle differences that align with the theme that Bicc1 may contribute to the PKD defects, yet are mechanistically inconclusive.

These results are potentially interesting, despite the limitation, also recognized by the authors, that BICC1 mutations seem exceedingly rare in PKD patients and may not "significantly contribute to the mutational load in ADPKD or ARPKD". The manuscript has several intrinsic limitations that must be addressed.

The manuscript contains factual errors, imprecisions, and language ambiguities. This has the effect of making this reviewer wonder how thorough the research reported and analyses have been.

Comments on revision:

My comments have been addressed.

Reviewer #3 (Public review):

Summary:

This study investigates the role of BICC1 in the regulation of PKD1 and PKD2 and its impact on cytogenesis in ADPKD. By utilizing co-IP and functional assays, the authors demonstrate physical, functional, and regulatory interactions between these three proteins.

Strengths:

(1) The scientific principles and methodology adopted in this study are excellent, logical, and reveal important insights into the molecular basis of cystogenesis.

(2) The functional studies in animal models provide tantalizing data that may lead to a further understanding and may consequently lead to the ultimate goal of finding a molecular therapy for this incurable condition.

(3) In describing the patients from the Arab cohort, the authors have provided excellent human data for further investigation in large ADPKD cohorts. Even though there was no patient material available, such as HUREC, the authors have studied the effects of BICC1 mutations and demonstrated its functional importance in a Xenopus model.

Weaknesses:

This is a well-conducted study and could have been even more impactful if primary patient material was available to the authors. A further study in HUREC cells investigating the critical regulatory role of BICC1 and potential interaction with mir-17 may yet lead to a modifiable therapeutic target.

Conclusion:<br /> The authors achieve their aims. The results reliably demonstrate the physical and functional interaction between BICC1 and PKD1/PKD2 genes and their products.

The impact is hopefully going to be manifold:

(1) Progressing the understanding of the regulation of the expression of PKD1/PKD2 genes.

Comments on revision:

My comments have been addressed and sorted.

Author response:

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

Reviewer #1 (Public review):

(1) The authors devote significant effort to characterizing the physical interaction between Bicc1 and Pkd2. However, the study does not examine or discuss how this interaction relates to Bicc1's well-established role in posttranscriptional regulation of Pkd2 mRNA stability and translation efficiency.

The reviewer is correct that the present study has not addressed the downstream consequences of uthis interaction considering that Bicc1 is a posttranscriptional regulator of Pkd2 (and potentially Pkd1). We think that the complex of Bicc1/Pkd1/Pkd2 retains Bicc1 in the cytoplasm and thus restrict its activity in participating in posttranscriptional regulation (see Author response image 1). We, however, do not yet have data to support this and thus have not included this model in the manuscript. Yet, we have updated the discussion of the manuscript to further elaborate on the potential mechanism of the Bicc1/Pkd1/Pkd2 complex.

We have updated the discussion to include a discussion on the potential consequences on posttranscriptional regulation by Bicc1.

Author response image 1.

Model of BICC1, PC1 and PC2 self-regulation. In this model Bicc1 acts as a positive regulator of PKD gene expression. In the presence of ‘sufficient’ amounts of PC1/PC2 complex, it is tethered to the complex and remains biologically inactive (Fig. 1A). However, once the levels of the PC1/PC2 complex are reduced, Bicc1 is now present in the cytoplasm to promote expression of the PKD proteins, thereby raising their levels (Fig. 4B), which then in turn will ‘shutdown’ Bicc1 activity by again tethering it to the plasma membrane.

(2) Bicc1 inactivation appears to downregulate Pkd1 expression, yet it remains unclear whether Bicc1 regulates Pkd1 through direct interaction or by antagonizing miR-17, as observed in Pkd2 regulation. This should be further examined or discussed.

This is a very interesting comment. Vishal Patel published that PKD1 is regulated by a mir-17 binding site in its 3’UTR (PMID: 35965273). We, however, have not evaluated whether BICC1 participates in this regulation. A definitive answer would require utilization of the mice described in above reference, which is beyond the scope of this manuscript. We, however, have revised the discussion to elaborate on this potential mechanism. 

We have updated the discussion to include a statement on the potential direct regulation of Pkd1 mRNA by Bicc1.

(3) The evidence supporting Bicc1 and ADPKD gene cooperativity, particularly with Pkd1, in mouse models is not entirely convincing, likely due to substantial variability and the aggressive nature of Bpk/Bpk mice. Increasing the number of animals or using a milder Bicc1 strain, such as jcpk heterozygotes, could help substantiate the genetic interaction.

We have initially performed the analysis using our Bicc1 complete knockout, we previously reported on (PMID 20215348) focusing on compound heterozygotes. Yet, similar to the Pkd1/Pkd2 compound heterozygotes (PMID 12140187) no cyst development was observed when we sacrificed the mice as late as P21. Our strain is similar to the above mentioned jcpk, which is characterized by a short, abnormal transcript thought to result in a null allele (PMID: 12682776). We thank the reviewer for pointing us to the reference showing the heterozygous mice exhibit glomerular cysts in the adults (PMID: 7723240). This suggestion is an interesting idea we will investigate. In general, we agree with the reviewer that a better understanding of the contribution of Bicc1 to the adult PKD phenotype will be critical. To this end, we are currently generating a floxed allele of Bicc1 that will allow us to address the cooperativity in the adult kidney, when e.g. crossed to the Pkd1^RC/RC mice. Yet, these experiments are beyond the timeframe for this revision. 

No changes were made in the revised manuscript. 

Reviewer #2 (Public review):

(1) These results are potentially interesting, despite the limitation, also recognized by the authors, that BICC1 mutations seem exceedingly rare in PKD patients and may not "significantly contribute to the mutational load in ADPKD or ARPKD". The manuscript has several intrinsic limitations that must be addressed. 

As mentioned above, the study was designed to explore whether there is an interaction between BICC1 and the PKD1/PKD2 and whether this interaction is functionally important. How this translates into the clinical relevance will require additional studies (and we have addressed this in the discussion of the manuscript).

(2) The manuscript contains factual errors, imprecisions, and language ambiguities. This has the effect of making this reviewer wonder how thorough the research reported and analyses have been. 

We respectfully disagree with the reviewer on the latter interpretation. The study was performed with rigor. We have carefully assessed the critiques raised by the reviewer. As presented below, most of the criticisms raised by the reviewer have been easily addressed in the revised version of the manuscript. Yet, none of the critiques seems to directly impact the overall interpretation of the data. 

Reviewer #1 (Recommendations for the authors):

(1) The manuscript requires further editing. For example, figure panels and legends are mismatched in Figure 1

We have corrected the labeling of Figure 1. 

(2) Y-axis units and values are inconsistent in Figures 4b-4g, Supplementary Figures S2e and S2f are not referenced in the text, genotypes are missing in Supplementary Figure S3f, and numerous typographical errors are present.

In respect to the y-axis in Figure 4b-g, the scale is different for each of them, but that is intentional as one would lose the differences if they were all scaled identically. But we have now mentioned this in the figure legend to make the reader aware of it. In respect to the Supplemental Figure S2e,f, we included the panels in the description of the mutant BICC1 lines, but unfortunately forgot to reference them. This has now been done.

We have updated the labeling of the Y-axis for the cystic indices adding “[%]” as the unit and updated the figure legend of Figure 4. We have included the genotypes in Supplementary Figure S3f. The Supplementary Figure S2e,f is now mentioned in the supplemental material (page 9, 2^nd paragraph). 

Reviewer #2 (Recommendations for the authors):

(1) Previous data from mouse, Xenopus, and zebrafish suggest a crucial role for the RNAbinding protein Bicc1 in the pathogenesis of PKD, although BICC1 mutations in human PKD have not been previously reported." The cited sources (and others that were not cited) link Bicc1 mutations to renal cysts, similar to a report by Kraus (PMID: 21922595) that the authors cite later. However, a more direct link to PKD was reported by Lian and colleagues using whole Pkd1 mice (PMID: 20219263) and by Gamberi and colleagues using Pkd1 kidneys and human microarrays (PMID: 28406902). Although relevant, neither is cited here, and only the former is cited later in the manuscript.

Thanks for pointing this out. We have added these three citations.

We have added these three citations (PMID: 21922595, PMID: 20219263 and PMID: 28406902) in the indicated sentence.

(2) In Figure 1B, the lanes do not seem to correspond among panels, particularly evident in the panel with myc-mBicc1. Hence, it is difficult to agree with the presented conclusions.

We have corrected the labeling of the lanes in Figure 1b.

(3) In the Figure 1 legend: "(g) Western blot analysis following co-IP experiments, using an anti-mouse Bicc1 or anti-goat PC2 antibody as bait, identified protein interactions between endogenous PC2 and BICC1 in UCL93 cells. Non-immune goat and mouse IgG were included as a negative control." There is no mention of panel H, although this reviewer can imagine what the authors meant. The capitalization differs in the figure and legend. More troublingly, in panel G, a non-defined star indicates a strong band present in both immune and non-immune control.

We have corrected the figure legend of Figure 1 and clarified the non-specific band in the figure legend.

(4) In Figure 4, the authors do not show the matched control for the Bicc1 Pkd1 interaction in panel d, nor do they show a scale bar in either a) or d). Thus, the phenotypic severity cannot be properly assessed.

Thanks for pointing out the missing scale bars, which have now been added. In respect to the two kidneys shown in Figure 4d, the two kidneys shown are from littermates to illustrate the kidney size in agreement with the cumulative data shown in Figure 4e. Unfortunately, this litter did not have a wildtype control. As the data analysis in Figure 4e is based on littermates, mixing and matching kidneys of different litters does not seem appropriate. Thus, we have omitted showing a wildtype control in this panel. However, the size of the wildtype kidney can be seen in Figure 4a.

We have added the scale bar to both panels and have updated the figure legend to emphasize that the kidneys shown are from littermates and that no wildtype littermate was present in this litter.

(5) "Surprisingly, an 8-fold stronger interaction was observed between full-length PC1 and myc-mBicc1-ΔKH compared to mycmBicc1 or myc-mBicc1-ΔSAM." Assuming all the controls for protein folding and expression levels have been carried out and not shown/mentioned, this sentence seems to contradict the previous statement that Bicc1deltaSAM reduced the interaction with PC1 by 55%. Because the full length and SAM deletion have different interaction strengths, the latter sentence makes no sense.

The reduction in the levels of myc-mBicc1-ΔSAM compared to wildtype mycmBicc1 in respect to PC1 binding was not significant. We have clarified this in the text.

We have corrected the sentence and modified the Figure accordingly. 

(6) Imprecise statements make a reader wonder how to interpret the data: "More than three independent experiments were analyzed." Stating the sample size or including it in the figure would save space and improve confidence in the data presented.

We have stated the exact number of animals per conditions above each of the bars.

(7) "Next, we performed a similar mouse study for Pkd1 by reducing the gene dose of Pkd1 postnatally in the collecting ducts using a Pkhd1-Cre as previously described40" What did the authors mean?

The reference was included to cite the mouse strain, but realized that it can be mis-interpreted that the exact experiments has been performed previously. We have clarified this in the text.

We have reworded the sentence to avoid misinterpretation. 

(8) The authors examined the additive effects of knocking down Bicc1, Pkd1, and Pkd2 with morpholinos in Xenopus and, genetically, in mice. While the Bicc1[+/-] Pkd1 or 2[+/-] double heterozygote mice did not show phenotypes, the authors report that the Bicc1[-/-] Pkd1 or 2 [+/-] did instead show enlarged kidneys. What is the phenotype of a Bicc1[+/-] Pkd1 or 2 [-/-]? What we learn from the author's findings among the PKD population suggests that the latter situation would be potentially translationally relevant.

The mouse experiments were designed to address a cooperativity between Bicc1 and either Pkd1 or Pkd2 and whether removal of one copy of Pkd1 or Pkd2 would further worsen the Bicc1 cystic kidney phenotype. Thus, the parental crosses were chosen to maximize the number of animals obtained for these genotypes. Unfortunately, these crosses did not yield the genotypes requested by the reviewer. To address the contribution of Bicc1 towards the PKD population, we will need to perform a different cross, where we eliminate Pkd1 or Pkd2 in a floxed background of Bicc1 postnatally in adult mice. While we are gearing up to perform such an experiment, this is timewise beyond the scope of the manuscript. In addition, please note that we have addressed the question about the translation towards the PKD population already in the discussion of the original submission (page 13/14, last/first paragraph).

No changes have been made to the revised version of the manuscript.

(9) How do the authors interpret the milder effects of the Bicc1[-/-] Pkd1[+/-] compared to Bicc1[-/-] Pkd2[+/-] relative to the respective protein-protein interactions?

The milder effects are due to the nature of the crosses. While the Pkd2 mutant is a germline mutation, the Pkd1 mutant is a conditional allele eliminating Pkd1 only in the collecting ducts of the kidney. As such, we spare other nephron segments such as the proximal tubules, which also significantly contribute to the cyst load. As such these mouse data support the interaction between Pkd1 and Pkd2 with Bicc1, but do not allow us to directly compare the outcomes. While this was mentioned in the previous version of the manuscript, we have expanded on this in the revised version of the manuscript.

We have expanded the results section in the revised version of the manuscript highlighting that the two different approaches cannot be directly compared.

(10) How do the authors interpret that the strong Bicc1[Bpk] Pkd1 or Pkd2 double heterozygote mice did not have defects and "kidneys from Bicc1+/-:Pkd2+/- did not exhibit cysts (data not shown)", when the VEO PKD patients and - although not a genetic reduction - also the morpholino-treated Xenopus did?

VEO PKD patients are characterized by a loss of function of PKD1 or PKD2 and – as we propose in this manuscript - that BICC1 further aggravates the phenotype. Yet, we do not address either in the mouse or Xenopus experiments whether BICC1 is a genetic modifier. We are simply addressing whether the two genes show a genetic interaction. In the mouse studies, we eliminate one copy of Pkd1 or Pkd2 in the background of a hypomorphic allele of Bicc1. Similarly, in the Xenopus experiments, we employ suboptimal doses of the morpholino oligomers, i.e., concentrations that did not yield a phenotypic change and then asked whether removing both together show cooperativity. It is important to state that this is based on a biological readout and not defined based on the amount of protein. While we have described this already in the original manuscript (page 7, first paragraph), we have amended our description of the Xenopus experiment to make this even clearer. 

Finally, we agree with the reviewer that if we were to address whether Bicc1 is a modifier of the PKD phenotype in mouse, we would need to reduce Bicc1 function in a Pkd1 or Pkd2 mutants. Yet, we have recognized this already in the initial version of the manuscript in the discussion (page 14, first paragraph).

We have expanded the results section when discussing the suboptimal amounts of the morpholino oligos (Page 6, 1^st paragraph).

(11) Unclear: "While variants in BICC1 are very rare, we could identify two patients with BICC1 variants harboring an additional PKD2 or PKD1 variant in trans, respectively." Shortly after, the authors state in apparent contradiction that "the patients had no other variants in any of other PKD genes or genes which phenocopy PKD including PKD1, PKD2, PKHD1, HNF1s, GANAB, IFT140, DZIP1L, CYS1, DNAJB11, ALG5, ALG8, ALG9, LRP5, NEK8, OFD1, or PMM2."

The reviewer is correct. This should have been phrased differently. We have now added “Besides the variants reported below” to clarify this more adequately.

The sentence was changed to start with “Besides the variants reported below, […].”

(12) "The demonstrated interaction of BICC1, PC1, and PC2 now provides a molecular mechanism that can explain some of the phenotypic variability in these families." How do the authors reconcile this statement with their reported ultra-rare occurrence of the BICC1 mutations?

As mentioned in the manuscript and also in response to the other two reviewers, Bicc1 has been shown to regulate Pkd2 gene expression in mice and frogs via an interaction with the miR-17 family of microRNAs. Moreover, the miR-17 family has been demonstrated to be critical in PKD (PMID: 30760828, PMID: 35965273, PMID: 31515477, PMID: 30760828). In fact, both other reviewers have pointed out that we should stress this more since Bicc1 is part of this regulatory pathway. Future experiments are needed to address whether Bicc1 contributes to the variability in ADPKD onset/severity. Yet, this is beyond the scope of this study. 

Based on the comments of the two other reviewers we have further addressed the Bicc1/miR-17 interaction.

(13) The manuscript should use correct genetic conventions of italicization and capitalization. This is an issue affecting the entire manuscript. Some exemplary instances are listed below.

(a) "We also demonstrate that Pkd1 and Pkd2 modifies the cystic phenotype in Bicc1 mice in a dose-dependent manner and that Bicc1 functionally interacts with Pkd1, Pkd2 and Pkhd1 in the pronephros of Xenopus embryos." Genes? Proteins?

The data presented in this section show that a hypomorphic allele of Bicc1 in mouse and a knockdown in Xenopus yields this. As both affect the proteins, the spelling should reflect the proteins.

No changes have been made in the revised manuscript.

(b) The sentence seems to use both the human and mouse genetic capitalization, although it refers to experiments in the mouse system “to define the Bicc1 interacting domains for PC2 (Fig. 2d,e). Full-length PC2 (PC2-HA) interacted with full-length myc-mBICC1.”

We agree with the review that stating the species of the molecules used is critical, we have adapted a spelling of Bicc1, where BICC1 is the human homologue, mBicc1 is the mouse homologue and xBicc1 the Xenopus one.

We have highlighted the species spelling in the methods section and labeled the species accordingly throughout the manuscript and figures. 

(14) “Together these data supported our biochemical interaction data and demonstrated that BICC1 cooperated with PKD1 and PKD2.” Are the authors implying that these results in mice will translate to the human protein?

We agree that we have not formally shown that the same applies to the human proteins. Thus, we have changed the spelling accordingly.

We have revised the capitalization of the proteins. 

(15) The text is often unclear, terse, or inconsistent.

(a) “These results suggested that the interaction between PC1 and Bicc1 involves the SAM but not the KH/KHL domains (or the first 132 amino acids of Bicc1). It also suggests that the N-terminus could have an inhibitory effect on PC1-BICC1 association.” How do the authors define the N-terminus? The first 132 aa? KH/KHL domains?

This was illustrated in the original Figure 2A. The DKH constructs lack the first 351 amino acids. 

To make this more evident, we have specified this in the text as well.

(b) Similarly, the authors state below, "Unlike PC1, PC2 interacted with mycmBICC1ΔSAM, but not myc-mBICC1-ΔKH suggesting that PC2 binding is dependent on the N-terminal domains but not the SAM domain." It is unclear if the authors refer to the KH/KHL domains or others. Whatever the reference to the N-terminal region, it should also be consistent with the section above.

This is now specified in the text.

(c) Unclear: "We have previously demonstrated that Pkd2 levels are reduced in a complete Bicc1 null mice,22 performing qRT-PCR of P4 kidneys (i.e. before the onset of a strong cystic phenotype), revealed that Bicc1, Pkd1 and Pkd2 were statistically significantly down9 regulated (Fig. 4h-j)".

We have changed the text to clarify this. 

(d) “Utilizing recombinant GST domains of PC1 and PC2, we demonstrated that BICC1 binds to both proteins in GST-pulldown assays (Fig. 1a, b)." GST-tagged domains? Fusions?

We have changed the text to clarify this. 

(e) "To study the interaction between BICC1, PKD1 and PKD2 we combined biochemical approaches, knockout studies in mice and Xenopus, genetic engineered human kidney cells" > genetically engineered.

We have changed the text to clarify this.

(f) Capitalization (e.g., see Figure S3, ref. the Bpk allele) and annotation (e.g., Gly821Glu and G821E) are inconsistent.

We have homogenized the labeling of the capitalization and annotations throughout the manuscript. 

(g) What do the authors mean by "homozygous evolutionarily well-conserved missense variant"?

We have changed this is the revised version of the manuscript. 

Reviewer #3 (Public review/Recommendations to the authors):

(1) A further study in HUREC cells investigating the critical regulatory role of BICC1 and potential interaction with mir-17 may yet lead to a modifiable therapeutic target.

(2) This study should ideally include experiments in HUREC material obtained from patients/families with BICC1 mutations and studying its effects on the PKD1/2 complex in primary cell lines.

This is an excellent suggestion. We agree with the reviewer that it would have been interesting to analyze HUREC material from the affected patients. Unfortunately, besides DNA and the phenotypic analysis described in the manuscript neither human tissue nor primary patient-derived cells collected once the two patients with the BICC1 p.Ser240Pro variant passed away.

No changes to the revised manuscript have been made to address this point.

(3) Please remove repeated words in the following sentence in paragraph 2 of the introduction: "BICC1 encodes an evolutionarily conserved protein that is characterized by 3 K-homology (KH) and 2 KH-like (KHL) RNA-binding domains at the N-terminus and a SAM domain at the C-terminus, which are separated by a by a disordered intervening sequence (IVS).23-28".

This has been changed.

eLife Assessment

This study provides new single-cell multi-omics datasets that may be useful in the study of early cardiac lineages. However, the authors' conclusions regarding the mutual regulation of key regulators for cardiac specification and new cardiac lineage trajectories are inadequately supported by persuasive analysis and do not align with prior published studies. If revised to address the serious caveats adequately, the findings may be of interest to researchers in the field of cardiac development and congenital heart disease.

Reviewer #1 (Public review):

Summary:

In this study, the authors identified and described the transcriptional trajectories leading to CMs during early mouse development, and characterized the epigenetic landscapes that underlie early mesodermal lineage specification.

The authors identified two transcriptomic trajectories from a mesodermal population to cardiomyocytes, the MJH and PSH trajectories. These trajectories are relevant to the current model for the First Heart Field (FHF) and the Second Heart Field (SHF) differentiation. Then, the authors characterized both gene expression and enhancer activity of the MJH and PSH trajectories, using a multiomics analysis. They highlighted the role of Gata4, Hand1, Foxf1, and Tead4 in the specification of the MJH trajectory. Finally, they performed a focused analysis of the role of Hand1 and Foxf1 in the MJH trajectory, showing their mutual regulation and their requirement for cardiac lineage specification.

Strengths:

The authors performed an extensive transcriptional and epigenetic analysis of early cardiac lineage specification and differentiation which will be of interest to investigators in the field of cardiac development and congenital heart disease. The authors considered the impact of the loss of Hand1 and Foxf1 in-vitro and Hand1 in-vivo.

Weaknesses:

The authors used previously published scRNA-seq data to generate two described transcriptomic trajectories.

(1) Details of the re-analysis step should be added, including a careful characterization of the different clusters and maker genes, more details on the WOT analysis, and details on the time stamp distribution along the different pseudotimes. These details would be important to allow readers to gain confidence that the two major trajectories identified are realistic interpretations of the input data.

The authors have also renamed the cardiac trajectories/lineages, departing from the convention applied in hundreds of papers, making the interpretation of their results challenging.

(2) The concept of "reverse reasoning" applied to the Waddington-OT package for directional mass transfer is not adequately explained. While the authors correctly acknowledged Waddington-OT's ability to model cell transitions from ancestors to descendants (using optimal transport theory), the justification for using a "reverse reasoning" approach is missing. Clarifying the rationale behind this strategy would be beneficial.

(3) As the authors used the EEM cell cluster as a starting point to build the MJH trajectory, it's unclear whether this trajectory truly represents the cardiac differentiation trajectory of the FHF progenitors:<br /> - This strategy infers that the FHF progenitors are mixed in the same cluster as the extra-embryonic mesoderm, but no specific characterization of potential different cell populations included in this cluster was performed to confirm this.

- The authors identified the EEM cluster as a Juxta-cardiac field, without showing the expression of the principal marker Mab21l2 per cluster and/or on UMAPs.

- As the FHF progenitors arise earlier than the Juxta-cardiac field cells, it must be possible to identify an early FHF progenitor population (Nkx2-5+; Mab21l2-) using the time stamp. It would be more accurate to use this FHF cluster as a starting point than the EEM cluster to infer the FHF cardiac differentiation trajectory.

These concerns call into question the overall veracity of the trajectory analysis, and in fact, the discrepancies with prior published heart field trajectories are noted but the authors fail to validate their new interpretation. Because their trajectories are followed for the remainder of the paper, many of the interpretations and claims in the paper may be misleading. For example, these trajectories are used subsequently for annotation of the multiomic data, but any errors in the initial trajectories could result in errors in multiomic annotation, etc, etc.

(4) As mentioned in the discussion, the authors identified the MJH and PSH trajectories as non-overlapping. But, the authors did not discuss major previously published data showing that both FHF and SHF arise from a common transcriptomic progenitor state in the primitive streak (DOI: 10.1126/science.aao4174; DOI: 10.1007/s11886-022-01681-w). The authors should consider and discuss the specifics of why they obtained two completely separate trajectories from the beginning, how these observations conflict with prior published work, and what efforts they have made at validation.

(5) Figures 1D and E are confusing, as it's unclear why the authors selected only cells at E7.0. Also, panels 1D 'Trajectory' and 'Pseudotime' suggest that the CM trajectory moves from the PSH cells to the MJH. This result is confusing, and the authors should explain this observation.

(6) Regarding the PSH trajectory, it's unclear how the authors can obtain a full cardiac differentiation trajectory from the SHF progenitors as the SHF-derived cardiomyocytes are just starting to invade the heart tube at E8.5 (DOI: 10.7554/eLife.30668).

The above notes some of the discrepancies between the author's trajectory analysis and the historical cardiac development literature. Overall, the discrepancies between the author's trajectory analysis and the historical cardiac development literature are glossed over and not adequately validated.

(7) The authors mention analyzing "activated/inhibited genes" from Peng et al. 2019 but didn't specify when Peng's data was collected. Is it temporally relevant to the current study? How can "later stage" pathway enrichment be interpreted in the context of early-stage gene expression?

(8) Motif enrichment: cluster-specific DAEs were analyzed for motifs, but the authors list specific TFs rather than TF families, which is all that motif enrichment can provide. The authors should either list TF families or state clearly that the specific TFs they list were not validated beyond motifs.

(9) The core regulatory network is purely predictive. The authors again should refrain from language implying that the TFs in the CRN have any validated role.

Regarding the in vivo analysis of Hand1 CKO embryos, Figures 6 and 7:

(10) How can the authors explain the presence of a heart tube in the E9.5 Hand1 CKO embryos (Figure 6B) if, following the authors' model, the FHF/Juxta-cardiac field trajectory is disrupted by Hand1 CKO? A more detailed analysis of the cardiac phenotype of Hand1 CKO embryos would help to assess this question.

(11) The cell proportion differences observed between Ctrl and Hand1 CKO in Figure 6D need to be replicated and an appropriate statistical analysis must be performed to definitely conclude the impact of Hand1 CKO on cell proportions.

(12) The in-vitro cell differentiations are unlikely to recapitulate the complexity of the heart fields in-vivo, but they are analyzed and interpreted as if they do.

(13) The schematic summary of Figure 7F is confusing and should be adjusted based on the following considerations:<br /> (a) the 'Wild-type' side presents 3 main trajectories (SHF, Early HT and JCF), but uses a 2-color code and the authors described only two trajectories everywhere else in the article (aka MJH and PSH). It's unclear how the SHF trajectory (blue line) can contribute to the Early HT, when the Early HT is supposed to be FHF-associated only (DOI: 10.7554/eLife.30668). As mentioned previously in Major comment 3., this model suggests a distinction between FHF and JCF trajectories, which is not investigated in the article.<br /> (b) the color code suggests that the MJH (FHF-related) trajectory will give rise to the right ventricle and outflow tract (green line), which is contrary to current knowledge.

Minor comments:

(1) How genes were selected to generate Figure 1F? Is this a list of top differentially expressed genes over each pseudotime and/or between pseudotimes?

(2) Regarding Figure 1G, it's unclear how inhibited signaling can have an increased expression of underlying genes over pseudotimes. Can the authors give more details about this analysis and results?

(3) How do the authors explain the visible Hand1 expression in Hand1 CKO in Figure S7C 'EEM markers'? Is this an expected expression in terms of RNA which is not converted into proteins?

