Reviewer #3 (Public Review):

Summary:

It has been demonstrated that cardiac lymphatics are essential for cardiac health and function. Moreover, post-myocardial infarction, targeting lymphatics by stimulating lymphangiogenesis has been shown to improve cardiac inflammation, fibrosis, and function. Then, the aim of this study was to evaluate the transcriptomic changes of cardiac lymphatic endothelial cells (LECs) after a myocardial infarction, which could reveal new therapeutic targets targeting lymphatic function. Moreover, investigating the cell-cell communication between lymphatic and immune cells would give critical information for a better understanding of the disease.

Strengths:

The use of scRNAseq data to evaluate LECs is an effective strategy considering the small proportion of LECs compared to blood endothelial cells. The extensive bioinformatic analysis used by the authors for three different data sets.

Weaknesses:

Among a total of 44,860 cells, only 242 LECs and 5,688 endothelial cells were identified. This small number of LECs is not representative and is insufficient to reliably distinguish four different clusters. The bioinformatic analysis is not supported by significant results in their in vivo and in vitro experiments.

eLife assessment

This useful study presents a real-time transcriptomics analysis, with the aim of providing rapid access to sequenced data to reduce the costs associated with Oxford Nanopore long-read technology. Although the authors illustrate the compelling utility of this approach with three diverse experimental setups, issues with study design and analysis result in incomplete supporting evidence.

Reviewer #1 (Public Review):

Summary:

In this study, the authors developed three case studies: (1) transcriptome profiling of two human cell cultures (HEK293 and HeLa), (2) identification of experimentally enriched transcripts in cell culture (RiboMinus and RiboPlus treatments), and (3) identification of experimentally manipulated genes in yeast strains (gene knockouts or strains transformed with plasmids containing the deleted gene for overexpression). Sequencing was performed using the Oxford Nanopore Technologies (ONT), the only technology that allows for real-time analysis. The real-time transcriptomic analysis was performed using NanopoReaTA, a recent toolbox for comparative transcriptional analyses of Nanopore-seq data, developed by the group (Wierczeiko and Pastore et al. 2023). The authors aimed to show the use of the tool developed by them in data generated by ONT, evidencing the versatility of the tool and the possibility of cost reduction since the sequencing by ONT can be stopped at any time since enough data were collected.

Strengths:

Given that Oxford Nanopore Technologies offers real-time sequencing, it is extremely useful to develop tools that allow real-time data analysis in parallel with data generation. The authors demonstrated that this strategy is possible for both human cell lines and yeasts in the case studies presented. It is a useful strategy for the scientific community and it has the potential to be integrated into clinical applications for rapid and cost-effective quality checks in specific experiments such as overexpression of genes.

Weaknesses:

In relation to the RNA-Seq analyses, for a proper statistical analysis, a greater number of replicates should have been performed. The experiments were conducted with a minimal number of replicates (2 replicates for case study 1 and 2 and 3 replicates for case study 3).

Regarding the experimental part, some problems were observed in the conversion to double-stranded and loading for Nanopore-Seq, which were detailed in Supplementary Material 2. This fact is probably reflected in the results where a reduction in the overall sequencing throughput and detected gene number for HEK293 compared to HeLa were observed (data presented in Supplementary Figure 2). It is necessary to use similar quantities of RNA/cDNA since the sequencing occurs in real-time. The authors should have standardized the experimental conditions to proceed with the sequencing and perform the analyses.

Reviewer #2 (Public Review):

Summary:

Transcriptomics technologies play important roles in biological studies. Technologies based on second-generation sequencing, such as mRNA-seq, face some serious obstacles, including isoform analysis, due to short read length. Third-generation sequencing technologies perfectly solve these problems by having long reads, but they are much more expensive. The authors presented a useful real-time strategy to minimize the cost of sequencing with Oxford Nanopore Technologies (ONT). The authors performed three sets of experiments to illustrate the utility of the real-time strategy. However, due to the problems in experimental design and analysis, their aims are not completely achieved. If the authors can significantly improve the experiments and analysis, the strategy they proposed will guide biologists to conduct transcriptomics studies with ONT in a fast and cost-effective way and help studies in both basic research and clinical applications.

Strengths:

The authors have recently developed a computational tool called NanopoReaTA to perform real-time analysis when cDNA/RNA samples are sequenced with ONT (Wierczeiko et al., 2023). The advantage of real-time analysis is that the sequencing can be stopped once enough data is collected to save cost. Here, they described three sets of experiments: a comparison between two human cell lines, a comparison among RNA preparation procedures, and a comparison between genetically modified yeasts. Their results show that the real-time strategy works for different species and different RNA preparation methods.

Weaknesses:

However, especially considering that the computational tool NanopoReaTA is their previous work, the authors should present more helpful guidelines to perform real-time ONT analysis and more advanced analysis methods. There are four major weaknesses:

(1) For all three sets of experiments, the authors focused on sample clustering and gene-level differential expression analysis (DEA), and only did little analysis on isoform level and even nothing in any figures in the main text. Sample clustering and gene-level DEA can be easily and well done using mRNA-seq at a much cheaper cost. Even for initial data quality checking, mRNA-seq can be first done in Illumina MiSeq/NextSeq which is quick, before deep sequencing in HiSeq/NovaSeq. The real power of third-generation RNA sequencing is the isoform analysis due to the long read length. At least for now, PacBio Iso-seq is very expensive and one cannot analyze the data in real-time. Thus, the authors should focus on the real-time isoform analysis of ONT to show the advantages.

(2) The sample sizes are too small in all three sets of experiments: only two for sets 1 and 2, and three for set 3. For DEA, three is the minimal number for proper statistics. But a sample size of three always leads to very poor power. Nowadays, a proper transcriptomics study usually has a larger sample size. Besides the power issue, biological samples always contain many outliers due to many reasons. It is crucial to show whether the real-time analysis also works for larger sample sizes, such as 10, i.e., 20 samples in total. Will the performance still hold when the sample number is increasing? What is the maximum sample number for an ONT run? If the samples need to be split into multiple runs, how the real-time analysis will be adjusted? These questions are quite useful for researchers who plan to use ONT.

(3) According to the manuscript, real-time analysis checks the sequencing data in a few time points, this is usually called sequential analysis or interim analysis in statistics which is usually performed in clinical trials to save cost. Care must be taken while performing these analyses, as repeated checks on the data can inflate the type I error rate. Thus, the authors should develop a sequential analysis procedure for real-time RNA sequencing.

(4) The experimental set 1 (comparison between two completely different human cell lines) and experimental set 2 (comparison among RNA preparation procedures) are not quite biologically meaningful. If it is possible, it is better for the authors to perform an experiment more similar to a real situation for biological discovery. Then the manuscript can attract more researchers to follow its guidelines.

Author response:

Reviewer #1 (Public Review):  

Weaknesses:  

The weakness of this study lies in the fact that many of the genomic datasets originated from novel methods that were not validated with orthogonal approaches, such as DNA-FISH. Therefore, the detailed correlations described in this work are based on methodologies whose efficacy is not clearly established. Specifically, the authors utilized two modified protocols of TSA-seq for the detection of NADs (MKI67IP TSA-seq) and LADs (LMNB1-TSA-seq). Although these methods have been described in a bioRxiv manuscript by Kumar et al., they have not yet been published. Moreover, and surprisingly, Kumar et al., work is not cited in the current manuscript, despite its use of all TSA-seq data for NADs and LADs across the four cell lines. Moreover, Kumar et al. did not provide any DNA-FISH validation for their methods. Therefore, the interesting correlations described in this work are not based on robust technologies.    

An attempt to validate the data was made for SON-TSA-seq of human foreskin fibroblasts (HFF) using multiplexed FISH data from IMR90 fibroblasts (from the lung) by the Zhuang lab (Su et al., 2020). However, the comparability of these datasets is questionable. It might have been more reasonable for the authors to conduct their analyses in IMR90 cells, thereby allowing them to utilize MERFISH data for validating the TSA-seq method and also for mapping NADs and LADs. 

We disagree with the statement that the TSA-seq approach and data has not been validated by orthogonal approaches and with the conclusion that the TSA-seq approach is not robust as summarized here and detailed below in “Specific Comments”.  TSA-seq is robust because it is based only on the original immunostaining specificity provided by the primary and secondary antibodies plus the diffusion properties of the tyramide-free radical. TSA-seq has been extensively validated by microscopy and by the orthogonal genomic measurements provided by LMNB1 DamID and NAD-seq.  This includes: a) the initial validation by FISH of both nuclear speckle (to an accuracy of ~50 nm) and nuclear lamina TSA-seq  and the cross-validation of nuclear lamina TSA-seq with lamin B1 DamID in a first publication (Chen et al, JCB 2018, doi: 10.1083/jcb.201807108); b) the further validation of SON TSA-seq by FISH in a second publication ((Zhang et al, Genome Research 2021, doi:10.1101/gr.266239.120); c) the cross-validation of nucleolar TSA-seq using NAD-seq and the validation by light microscopy of the predictions of differences in the relative distributions of centromeres, nuclear speckles, and nucleoli made from nuclear speckle, nucleolar, and pericentric heterochromatin TSA-seq in the Kumar et al, bioRxiv preprint (which is in a last revision stage involving additional formatting for the journal requirements) doi:https://doi.org/10.1101/2023.10.29.564613; d) the extensive validation of nuclear speckle, LMNB1, and nucleolar TSA-seq generated in HFF human fibroblasts using published light microscopy distance measurements of hundreds of probes generated by multiplexed immuno-FISH MERFISH data (Su et al, Cell 2020, https://doi.org/10.1016/j.cell.2020.07.032), as we described for nucleolar TSA-seq in the Kumar et al, bioRxiv preprint and to some extent for LMNB1 and SON TSA-seq in the current manuscript version (see Specific Comments with attached Author response image 2).

Reviewer 1 raised concerns regarding this FISH validation given that the HFF TSA-seq and DamID data was compared to IMR90 MERFISH measurements.  The Su et al, Cell 2020 MERFISH paper came out well after the 4D Nucleome Consortium settled on HFF as one of the two main “Tier 1” cell lines.  We reasoned that the nuclear genome organization in a second fibroblast cell line would be sufficiently similar to justify using IMR90 FISH data as a proxy for our analysis of our HFF data. Indeed, there is a high correlation between the HFF TSA-seq and distances measured by MERFISH to nuclear lamina, nucleoli, and nuclear speckles (Author response image 1).  Comparing HFF SON-TSA-seq data with published IMR90 SON TSA-seq data (Alexander et al, Mol Cell 2021, doi.org/10.1016/j.molcel.2021.03.006), the HFF SON TSA-seq versus MERFISH scatterplot is very similar to the IMR90 SON TSA-seq versus MERFISH scatterplot.  We acknowledge the validation provided by the IMR90 MERFISH is limited by the degree to which genome organization relative to nuclear locales is similar in IMR90 and HFF fibroblasts. However, the correlation between measured microscopic distances from nuclear lamina, nucleoli, and nuclear speckles and TSA-seq scores is already quite high. We anticipate the conclusions drawn from such comparisons are solid and will only become that much stronger with future comparisons within the same cell line.

Author response image 1.

Scatterplots showing the correlation between TSA-seq and MERFISH microscopic distances. Top: IMR90 SON TSA-seq (from Alexander et al, Mol Cell 2021) (left) and HFF SON TSA-seq (right) (x-axis) versus distance to nuclear speckles (y-axis). Bottom: HFF Lamin B1 TSA-seq (x-axis) versus distance to nuclear lamina (y-axis) (left) and HFF MKI67IP (nucleolar) TSA-seq (x-axis) versus distance to nucleolus (y-axis) (right).

In our revision, we will add justification of the use of IMR90 fibroblasts as a proxy for HFF fibroblasts through comparison of available data sets. 

Reviewer #2 (Public Review):  

Weaknesses:  

The experiments are largely descriptive, and it is difficult to draw many cause-and-effect relationships. Similarly, the paper would be very much strengthened if the authors provided additional summary statements and interpretation of their results (especially for those not as familiar with 3D genome organization). The study would benefit from a clear and specific hypothesis.

We acknowledge that this study was hypothesis-generating rather than hypothesis-testing in its goal. This research was funded through the NIH 4D-Nucleome Consortium, which had as its initial goal the development, benchmarking, and validation of new genomic technologies.  Our Center focused on the mapping of the genome relative to different nuclear locales and the correlation of this intranuclear positioning of the genome with functions- specifically gene expression and DNA replication timing. By its very nature, this project has taken a discovery-driven versus hypothesis-driven scientific approach.  Our question fundamentally was whether we could gain new insights into nuclear genome organization through the integration of genomic and microscopic measurements of chromosome positioning relative to multiple different nuclear compartments/bodies and their correlation with functional assays such as RNA-seq and Repli-seq.

Indeed, as described in this manuscript, this study resulted in multiple new insights into nuclear genome organization as summarized in our last main figure.  We believe our work and conclusions will be of general interest to scientists working in the fields of 3D genome organization and nuclear cell biology.  We anticipate that each of these new insights will prompt future hypothesis-driven science focused on specific questions and the testing of cause-and-effect relationships. 

Given the extensive scope of this manuscript, we were limited in the extent that we could describe and summarize the background, data, analysis, and significance for every new insight. In our editing to reach the eLife recommended word count, we removed some of the explanations and summaries that we had originally included. 

As suggested by Reviewer 2, in our revision we will add back additional summary and interpretation statements to help readers unfamiliar with 3D genome organization.

Specific Comments in response to Reviewer 1:

(1)  We disagree with the comment that TSA-seq has not been cross-validated by other orthogonal genomic methods.  In the first TSA-seq paper (Chen et al, JCB 2018, doi: 10.1083/jcb.201807108), we showed a good correlation between the identification of iLADs and LADs by nuclear lamin and nuclear speckle TSA-seq and the orthogonal genomic method of lamin B1 DamID, which is reproduced using our new TSA-seq 2.0 protocol in this manuscript.  Similarly, in the Kumar et al, bioRxiv preprint (doi:https://doi.org/10.1101/2023.10.29.564613), we showed a general agreement between the identification of NADs by nucleolar TSA-seq and the orthogonal genomic method of NAD-seq.  (We expect this preprint to be in press soon; it is now undergoing a last revision involving only reformatting for journal requirements.) Additionally, we also showed a high correlation between Hi-C compartments and subcompartments and TSA-seq in the Chen et al, JCB 2018 paper. Specifically, there is an excellent correlation between the A1 Hi-C subcompartment and Speckle Associated Domains as detected by nuclear speckle TSA-seq.  Additionally, the A2 Hi-C subcompartment correlated well with iLAD regions with intermediate nuclear speckle TSA-seq scores, and the B2 and B3 Hi-C subcompartments with LADs detected by both LMNB TSA-seq and LMNB1 DamID.  More generally, Hi-C A and B compartment identity correlated well with predictions of iLADs versus LADs from nuclear speckle and nuclear lamina TSA-seq.

(2)  In the Chen et al, JCB 2018 paper we also qualitatively and quantitatively validated TSA-seq using FISH.  Qualitatively, we showed that both nuclear speckle and nuclear lamin TSA-seq correlated well with distances to nuclear speckles versus the nuclear lamina, respectively, measured by immuno-FISH.

Quantitatively, we showed that SON TSA-seq could be used to estimate the microscopic mean distance to nuclear speckles with mean and median residuals of ~50 nm.  First, we used light microscopy to show that the spreading of tyramide-biotin signal from a point-source of TSA staining fits well with the exponential decay predicted theoretically by reaction-diffusion equations assuming a steady rate of tyramide-biotin free radical generation by the HRP enzyme and a constant probability throughout the nucleus of free-radical quenching (through reaction with protein tyrosine residues and nucleic acids).  Second, we used the exponential decay constant measured by light microscopy together with FISH measurements of mean speckle distance for several genomic regions to fit an exponential function and to predict distance to nuclear speckles genome-wide directly from SON TSA-seq sequencing reads.  Third, we used this approach to test the predictions against a new set of FISH measurements, demonstrating an accuracy of these predictions of ~50 nm.

(3)  The importance of the quantitative validation by immuno-FISH of using TSA-seq to estimate mean distance to nuclear speckles is that it demonstrates the robustness of the TSA-seq approach.  Specifically, it shows how the TSA-seq signal is predicted to depend only on the specificity of the primary and secondary antibody staining and the diffusion properties of the tyramide-biotin free radicals produced by the HRP peroxidase.  This is fundamentally different from the significant dependence on antibodies and choice of marker proteins for molecular proximity assays such as DamID, ChIP-seq, and Cut and Run/Tag which depend on molecular proximity for labeling and/or pulldown of DNA.

This robustness leads to specific predictions.  First, it predicts similar TSA-seq signals will be produced using antibodies against different marker proteins against the same nuclear compartment.  This is because the exponential decay constant (distance at which the signal drops by one half) for the spreading of the TSA is in the range of several hundred nm, as measured by light microscopy for several TSA staining conditions.  Indeed, we showed in the Chen et al, JCB 2018 paper that antibodies against two different nuclear speckle proteins produced very similar TSA-seq signals while antibodies against LMNB versus LMNA also produced very similar TSA-seq signals.  Similarly, we showed in the Kumar et al preprint that antibodies against four different nucleolar proteins showed similar TSA-seq signals, with the highest correlation coefficients for the TSA-seq signals produced by the antibodies against two GC nucleolar marker proteins and the TSA-seq signals produced by the antibodies against two FC/DFC nucleolar marker proteins.

Author response image 2.

Comparison of TSA-seq data from different cell lines versus IMR90 MERFISH.  The observed correlation between SON (nuclear speckle) TSA-seq versus MERFISH is nearly as high for TSA-seq data from HFF as it is for TSA-seq data from the IMR90 cell line (Alexander et al, Mol Cell 2021) in which the MERFISH was performed. The correlations for SON, LMNB1 (nuclear lamina) and MKI67IP (nucleolus) versus MERFISH are highest for HFF TSA-seq data as compared to TSA-seq data from other cell lines (H1, K562, HCT116).  Comparison of measured distances to nuclear locale (y-axis) versus TSA-seq scores (x-axis) from different cell lines labeled in red. Left to right: SON, LMNB1, and MKI67IP.  Top to bottom: SON TSA-seq versus MERFISH for two TSA-seq replicates; TSA-seq from HFF, H1, K562, and HCT116 versus MERFISH.

Second, it predicts that the quantitative relationship between TSA-seq signal and mean distance from a nuclear compartment will depend on the convolution of the predicted exponential decay of spreading of the TSA signal produced by a point source with the more complicated staining distribution of nuclear compartments such as the nuclear lamina or nucleoli.  We successfully used this concept to explain the differences emerging between LMNB1 DamID and TSA-seq signals for flat nuclei and to recognize the polarized distribution of different LADs over the nuclear periphery.

(4)  After our genomic data production and during our data analysis, a valuable resource from the Zhuang lab was published, using MERFISH to visualize hundreds of genomic loci in IMR90 cells. We acknowledge that the much more extensive validation of TSA-seq by the multiplexed immuno-FISH MERFISH data is dependent on the degree to which the nuclear genome organization is similar between IMR90 and HFF fibroblasts.  However, the correlation between distances to nuclear speckles, nucleoli, and the nuclear lamina measured in IMR90 fibroblasts and the nuclear speckle, nucleolar, and nuclear lamina TSA-seq measured in HFF fibroblasts is already striking (See Author response image 1).  With regard to SON TSA-seq, the MERFISH versus HFF TSA-seq correlation is close to what we observe using published IMR90 SON TSA-seq data (correlation coefficients of 0.89 (IMR90 TSA-seq) versus 0.86 (HFF TSA-seq).  Moreover, this correlation is highest using TSA-seq data from HFF cells as compared to the three other cell lines. (see Author response image 2).  We believe these correlations can be considered a lower bound on the actual correlations between the FISH distances and TSA-seq that we would have observed if we had performed both assays on the same cell line. 

(5)  Currently, we still require tens of millions of cells to perform each TSA-seq assay.  This requires significant expansion of cells and a resulting increase in passage numbers of the IMR90 cells before we can perform the TSA-seq. During this expansion we observe a noticeable slowing of the IMR90 cell growth as expected for secondary cell lines as we approach the Hayflick limit.  We still do not know to what degree nuclear organization relative to nuclear locales may change as a function of cell cycle composition (ie percentage of cycling versus quiescent cells) and cell age.  Thus, even if we performed TSA-seq on IMR90 cells we would be comparing MERFISH from lower passages with a higher percentage of actively proliferating cells with TSA-seq from higher passages with a higher percentage of quiescent cells. 

We are currently working on a new TSA-seq protocol that will work with thousands of cells.  We believe it is better investment of time and resources to wait until this new protocol is optimized before we repeat TSA-seq in IMR90 cells for a better comparison with multiplexed FISH data. 

Specific Comments in response to Reviewer 2:

(1)  As we acknowledge in our Response summary, we were limited in the degree to which we could actually follow-up our findings with experiments designed to test specific hypotheses generated by our data.  However, we do want to point out that our comparison of wild-type K562 cells with the LMNA/LBR double knockout was designed to test the long-standing model that nuclear lamina association of genomic loci contributes to gene silencing.  This experiment was motivated by our surprising result that gene expression differences between cell lines correlated strongly with differences in positioning relative to nuclear speckles rather than the nuclear lamina.  Despite documenting in these double knockout cells a decreased nuclear lamina association of most LADs, and an increased nuclear lamina association of the “p-w-v” fiLADs identified in this manuscript, we saw no significant change in gene expression in any of these regions as compared to wild-type K562 cells.  Meanwhile, distances to nuclear speckles as measured by TSA-seq remained nearly constant.

We would argue that this represents a specific example in which new insights generated by our genomics comparison of cell lines led to a clear and specific hypothesis and the experimental testing of this hypothesis.

In response to Reviewer 2, we are modifying the text to make this clearer and to explicitly describe how we were testing the hypothesis that distance to nuclear lamina is correlated with but not causally linked to gene expression and how to test this hypothesis we used a DKO of LMNA and LBR to change distances relative to the nuclear lamina and to test the effect on gene expression.

eLife assessment

This study develops a useful metric for quantifying codon usage adaptation - the Codon Adaptation Index of Species (CAIS). This metric permits direct comparisons of the strength of selection at the molecular level across species. The study is based on solid evidence, and the authors identify relationships between CAIS and the presence of disordered protein domains. Other correlations, such as the one between CAIS and body size, are weak and non-significant. In summary, the study introduces an interesting new approach to quantifying codon usage across species, which may be helpful in attempts to measure selection at the molecular level.

Reviewer #2 (Public Review):

Assessment

This study develops a potentially useful metric for quantifying codon usage adaptation – the Codon Adaptation Index of Species (CAIS) – that is intended to allow for more direct comparisons of the strength of selection at the molecular level across species by controlling for interspecies variation in amino acid usage and GC content. As evidence to support there claim CAIS better controls for GC content and amino acid usage across species, they note that CAIS has only a weak positive correlation with GC% (that does not stand up to multiple hypothesis testing correction) while CAI has a clear negative correlation with GC%. Using CAIS, they find better adapted species have more disordered protein domains; however, excitement about these findings is dampened due to (1) this result is also observed using the effective number of codons (ENC) and

(2) concerns over the interpretation of CAIS as a proxy for the effectiveness of selection.

Public Review

Summary

The goal of the authors in this study is to develop a more reliable approach for quantifying codon usage such that it is more comparable across species. Specifically, the authors wish to estimate the degree of adaptive codon usage, which is potentially a general proxy for the strength of selection at the molecular level. To this end, the authors created the Codon Adaptation Index for Species (CAIS) that attempts to control for differences in amino acid usage and GC% across species. Using their new metric, the authors observe a positive relationship between CAIS and the overall “disorderedness” of a species protein domains. I think CAIS has the potential to be a valuable tool for those interested in comparing codon adaptation across species in certain situations. However, I have certain theoretical concerns about CAIS as a direct proxy for the efficiency of selection sNe when mutation bias changes across species.

Strengths

(1) I appreciate that the authors recognize the potential issues of comparing CAI when amino acid usage varies and correct for this in CAIS. I think this is sometimes an under-appreciated point in the codon usage literature, as CAI is a relative measure of codon usage bias (i.e. only considers synonyms). However, the strength of natural selection on codon usage can potentially vary across amino acids, such that comparing mean CAI between protein regions with different amino acid biases may result in spurious signals of statistical significance.

(2) The CAIS metric presented here is generally applicable to any species that has an annotated genome with protein-coding sequences. A significant improvement over the previous version is the implementation of software tool for applying this method.

(3) The authors do a better job of putting their results in the context of the underlying theory of CAIS compared to the previous version.

(4) The paper is generally well-written.

Weaknesses

(1) The previously observed correlation between CAIS and body size was due to a bug when calculating phylogenetic independent contrasts. I commend the authors for acknowledging this mistake and updating the manuscript accordingly. I feel that the unobserved correlation between CAIS and body size should remain in the final version of the manuscript. Although it is disappointing that it is not statistically significant, the corrected results are consistent with previous findings (Kessler and Dean 2014).

(2) I appreciate the authors for providing a more detailed explanation of the theoretical basis model. However, I remain skeptical that shifts in CAIS across species indicates shifts in the strength of selection. I am leaving the math from my previous review here for completeness.

As in my previous review, let’s take a closer look at the ratio of observed codon frequencies vs. expected codon frequencies under mutation alone, which was previously notated as RSCUS in the original formulation. In this review, I will keep using the RSCUS notation, even though it has been dropped from the updated version. The key point is this is the ratio of observed and expected codon frequencies. If this ratio is 1 for all codons, then CAIS would be 0 based on equation 7 in the manuscript – consistent with the complete absence of selection on codon usage. From here on out, subscripts will only be used to denote the codon and it will be assumed that we are only considering the case of r = genome for some species s.

I think what the authors are attempting to do is “divide out” the effects of mutation bias (as given by Ei), such that only the effects of natural selection remain, i.e. deviations from the expected frequency based on mutation bias alone represents adaptive codon usage. Consider Gilchrist et al. GBE 2015, which says that the expected frequency of codon i at selection-mutation-drift equilibrium in gene g for an amino acid with Na synonymous codons is

where ∆M is the mutation bias, ∆η is the strength of selection scaled by the strength of drift, and φg is the gene expression level of gene g. In this case, ∆M and ∆η reflect the strength and direction of mutation bias and natural selection relative to a reference codon, for which ∆M,∆η = 0. Assuming the selection-mutation-drift equilibrium model is generally adequate to model of the true codon usage patterns in a genome (as I do and I think the authors do, too), the Ei,g could be considered the expected observed frequency codon i in gene g

E[Oi,g].

Let’s re-write the  in the form of Gilchrist et al., such that it is a function of mutation bias ∆M. For simplicity we will consider just the two codon case and assume the amino acid sequence is fixed. Assuming GC% is at equilibrium, the term gr and 1 − gr can be written as

where µx→y is the mutation rate from nucleotides x to y. As described in Gilchrist et al. MBE 2015 and Shah and Gilchrist PNAS 2011, the mutation bias . This can be expressed in terms of the equilibrium GC content by recognizing that

As we are assuming the amino acid sequence is fixed, the probability of observing a synonymous codon i at an amino acid becomes just a Bernoulli process.

If we do this, then

Recall that in the Gilchrist et al. framework, the reference codon has ∆MNNG,NNG \= 0 =⇒ e−∆MNNG,NNG \=

(1) Thus, we have recovered the Gilchrist et al. model from the formulation of Ei under the assumption that natural selection has no impact on codon usage and codon NNG is the pre-defined reference codon. To see this, plug in 0 for ∆η in equation (1).

We can then calculate the expected RSCUS using equation (1) (using notation E[Oi]) and equation (6) for the two codon case. For simplicity assume, we are only considering a gene of average expression (defined as ). Assume in this case that NNG is the reference codon (∆MNNG,∆ηNNG \= 0).

This shows that the expected value of RSCUS for a two codon amino acid is expected to increase as the strength of selection ∆η increases, which is desired. Note that ∆η in Gilchrist et al. is formulated in terms of selection against a codon relative to the reference, such that a negative value represents that a codon is favored relative to the reference. If ∆η = 0 (i.e. selection does not favor either codon), then E[RSCUS] = 1. Also note that the expected RSCUS does not remain independent of the mutation bias. This means that even if sNe (i.e. the strength of natural selection) does not change between species, changes to the strength and direction of mutation bias across species could impact RSCUS. Assuming my math is right, I think one needs to be cautious when interpreting CAIS as representative of the differences in the efficiency of selection across species except under very particular circumstances.

Consider our 2-codon amino acid scenario. You can see how changing GC content without changing selection can alter the CAIS values calculated from these two codons. Particularly problematic appears to be cases of extreme mutation biases, where CAIS tends toward 0 even for higher absolute values of the selection parameter. Codon usage for the majority of the genome will be primarily determined by mutation biases,

with selection being generally strongest in a relatively few highly-expressed genes. Strong enough mutation biases ultimately can overwhelm selection, even in highly-expressed genes, reducing the fraction of sites subject to codon adaptation.

Peer review image 1.

Peer review image 2.

CAIS (Low Expression)

Peer review image 3.

CAIS (Average Expression)

Peer review image 4.

CAIS (High Expression)

If we treat the expected codon frequencies as genome-wide frequencies, then we are basically assuming this genome made up entirely of a single 2-codon amino acid with selection on codon usage being uniform across all genes. This is obviously not true, but I think it shows some of the potential limitations of the CAIS approach. Based on these simulations, CAIS seems best employed under specific scenarios. One such case could be when it is known that mutation bias varies little across the species of interest. Looking at the species used in this manuscript, most of them have a GC content around 0.41, so I suspect their results are okay (assuming things like GC-biased gene conversion are not an issue). Outliers in GC content probably are best excluded from the analysis.

Although I have not done so, I am sure this could be extended to the 4 and 6 codon amino acids. One potential challenge to CAIS is the non-monotonic changes in codon frequencies observed in some species (again, see Shah and Gilchrist 2011 and Gilchrist et al. 2015).

Author response:

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

In addition to our responses to reviewer suggestions below, a minor bug in the calculation of CAIS was brought to our attention by a reader of our preprint. We have corrected this bug and rerun analyses, whose results became slightly stronger as noise was removed. While we were doing that, someone pointed out to us that our equations were almost the same as Kullback-Leibler divergence, which explains why our metric performed so well. We have made the numerically trivial (see before vs. after figure below) mathematical change to use Kullback-Leibler divergence instead, and now have a better story, with a solid basis in information theory, as to why CAIS works.

Author response image 1.

Unfortunately, we discovered a second bug that caused our PIC correction code to fail to perform the needed correction for phylogenetic confounding. The previously reported correlation between CAIS (or ENC) with body mass no longer survives PIC-correction. We have therefore removed this analysis from the manuscript. Our story now stands more on the theoretical basis of CAIS and ENC than on the post facto validation than it previously did. We now also present CAIS and ENC on a more equal footing. ENC results are slightly stronger, while CAIS has the complementary advantage of correcting for amino acid frequencies.

The work involved in these changes, as well as some of the responses to reviews below, justifies changing the second author into a co-first author, and adding an additional coauthor (Hanon McShea) who discovered the second bug.

Reviewer #1 (Public Review): 

In this manuscript, the authors propose a new codon adaptation metric, Codon Adaptation Index of Species (CAIS), which they present as an easily obtainable proxy for effective population size. To permit between-species comparisons, they control for both amino acid frequencies and genomic GC content, which distinguishes their approach from existing ones. Having confirmed that CAIS negatively correlates with vertebrate body mass, as would be expected if small-bodied species with larger effective populations experience more efficient selection on codon usage, they then examine the relationship between CAIS and intrinsic structural disorder in proteins. 

The idea of a robust species-level measure of codon adaptation is interesting. If CAIS is indeed a reliable proxy for the effectiveness of selection, it could be useful to analyze species without reliable life history- or mutation rate data (which will apply to many of the genomes becoming available in the near future). 

A key question is whether CAIS, in fact, measures adaptation at the codon level. Unfortunately, CAIS is only validated indirectly by confirming a negative correlation with body mass. As a result, the observations about structural disorder are difficult to evaluate. 

As discussed in the preamble above, we have replaced the body mass validation with a stronger theoretical basis in information theory.

A potential problem is that differences in GC between species are not independent of life history. Effective population size can drive compositional differences due to the effects of GC-biased gene conversion (gBGC). As noted by Galtier et al. (2018), genomic GC correlates negatively with body mass in mammals and birds. It would therefore be important to examine how gBGC might affect CAIS, and to what extent it could explain the relationship between CAIS and body mass. 

Suppose that gBGC drives an increase in GC that is most pronounced at 3rd codon positions in highrecombination regions in small-bodied species. In this case, could observed codon usage depart more strongly from expectations calculated from overall genomic GC in small vertebrates compared to large ones? The authors also report that correcting for local intergenic GC was unsuccessful, based on the lack of a significant negative relationship with body mass (Figure 3D). In principle, this could also be consistent with local GC providing a relatively more appropriate baseline in regions with high recombination rates. Considering these scenarios would clarify what exactly CAIS is capturing. 

Figure 3 (previously Supplementary Figures S5A and S5B) shows that CAIS is negligibly correlated with %GC (not robust to multiple comparisons correction), and ENC not at all. We believe this is evidence against the possibility brought up by the reviewer, i.e. that Ne might affect gBGC (and hence global %GC). This relationship, if present, could act as a confounding effect, but it is not present within our species dataset. 

Note that we expect our genomic-GC-based codon usage expectations to reflect unchecked gBGC in an average genomic region, independently of whether that species has high or low Ne. Our working model is that non-selective forces, include gBGC as well as conventional mutation biases, vary among species, and that they rather than selection determine each species’ genome-wide %GC. By correcting for genome-wide %GC, CAIS and ENC correct for both mutation bias and gBGC, in order to isolate the effects of selection.

This argument, based on an average genomic region, is vulnerable to gene-rich genomic regions having differentially higher recombination rates and hence GC-biased gene conversion. However, we do not see the expected positive correlation between |𝐥𝐨𝐜𝐚𝐥 𝐆𝐂 - global GC| and CAIS (see new Figure 5), again suggesting that gene conversion strength is not a confounding factor acting on CAIS.

Given claims about "exquisitely adapted species", the case for using CAIS as a measure of codon adaptation would also be stronger if a relationship with gene expression could be demonstrated. RSCU is expected to be higher in highly expressed genes. Is there any evidence that the equivalent GCcontrolled measure behaves similarly? 

Correlations with gene expression are outside the scope of the current work, which is focused on producing and exploiting a single value of codon adaptation per species. It is indeed possible that our general approach of using Kullback-Leibler divergence to correct for genomic %GC could be useful in future work investigating differences among genes.  

The manuscript is overall easy to follow, though some additional context may be helpful for the general reader. A more detailed discussion of how this work compares to the approach taken by Galtier et al. (2018), which accounted for GC content and gBGC when examining codon preferences, would be appropriate, for example. In addition, it would have been useful to mention past work that has attempted to explicitly quantify selection on codon usage. 

One key difference between our work and that of Galtier et al. 2018 is that our approach does not rely on identifying specific codon preferences as a function of species. Our approach might therefore be robust to scenarios where different genes have different codon preferences (see Gingold et al. 2014 https://doi.org/10.1016/j.cell.2014.08.011). At a high level, our results are in broad agreement with those of Galtier et al., 2018, who found that gBGC affected all animal species, regardless of Ne, and who like us, found that the degree of selection on codon usage depended on Ne.

Reviewer #2 (Public Review): 

## Summary 

The goal of the authors in this study is to develop a more reliable approach for quantifying codon usage such that it is more comparable across species. Specifically, the authors wish to estimate the degree of adaptive codon usage, which is potentially a general proxy for the strength of selection at the molecular level. To this end, the authors created the Codon Adaptation Index for Species (CAIS) that controls for differences in amino acid usage and GC% across species. Using their new metric, the authors find a previously unobserved negative correlation between the overall adaptiveness of codon usage and body size across 118 vertebrates. As body size is negatively correlated with effective population size and thus the general strength of natural selection, the negative correlation between CAIS and body size is expected. The authors argue this was previously unobserved due to failures of other popular metrics such as Codon Adaptation Index (CAI) and the Effective Number of Codons (ENC) to adequately control for differences in amino acid usage and GC content across species. Most surprisingly, the authors also find a positive relationship between CAIS and the overall "disorderedness" of a species protein domains. As some of these results are unexpected, which is acknowledged by the authors, I think it would be particularly beneficial to work with some simulated datasets. I think CAIS has the potential to be a valuable tool for those interested in comparing codon adaptation across species in certain situations. However, I have certain theoretical concerns about CAIS as a direct proxy for the efficiency of selection $sN_e$ when the mutation bias changes across species.  

## Strengths 

(1) I appreciate that the authors recognize the potential issues of comparing CAI when amino acid usage varies and correct for this in CAIS. I think this is sometimes an under-appreciated point in the codon usage literature, as CAI is a relative measure of codon usage bias (i.e. only considers synonyms). However, the strength of natural selection on codon usage can potentially vary across amino acids, such that comparing mean CAI between protein regions with different amino acid biases may result in spurious signals of statistical significance (see Cope et al. Biochemica et Biophysica Acta - Biomembranes 2018 for a clear example of this). 

We now cite Cope et al. as an example of how amino acid composition can act as a confounding factor.

(2) The authors present numerous analysis using both ENC and mean CAI as a comparison to CAIS, helping given a sense of how CAIS corrects for some of the issues with these other metrics. I also enjoyed that they examined the previously unobserved relationship between codon usage bias and body size, which has bugged me ever since I saw Kessler and Dean 2014. The result comparing protein disorder to CAIS was particularly interesting and unexpected. 

Unfortunately, our previous PIC correction code was buggy, and in fact the relationship with body size does not survive PIC correction (although it is strong prior to PIC correction). We have therefore removed it from the paper. However, the more novel result on protein disorder remains strong.

(3) The CAIS metric presented here is generally applicable to any species that has an annotated genome with protein-coding sequences. 

## Weaknesses 

(1) The main weakness of this work is that it lacks simulated data to confirm that it works as expected. This would be particularly useful for assessing the relationship between CAIS and the overall effect of protein structure disorder, which the authors acknowledge is an unexpected result. I think simulations could also allow the authors to assess how their metric performs in situations where mutation bias and natural selection act in the same direction vs. opposite directions. Additionally, although I appreciate their comparisons to ENC and mean CAI, the lack of comparison to other popular codon metrics for calculating the overall adaptiveness of a genome (e.g. dos Reis et al.'s $S$ statistic, which is a function of tRNA Adaptation Index (tAI) and ENC) may be more appropriate. Even if results are similar to $S$, CAIS has a noted advantage that it doesn't require identifying tRNA gene copy numbers or abundances, which I think are generally less readily available than genomic GC% and protein-coding sequences. 

The main limitation of dos Reis’s test in our view is that, like the better versions of CAI, it requires comparable orthologs across species. See also the discussion below re the benefits of proteome-wide approach. We now also note the advantage of not needing tRNA gene copy numbers and abundances. 

Simulated datasets would be great, but we think it a nice addition rather than must-have, in particular because we are skeptical about whether our understanding of all relevant processes is good enough such that simulations would add much to our more heuristic argument along the lines of Figure 2. E.g. the complications of Gingold et al. 2014 cited above are pertinent, but incorporating them would make simulations quite involved. Instead, we now have a stronger theoretical justification for CAIS grounded in information theory. We have significantly expanded discussion of Figure 2 to give a clearer idea of the conceptual underpinnings of CAIS and ENC.

The authors mention the selection-mutation-drift equilibrium model, which underlies the basic ideas of this work (e.g. higher $N_e$ results in stronger selection on codon usage), but a more in-depth framing of CAIS in terms of this model is not given. I think this could be valuable, particularly in addressing the question "are we really estimating what we think we're estimating?" 

Let's take a closer look at the formulation for RSCUS. From here on out, subscripts will only be used to denote the codon and it will be assumed that we are only considering the case of r = genome for some species s.

I think what the authors are attempting to do is "divide out" the effects of mutation bias (as given by $E_i$), such that only the effects of natural selection remain, i.e. deviations from the expected frequency based on mutation bias alone represent adaptive codon usage. Consider Gilchrist et al. MBE 2015, which says that the expected frequency of codon i at selection-mutation-drift equilibrium in gene g for an amino acid with Na synonymous codons is

where ∆M is the mutation bias, ∆η is the strength of selection scaled by the strength of drift, and φg is the gene expression level of gene g. In this case, ∆M and ∆η reflect the strength and direction of mutation bias and natural selection relative to a reference codon, for which ∆M,∆η = 0. Assuming the selection-mutation-drift equilibrium model is generally adequate to model of the true codon usage patterns in a genome (as I do and I think the authors do, too), the Ei,g could be considered the expected observed frequency codon i in gene g

E[Oi,g].

Let’s re-write the  in the form of Gilchrist et al., such that it is a function of mutation bias ∆M. For simplicity we will consider just the two codon case and assume the amino acid sequence is fixed. Assuming GC% is at equilibrium, the term gr and 1 − gr can be written as

where µx→y is the mutation rate from nucleotides x to y. As described in Gilchrist et al. MBE 2015 and Shah and Gilchrist PNAS 2011, the mutation bias .This can be expressed in terms of the equilibrium GC content by recognizing that

As we are assuming the amino acid sequence is fixed, the probability of observing a synonymous codon i at an amino acid becomes just a Bernoulli process. 

If we do this, then 

Recall that in the Gilchrist et al. framework, the reference codon has ∆MNNG,NNG \= 0 =⇒ e−∆MNNG,NNG \=1. Thus, we have recovered the Gilchrist et al. model from the formulation of $E_i$ under the assumption that natural selection has no impact on codon usage and codon NNG is the pre-defined reference codon. To see this, plug in 0 for ∆η in equation (1).. 

We can then calculate the expected RSCUS using equation (1) (using notation E[Oi]) and equation (6) for the two codon case. For simplicity assume, we are only considering a gene of average expression (defined as ). Assume in this case that NNG is the reference codon (∆MNNG,∆ηNNG \= 0).

This shows that the expected value of RSCUS for a two-codon amino acid is expected to increase as the strength of selection $\Delta\eta$ increases, which is desired. Note that $\Delta\eta$ in Gilchrist et al. is formulated in terms of selection *against* a codon relative to the reference, such that a negative value represents that a codon is favored relative to the reference. If $\Delta\eta = 0$ (i.e. selection does not favor either codon), then $E[RSCUS] = 1$. Also note that the expected RSCUS does not remain independent of the mutation bias. This means that even if $sN_e$ (i.e. the strength of natural selection) does not change between species, changes to the strength and direction of mutation bias across species could impact RSCUS. Assuming my math is right, I think one needs to be cautious when interpreting CAIS as representative of the differences in the efficiency of selection across species except under very particular circumstances. One such case could be when it is known that mutation bias varies little across the species of interest. Looking at the species used in this manuscript, most of them have a GC content ranging around 0.41, so I suspect their results are okay. 

Although I have not done so, I am sure this could be extended to the 4 and 6 codon amino acids. 

We thank Reviewer 2 for explicitly laying out the math that was implicit in our Figures 1 and 2. While we keep our more heuristic presentation, our revised manuscript now more clearly acknowledges that the per-site codon adaptation bias depicted in Figure 1 has limited sensitivity to s*Ne. The reason that we believe our approach worked despite this, is that we think the phenomenon is driven by what is shown in Figure 2. I.e., where Ne makes a difference is by determining the proteome-wide fraction of codons subject to significant codon adaptation, rather than by determining the strength of codon adaptation at any particular site or gene. We have made multiple changes to the texts to make this point clearer.

Another minor weakness of this work is that although the method is generally applicable to any species with an annotated genome and the code is publicly available, the code itself contains hard-coded values for GC% and amino acid frequencies across the 118 vertebrates. The lack of a more flexible tool may make it difficult for less computationally-experienced researchers to take advantage of this method. 

Genome-wide %GC values are hard-coded because they were taken from the previous study of James et al. (2023) https://doi.org/10.1093/molbev/msad073. As summarized in the manuscript, genome-wide %GC was a byproduct of a scan of all six reading frames across genic and intergenic sequences available from NCBI with access dates between May and July 2019. The more complicated code used to calculate the intergenic %GC, and the code used to calculate amino acid frequencies is located at https://github.com/MaselLab/CodonAdaptation-Index-of-Species. Luckily, someone else just wrote a simpler end to end pipeline for us, on the basis of our preprint. We now note this in the Acknowledgements, and link to it: https://github.com/gavinmdouglas/handy_pop_gen/blob/main/CAIS.py.

eLife assessment

This is a valuable study in which the authors provide an expression profile of the human blood fluke, Schistosoma mansoni. A strength of this solid study is in its inclusion of in situ hybridisation to validate the predictions of the transcript analysis.

Reviewer #1 (Public Review):

In this work, the authors provide a valuable transcriptomic resource for the intermediate free-living transmission stage (miracidium larva) of the blood fluke. The single-cell transcriptome inventory is beautifully supplemented with in situ hybridization, providing spatial information and absolute cell numbers for many of the recovered transcriptomic states. The identification of sex-specific transcriptomic states within the populations of stem cells was particularly unexpected. The work comprises a rich resource to complement the biology of this complex system.

Comments on revised version:

I have read through the responses and the revised manuscript. I think together this results in an improved version.

Reviewer #2 (Public Review):

Summary:

In this manuscript the authors have generated a single-cell atlas of the miracidium, the first free-living stage of an important human parasite, Schistosoma mansoni. Miracidia develop from eggs produced in the mammalian (human) host and are released into freshwater, where they can infect the parasite's intermediate snail host to continue the life cycle. This study adds to the growing single-cell resources that have already been generated for other life-cycle stages and, thus, provides a useful resource for the field.

Strengths:

Beyond generating lists of genes that are differentially expressed in different cell types, the authors validated many of the cluster-defining genes using in situ hybridization chain reaction. In addition to providing the field with markers for many of the cell types in the parasite at this stage, the authors use these markers to count the total number of various cell types in the organism. Because the authors realized that their cell isolation protocols were biasing the cell types they were sequencing, they applied a second method to help them recover additional cell types.

Schistosomes have ZW sex chromosomes and the authors make the interesting observation that the stem cells at this stage are already expressing sex (i.e. W)-specific genes.

Comments on revised version:

The manuscript has been improved after revisions. The methods, data and analyses broadly support the claims with only minor weaknesses.

Author response:

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

eLife assessment

This is a valuable study in which the authors provide an expression profile of the human blood fluke, Schistosoma mansoni. A strength of this solid study is in its inclusion of in situ hybridisation to validate the predictions of the transcript analysis.

We thank the reviewers and the editor for their effort and expertise in reviewing our manuscript. We have made changes based on the reviews and believe this has greatly strengthened our manuscript. We appreciate their insightful comments and suggestions.

Public Reviews:

Reviewer #1 (Public Review):

In this work, the authors provide a valuable transcriptomic resource for the intermediate free-living transmission stage (miracidium larva) of the blood fluke. The single-cell transcriptome inventory is beautifully supplemented with in situ hybridization, providing spatial information and absolute cell numbers for many of the recovered transcriptomic states. The identification of sex-specific transcriptomic states within the populations of stem cells was particularly unexpected. The work comprises a rich resource to complement the biology of this complex system, however falls short in some technical aspects of the bioinformatic analyses of the generated sequence data.

(1) Four sequencing libraries were generated and then merged for analysis, however, the authors fail to document any parameters that would indicate that the clustering does not suffer from any batch effects.

We thank the reviewer for this comment which has given us the opportunity to elaborate on this interesting point. Consequently, we have added evidence to show that the data do not suffer from batch effects between samples (e.g. between sorted samples 1 and 4, and unsorted samples 2 and 3). We now show that there are contributions to all clusters from sorted and unsorted samples and highlight the benefits to using both conditions in a cell atlas with unknown cell types.

Accordingly, we have now added the following paragraph to line 153:

There were contributions from sorted and unsorted samples in almost all clusters (except ciliary plates). We found that some cell/tissue types had similar recovery from both methods (e.g. Stem A, Muscle 2, and Tegument), others were preferentially recovered by sorting (e.g Neuron 1, Neuron 4, and Stem E), and some were depleted by sorting (e.g. Parenchyma 1, Protonephridia, and Ciliary plates) (Supplementary Figure 1) , Supplementary Table 4). This variation in recovery, therefore, enabled us to maximise the discovery and inclusion of different cell types in the atlas.

We have now added a Supplementary Figure 1 showing the contribution of sorted and unsorted cells to the Seurat clusters. We have also included a Supplementary Table 4 detailing the cell number contribution for both conditions and the percentages in order to easily compare differential recovery between cell types.

These are added to the manuscript.

(2) Additionally, the authors switch between analysis platforms without a clear motivation or explanation of what the fundamental differences between these platforms are. While in theory, any biologically robust observation should be recoverable from any permutation of analysis parameters, it has been recently documented that the two popular analysis platforms (Seurat - R and scanPy python) indeed do things slightly differently and can give different results (https://www.biorxiv.org/content/10.1101/2024.04.04.588111v1). For this reason, I don't think that one can claim that Seurat fails to find clusters resolved by SAM without running a similar pipeline on the cluster alone as was done with SAM/scanPy here. The manuscript itself needs to be checked carefully for misleading statements in this regard.

We thank the reviewer for this comment and agree that it’s important to increase the clarity on this matter. We have added additional detail to explain that results of subclustering Neuron 1 using Seurat and SAM/ScanPy were broadly similar, but that we presented the results from the SAM/ScanPy analysis due to the strengths of SAM in detecting small differences in gene expression (Tarashanky et al., 2019 PMID: 31524596). We have included here the UMAP showing subclustering of Neuron 1 in Seurat for comparison.

Author response image 1.

UMAP showing subclustering of Neuron 1 cluster in Seurat (SCT normalisation, PC = 19, resolution = 0.3).

We’ve added this additional text to the ‘Neuron abundance and diversity’ section on line 220:

We explored whether Neuron 1 could be further subdivided into transcriptionally distinct cells by subclustering (Supplementary Figure 2; Supplementary Table 6) using the self-assembling manifold (SAM) algorithm (Tarashansky et al., 2019) with ScanPy (Wolf et al., 2018), given its reported strength in discerning subtle variation in gene expression (Tarashansky et al., 2019), although a similar topology was subsequently found using Seurat.

(3) Similarly, the manuscript contains many statements regarding clusters being 'connected to', or forming a 'bridge' on the UMAP projection. One must be very careful about these types of statements, as the relative position of cells on a reduced-dimension cell map can be misleading (see Chari and Pachter 2023). To support these types of interpretations, the authors should provide evidence of gene expression transitions that support connectivity as well as stability estimates of such connections under different parameter conditions. Otherwise, these descriptors hold little value and should be dropped and the transcriptomic states simply defined as clusters with no reference to their positions on the UMAP.

We thank the reviewer for this thoughtful comment. We agree and have rephrased those statements accordingly e.g. line numbers 218, 439, 543, and 557.

(4) The underlying support for the clusters as transcriptomically unique identities is not well supported by the dot plots provided. The authors used very permissive parameters to generate marker lists, which hampers the identification of highly specific marker genes. This permissive approach can allow for extensive lists of upregulated genes for input into STRING/GO analyses, this is less useful for evaluating the robustness of the cluster states. Running the Seurat::FindAllMarkers with more stringent parameters would give a more selective set of genes to display and thereby increase the confidence in the reader as to the validity of profiles selected as being transcriptomically unique.