(4) The authors do not address the potential presence of doublets (merged cells) within their newly generated dataset. While they mention using "SCTransform" for normalization and artifact removal, it's unclear if doublet removal was explicitly performed.

Comments on revised version:

Summary:

The authors have not addressed the major philosophical problems with the initial submission. They interpret their data without care to conform to years of prior publications in the field. This causes the authors to draw fanciful conclusions that are highly likely to be inaccurate (at best).

Q1R1: The authors gave more details about the characterization of cell types and the two identified trajectories.

a) It remains unclear how the authors generated this list. Are they manually selected genes based on relevant literature or an unbiased marker gene identification analysis? Either references should be added, or the bioinformatics explanation should be included in the method section.<br /> b) Revised text satisfies the comment.<br /> c) Revised text satisfies the comment.

Other comments:

Figure 1F: left annotation needs to be corrected (two "JCF specific").

Q2R1: Revised text satisfies the comment.

Q3R1 (1): Revised text satisfies the comment.

Q3R1 (2): a) The explanation of how the authors built the JCF trajectory makes sense and the renaming from "MJH" to "JCF" is correct and better represents the identification that was made using time points from E7.5 to E8.5. However, the explanation given does not answer our original question. Our original comment asked about the FHF differentiation trajectory. The authors built the "MJH" trajectory as the combined "FHF/JCF" trajectory, however, it is not directly established whether the FHF and JCF progenitor differentiation trajectories are the same. The authors did not directly try to identify the FHF and JCF trajectories separately using appropriate real time windows but only assumed that they were the same. Every link between JCF and FHF trajectories assuming that they are shared without prior identification of the FHF progenitor differentiation trajectory should be removed from the manuscript (e.g. page 4: "namely the JCF trajectory (the Hand1-expressing early extraembryonic mesoderm - JCF and FHF - CM)").

b) Adding the Mab21l2 ICA plot satisfies the comment.

c) The explanation given by the authors regarding the FHF trajectory analysis is missing important details. The authors started the reverse trajectory analysis from E7.75 cardiomyocytes as being the FHF.

- The authors should be mindful with the distinction between FHF progenitors and FHF-derived cardiomyocytes.<br /> - It is unclear whether cells called after the starting point (E7.75 CMs) in the reverse FHF trajectory, were collected prior E7.75. Can the authors add more details, and a real time point distribution along the FHF pseudotime to their analysis? Also, what cells belong to the FHF trajectory after the E7.75 CMs in the reverse direction? These cells should be shown as in Figure 1A and 1B for the JCF and SHF trajectories.<br /> - As the FHF arises first and differentiates into the cardiac crescent prior to or at the same time the JCF and SHF emerge, it is impossible for late progenitors (JCF and SHF) to contribute to the early FHF progenitor pool. Therefore, the observation that "both JCF and SHF lineages contribute to the early FHF progenitor population" can not be correct. It is also not what Dominguez et al showed. This misinterpretation goes against the current literature (e.g. DOI: 10.1038/ncb3024) and will leads to confusion.

Q4R1: Revised text and figure satisfy the comment.

Q5R1: The answer satisfies the comment.

Q6R1: a) The authors did not address the question and did not change their language in the manuscript. As SHF-derived cardiomyocytes are missing (because they are generated after E8.5), the part of the SHF trajectory going from SHF progenitors to the E8.5 heart tube must be inaccurate.

b) The authors correctly mentioned, both JCF and SHF will contribute to the four-chamber heart. However, as the dataset used by the authors spans only to E8.5 (which is days before the completion of the four-chamber heart), and all SHF and the vast majority of JCF contributions don't reach the heart until after E8.5, any claims about trajectories from JCF/SHF progenitor pools to cardiomyocytes should be removed because they do not correspond to prior published and accepted work.

Q7R1: Especially because gene expression levels change over time, the authors might have considered genes as specific and restricted to a pathway based on their expression at a given time (e.g. later time), but at another time (e.g. earlier time), the same genes could have another expression pattern and not be pathway-specific anymore.

Q8R1: Revised text satisfies the comment.

Q9R1: Revised text satisfies the comment.

Q10R1: Thank you for analyzing deeper the cardiac phenotype of the Hand1 cKO embryos.

Regarding the presence of a heart tube, while, following the authors' model the FHF/JCF trajectory is disrupted:

- Renaming the "MSH" to "JCF" is more accurate to the data shown by the authors as mainly the EEM is altered after Hand1 cKO.<br /> - The presence of the heart tube suggests that even if the JCF is altered, the FHF can still produce a cardiac crescent and a heart tube (as observed in Hand1-null embryos DOI: 10.1038/ng0398-266). The schematic Figure 7F suggests that only the SHF contribution will allow the formation of the heart tube. This unorthodox idea would need to be assessed by an alternate approach. More likely is that the model simply ignores the FHF contribution (the most important up to E8.5). The schematic is therefore incomplete and inaccurate and should be removed or edited to correspond to the prior literature.

Q11R1: It is unclear what "replicates" mean in the authors' answer, as if they have been pooled without replicate-specific barcodes they are no longer replicates and should be considered as a single sample. This should be explicitly written in the method section.<br /> Thank you for your IF staining/quantification. If DAPI was used, it should be written in the figure caption.

Q12R1: Revised text satisfies the comment.

Q13R1: The answer given by the authors did not satisfy the comment because of the following:

- The authors investigated two differentiation trajectories (JCF and SHF) in the article but Figure 7F presents three trajectories (JCF, SHF, and Early HT). The "Early HT" is neither mentioned, nor discussed in the manuscript.<br /> - Figure 7F suggests that the "Early HT" trajectory corresponds to a combination of the SHF and JCF trajectories but does not mention the early FHF trajectory. This is going against the current literature. This relates to the comments of Q10R1.<br /> - As the authors rightly point out, the SHF will be contributing to the heart tube, but through a cell invasion of the already differentiated heart tube (10.1016/j.devcel.2023.01.010). Our prior comments did not question the implication of the SHF to the looping and ballooning process but mentioned that the heart tube arises before the invasion from SHF and is FHF-derived. Figure 7F in the context of Hand1-null suggest that the heart tube will form from the SHF lineage, which is confusing as the SHF is known to contribute by invasion of the (already-formed) FHF-derived heart tube. The FHF lineage is missing from the authors' model.<br /> - In the revised manuscript, the FHF trajectory analysis is still unclear and suggests that the JCF and SHF progenitors contribute to the FHF progenitor which is going against current literature. This relates to the comments of Q3R1 (2).

Overall, the schematic Figure 7F is very confusing as it does not follow already published data without being fully validated and therefore is inaccurate and misleading.

Minor comments:

The answers satisfy the minor comments.

Reviewer #2 (Public review):

Summary of goals:

The aims of the study were to identify new lineage trajectories for the cardiac lineages of the heart, and to use computational and cell and animal studies to identify and validate new gene regulatory mechanisms involved in these trajectories.

Strengths:

Overall: the study addresses the long standing yet still not fully answered questions of what drives the earliest specification mechanisms of the heart lineages. The introduction demonstrates a good understanding of the relevant lineage trajectories that have been previously established, and the significance of the work is well described. The study takes advantage of several recently published data sets and attempts t use these in combination to uncover any new mechanisms underlying early mesoderm/cardiac specification mechanisms. A strength of the study is the use of an in vitro model system (mESCs) to assess the functional relevance of the key players identified in the computational analysis, including innovative technology such as CRISPR-guided enhancer modulations. Lastly, the study generates mesoderm-specific Hand1 LOF embryos and assesses the differentiation trajectories in these animals, which represents a strong complementary approach to the in vitro and computational analysis earlier in the paper. The manuscript is clearly written and the methods section is detailed and comprehensive.

Comments and Weaknesses:

I unfortunately still have the same concerns I had for the original submission. There are many strong claims about lineage trajectories and population relationships that are based purely on the analysis of a number of datasets, some published and a few new datasets.

The methods used involve significant input bias, and some of the less user-biased approaches, such as the new RNA velocity analysis on the JCF/SHF trajectories, are included only in the response to reviewers but not in the manuscript (R1R2), as far as I can tell. This analysis does not seem to suggest that CMs are generated from both trajectories, but it is difficult to know as they provide so little information on what exactly they did.<br /> The conclusions are particularly concerning not only because they are largely based on computational analysis, but also because they contradict well-described concepts (which are supported by in vivo lineage tracing).<br /> I want to give them credit for having done some additional experiments. That said, the new data added for the validation of some of their concepts (mESC Fig 5F and embryos Fig S8C) do not strengthen their conclusions in my opinion. The mESC data were not quantified, and the embryo data looks like quantifications were done in different planes of a single embryo, but it's hard to tell as little information is provided. Even with accurate quantification, I believe the IF analysis for VIM in Hand1 cKO embryos is not sufficient to back up their claims on the role of Hand1 in driving the JCF lineage.

Reviewer #3 (Public review):

In this manuscript, the Xie et al. delineate two cardiac lineage trajectories using pseudo-time and epigenetic analyses, tracing development from E6.5 to E8.5, culminating in cardiomyocytes (CMs). The authors propose that mutual regulation between the transcription factors Hand1 and Foxf1 plays a role in specifying a first cardiac lineage.

Following the first round of revision, the authors have renamed their EEM-JCF/FHF (MJH) and PM-SHF (PSH) trajectories JCF and SHF. However, their use of this terminology is confusing. The so-called JCF trajectory appears to represent a mixture of JCF and FHF, as Hand1-expressing early extraembryonic mesoderm contributes to FHF-derived cardiomyocytes (e.g., HCN4+, Tbx5+). The authors then argue that JCF arises from Hand1+ cells and is therefore distinct from FHF, yet elsewhere suggest that both JCF and SHF contribute to FHF. This introduces conceptual inconsistencies.

Furthermore, the expression of Hand1, Foxf1, and Bmp4 in the lateral plate mesoderm complicates the assertion that JCF is distinct from FHF (Development 2015; 142: 3307-3320; Nat Rev Mol Cell Biol, https://www.nature.com/articles/nrm2618; Circ Res 2021, https://doi.org/10.1161/CIRCRESAHA.121.318943). Mab21l2 expression also overlaps with the cardiac crescent. The designation of Tbx20 as a "key JCF-specific gene" is problematic, why should it not equally be considered an FHF-specific marker (https://pmc.ncbi.nlm.nih.gov/articles/PMC10629681)? Perhaps the JCF trajectory represent a subset of FHF. A designation such as "JCF/FHF" may therefore be more appropriate.

In Figure 1A, the decision to define a single CM state as the endpoint of both trajectories is also problematic. FHF and SHF are known to give rise to distinct CM subtypes, yet in the authors' reconstruction both lineages converge on one CM population. This was the point raised in Question 1 of my initial review. If both trajectories converge on the same CM state, are they truly independent lineages? This interpretation remains unclear and potentially misleading.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public Review):

Summary:

In this study, the authors identified and described the transcriptional trajectories leading to CMs during early mouse development, and characterized the epigenetic landscapes that underlie early mesodermal lineage specification.

The authors identified two transcriptomic trajectories from a mesodermal population to cardiomyocytes, the MJH and PSH trajectories. These trajectories are relevant to the current model for the First Heart Field (FHF) and the Second Heart Field (SHF) differentiation. Then, the authors characterized both gene expression and enhancer activity of the MJH and PSH trajectories, using a multiomics analysis. They highlighted the role of Gata4, Hand1, Foxf1, and Tead4 in the specification of the MJH trajectory. Finally, they performed a focused analysis of the role of Hand1 and Foxf1 in the MJH trajectory, showing their mutual regulation and their requirement for cardiac lineage specification.

Strengths:

The authors performed an extensive transcriptional and epigenetic analysis of early cardiac lineage specification and differentiation which will be of interest to investigators in the field of cardiac development and congenital heart disease. The authors considered the impact of the loss of Hand1 and Foxf1 in-vitro and Hand1 in-vivo.

Weaknesses:

The authors used previously published scRNA-seq data to generate two described transcriptomic trajectories.

We agree that a two-route cardiac development model has been described, which is consistent with our analyses. However, the developmental origins and key events by early lineage specification is unclear. Our study provided new insights from the following aspects:

a) Computational analyses inferred the earliest cardiac fate segregation by E6.75-7.0.

b) Provided the new-generated E7.0 multi-omics data which revealed the transcriptomic and chromatin accessibility landscape.

c) Utilized multi-omics and ChIP-seq data to construct a core regulatory network underlying the JCF lineage specification.

d) Applied in vitro and in vivo analyses, which elucidated the synergistic and different roles of key transcription factors, HAND1 and FOXF1.

Q1R1: Details of the re-analysis step should be added, including a careful characterization of the different clusters and maker genes, more details on the WOT analysis, and details on the time stamp distribution along the different pseudotimes. These details would be important to allow readers to gain confidence that the two major trajectories identified are realistic interpretations of the input data.

R1R1: Thank you for the valuable suggestion. In the last version, we characterized the two major trajectories by identifying their common or specific gene sets, and by profiling the expression dynamics along pseudotime (Figure 1F). But we realized a careful description was not provided. In the revised manuscript, we have made the following improvements:

a) Provided marker gene analyses based on cell types as well as developmental lineages to support the E7.0 progenitor clusters (Figure S1F).

b) For Figure 1F: revised the text and introduced characteristic genes for the two trajectories.

c) For WOT analysis: provided more details in the first paragraph of the ‘Results’ section.

R2R1: The authors have also renamed the cardiac trajectories/lineages, departing from the convention applied in hundreds of papers, making the interpretation of their results challenging.

R2R1: Agreed. We have changed the MJH as JCF lineage and PSH as SHF lineage.

Q3R1: The concept of "reverse reasoning" applied to the Waddington-OT package for directional mass transfer is not adequately explained. While the authors correctly acknowledged Waddington-OT's ability to model cell transitions from ancestors to descendants (using optimal transport theory), the justification for using a "reverse reasoning" approach is missing. Clarifying the rationale behind this strategy would be beneficial.

R3R1: Thank you for pointing out the unclear explanation. As mentioned in R1R1, we have clarified the rationale in the revised manuscript. 

We would like to provide some additional details: WOT is designed for time-series scRNA-seq data where the time/stage each single cell is given. At any adjacent time points t_i and t_i+1, WOT estimates the transition probability of all cells at t_i to all cells at t_i+1. One can select a cell set of interest at any time point t_i to infer their ancestors at t_i-1 or their descendants at t_i+1 by sums of the transition probabilities. As introduced in the original paper, WOT allows for both ‘forward’ and ‘reverse’ inference (DOI: 10.1016/j.cell.2019.01.006).

Q3R1: As the authors used the EEM cell cluster as a starting point to build the MJH trajectory, it's unclear whether this trajectory truly represents the cardiac differentiation trajectory of the FHF progenitors:

- This strategy infers that the FHF progenitors are mixed in the same cluster as the extra-embryonic mesoderm, but no specific characterization of potential different cell populations included in this cluster was performed to confirm this.

To build the MJH trajectory, we performed a two-step analysis:

(1) Firstly, we used E8.5 CM cells as a starting point to perform WOT computational reverse lineage tracing and identify CM progenitors at each time point.

(2) Secondly, we selected EEM cells from the E7.5 CM progenitor pool, as a starting point to perform WOT analysis. Cells along this trajectory consist of the JCF lineage (Figure 1B).

The reason why we chose to use this subset of E7.5 EEM cells was due to its purity. It is distinct from the SHF lineage as suggested by their separation in the UMAP. It is also different from FHF cells as no FHF/CM markers were detected by E7.5. 

It is admitted that it is infeasible to achieve 100% purity in this single cell omics analysis, but we believe the current strategy of defining the JCF lineage is reasonable. The distinct gene expression dynamics (Figure 1F) and spatial mapping results (Figure 1C), between JCF and SHF lineages, also supported our conclusion.

- The authors identified the EEM cluster as a Juxta-cardiac field, without showing the expression of the principal marker Mab21l2 per cluster and/or on UMAPs.

Thank you for your suggestion. We have added Mab21l2 expression plots in the ICA layout (new Figure S1D), showing its transient expression dynamics, consistent with Tyser et al (DOI: 10.1126/science.abb2986).

- As the FHF progenitors arise earlier than the Juxta-cardiac field cells, it must be possible to identify an early FHF progenitor population (Nkx2-5+; Mab21l2-) using the time stamp. It would be more accurate to use this FHF cluster as a starting point than the EEM cluster to infer the FHF cardiac differentiation trajectory.

We appreciate your insights. We used the early FHF progenitor population (E7.75 Nkx2-5+; Mab21l2- CM cells) as the starting point and identified its progenitor cells by E7.0 (Figure S2A). Results suggest both JCF and SHF lineages contribute to the early FHF progenitor population, consistent with live imaging-based single cell tracing by Dominguez et al (DOI: 10.1016/j.cell.2023.01.001).

These concerns call into question the overall veracity of the trajectory analysis, and in fact, the discrepancies with prior published heart field trajectories are noted but the authors fail to validate their new interpretation. Because their trajectories are followed for the remainder of the paper, many of the interpretations and claims in the paper may be misleading. For example, these trajectories are used subsequently for annotation of the multiomic data, but any errors in the initial trajectories could result in errors in multiomic annotation, etc, etc.

Thank you for your valuable comments. In the revised manuscript, we have added details about the trajectory analysis including the procedure of WOT lineage inference, marker gene expression and early FHF lineage tracing. We also renamed the two trajectories to avoid confusion with prior published heart field trajectories. Generally, our trajectories are consistent with the published evidence about two major lineages contributing to the linear heart tube:

a) Clonal analysis: two trajectories exist which demonstrate differential contribution to the E8.5 cardiac tube (Meilhac et al, DOI: 10.1016/s1534-5807(04)00133-9).

b) Live imaging: JCF cells contribute to the forming heart (Tyser et al, DOI: 10.1126/science.abb2986; Dominguez et al, DOI: 10.1016/j.cell.2023.01.001).

c) Genetic labelling based lineage tracing: early Hand1+ mesodermal cells differentiate and contribute to the cardiac crescent (Zhang et al, DOI: 10.1161/CIRCRESAHA.121.318943).

Molecular events by the initial segregation of the two lineages were not characterized before, which are the main focus of our paper. Our analyses suggest that the JCF lineage segregates earlier from the nascent/mixed mesoderm status, also consistent with the clonal analysis (Meilhac et al, DOI: 10.1016/s1534-5807(04)00133-9).

Q4R1: As mentioned in the discussion, the authors identified the MJH and PSH trajectories as nonoverlapping. But, the authors did not discuss major previously published data showing that both FHF and SHF arise from a common transcriptomic progenitor state in the primitive streak (DOI: 10.1126/science.aao4174; DOI: 10.1007/s11886-022-01681-w). The authors should consider and discuss the specifics of why they obtained two completely separate trajectories from the beginning, how these observations conflict with prior published work, and what efforts they have made at validation.

R4R1: Thank you for the important question. For trajectory analysis, we assigned cells to the trajectory with higher fate probability, resulting in ‘non-overlapping’ cell sets. However, the statement of ‘two non-overlapping trajectories’ is inaccurate. We performed analysis of fate divergence between two trajectories (which was not shown in the first version), which suggests, before E7.0, mesodermal cells have similar probabilities to choose either trajectory (Figure S1E). We agree with you and previously published data that the JCF and SHF arise from a common progenitor pool. Correction has been made in the revised manuscript.

Q5R1: Figures 1D and E are confusing, as it's unclear why the authors selected only cells at E7.0. Also, panels 1D 'Trajectory' and 'Pseudotime' suggest that the CM trajectory moves from the PSH cells to the MJH. This result is confusing, and the authors should explain this observation.

R5R1: Thank you for pointing out the confusion. As mentioned in R4R1, trajectory analysis indicates JCFSHF fate segregation by E7.0 and we used Figures 1D and E to characterize the cellular status. By E7.0, JCF progenitors are at EEM or MM status, while SHF progenitors are still at the earlier differentiation stage (NM). This result is consistent with previous clonal analysis (Meilhac et al, DOI: 10.1016/s1534-5807(04)00133-9) which demonstrates an apparent earlier segregation of the first lineage. Our interpretation of the pseudotime analysis is that it represents different levels of differentiation, instead of developmental direction.

Q6R1: Regarding the PSH trajectory, it's unclear how the authors can obtain a full cardiac differentiation trajectory from the SHF progenitors as the SHF-derived cardiomyocytes are just starting to invade the heart tube at E8.5 (DOI: 10.7554/eLife.30668).

R6R1.1: We agree with your opinion. Our trajectory analysis covers E8.5 SHF-derived CM cells and progenitors. Cells that differentiate as CM cells after E8.5 were missed.

The above notes some of the discrepancies between the author's trajectory analysis and the historical cardiac development literature. Overall, the discrepancies between the author's trajectory analysis and the historical cardiac development literature are glossed over and not adequately validated.

R6R1.2: Historical cardiac development related literature provided evidence, using multiple techniques, which support the existence of two cardiac lineages with common progenitors at the beginning and overlapping contribution of the four-chamber heart. Our trajectory analysis is in agreement with this model and provides more detailed molecular insights about lineage segregation by E7.0. Thank you for pointing out our mistakes describing the observations. We have corrected the text and provided additional data (Figure S1D-F and S2), aiming to resolved the confusions.

Q7R1: The authors mention analyzing "activated/inhibited genes" from Peng et al. 2019 but didn't specify when Peng's data was collected. Is it temporally relevant to the current study? How can "later stage" pathway enrichment be interpreted in the context of early-stage gene expression?

R7R1: The gene sets of "activated/inhibited genes" were collected from several published perturbation datasets (Gene Expression Omnibus accession numbers GSE48092, GSE41260, GSE17879, GSE69669, GSE15268 and GSE31544) using mouse ES cells or embryos. For a specific pathway, the gene set is fixed but the gene expression levels, which change over time, reflect the pathway enrichment. This explains the differential pathway enrichment between early and late stages.

Q8R1: Motif enrichment: cluster-specific DAEs were analyzed for motifs, but the authors list specific TFs rather than TF families, which is all that motif enrichment can provide. The authors should either list TF families or state clearly that the specific TFs they list were not validated beyond motifs.

R8R1: Thank you for your comment. For the DAE motif analysis, we firstly inferred the motif and TF families, then tested which specific TFs are expressed in the corresponding cell cluster. We have added this information in the legend of Figure 2D.

Q9R1: The core regulatory network is purely predictive. The authors again should refrain from language implying that the TFs in the CRN have any validated role.

R9R1: Thank you for your kind suggestion. We have revised the manuscript to avoid any misleading implications, as follows:

“Through single-cell multi-omics analysis, a predicted core regulatory network (CRN) in JCF is identified, consisting of transcription factors (TFs) GATA4, TEAD4, HAND1 and FOXF1.”

Q10R1: Regarding the in vivo analysis of Hand1 CKO embryos, Figures 6 and 7:

How can the authors explain the presence of a heart tube in the E9.5 Hand1 CKO embryos (Figure 6B) if, following the authors' model, the FHF/Juxta-cardiac field trajectory is disrupted by Hand1 CKO? A more detailed analysis of the cardiac phenotype of Hand1 CKO embryos would help to assess this question.

R10R1: Thank you for your valuable suggestion. In the revised manuscript, we have added detailed analysis of the cardiac phenotype of Hand1 CKO embryo (Figure S8C). Data suggest that by E8.5 when heart looping initiate in control group (14/17), the hearts of Hand1 CKO embryos (3/3) still demonstrate a linear tube morphology. By E9.5 when atrium and ventricle become distinct in WT embryos, heart looping of Hand1 CKO embryos is abnormal. The cardiac defects of our MESP1CRE driven Hand1 conditional KO are consistent with those of Hand1-null mutant mice (Doi: 10.1038/ng0398-266; D oi: 10.1038/ng0398-271).

Author response image 1.

The bright field images of E8.5-E9.5 Ctrl and Hand1 CKO mouse embryos. The arrows indicating the embryonic heart (h) and head folds (hf). Scale bars (E8.5): 200 μm; scale bars (E9.5): 500 μm.

Q11R1: The cell proportion differences observed between Ctrl and Hand1 CKO in Figure 6D need to be replicated and an appropriate statistical analysis must be performed to definitely conclude the impact of Hand1 CKO on cell proportions.

R11R1: We appreciate your valuable suggestion. As Figure 6D is based on scRNA-seq experiment, where replicates were merged as one single sequencing library, statistical analysis is infeasible. To address potential concerns about cell proportions, we added IF staining experiments of EEM marker gene, Vim, in serial embryo sections (Figure S8D). Statistical analysis indicates a significant decrease of VIM+ EEM cell proportion of Hand1 CKO embryos.

Q12R1: The in-vitro cell differentiations are unlikely to recapitulate the complexity of the heart fields invivo, but they are analyzed and interpreted as if they do.

R12R1: We agree with your opinion. In the revised manuscript, we tuned down the interpretation of the invitro cell differentiation data. 

Previous version:

I.  “The analysis indicated that HAND1 and FOXF1 could dually regulate MJH specification through directly activating the MJH specific genes and inhibiting the PSH specific genes.”

II. “Together, our data indicated that mutual regulation between HAND1 and FOXF1 could play a key role in MJH cardiac progenitor specification.”

III. “Thus, our data further supported the specific and synergistic roles of HAND1 and FOXF1 in MJH cardiac progenitor specification.”

Revised version:

I.  “The analysis indicated that HAND1 and FOXF1 were able to directly activate the JCF specific genes.”

II. “Together, our in vitro experimental data indicated that mutual regulation between HAND1 and FOXF1 could play a key role in activation of JCF specific genes.”

III. “These results suggest that HAND1 and FOXF1 may cooperatively regulate early cardiac lineage specification by promoting JCF-associated gene expression and suppressing alternative mesodermal programs.”

Q13R1: The schematic summary of Figure 7F is confusing and should be adjusted based on the following considerations:

(a) the 'Wild-type' side presents 3 main trajectories (SHF, Early HT and JCF), but uses a 2-color code and the authors described only two trajectories everywhere else in the article (aka MJH and PSH). It's unclear how the SHF trajectory (blue line) can contribute to the Early HT, when the Early HT is supposed to be FHF-associated only (DOI: 10.7554/eLife.30668). As mentioned previously in Major comment 3., this model suggests a distinction between FHF and JCF trajectories, which is not investigated in the article.

R13R1(a): Thank you for your great insights. The paper you mentioned used Nkx2.5_cre/+; Rosa26tdtomato+/- and _Nkx2.5_eGFP embryos to reconstruct the cardiac morphologies between E7.5 and E8.2. Their 3D models clearly demonstrate the transition from yolk sac to FHF and then SHF (Figure 2A’ and A’’). The location of yolk sac is defined as JCF in later literature (DOI: 10.1126/science.abb2986). However, as _Nkx2.5 mainly marks cells after the entry of the heart tube, it is unable to reflect the lineage contribution by JCF or SHF. As in R3R1, more and more evidence support the contribution of both lineages to the Early HT, which is discussed in a recent review paper (DOI: 0.1016/j.devcel.2023.01.010).

(b) the color code suggests that the MJH (FHF-related) trajectory will give rise to the right ventricle and outflow tract (green line), which is contrary to current knowledge.

R13R1(b): Thank you for pointing out the confusion. The coloring of outflow tract is not an indication of JCF lineage contribution. We have changed the color of JCF/SHF trajectory in the revised model.

Minor comments:

Q14R1: How genes were selected to generate Figure 1F? Is this a list of top differentially expressed genes over each pseudotime and/or between pseudotimes?

R14R1: For each trajectory, we ranked genes by the correlation between expression levels and pseudotime.

Top 1000 genes for each group were selected.

Q15R1: Regarding Figure 1G, it's unclear how inhibited signaling can have an increased expression of underlying genes over pseudotimes. Can the authors give more details about this analysis and results?

R15R1: The increased expression of ‘inhibited genes’ could be explained as an indication of decreasing signaling levels or compensation effect by other signaling pathways. We appreciate your kind suggestion. Details about this analysis have been added in the Method section.