The Reviewer is correct in noting that we used a permissive approach to enable a better understanding of the biology of each cluster, based on analysing enriched functions. However, we disagree about the suitability of the approach for finding markers. First, the permissive approach produced longer candidate lists, but those with the best AUC scores for each cluster are at the top of the list for each cluster. Second, some of the markers with lower expression also revealed interesting biology (e.g. Notum in the muscles). Furthermore, we used filtering on the marker genes lists to increase the minimum marker gene scores for analyses such as the GO analyses (details in the GO section of the methods). It’s important to stress that our approach also utilised validation by FISH for top marker genes, as well as biologically informative genes that were lower down the marker gene list.

(5) Figure 5B shows a UMAP representation of cell positions with a statement that the clustering disappears. As a visual representation of this phenomenon, the UMAP is a very good tool, however, to make this statement you need to re-cluster your data after the removal of this gene set and demonstrate that the data no longer clusters into A/B and C/D.

We’ve added Supplementary Figure 13 to show that after removing WSR and ZSR genes and reclustering, the data no longer clusters in A/B and C/D, even at a higher resolution where clusters appear oversplit.

Also, as a reader, these data beg the question: which genes are removed here? Is there an over-representation of any specific 'types' of genes that could lead to any hypotheses of the function? Perhaps the STRING/GO analyses of this gene set could be informative.

We have performed GO-enrichment analyses on W-specific genes, Z-specific genes and both together compared to the rest of the genome, but we did not find very informative results (see Supplementary Table 13 that we have now added, line 464). This may be due to the large difference in size. There are approx 900 Z-specific genes (males two copy, females one copy), while approx 30 W-specific genes many of which have homologs in the Z-specific region of the genome. Instead we suggest that tissue-specific regulation of gene dosage compensation is the more likely explanation as reported for other species (Valsecchi et al. 2018).

(6) How do the proportions of cell types characterized via in situ here compare to the relative proportions of clusters obtained? It does not correspond to the percentages of the clusters captured (although this should be quantified in a similar manner in order to make this comparison direct: 10,686/20,478 = ~50% vs. 7%), how do you interpret this discrepancy? While this is mentioned in the discussion, there is no sufficient postulation as to why you have an overabundance of the stem cells compared to their presence in the tissue. While it is true that you could have a negative selection of some cell types, for example as stated the size of the penetration glands exceeds both that of the 10x capabilities (40uM), and the 30uM filters used in the protocol, this does not really address why over half of the captured cells represent 'stem cells'. A more realistic interpretation would be biological rather than merely technical. For example, while the composition of the muscle cells and the number of muscle transcriptomes captured are quite congruent at ~20%, the organism is composed of more than 50% of neurons, but only 15% of the transcriptomic states are assigned to neuronal. Could it be that a large fraction of the stem cells are actually neural progenitors? Are there other large inconsistencies between the cluster sizes and the fraction of expected cells? Could you look specifically at early transcription factors that are found in the neurons (or other cell types) within the various stem cell populations to help further refine the precursor/cell type relationships?

Yes, it is really interesting that more than 50% of cells in the animal are neurons whereas more than 50% of cells in scRNAseq data are stem cells. This dataset provides a unique opportunity to compare tissue composition in the whole animal to the corresponding single cell RNAseq dataset.

The table (in Supplementary Table 17) shows the percentage of cells from each tissue type in the miracidium (identified via in situ hybridisation of tissue-type marker genes) and in the scRNAseq to understand this phenomenon.

This table shows that the single cell protocol used in this study negatively selected for nerves and tegument, and positively selected for stem and parenchyma. The composition of the muscle and protonephridia cells and the number of muscle and protonephridia transcriptomes captured are quite congruent.

This technical finding is also biologically consistent. For instance, the tegument cells span the body wall muscles, with the cell bodies below and a syncytial layer above. It is not known how the tegument fragments during the dissociation process, and which parts of the cells get packaged by the 10X GEMs. Because of tegumental structure, the cells are likely prone to damage, and therefore we speculate that is why the tegument cells are under-represented in our 10X data. Unusually shaped fragments may not have been captured in 10X GEMs and of those that were, damaged or distressed tegument cells/fragments may have been excluded post-sequencing, by QC filters including cell calling, mitochondrial percentage and low transcript count (e.g. if there there was a tegumental fragment with 100 transcripts it would have not passed QC). Stem cells are spherical with a large nucleus:cytoplasm ratio, likely making them more robust during dissociation and more likely to be captured in 10X GEMs.

We don’t think that a large fraction of the stem cells are actually neural progenitors because:

(1) we used previously reported marker genes of different tissue types to identify the single cell RNAseq clusters, e.g. Ago2-1 for stem cells, which has been used in multiple life stages.

(2) The stem cell transcriptomes express many previously reported stem cell marker genes.

(3) We found that the stem cells from the single cell data generally had higher numbers of transcripts than the other cell types which is consistent with the Wang et al. 2013 observation that RNA marker POPO-1 could distinguish germinal (stem) cells from other cell types as they are RNA rich.

(4) We also found higher numbers of ribosomal related transcripts in our stem cell transcriptomes, which is consistent with Pan’s observation that part of the distinct morphology of stem cells is densely packed ribosomes in the cytoplasm.

In order to elaborate on this discussion we have generated new visualisations:

(1) A UMAP of the stem cell marker ago2-1 (Supplementary figure 10), to further illustrate our evidence in classifying the stem cell clusters

(2) A co-expression plot of the stem cell marker ago2-1 with neural marker complexin to confirm that there is little coexpression (the most coexpression being in Neuron 1 and Stem F). We identified that 15.56% of cells in the Stem F cluster show some expression of complexin (neural marker), suggesting that a small fraction of Stem F may be early/precursor neurons, but the gene expression indicates that the majority of cells in Stem F are more likely to be stem cells than any other tissue type. There is little to no complexin expression in the other stem clusters.

(3) Expression plots of the 5 neurogenins (TFs involved in neuronal differentiation) we could identify using WormBase ParaSite in these data. Four of the five showed very little expression, and not in specific clusters. The fifth (Smp_072470) showed slightly more expression, though still sparse, mostly across the stem and neural clusters not enough to indicate that any of the stem clusters are neural progenitors.

Author response image 2.

Coexpression UMAP showing the expression of stem cell marker Ago2-1 and neural marker complexin.

Author response image 3.

UMAPs showing the expression five putative neurogenins of S.mansoni.

Reviewer #2 (Public Review):

Summary:

In this manuscript the authors have generated a single-cell atlas of the miracidium, the first free-living stage of an important human parasite, Schistosoma mansoni. Miracidia develop from eggs produced in the mammalian (human) host and are released into freshwater, where they can infect the parasite's intermediate snail host to continue the life cycle. This study adds to the growing single-cell resources that have already been generated for other life-cycle stages and, thus, provides a useful resource for the field.

Strengths:

Beyond generating lists of genes that are differentially expressed in different cell types, the authors validated many of the cluster-defining genes using in situ hybridization chain reaction. In addition to providing the field with markers for many of the cell types in the parasite at this stage, the authors use these markers to count the total number of various cell types in the organism. Because the authors realized that their cell isolation protocols were biasing the cell types they were sequencing, they applied a second method to help them recover additional cell types.

Schistosomes have ZW sex chromosomes and the authors make the interesting observation that the stem cells at this stage are already expressing sex (i.e. W)-specific genes.

Weaknesses:

The sample sizes upon which the in situ hybridization results and cell counts are based are either not stated (in most cases) or are very small (n=3). This lack of clarity about biological replicates and sample sizes makes it difficult for the reader to assess the robustness of the results and the extremely small sample sizes (when provided) are a missed opportunity to explore the variability of the system, or lack thereof.

We have now added more details about the methods we used for validating cell type marker genes by in situ hybridisation. We have added to the methods that ‘We carried out at least three in situ hybridisation experiments for each marker gene we validated (each experiment was a biological replicate). From each experiment we imaged (by confocal microscopy) at least 10 miracidia (technical replicates) per marker gene experiment.’ on line 1036.

In the figure legends we have added the number of miracidia that were screened, and documented the percentage of the screened larvae that showed the in situ gene expression pattern that is seen in the images in the figures, and that we described in the text.

We manually segmented the nuclei of pan tissue marker genes, and we did this for one miracidium in the case of all tissues, except stem cells where we segmented stem cells in five larvae. Manual segmentation of gene expression in a confocal z-stack is very time consuming. We consider that the variability of different cell and tissue types (stereotypy) between miracidia is beyond the scope of this paper and can be investigated in future work.

Although assigning transcripts to a given cell type is usually straightforward via in situ experiments, the authors fail to consider the potential difficulty of assigning the appropriate nuclei to cells with long cytoplasmic extensions, like neurons. In the absence of multiple markers and a better understanding of the nervous system, it seems likely that the authors have overestimated the number of neurons and misassigned other cell types based on their proximity to neural projections.

This is a valid point, and we acknowledge the difficulties of assigning a nucleus to a cell using mRNA expression only and in the absence of a cell membrane marker. We tried to address this issue by labelling the cell membranes using an antibody against beta catenin after the HCR in situ protocol. This method has been used successfully on sections on slides (Schulte et al., 2024), but we failed to get usable results in our miracidia whole-mounts. The beta catenin localisation marked the membranes of the gland cells but didn’t do the same for the neurons or other cell types (see image below).

Author response image 4.

Image showing a maximum intensity projection of a subvolume of a confocal z-stack of a miracidia wholemount in situ hybridisation (by HCR) for paramyosin counterstained with a beta catenin antibody (1:600 concentration of Sigma C2206). The cell membrane of a lateral gland is clearly labelled, but those of the neurons of the brain and the paramyosin+ muscle cells are not.

Our observation that 57% of the cells in a miracidium are nerves is high compared to the C.elegans hermaphrodite adult in which 302 out of 959 cells are neurons (Hobert et al., 2016), few studies have equivalent data with which to make comparisons. Despite this, and the limitation described above, we believe that we have not overestimated the number of neural cells. During the process of validating the marker genes and closely examining gene expression in hundreds of miracidia, we noted that the nuclei of different tissue types are distinct and recognisable (see figure below). The nuclei of stem, tegument and parenchymal cells are comparatively large and spherical with obvious nucleoli (i). The four nuclei of the apical gland cell are angular, pentagonal in shape and sit adjoining each other (inside red dashed circle, i-iii), those of the two lateral glands are bilaterally symmetrical and surrounded by flask shaped cytoplasm (arrows, iv). The nuclei of the body wall muscle cells are peripheral and flattened on the outer edge (iii). The notum+ muscle cell nuclei are anterior of the apical gland (manuscript Figure 2E). The only other two tissue types are the nerves and protonephridia, and their nuclei are smaller and more compact/condensed. In situ expression of the protonephridia marker suggests that 6 cells make up the protonephridial system (manuscript Figure 4 B&E). Therefore, by process of elimination, the remaining nuclei should belong to neurons. The complexin expression pattern supports this and we counted 209 nuclei that were surrounded by cpx transcript expression. To help the reader interpret this for themselves we have added confocal z-stacks of miracidia where tissue level markers have been multiplexed (supplementary videos 18-20). We counted all tissue type cells individually and the tissue type cell numbers added up to the overall cell count.

Author response image 5.

Image showing the diversity of nucleus morphology between tissue types in the miracidium.

Biologically, it is not surprising that this larva is dominated by neural cells. It must navigate a complex aquatic environment and identify a suitable mollusc host in less than 12 hours. It is a non-feeding vehicle that must deliver the stem cells to a suitable environment where they can develop into the subsequent life cycle stage. Accordingly, the cell type composition reflects this challenge.

The conclusion that germline genes are expressed in the miracidia stem cells seems greatly overstated in the absence of any follow-up validation. The expression scales for genes like eled and boule are more than 3 orders of magnitude smaller than those used for any of the robustly expressed genes presented throughout the paper. These scales are undefined, so it isn't entirely clear what they represent, but neither of these genes is detected at levels remotely high (or statistically significant) enough to survive filters for cluster-defining genes.

Given that germ cells often develop early in embryogenesis and arrest the cell cycle until later in development, and that these transcripts reveal no unspliced forms, it seems plausible that the authors are detecting some maternally supplied transcripts that have yet to be completely degraded.

We agree that the expression of genes such as eled and boule are low. We made this clear in the figure legends and text, and have now added scale information to the figure legends. We did not explore these genes as cluster-defining genes, partly due to their comparatively low levels of expression, but as genes already reported to be important in germ line specification. We found the expression of these genes to be consistent with our hypothesis that the Kappa stem cells may include germ line segregated cells, but our hypothesis does not rest on these lower-expressed genes.

It is certainly possible that we have detected some maternally supplied transcripts in the miracidia stem cells. However experiments to distinguish between zygotic and maternal transcripts using metabolic labelling of zygotic transcripts (e.g. Fishman et al. 2023) would be hard in this species due to the hard egg capsule and its ectolethical embryogenesis. Therefore this is out of scope for this work, but this would be a very interesting topic to follow up on and develop tools for.

We have added these sentences to the Discussion ln 746 ‘Intriguingly, the presence of spliced-only copies of the germline defining genes eled and boule could suggest that they are maternal transcripts that have been restricted to the primordial germ cells during embryogenesis, as is the case in Zebrafish embryos (Fishman et al., 2023). An alternative explanation is that unspliced transcripts exist for these lowly expressed genes but their abundance was below our threshold for detection.’

Reviewer #1 (Recommendations For The Authors):

Ln 138: specify the version of Seurat used, and reference the primary papers for this software. Also, from the dot plot shown here, these do not all appear to be supported by unique gene sets. How was the final clustering determined? This information is in the methods section, but a summary here could make it more robust for the readership.

In addition to the details in the methods section, we have added the version and referenced the version-specific primary paper for Seurat when it is first mentioned. We have also summarised the methods used to select the final clustering when we first present the results to aid in clarity.

We added to line 140 ‘Using Seurat (version 4.3.0) (Hao et al., 2021), 19 distinct clusters of cells were identified, along with putative marker genes best able to discriminate between the populations (Figure 1C & D and Supplementary Table 2 and 3). We used Seurat’s JackStraw and ElbowPlot, along with molecular cross-validation to select the number of principal components, and Seurat’s clustree to select a resolution where clusters were stable (Hao et al., 2021).’

Ln 147: isn't seven stem cell clusters a lot? See comment in public review.

We did not have preconceived expectations of the number of stem cell clusters, and were guided by the data and gene expression. In doing so we also discovered that four of those clusters were likely only two ‘biologically or functionally distinct’ clusters, but these split into four clusters based on the expression of genes on the sex-specific regions of the chromosomes, which was both unexpected and interesting.

Figure 1D: gene model names are un-informative for the general reader. Can you provide any putative gene identities here to render this plot interpretable? For example in the main text you state that Smp-085540 is paramyosin; please use this annotation in all your visual material (as is used in Figure 2A).

We have added gene names to the dotplots in all figures with the locus identifier (minus the ‘Smp’ prefix) in brackets after the gene name.

Ln 191:196 Identification of the two muscle clusters as circular and longitudinal muscles is very well supported. However, it would be interesting to look specifically at the genes that are different here. Did the authors attempt to specifically pull out genes differentially expressed between these two groups, or only examine the output of FindAllMarkers at this point?

We did indeed look specifically for genes differentially expressed between the muscle clusters, the results of which can be found in Supplementary Table 5 (Line 206). This analysis revealed “Wnt-11-1 (circular) and MyoD (longitudinal) were among the most differentially expressed genes”, which were important findings in our understanding of the muscle cells in the miracidium.

Ln 207: "connected to stem F" - does this refer specifically to their relative positions on the UMAP in Figure 1C? One must be very careful about these types of statements, as the relative position of cells on a reduced-dimension cell map can be misleading (public review).

We agree, and have rephrased accordingly.

Ln 209:211: Here the authors switch from Seurat (R) as an analysis package, to SAM (python) for subset analysis of one large neural cluster. The results indicate that there may be small populations of transcriptomically distinct neural subtypes also within the neural1 cluster, but that the vast majority of these cells do not express unique transcriptomic profiles. Also in the supplementary material for this (SF1) there is a question of whether or not there is any clustering according to batch effects.

In general, I find the neuronal section a little difficult to follow and it is unclear how many unique profiles are present and which are documented with in situ. I would recommend re-running the analysis on the entire neural subset (n1:5: complexin positive) and generating an inventory of putatively unique neural states with the associated in situ validation altogether in a main figure.

In response to comments above we have both clarified our reasoning for using SAM analysis, and presented more details on possible batch effects. We have gone through the neural system results in order to make it clearer for the reader to follow.

Ln 236: here the authors introduce a STRING analysis for the first time. Also, this method requires some introduction for the general audience in terms of its goals and general functionality and output.

We used STRING analysis on some well defined clusters to provide additional clues about function. At the first mention of STRING (neuron 3 results) we have added the following statement to give more introduction to the reader: “STRING analysis of the top 100 markers of Neuron 3 predicted two protein interaction networks with functional enrichment: ….”

Ln. 280:281. It is unclear why Steger et al is referenced here. In what way does a description of neural and glandular cell transcriptomic similarity in a Cnidarian inform your data on a member of the playhelmenthes? (which should also be referenced in the introduction: to which phylogenetic lineage does Schistosoma belong).

We have now added that the Schistosoma belong to the Platyhelminths on the first line of the introduction.

Ln 295 we have added ‘We expected to find a discrete cluster(s) for the penetration glands, and that it would show similarities to the neural clusters (as glandular cells arise from neuroglandular precursor cells in other animals, such as the sea anemone, Nematostella vectensis, Steger et al., 2022).’

Ln 339: explain the motivation for generating a further plate-based scRNA of the ciliary plates.

We wished to include the ciliary plates alongside the gland cells for plate based RNAseq as they are unique to the miracidium stage and wanted to make sure we had captured them in this study.

Ln 345: Define the tegumental cells for the general reader.

We have added further description on tegument cells in the introduction and tegument results section, e.g. on line 61, 366).

Ln 365: "this cluster" is imprecise. Which cluster are we looking at here?' Also: were flame cells already described morphologically at this stage, or is this the first description of the protonephridial system for this stage of the life cycle?

We have now clarified which cluster we are talking about in the text. The flame cells have been described using TEM before (Pan, 1980).

Stem Cells: also here you refer to cells as 'bridge' which refers to the configuration of the UMAP. While this is likely a biological representation of a different differentiation state, the nomination of this based solely on the UMAP representation should be avoided.

We have rephrased this.

Figure 5B: What is neuron 6? This was Neuron 3 in Figure 1.

Thank you for spotting these mistakes in the labelling, we have corrected them now.

Ln 421:438 - Here you represent a UMAP representation of the cell positions, but state that the clustering disappears. See comment in Public Review.

Modified accordingly, see response in public review.

Ln 472 "Cells in stem E, F, and G in silico clusters might be stressed/damaged/dying cells or cells in transcriptionally transitional states." Is there any evidence supporting either of these conclusions?

We found that 15.56% of the cells in Stem F expressed the neural marker complexin, leading us to consider the possibility that a fraction of these cells may be neural precursors. Stem F also had some cells with a mitochondrial % near the maximum threshold we set, suggesting they could be experiencing some stress. Since we could not identify clear markers for these clusters, their function and a more specific identity, beyond ‘stem’, is not yet known.

That the two stem cell populations contribute to different parts of the next life cycle stage is interesting. The combined analysis suffers from the same issues as the previous analysis in terms of sample distribution; are the 'grey' sporocyst cells also contributing to the stem A/B (kappa) C/D (delta/phi) clusters? This is not possible to tell from the plot as the miracidia may simply be plotted on the top. A different representation of sample contribution to clusters is warranted.

We have made an alternative visualisation here to demonstrate that the miracidia cells are not plotted on top of the sporocyst stem cells. Unfortunately this visual is hampered as there is not a straightforward way to split the panels. In the figure below, the left pane shows the miracidia cells, and the right pane shows the sporocyst cells. Below that, we have included the original figure for comparison. It can be clearly seen that there are three miracidia tegument cells in the sporocyst tegument cluster, and one sporocyst cell in the miracidia stem cells (Stem E), but the miracidia A/B and C/D stem cells are not plotted on top of any sporocyst cells.

Author response image 6.

Methods: Why is the multiplet rate estimate at >50% for the unsorted sample?

We have added more detail on this: “The estimated doublet rate was calculated based on 10X loading guidelines and adjusted for our sample concentrations”.

Reviewer #2 (Recommendations For The Authors):

(1) The manuscript would benefit from a more careful consideration of what was already known based on previous literature, which would help the authors to better put their results in context. For example, previous work suggested that one of the sporocyst stem cell populations (phi) gives rise to tegument and other temporary larval structures; this appears not to be mentioned here. The model in Figure 7 suggests that two of the stem cell populations are gone at day 15 post-infection; the literature shows that those cells can still be detected at this stage (there are just far fewer of them).

We have added the definition of Kappa, Delta and Phi as per Wang et al (2018) in the stem cell results p13 ln 428.

We have amended Figure 7 to include further elements from the Wang et al (2018) paper that show that mother sporocyst stem cells classified as delta and phi are still detectable on day 15 post-infection in mother sporocysts.

We intentionally didn’t put too much emphasis on fitting our data to the model of Wang et al (2018), because a) it’s a different life cycle stage and b) the single cell data the model was based on was from 35 stem cells and gathered using a different method, c) more recent data (Diaz, Attenborough et al. 2024) with 119 stem cells from sporocysts did not recover the same populations of stem cells. We therefore linked our data to previous literature where it was relevant but focused on being led by the data we gathered (>10,000 stem cells).

(2) To add some detail to the public comment about the lack of clarity about sample sizes and biological replicates, and how this leads to questions about the robustness of the results, Figures 4 B and F show the expression pattern for the same parenchyma marker (Smp_318890) in two different samples. The patterns appear quite distinctive. In B, the cell bodies are so clearly labeled that the signal appears oversaturated. In F the cell bodies are barely apparent. Based on the single-cell clustering, it should be possible to distinguish between Parenchyma clusters 1 and 2 based on the levels of this transcript. Careful quantification of signal intensity from multiple samples across multiple experiments might enable the authors to detect such differences.

The reason the expression patterns look different between panels 4Bii and 4F is that in 4Bii we have manually segmented the nuclei of the parenchymal cells in order to count them, whereas in the images in 4F there is no segmentation. We have made this more clear in this legend now, and also in the legends of Figures 2,3, and 5. If there was any signal intensity difference between parenchyma 1 and 2 cells based on expression of the marker gene, Smp_318890, it was not obvious. We carried out 6 experiments for parenchyma markers, multiplexing the pan-parenchyma marker, Smp_318890, with markers for parenchyma 2 but we were unable to distinguish between the two populations.

(3) The authors find that the "somatic" stem cells in miracidia seem to combine attributes of the previously defined delta and phi stem cells from sporocysts. Because the 3 classes of sporocyst stem cells were defined by expression of nanos-2 and fgfrA, using those probes in in-situ experiments could have helped them resolve whether or not the miracidial cells represent precursors that can adopt either fate or if the heterogeneity is already present in miracidia.

In silico expression of the marker genes for the 3 classes of sporocyst stem cells didn’t support those three classes in the miracidia stem cells (See supplementary table 10). We further subclustered the delta/phi cells to see if we could recover separate delta and phi populations but we were unable to do so. We therefore did not pursue in situ experiments of these genes. We instead prioritised cluster-defining genes in the miracidia stem cell populations rather than cluster defining genes in the sporocyst (defined by Wang et al., 2018), but we still explored these in silico. For example, instead of using klf to define Kappa (Wang et al 2018), we used UPPA to validate the Kappa population as it showed similar expression to klf but higher expression levels and was specific to that population. However, like Wang et al 2018, we did use p53, which is a cluster marker of delta and phi in sporocysts, as it showed clear and high expression in our miracidia delta/phi population. We were guided by our data and our knowledge of the literature. More in depth single cell RNAseq is needed from the mother and daughter sporocyst stages to understand the heterogeneity and fates of these stem populations.

(4) Scale bars should be included throughout the figures and the scale should be defined either on the figure or in the legend. Similarly, all the scales used for velocity and expression analysis should be defined.

We have added scale bars to all figures and legends.

The statements “Gene expression has been log-normalised and scaled using Seurat(v. 4.3.0)”, “Gene expression has been normalised (CPM) and log-transformed using scvelo(v. 0.2.4)”, or “Library size was normalised and gene expression values were log-normalised using SAM (v1.0.1) and Scanpy (v1.8.2)” has been added to all figures as appropriate.

(5) The table entitled In situ hybridization probes (Supplementary Table 15) contains no probe sequences, so any interested reader wishing to use these probes would have to design their own. To ensure the reproducibility of the results presented here, the authors should provide the probe sequences they used.

In Supplementary Table 15 we have added the Molecular Instruments Lot number of all the probes used. Anyone wanting to repeat the experiment can order the same probes from the company.

(6) It is unclear how useful the supplemental figures showing the STRING enrichment analyses will be for readers. Unannotated Smp gene identifiers provide no way to help readers digest the information in these hairballs. It would probably be best to replace the Smp names with useful annotations based on their orthologs; if not, these figures could probably be dropped entirely. (Also, the bottom panel of Supplementary Figure 7 has the word "Lorem" embedded on one of the connecting nodes.)

“Lorem” has been removed.

Many of the genes in these analyses do not have short descriptions, therefore we have used Smp gene identifiers in the STRING analysis supplementary figures. These ‘Smp_’ numbers can be used to search WormBase Parasite, where a description can be found and the history of the gene ID traced. This latter function facilitates searching for these genes in the literature and consistency between versions as gene models are updated.

Minor edits

(1) Figures 4A-D aren't cited in the text until after 4E-F are. It seems like moving the section on protonephridial cells (line 364) before the section on tegumental cells (line 345) better reflects the order of the figures.

Thank you for flagging this, we have updated the in-text citations of Figure 4.

(2) In-text references to Sarfati et al, 2021 should be to Nanes Sarfati, as listed in the references. Poteaux et al 2023 is cited in the text, but not in the reference list.

Both of these have been fixed.

eLife assessment

This important work provides evidence that glutamate and GABA are released from different synaptic vesicles at supramammillary axon terminals onto granule cells of the dentate gyrus. The study uses complementary electrophysiological and anatomical experimental approaches. Together, these provide solid evidence that the co-release of glutamate and GABA from different vesicles within the same terminal could modulate granule cell firing in a frequency-dependent manner, although thorough elimination of alternative mechanisms would have strengthened the study. The work will be of interest to neuroscientists investigating co-release of neurotransmitters in various synapses in the brain and those interested in subcortical control of hippocampal function.

Reviewer #1 (Public Review):

This study of mixed glutamate/GABA transmission from axons of the supramammillary nucleus to dentate gyrus seeks to sort out whether the two transmitters are released from the same or different synaptic vesicles. This conundrum has been examined in other dual-transmission cases and even in this particular pathway, there are different views. The authors use a variety of electrophysiological and immunohistochemical methods to reach the surprising (to me) conclusion that glutamate and GABA-filled vesicles are distinct yet released from the same nerve terminals. The strength of the conclusion rests on the abundance of data (approaches) rather than the decisiveness of any one approach, and I came away believing that the boutons may indeed produce and release distinct types of vesicles, but have reservations. Accepting the conclusion, one is now left with another conundrum, not addressed even in the discussion: how can a single bouton sort out VGLUTs and VIAATs to different vesicles, position them in distinct locations with nm precision, and recycle them without mixing? And why do it this way instead of with single vesicles having mixed chemical content? For example, could a quantitative argument be made that separate vesicles allow for higher transmitter concentrations? I feel the paper needs to address these problems with some coherent discussion, at minimum.

Major concerns:

(1) Throughout the paper, the authors use repetitive optogenetic stimulation to activate SuM fibers and co-release glutamate and GABA. There are several issues here: first, can the authors definitively assure the reader that all the short-term plasticity is presynaptic and not due to ChR2 desensitization? This has not been addressed. Second, can the authors also say that all the activated fibers release both transmitters? If for example 20% of the fibers retained a one-transmitter identity and had distinct physiological properties, could that account for some of the physiological findings?

(2) PPR differences in Figures 1F-I are statistically significant but still quite small. You could say they are more similar than different in fact, and residual differences are accounted for by secondary factors like differential receptor saturation.

(3) The logic of the GPCR experiments needs a better setup. I could imagine different fibers released different transmitters and had different numbers of mGluRs, so that one would get different modulations. On the assumption that all the release is from a single population of boutons, then either the mGluRs are differentially segregated within the bouton, or the vesicles have differential responsiveness to the same modulatory signal (presumably a reduced Ca current). This is not developed in the paper.

(4) The biphasic events of Figures 3 and S3: I find these (unaveraged) events a bit ambiguous. Another way to look at them is that they are not biphasic per se but rather are not categorizable. Moreover, these events are really tiny, perhaps generated by only a few receptors whose open probability is variable, thus introducing noise into the small currents.

(5) Figure 4 indicates that the immunohistochemical analysis is done on SuM terminals, but I do not see how the authors know that these terminals come from SuM vs other inputs that converge in DG.

(6) Figure 4E also shows many GluN1 terminals not associated with anything, not even Vglut, and the apparent numbers do not mesh with the statistics. Why?

(7) Do the conclusions based on the fluorescence immuno mesh with the apparent dimensions of the EM active zones and the apparent intermixing of labeled vesicles in immuno EM?

(8) Figure 6 is not so interesting to me and could be removed. It seems to test the obvious: EPSPs promote firing and IPSPs oppose it.

Reviewer #2 (Public Review):

Summary:

In this study, the authors investigated the release properties of glutamate/GABA co-transmission at the supramammillary nucleus (SuM)-granule cell (GC) synapses using in vitro electrophysiology and anatomical approaches at the light and electron microscopy level. They found that SuM to dentate granule cell synapses, which co-release glutamate and GABA, exhibit distinct differences in paired-pulse ratio, Ca2+ sensitivity, presynaptic receptor modulation, and Ca2+ channel-vesicle coupling configuration for each neurotransmitter. The study shows that glutamate/GABA co-release produces independent glutamatergic and GABAergic synaptic responses, with postsynaptic targets segregated. They show that most SuM boutons form distinct glutamatergic and GABAergic synapses in close proximity, characterized by GluN1 and GABAAα1 receptor labeling, respectively. Furthermore, they demonstrate that glutamate/GABA co-transmission exhibits distinct short-term plasticity, with glutamate showing frequency-dependent depression and GABA showing frequency-independent stable depression.

Their findings suggest that these distinct modes of glutamate/GABA co-release by SuM terminals serve as frequency-dependent filters of SuM inputs.

Strengths:

The conclusions of this paper are mostly well supported by the data.

Weaknesses:

Some aspects of Supplementary Figure 1A and the table need clarification. Specifically, the claim that the authors have stimulated an axon fiber rather than axon terminals is not convincingly supported by the diagram of the experimental setup. Additionally, the antibody listed in the primary antibodies section recognizes the gamma2 subunit of the GABAA receptor, not the alpha1 subunit mentioned in the results and Figure 4.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Hirai et al investigated the release properties of glutamate/GABA co-transmission at SuM-GC synapses and reported that glutamate/GABA co-transmission exhibits distinct short-term plasticity with segregated postsynaptic targets. Using optogenetics, whole-cell patch-clamp recordings, and immunohistochemistry, the authors reveal distinct transmission modes of glutamate/GABA co-release as frequency-dependent filters of incoming SuM inputs.

Strengths:

Overall, this study is well-designed and executed; conclusions are supported by the results. This study addressed a long-standing question of whether GABA and glutamate are packaged in the same vesicles and co-released in response to the same stimuli in the SuM-GC synapses (Pedersen et al., 2017; Hashimotodani et al., 2018; Billwiller et al., 2020; Chen et al., 2020; Li et al., 2020; Ajibola et al., 2021). Knowledge gained from this study advances our understanding of neurotransmitter co-release mechanisms and their functional roles in the hippocampal circuits.

Weaknesses:

No major issues are noted. Some minor issues related to data presentation and experimental details are listed below.

eLife assessment

This study provides a novel and valuable alternative explanation for volatility-induced changes in choice behavior, commonly attributed to learning-rate adaptations. Through rigorous and comprehensive computational modeling of previously published data, the authors provide convincing support for the claim that apparent learning-rate adaptations may instead reflect a mixture of decision strategies. Furthermore, they demonstrate that differential weighting of the optimal decision strategy is predicted by psychopathology common to depression and anxiety. This work should be of interest to a wide range of scientists, including psychologists, neuroscientists, computer scientists, and clinicians.

Reviewer #2 (Public Review):

Summary:

Previous research shows that humans tend to adjust learning in environments where stimulus-outcome contingencies become more volatile. This learning rate adaptation is impaired in some psychiatric disorders, such as depression and anxiety. In this tudy the authors reanalyze previously published data on a reversal learning task with two volatility levels. Through a new model they provide some evidence for an alternative explanation whereby the learning rate adaptation is driven by different decision-making strategies and not learning deficits. In particular, they propose that adjusting of learning can be explained by deviations from the optimal decision-making strategy (based on maximizing expected utility) due to response stickiness or focus on reward magnitude. Furthermore, a factor related to general psychopathology of individuals with anxiety and depression negatively correlated with the weight on the optimal strategy and response stickiness, while it correlated positively with the magnitude strategy (a strategy that ignores the probability of outcome).

The main strength of the study is a novel and interesting explanation of an otherwise well-established finding in human reinforcement learning. This proposal is supported by rigorously conducted parameter retrieval and the comparison of the novel model to a wide range of previously published models. The authors explore from many angles, if and why the predictions from the new proposed model are superior to previously applied models.

My previous concerns were addressed in the revised version of the manuscript. I believe that the article now provides a new perspective on a well-established learning effect and offer a novel set of interesting response models that can be applied to a wide array of decision-making problems.

I see two limitations of the study not mentioned in the discussion of the manuscript. First, the task features binary inputs and responses, therefore unexpected uncertainty (volatility) is impossible to differentiate from the uncertainty about outcomes, and exploration is inseparable from random choices. Future work could validate these findings in task designs that allow to distinguish these processes. Second, clinical results are based on a small sample of patients and should be interpreted with this in mind.

Reviewer #3 (Public Review):

Summary:

This paper presents a new formulation of a computational model of adaptive learning amid environmental volatility. Using a behavioral paradigm and data set made available by the authors of an earlier publication (Gagne et al., 2020), the new model is found to fit the data well. The model's structure consists of three weighted controllers that influence decisions on the basis of (1) expected utility, (2) potential outcome magnitude, and (3) habit. The model offers an interpretation of psychopathology-related individual differences in decision-making behavior in terms of differences in the relative weighting of the three controllers.

Strengths:

The newly proposed "mixture of strategies" (MOS) model is evaluated relative to the model presented in the original paper by Gagne et al., 2020 (here called the "flexible learning rate" or FLR model) and two other models. Appropriate and sophisticated methods are used for developing, parameterizing, fitting, and assessing the MOS model, and the MOS model performs well on multiple goodness-of-fit indices. Parameters of the model show decent recoverability and offer a novel interpretation for psychopathology-related individual differences. Most remarkably, the model seems to be able to account for apparent differences in behavioral learning rates between high-volatility and low-volatility conditions even with no true condition-dependent change in the parameters of its learning/decision processes. This finding calls into question a class of existing models that attribute behavioral adaptation to adaptive learning rates.

Weaknesses:

The authors have responded to the weaknesses noted previously.

Author response:

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

Public Reviews:

Reviewer #1:

Point 1.1

Summary: This paper describes a reanalysis of data collected by Gagne et al. (2020), who investigated how human choice behaviour differs in response to changes in environmental volatility. Several studies to date have demonstrated that individuals appear to increase their learning rate in response to greater volatility and that this adjustment is reduced amongst individuals with anxiety and depression. The present authors challenge this view and instead describe a novel Mixture of Strategies (MOS) model, that attributes individual differences in choice behaviour to different weightings of three distinct decision-making strategies. They demonstrate that the MOS model provides a superior fit to the data and that the previously observed differences between patients and healthy controls may be explained by patients opting for a less cognitively demanding, but suboptimal, strategy. 

Strengths: 

The authors compare several models (including the original winning model in Gagne et al., 2020) that could feasibly fit the data. These are clearly described and are evaluated using a range of model diagnostics. The proposed MOS model appears to provide a superior fit across several tests. 

The MOS model output is easy to interpret and has good face validity. This allows for the generation of clear, testable, hypotheses, and the authors have suggested several lines of potential research based on this. 

We appreciate the efforts in understanding our manuscript. This is a good summary.

Point 1.2

The authors justify this reanalysis by arguing that learning rate adjustment (which has previously been used to explain choice behaviour on volatility tasks) is likely to be too computationally expensive and therefore unfeasible. It is unclear how to determine how "expensive" learning rate adjustment is, and how this compares to the proposed MOS model (which also includes learning rate parameters), which combines estimates across three distinct decision-making strategies. 

We are sorry for this confusion. Actually, our motivation is that previous models only consider the possibility of learning rate adaptation to different levels of environmental volatility. The drawback of previous computational modeling is that they require a large number of parameters in multi-context experiments. We feel that learning rate adaptation may not be the only mechanisms or at least there may exist alternative explanations. Understanding the true mechanisms is particularly important for rehabilitation purposes especially in our case of anxiety and depression. To clarify, we have removed all claims about the learning rate adaptation is “too complex to understand”.

Point 1.3

As highlighted by the authors, the model is limited in its explanation of previously observed learning differences based on outcome value. It's currently unclear why there would be a change in learning across positive/negative outcome contexts, based on strategy choice alone. 

Thanks for mentioning this limitation. We want to highlight two aspect of work.

First, we developed the MOS6 model primarily to account for the learning rate differences between stable and volatile contexts, and between healthy controls and patients, not for between positive and negative outcomes. In the other words, our model does not eliminate the possibility of different learning rate in positive and negative outcomes.

Second, Figure 3A shows that FLR (containing different learning parameters for positive/negative outcomes) even performed worse than MOS6 (setting identical learning rate for positive/negative outcomes). This result question whether learning rate differences between positive/negative outcomes exist in our dataset.

Action: We now include this limitation in lines 784-793 in discussion:

“The MOS model is developed to offer context-free interpretations for the learning rate differences observed both between stable and volatile contexts and between healthy individuals and patients. However, we also recognize that the MOS account may not justify other learning rate effects based solely on strategy preferences. One such example is the valence-specific learning rate differences, where learning rates for better-than-expected outcomes are higher than those for worse-than-expected outcomes (Gagne et al., 2020). When fitted to the behavioral data, the context-dependent MOS22 model does not reveal valence-specific learning rates (Supplemental Note 4). Moreover, the valence-specific effect was not replicated in the FLR22 model when fitted to the synthesized data of MOS6.”

Point 1.4

Overall the methods are clearly presented and easy to follow, but lack clarity regarding some key features of the reversal learning task.

Throughout the method the stimuli are referred to as "right" and "left". It's not uncommon in reversal learning tasks for the stimuli to change sides on a trial-by-trial basis or counterbalanced across stable/volatile blocks and participants. It is not stated in the methods whether the shapes were indeed kept on the same side throughout. If this is the case, please state it. If it was not (and the shapes did change sides throughout the task) this may have important implications for the interpretation of the results. In particular, the weighting of the habitual strategy (within the Mixture of Strategies model) could be very noisy, as participants could potentially have been habitual in choosing the same side (i.e., performing the same motor movement), or in choosing the same shape. Does the MOS model account for this? 

We are sorry for the confusion. Yes, two shapes indeed changed sides throughout the task. We replaced the “left” and “right” with “stimulus 1” and “stimulus 2”. We also acknowledge the possibility that participants may develop a habitual preference for a particular side, rather than a shape. Due to the counterbalance design, habitual on side will introduce a random selection noise in choices, which should be captured by the MOS model through the inverse temperature parameter.  

Point 1.5

Line 164: "Participants received points or money in the reward condition and an electric shock in the punishment condition." What determined whether participants received points or money, and did this differ across participants? 

Thanks! We have the design clarified in lines 187-188:

“Each participant was instructed to complete two blocks of the volatile reversal learning task, one in the reward context and the other in the aversive context”,

and in lines:

“A total of 79 participants completed tasks in both feedback contexts. Four participants only completed the task in the reward context, while three participants only completed the aversive task.”

Point 1.6

Line 167: "The participant received feedback only after choosing the correct stimulus and received nothing else" Is this correct? In Figure 1a it appears the participant receives feedback irrespective of the stimulus they chose, by either being shown the amount 1-99 they are being rewarded/shocked, or 0. Additionally, what does the "correct stimulus" refer to across the two feedback conditions? It seems intuitive that in the reward version, the correct answer would be the rewarding stimulus - in the loss version is the "correct" answer the one where they are not receiving a shock? 

Thanks for raising this issue. We removed the term “correct stimulus” and revised the lines 162-166 accordingly:

“Only one of the two stimuli was associated with actual feedback (0 for the other one). The feedback magnitude, ranged between 1-99, is sampled uniformly and independently for each shape from trial to trial. Actual feedback was delivered only if the stimulus associated with feedback was chosen; otherwise, a number “0” was displayed on the screen, signifying that the chosen stimulus returns nothing.”

Point 1.7

Line 176: "The whole experiment included two runs each for the two feedback conditions." Does this mean participants completed the stable and volatile blocks twice, for each feedback condition? (i.e., 8 blocks total, 4 per feedback condition). 

Thanks! We have removed the term “block”, and now we refer to it as “context”. In particular, we removed phrases like “stable block” and “volatile block” and used “context” instead.

Action: See lines 187-189 for the revised version.

“Each participant was instructed to complete two runs of the volatile reversal learning task, one in the reward context and the other in the aversive context. Each run consisted of 180 trials, with 90 trials in the stable context and 90 in the volatile context (Fig. 1B).”

Point 1.8

In the expected utility (EU) strategy of the Mixture or Strategies model, the expected value of the stimulus on each trial is produced by multiplying the magnitude and probability of reward/shock. In Gagne et al.'s original paper, they found that an additive mixture of these components better-captured participant choice behaviour - why did the authors not opt for the same strategy here? 

Thanks for asking this. Their strategy basic means the mixture of PF+MO+HA, where PF stands for the feedback probability (e.g., 0.3 or 0.7) without multiplying feedback magnitude. However, ours are EU+MO+HA, where EU stands for feedback probability x feedback magnitude. We did compare these two strategies and the model using their strategy performed much worse than ours (see the red box below).

Author response image 1.

Thorough model comparison.

Point 1.9

How did the authors account for individuals with poor/inattentive responding, my concern is that the habitual strategy may be capturing participants who did not adhere to the task (or is this impossible to differentiate?). 

The current MOS6 model distinguishes between the HA strategy and the inattentive response. Due to the counterbalance design, the HA strategy requires participants to actively track the stimuli on the screen. In contrast, the inattentive responding, like the same motor movement mentioned in Point 1.4, should exhibit random selection in their behavioral data, which should be account by the inverse temperature parameter.

Point 1.10

The authors provide a clear rationale for, and description of, each of the computational models used to capture participant choice behaviour. 

• Did the authors compare different combinations of strategies within the MOS model (e.g., only including one or two strategies at a time, and comparing fit?) I think more explanation is needed as to why the authors opted for those three specific strategies. 

We appreciate this great advice. Following your advice, we conducted a thorough model comparisons. Please refer to Figure R1 above. The detailed text descriptions of all the models in Figure R1 are included in Supplemental Note 1.

Point 1.11

Please report the mean and variability of each of the strategy weights, per group. 

Thanks. We updated the mean of variability of the strategies in lines 490-503:

“We first focused on the fitted parameters of the MOS6 model. We compared the weight parameters (, , ) across groups and conducted statistical tests on their logits (, , ). The patient group showed a ~37% preference towards the EU strategy, which is significantly weaker than the ~50% preference in healthy controls (healthy controls’ : M = 0.991, SD = 1.416; patients’ : M = 0.196, SD = 1.736; t(54.948) = 2.162, p = 0.035, Cohen’s d = 0.509; Fig. 4A). Meanwhile, the patients exhibited a weaker preference (~27%) for the HA strategy compared to healthy controls (~36%) (healthy controls’ : M = 0.657,  SD = 1.313; patients’ : M = -0.162, SD = 1.561; t(56.311) = 2.455, p = 0.017, Cohen’s d = 0.574), but a stronger preference for the MO strategy (36% vs. 14%; healthy controls’ : M = -1.647,  SD = 1.930; patients’ : M = -0.034, SD = 2.091; t(63.746) = -3.510, p = 0.001, Cohen’s d = 0.801). Most importantly, we also examined the learning rate parameter in the MOS6 but found no group differences (t(68.692) = 0.690, p = 0.493, Cohen’s d = 0.151). These results strongly suggest that the differences in decision strategy preferences can account for the learning behaviors in the two groups without necessitating any differences in learning rate per se.”

Point 1.12

The authors compare the strategy weights of patients and controls and conclude that patients favour more simpler strategies (see Line 417), based on the fact that they had higher weights for the MO, and lower on the EU.

(1) However, the finding that control participants were more likely to use the habitual strategy was largely ignored. Within the control group, were the participants significantly more likely to opt for the EU strategy, over the HA? 2) Further, on line 467 the authors state "Additionally, there was a significant correlation between symptom severity and the preference for the HA strategy (Pearson's r = -0.285, p = 0.007)." Apologies if I'm mistaken, but does this negative correlation not mean that the greater the symptoms, the less likely they were to use the habitual strategy?

I think more nuance is needed in the interpretation of these results, particularly in the discussion. 

Thanks. The healthy participants seemed more likely to opt for the EU strategy, although this difference did not reach significance (paired-t(53) = 1.258, p = 0.214, Cohen’s d = 0.242). We systematically explore the role of HA. Compared to the MO, the HA saves cognitive resources but yields a significantly higher hit rate (Fig. 4A). Therefore, a preference for the HA over the MO strategy may reflect a more sophisticated balance between reward and complexity within an agent: when healthier subjects run out of cognitive resources for the EU strategy, they will cleverly resort to the HA strategy, adopting a simpler strategy but still achieving a certain level of hit rate. This explains the negative symptom-HA correlation. As clever as the HA strategy is, it is not surprising that the health control participants opt more for the HA during decision-making.

However, we are cautious to draw strong conclusion on (1) non-significant difference between EU and HA within health controls and (2) the negative symptom-HA correlation. The reason is that the MOS22, the context-dependent variant, 1) exhibited a significant higher preference for EU over HA (paired-t(53) = 4.070, p < 0.001, Cohen’s d = 0.825) and 2) did not replicate this negative correlation (Supplemental Information Figure S3).

Action: Simulation analysis on the effects of HA was introduced in lines 556-595 and Figure 4. We discussed the effects of HA in lines 721-733:

“Although many observed behavioral differences can be explained by a shift in preference from the EU to the MO strategy among patients, we also explore the potential effects of the HA strategy. Compared to the MO, the HA strategy also saves cognitive resources but yields a significantly higher hit rate (Fig. 4A). Therefore, a preference for the HA over the MO strategy may reflect a more sophisticated balance between reward and complexity within an agent (Gershman, 2020): when healthier participants exhaust their cognitive resources for the EU strategy, they may cleverly resort to the HA strategy, adopting a simpler strategy but still achieving a certain level of hit rate. This explains the stronger preference for the HA strategy in the HC group (Fig. 3A) and the negative correlation between HA preferences and symptom severity  (Fig. 5). Apart from shedding light on the cognitive impairments of patients, the inclusion of the HA strategy significantly enhances the model’s fit to human behavior (see examples in Daw et al. (2011); Gershman (2020); and also Supplemental Note 1 and Supplemental Figure S3).”

Point 1.13

Line 513: "their preference for the slowest decision strategy" - why is the MO considered the slowest strategy? Is it not the least cognitively demanding, and therefore, the quickest? 

Sorry for the confusion. In Fig. 5C, we conducted simulations to estimate the learning speed for each strategy. As shown below, the MO strategy exhibits a flat learning curve. Our claim on the learning speed was based solely on simulation outcomes without referring to cognitive demands. Note that our analysis did not aim to compare the cognitive demands of the MO and HA strategies directly.

Action: We explain the learning speed of the three strategies in lines 571-581.

Point 1.14

The authors argue that participants chose suboptimal strategies, but do not actually report task performance. How does strategy choice relate to the performance on the task (in terms of number of rewards/shocks)? Did healthy controls actually perform any better than the patient group? 

Thanks for the suggestion. The answers are: 1) EU is the most rewarding > the HA > the MO (Fig. 5A), and 2) yes healthy controls did actually perform better than patients in terms of hit rate (Fig. 2).

Action: We included additional sections on above analyses in lines 561-570 and lines 397-401.

Point 1.15

The authors speculate that Gagne et al. (2020) did not study the relationship between the decision process and anxiety and depression, because it was too complex to analyse. It's unclear why the FLR model would be too complex to analyse. My understanding is that the focus of Gagne's paper was on learning rate (rather than noise or risk preference) due to this being the main previous finding. 

Thanks! Yes, our previous arguments are vague and confusing. We have removed all this kind of arguments.

Point 1.16

Minor Comments: 

• Line 392: Modeling fitting > Model fitting 

• Line 580 reads "The MO and HA are simpler heuristic strategies that are cognitively demanding."

- should this read as less cognitively demanding? 

• Line 517: health > healthy 

• Line 816: Desnity > density 

Sorry for the typo! They have all been fixed.

Reviewer #2:

Point 2.1

Summary: Previous research shows that humans tend to adjust learning in environments where stimulus-outcome contingencies become more volatile. This learning rate adaptation is impaired in some psychiatric disorders, such as depression and anxiety. In this study, the authors reanalyze previously published data on a reversal-learning task with two volatility levels. Through a new model, they provide some evidence for an alternative explanation whereby the learning rate adaptation is driven by different decision-making strategies and not learning deficits. In particular, they propose that adjusting learning can be explained by deviations from the optimal decision-making strategy (based on maximizing expected utility) due to response stickiness or focus on reward magnitude. Furthermore, a factor related to the general psychopathology of individuals with anxiety and depression negatively correlated with the weight on the optimal strategy and response stickiness, while it correlated positively with the magnitude strategy (a strategy that ignores the probability of outcome). 

Thanks for evaluating our paper. This is a good summary.

Point 2.2

My main concern is that the winning model (MOS6) does not have an error term (inverse temperature parameter beta is fixed to 8.804). 

(1) It is not clear why the beta is not estimated and how were the values presented here chosen. It is reported as being an average value but it is not clear from which parameter estimation. Furthermore, with an average value for participants that would have lower values of inverse temperature (more stochastic behaviour) the model is likely overfitting.

(2) In the absence of a noise parameter, the model will have to classify behaviour that is not explained by the optimal strategy (where participants simply did not pay attention or were not motivated) as being due to one of the other two strategies.

We apologize for any confusion caused by our writing. We did set the inverse temperature as a free parameter and quantitatively estimate it during the model fitting and comparison. We also created a table to show the free parameters for each models. In the previous manuscript, we did mention “temperature parameter beta is fixed to 8.804”, but only for the model simulation part, which is conducted to interpret some model behaviors.