Q16R1: How do the authors explain the visible Hand1 expression in Hand1 CKO in Figure S7C 'EEM markers'? Is this an expected expression in terms of RNA which is not converted into proteins?

R16R1: Our opinion is that the visible Hand1 expression caused by the imperfect knock-out efficiency by Mesp1-Cre driven system.

Q17R1: The authors do not address the potential presence of doublets (merged cells) within their newly generated dataset. While they mention using "SCTransform" for normalization and artifact removal, it's unclear if doublet removal was explicitly performed.

R17R1: We appreciate your kind reminder. Doublet removal was performed using R package ‘DoubletFinder’ (DOI: 10.1016/j.cels.2019.03.003). We have added this information in the revised manuscript.

Reviewer #2 (Public review):

Summary of goals:

The aims of the study were to identify new lineage trajectories for the cardiac lineages of the heart, and to use computational and cell and animal studies to identify and validate new gene regulatory mechanisms involved in these trajectories.

Strengths:

The study addresses the long-standing yet still not fully answered questions of what drives the earliest specification mechanisms of the heart lineages. The introduction demonstrates a good understanding of the relevant lineage trajectories that have been previously established, and the significance of the work is well described. The study takes advantage of several recently published data sets and attempts to use these in combination to uncover any new mechanisms underlying early mesoderm/cardiac specification mechanisms. A strength of the study is the use of an in vitro model system (mESCs) to assess the functional relevance of the key players identified in the computational analysis, including innovative technology such as CRISPR-guided enhancer modulations. Lastly, the study generates mesoderm-specific Hand1 LOF embryos and assesses the differentiation trajectories in these animals, which represents a strong complementary approach to the in vitro and computational analysis earlier in the paper. The manuscript is clearly written and the methods section is detailed and comprehensive.

Comments and Weaknesses:

Overall: The computational analysis presented here integrates a large number of published data sets with one new data point (E7.0 single cell ATAC and RNA sequencing). This represents an elegant approach to identifying new information using available data. However, the data presentation at times becomes rather confusing, and relatively strong statements and conclusions are made based on trajectory analysis or other inferred mechanisms while jumping from one data set to another. The cell and in vivo work on Hand1 and Foxf1 is an important part of the study. Some additional experiments in both of these model systems could strongly support the novel aspects that were identified by the computational studies leading into the work.

We appreciate your positive comments and insightful suggestions. In the revised manuscript, we have incorporated additional analyses and experimental validations to address the concerns raised. Specifically, we added RNA velocity analysis to independently support the identification of the MJH and PSH trajectories, performed immunofluorescence staining of mesodermal and cardiac markers in Hand1 and Foxf1 knockout models, and included Vim staining-based quantification in Hand1 CKO embryos to assess developmental outcomes in vivo. Furthermore, we revised potentially overinterpreted conclusions, clarified methodological details of WOT analysis. These revisions have strengthened both the rigor and clarity of the manuscript.

Q1R2: Definition of MJH and PSH trajectory:

The study uses previously published data sets to identify two main new differentiation trajectories: the MJH and the PSH trajectory (Figure 1). A large majority of subsequent conclusions are based on in-depth analysis of these two trajectories. For this reason, the method used to identify these trajectories (WTO, which seems a highly biased analysis with many manually chosen set points) should be supported by other commonly used methods such as for example RNA velocity analysis. This would inspire some additional confidence that the MJH and PSH trajectories were chosen as unbiased and rigorous as possible and that any follow-up analysis is biologically relevant.

R1R2: We appreciate your valuable comments. It is totally agreed that other commonly used methods help strengthen our conclusion about the two main trajectories. To this end, we performed RNA velocity analysis for the cardiac specification. Results support the contribution to CM along the MJH and PSH routes.

Author response image 2.

UMAP layout is colored by cell types. Developmental directions, shown as arrows, are inferred by RNA-velocity analysis.

Actually, several recent studies indicated a convergence cardiac developing model where progenitors reach a myocardial state along two trajectories (DOI: 10.1016/j.devcel.2023.01.010). However, when and how specification between the two routes were unclear. Our data and analysis revealed a clear fate separation by E7.0 from transcriptomic and epigenetic perspectives, where unbiased RNA velocity analysis was performed (Figure 2C).

We would like to clarify how we performed WOT (DOI: 10.1016/j.cell.2019.01.006) analysis: the only manually chosen cell set was the starting set, which was all cardiomyocyte cells by E8.5, of computational reverse lineage tracing. The ancestor cells were predicted in an unbiased manner among all mesodermal cells.

Q2R2.1: Identification of MJH and PSH trajectory progenitors:

The study defines various mesoderm populations from the published data set (Figure 1A-E), including nascent mesoderm, mixed mesoderm, and extraembryonic mesoderm. It further assigns these mesoderm populations to the newly identified MJH/PSH trajectories. Based on the trajectory definition in Figure 1A it appears that both trajectories include all 3 mesoderm populations, albeit at different proportions and it seems thus challenging to assign these as unique progenitor populations for a distinct trajectory, as is done in the epigenetic study by comparing clusters 8 (MJH) and 2 (PSH)(Figure 2). 

R2R2.1: According to our model, the most significant difference between the two trajectories is their enrichment of EEM and PM cell types (Figure 1B), which represent the middle stages of cardiac development. Both trajectories begin as Mesp1+ Nascent mesoderm cells (Figure 1F), which is supported by Mesp1 lineage tracing (DOI: 10.1161/CIRCRESAHA.121.318943), and ends as cardiomyocytes. Our epigenetic analysis focused on the E7.0 stage when the two trajectories could be clearly separated and when JCF and SHF lineages were at mixed mesoderm and nascent mesoderm states, respectively. However, SHF lineage was predicted to bypass mixed mesoderm state later on.

Q2R2.2: Along similar lines, the epigenetic analysis of clusters 2 and 8 did not reveal any distinct differences in H3K4m1, H3K27ac, or H3K4me3 at any of the time points analyzed (Figure 2F). While conceptually very interesting, the data presented do not seem to identify any distinct temporal patterns or differences in clones 2 and 8 (Figure 2H), and thus don't support the conclusion as stated: "the combined transcriptome and chromatin accessibility analysis further supported the early lineage segregation of MJH and the epigenetic priming at gastrulation stage for early cardiac genes".

R2R2.2: In the epigenetic analysis, we delineated the temporal dynamics of E7.0 cluster-specific DAEs by selecting earlier (E6.5) and later (E7.5) time points. DAEs of C8 and C2 represent regulatory elements for the JCF and SHF lineages, respectively. We also included C1 DAEs as a reference to demonstrate the relative activity of C8 and C2. The overall temporal pattern suggests activation of C8 & C2, as their H3K4me1 and H3K27ac levels surpass C1 over time. Between C8 and C2, the following distinctions could be observed:

a) H3K4me1 levels of C8 are higher by E6.5 and E7.0, with low H3K27ac levels, indicating early priming of C8 DAEs.

b) By E7.5, H3K4me1 levels of C8 are caught up by C2 in E7.5 anterior mesoderm (E7.5_AM, Figure 2F column 3), where cardiac mesoderm is located.

c) H3K4me1 and H3K27ac levels of C8 are similar as C1 in the posterior mesoderm (E7.5_P, Figure 2F column 4) and much higher than C2.

d) From the perspective of chromatin accessibility, hundreds of characteristic DAEs were identified for C2 and C8 (Figure 2D), exemplified by the primed and active enhancers which were predicted to interact with cluster-specific genes (Figure 2H).

Together with the transcriptomic analyses (Figure 2C), these data are consistent with our conclusion about early lineage segregation and epigenetic priming.

Q3R2: Function of Hand1 and Foxf1 during early cardiac differentiation:

The study incorporated some functional studies by generating Hand1 and Foxf1 KO mESCs and differentiated them into mesoderm cells for RNA sequencing. These lines would present relevant tools to assess the role of Hand1 and Foxf1 in mesoderm formation, and a number of experiments would further support the conclusions, which are made for the most part on transcriptional analysis. For example, the study would benefit from quantification of mesoderm cells and subsequent cardiomyocytes during differentiation (via IF, or more quantitatively, via flow cytometry analysis). These data would help interpret any of the findings in the bulk RNAseq data, and help to assess the function of Hand1 and Foxf1 in generating the cardiac lineages. Conclusions such as "the analysis indicated that HAND1 and FOXF1 could dually regulate MJH specification through directly activating the MJH specific genes and inhibiting PSH specific genes" seem rather strong given the data currently provided.

R3R2: Thank you for your kind suggestions. We added IF staining of mesodermal (Zic3), JCF (Hand1) and cardiac markers (Tnnt2), followed by cell quantification. Results indicate that Hand1 and Foxf1 knockout leads to reduced commitment to the JCF lineage, evidenced by the loss of Hand1 expression, accumulation of undifferentiated Zic3+ mesoderm, and impaired cardiomyocyte formation (Tnnt2+), consistent with the up-regulation of JCF lineage specific genes and the downregulation of SHF lineage specific genes.

We also revised the conclusion as “These results suggest that HAND1 and FOXF1 may cooperatively regulate early cardiac lineage specification by promoting JCF-associated gene expression and suppressing alternative mesodermal programs.”.

(4) Analysis of Hand1 cKO embryos:

Adding a mouse model to support the computational analysis is a strong way to conclude the study. Given the availability of these early embryos, some of the findings could be strengthened by performing a similar analysis to Figure 7B&C and by including some of the specific EEM markers found to be differentially regulated to complement the structural analysis of the embryos.

R4R2: hank you for your positive comments and help. In the revised manuscript, we performed IF staining of EEM marker Vim in a similar fashion as Figure 7B&C (Figure S8D). In comparison with control embryos, the Hand1 CKO embryos demonstrated significant less number of Vim+ cells, further strengthening the conclusion that Hand1 CKO blocked the developmental progression toward JCF direction.

Q5R2: Current findings in the context of previous findings:

The introduction carefully introduces the concept of lineage specification and different progenitor pools. Given the enormous amount of knowledge already available on Hand1 and Foxf1, and their role in specific lineages of the early heart, some of this information should be added, ideally to the discussion where it can be put into context of what the present findings add to the existing understanding of these transcription factors and their role in early cardiac specification.

R5R2: We appreciate your positive comments and kind reminder. We have added discussion about how our study could be put into the body of findings on Hand1 and Foxf1. Although these two genes have been validated to be functionally important for heart development, it is unclear when and how they affect this process. Using in-vivo and in-vitro models and single cell multi-omics analyses, we provided evidence to fill the gaps from multiple aspects, including cell state temporal dynamics, regulatory network, and epigenetic regulation underlying the very early cardiac lineage specification.

Reviewer #3 (Public review):

Q1R3: In Figure 1A, could the authors justify using E8.5 CMs as the endpoint for the second lineage and better clarify the chamber identities of the E8.5 CMs analysed? Why are the atrial genes in Figure 1C of the PSH trajectory not present in Table S1.1, which lists pseudotime-dependent genes for the MJH/PSH trajectories from Figure 1F?

R1R3: Thank you for your comments. We used E8.5 CMs as the endpoint of the second (SHF) lineage because this stage represents a critical point where SHF-derived cardiomyocytes have begun distinct differentiation, allowing us to capture terminal lineage states reliably. The chamber identities of E8.5 CMs were determined based on known marker genes (DOI: 10.1186/s13059-025-03633-3). The atrial genes shown in Figure 1C reflect cluster-specific markers that may not meet the strict pseudotime-dependency criteria used to generate Table S1.1, which lists genes dynamically changing along the MJH/PSH trajectories.

Q2R3: Could the authors increase the resolution of their trajectory and genomic analyses to distinguish between the FHF (Tbx5+ HCN4+) and the JCF (Mab21l2+/ Hand1+) within the MJH lineage? Also, clarify if the early extraembryonic mesoderm contributes to the FHF.

R2R3: Thank you for your great suggestions. To distinguish between the FHF and JCF trajectories, we used early FHF progenitor population (E7.75 Nkx2-5+; Mab21l2- CM cells) as the starting point and performed WOT lineage inference (Figure S2A). Results suggest that both JCF and SHF progenitors contribute to the FHF, consistent with live imaging-based single cell tracing by Dominguez et al (DOI: 10.1016/j.cell.2023.01.001) and lineage tracing results by Zhang et al (DOI: 10.1161/CIRCRESAHA.121.318943). We also analyzed the expression levels of FHF marker genes (Tbx5, Hcn4) and observed their activation along both trajectories (Figure S2B).

Q3R3: The authors strongly assume that the juxta-cardiac field (JCF), defined by Mab21l2 expression at E7.5 in the extraembryonic mesoderm, contributes to CMs. Could the authors explain the evidence for this? Could the authors identify Mab21l2 expression in the left ventricle (LV) myocardium and septum transversum at E8.5 (see Saito et al., 2013, Biol Open, 2(8): 779-788)? If such a JCF contribution to CMs exists, the extent to which it influences heart development should be clarified or discussed.

R3R3: Thank you for the important question. For the JCF contribution to the heart tube, several lines of evidence have been published in recent years using micro-dissection of mouse embryonic heart (DOI: 10.1126/science.abb2986), live imaging (DOI: 10.1016/j.cell.2023.01.001) and lineage tracing approaches (DOI: 10.1161/CIRCRESAHA.121.318943). According to Tyser et al (DOI: 10.1126/science.abb2986), Mab21l2 expression is detected in septum transversum at E8.5 and the Mab21l2+ lineage contribute to LV, basically consistent with the literature you mentioned (Saito et al., 2013, Biol Open, 2(8): 779-788). Our lineage inference analyses further support the model and suggest earlier specification by JCF. However, the focus of our work is the transcriptional and epigenetic regulation of underlying the JCF developmental trajectory.

Q4R3: Could the authors distinguish the Hand1+ pericardium from JCF progenitors in their single-cell data and explain why they excluded other cell types, such as the endocardium/endothelium and pericardium, or even the endoderm, as endpoints of their trajectory analysis? At the NM and MM mesoderm stages, how did the authors distinguish the earliest cardiac cells from the surrounding developing mesoderm?

R4R3: We appreciate your insightful question. In our other study (DOI: 10.1186/s13059-025-03633-3), we tried to further divide the CM cells as subclusters and it seems that their difference is mainly driven by the segmentation of the heart tube (e.g. LV, RV, OFT etc.). By the E8.5 stage, we are unable to identify the Hand1+ pericardium cluster. 

Also, it seems infeasible to distinguish endocardium from other endothelium cells only using singlecell data. High resolution spatial transcriptome data is required. Alternatively, we analyzed the E7.0 mesodermal lineages and determined C5/6 as hematoendothelial progenitors. Marker gene analysis indicate that their lineage segregation has started by this stage (Figure S4C and Author response image 3).

Author response image 3.

UMAP layout, using scRNA-seq (Reference data) and snRNA-seq (Multiome data), is colored by cell types (left). Expression of hematoendothelial progenitor marker genes is shown (right).

We did observe the difference between the earliest cardiac cells from the surrounding developing mesoderm. As in Figure 1D, cells belonging to the JCF lineage (Hand1 high/Lefty2 low) were clustered at the EEM/MM end, in contrast to the NM cells.

Q5R3: Could the authors contrast their trajectory analysis with those of Lescroart et al. (2018), Zhang et al., Tyser et al., and Krup et al.?

R5R3: Thank you for the valuable suggestion. We compared our model with the suggested ones and summarized as follows:

(1) Lescroart et al: The JCF and SHF progenitor cells match their DCT2 (Bmp4+) and DCT3 (Foxc2+) clusters, respectively.

(2) Zhang et al: The JCF lineage matches their EEM-DC (developing CM)-CM trajectory. The SHF lineage is consistent with their NM-LPM (lateral plate mesoderm)-DC (developing CM)-CM trajectory. Notably, their EEM-DC-CM also expressed FHF marker (Tbx5) at later stages.

(3) Tyser et al: we performed data integration analysis and found the correspondence between JCF progenitors (EEM cells from the cardiac trajectory) and their Me5, as well as SHF progenitors (PM cells from the cardiac trajectory) with Me7. In their model, both Me5 and Me7 contribute to Me4 (representing the FHF), consistent with our results (see Tyser et al., 2021 and Pijuan-Sala et al., 2019).

(4) Krup et al also performed URD lineage inference, providing a model with CM (12) and Cardiac mesoderm (29) as cardiac end points. Their model did not seem to suggest distinct trajectories between JCF and SHF lineages, as both JCF (Hand1) and SHF (Isl1) markers co-expressed in CM.

Q6R3: Previous studies suggest that Mesp2 expression starts at E8 in the presomitic mesoderm (Saga et al., 1997). Could the authors provide in situ hybridization or HCR staining to confirm the early E7 Mesp2 expression suggested by the pseudo-time analysis of the second lineage.

R6R3: We validated the expression of E7 Mesp2 using Geo-seq spatial transcriptome data (Author response image 4, upper). Results suggest the high spatial enrichment of Mesp2 expression in primitive streak (T+) and/or nascent mesoderm (Mesp1+) cells, which correspond to the progenitors of the second lineage.

In situ hybridization data (PMID: 17360776) also supports the early expression of Mesp2 by E7 (Author response image 4, lower).

Author response image 4.

(Upper) E7 Geo-seq data for selected genes: T, Mesp1, and Mesp2. (Lower) Mesp2 expression during early development; image acquired from Morimoto et al. (PMID: 17360776).

Q7R3: Could the authors also confirm the complementary Hand1 and Lefty2 expression patterns at E7 using HCR or in situ hybridization? Hand1 expression in the first lineage is plausible, considering lineage tracing results from Zhang et al.

R7R3: Thank you for your great suggestion. We observed spatially complementary expression patterns of Hand1 and Lefty2 in the Geo-seq spatial transcriptomic data. In the mesoderm layer, Hand1 is highly expressed in the proximal end. While Lefty2+ cells exhibit preference toward the distal direction.

Author response image 5.

E7 Geo-seq data for selected genes: Hand1 and Lefty2.

Q8R3: Could the authors explain why Hand1 and Lefty2+ cells are more likely to be multipotent progenitors, as mentioned in the text?

R8R3: Thank you for your question. Here, we observed E7.0 Mesp1+ and Lefty2+ nascent mesodermal cells assigned to both the JCF and SHF lineages (Figure 1D), indicating their multipotency. On the other hand, we also found low expressions of JCF markers, Hand1 and Msx2, by the early stage of the SHF trajectory (Figure 1F). Thus, we concluded that both Hand1+ and Lefty2+ E7.0 mesodermal cells are likely to be multipotent.

Q9R3: Could the authors comment on the low Mesp1 expression in the mesodermal cells (MM) of the MJH trajectory at E7 (Figure 1D)? Is Mesp1 transiently expressed early in MJH progenitors and then turned off by E7? Have all FHF/JCF/SHF cells expressed Mesp1?

R9R3: Thank you for the insightful questions. Zhang et al. (PMID: 34162224) performed scRNA-seq analysis of Mesp1 lineage-traced cells, which indicate the contribution of Mesp1+ cells to FHF, JCF, and SHF. This is also supported by Dominguez et al. utilizing live imaging approaches (PMID: 36736300). Our temporal dynamics analysis suggests that along the JCF trajectory, Mesp1 is turned off as JCF characteristic genes were up regulated (Figure 1F and S1D).

Q10R3: Could the authors clarify if their analysis at E7 comprises a mixture of embryonic stages or a precisely defined embryonic stage for both the trajectory and epigenetic analyses? How do the authors know that cells of the second lineage are readily present in the E7 mesoderm they analysed (clusters 0, 1, and 2 for the multiomic analysis)?

R10R3: Thank you for your questions. Although embryos were collected at E7.0, the developmental stages could be variable. As exemplified by Karl Theiler’s book, “The House Mouse: Atlas of Embryonic Development”, mesoderm was visible for some E7.0 egg cylinders but not in others. To test whether cells of the second lineage are present in the E7.0 mesoderm, we analyzed the WOT lineage tracing results and the cell type composition by E7.0 (Author response image 6, left panel). Most cells belong to the nascent mesoderm (NM) or mixed mesoderm (MM), while almost no cells were assigned to the primitive streak (PS). To avoid the possibility that the E7.0 embryos represented later stages, we also analyzed the E6.75 cells of the second lineage (Author response image 6, middle panel). Results suggest that NM cells were still the dominant contributors to the second lineage, although ~22.6% cells were assigned to the PS. The abovementioned analyses were performed using the scRNA-seq data. The embryos of the E7.0 single-cell multi-omics represent similar developmental stages as the scRNAseq data, as suggested by the well-aligned UMAPs (Figure S1D, right panel). Thus, we conclude that for the multi-omics data, the cells of the second lineage are also readily present in the mesoderm.

Author response image 6.

(Left and middle) Lineage inference and cell type composition at E7.0 and E6.75. (Right) UMAPs of E7.0 multi-omics and scRNA-seq data.

Q11R3: Could the authors further comment on the active Notch signaling observed in the first and second lineages, considering that Notch's role in the early steps of endocardial lineage commitment, but not of CMs, during gastrulation has been previously described by Lescroart et al. (2018)?

R11R3: We appreciate your kind suggestion. As reported by Lescroart et al. (2018), using Notch1CreERT2/Rosa-tdTomato mice and tamoxifen administration at E6.5, early expression of Notch1 mostly marked endocardial cells (ECs, 76.9-83.9%), with minor contribution to the cardiomyocytes (6.0-16.6%) and to the epicardial cells (EPs, 6.0-6.5%). The lineage specificity of Notch1 is consistent with our E7.0 multi-omics data, where its expression was mainly observed in the NM and hematoendothelial progenitors (Author response image 7). Interestingly, expression of other NOTCH receptor genes (Notch2 and Notch3) and ligand genes (Dll1 and Dll3) in the CM lineages. Notch3 demonstrate higher expression in the first lineage, while Dll1 and Dll3 were highly expressed in the second lineage. The study by Lescroart et al. (2018) emphasized the role of Notch1 as an EC lineage marker, while our analyses aimed at the activity of the NOTCH pathway.

Author response image 7.

Expression of representative NOTCH genes at E7.0 (multi-omics data).

Q12R3: In cluster 8, Figure 2D, it seems that levels of accessibility in cluster 8 are relatively high for genes associated with endothelium/endocardium development in addition to MJH genes. Could the authors comment and/or provide further analysis?

R12R3: Thanks for you for raising this interesting point. To confirm the association of these genes with endothelium (EC) and/or MJH, we analyzed their expression levels by E7.0 (progenitor stage) and E8.0 (differentiated stage) (Author response image 8). Among target genes of MJH-specific DAEs (cluster 3/7/8 in Figure 2D), Pmp22, Mest, Npr1, Pkp2, and Pdgfb were expressed in the hematoendothelial progenitors. The Nrp1 gene and PDGF pathway play critical roles in endothelial development by modulating cell migration (PMID: 15920019 and 28167492), which is also important for MJH cells. In addition, we observed common ATAC-seq peaks in both hematoendothelial and MJH clusters (Author response image 9), indicating shared regulatory elements. Interestingly, Pdgfb is not expressed by CM in vivo, it is actively expressed in the CM of the in vitro system (Author response image 9). These results indicate regulatory and functional closeness between hematoendothelial and MJH cell groups, at early stages of lineage establishment.

Author response image 8.

Regulatory connection between MJH and endothelial cells (ECs).

Author response image 9.

Representative genome browser snapshots of scATAC-seq (aggregated gene expression and chromatin accessibility for each cluster) and RNA-seq at the Pdgfb locus.

Q13R3: Can the authors clarify why they state that cluster 8 DAEs are primed before the full activation of their target genes, considering that Bmp4 and Hand1 peak activities seem to coincide with their gene expression in Figure 2G?

R13R3: Thanks for your great question. The overall analyses indicate low to medium levels of H3K4me1 and H3K27ac by E6.5-7.0 at cluster 8 DAEs, which were fully activated by E7.5 (Figure 2F). Further inspections suggest different epigenetic status of individual DAEs (Figure 3H), which could be active (K4me1+/K27ac+), primed (K4me1+/K27ac-), or inactive (K4me1-/K27ac-). Thus, we concluded that many DAEs could be primed before full activation. The coincidence of enhancer peak activities and gene expression was observed by aggregating single cell clusters at a single stage E7.0, which does not rule out the possibility that these enhancers are epigenetically primed at earlier stages.

Q14R3: Did the authors extend the multiomic analysis to Nanog+ epiblast cells at E7 and investigate if cardiac/mesodermal priming exists before mesodermal induction (defined by T/Mesp1 onset of expression)?

R14R3: We appreciate your kind suggestion. We observed low levels of T/Mesp1 expression in the E7.0 Nanog+ epiblast cells (Author response image 10). Interestingly, the T+/Mesp1+ cells were not clustered toward any specific differentiation directions in the UMAP. We also analyzed DAE activities in each single cell by averaging over the C1/C2/C8 DAE sets. The C2 and C8 DAEs were clearly less active than the C1 DAEs. But C2/C8-DAE active cells were observed among the E7.0 Nanog+ epiblast cells. These data indicate the early priming exists in epiblast cells before the commitment to cardiac/mesodermal differentiation.

Author response image 10.

Gene expression and DAE activity levels of E7.0 Nanog+ epiblast cells shown in UMAP layout.

Q15R3: In the absence of duplicates, it is impossible to statistically compare the proportions of mesodermal cell populations in Hand1 wild-type and knockout (KO) embryos or to assess for abnormal accumulation of PS, NM, and MM cells. Could the authors analyse the proportions of cells by careful imaging of Hand1 wild-type and KO embryos instead?

R15R3: Thank you for your important question. To assess the proportions of mesodermal cell populations in E7.25 wild-type and Hand1-CKO embryos, we analyzed the serial coronal sections of the extraembryonic portions and performed staining of the Vim gene, which marks the extra-embryonic mesodermal (EEM) cells (Figure S8D). We then counted the numbers of mesodermal/Vim+ EEM cells and calculated the relative proportion of Vim+ EEM cells in each section. The proportion of Vim+ EEM cells was statistically lower in the Hand1-CKO embryo, consistent with our model that Hand1 deletion led to blocked MJH specification.

Q16R3: Could the authors provide high-resolution images for Figure 7 B-C-D as they are currently hard to interpret?

R16R3: Thank you for your suggestion. We have replaced Figure 7B-C-D with high-resolution images.

Recommendations for the authors:  

Reviewing Editor Comments:

Discussions among reviewers emphasize the importance of better addressing and validating the trajectory analysis by using more common and alternative bioinformatics and spatial approaches. Further discussion on whether there is a common transcriptional progenitor between the two trajectories is also required to enhance the significance of the study. For functional analysis, further validations are needed as the current data only partially support the claims. Please see public reviews for details.

Reviewer #2 (Recommendations For The Authors):

Beyond the suggestions made in the public review, below are some minor aspects for consideration:

The manuscript is well written overall but may benefit from a thorough read-through and editing of some minor grammatical errors.

We have carefully read through the manuscript and corrected minor grammatical errors to improve clarity and readability.

Figure 2C: RNA velocity information gets largely lost due to the color choice of EEM and MM (black) on which the direction of arrows can't be appreciated.

We have updated the color scheme in Figure 2C.

Figure 6D: sample information is partially cut off in the graph.

Sample information is completely shown now.

The last paragraph of the discussion has some formatting issues with the references.

We have corrected the formatting issues with the references.

The methods and results section does not comment on if, or how many embryos were pooled for the sequencing analysis performed for this study.

We have added the numbers of embryos for sequencing analyses in the methods section.

Reviewer #3 (Recommendations For The Authors):

Minor:

In the discussion, authors could reconsider the sentence: "The process of cardiac lineage segregation is a complex one that may involve TF regulatory networks and signaling pathways," as it is not informative.

We have re-written the sentence as: “Thus, additional regulation must exist and instructs the process of JCF-SHF lineage segregation.”

eLife Assessment

This study provides valuable information on the impact of Lamin A/C knockdown on gene expression using RNA-Seq analysis, as well as on telomere dynamics through live cell imaging. However, the conclusions remain inadequately supported by the current data, and several of the major technical concerns raised in the first round have not yet been fully resolved.