We agree with the concern that using the averaged value over the inverse temperature could lead to overfitting to more stochastic behaviors. To mitigate this issue, we now used the median as a more representative value for the population during simulation. Nonetheless, this change does not affect our conclusion (see simulation results in Figures 4&6).

Action: We now use the term “free parameter” to emphasize that the inverse temperature was fitted rather than fixed. We also create a new table “Table 1”  in line 458 to show all the free parameters within a model. We also update the simulation details in lines 363-391 for more clarifications.

Point 2.3

(3) A model comparison among models with inverse temperature and variable subsets of the three strategies (EU + MO, EU + HA) would be interesting to see. Similarly, comparison of the MOS6 model to other models where the inverse temperature parameter is fixed to 8.804).

This is an important limitation because the same simulation as with the MOS model in Figure 3b can be achieved by a more parsimonious (but less interesting) manipulation of the inverse temperature parameter.

Thanks, we added a comparison between the MOS6 and the two lesion models (EU + MO, EU + HA). Please refer to the figure below and Point 1.8.

We also realize that the MO strategy could exhibit averaged learning curves similar to random selection. To confirm that patients' slower learning rates are due to a preference for the MO strategy, we compared the MOS6 model with a variant (see the red box below) in which the MO strategy is replaced by Random (RD) selection that assigns a 0.5 probability to both choices. This comparison showed that the original MOS6 model with the MO strategy better fits human data.

Author response image 2.

Point 2.4

Furthermore, the claim that the EU represents an optimal strategy is a bit overstated. The EU strategy is the only one of the three that assumes participants learn about the stimulus-outcomes contingencies. Higher EU strategy utilisation will include participants that are more optimal (in maximum utility maximisation terms), but also those that just learned better and completely ignored the reward magnitude.

Thank you for your feedback. We have now revised the paper to remove all statement about “EU strategy is the optimal” and replaced by “EU strategy is rewarding but complex”. We agree that both the EU strategy and the strategy only focusing on feedback probability (i.e., ignoring the reward magnitude, refer to as the PF strategy) are rewarding but complex beyond two simple heuristics. We also included the later strategy in our model comparisons (see the next section Point 2.5).

Point 2.5

The mixture strategies model is an interesting proposal, but seems to be a very convoluted way to ask: to what degree are decisions of subjects affected by reward, what they've learned, and response stickiness? It seems to me that the same set of questions could be addressed with a simpler model that would define choice decisions through a softmax with a linear combination of the difference in rewards, the difference in probabilities, and a stickiness parameter. 

Thanks for suggesting this model. We did include the proposed linear combination models (see “linear comb.” in the red box below) and found that it performed significantly worse than the MOS6.

Action: We justified our model selection criterion in the Supplemental Note 1.

Author response image 3.

Point 2.6

Learning rate adaptation was also shown with tasks where decision-making strategies play a less important role, such as the Predictive Inference task (see for instance Nassar et al, 2010). When discussing the merit of the findings of this study on learning rate adaptation across volatility blocks, this work would be essential to mention. 

Thanks for mentioning this great experimental paradigm, which provides an ideal solution for disassociating the probability learning and decision process. We have discussed about this paradigm as well as the associated papers in discussion lines 749-751, 763-765, and 796-801.

Point 2.7

Minor mistakes that I've noticed:

Equation 6: The learning rate for response stickiness is sometimes defined as alpha_AH or alpha_pi.

Supplementary material (SM) Contents are lacking in Note1. SM talks about model MOS18, but it is not defined in the text (I am assuming it is MOS22 that should be talked about here).

Thanks! Fixed.

Reviewer #3:

Point 3.1

Summary: This paper presents a new formulation of a computational model of adaptive learning amid environmental volatility. Using a behavioral paradigm and data set made available by the authors of an earlier publication (Gagne et al., 2020), the new model is found to fit the data well. The model's structure consists of three weighted controllers that influence decisions on the basis of (1) expected utility, (2) potential outcome magnitude, and (3) habit. The model offers an interpretation of psychopathology-related individual differences in decision-making behavior in terms of differences in the relative weighting of the three controllers.

Strengths: The newly proposed "mixture of strategies" (MOS) model is evaluated relative to the model presented in the original paper by Gagne et al., 2020 (here called the "flexible learning rate" or FLR model) and two other models. Appropriate and sophisticated methods are used for developing, parameterizing, fitting, and assessing the MOS model, and the MOS model performs well on multiple goodness-of-fit indices. The parameters of the model show decent recoverability and offer a novel interpretation for psychopathology-related individual differences. Most remarkably, the model seems to be able to account for apparent differences in behavioral learning rates between high-volatility and low-volatility conditions even with no true condition-dependent change in the parameters of its learning/decision processes. This finding calls into question a class of existing models that attribute behavioral adaptation to adaptive learning rates. 

Thanks for evaluating our paper. This is a good summary.

Point 3.2<br /> (1) Some aspects of the paper, especially in the methods section, lacked clarity or seemed to assume context that had not been presented. I found it necessary to set the paper down and read Gagne et al., 2020 in order to understand it properly.

(3) Clarification-related suggestions for the methods section: <br /> - Explain earlier that there are 4 contexts (reward/shock crossed with high/low volatility). Lines 252-307 contain a number of references to parameters being fit separately per context, but "context" was previously used only to refer to the two volatility levels. 

Action: We have placed the explanation as well as the table about the 4 contexts (stable-reward/stable-aversive/volatile-reward/volatile-aversive) earlier in the section that introduces the experiment paradigm (lines 177-186):

“Participants was supposed to complete this learning and decision-making task in four experimental contexts (Fig. 1A), two feedback contexts (reward or aversive)  two volatility contexts (stable or volatile). Participants received points in the reward context and an electric shock in the aversive context. The reward points in the reward context were converted into a monetary bonus by the end of the task, ranging from £0 to £10. In the stable context, the dominant stimulus (i.e., a certain stimulus induces the feedback with a higher probability) provided a feedback with a fixed probability of 0.75, while the other one yielded a feedback with a probability of 0.25. In the volatile context, the dominant stimulus’s feedback probability was 0.8, but the dominant stimulus switched between the two every 20 trials. Hence, this design required participants to actively learn and infer the changing stimulus-feedback contingency in the volatile context.”

- It would be helpful to provide an initial outline of the four models that will be described since the FLR, RS, and PH models were not foreshadowed in the introduction. For the FLR model in particular, it would be helpful to give a narrative overview of the components of the model before presenting the notation. 

Action: We now include an overview paragraph in the section of computation model to outline the four models as well as the hypotheses constituted in the model (lines 202-220).  

- The subsection on line 343, describing the simulations, lacks context. There are references to three effects being simulated (and to "the remaining two effects") but these are unclear because there's no statement in this section of what the three effects are.

- Lines 352-353 give group-specific weighting parameters used for the stimulations of the HC and PAT groups in Figure 4B. A third, non-group-specific set of weighting parameters is given above on lines 348-349. What were those used for?

- Line 352 seems to say Figure 4A is plotting a simulation, but the figure caption seems to say it is plotting empirical data. 

These paragraphs has been rewritten and the abovementioned issues have been clarified. See lines 363-392.

Point 3.2

(2) There is little examination of why the MOS model does so well in terms of model fit indices. What features of the data is it doing a better job of capturing? One thing that makes this puzzling is that the MOS and FLR models seem to have most of the same qualitative components: the FLR model has parameters for additive weighting of magnitude relative to probability (akin to the MOS model's magnitude-only strategy weight) and for an autocorrelative choice kernel (akin to the MOS model's habit strategy weight). So it's not self-evident where the MOS model's advantage is coming from.

An intuitive understanding of the FLR model is that it estimates the stimuli value through a linear combination of probability feedback (PF, )and (non-linear) magnitude .See equation:

Also, the FLR model include the mechanisms of HA as:

In other words, FLR model considers the mechanisms about the probability of feedback (PF)+MO+HA (see Eq. XX in the original study), but our MOS considers the mechanisms of EU+MO+HA. The key qualitative difference lies between FLR and MOS is the usage of the expected utility formula (EU) instead the probability of feedback (PF). The advantage of our MOS model has been fully evidenced by our model comparisons, indicating that human participants multiply probability and magnitude rather than only considering probability. The EU strategy has also been suggested by a large pile of literature (Gershman et al., 2015; Von Neumann & Morgenstern, 1947).

Making decisions based on the multiplication of feedback probability and magnitude can often yield very different results compared to decisions based on a linear combination of the two, especially when the two magnitudes have a small absolute difference but a large ratio. Let’s consider two cases:

(1) Stimulus 1: vs. Stimulus 2:

(2) Stimulus 1: vs. Stimulus 2:

The EU strategy may opt for stimulus 2 in both cases, since stimulus 2 always has a larger expected value. However, it is very likely for the PF+MO to choose stimulus 1 in the first case. For example, when .  If we want the PF+MO to also choose stimulus to align with the EU strategy, we need to increase the weight on magnitude . Note that in this example we divided the magnitude value by 100 to ensure that probability and magnitude are on the same scale to help illustration.

In the dataset reported by Gagne, 2020, the described scenario seems to occur more often in the aversive context than in the reward context. To accurately capture human behaviors, FLR22 model requires a significantly larger weight for magnitude in the aversive context than in the reward context . Interestingly, when the weights for magnitude in different contexts are forced to be equal, the model (FLR6) fails, exhibiting an almost chance-level performance throughout learning (Fig. 3E, G). In contrast, the MOS6 model, and even the RS3 model, exhibit good performance using one identical set of parameters across contexts. Both MOS6 and RS3 include the EU strategy during decision-making. These findings suggest humans make decisions using the EU strategy rather than PF+MO.

The focus of our paper is to present that a good-enough model can interpret the same dataset in a completely different perspective, not necessarily to explore improvements for the FLR model.

Point 3.3

One of the paper's potentially most noteworthy findings (Figure 5) is that when the FLR model is fit to synthetic data generated by the expected utility (EU) controller with a fixed learning rate, it recovers a spurious difference in learning rate between the volatile and stable environments. Although this is potentially a significant finding, its interpretation seems uncertain for several reasons: 

- According to the relevant methods text, the result is based on a simulation of only 5 task blocks for each strategy. It would be better to repeat the simulation and recovery multiple times so that a confidence interval or error bar can be estimated and added to the figure. 

- It makes sense that learning rates recovered for the magnitude-oriented (MO) strategy are near zero, since behavior simulated by that strategy would have no reason to show any evidence of learning. But this makes it perplexing why the MO learning rate in the volatile condition is slightly positive and slightly greater than in the stable condition. 

- The pure-EU and pure-MO strategies are interpreted as being analogous to the healthy control group and the patient group, respectively. However, the actual difference in estimated EU/MO weighting between the two participant groups was much more moderate. It's unclear whether the same result would be obtained for a more empirically plausible difference in EU/MO weighting. 

- The fits of the FLR model to the simulated data "controlled all parameters except for the learning rate parameters across the two strategies" (line 522). If this means that no parameters except learning rate were allowed to differ between the fits to the pure-EU and pure-MO synthetic data sets, the models would have been prevented from fitting the difference in terms of the relative weighting of probability and magnitude, which better corresponds to the true difference between the two strategies. This could have interfered with the estimation of other parameters, such as learning rate. 

- If, after addressing all of the above, the FLR model really does recover a spurious difference in learning rate between stable and volatile blocks, it would be worth more examination of why this is happening. For example, is it because there are more opportunities to observe learning in those blocks?

I would recommend performing a version of the Figure 5 simulations using two sets of MOS-model parameters that are identical except that they use healthy-control-like and patient-like values of the EU and MO weights (similar to the parameters described on lines 346-353, though perhaps with the habit controller weight equated). Then fit the simulated data with the FLR model, with learning rate and other parameters free to differ between groups. The result would be informative as to (1) whether the FLR model still misidentifies between-group strategy differences as learning rate differences, and (2) whether the FLR model still identifies spurious learning rate differences between stable and volatile conditions in the control-like group, which become attenuated in the patient-like group. 

Many thanks for this great advice. Following your suggestions, we now conduct simulations using the median of the fitted parameters. The representations for healthy controls and patients have identical parameters, except for the three preference parameters; moreover, the habit weights are not controlled to be equal. 20 simulations for each representative, each comprising 4 task sequences sampled from the behavioral data. In this case, we could create error bars and perform statistical tests. We found that the differences in learning rates between stable and volatile conditions, as well as the learning rate adaptation differences between healthy controls and patients, still persisted.

Combined with the discussion in Point 3.2, we justify why a mixture-of-strategy can account for learning rate adaptation as follow. Due to (unknown) differences in task sequences, the MOS6 model exhibits more MO-like behaviors due to the usage of the EU strategy. To capture this behavior pattern, the FLR22 model has to increase its weighting parameter 1-λ for magnitude, which could ultimately drive the FLR22 to adjust the fitted learning rate parameters, exhibiting a learning rate adaptation effect. Our simulations suggest that estimating learning rate just by model fitting may not be the only way to interpret the data.

Action: We included the simulation details in the method section (lines 381-lines 391)

“In one simulated experiment, we sampled the four task sequences from the real data. We simulated 20 experiments with the parameters of to mimic the behavior of the healthy control participants. The first three are the median of the fitted parameters across all participants; the latter three were chosen to approximate the strategy preferences of real health control participants (Figure 4A). Similarly, we also simulated 20 experiments for the patient group with the identical values of , and , but different strategy preferences   . In other words, the only difference in the parameters of the two groups is the switched and . We then fitted the FLR22 to the behavioral data generated by the MOS6 and examined the learning rate differences across groups and volatile contexts (Fig. 6). ”

Point 3.4

Figure 4C shows that the habit-only strategy is able to learn and adapt to changing contingencies, and some of the interpretive discussion emphasizes this. (For instance, line 651 says the habit strategy brings more rewards than the MO strategy.) However, the habit strategy doesn't seem to have any mechanism for learning from outcome feedback. It seems unlikely it would perform better than chance if it were the sole driver of behavior. Is it succeeding in this example because it is learning from previous decisions made by the EU strategy, or perhaps from decisions in the empirical data?

Yes, the intuition is that the HA strategy seems to show no learning mechanism. But in reality, it yields a higher hit rate than MO by simply learning from previous decisions made by the EU strategy. We run simulations to confirm this (Figure 4B).

Point 3.5

For the model recovery analysis (line 567), the stated purpose is to rule out the possibility that the MOS model always wins (line 552), but the only result presented is one in which the MOS model wins. To assess whether the MOS and FLR models can be differentiated, it seems necessary also to show model recovery results for synthetic data generated by the FLR model. 

Sure, we conducted a model recovery analysis that include all models, and it demonstrates that MOS and FLR can be fully differentiated. The results of the new model recovery analysis were shown in Fig. 7.

Point 3.6

To the best of my understanding, the MOS model seems to implement valence-specific learning rates in a qualitatively different way from how they were implemented in Gagne et al., 2020, and other previous literature. Line 246 says there were separate learning rates for upward and downward updates to the outcome probability. That's different from using two learning rates for "better"- and "worse"-than-expected outcomes, which will depend on both the direction of the update and the valence of the outcome (reward or shock). Might this relate to why no evidence for valence-specific learning rates was found even though the original authors found such evidence in the same data set? 

Thanks. Following the suggestion, we have corrected our implementation of valence-specific learning rate in all models (see lines 261-268).

“To keep consistent with Gagne et al., (2020), we also explored the valence-specific learning rate,

is the learning rate for better-than-expected outcome, and for worse-than-expected outcome. It is important to note that Eq. 6 was only applied to the reward context, and the definitions of “better-than-expected” and “worse-than-expected” should change accordingly in the aversive context, where we defined for and for .

No main effect of valence on learning rate was found (see Supplemental Information Note 3)

Point 3.7

The discussion (line 649) foregrounds the finding of greater "magnitude-only" weights with greater "general factor" psychopathology scores, concluding it reflects a shift toward simplifying heuristics. However, the picture might not be so straightforward because "habit" weights, which also reflect a simplifying heuristic, correlated negatively with the psychopathology scores. 

Thanks. In contrast the detrimental effects of “MO”, “habit” is actually beneficial for the task. Please refer to Point 1.12.

Point 3.8

The discussion section contains some pejorative-sounding comments about Gagne et al. 2020 that lack clear justification. Line 611 says that the study "did not attempt to connect the decision process to anxiety and depression traits." Given that linking model-derived learning rate estimates to psychopathology scores was a major topic of the study, this broad statement seems incorrect. If the intent is to describe a more specific step that was not undertaken in that paper, please clarify. Likewise, I don't understand the justification for the statement on line 615 that the model from that paper "is not understandable" - please use more precise and neutral language to describe the model's perceived shortcomings. 

Sorry for the confusion. We have removed all abovementioned pejorative-sounding comments.

Point 3.9

4. Minor suggestions: 

- Line 114 says people with psychiatric illness "are known to have shrunk cognitive resources" - this phrasing comes across as somewhat loaded. 

Thanks. We have removed this argument.

- Line 225, I don't think the reference to "hot hand bias" is correct. I understand hot hand bias to mean overestimating the probability of success after past successes. That's not the same thing as habitual repetition of previous responses, which is what's being discussed here. 

Response: Thanks for mentioning this. We have removed all discussions about “hot hand bias”.

- There may be some notational inconsistency if alpha_pi on line 248 and alpha_HA on line 253 are referring to the same thing. 

Thanks! Fixed!

- Check the notation on line 285 - there may be some interchanging of decimals and commas.

Thanks! Fixed!

Also, would the interpretation in terms of risk seeking and risk aversion be different for rewarding versus aversive outcomes? 

Thanks for asking. If we understand it correctly, risk seeking and risk aversion mechanisms are only present in the RS models, which show clearly worse fitting performance. We thus decide not to overly interpret the fitted parameters in the RS models.

- Line 501, "HA and PAT groups" looks like a typo. 

- In Figure 5, better graphical labeling of the panels and axes would be helpful. 

Response: Thanks! Fixed!

REFERENCES

Daw, N. D., Gershman, S. J., Seymour, B., Dayan, P., & Dolan, R. J. (2011). Model-based influences on humans' choices and striatal prediction errors. Neuron, 69(6), 1204-1215.

Gagne, C., Zika, O., Dayan, P., & Bishop, S. J. (2020). Impaired adaptation of learning to contingency volatility in internalizing psychopathology. Elife, 9.

Gershman, S. J. (2020). Origin of perseveration in the trade-off between reward and complexity. Cognition, 204, 104394.

Gershman, S. J., Horvitz, E. J., & Tenenbaum, J. B. (2015). Computational rationality: A converging paradigm for intelligence in brains, minds, and machines. Science, 349(6245), 273-278.

Von Neumann, J., & Morgenstern, O. (1947). Theory of games and economic behavior, 2nd rev.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

We now further discuss these issues and the perspectives offered by future genomic work on lines 462-485.  

Reviewer #2 (Public Review):

Summary:

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

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

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

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

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

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

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

Strengths:

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

Weaknesses:

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

Our intuition is that ALE in its “dated” version does not necessarily fail on our dataset due to its size: ALE runs, but it provides unrealistic parameter estimates and is not able to output possible reconciliations, as mentioned in our Material and Methods section. We think this issue is mostly due to the fact that there is no pattern of codiversification: the coronavirus and mammal trees are so distinct that finding a reconciliation scenario between these trees with time-consistent switches is very difficult and ALE fails at estimating an amalgamated likelihood for such an unlikely scenario. We now ran the dated version of ALE independently on the smaller alpha and betacoronaviruses datasets. It still fails on the betacoronaviruses dataset.  On the alphacoronaviruses dataset, it does output significant reconciliations, however these reconciliations have a majority of events of transfers and losses, confirming that codiversification is unlikely in this clade.

Reviewer #3 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

We totally agree that sampling biases in the virome of mammals is a prominent issue, which is why we conducted a series of sensitivity analyses to test their effect on our main conclusions. We thoroughly tested the effect of (i) the unequal sampling effort across mammalian species that have been screened and (ii) the unequal screening of mammalian species across the mammalian tree of life by subsampling the data to correct for the unequal sampling effort (see Supporting Information Text). In both cases, we still reported low support for a scenario of codiversification, the origin in bats in East Asia, the preferential host switches within mammalian orders, and the rare spillovers from bats to humans. The robustness of our findings to sampling biases may be explained by the fact that the cophylogenetic approach we used (ALE) explicitly accounts for undersampling by assuming that all host switches involve unsampled intermediate hosts. To address the reviewer's comment, we now better underline the importance of sampling biases in our main text (see Discussion, lines 487-494) with supporting references (note that we did not find the Cohen et al. Nature Comm reference). We also better highlight our sensitivity analyses by moving them from the Supporting Information Text to the main text. 

We agree that distinguishing between alpha and beta coronaviruses provides useful additional insights. We have run separate cophylogenetic analyses for these two sub-clades and now report the results of these additional analyses in the revised manuscript, and put them in context with the existing literature about the two sub-clades.

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

Reviewer #1 (Recommendations For The Authors):

(1) Overall I found this paper to be quite difficult to follow. The text needs clearer structure, which can be helped by writing in shorter paragraphs and adding section headings. For example, there are some very long paragraphs starting on L83, L176, L215, L511, and L598.

We have now added section headings and divided these paragraphs into smaller ones.

(2) It would be helpful to define some of the key terminology relating to the evolutionary interactions between the viruses and their hosts. Some of the terms that are typically used in the context include "coevolution", "cospeciation", "codivergence", and "codiversification". These have different meanings and need to be used carefully. The paper mostly deals with "codivergence" between coronaviruses and their host species.

We now provide a list of definitions in Box S1. These definitions are as in our recent article clarifying the differences between these patterns/processes (Perez-Lamarque & Morlon 2024).

Specific comments

L83-L105: This paragraph can be written more concisely.

We prefer to keep this paragraph like this as it contains key explanations that are necessary for understanding our approach and results.  

Figure 1: The timescales of the trees are rather confusing. The different scales are indicated by the gray shading but this is easy to overlook. Maybe stretching or compressing the trees horizontally would help to emphasise the different timescales.

Done.

Figure 2: Note that the maximum clade credibility tree is a specific tree sampled from the posterior distribution - it is not a consensus tree. In the figure caption, the meaning of "location" is unclear.

We have removed the word “consensus”, thank you for noting this. We have replaced “location” by “branching order”. 

L461: How was the model chosen, and why were different models used in the BEAST and PhyloBayes analyses?

We did our PhyloBayes analyses first and used the LG model following methodology outlined in previous studies using ALE (e.g. Groussin et al. 2017; Dorrell et al. 2021). Unfortunately, the LG model is not available in the default version of BEAST2 so we had to use a different model (the WAG model). We have now run BEAST2 with the LG model (thanks to the BEAST_CLASSIC package) and we obtained very similar results (see Figure below showing the BEAST consensus trees obtained with the WAG or LG models – they only slightly differ by the branching of the u7351 OTU). We have now added this information in the Methods section. 

Author response image 1.

L477: It is not clear to me how the PhyloBayes and BEAST analyses differ. Please expand the explanation of why PhyloBayes was used here.

We have now clarified this (lines 594-597). 

L568: Why not test explicitly for recombination?

We did test for the occurrence of recombination using several approaches, including

OpenRDP (https://github.com/PoonLab/OpenRDP), our own custom code, and Gubbins (Croucher et al. 2015). These tests were however inconclusive, indicating either the absence or presence of recombination, thus suggesting that the palmprint region is too short to infer anything about recombination. We thus do not exclude the possibility that recombination occurred, and test the robustness of our results to recombination by running our analyses on different sub-parts of the palmprint region. We have clarified this in our Material & Methods.

L618: "DNA sequences" -> "RNA sequences"

Done.

The paper contains numerous minor grammatical errors and would benefit from careful proofreading and editing. Please check the use of plurals and apostrophes. Some of the errors are listed below:

L49: "As several" -> "As with several"

Done.

L178: "reconciliates" -> "reconciles"?

Done.

L199: "extent" -> "extant"

Done.

L289: This sentence needs rephrasing to avoid a triple negative ("cannot ... reject ... not present")

Done.

L469: "temporary" -> "temporal"

Done.

L470: "neglectable" -> "negligible"

Done.

L577: "not only relying" -> "not relying only"

Done.

Reviewer #2 (Recommendations For The Authors):

The study is generally well-constructed and its results are convincing. However, considering the availability of a dated host tree, conducting a dated reconciliation analysis could be beneficial. Creating a smaller sub-dataset and performing a dated reconciliation analysis would likely be a valuable addition to the research.

We have now run the dated version of ALE on both the alpha and betacoronaviruses subclades. ALE dated still does not output reconciliations on the betacoronaviruses dataset, but it does on the smaller alphacoronaviruses dataset. We found significant reconciliations, indicating that mammal-alphacoronavirus associations are not random with respect to phylogeny, but the reconciliations involved more host switch and loss events (38 switches + 29 losses) than cospeciation events (65), indicating cophylogenetic signal in the absence of phylogenetic congruence (Perez-Lamarque & Morlon 2024). We now present the results on lines 264-282.  

Reviewer #3 (Recommendations For The Authors):

I think the results are written in a very speculative way, with many sentence fragments that should really be part of the discussion.

We have carefully checked our Results section and rephrased or removed formulation that may have been perceived as speculative.  

There are a lot of considerations in this manuscript about spread and future pandemics, but I think this is very far from the topic of this paper. When we quantified the coevolutionary risk of bats-betacovs in a recent paper (Forero et al. 2024, Virus Evol.), we only briefly touched upon this discussion because we compared our outputs with a measure of human population density. I don't think the manuscript needs to talk about epidemiology at all, and it would probably be more useful as a purely evo-bio piece.

We think that it is useful to discuss the potential implications of our results for future pandemics, even though we agree that this discussion is rather speculative. We have removed the mention of predictions in the Abstract and have softened our wording in the Discussion.  