Reviewer #1 (Public review):

I am afraid that the manuscript has not improved much. The authors have barely addressed my specific comments, and the manuscript remains descriptive with little logic in the analyses, and no coherence between the RNA-seq work and the telomere dynamics analysis. The revised title still suggests more causality/mechanism than is demonstrated in the results.

Of my three main technical concerns, two critical ones were not properly addressed, and for the third concern the answer is not entirely clear. So on balance, in my view the revised manuscript still does not meet the scientific standards of the field.

(1) Knockdowns should be verified at the protein level:

Authors state that they are working on this, but the results are not included in the revised manuscript.

(2) Multiple shRNAs for each protein, or and alternative method such as CRISPR deletion or degron technology, must be tested to rule out such off-target effects:

Authors state that they are working on this, but have not included the results in the revised manuscript.

(3) It was not clear whether the replicate experiments are true biological replicates (i.e. done on different days).

Authors give a somewhat ambiguous answer in the rebuttal: "samples [...] were derived from independently prepared cultures in separate experimental setups". A simple answer would have been "yes they were done on different days", but this is not what is stated, so I still wonder about the experimental design. The Methods text only states "Each experiment was performed with a minimum of three biological replicates" without clarifying how this was implemented.

Reviewer #2 (Public review):

Summary:

This study focused on the roles of the nuclear envelope proteins lamin A and C, as well as nesprin-2, encoded by the LMNA and SYNE2 genes, respectively, on gene expression and chromatin mobility. It is motivated by the established role of lamins in tethering heterochromatin to the nuclear periphery in lamina-associated domains (LADs) and modulating chromatin organization. The authors show that depletion of lamin A, lamin A and C, or nesprin-2 results in differential effects of mRNA and lnRNA expression, primarily affecting genes outside established LADs. In addition, the authors used fluorescent dCas9 labeling of telomeric genomic regions combined with live-cell imaging to demonstrate that depletion of either lamin A, lamin A/C, or nesprin-2 increased the mobility of chromatin, suggesting an important role of lamins and nesprin-2 on chromatin dynamics.

Strengths:

The major strength of this study is the detailed characterization of changes in transcript levels and isoforms resulting from depletion of either lamin A, lamin A/C, or nesprin-2 in human osteosarcoma (U2OS) cells. The authors use a variety of advanced tools to demonstrate the effect of protein depletion on specific gene isoforms and to compare the effects on mRNA and lncRNA levels.

The TIRF imaging of dCas9 labeled telomeres allows for high resolution tracking of multiple telomeres per cell, thus enabling the authors to obtain detailed measurements of the mobility of telomeres within living cells and the effect of lamin A/C or nesprin-2 depletion.

Weaknesses:

Although the findings presented by the authors overall confirm existing knowledge about the ability of lamins A/C and nesprin to broadly affect gene expression, chromatin organization, and chromatin dynamics, the specific interpretation and the conclusions drawn from the data presented in this manuscript are limited by several technical and conceptual challenges.

One major limitation is that the authors only assess the knockdown of their target genes on the mRNA level, where they observe reductions of around 70%. Given that lamins A and C have long half-lives, the effect at the protein level might be even lower. This incomplete and poorly characterized depletion on the protein level makes interpretation of the results difficult. Assessing the effect of the knockdown on the protein level would provide more detailed information both on the extent of the actual protein depletion and the effect on specific lamin isoforms. Similarly, given that nesprin-2 has numerous isoforms resulting from alternative splicing and transcription initiation. In the current form of the manuscript, it remains unclear which specific nesprin-2 isoforms where depleted, and by what extent (on the protein level).

Another substantial limitation of the manuscript is that the current analysis, with exception of the chromatin mobility measurements, is exclusively based on transcriptomic measurements by RNA-seq and qRT-PCR, without any experimental validation of the predicted protein levels or proposed functional consequences. As such, conclusions about the importance of lamin A/C on RNA synthesis and other functions are derived entirely from gene ontology terms and are not sufficiently supported by experimental data. Thus, the true functional consequences of lamin A/C or nesprin depletion remain unclear.

Another substantial weakness is that the data and analysis presented in the manuscript raise some concerns about the robustness of the findings. Given that the 'shLMNA' construct is expected to deplete both lamin A and C, i.e., its effect encompasses the depletion of lamin A, which is achieved by the 'shLaminA' construct, one would expect a substantial overlap between the DEGs in the shLMNA and shLaminA conditions, with the shLMNA depletion producing a broader effect as it targets both lamin A and C. However, the Venn Diagram in Figure 4a, the genomic loci distribution in Figure 4b, and the correlation analysis in Suppl. Fig. S2 show little overlap between the shLMNA and shLaminA conditions, which is quite surprising. In the mapping of the DEGs shown in Fig. 4b, it is also surprising not to see the gene targeted by the shRNA, LMNA, found on chromosome 1, in the results for the shLMNA and shLamin A depletion.

The correlation analysis in Suppl. Figure S2 raises further questions. The authors use dox-inducible shRNA constructs to target lamin A (shLaminA), lamin A/C (shLMNA), or nesprin-2 (shSYNE2). Thus, the no-dox control (Ctr) for each of these constructs would be expected to be very similar to the non-target scrambled controls (Ctrl.shScramble and Dox.shScramble). However, in the correlation matrix, each of the no-dox controls clusters more closely with the corresponding dox-induced shRNA condition than with the Ctrl.shScramble or Dox.shScramble conditions, suggesting either a very leaky dox-inducible system, effects from clonal selection (although less likely, giving the pooling of three clones), or substantial batch effects in the processing. Either of these scenarios could substantially affect the interpretation of the findings.

The premise of the authors that lamins would only affect peripheral chromatin and genes at LADs neglects the fact that lamins A and C are also found in the nuclear interior, where they form stable structure and influence chromatin organization, and the fact that lamins A and C and nesprins additionally interact with numerous transcriptional regulators such as Rb, c-Fos, and beta-catenins, which could further modulate gene expression when lamins or nesprins are depleted.

The comparison of the identified DEGs to genes contained in LADs might be confounded by the fact that the authors relied on the identification of LADs from a previous study, which used a different human cell type (human skin fibroblasts) instead of the U2OS osteosarcoma cells used in the present study. As LADs are often highly cell type specific, the use of the fibroblast data set could lead to substantial differences in LADs.

Overall appraisal and context:

Despite its limitations, the present study further illustrates the important roles the nuclear envelope proteins lamin A, lamin C, and nesprin-2 have in chromatin organization, dynamics, and gene expression. It thus confirms results from previous studies previously reported for lamin A/C depletion. For example, the effect of lamin A/C depletion on increasing mobility of chromatin, had already been demonstrated by several other groups, such as Bronshtein et al. Nature Comm 2015 (PMID: 26299252) and Ranade et al. BMC Mol Cel Biol 2019 (PMID: 31117946). Additionally, the effect of lamin A/C depletion on gene and protein expression has already been extensively studied in a variety of other cell lines and model systems, including detailed proteomic studies (PMIDs 23990565 and 35896617).

The finding that that lamin A/C or nesprin depletion not only affects genes at the nuclear periphery but also the nuclear interior is not particularly surprising giving the previous studies and the fact that lamins A and C are also founding within the nuclear interior, where they affect chromatin organization and dynamics, and that lamins A/C and nesprins directly interact with numerous transcriptional regulators that could further affect gene expression independent from their role in chromatin organization.

The isoform specific effects of LMNA depletion on chromatin mobility and gene expression are not entirely surprising, as recent work by the Medalia group identified a lamin A-specific chromatin binding site not present in lamin C (PMID: 40750945). This work should be cited in the manuscript.

The authors provide a detailed analysis of isoform switching in response to lamin A/C or nesprin-depletion, but the underlying mechanism remains unclear. Similarly, their analysis of the genomic location of the observed DEGs shows the wide-ranging effects of lamin A/C or nesprin depletion, but lets the reader wonder how these effects are mediated. A more in-depth analysis of predicted regulator factors and their potential interaction with lamins A/C or nesprin would be beneficial in gaining more mechanistic insights.

Additional note regarding the revised manuscript:

The authors have made several revisions to the manuscript, including the title and abstract. The above comments have been updated to reflect the latest manuscript version.

These text revisions made by the authors provide some more detailed discussion of context and interpretation of the work, improving the clarity of the manuscript. However, they do not fundamentally alleviate many of the concerns previously expressed regarding the lack of mechanistic insights and various technical aspects of the study, i.e., use of a single shRNA for knockdown, lack of knockdown validation on the protein level, potential off-target effects of the shRNA, batch-effects of the transcriptomic analysis, cell-type specific differences in LADs, etc. Without further experimental data, the manuscript offers a mostly descriptive analysis on the effect of LMNA and SYNE2 depletion on gene expression and telomere mobility. The manuscript might be useful as a reference data sets for comparison with other LMNA or SYNE2 depletion studies, albeit with various caveats regarding its interpretation due to the technical concerns raised by the reviewers.

Author response:

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

Reviewer #1 (Public review):

This manuscript reports a descriptive study of changes in gene expression after knockdown of the nuclear envelope proteins lamin A/C and Nesprin2/SYNE2 in human U2OS cells. The readout is RNA-seq, which is analyzed at the level of gene ontology and focused investigation of isoform variants and non-coding RNAs. In addition, the mobility of telomeres is studied after these knockdowns, although the rationale in relation to the RNA-seq analyses is rather unclear.

We sincerely thank the reviewer for the thoughtful summary and valuable feedback. Regarding the telomere mobility analyses, our intention was to provide additional evidence supporting the hypothesis that knockdown of lamins and nesprins disrupts nuclear architecture. Although the connection to the RNA-seq data was not explicitly detailed, we believe that the increased telomere mobility may reflect broader changes in chromatin organization, which could contribute to the observed differential gene expression. We have revised the manuscript to clarify this rationale and improve the integration between the two analyses.

RNA-seq after knockdown of lamin proteins has been reported many times, and the current study does not provide significant new insights that help us to understand how lamins control gene expression. This is particularly because the vast majority of the observed effects on gene expression appear to occur in regions that are not bound by lamin A. It seems likely that these effects are indirect. There is also virtually no overlap between genes affected by laminA/C and by SYNE2, which remains unexplained; for example, it would be good to know whether laminA/C and SYNE2 bind to different genomic regions. The claim in the Title and Abstract that LMNA governs gene expression / acts through chromatin organization appears to be based only on an enrichment of gene ontology terms "DNA conformation change" and "covalent chromatin conformation" in the RNA-seq data. This is a gross over-interpretation, as no experimental data on chromatin conformation are shown in this study. The analyses of transcript isoform switching and ncRNA expression are potentially interesting but lack a mechanistic rationale: why and how would these nuclear envelope proteins regulate these aspects of RNA expression? The effects of lamin A on telomere movements have been reported before; the effects of SYNE2 on telomere mobility are novel (to my knowledge), but should be discussed in the light of previously documented effects of SUN1/2 on the dynamics of dysfunctional telomeres (Lottersberger et al, Cell 2015).

We sincerely thank the reviewer for this thoughtful and detailed critique. We agree that RNA-seq following knockdown of lamin proteins has been previously reported and appreciate the concern regarding the novelty and mechanistic interpretation of our findings. However, For our study, we revealed novel findings that there is distinct isoform switching and lncRNA affected by lamins and nesprins, which have not been reported yet by previous studies. Furthermore, we also revealed not only lamin A, but also nesprin-2 could also affect chromatin mobility.

For the analysis of LMNA ChIP-seq data from  human fibroblast (Kohta Ikegami, 2021). Their data revealed that Lamin A/C modulates gene expression through interactions with enhancers. The pathogenesis of disorders associated with LMNA mutations may stem primarily from disruptions in this gene regulatory function, rather than from impaired tethering of chromatin to LADs.

We acknowledge the reviewer’s concern that gene ontology enrichment related to chromatin conformation alone is insufficient to support claims about chromatin structural changes. We have therefore revised the “Title” and “Abstract” to avoid overstating conclusions and to more accurately reflect the scope of our data.

Regarding telomere dynamics, while Lamin A's role has indeed been previously documented, our study provides evidence that SYNE2/Nesprin-2 also regulates telomere mobility. We have now expanded the discussion to include prior work, particularly the findings of Lottersberger et al. (Cell, 2015), to better contextualize our results and distinguish the contributions of SYNE2.

Finally, we appreciate the reviewer’s suggestion about transcript isoform and noncoding RNA expression. While our study primarily provides descriptive data, we agree that further mechanistic investigation is warranted. We have clarified this point in the “Discussion” and framed our findings as a foundation for future studies exploring the broader regulatory roles of nuclear envelope proteins.

We are grateful for the reviewer’s comments, which have helped us improve the clarity and rigor of our manuscript. Please see the revised highlights in our revised manuscript.

As indicated below, I have substantial concerns about the experimental design of the knockdown experiments.

Altogether, the results presented here are primarily descriptive and do not offer a significant advance in our understanding of the roles of LaminA and SYNE2 in gene regulation or chromatin biology, because the results remain unexplained mechanistically and functionally. Furthermore, the RNAseq datasets should be interpreted with caution until off-target effects of the shRNAs can be ruled out.

We fully acknowledge that the original version of our manuscript lacked sufficient mechanistic insight. In response, we have revised the manuscript to include additional analyses and explanations that clarify the potential functional relevance of our findings. For example, we added following text “These findings further underscore the functional relevance of lamin A in coordinating transcriptional programs through modulation of nuclear architecture. In contrast, LMNA knockdown led to differential expression of genes enriched in pathways related to chromatin organization, suggesting potential disruptions in chromatin regulatory networks. Although direct measurements of chromatin conformation were not performed, these transcriptional changes indicate that LMNA may contribute to maintaining nuclear architecture and genomic stability, which aligns with its established involvement in laminopathies and genome integrity disorders.“ More analyses could be found in the main text.

Regarding the concern about off-target effects of the shRNA-based knockdowns, we agree that this is an important consideration. While shRNA approaches inherently carry the risk of off-target effects, we have now performed additional analyses that help address this issue. These analyses support the specificity of our observations and suggest that the majority of gene expression changes are likely to be directly related to the targeted knockdown. Nonetheless, we have clearly stated the limitations of the approach in the revised discussion and emphasized the need for future validation using complementary methods.

We hope that these revisions strengthen the overall impact and interpretability of our study.

Specific comments:

(1) Knockdowns were only monitored by qPCR. Efficiency at the protein level (e.g., Western blots) needs to be determined.

We agree that complementary protein-level validation (e.g., by Western blot) would strengthen the findings, and we are in the process of obtaining suitable reagents to address this point in future experiments. We have now clarified this limitation in the revised manuscript  

(2) For each knockdown, only a single shRNA was used. shRNAs are infamous for offtarget effects; therefore, multiple shRNAs for each protein, or an alternative method such as CRISPR deletion or degron technology, must be tested to rule out such offtarget effects.

We fully acknowledge the concern regarding the use of only a single shRNA per knockdown and agree that shRNAs are prone to off-target effects. We recognize the importance of validating our findings using multiple independent shRNAs or alternative knockdown strategies, such as CRISPR deletion or degron-based approaches, to ensure specificity. To address this concern, we have conducted qPCR confirmation the knockdown of target proteins from RNA-seq findings, further supporting the validity of our data. In line with this, we are currently optimizing an auxin-inducible degron system (AtAFB2) for targeted and controlled depletion of lamin C. Our preliminary results indicate approximately a 40% knockdown efficiency after 16 hours of auxin induction, highlighting the necessity for further system optimization (Author response image 1). Future experiments will integrate this improved degron technology alongside multiple independent approaches to rigorously address and mitigate concerns about off-target effects, thereby enhancing the robustness and reproducibility of our data.

Author response image 1.

FACS analysis of the lamin C degron system at 0, 1, 3, and 16 hours postinduction with 500 μM indole-3-acetic acid (IAA) (Sigma).

(3) It is not clear whether the replicate experiments are true biological replicates (i.e., done on different days) or simply parallel dishes of cells done in a single experiment (= technical replicates). The extremely small standard deviations in the RT-qPCR data suggest the latter, which would not be adequate.

We appreciate the reviewer’s insightful comment regarding the nature of our replicates. The RT-qPCR experiments were indeed performed as true biological replicates, with samples collected on different days and from independently cultured cell batches. We have added this to the manuscript Methods. While we observed some variability in the Scramble control group, the low standard deviations in the shRNAtreated samples likely reflect the consistent and efficient knockdown of target genes.

For the RNA-seq experiments, samples were collected as two batches during RNA extraction and library preparation. The samples still represent biological replicates, as they were derived from independently prepared cultures in separate experimental setups. This approach was chosen to strike a balance between biological variation and technical consistency, thereby improving the reliability of the RNA-seq results.

Reviewer #2 (Public review):

Summary:

This study focused on the roles of the nuclear envelope proteins lamin A and C, as well as nesprin-2, encoded by the LMNA and SYNE2 genes, respectively, on gene expression and chromatin mobility. It is motivated by the established role of lamins in tethering heterochromatin to the nuclear periphery in lamina-associated domains (LADs) and modulating chromatin organization. The authors show that depletion of lamin A, lamin A and C, or nesprin-2 results in differential effects of mRNA and lncRNA expression, primarily affecting genes outside established LADs. In addition, the authors used fluorescent dCas9 labeling of telomeric genomic regions combined with live-cell imaging to demonstrate that depletion of either lamin A, lamin A/C, or nesprin-2 increased the mobility of chromatin, suggesting an important role of lamins and nesprin2 in chromatin dynamics.

We sincerely appreciate the reviewer’s thoughtful summary of our study and the key findings. Our work is indeed motivated by the well-established roles of lamin A/C in chromatin tethering at the nuclear periphery and the emerging understanding of their broader influence on chromatin organization and gene regulation. In our study, we aimed to further explore these roles by examining the consequences of depleting lamin A, lamin A/C, and nesprin-2 (SYNE2) on both gene expression and chromatin mobility.

As the reviewer accurately notes, we observed differential effects on mRNA and lncRNA expression, with many changes occurring outside of previously defined LADs. This finding suggests that lamins and nesprin-2 may also influence transcriptional regulation through mechanisms beyond direct LAD association. Furthermore, using live-cell imaging of fluorescently labeled telomeric regions, we demonstrated that loss of these nuclear envelope components leads to increased chromatin mobility, supporting their role in maintaining chromatin stability and nuclear architecture.

We thank the reviewer for highlighting these aspects, which we believe contribute to a more nuanced understanding of how nuclear envelope proteins modulate chromatin behavior and gene regulation.

Strengths:

The major strength of this study is the detailed characterization of changes in transcript levels and isoforms resulting from depletion of either lamin A, lamin A/C, or nesprin-2 in human osteosarcoma (U2OS) cells. The authors use a variety of advanced tools to demonstrate the effect of protein depletion on specific gene isoforms and to compare the effects on mRNA and lncRNA levels.

The TIRF imaging of dCas9-labeled telomeres allows for high-resolution tracking of multiple telomeres per cell, thus enabling the authors to obtain detailed measurements of the mobility of telomeres within living cells and the effect of lamin A/C or nesprin-2 depletion.

We are grateful that the reviewer recognized the comprehensive analysis of transcript and isoform changes upon depletion of lamin A, lamin A/C, or nesprin-2 in U2OS cells. We also thank the reviewer for acknowledging our use of advanced tools to investigate isoform-specific effects and to distinguish between changes in mRNA and lncRNA expression.

Furthermore, we are pleased that the reviewer highlighted the strength of our TIRF imaging approach using dCas9-labeled telomeres. This technique enabled us to capture high-resolution, multi-locus dynamics within single living cells, and we agree that it is instrumental in revealing the impact of lamin A/C and nesprin-2 depletion on telomere mobility.

Weaknesses:

Although the findings presented by the authors overall confirm existing knowledge about the ability of lamins A/C and nesprin to broadly affect gene expression, chromatin organization, and chromatin dynamics, the specific interpretation and the conclusions drawn from the data presented in this manuscript are limited by several technical and conceptual challenges.

One major limitation is that the authors only assess the knockdown of their target genes on the mRNA level, where they observe reductions of around 70%. Given that lamins A and C have long half-lives, the effect at the protein level might be even lower. This incomplete and poorly characterized depletion on the protein level makes interpretation of the results difficult. The description for the shRNA targeting the LMNA gene encoding lamins A and C given by the authors is at times difficult to follow and might confuse some readers, as the authors do not clearly indicate which regions of the gene are targeted by the shRNA, and they do not make it obvious that lamin A and C result from alternative splicing of the same LMNA gene. Based on the shRNA sequences provided in the manuscript, one can conclude that the shLaminA shRNA targets the 3' UTR region of the LMNA gene specific to prelamin A (which undergoes posttranslational processing in the cell to yield lamin A). In contrast, the shRNA described by the authors as 'shLMNA' targets a region within the coding sequence of the LMNA gene that is common to both lamin A and C, i.e., the region corresponding to amino acids 122-129 (KKEGDLIA) of lamin A and C. The authors confirm the isoform-specific effect of the shLaminA isoform, although they seem somewhat surprised by it, but do not confirm the effect of the shLMNA construct. Assessing the effect of the knockdown on the protein level would provide more detailed information both on the extent of the actual protein depletion and the effect on specific lamin isoforms. Similarly, given that nesprin-2 has numerous isoforms resulting from alternative splicing and transcription initiation. In the current form of the manuscript, it remains unclear which specific nesprin-2 isoforms were depleted, and to what extent (on the protein level).

We have revised the Methods section to include a clearer and more detailed description of the shRNA design, including the specific regions of the LMNA gene targeted by each construct, as well as the relationship between lamin A and C isoforms resulting from alternative splicing. We agree that this clarification will help prevent confusion for readers.

Regarding the shLMNA construct, we acknowledge the importance of confirming the knockdown at the protein level, especially given the long half-lives of lamin proteins. In our revised manuscript, we now refer to Supplementary Figure S2, which demonstrates that the shLMNA construct effectively reduces both lamin A and lamin C transcript levels. While we initially focused on mRNA quantification, we recognize that additional proteinlevel validation is valuable and have accordingly emphasized this point in the revised discussion.

We also appreciate the comment on nesprin-2 isoforms. Given the complexity of nesprin-2 splicing, we are currently working to further characterize the specific isoforms affected and will aim to include protein-level data in a future study. 

Another substantial limitation of the manuscript is that the current analysis, with the exception of the chromatin mobility measurements, is exclusively based on transcriptomic measurements by RNA-seq and qRT-PCR, without any experimental validation of the predicted protein levels or proposed functional consequences. As such, conclusions about the importance of lamin A/C on RNA synthesis and other functions are derived entirely from gene ontology terms and are not sufficiently supported by experimental data. Thus, the true functional consequences of lamin A/C or nesprin depletion remain unclear. Statements included in the manuscript such as "our findings reveal that lamin A is essential for RNA synthesis, ..." (Lines 79-80) are thus either inaccurate or misleading, as the current data do not show that lamin A is ESSENTIAL for RNA synthesis, and lamin A/C and lamin A deficient cells and mice are viable, suggesting that they are capable of RNA synthesis.

We agree that our current data do not support the claim that lamin A is essential for RNA synthesis, and we acknowledge the importance of distinguishing between correlation and causal relations in our conclusions. In light of this, we have revised the statement in the manuscript to more accurately reflect our findings:

“Our findings suggest that lamin A contributes to RNA synthesis, supports chromatin spatial organization through LMNA, and that SYNE2 influences chromatin modifications as reflected in transcript levels.”

We hope this revision better aligns with the limitations of our dataset and addresses the reviewer’s concerns regarding the interpretation of functional consequences based solely on transcriptomic data.

Another substantial weakness is that the data and analysis presented in the manuscript raise some concerns about the robustness of the findings. Given that the 'shLMNA' construct is expected to deplete both lamin A and C, i.e., its effect encompasses the depletion of lamin A, which is achieved by the 'shLaminA' construct, one would expect a substantial overlap between the DEGs in the shLMNA and shLaminA conditions, with the shLMNA depletion producing a broader effect as it targets both lamin A and C. However, the Venn Diagram in Figure 4a, the genomic loci distribution in Figure 4b, and the correlation analysis in Supplementary Figure S2 show little overlap between the shLMNA and shLaminA conditions, which is quite surprising. In the mapping of the DEGs shown in Figure 4b, it is also surprising not to see the gene targeted by the shRNA, LMNA, found on chromosome 1,  in the results for the shLMNA and shLamin A depletion.

We have added the discussion into the revised edition: “Interestingly, although both shLMNA and shLaminA constructs target lamin A, with shLMNA additionally depleting lamin C, the DEGs identified under these two conditions show limited overlap. This unexpected finding suggests that depletion of lamin C in the shLMNA condition may trigger distinct or compensatory transcriptional responses that are not elicited by lamin A knockdown alone. Furthermore, variation in shRNA efficiency or off-target effects may contribute to these differences. Notably, despite directly targeting LMNA, the overlap in DEGs between the two conditions remained limited under our stringent threshold criteria. Together, these observations highlight the complex and non-linear regulatory roles of lamin isoforms in gene expression and underscore the need for further mechanistic studies to dissect their individual and combined contributions [28,29].”

The correlation analysis in Supplementary Figure S2 raises further questions. The authors use doc-inducible shRNA constructs to target lamin A (shLaminA), lamin A/C (shLMNA), or nesprin-2 (shSYNE2). Thus, the no-dox control (Ctr) for each of these constructs would be expected to be very similar to the non-target scrambled controls (Ctrl.shScramble and Dox.shScramble). However, in the correlation matrix, each of the no-dox controls clusters more closely with the corresponding dox-induced shRNA condition than with the Ctrl.shScramble or Dox.shScramble conditions, suggesting either a very leaky dox-inducible system, strong effects from clonal selection, or substantial batch effects in the processing. Either of these scenarios could substantially affect the interpretation of the findings. For example, differences between different clonal cell lines used for the studies, independent of the targeted gene, could explain the limited overlap between the different shRNA constructs and result in apparent differences when comparing these clones to the scrambled controls, which were derived from different clones.

We thank the reviewer for this thoughtful observation. We would like to clarify that the samples shown in Supplementary Figure S2 were processed and sequenced in two separate batches, and the data presented in the correlation matrix are unnormalized. As such, batch effects are indeed present and likely contribute to the clustering pattern observed, particularly the closer similarity between the dox-induced and no-dox samples for each individual shRNA construct.

Importantly, our analyses focus on within-construct comparisons (i.e., doxycyclinetreated vs untreated samples for the same shRNA), rather than direct comparisons across different constructs or scrambled controls. Each experimental pair (dox vs nodox) was processed in parallel within its respective batch to ensure internal consistency. Thus, while the global clustering pattern may reflect batch-related differences or baseline variations between independently derived cell lines, these factors do not affect the main conclusions drawn from the within-construct differential expression analysis.

The manuscript also contains several factually inaccurate or incorrect statements or depictions. For example, the depiction of the nuclear envelope in Figure 1 shows a single bilipid layer, instead of the actual double bi-lipid layer of the inner and outer nuclear membranes that span the nuclear lumen. The depiction further lacks SUN domain proteins, which, together with nesprins, form the LINC complex essential to transmit forces across the nuclear envelope. The statement in line 214 that "Linker of nucleoskeleton and cytoskeleton (LINC) complex component nesprin-2 locates in the nuclear envelope to link the actin cytoskeleton and the nuclear lamina" is not quite accurate, as nesprin-2 also links to microtubules via dynein and kinesin.

We sincerely thank the reviewer for pointing out these important inaccuracies. In response, we have revised Figure 1 to accurately depict the nuclear envelope as a double bi-lipid membrane and included SUN domain proteins to better reflect the structural components of the LINC complex. Additionally, we have updated the statement and citations 

This is the revised part that is incorporated in the manuscript “The linker of nucleoskeleton and cytoskeleton (LINC) complex component nesprin-2 is a nuclear envelope protein that connects the nucleus to the cytoskeleton by interacting not only with actin filaments but also with microtubules through motor proteins such as dynein and kinesin. This structural linkage contributes to cellular architecture and facilitates mechanotransduction between the nuclear interior and the extracellular matrix (ECM) [8,21]

”We appreciate the reviewer’s insights, which have helped improve the accuracy and clarity of our manuscript.