References:

Croucher, N.J., Page, A.J., Connor, T.R., Delaney, A.J., Keane, J.A., Bentley, S.D., et al. (2015). Rapid phylogenetic analysis of large samples of recombinant bacterial whole genome sequences using Gubbins. Nucleic Acids Res., 43, e15.

Dorrell, R.G., Villain, A., Perez-Lamarque, B., Audren de Kerdrel, G., McCallum, G., Watson, A.K., et al. (2021). Phylogenomic fingerprinting of tempo and functions of horizontal gene transfer within ochrophytes. Proc. Natl. Acad. Sci., 118, e2009974118.

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

Groussin, M., Mazel, F., Sanders, J.G., Smillie, C.S., Lavergne, S., Thuiller, W., et al. (2017).

Unraveling the processes shaping mammalian gut microbiomes over evolutionary time. Nat. Commun., 8, 14319.

Perez-Lamarque, B. & Morlon, H. (2024). Distinguishing cophylogenetic signal from phylogenetic congruence clarifies the interplay between evolutionary history and species interactions. Syst. Biol.

eLife assessment

Maestri et al report the absence of phylogenetic evidence supporting codiversification of mammalian coronaviruses and their hosts, leading to the important conclusion that the evolutionary history of the virus and its hosts are decoupled through frequent host switches. The evidence for frequent host switching, derived from state-of-the-art probabilistic modeling of co-evolution, is convincing. The study adds a new perspective to the ongoing debate over the timescale of coronavirus evolution.

Reviewer #1 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

Reviewer #2 (Public Review):

Summary:

In their study titled "Recent evolutionary origin and localized diversity hotspots of mammalian coronaviruses," authors Benoît Perez-Lamarque, Renan Maestri, Anna Zhukova, and Hélène Morlon investigate the complex evolutionary history of coronaviruses, particularly those affecting mammals, including humans. The study focuses on unraveling the evolutionary trajectory of these viruses, which have shown a high propensity for causing pandemics, as evidenced by the SARS-CoV2 outbreak.<br /> The research addresses a significant gap in our understanding of the evolutionary dynamics of coronaviruses, particularly their history, patterns of host-to-host transmission, and geographical spread. These aspects are important for predicting and managing future pandemic scenarios.

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

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

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

The research also points out the high rates of host-switching within mammalian orders, including between humans, domesticated animals, and non-flying wild mammals.<br /> In conclusion, the study by Perez-Lamarque and colleagues presents an important quantitative advance in our understanding of the evolutionary history of mammalian coronaviruses. It suggests that the long-held belief in extensive virus-host codiversification may have been substantially overestimated, paving the way for a reevaluation of how we understand, predict, and potentially control the spread of these viruses.

Strengths:

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

Weaknesses:

The authors could only use the "undated" model in ALE, with the dated method (which only allows time-consistent transfers) failing on their dataset. The authors did attempt to address this issue in the revision, albeit with limited success.

eLife assessment

In this useful study, the authors tested the ability of bumblebees to use bird-view and ground-view for homing in cluttered landscapes using modeling and behavioral experiments, claiming that bumblebees rely most on ground-views for homing. However, due to a lack of analysis of the bees' behavior during training and a lack of information as to how the homing behavior of bees develops over time, the evidence supporting their claims is currently incomplete. Moreover, there was concern that the experimental environment was not representative of natural scenes, thus limiting the findings of the study.

Reviewer #1 (Public Review):

Summary:

In this paper, the authors aimed to test the ability of bumblebees to use bird-view and ground-view for homing in cluttered landscapes. Using modelling and behavioural experiments, the authors showed that bumblebees rely most on ground-views for homing.

Strengths:

The behavioural experiments are well-designed, and the statistical analyses are appropriate for the data presented. 

Weaknesses:

Views of animals are from a rather small catchment area.

Missing a discussion on why image difference functions were sufficient to explain homing in wasps (Murray and Zeil 2017).

The artificial habitat is not really 'cluttered' since landmarks are quite uniform, making it difficult to infer ecological relevance.

Reviewer #2 (Public Review):

Summary:

In a 1.5m diameter, 0.8m high circular arena bumblebees were accustomed to exiting the entrance to their nest on the floor surrounded by an array of identical cylindrical landmarks and to forage in an adjacent compartment which they could reach through an exit tube in the arena wall at a height of 28cm. The movements of one group of bees were restricted to a height of 30cm, the height of the landmark array, while the other group was able to move up to heights of 80cm, thus being able to see the landmark array from above.

During one series of tests, the flights of bees returning from the foraging compartment were recorded as they tried to reach the nest entrance on the floor of the arena with the landmark array shifted to various positions away from the true nest entrance location. The results of these tests showed that the bees searched for the net entrance in the location that was defined by the landmark array.

In a second series of tests, access to the landmark array was prevented from the side, but not from the top, by a transparent screen surrounding the landmark array. These tests showed that the bees of both groups rarely entered the array from above, but kept trying to enter it from the side.<br /> The authors express surprise at this result because modelling the navigational information supplied by panoramic snapshots in this arena had indicated that the most robust information about the location of the nest entrance within the landmark array was supplied by views of the array from above, leading to the following strong conclusions:<br /> line 51: "Snapshot models perform best with bird's eye views";<br /> line 188: "Overall, our model analysis could show that snapshot models are not able to find home with views within a cluttered environment but only with views from above it.";<br /> line 231: "Our study underscores the limitations inherent in snapshot models, revealing their inability to provide precise positional estimates within densely cluttered environments, especially when compared to the navigational abilities of bees using frog's-eye views."

Strengths:

The experimental set-up allows for the recording of flight behaviour in bees, in great spatial and temporal detail. In principle, it also allows for the reconstruction of the visual information available to the bees throughout the arena.

Weaknesses:

Modelling:<br /> Modelling left out information potentially available to the bees from the arena wall and in particular from the top edge of the arena and cues such as cameras outside the arena. For instance, modelled IDF gradients within the landmark array degrade so rapidly in this environment, because distant visual features, which are available to bees, are lacking in the modelling. Modelling furthermore did not consider catchment volumes, but only horizontal slices through these volumes.

Behavioural analysis:<br /> The full potential of the set-up was not used to understand how the bees' navigation behaviour develops over time in this arena and what opportunities the bees have had to learn the location of the nest entrance during repeated learning flights and return flights.

Without a detailed analysis of the bees' behaviour during 'training', including learning flights and return flights, it is very hard to follow the authors' conclusions. The behaviour that is observed in the tests may be the result of the bees' extended experience shuttling between the nest and the entry to the foraging arena at 28cm height in the arena wall. For instance, it would have been important to see the return flights of bees following the learning flights shown in Figure 17.

Basically, both groups of bees (constrained to fly below the height of landmarks (F) or throughout the height of the arena (B)) had ample opportunities to learn that the nest entrance lies on the floor of the landmark array. The only reason why B-bees may not have entered the array from above when access from the side was prevented, may simply be that bumblebees, because they bumble, find it hard to perform a hovering descent into the array.

General:

The most serious weakness of the set-up is that it is spatially and visually constrained, in particular lacking a distant visual panorama, which under natural conditions is crucial for the range over which rotational image difference functions provide navigational guidance. In addition, the array of identical landmarks is not representative of natural clutter and, because it is visually repetitive, poses un-natural problems for view-based homing algorithms. This is the reason why the functions degrade so quickly from one position to the next (Figures 9-12), although it is not clear what these positions are (memory0-memory7).<br /> In conclusion, I do not feel that I have learnt anything useful from this experiment; it does suggest, however, that to fully appreciate and understand the homing abilities of insects, there is no alternative but to investigate these abilities in the natural conditions in which they have evolved.

Author response:

Reviewer 1 (Public Review):

“Summary:

In this paper, the authors aimed to test the ability of bumblebees to use bird-view and ground-view for homing in cluttered landscapes. Using modelling and behavioural experiments, the authors showed that bumblebees rely most on ground-views for homing.

Strengths:

The behavioural experiments are well-designed, and the statistical analyses are appropriate for the data presented.

Weaknesses:

Views of animals are from a rather small catchment area.

Missing a discussion on why image difference functions were sufficient to explain homing in wasps (Murray and Zeil 2017).

The artificial habitat is not really 'cluttered' since landmarks are quite uniform, making it difficult to infer ecological relevance.”

Thank you for your thorough evaluation of our study. We aimed to investigate local homing behaviour on a small scale, which is ecologically relevant given that the entrance of bumblebee nests is often inconspicuously hidden within the vegetation. This requires bees to locate their nest entrance using views within a confined area. While many studies have focused on larger scales using radar tracking (e.g. Capaldi et al. 2000; Osborne et al. 2013; Woodgate et al. 2016), there is limited understanding of the mechanisms behind local homing on a smaller scale, especially in dense environments.

We appreciate your suggestion to include the study by Murray and Zeil (2017) in our discussion. Their research explored the catchment areas of image difference functions on a larger spatial scale with a cubic volume of 5m x 5m x 5m. Aligned with their results, we found that image difference functions pointed towards the location of the objects surrounding the nest when the images were taken above the objects. However, within the clutter, i.e. the dense set of objects surrounding the nest, the model did not perform well in pinpointing the nest position.

We agree with your comment about the term "clutter". Therefore, we will refer to our landmark arrangement as a "dense environment" instead. Uniformly distributed objects do indeed occur in nature, as seen in grasslands, flower meadows, or forests populated with similar plants.

Reviewer 2 (Public Review):

Summary:

In a 1.5m diameter, 0.8m high circular arena bumblebees were accustomed to exiting the entrance to their nest on the floor surrounded by an array of identical cylindrical landmarks and to forage in an adjacent compartment which they could reach through an exit tube in the arena wall at a height of 28cm. The movements of one group of bees were restricted to a height of 30cm, the height of the landmark array, while the other group was able to move up to heights of 80cm, thus being able to see the landmark array from above.

During one series of tests, the flights of bees returning from the foraging compartment were recorded as they tried to reach the nest entrance on the floor of the arena with the landmark array shifted to various positions away from the true nest entrance location. The results of these tests showed that the bees searched for the net entrance in the location that was defined by the landmark array.

In a second series of tests, access to the landmark array was prevented from the side, but not from the top, by a transparent screen surrounding the landmark array. These tests showed that the bees of both groups rarely entered the array from above, but kept trying to enter it from the side.

The authors express surprise at this result because modelling the navigational information supplied by panoramic snapshots in this arena had indicated that the most robust information about the location of the nest entrance within the landmark array was supplied by views of the array from above, leading to the following strong conclusions:

line 51: "Snapshot models perform best with bird's eye views"; line 188: "Overall, our model analysis could show that snapshot models are not able to find home with views within a cluttered environment but only with views from above it."; line 231: "Our study underscores the limitations inherent in snapshot models, revealing their inability to provide precise positional estimates within densely cluttered environments, especially when compared to the navigational abilities of bees using frog's-eye views." Strengths:

The experimental set-up allows for the recording of flight behaviour in bees, in great spatial and temporal detail. In principle, it also allows for the reconstruction of the visual information available to the bees throughout the arena.

The experimental set-up allows for the recording of flight behaviour in bees, in great spatial and temporal detail. In principle, it also allows for the reconstruction of the visual information available to the bees throughout the arena.

Weaknesses:

Modelling:

Modelling left out information potentially available to the bees from the arena wall and in particular from the top edge of the arena and cues such as cameras outside the arena. For instance, modelled IDF gradients within the landmark array degrade so rapidly in this environment, because distant visual features, which are available to bees, are lacking in the modelling. Modelling furthermore did not consider catchment volumes, but only horizontal slices through these volumes.

When we started modelling the bees’ homing based on image-matching, we included the arena wall. However, the model simulations pointed only coarsely towards the clutter but not toward the nest position. We hypothesised that the arena wall and object location created ambiguity. Doussot et al. (2020) showed that such a model can yield two different homing locations when distant and local cues are independently moved. Therefore, we reduced the complexity of the environment by concentrating on the visual features, which were moved between training and testing. (Neither the camera nor the wall were moved between training and test). We acknowledge that this information should have been provided to substantiate our reasoning. As such, we will include model results with the arena wall in the revised paper.

As we wanted to investigate if bees would use ground views or bird’s eye views to home in a dense environment, we think the catchment volumes would provide qualitatively similar, though quantitatively more detailed information as catchment slices. Our approach of catchment slices is sufficient to predict whether ground or bird' s-eye views perform better in leading to the nest, and we will, therefore, not include further computations of catchment volumes.

Behavioural analysis:

The full potential of the set-up was not used to understand how the bees' navigation behaviour develops over time in this arena and what opportunities the bees have had to learn the location of the nest entrance during repeated learning flights and return flights.

Without a detailed analysis of the bees' behaviour during 'training', including learning flights and return flights, it is very hard to follow the authors' conclusions. The behaviour that is observed in the tests may be the result of the bees' extended experience shuttling between the nest and the entry to the foraging arena at 28cm height in the arena wall. For instance, it would have been important to see the return flights of bees following the learning flights shown in Figure 17.

Basically, both groups of bees (constrained to fly below the height of landmarks (F) or throughout the height of the arena (B)) had ample opportunities to learn that the nest entrance lies on the floor of the landmark array. The only reason why B-bees may not have entered the array from above when access from the side was prevented, may simply be that bumblebees, because they bumble, find it hard to perform a hovering descent into the array.

A prerequisite for studying the learning flight in a given environment is showing that the bees manage to return to their home. Here, our primary goal was to demonstrate this within a dense environment. While we understand that a detailed analysis of the learning and return flights would be valuable, we feel this is outside the scope of this particular study.

Multi-snapshot models have been repeatedly shown to be sufficient to explain the homing behaviour in natural as well as artificial environments. A model can not only be used to replicate but also to predict a given outcome and shape the design of experiments. Here, we used the models to shape the experimental design, as it does not require the entire history of the bee's trajectory to be tested and provides interesting insight into homing in diverse environments.

Our current knowledge of learning flights did not permit these investigations of bee training. Firstly, our setup does not allow us to record each inbound and outbound flight of the bumblebees during training. Doing so would require blocking the entire colony for extended time periods, potentially impairing the motivation of the bees to forage or the survival and development of the colony. Secondly, the exact locations where bees learn or if and whether they continuously learn by weighting the visual experience based on their positions and orientations is not always clear. It makes it difficult to categorise these flights accurately in learning and return flights. Additionally, homing models remain elusive on the learning mechanisms at play during the learning flights. Therefore, we believe that continuous effort must be made to understand bees' learning and homing ability. We felt it was necessary first to establish that bees could navigate back to the nest in a dense, cluttered environment. With this understanding, we are currently conducting a detailed study of the bees' learning flights in various dense environments and provide these results in a separate article.

While we acknowledge that the bees had ample opportunities to learn the location of the nest entrance, we believe that their behaviour of entering the dense environment at a very low altitude cannot be solely explained by extended experience. It is possible that the bees could have also learned to enter at the edge of the objects or above the objects before descending within the clutter.

General:

The most serious weakness of the set-up is that it is spatially and visually constrained, in particular lacking a distant visual panorama, which under natural conditions is crucial for the range over which rotational image difference functions provide navigational guidance. In addition, the array of identical landmarks is not representative of natural clutter and, because it is visually repetitive, poses un-natural problems for view-based homing algorithms. This is the reason why the functions degrade so quickly from one position to the next (Figures 9-12), although it is not clear what these positions are (memory0-memory7).

In conclusion, I do not feel that I have learnt anything useful from this experiment; it does suggest, however, that to fully appreciate and understand the homing abilities of insects, there is no alternative but to investigate these abilities in the natural conditions in which they have evolved.

We respectfully disagree with the evaluation that our study does not provide new insights due to the controlled lab conditions. Both field and lab research are absolutely necessary and should feed each other. Dismissing the value of controlled lab experiments would overlook the contributions of previous lab-based research, which has significantly advanced our understanding of animal behaviour. It is only possible to precisely define the visual test environments under laboratory conditions and to identify the role of these components for the behaviour through targeted variation of individual components of the environment. These results should guide field-based experiments for validation.

Our lab settings are a kind of abstraction of natural situations focusing on those aspects that are at the centre of the research question. Our approach here was that bumblebees have to find their inconspicuous nest hole in nature, which is difficult to find in often highly dense environments, and ultimately on a spatial scale in the metre range. We first wanted to find out if bumblebees can find their nest hole under the particularly challenging condition that all objects surrounding the nest hole are the same. This was not yet clear. Uniformly distributed objects may, however, also occur in nature, as seen with visually inconspicuous nest entrances of bumblebees in grass meadows, flower meadows, or forests with similar plants. We agree that the term "clutter" is not well-defined in the literature and will refer to our environment as a "dense environment."

Despite the lack of a distant visual panorama, or also UV light, wind, or other confounding factor inherent to field work, the bees successfully located the nest position even when we shifted the dense environment within the flight arena. We used rotational-image difference functions based on snapshots taken around the nest position to predict the bees' behaviour, as this is one of the most widely accepted and computationally most parsimonious

mechanisms for homing. This approach also proved effective in our more restricted conditions, where the bees still managed to pinpoint their home.

Reviewer #1 (Public Review):

Summary:

Das and Menon describe an analysis of a large open-source iEEG dataset (UPENN-RAM). From encoding and recall phases of memory tasks, they analyzed power and phase-transfer entropy as a measure of directed information flow in regions across a hypothesized tripartite network system. The anterior insula (AI) was found to have heightened high gamma power during encoding and retrieval, which corresponded to suppression of high gamma power in the posterior cingulate cortex (PCC) during encoding but not recall. In contrast, directed information flow from (but not to) AI to mPFC/PCC and dorsal posterior parietal/middle frontal cortex is high during both time periods when PTE is analyzed with broadband but not narrowband activity. They claim that these findings significantly advance an understanding of how network communication facilitates cognitive operations such as control over memory and that the AI of the salience network (SN) is responsible for governing the switch between the frontoparietal network (FPN) and default-mode network (DMN) when shifting between externally- and internally-driven processing.

I find this question interesting and important and agree with the authors that iEEG presents a unique opportunity to investigate the temporal dynamics within network nodes. However, I am not convinced that their claims are supported by the results currently presented. In particular, the fact that network-level communication is not modulated significantly compared to rest and does not relate to behavior suggests that PTE analyses may not be tapping into task-relevant communication. Moreover, dissociation of network effects - present during both encoding and recall - from local power suppression effects - present only during encoding - suggests that these sets of results may index separate and not unitary task processes.

Strengths:

- The authors present results from an impressively sized iEEG sample. For reader context, this type of invasive human data is difficult and time-consuming to collect and many similar studies in high-level journals include 5-20 participants, typically not all of whom have electrodes in all regions of interest. It is excellent that they have been able to leverage open-source data in this way.

- Preprocessing of iEEG data also seems sensible and appropriate based on field standards.

- The authors tackle the replication issues inherent in much of the literature by replicating findings across task contexts, demonstrating that the principles of network communication evidenced by their results generalize in multiple task memory contexts. Again, the number of iEEG patients who have multiple tasks' worth of data is impressive.

Weaknesses:

• The motivation for investigating the tripartite network during memory tasks is not currently well-elaborated. Though the authors mention, for example, that "the formation of episodic memories relies on the intricate interplay between large-scale brain networks (p. 4)", there are no citations provided for this statement, and the reader is unable to evaluate whether the nodes and networks evidenced to support these processes are the same as networks measured here.

• In addition, though the tripartite network has been proposed to support cognitive control processes, and the neural basis of cognitive control is the framed focus of this work, the authors do not demonstrate that they have measured cognitive control in addition to simple memory encoding and retrieval processes. Tasks that have investigated cognitive control over memory (such as those cited on p. 13 - Badre et al., 2005; Badre & Wagner, 2007; Wagner et al., 2001; Wagner et al., 2005) generally do not simply include encoding, delay, and recall (as the tasks used here), but tend to include some manipulation that requires participants to engage control processes over memory retrieval, such as task rules governing what choice should be made at recall (e.g., from Badre et al., 2005 Fig. 1: congruency of match, associative strength, number of choices, semantic similarity). Moreover, though there are task-responsive signatures in the nodes of the tripartite networks, concluding that cognitive control is present because cognitive control networks are active would be a reverse inference.

• It is currently unclear if the directed information flow from AI to DMN and FPN nodes truly arises from task-related processes such as cognitive control or if it is a function of static brain network characteristics constrained by anatomy (such as white matter connection patterns, etc.). This is a concern because the authors did not find that influences of AI on DMN or FPN are increased relative to a resting baseline (collected during the task) or that directed information flow differs in successful compared to unsuccessful retrieval. I doubt that this AI influence is 1) supporting a switch between the DMN and FPN via the SN or 2) relevant for behavior if it doesn't differ from baseline-active task or across accuracy conditions. An additional comparison that may help investigate whether this is reflective of static connectivity characteristics would be a baseline comparison during non-task rest or sleep periods.

• Related to the above concern, it is also questionable how directed information flow from AI facilitates switching between FPN and DMN during both encoding and recall if high gamma activity does not significantly differ in AI versus PCC or mPFC during recall as it does during encoding. It seems erroneous to conclude that the network-level communication is happening or happening with the same effect during both task time points when these effects are decoupled in such a way from the power findings.

• Missing information about the methods used for time-frequency conversion for power calculation and the power normalization/baseline-correction procedure bars a thorough evaluation of power calculation methods and results.

If revisions to the manuscript can address concerns about directed information flow possibly being due to anatomical constraints - such as by indicating that directed information flow is not present during non-task rest or sleep - this work may convey important information about the structure and order of communication between these networks during attention to tasks in general. However, the ability of the findings to address cognitive control-specific communication and the nature of neurophysiological mechanisms of this communication - as opposed to the temporal order and structure of recruited networks - may be limited.

Because phase-transfer entropy is presented as a "causal" analysis in this investigation (PTE), I also believe it is important to highlight for readers recent discussions surrounding the description of "causal mechanisms" in neuroscience (see "Confusion about causation" section from Ross and Bassett, 2024, Nature Neuroscience). A large proportion of neuroscientists (admittedly, myself included) use "causal" only to refer to a mechanism whose modulation or removal (with direct manipulation, such as by lesion or stimulation) is known to change or control a given outcome (such as a successful behavior). As Ross and Bassett highlight, it is debatable whether such mechanistic causality is captured by Granger "causality" (a.k.a. Granger prediction) or the parametric PTE, and the imprecise use of "causation" may be confusing. The authors could consider amending language regarding this analysis if they are concerned about bridging these definitions of causality across a wide audience.

eLife assessment

In this manuscript, the authors present valuable findings on the apparent role of a salience-network anterior insula node in directing fronto-parietal and default-mode network activity within a tripartite network during control of memory, drawn from an impressive invasive human neurophysiological dataset. While we commend the use of a large intracranial EEG dataset to approach this question, the study at present is incomplete in its methodologies, analysis, and interpretation to support the authors' central claims. The manuscript could be improved by addressing the concerns described.

Reviewer #2 (Public Review):

In this study, the authors leverage a large public dataset of intracranial EEG (the University of Pennsylvania RAM repository) to examine electrophysiologic network dynamics involving the participation of salience, frontoparietal, and default mode networks in the completion of several episodic memory tasks. They do this through a focus on the anterior insula (AI; salience network), which they hypothesize may help switch engagement between the DMN and FPN in concert with task demands. By analyzing high-gamma spectral power and phase transfer entropy (PTE; a putative measure of information "flow"), they show that the AI shows higher directed PTE towards nodes of both the DMN and FPN, during encoding and recall, across multiple tasks. They further demonstrate that high-gamma power in the PCC/precuneus is decreased relative to the AI during memory encoding. They interpret these results as evidence of "triple-network" control processes in memory tasks, governed by a key role of the AI.

I commend the authors on leveraging this large public dataset to help contextualize network models of brain function with electrophysiological mechanisms - a key problem in much of the fMRI literature. I also appreciate that the authors emphasized replicability across multiple memory tasks, in an effort to demonstrate conserved or fundamental mechanisms that support a diversity of cognitive processes. However, I believe that their strong claims regarding causal influences within circumscribed brain networks cannot be supported by the evidence as presented. In my efforts to clearly communicate these inadequacies, I will suggest several potential analyses for the authors to consider that might better link the data to their central hypotheses.

(1) As a general principle, the effects that the authors show - both in regards to their high-gamma power analysis and PTE analysis - do not offer sufficient specificity for a reader to understand whether these are general effects that may be repeated throughout the brain, or whether they reflect unique activity to the networks/regions that are laid out in the Introduction's hypothesis. This lack of specificity manifests in several ways, and is best communicated through examples of control analyses.

First, the PTE analysis is focused solely on the AI's interactions with nodes of the DMN and FPN; while it makes sense to focus on this putative "switch" region, the fact that the authors report significant PTE from the AI to nodes of both networks, in encoding and retrieval, across all tasks and (crucially) also at baseline, raises questions about the meaningfulness of this statistic. One way to address this concern would be to select a control region that would be expected to have little/no directed causal influence on these networks and repeat the analysis. Alternatively (or additionally), the authors could examine the time course of PTE as it evolves throughout an encoding/retrieval interval, and relate that to the timing of behavioral events or changes in high-gamma power. This would directly address an important idea raised in their own Discussion, "the AI is well-positioned to dynamically engage and disengage with other brain areas."

Second, the authors state that high-gamma suppression in the PCC/precuneus relative to the AI is an anatomically specific signature that is not present in the FPN. This claim does not seem to be supported by their own evidence as presented in the Supplemental Data (Figures S2 and S3), which to my eye show clear evidence of relative suppression in the MFG and dPPC (e.g. S2a and S3a, most notably) which are notated as "significant" with green bars. I appreciate that the magnitude of this effect may be greater in the PCC/precuneus, but if this is the claim it should be supported by appropriate statistics and interpretation.