The statement that "Our data show that Lamin A knockdown specifically reduced the usage of its primary isoform, suggesting a potential role in chromatin architecture regulation, while other LMNA isoforms remained unaffected, highlighting a selective effect" (lines 407-409) is confusing, as the 'shLaminA' shRNA specifically targets the 3' UTR of lamin A that is not present in the other isoforms. Thus, the observed effect is entirely consistent with the shRNA-mediated depletion, independent of any effects on chromatin architecture.

We have rephrased the statement “Our data show that knockdown with shLaminA, which specifically targets the 3' UTR unique to the lamin A isoform, selectively reduced lamin A expression without affecting other LMNA isoforms.”

The premise of the authors that lamins would only affect peripheral chromatin and genes at LADs neglects the fact that lamins A and C are also found in the nuclear interior, where they form stable structure and influence chromatin organization, and the fact that lamins A and C and nesprins additionally interact with numerous transcriptional regulators such as Rb, c-Fos, and beta-catenins, which could further modulate gene expression when lamins or nesprins are depleted.

Based on the reviewer’s comment we have added the statement into Discussion part “Beyond their well-established role in tethering heterochromatin at the nuclear periphery through lamina-associated domains (LADs), A-type lamins (lamins A and C) also localize to the nuclear interior, where they contribute to chromatin organization and gene regulation independently of LADs [27,28]. Nuclear lamins can form intranuclear foci that associate with active chromatin and are implicated in supporting transcriptional activity. Additionally, both lamins and nesprins participate in diverse protein-protein interactions that may influence transcriptional regulation. For example, lamin A/C interacts with the retinoblastoma protein (Rb) to modulate E2F-dependent transcription [29], and with c-Fos to regulate its nuclear retention and activity [30]. While βcatenin acts as a co-activator in Wnt signaling relies on nuclear translocation and interaction with transcriptional complexes, and evidence suggests that nuclear architecture and envelope components, including nesprins, can influence this process [31]. Therefore, the observed gene expression changes following depletion of lamins or nesprins are likely not restricted to genes located within lamina-associated domains (LADs), but may also result from broader perturbations in nuclear architecture and transcriptional regulatory networks. This is consistent with our findings that lamins and nesprins influence gene expression in distal, non-LAD regions.”

The comparison of the identified DEGs to genes contained in LADs might be confounded by the fact that the authors relied on the identification of LADs from a previous study (ref #28), which used a different human cell type (human skin fibroblasts) instead of the U2OS osteosarcoma cells used in the present study. As LADs are often highly cell-type specific, the use of the fibroblast data set could lead to substantial differences in LADs.

DamID in various mammalian cell types has shown that some LADs are cell-type invariant (constitutive LADs [cLADs]), while others interact with the NL in only certain cell types (facultative LAD [fLADs]) (Bas van Steensel, 2017). We agree that facultative LADs (fLADs), which comprise approximately half of all LADs, are often highly cell-type specific. We acknowledge that this specificity may influence the interpretation of our findings. At present, publicly available LAD datasets for U2OS cells are limited to those associated with LMNB. We concur that generating LMNA-specific LAD maps in U2OS cells would enhance the accuracy and relevance of our analyses, and we view this as an important direction for future research.

Another limitation of the current manuscript is that, in the current form, some of the figures and results depicted in the figures are difficult to interpret for a reader not deeply familiar with the techniques, based in part on the insufficient labeling and figure legends. This applies, for example, to the isoform use analysis shown in Figure 3d or the GenometriCorr analysis quantifying spatial distance between LADs and DEGs shown in Figure 4c.

For Figure 3, we added text in the caption to make the figure more readable “Isoform switching analysis reveals differential expression of alternative transcript variants between conditions, highlighting a shift in predominant isoform usage.” For Figure 4c, we added text in the caption “GenometriCorr analysis was used to quantify the spatial relationship between LADs and DEGs, evaluating whether the observed genomic proximity deviates from random expectation through empirical distributionbased statistical testing of pairwise distances between genomic intervals.” And also in the ‘Methods”.

Overall appraisal and context:

Despite its limitations, the present study further illustrates the important roles the nuclear envelope proteins lamin A, lamin C, and nesprin-2 have in chromatin organization, dynamics, and gene expression. It thus confirms results from previous studies (not always fully acknowledged in the current manuscript) previously reported for lamin A/C depletion. For example, the effect of lamin A/C depletion on increasing mobility of chromatin had already been demonstrated by several other groups, such as Bronshtein et al. Nature Comm 2015 (PMID: 26299252) and Ranade et al. BMC Mol Cel Biol 2019 (PMID: 31117946). Additionally, the effect of lamin A/C depletion on gene and protein expression has already been extensively studied in a variety of other cell lines and model systems, including detailed proteomic studies (PMIDs 23990565 and 35896617).

We add more discussions as below “Our findings reinforce the pivotal roles of nuclear envelope proteins lamin A, LMNA and nesprin 2 in regulating chromatin organization, chromatin mobility, and gene expression. These results are consistent with and extend prior studies investigating the consequences of lamin depletion. For instance, increased chromatin mobility following the loss of lamin A/C has been previously demonstrated using live-cell imaging approaches [26,35], supporting our observations of nuclear structural relaxation and chromatin redistribution. Additionally, proteomic profiling following lamin A depletion has been extensively documented across both cellular and mouse models, providing valuable insights into the molecular consequences of nuclear envelope disruption [36,37]. While these earlier studies provide a strong foundation, our work contributes novel insights by integrating isoform-specific perturbations with spatial chromatin measurements. This approach emphasizes contextdependent regulatory mechanisms that involve not only lamina-associated regions but also nesprin-associated domains and distal genomic loci, thereby expanding the current understanding of nuclear envelope protein function in gene regulation.”

The finding that that lamin A/C or nesprin depletion not only affects genes at the nuclear periphery but also the nuclear interior is not particularly surprising giving the previous studies and the fact that lamins A and C are also founding within the nuclear interior, where they affect chromatin organization and dynamics, and that lamins A/C and nesprins directly interact with numerous transcriptional regulators that could further affect gene expression independent from their role in chromatin organization.

We have added the following statement into the Discussion part “Beyond their well-established role in tethering heterochromatin at the nuclear periphery through lamina-associated domains (LADs), A-type lamins (lamins A and C) also localize to the nuclear interior, where they contribute to chromatin organization and gene regulation independently of LADs [27,28]. Nuclear lamins can form intranuclear foci that associate with active chromatin and are implicated in supporting transcriptional activity. Additionally, both lamins and nesprins participate in diverse protein-protein interactions that may influence transcriptional regulation. For example, lamin A/C interacts with the retinoblastoma protein (Rb) to modulate E2F-dependent transcription [29], and with c-Fos to regulate its nuclear retention and activity [30]. While β-catenin acts as a co-activator in Wnt signaling relies on nuclear translocation and interaction with transcriptional complexes, and evidence suggests that nuclear architecture and envelope components, including nesprins, can influence this process [31]. Therefore, the observed gene expression changes following depletion of lamins or nesprins are likely not restricted to genes located within lamina-associated domains (LADs), but may also result from broader perturbations in nuclear architecture and transcriptional regulatory networks. This is consistent with our findings that lamins and nesprins influence gene expression in distal, non-LAD regions.”

The authors provide a detailed analysis of isoform switching in response to lamin A/C or nesprin depletion, but the underlying mechanism remains unclear. Similarly, their analysis of the genomic location of the observed DEGs shows the wide-ranging effects of lamin A/C or nesprin depletion, but lets the reader wonder how these effects are mediated. A more in-depth analysis of predicted regulator factors and their potential interaction with lamins A/C or nesprin would be beneficial in gaining more mechanistic insights.

We agree that the current findings, while highlighting the broad impact of lamin A/C or nesprin depletion on isoform usage and gene expression, do not fully elucidate the underlying regulatory mechanisms. We acknowledge the importance of identifying upstream regulators and understanding their potential interactions with lamins and nesprins. Future investigations integrating epigenetic approaches, such as ChIP-seq for transcription factors and chromatin-associated proteins, will be essential to clarify how lamins and nesprins contribute to isoform switching and to uncover the mechanistic basis of these regulatory effects.

Reviewer #3 (Public review):

Summary:

This manuscript describes DOX inducible RNAi KD of Lamin A, LMNA coded isoforms as a group, and the LINC component SYNE2. The authors report on differentially expressed genes, on differentially expressed isoforms, on the large numbers of differentially expressed genes that are in iLADs rather than LADs, and on telomere mobility changes induced by 2 of the 3 knockdowns.

Strengths:

Overall, the manuscript might be useful as a description for reference data sets that could be of value to the community.

We acknowledge that the initial version of our manuscript lacked comprehensive comparisons with previous studies. In our revised manuscript, we have included more detailed discussions highlighting how our findings complement and extend existing knowledge. Specifically, our study presents novel insights into the role of lamins and nesprins in regulating non-coding RNAs and isoform switching, areas that have not been extensively explored in prior literatures. We hope these additions will clarify the contribution of our work and demonstrate the potential value to the field.

Weaknesses:

The results are presented as a type of data description without formulation of models or explanations of the questions being asked and without follow-up. Thus, conceptually, the manuscript doesn't appear to break new ground.

In our study, we proposed a conceptual model in which gene expression changes are linked to RNA synthesis, chromatin conformation alterations, and chromatin modifications, potentially mediated by lamin A, LMNA, and nesprin-2 at the transcriptional level. However, we acknowledge that this model remains preliminary and largely unexplored. We agree that additional mechanistic insights and identification of specific regulatory factors are needed to strengthen this framework. Future studies will aim to experimentally validate these hypotheses and clarify the pathways and regulators involved.

Not discussed is the previous extensive work by others on the nucleoplasmic forms of LMNA isoforms. Also not discussed are similar experiments- for instance, gene expression changes others have seen after lamin A knockdowns or knockouts, or the effect of lamina on chromatin mobility, including telomere mobility - see, for example, a review by Roland Foisner (doi.org/10.1242/jcs.203430) on nucleoplasmic lamina. The authors need to do a thorough search of the literature and compare their results as much as possible with previous work.

We sincerely thank the reviewer for pointing out the important body of previous work on the nucleoplasmic forms of LMNA isoforms and the impact of lamin A depletion on gene expression and chromatin mobility. In the revised version, we have now included relevant citations. Please see the highlights in the Discussion.

The authors don't seem to make any attempt to explore the correlation of their findings with any of the previous data or correlate their observed differential gene expression with other epigenetic and chromatin features. There is no attempt to explore the direction of changes in gene expression with changes in nuclear positioning or to ask whether the genes affected are those that interact with nucleoplasmic pools of LMNA isoforms. The authors speculate that the DEG might be related to changing mechanical properties of the cells, but do not develop that further.

We sincerely appreciate the reviewer’s insightful comments. In our revised manuscript, we have addressed this concern by comparing our telomere mobility results with previously published data (Bronshtein et al., 2015), and we observe consistent findings showing that lamin A depletion leads to increased telomere motility. Furthermore, our study provides novel evidence that nesprin-2 depletion similarly enhances telomere migration, suggesting a broader role for nuclear envelope components in chromatin dynamics.

We acknowledge the importance of integrating gene expression data with epigenetic and chromatin features. However, to our knowledge, such datasets are currently limited for U2OS cells, particularly in the context of lamin and nesprin perturbation. We agree that understanding the correlation between differentially expressed genes and nuclear positioning or interactions with nucleoplasmic pools of LMNA isoforms is a promising direction. We are actively planning future studies that include chromatin profiling and mechanical perturbation assays to further explore these mechanisms.

The technical concerns include: 1) Use of only one shRNA per target. Use of additional shRNAs would have reduced concern about possible off-target knockdown of other genes; 2) Use of only one cell clone per inducible shRNA construct. Here, the concern is that some of the observed changes with shRNA KDs might show clonal effects, particularly given that the cell line used is aneuploid. 3) Use of a single, "scrambled" control shRNA rather than a true scrambled shRNA for each target shRNA.

(1) Regarding the use of a single shRNA per target, we agree that utilizing multiple independent shRNAs would strengthen the conclusions. In our study, we selected validated shRNA sequences with minimal predicted off-targets and confirmed knockdown efficiency at mRNA level (by qPCR).

(2) As for the use of a single cell clones per inducible construct, we understand the concern that clonal variability, particularly in an aneuploid cell line, could influence the observed phenotypes. To clarify this, we have revised in the manuscript “Multiple independent clones per shRNA were screened for knockdown efficiency using reverse transcription quantitative real-time PCR (RT-qPCR). Three clones demonstrating robust and consistent knockdown were selected and expanded. These clones were subsequently pooled to minimize clonal variability and used for downstream analyses, including RNA-seq”. To mitigate this, we ensured consistent results across biological replicates and used inducible systems to reduce variability introduced by random integration. 

(3) We also acknowledge that the use of a single scrambled shRNA control, rather than matched scrambled controls for each construct, is a limitation. While we used a standard non-targeting scrambled shRNA commonly applied in similar studies, we understand that distinct scrambled sequences might better control for construct-specific effects. .

Reviewer #1 (Recommendations for the authors):

Please make the processed RNA-seq data available for each individual experiment, not only the raw reads and averaged data.

In response to your suggestion, we have now included the raw count data for each individual experiment in Supplementary Table S5 to enhance transparency and reproducibility.   

Reviewer #2 (Recommendations for the authors):

The current text contains numerous typos, and some of the text could benefit from additional editing for clarity and conciseness. In addition, several statements, particularly in the section encompassing lines 321-329, lack supporting references.

In our revised version, we have carefully edited the text for clarity and conciseness.

We have included related citations from lines 321-329: “The majority of genes located within LADs tend to be transcriptionally repressed or expressed at low levels. This is because LADs are associated with heterochromatin , a tightly packed form of DNA that is generally inaccessible to the cellular machinery required for gene expression 12,23. Lamin mutations and levels have shown to disrup LAD organization and gene expression that have been implicated in various diseases, including cancer and laminopathies 24,25.”

The figures would benefit from better labeling, including a clear schematic of which specific regions of the LMNA and SYNE2 genes are targeted by the different shRNA constructs, and by labeling the different isoforms in Figure S1 with the common names. Furthermore, note that lamin A arises from posttranslational processing of prelamin A, not from a different transcript. Likely, the "different LMNA genes" shown in Supplementary Figure S1 are just different annotations, with the exceptions of the splice isoforms lamin C and lamin delta10.

In the Method, we have clearly denoted the design of corresponding shRNAs as suggested “The shRNA designated as shLMNA targets a region within the coding sequence of LMNA that is shared by both lamin A and lamin C, corresponding to amino acids 122–129 (KKEGDLIA) of lamin A/C (RefSeq: NM_001406985.1). The shRNA against SYNE2 (shSYNE2) targets a sequence encoding amino acids 5133– 5140 (KRYERTEF) of the SYNE2 protein (RefSeq: NM_182914.3).”

For Figure S1, we have added common isoform names to figure and captions. “lamin A (ENST00000368300.9), LMNA 227 (ENST00000675431.1), pre-lamin A/C (ENST00000676385.2), and lamin C (ENST00000677389.1)."

Several statements about the novelty of the findings or approach are inaccurate. For example, the authors state in the introduction that "However, whether lamins and nesprins actively govern chromatin remodeling and isoform switching beyond their wellcharacterized functions in mechanotransduction remains an open question", as several previous studies have provided detailed characterization of lamin A/C depletion or mutations on chromatin organization, mobility, and gene expression. The authors should revise these statements and better acknowledge the previous work.

We have added the citations of previous works and revised the text “While significant progress has been made in understanding the role of lamins in genome organization, the precise mechanisms by which lamins and nesprins regulate gene expression through distal chromatin interactions remain incompletely understood [10,11]. Notably, recent evidence suggests a reciprocal interplay between transcription and chromatin conformation, where gene activity can influence chromatin folding and vice versa [12]. However, whether lamins and nesprins actively govern chromatin remodeling and isoform switching beyond their well-characterized functions in mechanotransduction remains an open question.”

Reviewer #3 (Recommendations for the authors):

Overall, the manuscript might be useful as a description for reference data sets that could be of value to the community. Otherwise, I did not derive meaningful biological insights from the manuscript. It was not clear to me also how much might be repeating previous work already reported in the literature (see below). For example, I cited a review on nucleoplasmic lamins by Roland Foisner at the end of the specific comments - scanning it very quickly shows that there are already papers on increased chromatin mobility after lamin perturbations, including telomeres. I know there have also been studies of changes in gene expression after lamin A and B KD. The authors need to do a thorough search of the literature and compare their results as much as possible with previous work.

We acknowledge that the roles of lamins in regulating chromatin dynamics and gene expression, including the effects of lamin perturbations on chromatin mobility and telomere behavior, have been previously reported. In response, we have revised the manuscript to incorporate relevant citations and to better contextualize our results within the existing literature. Importantly, to our knowledge, the finding that nesprin-2 influences telomere mobility has not been previously reported, and we have highlighted this novel observation in the revised text.

In response, we have now conducted a more comprehensive literature review and revised the manuscript accordingly to better contextualize our findings. Specifically, we have added comparisons to prior studies reporting chromatin mobility changes following lamin A/C depletion. We also now emphasize the novel aspects of our study, such as the isoform-specific perturbations and the integration of spatial chromatin organization with transcriptomic outcomes.

We hope these revisions strengthen the manuscript’s contribution as both a useful resource and a mechanistic investigation.

Not even acknowledged is the previous extensive work on the nucleoplasmic forms of LMNA isoforms - I know Robert Goldman published extensively on this, implicating lamin A, for example, on DNA replication in the nuclear interior as well as transcription. More recently, Roland Foisner worked on this, including with molecular approaches. For example, a 2017 review mentions previous ChIP-seq mapping of lamin A binding to iLAD genes and also describes previous work on chromatin mobility, including telomere mobility. Yet the entire writing in the manuscript seems to only discuss the role of LMNA isoforms in the nuclear lamina per se, explaining the surprise in seeing many iLAD genes differentially expressed after KD.

We have added related studies as suggested by the reviewer and  added the following statement: “Nucleoplasmic lamins bind to chromatin and have been indicated to regulate chromatin accessibility and spatial chromatin organization [24]. Lamins in the nuclear interior regulate gene expression by dynamically binding to heterochromatic and euchromatic regions, influencing epigenetic pathways and chromatin accessibility. They also contribute to chromatin organization and may mediate mechanosignaling [25]. However, the contribution of nesprins and lamins to isoform switch and chromatin dynamics has not been fully understood [7,10,26]. ”

Overall, I found a surprising lack of review and citation of previous work (see Specific comments below), including the lack of citations for various declarative statements about previous conclusions in the field about lamin A.

(1) Introduction:

"However, the contribution of nesprins and lamins to gene 220 expression has not been fully understood."

There is a literature about changes in gene expression- at least for lamin KD and KO- both in vitro and in vivo- that the authors could and should review and summarize here.

To address this, we have now revised the manuscript to include a more comprehensive discussion of the relevant literature and added appropriate citations in the corresponding section. We hope this addition provides better context for our current findings and clarifies the contribution of lamins and nesprins to gene regulation.

(2) Results:

"A fragment of shRNA that targeting 3' untranslated region (UTR) in LMNA genes was chosen to knockdown lamin A (shLaminA). A fragment of shRNA that targeting coding sequence (CDS) region in LMNA genes was chosen to knockdown LMNA (shLMNA)". The authors should explain more - does one KD both lamin A and C (shLMNA), versus the other being specific to lamin A but not lamin C? It appears so from later text, but the authors should explicitly explain their targeting strategy right at the beginning to make this clear.

To make the method clearer, we have clear added the text “The shRNA against lamin A (shLaminA) targets the 3′ untranslated region (UTR) of the LMNA gene, specific to prelamin A, which is post-translationally processed into mature lamin A. The shRNA designated as shLMNA targets a region within the coding sequence of LMNA that is shared by both lamin A and lamin C, corresponding to amino acids 122–129 (KKEGDLIA) of lamin A/C (RefSeq: NM_001406985.1). The shRNA against SYNE2 (shSYNE2) targets a sequence encoding amino acids 5133–5140 (KRYERTEF) of the SYNE2 protein (RefSeq: NM_182914.3).”

But more importantly, the convention with RNAi is to demonstrate consistent results with at least two different small RNAs. This is to rule out that a physiological result is due to the KD of a non-target gene(s) rather than the target gene. The scrambled shRNA controls are not sufficient for this as they test a general effect of the shRNA culture conditions, including tranfection and dox treatment, etc, rather than a specific KD of a different gene(s) than the target due to off-target RNAi.

We fully acknowledge the concern regarding the use of only a single shRNA per knockdown and agree that shRNAs are prone to off-target effects. However, we have conducted qPCR confirmation of key RNAseq findings, which strongly supports the specificity and validity of our observed results. Additionally, we recognize the importance of validating our findings using multiple independent shRNAs or alternative knockdown strategies, such as CRISPR deletion or degron-based approaches. To address this rigorously, we are currently optimizing an auxin-inducible degron system (AtAFB2) for targeted depletion of lamin C. Our preliminary data indicate approximately 40% knockdown efficiency after 16 hours of auxin induction, highlighting ongoing optimization efforts (Author response image 1). Future experiments will integrate this improved degron system and multiple independent shRNAs to further substantiate our results and definitively rule out potential off-target effects, thereby enhancing the robustness and reproducibility of our data.

(3) "Single-cell clones 114 were subsequently isolated and expanded in the presence of 2 μg ml-1 puromycin to 115 establish doxycycline-inducible shRNA-knockdown stable cell lines."

The authors need to describe explicitly in the Results how exactly they did these experiments. Did they do their analysis using a single clone from each lentivirus shRNA transduction? Did they do analysis - ie RNA-seq- on several clones from the same shRNA transduction and compare? Did they pool clones together?

In our study, single-cell clones and pooled the three independent clones were mixed following lentiviral transduction with doxycycline-inducible shRNA constructs and selected with 2 μg/ml puromycin. For each shRNA, we screened multiple clones for knockdown efficiency and selected a representative clone exhibiting robust knockdown for downstream experiments, including RNA-seq. We did pool three multiple clones; all functional analyses were performed on pooled clones. We have now revised the Method section to explicitly describe this experimental design: “Multiple independent clones per shRNA were screened for knockdown efficiency using reverse transcription quantitative real-time PCR (RT-qPCR). Three clones demonstrating robust and consistent knockdown were selected and expanded. These clones were subsequently pooled to minimize clonal variability and used for downstream analyses, including RNAseq.”

One confounding problem is that there are clonal differences among cells cloned from a single cell line. This is particularly true for aneuploid cell lines like U2OS. Ideally, they would use mixed clones, but if not, they should at least explain what they did.

We added the text to method “Three single-cell clones exhibiting robust knockdown efficiency were individually expanded and subsequently pooled. The pooled clones were maintained in medium containing 2 µg ml ¹ puromycin to establish stable cell lines with doxycycline-inducible shRNA expression. Multiple independent clones per shRNA were screened for knockdown efficiency using reverse transcription quantitative real-time PCR (RT-qPCR). Three clones demonstrating robust and consistent knockdown were selected and expanded. These clones were subsequently pooled to minimize clonal variability and used for downstream analyses, including RNA-seq.”

(4) I am confused by their shScramble control. This is typically done for each shRNA- ie, a separate scrambled control for each of the different target shRNAs. This is because there are nucleotide composition effects, so the scrambled idea is to keep the nucleotide composition the same.

However, looking at STable 1 and SFig. 2- shows they used a single scrambled control, thus not controlling for different nucleotide composition among the three shRNAs that they used.

In our study, we used a single non-targeting shRNA (shScramble) as a control to account for potential effects of the shRNA vector and delivery system. This approach is commonly accepted in the field when the scrambled sequence is validated as non-targeting and does not share significant homology with the genes of interest. While we acknowledge that using separate scrambled controls matched in nucleotide composition for each targeting shRNA can further minimize sequence-dependent effects, we believe that the use of a single validated scramble control is appropriate for the scope of this study.

(5) In Figure 2 - what is on the x-axis? Number of DEG? Please state this explicitly in the figure legend.

We have added “Counts” as figure legend, and added the caption “Gene counts are displayed on the x-axis.”

(6) More importantly, in Figure 2 they only show pathway analysis of DEG. They should show more: a) Fold-change of DEG displayed for all DEG; b) Same for genes in LADs vs iLADs. More explicitly, are the DEG primarily in LADs or iLADs, or a mix? Are the DEGs in LADs biased towards increased expression, as might be expected for LAD derepression? Conversely, what about iLADs - is there a bias towards increased or decreased expression?

We agree that a more detailed characterization of the differentially expressed genes (DEGs) will strengthen the conclusions. In response we have revised the manuscript as following: “Furthermore, differential expression analysis revealed that the majority of DEGs following depletion of lamins and nesprins were located outside lamina-associated domains (non-LADs). Specifically, for shLaminA knockdown, 8 DEGs within LADs were downregulated and 8 were upregulated, whereas 59 non-LAD DEGs were downregulated and 79 were upregulated. For shLMNA, 7 LAD-associated DEGs were downregulated and 15 were upregulated, with 88 downregulated and 140 upregulated DEGs in non-LAD regions. In the case of shSYNE2 knockdown, 161 LAD DEGs were downregulated and 108 were upregulated, while 2,009 non-LAD DEGs were downregulated and 1,851 were upregulated (Figure 2d). These results indicate that the transcriptional changes resulting from the loss of lamins or nesprins predominantly occur at non-LAD genomic regions.”

We appreciate the reviewer’s comments, which helped improve the clarity and depth of our analysis.

(7) Is there a scientific rationale for the authors' focus on DE of isoforms? Is this somehow biologically meaningful and different from the overall DE of all genes? The authors should explain in the Results section what their motivation was in deciding to do this analysis.

We have add the following statement in response to the reviewer “To uncover transcript-specific regulatory changes, we performed isoform-level differential expression analysis. Many genes produce functionally distinct isoforms, and shifts in their usage can occur without changes in total gene expression, making isoform-level analysis essential for detecting subtle but meaningful transcriptional regulation.  Our analysis demonstrated that depletion of lamins and nesprins induced significant alterations in specific transcript isoforms, indicating regulatory changes in alternative splicing or transcription initiation that are not captured by gene-level differential expression analysis.”

(8) "Expectedly, the DEGs from 327 depletion of lamin A, LMNA, and SYNE2 seldom intersected with genes in 328 LADs (Figure 4a)."

Why was this expected? The authors have only cited one review paper. Others have seen significant numbers of genes in LADs that are DE after KD of lamina proteins. What was the fold cutoff used for DE? Was there a cutoff for the level of expression prior to KD? The authors should cite relevant primary literature showing that there are active genes in LADs and that some perturbations of the lamina proteins do result in DE of genes in LADs.

We acknowledge the reviewer's concerns regarding our statement: "Expectedly, the DEGs from 327 depletion of lamin A, LMNA, and SYNE2 seldom intersected with genes in 328 LADs (Figure 4a)." To clarify, this expectation stems from previous observations that LAD-associated genes are typically transcriptionally silent or expressed at very low levels (Guelen et al., 2008). However, dynamic changes in LADs and gene expression status do occur during cellular differentiation (Peric-Hupkes et al., 2010), and some LAD-resident genes can become active and transcriptionally responsive under specific conditions, such as T cell activation. We applied specific foldchange and baseline expression level thresholds in our analysis, as detailed in the Methods section. We added the following text in the “Method”: “Differential gene expression analysis was performed using thresholds of baseMean > 50, absolute log fold change > 0.5, and p-value < 0.05.”  We agree that additional relevant primary literature demonstrating active gene expression changes within LADs upon perturbation of lamina proteins should be cited and we have added the following statement:

“LADs exhibit dynamic reorganization and changes in gene expression during cellular differentiation [30]. Although genes within LADs are generally transcriptionally silent or expressed at low levels [31], some LAD-resident genes remain active and can be transcriptionally modulated in response to specific stimuli, such as T cell activation [32].”

(9) "Expectedly, the DEGs from 327 depletion of lamin A, LMNA, and SYNE2 were seldomly intersected with genes in 328 LADs (Figure 4a)." I disagree with the wording of "seldom" which by definition means rarely. I don't see that this applies to the significant number of genes that are in LADs that are DE as shown in the Venn diagram, Fig. 4a. For example, this includes 57 genes for the shLamin A and ~400 genes for the shSYNE2.

Is there anything of note about which genes are DE within LADs?

We have rephrased the text to the following “The Venn diagram analysis revealed limited overlap between DEGs resulting from knockdown of lamin A (shLaminA), LMNA (shLMNA), or SYNE2 (shSYNE2) and genes located within laminaassociated domains (LADs). Specifically, only a small subset of DEGs intersected with LAD-associated genes across all three knockdowns, suggesting that the majority of transcriptional changes occur outside LAD regions”. The DEGs in LADs and non-LADs were shown in supplementary Table S4.

(10) "The relative distance from DE genes (query features) to LADs (reference feature) is plotted by GenometriCorr package (v 1.1.24). The color depicting deviation from the expected distribution and the line indicating the density of the data at relative distance are shown." The authors should explicitly describe what the reference "expected distribution" was based on. This is all very cryptic right now, so we can't assess the biological possible significance. Third, they should clearly explain what is plotted on the x and y axes of Figure 4C. I really don't have a clue. I assume the x-axis is some measure of "relative distance" but what on earth does that mean? I really don't understand this plot, which is crucial to the whole story. What is on the y-axis? Density of DEGs? What? And they need to explain not only what is plotted on the x and y axes but also provide units.

We have revised the text to clarify that the GenometriCorr analysis (v1.1.24) was used to assess the spatial association between differentially expressed genes (DEGs, query features) and lamina-associated domains (LADs, reference features). Specifically, this method evaluates whether the observed distances between query and reference genomic intervals significantly deviate from a null distribution generated by random permutation of query features across the genome, while preserving size and chromosomal context.

In the revised figure legend and main text, we now clarify that the x-axis represents the relative genomic distance between each differentially expressed gene (DEG) and the nearest LAD, scaled between –1 and 1, where values near 0 indicate close proximity, and values approaching –1 or 1 reflect greater distances on either side of the LADs. The y-axis denotes the density (or proportion) of query features (DEGs) at each relative distance bin. The color gradient overlays the plot to indicate deviation from the expected null distribution (based on randomized query positions): red indicates enrichment (closer than expected), while blue indicates depletion (further than expected).

“GenometriCorr analysis (v1.1.24) was used to assess the spatial relationship between DEGs (query) and LADs (reference) [48]. The x-axis shows the relative genomic distance between each DEG and the nearest LAD, scaled from –1 (far upstream) to 1 (far downstream), with 0 indicating closest proximity. The y-axis represents the density of DEGs at each distance bin. A color gradient indicates deviation from a randomized null distribution: red signifies enrichment (closer than expected), and blue signifies depletion. Statistical significance was determined using the Jaccard test (p < 0.05).”

Second, to correlate with other features and to give more meaning, the authors should show the chromosome location of the DEGs and scale this by the actual DNA sequence distances. This will be needed to correlate with other features from other studies.

The genomic positions of DEGs have now been displayed in Figure 4b, with distances shown in base pairs to facilitate cross-reference with other features in future studies.

Third, they should attempt some kind of analysis themselves to try to understand what might correlate with the DEGs. To begin with, they might try to correlate with lamin A ChiP-seq or other molecular proximity assays. Others in fact have shown that lamin A interacts with 5' regulatory regions of a subset of genes- presumably this is the diffuse nucleoplasmic pool of lamin A that has been studied by others in the past.

We agree that understanding potential regulatory mechanisms underlying DEG distribution is essential. In response, we have expanded our analysis (Figure 2d) to highlight that a substantial portion of DEGs are located outside of LADs, suggesting potential regulation by the nucleoplasmic pool of lamin A. This is consistent with previous studies showing lamin A interaction with regulatory elements such as 5′ UTRs and enhancers, independent of LAD localization. We have now cited relevant literature to support this hypothesis.

Fourth, in the table, they should go beyond just giving the fold change in expression. Particularly for genes that are expressed at very low levels, this is not particularly meaningful as it is very sensitive to noise. They should provide a metric related to levels of expression both before and after the KD.

We acknowledge the reviewer’s concern regarding fold-change interpretation for low-abundance transcripts. To improve clarity and interpretability, we have now included Supplementary Table S4, which provides the raw counts and baseMean values (average normalized expression across all samples) for all DEGs. Additionally, we note that in our differential expression analysis, genes with baseMean < 50 and absolute log₂fold change > 0.5 were filtered out to reduce potential noise from low-expression genes.

(11) The figure legend and description in the Results section were completely inadequate. I had little understanding of what was being plotted. It is not sufficient to simply state the name of some software package that they used to measure "XYZ" and to show the results. It has no meaning for the average reader.

Without some type of explanation of rationale, questions being asked, and conclusions made of biological relevance, this section made zero impact on me.

Yes- details can be provided in the Methods. But conceptually, the methods and the conceptual underpinnings of the approach and as the question being asked and the rationale for the approach, with the significance of the results, need to be developed in the Results section.

In response, we have revised the “Results” section to better articulate the rationale behind the analysis, the specific biological questions we aimed to address, and the conceptual relevance of the method used. We have also clarified the meaning of the plotted data and how it supports our conclusions.

While technical details remain in the “Methods” section, we now provide a more accessible narrative in the Results to guide the reader through the approach and highlight the biological significance of our findings. We hope these revisions make the section more informative and impactful.

(12) The telomere movement part of the manuscript seems to come out of nowhere. Why telomeres? Where are telomeres normally positioned, particularly relative to the nuclear lamina? Does this change with the KDs - particularly for those that increase motion? The MSD for SYNE2 appears unconstrained- they should explore longer delta time periods to see if it reaches a point of constrained movement.

If the telomeres are simply tethered at the nuclear lamina, then is that the explanation- that they become untethered? But if they are not typically at the periphery, then where are they relative to other nuclear compartments? And why is there mobility changing? Is it related to the loss of nuclear lamina positioning of adjacent LAD regions to the telomeres? Is it an indirect, secondary effect? What would they see after an acute KD? What about other chromosome regions? Again, there is little explanation for the rationale for these observations. It is one of many possible experiments they could have done. Why did they do this one?

We added the following explanation “Although telomeres are not uniformly tethered to the nuclear lamina, they can transiently associate with the nuclear periphery, particularly during post-mitotic nuclear reassembly, through interactions involving SUN1 and RAP1 36. Given that lamins and nesprins are key components of the nuclear envelope that regulate chromatin organization and mechanics 37,38, we examined telomere dynamics as a proxy for changes in nuclear architecture. Using EGFP-tagged dCas9 to label telomeric regions in live U2OS cells, we assessed whether knockdown of these proteins leads to increased telomere mobility, reflecting a loss of structural constraint or altered chromatin–nuclear envelope interactions 17.” And “To probe how nuclear envelope components regulate chromatin dynamics, we tracked telomeres as a representative genomic locus whose mobility reflects changes in nuclear mechanics and chromatin organization. Although telomeres are not stably tethered to the nuclear lamina, their motion can be influenced by nuclear architecture and transient peripheral associations [36]. Upon depletion of lamin A, LMNA, or SYNE2, we observed significantly increased telomere mobility and nuclear area explored, quantified by mean square displacement and net displacement (Figure 6b–c, Supplementary Movie S1). These changes likely reflect altered chromatin–lamina interactions or disrupted nuclear mechanical constraints, consistent with prior studies showing that lamins modulate chromatin dynamics and nuclear stiffness [37,38,39]. Thus, our findings support a role for lamins and nesprins in constraining chromatin motion through nuclear structural integrity.”

(13) "Notably, Lamin A depletion led to enrichment of 392 pathways associated with RNA biosynthesis, supporting its previously suggested role 393 in transcriptional activation and ribonucleotide metabolism."

There is a literature on this. Say more and cite the references.

Notably, lamin A depletion led to enrichment of pathways associated with RNA biosynthesis, supporting its previously suggested role in transcriptional activation and ribonucleotide metabolism 45.  

(14) "This aligns with prior studies indicating that Lamin A contributes to chromatin accessibility and RNA polymerase activity." Again, there is a literature on this. Say more and cite the references.

This aligns with prior studies indicating that lamin A contributes to chromatin accessibility and RNA polymerase activity 46. These findings further underscore the functional relevance of lamin A in coordinating transcriptional programs through modulation of nuclear architecture.

(15) "In contrast, LMNA knockdown was linked to alterations in chromatin conformation." No. The authors show gene ontology and implicate perturbed RNA levels for genes implicated in "chromatin conformation". That is not the same thing as measuring chromatin conformation, which is not done, and showing changes in conformation.

Based on the reviewer’s comment we have revised the text as the following: “In contrast, LMNA knockdown led to differential expression of genes enriched in pathways related to chromatin organization, suggesting potential disruptions in chromatin regulatory networks. Although direct measurements of chromatin conformation were not performed, these transcriptional changes indicate that LMNA may contribute to maintaining nuclear architecture and genomic stability, which aligns with its established involvement in laminopathies and genome integrity disorders.”

(16) "The findings that DEGs are predominantly located in non-LAD regions highlight a unique regulatory aspect of lamins and nesprins, emphasizing their spatial specificity in gene expression". Is this novel? Can the authors separate direct from indirect effects? Is the percentage of genes in LADs that are altered in expression different from the percentage of genes in iLADs that are altered in expression? There are many more active genes in iLADs, so one expects more DEGs in iLADs even if this is random. Also - how does this correlate with lamin A binding near 5' regulatory regions detected by ChIP-seq? See the following review for references to this question and also previous work on lamin A versus chromatin mobility, including telomeres. J Cell Sci (2017) 130 (13): 2087-2096. https://doi.org/10.1242/jcs.203430

We appreciate the reviewer’s valuable comments and feedback, we have revised the manuscript as the following to address the feedback. “Furthermore, differential expression analysis revealed that the majority of DEGs following depletion of lamins and nesprins were located outside lamina-associated domains (non-LADs). Specifically, for shLaminA knockdown, 8 DEGs within LADs were downregulated and 8 were upregulated, whereas 59 non-LAD DEGs were downregulated and 79 were upregulated. For shLMNA, 7 LAD-associated DEGs were downregulated and 15 were upregulated, with 88 downregulated and 140 upregulated DEGs in non-LAD regions. In the case of shSYNE2 knockdown, 161 LAD DEGs were downregulated and 108 were upregulated, while 2,009 non-LAD DEGs were downregulated and 1,851 were upregulated (Figure 2d, Supplementary Table S4). These results indicate that the transcriptional changes resulting from the loss of lamins or nesprins predominantly occur at non-LAD genomic regions.

The percentage of DEGs was consistently higher in non-LADs, which are gene rich and transcriptionally active, whereas LADs, known to be enriched for silent or lowly expressed genes, showed fewer expression changes. These findings are consistent with previous studies demonstrating that active genes are more prevalent in non-LADs and that LAD associated genes are generally repressed or less responsive to perturbation [27,28]. Together, these results support a model in which lamins and nesprins influence gene expression through both structural organization and promoter proximal interactions, particularly within euchromatic nuclear regions [10,26,29].”

eLife Assessment

This important work represents an advance in our understanding of resident myeloid cells in the zebrafish brain, particularly as it provides a molecular definition of dendritic cell subtypes associated with their localization. Combined evidence from single cell transcriptomics and histology is compelling. The associated atlas will be used as a resource by the zebrafish community and beyond.

Reviewer #1 (Public review):

Using several zebrafish reporter lines, the authors characterized immune cells in the adult zebrafish brain, identifying a population of DC-like cells with distinct regional distribution and transcriptional profiles. These cells were distinct from microglia and other macrophages, closely resembling murine cDC1s. Analysis of different mutants revealed that this DC population depends on Irf8, Batf3 and Csf1rb, but not Csf1ra.

This elegantly designed study provides compelling evidence for additional heterogeneity among brain mononuclear phagocytes in zebrafish, encompassing microglia, macrophages, and DC-like cells. It advances our understanding of the immune landscape in the zebrafish brain and facilitates better distinction of these cell types from microglia.

Reviewer #2 (Public review):

The authors made an atlas of single-cell transcriptome of on a pure population of leukocytes isolated from the brain of adult Tg(cd45:DsRed) transgenic animals by flow cytometry. Seven major leukocyte populations were identified, comprising microglia, macrophages, dendritic-like cells, T cells, natural killer cells, innate lymphoid-like cells and neutrophils. Each cluster was analyzed to characterize subclusters. Among lymphocytes, in addition to 2 subclusters expressing typical T cell markers, a group of il4+ il13+ gata3+ cells was identified as possible ILC2. This hypothesis is supported by the presence of this population in rag2KO fish, in which the frequency of lck and zap70+ cells is strongly reduced. The use of KO lines for such validations is a strength of this work (and the zebrafish model).

The subcluster analysis of mpeg1.1 + myeloid cells identified 4 groups of microglial cells, one novel group of macrophage like cells (expressing s100a10b, sftpbb, icn, fthl27, anxa5b, f13a1b and spi1b), and several groups of DC like cells expressing the markers siglec15l, ccl19a.1, ccr7, id2a, xcr1a.1, batf3, flt3, chl1a and hepacam2.Combining these new markers and transgenic reporter fish lines, the authors then clarified the location of leukocyte subsets within the brain, showing for example that DC-like cells stand as a parenchymal population along with microglia. Reporter lines were also used to perform detailed analysis of cell subsets, and cross with a batf3 mutant demonstrated that DC like cells are batf3 dependent, which was similar to mouse and human cDC1. Finally, analysis of classical mononuclear phagocyte deficient zebrafish lines showed they have reduced numbers of microglia but exhibit distinct DC-like cell phenotypes. A weakness of this study is that it is mainly based on FACS sorting, which might modify the proportion of different subtypes.

This atlas of zebrafish brain leukocytes is an important new resource to scientists using the zebrafish models for neurology, immunology and infectiology, and for those interested in the evolution of brain and immune system.

Reviewer #3 (Public review):

Rovira, et al., aim to characterize immune cells in the brain parenchyma and identify a novel macrophage population referred to as "dendritic-like cells". They use a combination of single-cell transcriptomics, immunohistochemistry, and genetic mutants to conclude the presence of this "dendritic-like cell" population in the brain. The strength of this manuscript is the identification of dendritic cells in the brain, which are typically found in the meningeal layers and choroid plexus. In addition, Rovira, et al., findings are supported by the findings of the Wen lab and a recent Cell Reports paper. Congratulations on the nice work!

Author response:

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

Reviewer #1 (Public Review):

Weaknesses:

While scRNA-seq data clearly revealed different subsets of microglia, macrophages, and DCs in the brain, it remains somewhat challenging to distinguish DC-like cells from P2ry12- macrophages by immunohistochemistry or flow cytometry.

Indeed, in flow cytometry analyses of adult brain samples, the p2ry12^-; mpeg1⁺ fraction could, in theory, encompass not only DC-like cells but also other macrophage subsets, as well as B cells, since B cells have been reported to express mpeg1 in zebrafish (Ferrero et al., 2020; Moyse et al., 2020). Nevertheless, our data strongly indicate that within the brain parenchyma, DC-like cells represent the predominant component of this population. This conclusion is supported by the pronounced reduction of p2ry12^-; mpeg1⁺ cells in brain sections from ba43 mutants, in which DC development is impaired. Currently, further phenotypic resolution is constrained by the limited availability of zebrafish-specific antibodies and the restricted palette of fluorescent reporter lines capable of distinguishing MNP subsets. We anticipate that future efforts, including the generation of novel transgenic lines informed by our dataset (initiatives already underway in our group), will enable more precise discrimination among these distinct subsets.

Reviewer #2 (Public Review):

A weakness of this study is that it is mainly based on FACS sorting, which might modify the proportion of different subtypes.

We agree that reliance solely on FACS could potentially introduce biases in the proportions of different subtypes. To minimize this concern, we complemented our flow cytometry data with quantification performed directly on brain sections using immunohistochemistry. This approach allowed us to validate cell population distributions in situ, thereby confirming that the trends observed by FACS accurately reflect the cellular composition of microglia and DC-like cells within the brain parenchyma.

Reviewer#3 (Public Review):

A weakness is the lack of specific reporters or labeling of this dendritic cell population using specific genes found in their single-cell dataset. Additionally, it is difficult to remove the meningeal layers from the brain samples and thus can lead to confounding conclusions. Overall, I believe this study should be accepted contingent on sufficient labeling of this population and addressing comments.

While the generation of DC-like specific transgenic lines is indeed a promising direction (and such efforts are currently underway in our group), creating and validating these lines is time-consuming. Importantly, although these additional tools will be valuable for future functional investigations, we believe they would not impact the main conclusions or core message of our current work, where we already provide detailed spatial information on DC-like cells, and we demonstrated their lineage identity through the use of our newly generated batf3 mutant line. 

Recommendations for the authors:

Major Comments: 

The authors should discuss another recent report demonstrating DCs in the zebrafish brain, which also developed independently of Csf1ra, and compare the two datasets (Zhou et al. Cell reports, 2023).

Thank you for highlighting the study by Zhou et al., which offers complimentary insight into the dendritic cell population in the zebrafish brain. We note that in this work, the authors reclassify ccl34b.1^- mpeg1⁺ brain-resident cells as conventional DCs, thus revising their earlier interpretation of these cells as microglia (Wu et al., 2020). This shift in interpretation is based on their transcriptional comparison between the previously characterized ccl34b.1^- mpeg1⁺ population and a new dataset of brain

mpeg1⁺ cells. This updated classification aligns closely with our findings. Given that our data already demonstrate the equivalence between the DC-like cells described in our study and the ccl34b.1^- mpeg1⁺ population, repeating a direct transcriptional comparison would be redundant. We have now included a discussion of this work in the revised manuscript. Specifically, we have added the following sentences in the discussion: “Importantly, since the submission of our manuscript, the Wen lab published an independent study in which they now reclassify the ccl34b.1^- mpeg1⁺ cells in the zebrafish brain as cDCs, revising their earlier interpretation of these cells as microglia (Zhou et al., 2023)”. 

Data reported in Figure 5 should be quantified (cell numbers, how many brains analyzed). 

Thank you for this comment. We would like to clarify that the primary purpose of Figure 5 (and Figure 5 supplement 1) is to provide an initial qualitative overview of the different MNP subsets present in the adult brain, using the currently available transgenic and immunohistochemical tools. These descriptive analyses were instrumental in identifying the most reliable combination, namely the Tg(p2ry12:p2ry12GFP; mpeg1.1:mCherry) double transgenic line in conjunction with L-plastin immunostaining, to distinguish microglia from other parenchymal MNPs. Quantitative analyses using this optimized strategy are presented in Figure 7 (Figure 7 supplement 1), where we systematically enumerate the different MNPs. We therefore believe that performing additional quantification in Figure 5 would be redundant with the more robust data already shown in Figure 7. As requested, we have now included in the Figure 5 legend that images are representative of brain tissue sections from 2-3 fish. 

The title mentions an "atlas", but there is no searchable database or website associated with the paper. Please provide one.

We agree and fully support the importance of data accessibility. To facilitate use of our dataset by the scientific community, we have developed a user-friendly, searchable web interface that allows users to explore gene expression pacerns within our dataset. This website is available at https://scrna-analysis zebrafish.shinyapps.io/scatlas/

This information has now been included in the “Data availability statement” section of the manuscript.  

Reviewer #1 (Recommendations For The Authors): 

Specific comments: 

The authors should discuss another recent report demonstrating DCs in the zebrafish brain, which also developed independently of Csf1ra, and compare the two datasets (Zhou et al. Cell reports, 2023). 

Thank you for this suggestion. Please refer to our response in the major comments section, where we address this point in detail.

Within macrophages, the authors identified 5 clusters including 4 microglia clusters and 1 MF cluster (Figure 4). Does the laUer relate to 'BAMs' and express markers previously described in murine BAMs, including Lyve1, CD206, etc.? Or to monocytes? By flow cytometry, monocytes were detected (Figure 1B), but not by scRNA-seq.  

You have raised an important point here. As described in lines 197-202 (“results” section), the cells in the MF cluster exhibit a macrophage identity, based on their expression of classical macrophage markers such as marco, mfap4 or csf1ra. However, we were unable to confidently annotate this cluster more specifically. We also considered whether this population might resemble mammalian BAMs or monocytes, cell types that, to our knowledge, have not yet been clearly identified in zebrafish. However, orthologous markers typically associated with murine BAMs were not detected (lyve1) or not specifically enriched (mrc1a/mrc1b) in the MF cluster (see below). Based on these findings, we can only cautiously propose that this cluster may represent blood-derived macrophages and / or monocytes.

To further address your suggestion, we performed a cell type enrichment analysis using the marker genes of the MF cluster, following the same strategy as for the microglia and DC-like clusters presented in Figure 4 supplement 2 C,D. This analysis revealed significant for “monocytes” and “macrophages”, further supporting a general monocytic/macrophage identity (see below). At present, further characterization of this cluster is limited by the lack of zebrafish-specific antibodies and the restricted palette of fluorescent reporter lines that distinguish among MNP subsets. We anticipate that future studies, including the development of new transgenic lines guided by our dataset, will allow for a more precise analysis of this distinct population. 

Author response image 1.

Do all 4 DC clusters identified by scRNA-seq represent cDC1s? or are there also cDC2s, and cDC3s present?  

In our analyses, the four dendritic cell clusters identified by scRNA-seq (DC1-DC4) exhibit transcriptional profiles consistent with a conventional type 1 dendritic cell (cDC1) identity. These clusters uniformly express hallmark cDC1-associated genes, while lacking expression of markers typically associated with mammalian cDC2 or plasmacytoid dendritic cells (pDCs). For instance, irf4, a key transcription factor required for cDC2 development, is not detected in our dataset. Similarly, we do not observe expression of genes characteristic of pDCs. 

That said, the absence of cDC2 or pDC-like signatures in our dataset does not rule out the presence of these populations in zebrafish.  

While they show that DC-like cells did not express Csf1rb (Figure 4D) or other macrophage/microglia genes, DC-like cells were affected in the Csf1rb mutants and in double mutants, demonstrating that their development depends on Csf1rb signaling, as known for macrophages but not DCs. Can the authors discuss this in more detail with regard to DC differentiation/precursors? 

Thank you for pointing this out. As previously demonstrated, CSF1R signaling in zebrafish is more complex than in mammals, due to the presence of two paralogs, csf1ra and csf1rb, which exhibit partially non-overlapping functions (Ferrero et al., 2021). We and others have shown that csf1rb signaling is implicated in the regulation of definitive hematopoiesis, particularly in the regulation of hematopoietic stem cell (HSC)-derived myelopoiesis. Although the developmental origin of zebrafish brain DC-like cells remains uncharacterized, their reduced numbers in the csf1rb mutant, despite their lack of csf1rb expression, supports the current model in which csf1rb acts at the progenitor level, promoting myeloid lineage commitment. According to this, csf1rb disruption affects the differentiation of multiple myeloid subsets, which likely include DC-like cells. We have developed this point in the discussion section (lines 502506).  

Do the DCs express Csf1ra? 

Csf1ra transcripts are not found in DCs in our dataset. As shown below, csf1ra expression is restricted to the microglia and macrophage clusters. These observations are in line with those made by Zhou et al., 2023.

Author response image 2.

Fig. 5, the number of brains analyzed should be added, and also quantifications of cell numbers included. It is mentioned (line 260) that P2ry12GFP+mpeg1mCherry+ microglia are abundant across brain regions while P2ry12GFP- mpeg1mCherry+ cells particularly localize in the ventral part of the posterior brain parenchyma. It would be nice if images of the different brain regions were provided. 

Regarding the quantification, we refer to our response in the major comments section, where we explain that detailed quantification of microglia and other MNP subsets is provided in Figure 7, using a more refined strategy for distinguishing cell types.

As requested, we have now included representative sections from the forebrain, midbrain and hindbrain of adult Tg(mhc2dab:GFP; cd45:DsRed) fish. These images illustrate the spatial distribution of DC-like cells across brain regions. Notably, DC-like cells are most abundant in the ventral areas of the midbrain and hindbrain, and are also present in the posterior telencephalon, particularly concentrated in the region of the commissura anterior. This regional annotation is based on the zebrafish brain atlas by Wullimann et al., 1996 (Neuroanatomy of the zebrafish brain, https://doi.org/10.1007/978-3-0348-8979-7).

These additional images have been included in Figure 5 Supplement 1 (A-E).

It is sometimes not evident whether the Pr2y12- cells included DC-like cells and macrophages, which should be discussed. 

Thank you for bringing this to our attention. Upon review, we agree this point required clearer explanation throughout the text, particularly beginning with the description of putative DC-like cells in Figure 5. We have now revised the manuscript to improve clarity and becer guide readers through the phenotypic identification of DC-like cells using the Tg(p2ry12:p2ry12-GFP;mpeg1:mCherry) line. Specifically, we have modified the titles in the results section from page 5 to page 9, so that readers can more easily follow the step-by-step approach we used to distinguish DC-like cells from microglia. 

To directly address your comment: the p2ry12^-; mpeg1⁺ fraction may, in theory, include not only DC-like cells but also other macrophage subsets and B cells, as B cells have been shown to express mpeg1 in zebrafish (Ferrero et al., 2020; Moyse et al., 2020). Nevertheless, our data strongly indicate that within the brain parenchyma, DC-like cells represent the predominant component of this population. This conclusion is supported by the pronounced reduction of p2ry12^-; mpeg1⁺ cells in brain sections from ba43 mutants, in which DC development is impaired. 

We have revised the text accordingly to clarify this point in the results section of the manuscript (line 355).

For example, the DC-like cell population in Figure 6C appears to include two populations of cells. Thus, it is unclear whether the sorted mhc2dab:GFP+;CD45:DsRedhi population for bulk-seq also contains the MF population identified in Fig. 2. 

Thank you for this thoughtful observation. During the course of this study, we indeed considered how best to isolate non-microglial macrophages in order to specifically recover the MF population identified in our scRNA-seq analysis. However, with the current repertoire of fluorescent transgenic zebrafish lines, it remains technically challenging to selectively isolate non-microglial macrophages from the adult brain. As a result, the mhc2dab:GFP₊; cd45:DsRedhi sorted population used for bulk RNA-seq may indeed include a mixture of DC-like and other mononuclear phagocytes, potentially the MF population. In contrast, our data demonstrate that the Tg(p2ry12:p2ry12-GFP) line provides a more selective tool for isolating microglia, minimizing contamination from other mononuclear phagocyte subsets.

In Figure 7, a reduction of GFP-mpeg+ cells can be seen in baf3 mutants. Could the remaining cells be the (non-microglia) macrophages? Or in Figure 8, could the remaining P2ry12GFP-Lcp1+ cells in Irf8 mutants be macrophages? 

Indeed, we believe it is likely that the remaining mpeg1⁺ cells observed in ba43 mutants include non-microglial macrophages and/or B cells, as we and others previously showed that zebrafish B cells express mpeg1.1 transcripts and are labeled in the mpeg1.1 reporters (Ferrero et al., 2020). This interpretation is further supported by the observation that the reduction in mepg1+ cells is more pronounced in brain sections than in flow cytometry samples, where non-parenchymal mpeg+ cells, such as peripheral macrophages or B cells, are likely enriched. To explore this possibility, we attempted to assess the expression of MF- and B cell-specific markers in the remaining mpeg1+ population isolated from ba43 mutants. However, due to the very low numbers of cells recovered per animal, we were limited to analyzing only a few markers. Despite multiple attempts, qPCR analyses proved unconclusive, likely due to low transcript abundance. We thank you for your understanding of the technical limitations that currently prevent a more definitive characterization of these remaining cells.  