(2) I commend the authors on emphasizing replicability, but I found their Bayes Factor (BF) analysis to be difficult to interpret and qualitatively inconsistent with the results that they show. For example, the authors state that BF analysis demonstrates "high replicability" of the gamma suppression effect in Figure 3a with that of 3c and 3d. While it does appear that significant effects exist across all three tasks, the temporal structure of high gamma signals appears markedly different between the two in ways that may be biologically meaningful. Moreover, it appears that the BF analysis did not support replicability between VFR and CATVFR, which is very surprising; these are essentially the same tasks (merely differing in the presence of word categories) and would be expected to have the highest degree of concordance, not the lowest. I would suggest the authors try to analytically or conceptually reconcile this surprising finding.

To aid in interpretability, it would be extremely helpful for the authors to assess across-task similarity in high-gamma power on a within-subject basis, which they are well-powered to do. For example, could they report the correlation coefficient between HGP timecourses in paired-associates versus free-recall tasks, to better establish whether these effects are consistent on a within-subject basis? This idea could similarly be extended to the PTE analysis. Across-subject correlations would also be a welcome analysis that may provide readers with better-contextualized effect sizes than the output of a Bayes Factor analysis.

Reviewer #1 (Public Review):

Summary:

The investigation delves into allosteric modulation within the glycosylated SARS-CoV-2 spike protein, focusing on the fatty acid binding site. This study uncovers intricate networks connecting the fatty acid site to crucial functional regions, potentially paving the way for developing innovative therapeutic strategies.

Strengths:

This article's key strength lies in its rigorous use of dynamic nonequilibrium molecular dynamics (D-NEMD) simulations. This approach provides a dynamic perspective on how the fatty acid binding site influences various functional regions of the spike. A comprehensive understanding of these interactions is crucial in deciphering the virus's behavior and identifying potential targets for therapeutic intervention.

Weaknesses:

The presented evidence is compelling but could be better if this study is supported with sequence analysis to facilitate a complete view of the allosteric networks. The thorough analysis of the simulation results is partially aligned with the discussion because observed in the replicates and the monomers an asymmetry in the perturbations generated by D-NEMD, even when we're using 210 nonequilibrium MD of 10 ns. While the authors claim that the strategy used in this article has been previously validated, the complexity of the spike and the interactions analyzed have required a robust statistical analysis, which is not shown quantitatively. The investigation examines the allosteric modulation within the glycosylated SARS-CoV-2 spike protein, emphasizing the significance of the fatty acid binding site in influencing the structural dynamics and communication pathways essential for viral function, potentially facilitating the development of novel therapeutic strategies. The presented evidence is compelling but needs to be supported by sequence analysis, which will facilitate understanding of the scientific community.

Minor considerations:

Figure S3 shows a discrepancy in the presentation of residue values S325 in the plots of Chains A, B, and C. While chain A shows a value near 0.1, chains B and C plots do not have any value.

Please explain why the plots of figures S6, S7, and S8 show significant changes in several regions, such as RBM and Furin Site. Can these changes be explained?

The flow of the allosteric interaction is complex to visualize just by looking at structures. Could you please include a diagram showing the flow of allosteric interactions (in a sequence diagram or using the structure of the protein)? Or could you include a vector showing how the perturbation done in the FA Active site takes contact with other relevant regions of the Spike protein?

Reviewer #3 (Public Review):

Summary:

In a previous study, the authors analyzed the dynamics of the SARS-CoV2 spike protein through lengthy MD simulations and an out-of-equilibrium sampling scheme. They identified an allosteric interaction network linking a lipid-binding site to other structurally important regions of the spike. However, this study was conducted without considering the impact of glycans. It is now known that glycans play a crucial role in modulating spike dynamics. This new manuscript investigates how the presence of glycans affects the allosteric network connecting the lipid binding site to the rest of the spike. The authors conducted atomistic equilibrium and out-of-equilibrium MD simulations and found that while the presence of glycans influences the structural responses, it does not fundamentally alter the connectivity between the fatty acid site and the rest of the spike.

Strengths:

The manuscript's findings are based on an impressive amount of sampling. The methods and results are clearly outlined, and the analysis is conducted meticulously.

Weaknesses:

The study does not clearly show any new findings. The authors themselves acknowledge that the manuscript mainly presents negative results-indicating that glycans do not significantly impact the allosteric network previously reported in other publications. All the results in the paper are based on a single methodology, and additional independent approaches would be needed to confirm the robustness of these findings. Allosteric networks arise from subtle correlations in protein structural dynamics, and it's uncertain whether the results discussed in this manuscript stem exclusively from the chosen force field and other modeling and analysis decisions, or if they indeed reflect something real.

eLife assessment

This manuscript focuses on understanding if and how the glycosylation of SARS-CoV2 spike protein affects a putative allosteric network of interactions controlled by the binding of a fatty acid. The main conclusion is that glycans do not significantly affect the network of allosteric interactions. This useful information - albeit mainly consisting of negative results - is based on solid evidence. It will be of interest to scientists focusing on SARS CoV2 protein structure and dynamics.

Reviewer #2 (Public Review):

This is a nice paper illustrating the use of equilibrium/non-equilibrium MD simulations to explore allosteric communication in the Spike protein. The results are described in detail and suggest a complex network of signal transmission patterns. The topic is not completely novel as it has been studied before by the same authors and the impact of glycosylation is moderated and localized at the furin site, so not many new conclusions emerge here. It is suggested that mutations are commonly found in the communication pathway which is interesting, but the authors fail to provide evidence that this is related to a positive selection and not simply to a random effect related to mutations at points that are not crucial for stability or function. One interesting point is the connection of the FA site with an additional site binding heme group. It will be interesting to see reversibility, i.e. removal of the ligand at this site is producing perturbation at the FA site?, does it produce other effects suggesting a cascade of allosteric effects? Finally, the paper lacks details to help reproducibility, in particular, I do not see details on D-NEMD calculations. One interesting point is the connection of the FA site with an additional site binding heme group.

eLife assessment

This is an important study, as PIM1/2 control of protein synthesis in differentiated cells has implications beyond T cells. The evidence is convincing in that it makes extensive use of the mouse knockout model and validation in mouse T cells with inhibitors. A rescue experiment in mouse KO T cells would be even stronger than the inhibitor studies to validate the KO phenotype and the evidence would be truly impressive if the results from the rescue experiment support the working model. Extending the observations to human T cells would also be a step towards translation and would further increase the potential impact of the work.

Reviewer #1 (Public Review):

Summary and Strengths:

The study focuses on PIM1 and 2 in CD8 T cell activation and differentiation. These two serine/threonine kinases belong to a large network of Serine/Threonine kinases that acts following engagement of the TCR and of cytokine receptors and phosphorylates proteins that control transcriptional, translational and metabolic programs that result in effector and memory T cell differentiation. The expression of PIM1 and PIM2 is induced by the T-cell receptor and several cytokine receptors. The present study capitalized on high-resolution quantitative analysis of the proteomes and transcriptomes of Pim1/Pim2-deficient CD8 T cells to decipher how the PIM1/2 kinases control TCR-driven activation and IL-2/IL-15-driven proliferation, and differentiation into effector T cells.<br /> Quantitative mass spectrometry-based proteomics analysis of naïve OT1 CD8 T cell stimulated with their cognate peptide showed that the PIM1 protein was induced within 3 hours of TCR engagement and its expression was sustained at least up to 24 hours. The kinetics of PIM2 expression was protracted as compared to that of PIM1. Such TCR-dependent expression of PIM1/2 correlated with the analysis of both Pim1 and Pim2 mRNA. In contrast, Pim3 mRNA was only expressed at very low levels and the PIM3 protein was not detected by mass spectrometry. Therefore, PIM1 and 2 are the major PIM kinases in recently activated T cells. Pim1/Pim2 double knockout (Pim dKO) mice were generated on a B6 background and found to express a lower number of splenocytes. No difference in TCR/CD28-driven proliferation was observed between WT and Pim dKO T cells over 3 days in culture. Quantitative proteomics of >7000 proteins further revealed no substantial quantitative or qualitative differences in protein content or proteome composition. Therefore, other signaling pathways can compensate for the lack of PIM kinases downstream of TCR activation.

Considering that PIM1 and PIM2 kinase expression is regulated by IL-2 and IL-15, antigen-primed CD8 T cells were expanded in IL-15 to generate memory phenotype CD8 T cells or expanded in IL-2 to generate effector cytotoxic T lymphocytes (CTL). Analysis of the survival, proliferation, proteome, and transcriptome of Pim dKO CD8 T cells kept for 6 days in IL-15 showed that PIM1 and PIM2 are dispensable to drive the IL-15-mediated metabolic or differentiation programs of antigen-primed CD8 T cells. Moreover, Pim1/Pim2-deficiency had no impact on the ability of IL-2 to maintain CD8 T cell viability and proliferation. However, WT CTL downregulated the expression of CD62L whereas the Pim dKO CTL sustained higher CD62L expression. Pim dKO CTL was also smaller and less granular than WT CTL. Comparison of the proteome of day 6 IL-2 cultured WT and Pim dKO CTL showed that the latter expressed lower levels of the glucose transporters, SLC2A1 and SLC2A3, of a number of proteins involved in fatty acid and cholesterol biosynthesis, and CTL effector proteins such as granzymes, perforin, IFNg, and TNFa. Parallel transcriptomics analysis showed that the reduced expression of perforin and some granzymes correlated with a decrease in their mRNA whereas the decreased protein levels of granzymes B and A, and the glucose transporters SLC2A1 and SLC2A3 did not correspond with decreased mRNA expression. Therefore, PIM kinases are likely required for IL-2 to maximally control protein synthesis in CD8 CTL. Along that line, the translational repressor PDCD4 was increased in Pim dKO CTL and pan-PIM kinase inhibitors caused a reduction in protein synthesis rates in IL-2-expanded CTL. Finally, the differences between Pim dKO and WT CTL in terms of CD62L expression resulted in Pim dKO CTL but not WT CTL retained the capacity to home to secondary lymphoid organs. In conclusion, this thorough and solid study showed that the PIM1/2 kinases shape the effector CD8 T cell proteomes rather than transcriptomes and are important mediators of IL2-signalling and CD8 T cell trafficking.

Weaknesses:

None identified by this reviewer.

Reviewer #2 (Public Review):

Summary:

Using a suite of techniques (e.g., RNA seq, proteomics, and functional experiments ex vivo) this paper extensively focuses on the role of PIM1/2 kinases during CD8 T-cell activation and cytokine-driven (i.e., IL-2 or IL-15) differentiation. The authors' key finding is that PIM1/2 enhances protein synthesis in response to IL-2 stimulation, but not IL-15, in CD8+ T cells. Loss of PIM1/2 made T cells less 'effector-like', with lower granzyme and cytokine production, and a surface profile that maintained homing towards secondary lymphoid tissue. The cytokines the authors focus on are IL-15 and Il-2, which drive naïve CD8 T cells towards memory or effector states, respectively. Although PIM1/2 are upregulated in response to T-cell activation and cytokine stimulation (e.g., IL-15, and to a greater extent, IL-2), using T cells isolated from a global mouse genetic knockout background of PIM1/2, the authors find that PIM1/2 did not significantly influence T-cell activation, proliferation, or expression of anything in the proteome under anti-CD3/CD28 driven activation with/without cytokine (i.e., IL-15) stimulation ex vivo. This is perhaps somewhat surprising given PIM1/2 is upregulated, albeit to a small degree, in response to IL-15, and yet PIM1/2 did not seem to influence CD8+ T cell differentiation towards a memory state. Even more surprising is that IL-15 was previously shown to influence the metabolic programming of intestinal intraepithelial lymphocytes, suggesting cell-type specific effects from PIM kinases. What the authors went on to show, however, is that PIM1/2 KO altered CD8 T cell proteomes in response to IL-2. Using proteomics, they saw increased expression of homing receptors (i.e., L-selectin, CCR7), but reduced expression of metabolism-related proteins (e.g., GLUT1/3 & cholesterol biosynthesis) and effector-function related proteins (e.g., IFNy and granzymes). Rather neatly, by performing both RNA-seq and proteomics on the same IL-2 stimulated WT vs. PIM1/2 KO cells, the authors found that changes at the proteome level were not corroborated by differences in RNA uncovering that PIM1/2 predominantly influence protein synthesis/translation. Effectively, PIM1/2 knockout reduced the differentiation of CD8+ T cells towards an effector state. In vivo adoptive transfer experiments showed that PIM1/2KO cells homed better to secondary lymphoid tissue, presumably owing to their heightened L-selectin expression (although this was not directly examined).

Strengths:

Overall, I think the paper is scientifically good, and I have no major qualms with the paper. The paper as it stands is solid, and while the experimental aim of this paper was quite specific/niche, it is overall a nice addition to our understanding of how serine/threonine kinases impact T cell state, tissue homing, and functionality. Of note, they hint towards a more general finding that kinases may have distinct behaviour in different T-cell subtypes/states. I particularly liked their use of matched RNA-seq and proteomics to first suggest that PIM1/2 kinases may predominantly influence translation (then going on to verify this via their protein translation experiment - although I must add this was only done using PIM kinase inhibitors, not the PIM1/2KO cells). I also liked that they used small molecule inhibitors to acutely reduce PIM1/2 activity, which corroborated some of their mouse knockout findings - this experiment helps resolve any findings resulting from potential adaptation issues from the PIM1/2 global knockout in mice but also gives it a more translational link given the potential use of PIM kinase inhibitors in the clinic. The proteomics and RNA seq dataset may be of general use to the community, particularly for analysis of IL-15 or IL-2 stimulated CD8+ T cells.

Weaknesses:

It would be good to perform some experiments in human T cells too, given the ease of e.g., the small molecule inhibitor experiment. Would also be good for the authors to include a few experiments where PIM1/2 have been transduced back into the PIM1/2 KO T cells, to see if this reverts any differences observed in response to IL-2 - although the reviewer notes that the timeline for altering primary T cells via lentivirus/CRISPR may be on the cusp of being practical such that functional experiments can be performed on day 6 after first stimulating T cells. Other experiments could also look at how PIM1/2 KO influences the differentiation of T cell populations/states during ex vivo stimulation of PBMCs or in vivo infection models using (high-dimensional) flow cytometry (rather than using bulk proteomics/RNA seq which only provide an overview of all cell combined). Alongside this, performing a PCA of bulk RNA seq/proteomes or Untreated vs. IL-2 vs. IL-15 of WT and PIM1/2 knockout T cells would help cement their argument in the discussion about PIM1/2 knockout cells being distinct from a memory phenotype.

Author response:

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

Editors’ recommendations for the authors

The reviewers recommend the following: 

(a) Digging deeper into the discussion of the density-dependent dispersal. 

(b) Clarifying the microfluidic setup.  

(c) Clarifying the description and interpretation of the transcriptomic evidence. 

(d) Toning down carbon cycle connections (some reviewers felt the evidence did not fully support the claims). 

We would like to thank the editors for their thoughtful evaluation of our manuscript and their clear suggestions. We have revised the manuscript in the light of these comments, as we outline below and address in detail in the point-by-point response to the reviewers’ comments that follows. 

(a) We have expanded the discussion of density-dependent dispersal and revised Figure 2C to improve clarity. 

(b) We have also added further information concerning the microfluidic setup in the results section and provide an illustration of the setup in a new figure panel, Figure 1A.

(c) Addressing the reviewers’ comments on the transcriptomic analysis, we have added more information in the description and interpretation of the results. 

(d) We have rephrased the text describing the role of degradation-dispersal cycles for carbon cycling to highlight it as the motivation of this study and emphasize the link to literature on foraging, without creating expectations of direct measurements of global carbon cycling.

Public Reviews:

Reviewer #1 (Public Review):

[...]

Weaknesses: 

Much of the genetic analysis, as it stands, is quite speculative and descriptive. I found myself confused about many of the genes (e.g., quorum sensing) that pop up enriched during dispersal quite in contrast to my expectations. While the authors do mention some of this in the text as worth following up on, I think the analysis as it stands adds little insight into the behaviors studied. However, I acknowledge that it might have the potential to generate hypotheses and thus aid future studies. Further, I found the connections to the carbon cycle and marine environments in the abstract weak --- the microfluidics setup by the authors is nice, but it provides limited insight into naturalistic environments where the spatial distribution and dimensionality of resources are expected to be qualitatively different. 

We thank the reviewer for their suggestions to improve our manuscript. We agree that the original manuscript would have benefitted from more detailed interpretation of the observed changes in gene expression. We have revised the manuscript to elaborate on the interpretation of the changes in expression of quorum sensing genes (see response to reviewer 1, comment 3), motility genes (see response to reviewer 1, comment 6), alginate lyase genes (see response to reviewer 1, comment 7 and reviewer 2, comment 2), and ribosomal and transporter genes (see response to reviewer 2, comment 2).

In general, we think that the gene expression study not only supports the phenotypic observations that we made in the microfluidic device, such as the increased swimming motility when exposed to digested alginate medium, but  also adds further insights. Our reasoning for studying the transcriptomes in well mixed-batch cultures was the inability to study gene expression dynamics to support the phenotypic observations about differential motility and chemotaxis in our microfluidics setup. The transcriptomic data clearly show that even in well-mixed environments, growth on digested alginate instead of alginate is sufficient to increase the expression of motility and chemotaxis genes. In addition, the finding that expression of alginate lyases and metabolic genes is increased during growth on digested alginate was revealed through the analysis of transcriptomes, something which would not have been possible in the microfluidic setup. We agree with the reviewer that our analyses implicate further, perhaps unexpected, mechanisms like quorum sensing in the cellular response to breakdown products, and that this represents an interesting avenue for further studies.

Finally, we  also agree with the reviewer that it would be good to be more explicit in the text that our microfluidic system cannot fully capture the complex dynamics of natural environments. Our approach does, however, allow the characterization of cellular behaviors at spatial and temporal scales that are relevant to the interactions of bacteria, and thus provides a better understanding of colonization and dispersal of marine bacteria in a manner that is not possible through in situ experiments. We have edited our manuscript to highlight this and modified our statements regarding carbon cycling towards emphasizing the role degradation-dispersal cycles in remineralization of polysaccharides (see response to reviewer 1, comment 2).  

Reviewer #2 (Public Review):

[...]

Weaknesses: 

The explanation of the microfluidics measurements is somewhat confusing but I think this could be easily remedied. The quantitative interpretation of the dispersal data could also be improved and I'm not clear if the data support the claim made. 

We thank the reviewer for their comments and helpful suggestions. We have revised the manuscript with these suggestions in mind and believe that the manuscript is improved by a more detailed explanation of the microfluidic setup. We have added more information in the text (detailed in response to reviewer 2, comments 1 and 2) and have added a depiction of the microfluidic setup (Fig. 1A). We have also modified the presentation and discussion of the dispersal data (Fig. 2C), as described in detail below in response to reviewer 2, comment 4, and argue that they clearly show density-dependent dispersal. We believe that this modification of how the results are presented provides a more convincing case for our main conclusion, namely that the presence of degradation products controls bacterial dispersal in a density-dependent manner.  

Reviewer #3 (Public Review):

[...]

Weaknesses: 

I find this paper very descriptive and speculative. The results of the genetic analyses are quite counterintuitive; therefore, I understand the difficulty of connecting them to the observations coming from experiments in the microfluidic device. However, they could be better placed in the literature of foraging - dispersal cycles, beyond bacteria. In addition, the interpretation of the results is sometimes confusing. 

We thank the reviewer for their suggestions to improve the manuscript. We have edited the manuscript to interpret the results of this study more clearly, in particular with regard to the fact that breakdown products of alginate cause cell dispersal (see response to reviewer 2, comment 1), gene expression changes of ribosomal proteins and transporters (see response to reviewer 2, comment 2), as well as genes relating to alginate catabolism (see response to reviewer 2, comment 3).

To provide more context for the interpretation of our results we now also embed our findings in more detail in the previous work on foraging strategies and dispersal tradeoffs.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

(1) The authors should clarify in more detail what they mean by density dependence in Figure 2. Usually density dependence refers to a per capita dependence, but here it seems that the per capita rate of dispersal might be roughly independent of density (Figure 2c; if you double the number of cells it doubles the number of cells leaving). Rather it seems the dispersal is such that the density of remaining cells falls below a threshold (~300 cells). 

We thank the reviewer for raising this important point. To analyze the data more explicitly in terms of per capita dependence and so make the density dependence in the dispersal from the microfluidic chambers more clear, we have modified Figure 2C and edited the text. 

In the modified Figure 2C, we computed the fraction of dispersed cells for each chamber (i.e the change in cell number divided by the cell number at the time of the nutrient switch). This quantity directly reveals the per-capita dependence, as mentioned by reviewer 1, and is now represented on the y-axis of Figure 2C instead of the absolute change in cell number. 

These data demonstrate that the fraction of dispersed cells increases with increasing numbers of cells present in the chamber at the time of switching, with more highly populated chambers showing a higher fraction of dispersed cells. These findings indicate that there is a strong density dependence in the dispersal process.

As pointed out by reviewer 1, another interesting aspect of the data is the transition at low cell number. The fraction of dispersed cells is negative in the case of the chamber with approximately 70 cells, consistent with no dispersal at this low density, and a moderate density increase as a function of continued growth.  

In addition to the new analysis presented in Figure 2C, we have modified the paragraph that discusses this result as follows (line 208):

“We indeed found that the nutrient switch caused a few or no cells to disperse from small cell groups (Fig. 2B), whereas a large fraction of cells from large cell groups dispersed (Fig. 2C). In fact, the e fraction of cells that dispersed upon imposition of the nutrient switch showed a strong positive relationship with the number of cells present, meaning that cells in chambers with many cells were more likely to disperse than cells in chambers with fewer cells (Fig. 2C).”

(2) The authors should tone down their claims about the carbon cycle in the abstract. I do not believe the results as they stand could be used to understand degradation-dispersal cycles in marine environments relevant to the carbon cycle, since these behaviors have been studied in microfluidic environments which in my understanding are quite different. As such, statements such as "degradation-dispersal cycles are an integral part in the global carbon cycle, we know little about how cells alternate between degradation and motility" and "Overall, our findings reveal the cellular mechanisms underlying bacterial degradation-dispersal cycles that drive remineralization in natural environments" are overstated in the abstract. 

We appreciate the reviewer’s comments regarding the connections of our work with the carbon cycle. We have now rephrased these statements in our manuscript to describe a potential connection between our work and the marine carbon cycle. The colonization of polysaccharides particles by bacteria and subsequent degradation has been widely acknowledged to play a significant role in controlling the carbon flow in marine ecosystems. (Fenchel, 2002; Preheim et al., 2011; Yawata et al., 2014, 2020). We still refer to carbon flow in the revised manuscript, though cautiously, as microbial remineralization of biomass, which is recognized as an important factor in the marine biological carbon pump (e.g., (Chisholm, 2000; Jiao et al., 2024). As stated in the previous version of the manuscript, the main motivation of our work was to study the growth behaviors of marine heterotrophic bacteria during polysaccharide degradation, especially to understand when bacteria depart already colonized and degraded particles and find novel patches to grow and degrade, a process that is poorly understood. Therefore, it is conceivable that degradation-dispersal cycles do play a role in the flow of carbon in marine ecosystems. However, we acknowledge that the carbon cycle is influenced by a multitude of biological and chemical processes, and the bacterial degradation-dispersal cycle might not be the sole mechanism at play. 

We also appreciate the reviewer’s comments highlighting that the complexity of natural environments is not fully captured in our microfluidics system. However, our microfluidics setup does allow us to quantify responses and behaviors of microbial groups at high spatial and temporal resolution, especially in the context of environmental fluctuations. Microbes in nature interact at small spatial scales and have to respond to changes in the environment, and the microfluidics setup enables the quantification of these responses. Moreover, dispersal of the bacterium V. cyclitrophicus that we use in our study, has been previously observed even during growth on particulate alginate (Alcolombri et al., 2021), but the cues and regulation controlling dispersal behaviors have been unclear.  Microfluidic experiments have now allowed us to study this process in a highly quantitative manner, and align well with observations from experiments from more nature-like settings. These quantitative experiments on bacterial strains isolated from marine particles are expected to constrain quantitative models of carbon degradation in the ocean (Nguyen et al., 2022).

We have now adjusted our statements throughout our manuscript to reflect the knowledge gaps in understanding the triggers of degradation-dispersal cycles and their links with carbon flow in marine ecosystems. The revised manuscript, especially, contains the following statements (line 47 and line 60):

“Even though many studies indicate that these degradation-dispersal cycles contribute to the carbon flow in marine systems, we know little about how cells alternate between polysaccharide degradation and motility, and which environmental factors trigger this behavioral switch.”

“Overall, our findings reveal cellular mechanisms that might also underlie bacterial degradation-dispersal cycles, which influence the remineralization of biomass in marine environments.”

(3) The authors should clarify why they think quorum-sensing genes are increased in expression on digested alginate. The authors currently mention that QS could be used to trigger dispersal, but given the timescales of dispersal in Figure 2 (~half an hour), I find it hard to believe that these genes are expressed and have the suggested effect on those timescales. As such I would have expected the other way round - for QS genes to be expressed highly during alginate growth, so that density could be sensed and responded to. Please clarify. 

We have now clarified this point in the revised manuscript. While the triggering of dispersal by quorum-sensing genes may indeed appear counterintuitive, and the response is rapid (we see dispersal of cells within 30-40 minutes), both observations are in line with previous studies in another model organism Vibrio cholerae. The dispersal time is similar to the dispersal time of V. cholerae cells from biofilms, as described by Singh and colleagues, (Figure 1E of Ref. Singh et al., 2017). In that case, induction of the quorum sensing dispersal regulator HapR was observed during biofilm dispersal within one hour after switch of condition (Fig. 2, middle panel of Ref. Singh et al., 2017). Even though the specific quorum sensing signaling molecules are probably different in our strain (there is no annotated homolog of the hapR gene in V. cyclitrophicus), we observed that the full set of quorum sensing genes was enriched in cells growing on digested alginate (as reported in line 314 and Fig. 4A).