Regarding the irf8 mutants (Figure 8), irf8 is a well-established master regulator of mononuclear phagocyte development. In mice, deficiency results in developmental defects and functional impairments across multiple myeloid lineages, including microglia, which exhibit reduced density (Kierdorf et al., 2013) and an immature phenotype (Vanhove and al., 2019). Similarly, in zebrafish, irf8 mutants show abnormal macrophage development, with an accumulation of immature and apoptotic cells during embryonic and larval stages (Shiau et al., 2014). Based on these findings, it is plausible that the residual p2ry12:GFP^- Lcp1⁺ cells observed in the irf8 mutant brains represent immature or arrested mononuclear phagocytes, possibly including both microglia and DC-like cells. This is supported by their distinct morphology and specific localization along the ventricle borders. However, as previously noted, our current tools do not permit to conclusively identify these cells.

Reviewer #2 (Recommendations For The Authors): 

A few sentences are not easy to understand for a "non zebrafish specialist". 

(1) Page 3 line 111 The sentence "Interestingly, analyses of brain cell suspensions from double transgenics showed p2ry12:GFP+ microglia accounted for half of cd45:DsRed+ cells (50.9 % {plus minus} 2.9; n=4) (Figure 1D,E). Considering that mpeg1:GFP+ cells comprised ~75% of all leukocytes, these results indicated that approximately 25% of brain mononuclear phagocytes do not express the microglial p2ry12:GFP+ transgene." is not clear. This point is significant and deserves a more detailed explanation. 

We apologize for the lack of clarity in this section. The quantification presented in Figure 1 refers specifically to cd45:Dsred⁺ leukocytes, meaning that the reported percentages of p2ry12:GFP⁺ and mpeg1:GFP⁺ cells are calculated relative to the total cd45+ population (defined as 100%). Specifically, we observed that approximately 51% of all cd45+ cells were p2r12:GFP⁺ microglia, while around ti5% were mpeg1:GFP⁺. From these values, we infer that about 25% of mpeg1:GFP⁺ leukocytes do not express the p2ry12:GFP transgene and therefore likely represent non-microglial mononuclear phagocytes. We agree that this distinction is important and have revised the text accordingly to clarify the interpretation for readers who may be less familiar with zebrafish transgenic lines or gating strategies. See page 3, lines 107 117.

(2) Line 522; Like human and mouse ILC2s, "these cells do not express the T cell receptor cd4-1" is confusing (T cell receptor should be reserved to the ag specific TCR). Also, was TCR isotypes expression analyzed (and how was genome annotation used in this case ?) 

Thank you for this insightful comment.  We agree that the term “T cell receptor” should be used specifically to refer to antigen-specific TCRs, and we have revised the discussion accordingly to avoid any confusion. Regarding your question on the analysis of TCR isotype expression and the use of genome annotation: due to technical limitations, we did not pursue TCR isotype-level analysis in this study. Instead, we relied on established markers such as cd4-1 and cd8a to distinguish T cell populations, acknowledging that cd4-1 is not expressed by ILC2-like cells in our dataset. We have clarified these points in the relevant sections of the manuscript (see lines 168 and 535)

The analysis of single-cell data might be more detailed, with more explanation about possible doublet identification and normalization procedures. 

Thank you for highlighting the need for additional clarity regarding our scRNA-seq analysis.

As noted in the Seurat tutorial, “cell doublets or multiplets often exhibit abnormally high gene count” (https://sa7jalab.org/seurat/archive/v3.0/pbmc3k_tutorial). To evaluate this, we performed a dedicated doublet detection analysis using the scDblFinder R package (https://rdrr.io/bioc/scDblFinder/f/vigneces/2_scDblFinder.Rmd). Our results indicated that the proportion of predicted doublets is low (see Figure below), and when present, these doublets are distributed among the different clusters. This contrasts with the typical clustering of doublets into discrete groups and indicates that our single-cell sequencing workflow was sufficiently robust to predominantly capture singlets.

Regarding normalization, we have clarified this in the manuscript. Briefly, single-cell data were normalized using Seurat’s SCTransform method with the following custom parameters: “variable.features.n=4000 and return.only.var.genes=F”. These settings are now clearly described to ensure reproducibility.

Author response image 3.

Reviewer #3 (Recommendations For The Authors):

Major issues

Though baf3 mutants were generated the manuscript will greatly benefit from in situ labeling by RNAscope or the generation of transgenic reporters to conclusively localize this dendritic cell population and address any potential contamination issues. 

We thank you for this constructive suggestion. We agree that in situ labeling approaches such as RNAscope would offer valuable complementary insights. In our current study, however, we already provide detailed spatial information on DC-like cells, and we demonstrated their lineage identity through the use of our newly generated batf3 mutant line. 

To address concerns regarding potential contamination, we have carefully analyzed more than two dozens adult brains to date and consistently observed abundant DC-like cells within the brain parenchyma, exhibiting a reproducible and specific spatial distribution, as described in the manuscript. This consistent localization across multiple samples strongly supports the genuine presence of these cells in the brain rather than artifactual contamination.

While the generation of DC-like specific transgenic lines is indeed a promising direction (and such efforts are currently underway in our group) we note that creating and validating these lines is time-consuming and falls beyond the scope of the present study. Importantly, although these additional tools will be valuable for future functional investigations, we believe they would not impact the main conclusions or core message of our current work. 

The morphological characterization of CD45:DsRed+ macrophages stained with May-Grunwald-Giemsa has been previously reported in the paper, "Characterization of the mononuclear phagocyte system in the zebrafish" Wittamer et al., 2011."Morphologic analyses revealed that the majority of cells exhibited the characteristics of monocytes/macrophages namely low nuclear to cytoplasm ratios and a high number of cytoplasmic vacuoles (Figure 3B). 

We thank you for pointing out the reference to Wittamer et al., 2011. In that study, we indeed provided the first morphological characterization of mononuclear phagocytes (MNPs) in various adult zebrafish organs using the cd45:DsRed line in combination with the mhc2dab:GFP reporter. The focus was primarily on MNPs across peripheral tissues. In the current study, our aim is broader: we investigate the full diversity of brain immune cells, using cd45 as a general marker for leukocytes. As part of this comprehensive characterization, we applied MGG staining, a widely accepted cytological technique, to gain morphological insight into the sorted CD45:DsRed+ population. This method remains a valuable and rapid approach to visually assess cell type heterogeneity, especially when evaluating samples where multiple immune cell lineages may be present. 

While there is some overlap with the methodology used in Wittamer et al., the context, scope, and tissue examined differ substantially. Thus, the inclusion of MGG staining in this study serves to complement our broader transcriptomic analyses by providing supporting morphological evidence specific to brain-resident immune cells.

We have now clarified this distinction in the revised manuscript to better differentiate the current work from our previous findings (see line 85).

Figure 5 data should be quantified.

Please refer to our response in the major comments section, where we address this question in detail.

Figure 7- Figure Supplement 1. J, K has no CD45:DsRed positive cells in baf3 mutants, which is counterintuitive because CD45:DsRed should capture all hematopoietic cells and is not specific to dendritic cells. 

It is correct that cd45 is a general leukocyte marker, labeling all immune cells, including dendritic cells. In this Figure, we used the Tg(cd45:DsRed) transgenic line to visualize the phenotype because it offers an alternative to IHC, with the advantage of strong endogenous fluorescence and easier screening of vibratome sections. However, this technique has limitations: due to fixation, only cells with high fluorescence (e.g. cd45^highdendritic cells) are captured, while those with medium/low expression (e.g. cd45^low microglia) are often not visible. This explains why fewer cells are observed in both wild-type and ba43 mutant brains (Figure 5 KN, Figure 7 – supplement 1 JK). While this approach is quicker and allows for thicker sections, IHC remains the preferred method for the rest of the analyses, including the use of additional markers to identify all relevant cell populations. 

Thank you for bringing this point of confusion to our attention. To improve clarity, we have amended the text in the relevant sections (see lines 704-706, and legend of Figure 7 Supplement 1)

Minor issues: 

The terms in the title, "A single-cell transcriptomic atlas..." are used. What is meant by "atlas"? A searchable database or website is not provided.

Please refer to our response in the major comments section, where we explain that we have made our dataset accessible through a searchable web interface (https://scrna-analysiszebrafish.shinyapps.io/scatlas/) which is now referenced in the Data Availability Statement.

This reviewer considers that it is offensive to use terminology such as "poorly characterized" in reference to others' work. 

Thank you for pointing this out. We understand the concern and have revised the wording to ensure it remains respectful and neutral when referring to previous work. The changes are reflected in lines 20 and 49.

The introduction of this manuscript should consider restructuring and editing. Example: Lines 51-57 introduce the importance of immune cells in zebrafish regeneration studies. However, this study does not investigate such processes. Additionally, the authors focus on the concept of immune heterogeneity in the brain throughout the text however, these studies have been conducted previously by others (Silva et al., 2021) at single-cell level.

The novelty of this manuscript is the identification of "dendritic-like cells" and yet the introduction and text are limited to 68-71 lines. The introduction would benefit by introducing this cell type "dendritic-like cells" and differences between vertebrates. 

Thank you for these valuable comments. In response, we have revised the introduction to better align with the focus of the study (see edited text in page 2). We now emphasize that, while macrophages have been extensively studied in zebrafish, dendritic cells remain much less well characterized in this model.  Also, while we acknowledge that Silva et al. addressed aspects of immune heterogeneity in the zebrafish brain, their study primarily focused on mononuclear phagocytes. In contrast, our work provides a broader and more detailed characterization of the brain immune landscape, integrating transcriptomic data with multiple fluorescent reporter lines and hematopoietic mutants to strengthen cell identity assignments. Importantly, we note that Silva et al. classified DC-like cells within the microglial compartment, whereas our findings support that these cells represent a distinct population. While our data challenge this specific aspect of their conclusions, we believe both studies offer complementary insights that collectively advance our understanding of zebrafish brain immunity. 

Though Figure 6 is a great conformation of scRNA sequencing, it seems redundant and should be supplemental data.

We respectfully disagree with the reviewer’s suggestion. We believe that presenting the data in Figure 6 as the main figure enhances its visibility and impact, particularly highlighting the distinction between microglia and DC-like cells, an aspect we consider highly valuable information for the zebrafish research community. This is especially important given that our conclusions challenge two previous independent reports, further underscoring the relevance of these findings to the field.

eLife Assessment

This work provides high-precision single-cell data on the relationship between DnaA activity and cell size, offering important insights for the field of cell cycle control. These findings motivate a novel and intriguing hypothesis for DNA replication initiation -the "extrusion model"- in which DNA-binding proteins modulate free DnaA availability in response to biomass-DNA imbalance. While the current indirect evidence does not fully establish the model, an experimental perturbation involving H-NS offers convincing support for its plausibility, laying the groundwork for future investigation.

Reviewer #1 (Public review):

Summary:

The study by Li and coworkers addresses the important and fundamental question of replication initiation in Escherichia coli, which remains open despite of many classic and recent works. It leverages single-cell mRNA-FISH experiments in strains with titratable DnaA and novel DnaA activity reporters to monitor DNA activity peaks versus size. The authors find oscillations in DnaA activity and show that their peaks correlate well with the estimated population-average replication initiation volume across conditions and imposed dnaA transcription levels. The study also proposes a novel and interesting extrusion model where DNA-binding proteins regulate free DnaA availability in response to biomass-DNA imbalance. Experimental perturbations of H-NS support the model validity, addressing key gaps in current replication control frameworks.

Strengths:

I find the study interesting and well conducted, and I think its main strong points are (i) the novel reporters obtained with systematic synthetic biology methods, and combined with a titratable dnaA strain, (ii) the interesting perturbations (titration, production arrest and H-NS) and (iii) the use of single-cell mRNA FISH to monitor transcripts directly. The proposed extrusion model is also interesting, though not fully validated, and I think it will contribute positively to the future debate.

Weaknesses and Limitations

A relevant limitation in novelty is that DnaA activity and concentration oscillations have been reported by the cited Iuliani and coworkers previously by dynamic microscopy, and to a smaller extent by the other cited study by Pountain and coworkers using mRNA FISH.

An important limitation is that the study is not dynamic. While monitoring mRNA is interesting and relevant, the current study is based on concentrations and not time variations (or nascent mRNA). Conversely, the study by Iuliani and coworkers, while having the drawback of monitoring proteins it can access directly production rates. It would be interesting for future studies to monitor the strains and reporters dynamically, as well as using (as a control) the technique of this study on the chromosomal reporters used by Iuliani et al.

While the implemented code is made available and the parameter values are given in the text, important details are missing regarding the mathematical models (mathematical definitions, clear discussions of ingredients and main assumptions, and choices made in the deployment of such models, which are presented briefly in the Methods section). The reader is not given sufficient tools to understand the predictions of different models and no analytical estimates are used and the falsification procedures are not clear. More transparency and depth in the analysis would be needed to use the models as more than a heuristic tool for qualitative arguments. The Berger model for example has many parameters and many regimes and behaviors. When models are compared to data (e.g. in fig. 2G) it is not clear how parameters were fixed, and whether and how the model prediction depends on adjustable parameters.

Importantly, the statement about tight correlations of peak volumes and average estimated initiation volume does not establish coincidence. Crucially, the data rely on average initiation volumes, and the estimate procedure relies on assumptions that could lead to systematic biases and uncertainties added to the population variability (in any case error bars are not provided).

The delays observed by the authors (in both directions) between the peaks of DnaA-activity conditional averages with respect to volume and the average estimated initiation volumes are not incompatible with those observed dynamically by Iuliani and coworkers. The direct experiment to prove the authors' point would be to use a direct proxy of replication initiation such as SeqA or DnaN and monitor initiations and quantify DnaA activity peaks jointly, with dynamic measurements.

While not being an expert I had the doubt that the fact that the reporters are on plasmid (despite a normalization control that seems very sensible) might affect the measurements. The approach is different from the aforementioned previous study, which used a chromosomal reporter placed symmetrically, at the same distance from the origin of replication as the original dnaA promoter.

Overall Appraisal:

In summary, this appears to me as a very interesting study providing valuable high-precision data and a novel testable hypothesis, the extrusion model, supported by relevant perturbation experiments and open to future explorations.

Comments on revisions:

I am happy with the replies and the revisions.

The main outstanding point remains that reconstructing the mathematical model details from the text (and having to rely on the code) is not optimal for a reader. However, I do understand that the authors intend to use the models as a heuristic tool only and possibly plan a theoretical study where they explore the models more systematically.

Reviewer #2 (Public review):

Summary:

The authors show that in E. coli the initiator protein DnaA oscillates post-translationally: its activity rises and peaks exactly when DNA replication begins, even if dnaA transcription is held constant. To explain this, they propose an "extrusion" mechanism in which nucleoid-associated proteins such as H-NS, whose amount grows with cell volume, dislodge DnaA from chromosomal binding sites; modelling and H-NS perturbations reproduce the observed drop in initiation mass and extra initiations seen after dnaA shut-down. Together, the data and model link biomass growth to replication timing through chromosome-driven, post-translational control of DnaA, filling gaps left by classic titration and ATP/ADP-switch models.

Strengths:

(1) Introduces an "extrusion" model that adds a new post-translational layer to replication control and explains data unexplained by classic titration or ATP/ADP-switch frameworks.

(2) A major asset of the study is that it bridges the longstanding gap between DnaA oscillations and DNA-replication initiation, providing direct single-cell evidence that pulses of DnaA activity peak exactly at the moment of initiation across multiple growth conditions and genetic perturbations.

(3) A tunable dnaA strain and targeted H-NS manipulations shift initiation mass exactly as the model predicts, giving model-driven validation across growth conditions.

(4) A purpose-built Psyn66 reporter combined with mRNA-FISH captures DnaA-activity pulses with cell-cycle resolution, providing direct, compelling data.

Weaknesses:

(1) What happens to the (C+D) period and initiation time as the dnaA mRNA level changes? This is not discussed in the text or figure and should be addressed.

(2) It is unclear what is meant by "relative dnaA mRNA level." Relative to what? Wild-type expression? Maximum expression? This should be explicitly defined.

(3) It would be helpful to provide some intuition for why an increase in dnaA mRNA level leads to a decrease in initiation mass per ori and an increase in oriC copy number.

(4) The titration and switch models do not explicitly include dnaA mRNA in the dynamics of DnaA protein. Yet, in Figure 2G, initiation mass is shown to decrease linearly with dnaA mRNA level in these models. How was dnaA mRNA level represented or approximated in these simulations?

(5) Is Schaechter's law (i.e., exponential scaling of average cell size with growth rate) still valid under the different dnaA mRNA expression conditions tested?

(6) The manuscript should explain more explicitly how the extrusion model implements post-translational control of DnaA and, in particular, how this yields the nonlinear drop in relative initiation mass versus dnaA mRNA seen in Fig. 6E. Please provide the governing equation that links total DnaA, the volume-dependent "extruder" pool, and the threshold of free DnaA at initiation, and show-briefly but quantitatively-how this equation produces the observed concave curve.

(7) Does this Extrusion model give well well-known adder per origin, i.e., initiation to initiation is an adder.

(8) DnaA protein or activity is never measured; mRNA is treated as a linear proxy. Yet the authors' own narrative stresses post-translational (not transcriptional) control of DnaA. Without parallel immunoblots or activity readouts, it is impossible to know whether a six-fold mRNA increase truly yields a proportional rise in active DnaA.

(9) Figure 2 infers both initiation mass and oriC copy number from bulk measurements (OD₆₀₀ per cell and rifampicin-cephalexin run-out) instead of measuring them directly in single cells. Any DnaA-dependent changes in cell size, shape, or antibiotic permeability could skew these bulk proxies, so the plotted relationships may not accurately reflect true initiation events.

Comments on revisions:

The authors have addressed all of my previous concerns, questions, and suggestions sufficiently.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Li and coworkers addresses the important and fundamental question of replication initiation in Escherichia coli, which remains open, despite many classic and recent works. It leverages single-cell mRNA-FISH experiments in strains with titratable DnaA and novel DnaA activity reporters to monitor DNA activity peaks versus size. The authors find oscillations in DnaA activity and show that their peaks correlate well with the estimated population-average replication initiation volume across conditions and imposed dnaA transcription levels. The study also proposes a novel extrusion model where DNA-binding proteins regulate free DnaA availability in response to biomass-DNA imbalance. Experimental perturbations of H-NS support the model validity, addressing key gaps in current replication control frameworks.

Strengths:

I find the study interesting and well conducted, and I think its main strong points are:

(1) the novel reporters obtained with systematic synthetic biology methods, and combined with a titratable dnaA strain.

(2) the interesting perturbations (titration, production arrest, and H-NS).

(3) the use of single-cell mRNA FISH to monitor transcripts directly.

The proposed extrusion model is also interesting, though not fully validated, and I think it will contribute positively to the future debate.

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

Weaknesses and Limitations:

(1) A relevant limitation in novelty is that DnaA activity and concentration oscillations have been reported by the cited Iuliani and coworkers previously by dynamic microscopy, and to a smaller extent by the other cited study by Pountain and coworkers using mRNA FISH.

(2) An important limitation is that the study is not dynamic. While monitoring mRNA is interesting and relevant, the current study is based on concentrations and not time variations (or nascent mRNA). Conversely, the study by Iuliani and coworkers, while having the drawback of monitoring proteins, can directly assess production rates. It would be interesting for future studies or revisions to monitor the strains and reporters dynamically, as well as using (as a control) the technique of this study on the chromosomal reporters used by Iuliani et al.

We acknowledge the value of dynamic measurements and clarify our methodological rationale.

While luliani et al. provided valuable temporal resolution through protein dynamics, our mRNA FISH approach achieves direct decoupling of transcriptional vs. post-translational regulation (Fig 4F-H), and condition flexibility across 7 growth rates (30-66 min doubling times). This trade-off sacrifices temporal resolution for enhanced population-scale resolution and perturbation flexibility. To directly address temporal coupling, future work will implement dual-color live imaging of DnaA activity concurrent with replication initiation events.

(3) Regarding the mathematical models, a lot of details are missing regarding the definitions and the use of such models, which are only presented briefly in the Methods section. The reader is not given any tools to understand the predictions of different models, and no analytical estimates are used. The falsification procedures are not clear. More transparency and depth in the analysis are needed, unless the models are just used as a heuristic tool for qualitative arguments (but this would weaken the claims). The Berger model, for example, has many parameters and many regimes and behaviors. When models are compared to data (e.g., in Figure 2G), it is not clear which parameters were used, how they were fixed, and whether and how the model prediction depends on parameters.

We agree that model transparency is essential for quantitative validation. To address this, all model parameters (DnaA synthesis rate, activation/deactivation rates etc.) are explicitly tabulated in Supplementary Information Table S6. For the titration (Hansen et al. 1991) and extrusion models, we derive analytical expressions for initiation mass (IM) sensitivity to DnaA expression in Supplementary Note 1. For Figure 2G/S6, we used published parameters (Berger & Wolde 2022 SI Table 2) with experiment growth conditions (μ = 1.54 h^-1).

The extrusion model's validation relies primarily on its ability to resolve paradoxical initiation events under dnaA shutdown (Fig 6C), a test where other models fail categorically. While the Berger titration-switch hybrid can fit steady-state IM trends (Fig S6A), it cannot reproduce post-shutdown dynamics without ad hoc modifications (Fig S6B). We acknowledge that comprehensive analysis of all model regimes exceeds this study's scope but provide full simulation code for independent verification: https://github.com/BaiYangBqdq/dynamics_of_biomass_DNA_coordination

(4) Importantly, the main statement about tight correlations of peak volumes and average estimated initiation volume does not establish coincidence, and some of the claims by the authors are unclear in these respects (e.g., when they say "we resolve a 1:1 coupling between DnaA activity thresholds and replication initiation", the statement could be correct but is ambiguous). Crucially, the data rely on average initiation volumes (on which there seems to be an eternally open debate, also involving the authors), and the estimate procedure relies on assumptions that could lead to biases and uncertainties added to the population variability (in any case, error bars are not provided).

We acknowledge the limitations of population-level inference and have refined our claims: "Replication initiation volume scales proportionally with peak DnaA activity volume with a slope of 1.0 (R₂=0.98, Fig 7G), indicating predictive correspondence rather than absolute coincidence. While population-level  𝑉_𝑖 estimation cannot resolve single-cell stochasticity, the consistent 𝑉*: 𝑉_𝑖 relationship across 20 conditions suggest DnaA activity thresholds predict initiation timing within physiological error margins”. Future work will implement simultaneously DnaA activity and replication forks by using microfluidic single-cell tracking.

(5) The delays observed by the authors (in both directions) between the peaks of DnaAactivity conditional averages with respect to volume and the average estimated initiation volumes are not incompatible with those observed dynamically by Iuliani and coworkers. The direct experiment to prove the authors' point would be to use a direct proxy of replication initiation, such as SeqA or DnaN, and monitor initiations and quantify DnaA activity peaks jointly, with dynamic measurements.

We acknowledge the observed temporal deviations between DnaA activity peaks (𝑉*) and population-derived volumes at initiation ( 𝑉_𝑖) in certain conditions, in line with the findings of Iuliani et al. This might be mechanistically consistent with the time required for orisome assembly or oriC sequestration. They do not contradict our core finding that initiation occurs at a defined DnaA activity threshold (slope=1.0, R₂=0.98 in 𝑉*: 𝑉_𝑖 correlation).

(6) While not being an expert, I had some doubt that the fact that the reporters are on plasmid (despite a normalization control that seems very sensible) might affect the measurements. Also, I did not understand how the authors validated the assumptions that the reporters are sensitive to DnaA-ATP specifically. It seems this assumption is validated by previous studies only.

We employed a plasmid-based reporter system to circumvent the significant confounding effects of chromosomal position on promoter activity, as extensively documented by Pountain et al., where local genomic context (e.g., nucleoid occlusion, supercoiling gradients, and neighboring operons) introduces uncontrolled variability. By housing the P_syn66 test promoter and P_con normalization control in identical low-copy pSC101 vectors (<8 copies/ cell, Peterson & Phillips, Plasmid 2008), we ensured they experience equivalent physical and biochemical environments. This ratiometric design, where DnaA activity is calculated, actively corrects for global fluctuations in RNA polymerase availability, nucleotide pools, and plasmid copy number. Critically, P_syn66’s architecture emulates natural DnaA-responsive elements: its strong DnaAboxes report free DnaA concentration, while its weak box is preferentially bound by DnaA-ATP (Speck et al., EMBO journal 1999), mirroring the nucleotide-state sensitivity of oriC and the native dnaA promoter. This system was indispensable for our central finding, as it uniquely enabled the decoupling of DnaA activity oscillations from transcriptional feedback (Fig. 4F-H), an experiment fundamentally impossible with chromosomally integrated reporters due to autoregulatory interference.

Overall Appraisal:

In summary, this appears as a very interesting study, providing valuable data and a novel hypothesis, the extrusion model, open to future explorations. However, given several limitations, some of the claims appear overstated. Finally, the text contains some selfevaluations, such as "our findings redefine the paradigm for replication control", etc., that appear exaggerated.

We thank the reviewer for highlighting the need for precise language in framing our conclusions. We have implemented the following substantive revisions throughout the manuscript to ensure claims align strictly with empirical evidence:

(1) Changed "redefine the paradigm for replication control" into "advance the paradigm for replication control" (Introduction)

(2) Changed "redefine bacterial cell cycle control" into "refine bacterial cell cycle control as a dynamic interplay..." (Discussion)

(3) Removed the term "spatial" from the Discussion's description of DnaA-chromosome interactions (Discussion, first paragraph).

(4) Changed "provides a blueprint" into "provides a valuable tool for dissecting spatial regulation..." (Discussion, final paragraph)

(5) Scrutinized all superlatives (e.g., "critical feat" into "important capability"; "fundamental principle of cellular organization" into "potential organizational strategy")

(6) Replaced the instances of "robust" with evidence-backed descriptors (e.g., "sensitive," "consistent")

(7) We agree that the extrusion model requires further validation and have emphasized this in Discussion: "While H-NS perturbation supports extrusion mechanism, future work should identify the full extruder interactome and elucidate how metabolic signals modulate their activity" (final paragraph)

This calibrated language more accurately represents our study as a conceptual advance with testable mechanisms, not a complete paradigm shift.

Reviewer #2 (Public review):

Summary:

The authors show that in E. coli, the initiator protein DnaA oscillates post-translationally: its activity rises and peaks exactly when DNA replication begins, even if dnaA transcription is held constant. To explain this, they propose an "extrusion" mechanism in which nucleoidassociated proteins such as H-NS, whose amount grows with cell volume, dislodge DnaA from chromosomal binding sites; modelling and H-NS perturbations reproduce the observed drop in initiation mass and extra initiations seen after dnaA shut-down. Together, the data and model link biomass growth to replication timing through chromosome-driven, posttranslational control of DnaA, filling gaps left by classic titration and ATP/ADP-switch models.

Strengths:

(1) Introduces an "extrusion" model that adds a new post-translational layer to replication control and explains data unexplained by classic titration or ATP/ADP-switch frameworks.

(2) A major asset of the study is that it bridges the longstanding gap between DnaA oscillations and DNA-replication initiation, providing direct single-cell evidence that pulses of DnaA activity peak exactly at the moment of initiation across multiple growth conditions and genetic perturbations.

(3) A tunable dnaA strain and targeted H-NS manipulations shift initiation mass exactly as the model predicts, giving model-driven validation across growth conditions.

(4) A purpose-built Psyn66 reporter combined with mRNA-FISH captures DnaA-activity pulses with cell-cycle resolution, providing direct, compelling data.

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

Weaknesses:

(1) What happens to the (C+D) period and initiation time as the dnaA mRNA level changes? This is not discussed in the text or figure and should be addressed.

We thank the reviewer for this important observation. Our data demonstrate that increased dnaA mRNA levels induce two compensatory changes in cell cycle progression:

(1) Earlier replication initiation, manifested as a reduced initiation mass: the initiation mass decreased from 5.6 to 2.6 (OD₆₀₀·ml per 10¹⁰ cells) as the relative dnaA mRNA level increased from 0.2 to 7.2 (normalized to the wild-type level) (Fig. 2F, red).

(2) Prolonged C+D period: Increased by approximately 60% (from 1.05 to 1.66 hours, Fig. 2F blue).

The complete quantitative relationship is now explicitly described in the Results section: “Concurrently, the initiation mass was reduced by 50%, and the period from initiation to division (C+D) was increased by ~60% (Fig. 2F)”

(2) It is unclear what is meant by "relative dnaA mRNA level." Relative to what? Wild-type expression? Maximum expression? This should be explicitly defined.

The relative dnaA mRNA level was obtained by normalizing to that in wild-type MG1655 cells grown in the same medium. To clarify this point, we have now marked the wild-type level in Fig. 1B, and a clear description of this has also been included in the figure caption.

(3) It would be helpful to provide some intuition for why an increase in dnaA mRNA level leads to a decrease in initiation mass per ori and an increase in oriC copy number.

Thank you for your valuable suggestion. Increased dnaA mRNA accelerates DnaA accumulation, causing cells to reach the initiation threshold at a smaller cell size (reducing initiation mass, Fig. 2F red). This earlier initiation increases oriC copies per cell at populational level (Fig. 2E). This mechanistic interpretation now appears in the Results: “As the DnaA expression level increases, DnaA activity reaches the initiation threshold earlier. Given that cell mass remained nearly unchanged, this earlier initiation led to an increase in population-averaged cellular oriC numbers (Fig. 2E).”

(4) The titration and switch models do not explicitly include dnaA mRNA in the dynamics of DnaA protein. Yet, in Figure 2G, initiation mass is shown to decrease linearly with dnaA mRNA level in these models. How was dnaA mRNA level represented or approximated in these simulations?

All models presented in this article omit explicit modeling of dnaA mRNA dynamics for simplicity. However, at steady state, the relative level of dnaA mRNA can be approximated by the relative expression rate of DnaA protein, as both reflect the expression level of DnaA. This detail is now clarified in the caption of Figure 2G.

(5) Is Schaechter's law (i.e., exponential scaling of average cell size with growth rate) still valid under the different dnaA mRNA expression conditions tested?

Schaechter's law describes the exponential scaling of average cell size with growth rate in bacteria. In our prior work (Zheng et al., Nature Microbiology 2020), where we demonstrated that Schaechter's law fails in slow-growth regimes. However, in current study, growth rate remained constant across different dnaA expression levels (Fig. 2C), and cell mass showed no significant change (Fig. 2D). Since Schaechter's law specifically addresses how cell size scales with growth rate, it does not apply here, as growth rate was invariant in our perturbations, which selectively alter replication initiation dynamics, not growth rate or size scaling.

(6) The manuscript should explain more explicitly how the extrusion model implements posttranslational control of DnaA and, in particular, how this yields the nonlinear drop in relative initiation mass versus dnaA mRNA seen in Figure 6E. Please provide the governing equation that links total DnaA, the volume-dependent "extruder" pool, and the threshold of free DnaA at initiation, and show - briefly but quantitatively - how this equation produces the observed concave curve.

The governing equations linking initiation mass and DnaA expression level is now provided in Supplementary Note S1 for both the titration and the extrusion model. In general, the dependence of initiation mass (𝑉_𝐼) on dnaA expression level (𝛼_𝐴) dependency takes an inverse 1 proportionality form: . In the extrusion model, the incorporated extruder protein is assumed to have similar synthesis dynamics as DnaA and can release DnaA from DnaA-box. After denoting the synthesis rate of the extruder as 𝛼_𝐻, the combined effect of DnaA and the extruder on replication initiation can be briefly described as: . Then the additive contribution of 𝛼_𝐻 dampens the sensitivity of initiation mass to changes in 𝛼_𝐴, resulting in a significantly flattened curve. As a result, the predicted 𝑉_𝐼 − 𝛼_𝐴 relationship has a concave shape in the semi-log plots.

(7) Does this Extrusion model give well well-known adder per origin, i.e., initiation to initiation is an adder.

Yes, the extrusion model can provide the initiation-to-initiation adder phenomenon, this information was provided in fig. S3C.

(8) DnaA protein or activity is never measured; mRNA is treated as a linear proxy. Yet the authors' own narrative stresses post-translational (not transcriptional) control of DnaA. Without parallel immunoblots or activity readouts, it is impossible to know whether a sixfold mRNA increase truly yields a proportional rise in active DnaA.

We acknowledge the reviewer's valid concern regarding the indirect nature of our DnaA activity measurements. While mRNA levels alone cannot resolve active DnaA dynamics, our approach integrates functional replication outcomes with a validated synthetic reporter to infer activity. Crucially, elevated dnaA mRNA causes demonstrable biological effects: earlier replication initiation (Fig. 2F) and increased oriC copies (Fig. 2E), directly confirming enhanced functional DnaA activity at the oriC locus. The P_syn66 reporter, engineered with DnaA-boxes mirroring oriC's architecture, provides orthogonal validation, showing progressive repression to dnaA induction (Fig. 3C). Our operational metric , bases on P_syn66 responds sensitively to DnaA-chromosome interactions within its characterized 8-fold dynamic range (Fig. 3C). Immunoblots would be inadequate here, as they cannot distinguish functionally critical pools: free versus chromosome-bound DnaA, or DnaA-ATP versus DnaAADP, precisely the post-translational states our study implicates in regulation. We therefore prioritize functional readouts (initiation timing) and the P_syn66 reporter, which probes the biologically active fraction relevant to replication control.

(9) Figure 2 infers both initiation mass and oriC copy number from bulk measurements (OD₆₀₀ per cell and rifampicin-cephalexin run-out) instead of measuring them directly in single cells. Any DnaA-dependent changes in cell size, shape, or antibiotic permeability could skew these bulk proxies, so the plotted relationships may not accurately reflect true initiation events.

We acknowledge the reviewer's valid methodological concern and clarify that while bulk measurements carry inherent limitations, our approach is grounded in established techniques with demonstrated reliability. Cell mass was inferred from OD600/cell, which correlates strongly with direct dry weight measurements and microscopic cell volumes across diverse growth conditions, as validated in our prior work (Zheng et al., Nature Microbiology 2020). Crucially, cell mass remained invariant across dnaA expression levels (Fig. 2D).

Regarding oriC quantification, the rifampicin-cephalexin run-out assay is a wildly applied for replication initiation studies. Our data shows expected 2ⁿ oriC distributions without abnormal ploidy (as shown below). While single-cell methods offer superior resolution, our bulk approach provides accurate population-level trends.

Author response image 1.

Recommendations for the authors:

Reviewing Editor Comments:

The reviewers felt that the mathematical modeling was not adequately explained in the paper, and that this affected the readability of the manuscript. The authors are encouraged to elaborate on this aspect of the paper (in addition to strengthening other claims, if possible, per the reviewers' comments).

We thank the editor and reviewers for their constructive feedback. We have comprehensively strengthened the mathematical modeling framework to enhance clarity and rigor.

Reviewer #1 (Recommendations for the authors):

The only revision I would do is a recalibration of the claims and a major effort to clarify the modeling part (including a detailed SI appendix), without necessarily performing additional work.

To enhance mathematical modeling transparency, we have completed model description in the method section and a parameter table with literature-sourced values in Supplementary Information Table S6. Moreover, analytical derivations of initiation mass dependencies are performed and presented in the Supplementary Information Note S1.

Of course, there are extra experiments (mentioned in the public review) that would help support some of the big claims, but that can be considered a different project.

Thank you for your suggestion. This will be addressed in our future work.

Minor suggestion: please put signposts or plot jointly to compare the maxima/minima in Figures 4D, E, G, and H.

We added dashed lines in Figures 4D, and E, to synchronize visualization of DnaA activity peaks and transcriptional minima across panels, facilitating direct biological comparisons.

Reviewer #2 (Recommendations for the authors):

(1) Should define what DNA activity is.

We have explicitly defined DnaA activity in the Introduction as “the capacity to initiate replication…” and noted that it is “governed by free DnaA concentration, DnaA-ATP/-ADP ratio, and orisome assembly competence”.

(2) Word repetition - “...grown in in Luria-Bertani (LB) medium...”.

Corrected.

(3) Typographical error - “FISH ... was preformed" should be "performed”.

Corrected.

(4) The manuscript alternates between “ng ml^-1” and “ng·ml^-1”; choose one style and apply it uniformly.

Standardized the units to ng·ml^-1 throughout.

(5) Reference duplicates - Some citations appear twice in the bibliography (e.g., "Bintu et al., 2005a/b" and "Bintu et al., 2005b" listed again later).

The studies by Bintu et al. (2005a, 2005b) represent separate works: 2005a details applications, and 2005b develops models.

eLife Assessment

This manuscript provides an improved version of an important cancer risk estimation tool and refines and expands upon resources that are currently available to the cancer genetics community. The new program is validated in a set of clinical pedigrees demonstrating its practical accuracy and relevance to the field. Collectively, the data are compelling and support the major conclusions of this manuscript.

Reviewer #1 (Public review):

Summary:

Although consanguinity is a rare clinical occurrence, it results in essentially a failure state for pedigree analysis algorithms by introducing loops that prevent accurate risk estimation. Therefore, Kubista et al. developed the graph-based "breakloops" function to allow their PanelPRO risk estimator (PMID 34406119) to successfully process consanguineous pedigrees.

Strengths:

This function allows them to first identify a loop in a pedigree, then decide which of two separate algorithms to best apply, Prim's or greedy, to optimize the introduction of clones to break these loops. As this function is automatic, it represents an improvement over previous similar algorithms, and also allows for the optimal algorithm to be chosen. The inclusion of pseudocode in the manuscripts provides a succinct summary of the logic behind the above: it greatly enhances the understanding of the function for those not necessarily computationally inclined.

After simulating a variety of consanguineous possibilities, the authors leveraged clinical pedigree data to validate their function. Integration of clinical pedigrees was extremely helpful in demonstrating the real-life applicability of this update. The successful inclusion of these clinical data justifies the claims they make regarding the ability to assess cancer risk in a wider range of family structures.

Weaknesses:

As consanguinity is inextricably linked with autosomal recessive disease, the discussion on the clinical implications of this new function is lacking.

Reviewer #2 (Public review):

Summary:

This paper introduces a new function within the Fam3Pro package that addresses the problem of breaking loops in family structures. When a loop is present, standard genotype peeling algorithms fail, as they cannot update genotypes correctly. The solution is to break these loops, but until now, this could not be done automatically and optimally.

The manuscript provides useful background on constructing graphs and trees from family data, detecting loops, and determining how to break them optimally for the case of no loops with multiple matings. For this situation, the algorithm switches between Prim's algorithm and a simple greedy approach and provides a solution. However, here, an optimal solution is not guaranteed.

The theoretical foundations-such as the representation of families as graphs or trees and the identification of loops-are clearly explained and well-illustrated with example pedigrees. The practical utility of the new function is demonstrated by applying it to a dataset containing families with loops.

This work has the potential for considerable impact, especially for medical researchers and individuals from families with loops. These families could previously not be analysed automatically and optimally. The new function changes that, enabling risk assessments and genetic calculations that were previously infeasible.

Strengths:

(1) The theoretical explanation of graphs, trees, and loop detection is clear and well-structured.

(2) The idea of switching between algorithms is original and appears effective.

(3) The function is well implemented, with minimal additional computational cost.

Weaknesses:

(1) In cases with multiple matings, the notion of a "close-to-optimal" solution is not clearly defined. It would be helpful to explain what this means-whether it refers to empirical performance, theoretical bounds, or something else.

(2) In the example pedigree discussed, multiple options exist for breaking loops, but it is unclear which is optimal.

(3) No example is provided where the optimal solution is demonstrably not reached.

(4) It is also unclear whether the software provides a warning when the solution might not be optimal.

Author response:

Response to Reviewer #1:

We plan to extend the discussion section to discuss the clinical implications of this new function. We will note the algorithm's applicability to broader genetic counseling contexts beyond cancer risk assessment.

Response to Reviewer #2:

We will clarify the four points raised:

(1) "Close-to-optimal" definition: We will explain that in multiple-mating cases, finding the global optimum is NP-hard (equivalent to the Weighted Feedback Vertex Set problem). We will clarify that our greedy algorithm provides practically efficient solutions suitable for clinical use, though without theoretical optimality guarantees.

(2) Example clarity: We will improve Figure 1's caption to explain the cost calculations and note that with equal weights, both shown solutions are equivalent.

(3) Non-optimal examples: We will describe scenarios where the greedy algorithm may not achieve the global optimum, particularly in multiple-mating cases with heterogeneous weights.

(4) Warning message: The current version not provide a warning when the solution might be non-optimal. This may be added in the future to the function.

We appreciate your feedback and suggestions to help improve the manuscript.

eLife Assessment

This study developed a novel continuous dot-motion decision-making task, in which participants can see another player's responses as well as their own, to measure perceptual performance and confidence judgments in a social context. The study is a useful contribution to social decision-making primarily by introducing a new task and offering convincing evidence on how participants are impacted by others' decisions during continuous perceptual choices. The manuscript delivers clear evidence that participants judgements are driven by metacognitive confidence over simpler primary uncertainty.

Reviewer #1 (Public review):

Summary:

This paper reports an interesting and clever task which allows the joint measurement of both perceptual judgments and confidence (or subjective motion strength) in real / continuous time. The task is used together with a social condition to identify the (incidental, task-irrelevant) impact of another player on decision-making and confidence. The paper is well-written and clear.

Strengths:

The innovation on the task alone is likely to be impactful for the field, extending recent continuous report (CPR) tasks to examine other aspects of perceptual decision-making and allowing more naturalistic readouts. One interesting and novel finding is the observation of dyadic convergence of confidence estimates even when the partner is incidental to the task performance, and that dyads tend to be more risk-seeking (indicating greater confidence) than when playing solo.

One concern with the novel task is whether confidence is disambiguated from a tracking of stimulus strength or coherence. The subjects' task is to track motion direction and use the eccentricity of the joystick to control the arc of a catcher - thus implementing a real-time sensitivity to risk (peri-decision wagering). The variable-width catcher has been used to good effect in other confidence/uncertainty tasks involving learning of the spread of targets (the Nassar papers). But in the context of an RDK task, one simple strategy here is to map eccentricity directly to (subjective) motion coherence - such that the joystick position at any moment in time is a vector with motion direction and strength. The revised version of the paper now includes a comprehensive analysis of the extent to which the metacognitive aspect of the task (the joystick eccentricity) tracks stimulus features such as motion coherence. The finding of a lagged relationship between task accuracy and eccentricity in conjunction with a relative lack of instantaneous relationships with coherence fluctuations, convincingly strengthens the inference that this component of the joystick response is metacognitive in nature, and dynamically tracking changes in performance. This importantly rebuts a more deflationary framing of the metacognitive judgment, in which what the subjects might be doing is tracking two features of the world - instantaneous motion strength and direction.

The claim that the novel task is tracking confidence is also supported by new analyses showing classic statistical features of explicit confidence judgments (scaling with aggregate accuracy, and tracking psychometric function slope) are obtained with the joystick eccentricity measure.

Reviewer #2 (Public review):

Summary:

Schneider et al examine perceptual decision-making in a continuous task setup when social information is also provided to another human (or algorithmic) partner. The authors track behaviour in a visual motion discrimination task and report accuracy, hit rate, wager, and reaction times, demonstrating that choice wager is affected by social information from the partner.

Strengths:

There are many things to like about this paper. The visual psychophysics has been undertaken with much expertise and care to detail. The reporting is meticulous and the coverage of the recent previous literature is reasonable. The research question is novel.

Comments on revisions:

The authors have addressed my suggestions adequately

Author response:

The following is the authors’ response to the original reviews

Reviewer 1:

Strengths:

The innovation on the task alone is likely to be impactful for the field, extending recent continuous report (CPR) tasks to examine other aspects of perceptual decision-making and allowing more naturalistic readouts. One interesting and novel finding is the observation of dyadic convergence of confidence estimates even when the partner is incidental to the task performance, and that dyads tend to be more risk-seeking (indicating greater confidence) than when playing solo. The paper is well-written and clear.”

We thank reviewer 1 for this encouraging evaluation. Below we address the identified weaknesses and recommendations.

(1) Do we measure metacognitive confidence?

One concern with the novel task is whether confidence is disambiguated from a tracking of stimulus strength or coherence. […] But in the context of an RDK task, one simple strategy here is to map eccentricity directly to (subjective) motion coherence - such that the joystick position at any moment in time is a vector with motion direction and strength. This would still be an interesting task - but could be solved without invoking metacognition or the need to estimate confidence in one's motion direction decision. […] what the subjects might be doing is tracking two features of the world - motion strength and direction. This possibility needs to be ruled out if the authors want to claim a mapping between eccentricity and decision confidence […].”

We thank reviewer 1 for pointing out that the joystick tilt responses of our subjects could potentially be driven by stimulus coherence instead of metacognitive decision confidence. Below, we present four arguments to address this point of concern:

(1.1) Similar physical coherence between high and low confidence states

Nominal motion coherence is a discrete value, but the random noisiness in the stimulus causes the actual frame-by-frame coherence to be distributed around this nominal value. Because of this, subjects might scale their joystick tilt report according to the coherence fluctuations around the nominal value. To check if this was the case, we use a median split to separate stimulus states into states with large versus small joystick tilt, individually for each nominal coherence. For each stimulus state, we extracted the actual instantaneous (frame-to-frame) motion coherence, which is based on the individual movements of dots in the stimulus patch between two frames, recorded in our data files.

First, we compared the motion coherence between stimulus states with large versus small joystick tilt. For each stimulus state, we calculated average instantaneous motion coherence, and analyzed the difference of the medians for the large versus small tilt distributions for each subject and each coherence level. The resulting histograms show the distribution of differences across all 38 subjects for each nominal coherence, and are, except for the coherence of 22%, not significantly different from zero across subjects (Author response image 1). For the 22% coherence condition, the difference amounts to 0.19% – a very small, non-perceptible difference. Thus, we do no find systematic differences between the average motion coherence in states with high versus low joystick tilt.

Author response image 1.

Histograms of within-subject difference between medians of average coherence distributions with large and small joystick tilt for all subjects. Coherence is color-coded (cyan – 0%, magenta – 98%). On top, the title of each panel illustrates the number of significant differences (Ranksum test in each subject) without correction for multiple comparisons (see Author response table 1 below). In the second row of the title, we show the result of the population t-test against zero. Only 22% coherence shows a significant bias. Positive values indicate higher average coherence for large joystick tilt.  

Author response table 1.

List of all individual significantly different coherence distributions between high and low tilt states, without correction for multiple comparisons. Median differences do not show a consistent bias (i.e. positive values) that would indicate higher average coherence for the large tilts.

(1.2) Short-term stimulus fluctuations have no effect

[…] But to fully characterise the task behaviour it also seems important to ask how and whether fluctuations in motion energy (assuming that the RDK frames were recorded) during a steady state phase are affecting continuous reporting of direction and eccentricity, prior to asking how social information is incorporated into subjects' behaviour.

In addition to the analysis of stimulus coherence and tilt averaged across each stimulus state (1.1), we analyzed moment-to-moment relationship between instantaneous coherence and ongoing reports of accuracy and tilt. Below, we provide evidence that short-term fluctuations in the instantaneous coherence (i.e. the motion energy of the stimulus) do not result in correlated changes in joystick responses, neither for tilt nor accuracy. For each continuous stimulus state, we calculated cross-correlation functions between the instantaneous coherence, tilt and accuracy, and then averaged the cross-correlation across all states of the same nominal coherence, and then across subjects. The resulting average cross-correlation functions are essentially flat. This further supports our interpretation that the joystick reports do not reflect short-term fluctuations of motion energy.

Author response image 2.

Cross-correlation between the length of the resultant vector with joystick accuracy (left) and tilt (right). Coherence is color-coded. Shaded background illustrates 95% confidence intervals.

(1.3) Joystick tilt changes over time despite stable average stimulus coherence

If perceptual confidence is derived from evidence integration, we should see changes over time even when the stimulus is stable. Here, we have analyzed the average slope of the joystick tilt as a function of time within each stimulus state for each subject and each coherence, to verify if our participants tilted their joystick more with additional evidence. This is illustrated with a violin plot below (Author response image 3). The linear slopes of the joystick tilt progression over the course of stimulus states are different between coherence levels. High coherence causes more tilt over time, resulting in positive slopes for most subjects. In contrast, low/no coherence results mostly in flat or negative slopes. This tilt progression over time indicates that low coherence results in lower confidence, as subjects do not wager more with weak evidence. In contrast, high coherence causes subjects to exhibit more confidence, indicated by positive slope of the joystick tilt.

Author response image 3.

Violin plots showing the fitted slopes of the joystick tilt time course in the last 200 samples (1667 ms) leading up to a next stimulus direction (cf. Figure 2D). Positive values signify an increase in joystick tilt over time. Each dot shows the average slope for one subject. Coherence is color-coded. The dashed line at zero indicates unchanged joystick tilt over the analyzed time window.

(1.4) Cross-correlation between response accuracy and joystick tilt

Similar to 1.2 above, we have cross-correlated the frame-by-frame changes of joystick accuracy and tilt for each individual stimulus state and each subject. Across subjects, changes in tilt occur later than changes in accuracy, indicating that changes in the quality of the report are followed by changes in the size of the wager. Given that this process is not driven by short-term changes in the motion energy of the stimulus (see 1.2 above), we interpret this as additional evidence for a metacognitive assessment of the quality of the behavioral report (i.e. accuracy) reflected in the size of the wager (our measure for confidence). (See Figure 2E).

(2) Peri-decision wagering is different to post-decision wagering

[…] One route to doing this would be to ask whether the eccentricity reports show statistical signatures of confidence that have been established for more classical punctate tasks. Here a key move has been to identify qualitative patterns in the frame of reference of choice accuracy - with confidence scaling positively with stimulus strength for correct decisions, and negatively with stimulus strength for incorrect decisions (the so-called X-pattern, for instance Sanders et al. 2016 Neuron […].

We thank reviewer 1 for the constructive feedback. Our behavioral data do not show similar signatures to the previously reported post-decision confidence expression (Desender et al., 2021; Sanders et al., 2016). The previously described patterns show, first of all, that confidence for the incorrect type1 decisions diverges from the correct type1 decisions, declining with stimulus strength (e.g. coherence), as compared to increase for correct decisions. In our task, there is a graded accuracy and (putative) confidence expression, but there are no correct or incorrect decisions – instead, there are hits and misses of the reward targets presented at nominal directions. Instead of a decline for misses, we observe an equally positive scaling with coherence for the confidence, both for hits and misses (Author response image 4A). This is because in our peri-decision wagering task, the expression of confidence causally determines the binary hit or miss outcome. The outcome in our task is a function of the two-dimensional joystick response: higher tilt (confidence) requires a more accurate response to successfully hit a target. Thus, a subject can display a high (but not high enough) level of accuracy and confidence but still remain unsuccessful. If we instead median-split the confidence reports by high and low accuracy (Author response image 4C), we observe a slight separation, especially for higher coherences, but still no clear different in slopes.

We do observe the other two dynamic signatures of confidence (Desender et al., 2021): signature 2 – monotonically increasing accuracy as a function of confidence (Author response image 4), and signature 3 – steeper type 1 psychometric performance (accuracy) for high versus low confidence (Author response image 4D).

Author response image 4.

Confidence (i.e., joystick tilt, left column) and accuracy reports (right column) for different stimulus coherence, sorted by discrete outcome (hit versus miss, upper row) and the complementary joystick dimension (lower row, based on median split).

Author response image 5.

Accuracy reports correlate positively with confidence reports. For each stimulus state, we averaged the joystick response in the time window between 500 ms (60 samples) after a direction change until the first reward target appearance. If there was no target, we took all samples until the next RDP direction change into account. This corresponds to data snippets averaged in Figure 2D. Thus, for each stimulus state, we extracted a single value for joystick accuracy and for tilt (confidence). Subsequently, we fitted a linear regression to the accuracy-confidence scatter within each subject and within each coherence level. The plot above shows the average linear regression between accuracy and confidence across all subjects (i.e., the slopes and intercepts were averaged across n=38 subjects). Coherence is color-coded.

(3)  Additional analyses regarding the continuous nature of our data

I was surprised not to see more analysis of the continuous report data as a function of (lagged) task variables. […]

Reviewer 1 requested more analyses regarding the continuous nature of our data. We agree that this is a useful addition to our paper, and thank reviewer 1 for this suggestion. To address this point, we revised main Figure 2 and provided additional panels. Panel D illustrates the continuous ramp-up of both accuracy and tilt (confidence) for high coherence levels, suggesting ongoing evidence integration and meta-cognitive assessment. Panel E shows the cross-correlation between frame-by-frame changes in accuracy and tilt (see 1.4 above). Here, we demonstrate that changes in the accuracy precede changes in joystick tilt, characterizing the continuous nature of the perceptual decision-making process.

(4) Explicit motivation regarding continuous social experiments

This paper is innovating on a lot of fronts at once - developing a new CPR task for metacognition, and asking exploratory questions about how a social setting influences performance on this novel task. However, the rationale for this combination was not made explicit. Is the social manipulation there to help validate the new task as a measure of confidence as dissociated from other perceptual variables? (see query 1 below). Or is the claim that the social influence can only be properly measured in the naturalistic CPR task, and not in a more established metacognition task?

Our rationale for the combination of real-time decision making and social settings was twofold:

i. Primates, including humans, are social species. Naturally, most behavior is centered around a social context and continuously unfolds in real-time. We wanted to showcase a paradigm in which distinct aspects of continuous perceptual decision-making could be assessed over time in individual and social environments.

ii. Human behavior is susceptible to what others think and do. We wanted to demonstrate that the sheer presence of a co-acting social partner affects continuous decision-making, and quantify the extent and direction of social modulation.

We agree that the motivation for combining the new task and this specific type of social co-action should be more clear. We have clarified this aspect in the Introduction, line 92-109. In brief, the continuous, free-flowing nature of the CPR task and real-time availability of social information made this design a very suitable paradigm for assessing unconstrained social influences. We see this study as the first step into disentangling the neural basis of social modulation in primates. See also the response to reviewer 2, point 2, below.

(5) Response to minor points

(5.1)  Clarification on behavioral modulation patterns

Lines 295-298, isn't it guaranteed to observe these three behavioral patterns (both participants improving, both getting worse, only one improving while the other gets worse) even in random data?

The reviewer is correct. We now simply illustrate these possibilities in Figure 4B and how these patterns could lead to divergence or convergence between the participants (see also line 282). Unlike random data, our results predominantly demonstrate convergence.

(5.2) Clarification on AUC distributions

Lines 703-707, it wasn't clear what the AUC values referred to here (also in Figure 3) - what are the distributions that are being compared? I think part of the confusion here comes from AUC being mentioned earlier in the paper as a measure of metacognitive sensitivity (correct vs. incorrect trial distributions), whereas my impression here is that here AUC is being used to investigate differences in variables (e.g., confidence) between experimental conditions.

We apologize for the confusion. Indeed, the AUC analysis was used for the two purposes:

(i) To assess the metacognitive sensitivity (line 175, Supplementary Figure 2).

(ii) To assess the social modulation of accuracy and confidence (starting at line 232, Figures 3-6). 

We now introduce the second AUC approach for assessing social modulation, and the underlying distributions of accuracy and confidence derived from each stimulus state, separately in each subject, in line 232.

(5.3) Clarification of potential ceiling effects

Could the findings of the worse solo player benefitting more than the better solo player (Figure 4c) be partly due to a compressive ceiling effect - e.g., there is less room to move up the psychometric function for the higher-scoring player?