We have added this information in the manuscript (line 317): 

“The set of quorum sensing genes was also positively enriched in cells growing on digested alginate (Fig. 4A and S4F, Table S13). This role in dispersal is in agreement with a previous study that showed induction of the quorum sensing master regulator in V. cholerae cells during dispersal from biofilms on a similar time scale as here (less than an hour) [28].”

Reviewer #2 (Recommendations For The Authors):

(1) Around line 144 - I don't really understand how you flow alginate through the microfluidic platform. It seems if the particles are transiently going through the microfluidic chamber then the flow rate and hence residence time of the alginate particles will matter a lot by controlling the time the cells have to colonize and excrete enzymes for alginate breakdown. Or perhaps the alginate is not particulate but is instead a large but soluble polymer? I think maybe a schematic of the microfluidic device would help -- there is an implicit assumption that we are familiar with the Dal Co et al device, but I don't recall its details and maybe a graphic added to Figure 1 would help. 

a. In reviewing the Dal Co paper I see that cells are trapped and the medium flows through channels and the plane where the cells are held. I am still a little confused about the size of the polymeric alginate -- large scale (>1um) particles or very small polymers? 

We have now provided a detailed description of our microfluidic experimental system. At the start of the experiments, cells are in fact not trapped within the microfluidic device, but grow and can move freely within a chamber designed with dimensions (sub-micron heights) so that growth occurs only as a monolayer. Cells were exposed to nutrients, either alginate or alginate digestion products, both in soluble form (not particles). These compounds were flowed into the device through a main channel, but entered the flowfree growth chambers by diffusion. To make these aspects of our experiments clearer, we have added further information on this in the Materials & Methods section (line 556), added this information in the abstract (line 51), and in the results (line123).

To make our microfluidic setup clearer, we have followed this advice and added a schematic as Figure 1A and have added more information on the setup to the main text (line 153):

“In brief, the microfluidic chips are made of an inert polymer (polydimethylsiloxane) bound to a glass coverslip. The PDMS layer contains flow channels through which the culture medium is pumped continuously. Each channel is connected to several growth chambers that are laterally positioned. The dimensions of these growth chambers (height: 0.85 µm, length: 60 µm, width: 90-120 µm) allow cells to freely move and grow as monolayers. The culture medium, containing either alginate or digested alginate in their soluble form, is constantly pumped through the flow channel and enters the growth chambers primarily through diffusion [15,16,4,17,8]. Therefore, the number of cells and their positioning within microfluidic chambers is determined by the cellular growth rate as well as by cell movement4. This setup combined with time-lapse microscopy allowed us to follow the development of cell communities over time.”

(2) What makes this confusing is the difference between Figure 1C and Figure S2A -- the authors state that the difference in Figure 1C is due to dispersal, but is there flow through the microfluidic device? So what role does that flow through the device have in dispersal? Is the adhesion of the cell groups driven at all by a physical interaction with high molecular weight polymers in the microfluidic devices or is this purely a biological effect? Could this also be explained by different real concentrations of nutrients in the two cases? 

We realize from this comment that the role of flow of the medium in the microfluidic setup was not clearly addressed in our manuscript. In fact, cells were not exposed to flow, and nutrients were provided to the growth chambers by diffusion. We have added a clearer explanation of this point on line 158:

“The culture medium, containing either alginate or digested alginate in their soluble form, is constantly pumped through the flow channel and enters the growth chambers primarily through diffusion [15,16,4,17,8]. Therefore, the number of cells and their positioning within microfluidic chambers is determined by the cellular growth rate as well as by cell movement4.“

One purely physical effect that we anticipate is that a high viscosity of the medium could immobilize cells. To address this point, we measured the viscosity of both alginate and digested alginate and conclude that the increase in viscosity is not strong enough to immobilize cells. We added a statement in the text (line 170)

“To test the role of increased viscosity of polymeric alginate in causing the increased aggregation of cells, we measured the viscosity of 0.1% (w/v) alginate or digested alginate dissolved in TR media. For alginate, the viscosity was 1.03±0.01 mPa·s (mean and standard deviation of three technical replicates) whereas the viscosity of digested alginate in TR media was found to be 0.74±0.01 mPa·s. Both these values are relatively close to the viscosity of water at this temperature (0.89 mPa·s18) and, while they may affect swimming behavior [19], they are insufficient to physically restrain cell movement [20].”

as well as a section in the Materials and Methods (line 594):

“Viscosity of the alginate and digested alginate solution

We measured the viscosity of alginate solutions using shear rheology measurements. We use a 40 mm cone-plate geometry (4° cone) in a Netzsch Kinexus Pro+ rheometer. 1200 uL of sample was placed on the bottom plate, the gap was set at 150 um and the sample trimmed. We used a solvent trap to avoid sample evaporation during measurement. The temperature was set to 25°C using a Peltier element. We measure the dynamic viscosity over a range of shear rates  = 0.1 – 100 s-1. We report the viscosity of each solution as the average viscosity measured over the shear rates 10 – 100 s-1, where the shear-dependence of the viscosity was low.

We measured the viscosity of 0.1% (w/V) alginate dissolved in TR media, which was 1.03 +/- 0.01 mPa·s (reporting the mean and standard deviation of three technical replicates.). The viscosity of 0.1% digested alginate in TR media was found to be 0.74+/-0.01 mPa·s. This means that the viscosity of alginate in our microfluidic experiments is 36% higher than of digested alginate, but the viscosities are close to those expected of water (0.89 mPa·s at 25 degree Celsius according to Berstad and colleagues [18]).”

While our microfluidic setup allows us to track the position and movement of cells in a spatially structured setting, these observations do not allow us to distinguish directly whether the differences in dispersal are a result of purely physical effects of polymers on cells or are a result of them triggering a biological response in cells that causes them to become sessile. It is known that bacterial appendages like pili interact with polysaccharide residues (Li et al., 2003). Therefore, it is quite plausible that cross-linking by polysaccharides can contribute growth behaviors on alginate. However, our analysis of gene expression demonstrates that flagellum-driven motility is decreased in the presence of alginate compared to digested alginate, alongside other major changes in gene expression. In addition, our measures of dispersal show that dispersal of cells when exposed to digested alginate is density dependent. Both observations suggest that the patterns in dispersal are governed by decision-making processes by cells resulting in changes in cell motility, rather than being a product of purely physical interactions with the polymer. 

The finding that viscosities of both alginate and digested alginate are similar to that of water, suggests that diffusion of nutrients in the growth chambers should be similar. Therefore, we think that the differences in real concentrations of nutrients is likely not contributing to the observed differences in behavior. 

(3) Why is Figure S1 arbitrary units? Does this have to do with the calibration of LC-MS? It would be better, it seems, to know the concentrations in real units of the monomer at least. 

We agree with the reviewer that it would have been better to have absolute concentrations for these compounds. However, to calibrate the mass spectrometer signals (ion counts) to absolute concentrations for the different alginate compounds, we would need an analytical standard of known concentration. We are not aware of such a standard and thus report only relative concentrations. We agree that the y-axis label of Figure S1 should not contain ‘arbitrary’ units, as it shows a ratio (of measurements in the same arbitrary units). We have edited the labels of Figure S1 accordingly and the figure legend in line 26 of the Supplemental Material (“Relative concentrations…”).

(4) Line 188 - density-dependent dispersal. The claim here is that "cells in chambers with many cells were more likely to disperse than cells in chambers with less cells." (my emphasis). Looking at the data in Figure 2C it appears that about 40% of the cells disperse irrespective of the density, before the switch to digested alginate. So it would seem that there is not a higher likelihood of dispersal at higher cell densities. For the very highest cell density, it does appear that this fraction is larger, but I'd be concerned about making this claim from what I understand to be a single experiment. To support the claim made should the authors plot Change in Cell number/Starting Cell number on the y-axis of Fig. 2C to show that the fraction is increasing? It would seem some additional data at higher starting cell densities would help support this claim more strongly. 

We thank the reviewer for this comment, which is in line with a remark made by reviewer 1 in their comment 1. In response to these two comments (and as described above), we have edited Figure 2C and now have plotted the change in cell number relative to starting cell number at the y axis to directly show the density dependence. We observe a positive (approximately linear) relationship between the fraction of dispersed cells with the number of cells present in the chamber at the time of switching. This indicates that there is a density dependence in the dispersal process, with highly populated chambers showing a higher fraction of dispersed cells. 

In addition to the change in Figure 2C, we have modified the paragraph around line 208: “We indeed found that the nutrient switch caused a few or no cells to disperse from small cell groups (Fig. 2B), whereas a large fraction of cells from large cell groups dispersed (Fig. 2C). In fact, the e fraction of cells that dispersed upon imposition of the nutrient switch showed a strong positive relationship with the number of cells present, meaning that cells in chambers with many cells were more likely to disperse than cells in chambers with fewer cells (Fig. 2C).”

The highest cell number at the start of the switch that we include is about 800 cells. The maximum number of cells that can fit into a chamber are ca. 1000 cells. Thus, 800 resident cells are close to the maximal density.

(5) A comment -- I find the result of significant chemotaxis towards alginate but not the monomers of alginate to be quite surprising. The ecological relevance of this (line 219) seems like an important result that is worth expanding on a bit at least in the discussion. For now, my question is whether the authors know of any mechanism by which chemotaxis receptors could respond to alginate but not the monomer. How can a receptor distinguish between the two? 

We agree that this result is surprising, given that oligomers can be more easily transported into the periplasm where sensing takes place, and they also provide an easier accessible nutrient source. Indeed, in case of the insoluble polymer chitin it has been shown that chemotaxis towards chitin is mediated by chitin oligomers (Bassler et al., 1991), which was suggested as a general motif to locate polysaccharide nutrient sources (Keegstra et al., 2022). However, a recent study has changed this perspective by showing widespread chemotaxis of marine bacteria towards the glucose-based marine polysaccharide laminarin, but not towards laminarin oligomers or glucose (Clerc et al., 2023). Together with our results on chemotaxis towards alginate (but not significantly toward alginate oligomers) this suggests that chemotaxis towards soluble polysaccharides can be mediated by direct sensing of the polysaccharide molecules.

As recommended, we expanded the discussion of the ecological relevance and also added more information on possible mechanisms of selective sensing of alginate and its breakdown products (around line 479).:

“Direct chemotaxis towards polysaccharides may facilitate the search for new polysaccharide sources after dispersal. We found that the presence of degradation products not only induces cell dispersal but also increases the expression of chemotaxis genes. Interestingly, we found that V. cyclitrophicus ZF270 cells show chemotaxis towards polymeric alginate but not digested alginate. This contrasts with previous findings for bacterial strains degrading the insoluble marine polysaccharide chitin, where chemotaxis was strongest towards chitin oligomers53, suggesting that oligomers may act as an environmental cue for polysaccharide nutrient sources55. However, recent work has shown that certain marine bacteria are attracted to the marine polysaccharide laminarin, and not laminarin oligomers56. Together with our results, this indicates that chemotaxis towards soluble polysaccharides may be mediated by the polysaccharide molecules themselves. The mechanism of this behavior is yet to be identified, but could be mediated by polysaccharide-binding proteins as have been found in Sphingomonas sp. A1 facilitating chemotaxis towards pectin57. Direct polysaccharide sensing adds complexity to chemosensing as polysaccharides cannot freely diffuse into the periplasm, which can lead to a trade-off between chemosensing and uptake58. Furthermore, most polysaccharides are not immediately metabolically accessible as they require degradation. But direct polysaccharide sensing can also provide certain benefits compared to using oligomers as sensory cues. First, it could enable bacterial strains to preferably navigate to polysaccharide nutrients sources that are relatively uncolonized and hence show little degradation activity. Second, strong chemotaxis towards degradation products could hinder a timely dispersal process as the dispersal then requires cells to travel against a strong attractant gradient formed by the degradation products. Overall, this strategy allows cells to alternate between degradation and dispersal to acquire carbon and energy in a heterogeneous world with nutrient hotspots [44,59–61].”

(6) Comment on lines 287-8 -- that the "positive enrichment of the gene set containing bacterial motility proteins matched the increase in motile cells that we observe in Fig 3E." I'm confused about what is meant by the word "matched" here. Is the implication that there is some quantitative correspondence between increased motility in Figure 3 and the change in expression in Figure 4? Or is the statement a qualitative one -- that motility genes are upregulated in the presence of digested alginate? Table S12 didn't help me answer this question. 

We thank the reviewer for their helpful comment. Our original statement was a qualitative one - observing that gene expression enrichment in genes associated with bacterial motility aligned with our expectations based on the previous observation of an increase in motile cells. We have now changed the wording to highlight the qualitative nature of this statement (line 315):

“The positive enrichment of the gene set containing bacterial motility proteins aligned with our expectations based on the increase in motile cells that we observed in Figure 3E (Fig. 4A, Table S12).”

(7) Line 326 - what is the explanation for the production of public enzymes in the presence of digest? How does this square with the previous narrative about cells growing on alginate digest expressing motility genes and chemotaxing towards alginate? It seems like the story is a bit tenuous here in the sense that digested alginates stimulate both motility - which is hypothesized to drive the discovery of new alginate particles - and lyase enzymes which are used to degrade alginate. So do the high motility cells that are chemotaxing towards alginate also express lyases en route? I'm of the opinion that constructing narratives like these in the absence of a more quantitative understanding of the colonization and degradation dynamics of alginate particles presents a major challenge and may be asking more of the data than the data can provide. 

a. I noted later that this is addressed later around lines 393 in the Discussion section.

Indeed, the notion that the presence of breakdown products triggers motility and also increases the expression of alginate lyases and other metabolic genes for alginate catabolism seems counterintuitive. We have now expanded our discussion of these results to contextualize these findings (around line 443):

"One reason for this observation may be that cells primarily rely on intracellular monosaccharide levels to trigger the upregulation of genes associated with polysaccharide degradation and catabolism, as has previously been observed for E. coli across various carbon sources [50,51]. In fact, the majority of carbon sources are sensed by prokaryotes through one‑component sensors inside the cell50. In the one‑component internal sensing scheme, the enzymes and transporters for the use of various carbon sources are expressed at basal levels, which leads to an increase in pathway intermediates upon nutrient availability. The pathway intermediates are sensed by an internal sensor, usually a transcription factor, and lead to the upregulation of transporter and enzyme expression [50,51]. This results in a positive feedback loop, which enables small changes in substrate abundance to trigger large transcriptional responses [50,52]. Thus, the presence of alginate breakdown products may likely result in increased expression of all components of the alginate degradation pathway, including the expression of degrading enzymes. As the gene expression analysis was performed on well-mixed cultures in culture medium containing alginate breakdown products, we therefore expect a strong stimulation of alginate catabolism. In a natural scenario, where cells disperse from a polysaccharide hotspot before its exhaustion, the expression of alginate catabolism genes may likely decrease again once the local concentration of breakdown products decreases. However, continued production of alginate lyases could also provide an advantage when encountering a new alginate source and continued production of alginate lyases may thus help cells to prepare for likely future environments. Further investigations of bacterial enzyme secretion in changing nutrient environments and at relevant spatial scales are required to improve our understanding of the regulation of enzyme secretion along nutrient gradients."

(8) I like Figure 6, and I think this hypothesis is a good result from this paper, but I think it would be important to emphasize this as a proposal that needs further quantitative analysis to be supported. 

We have now edited the manuscript to make this point more clear. While both degradation and dispersal are well-appreciated parts of microbial ecology, the transitions and underlying mechanisms are unclear. We have edited the discussion to improve the clarity (line 419): 

“This cycle of biomass degradation and dispersal has long been discussed in the context of foraging e.g., [44,45,13,46,47], but the cellular mechanisms that drive the cell dispersal remain unclear.”

Also, we have updated Figure 6 to indicate more clearly which new findings this work proposes (now bold font) and which previous findings that were made in different bacterial taxa and carbon sources that aligns with our  work (now light font). We edited the figure legend accordingly (line 503):

"By integrating our results with previous studies on cooperative growth on the same system, as well as results on dispersal cycles in other systems, we highlight where the specific results of this work add to this framework (bold font)."

Minor comments 

(1) Is there any growth on the enzyme used for alginate digestion? E.g. is the enzyme used to digest the alginate at sufficiently high concentrations that cells could utilize it for a carbon/nitrogen source? 

We thank the reviewer for raising this point. We added the following paragraph as Supplemental Text to address it (line 179):

“Protein amount of the alginate lyases added to create digested alginate

Based on the following calculation, we conclude that the amount of protein added to the growth medium by the addition of alginate lyases is so small that we consider it negligible. In our experiment we used 1 unit/ml of alginate lyases in a 4.5 ml solution to digest the alginate. As the commercially purchased alginate lyases are 10,000 units/g, our 4.5 ml solution contains 0.45 mg of alginate lyase protein. The digested alginate solution diluted 45x when added to culture medium. This means that we added 0.18 µg alginate lyase protein to 1 ml of culture medium.

As a comparison, for 1ml of alginate medium, 1000µg of alginate is added or for 1 ml of Lysogeny broth (LB) culture medium, 3,500 µg of LB are added.  Thus, the amount of alginate lyase protein that we added is ca. 5000 - 20,000 times smaller than the amount of alginate or LB that one would add to support cell growth. Therefore, we expect the growth that the digestion of the added alginate lyases would allow to be negligible.”

(2) The lines in Figure 2B are very hard to see. 

We have addressed this comment by using thicker lines in Figure 2B.

(3) The black background and images in Figure 3A and B are hard to see as well. 

We have now replaced Figure 3A and B, now using a white background.

(4) Typo at the beginning of line 251? 

Unfortunately we failed to find the typo referred to. We are happy to address it if it still exists in the revised manuscript.

Reviewer #3 (Recommendations For The Authors):

(1) I think there is not enough experimental evidence to conclude that the underlying cause of increased motility is the accumulation of digested alginate products. To conclusively show that this is the cause and not just some signal linked to cell density, perhaps the experiment should be repeated with a different carbon source. 

We thank the reviewer for their comment, which made us realize that we did not make the nature of the dispersal cue clear. The gene expression data was obtained from batch cultures and measured at the same approximate bacterial densities in batch, which indeed shows that the digested alginate is a sufficient signal for an increase in motility gene expression. This agrees very well with our observation that cells growing on digested alginate in microfluidic chambers have an increased fraction of motile cells in comparison with cells exposed to alginate (Fig 3E). However, we did not mean to suggest that the observed dispersal by bacterial motility is not influenced by cell density, in fact, we see that dispersal (and hence the increase in cell motility) in microfluidic chambers that are switched from polymeric to digested alginate depends on the bacterial density in the chamber, with higher bacterial densities showing increased dispersal. This shows that the presence of alginate oligomers does trigger dispersal through motility, but this signal affects bacterial groups in a cell density dependent manner.

Similar observations have been made in Caulobacter crescentus, which was found to form cell groups on the polymer xylan while cells disperse when the corresponding monomer xylose becomes available (D’Souza et al., 2021). We reference the additional work in lines 179 and 230. Taken together, these observations indicate a more general phenomenon in dispersal from polysaccharide substrates.

(2) About the expression data: 

• Ribosomal proteins and ABC transporters are enriched in cells grown on digested alginate and the authors discuss that this explains the difference in max growth rate between alginate and digested alginate. However, in Figure S2E the authors report no statistical difference between growth rates. 

We have now edited the manuscript to clarify this point. We found that cells grown on degradation products reached their maximal growth rate around 7.5 hours earlier (Fig. S2D) and showed increased expression of ribosomal biosynthesis and ABC transporters in late-exponential phase (Fig. 4A). We consider this shorter lag time as a sign of a different growth state and therefore a possible reason for the difference in ribosomal protein expression.

As the reviewer correctly points out, the maximum growth rates that were computed from the two growth curves were not significantly different (Fig. S2E). However, for our gene expression analysis, we harvested the transcriptome of cells that reached OD 0.39-0.41 (mid- to late-exponential phase). At this time point, the cell cultures may have differed in their momentary growth rate.

We edited the manuscript to make this clearer (line 287):

“Both observations likely relate to the different growth dynamics of V. cyclitrophicus ZF270 on digested alginate compared to alginate (Fig. S2A), where cells in digested alginate medium reached their maximal growth rate 7.5 hours earlier and thus showed a shorter lag time (Fig. S2D). As a consequence, the growth rate at the time of RNA extraction (mid-to-late exponential phase) may have differed, even though the maximum growth rate of cells grown in alginate medium and digested alginate medium were not found to be significantly different (Fig. S2E).”

• The increased expression of transporters for lyases in cells grown on digested alginate (lines 273-274 and 325-328) is very confusing and the explanation provided in lines 412-420 is not very convincing. My two cents on this: Expression of more enzymes and induction of motility might be a strategy to be prepared for more likely future environments (after dispersal, alginate is the most likely carbon source they will find). This would be in line with observed increased chemotaxis towards the polymer rather than the monomer (Similar to C. elegans). 

This comment is in line with reviewer 2, comment 7. In response to these two comments (and as described above), we expanded our discussion of these results to contextualize these findings (around line 443):

“One reason for this observation may be that cells primarily rely on intracellular monosaccharide levels to trigger the upregulation of genes associated with polysaccharide degradation and catabolism, as has previously been observed for E. coli across various carbon sources [50,51]. In fact, the majority of carbon sources are sensed by prokaryotes through one‑component sensors inside the cell [50]. In the one‑component internal sensing scheme, the enzymes and transporters for the use of various carbon sources are expressed at basal levels, which leads to an increase in pathway intermediates upon nutrient availability. The pathway intermediates are sensed by an internal sensor, usually a transcription factor, and lead to the upregulation of transporter and enzyme expression [50,51]. This results in a positive feedback loop, which enables small changes in substrate abundance to trigger large transcriptional responses [50,52]. Thus, the presence of alginate breakdown products may likely result in increased expression of all components of the alginate degradation pathway, including the expression of degrading enzymes. As the gene expression analysis was performed on well-mixed cultures in culture medium containing alginate breakdown products, we therefore expect a strong stimulation of alginate catabolism. In a natural scenario, where cells disperse from a polysaccharide hotspot before its exhaustion, the expression of alginate catabolism genes may likely decrease again once the local concentration of breakdown products decreases. However, continued production of alginate lyases could also provide an advantage when encountering a new alginate source and continued production of alginate lyases may thus help cells to prepare for likely future environments. Further investigations of bacterial enzyme secretion in changing nutrient environments and at relevant spatial scales are required to improve our understanding of the regulation of enzyme secretion along nutrient gradients.”

Additionally, we agree with the intriguing comment that continued expression of alginate lyases may also prepare cells for likely future environments. Further studies that aim to answer whether marine bacteria are primed by their growth on one carbon source towards faster re-initiation of degradation on a new particle will be an interesting research question. We now address this point in our manuscript (line 458):

“However, continued production of alginate lyases could also provide an advantage when encountering a new alginate source and continued production of alginate lyases may thus help cells to prepare for likely future environments. Further investigations of bacterial enzyme secretion in changing nutrient environments and at relevant spatial scales are required to improve our understanding of the regulation of enzyme secretion along nutrient gradients.“

(3) The yield reached by Vibrio on alginate is significantly higher than the yield in digested alginate, not similar, as stated in lines 133-134. Only cell counts are similar. Perhaps the author can correct this statement and speculate on the reason leading to this discrepancy: perhaps cells tend to aggregate in alginate despite the fact that these are well-mixed cultures. 

We have edited the description of the OD measurements accordingly and agree with the reviewer that aggregation is indeed a possible reason for the discrepancy (line 141):

“We also observed that the optical density at stationary phase was higher when cells were grown on alginate (Fig. S2B and C). However, colony counts did not show a significant difference in cell numbers (Fig. S3), suggesting that the increased optical density may stem from aggregation of cells in the alginate medium, as observed for other Vibrio species [7].”

(4) I suggest toning down the importance of the results presented in this study for understanding global carbon cycling. There is a link but at present it is too much emphasized. 

We have edited our statements regarding the carbon cycle. In the revised manuscript we stress the lack of direct quantifications of carbon cycling. . We still refer to carbon flow in the revised manuscript, as we would argue that microbial remineralization of biomass is recognized as an important factor in the marine biological carbon pump (e.g., Chisholm, 2000) and research on marine bacterial foraging investigates how bacterial cells manage to find and utilize this biomass.

Our revised manuscript contains the following modified statements (line 47 and line 60): “Even though many studies indicate that these degradation-dispersal cycles contribute to the carbon flow in marine systems, we know little about how cells alternate between polysaccharide degradation and motility, and which environmental factors trigger this behavioral switch.”

“Overall, our findings reveal cellular mechanisms that might also underlie bacterial degradation-dispersal cycles, which influence the remineralization of biomass in marine environments.”

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eLife assessment

This manuscript is a valuable contribution to our understanding of foraging behaviors in marine bacteria. The authors present a conceptual model for how a marine bacterial species consumes an abundant polysaccharide. Using experiments in microfluidic devices and through measurements of motility and gene expression, the authors offer convincing evidence that the degradation products of polysaccharide digestion can stimulate motility.

Reviewer #1 (Public Review):

Summary:

The authors attempt to understand how cells forage for spatially heterogeneous complex polysaccharides. They aimed to quantify the foraging behavior and interrogate its genetic basis. The results show that cells aggregate near complex polysaccharides and disperse when simpler byproducts are added. Dispersing cells tend to move towards the polysaccharide. The authors also use transcriptomics to attempt to understand which genes support each of these behaviors - with motility and transporter related genes being highly expressed during dispersal, as expected.

Strengths:

The paper is well written and builds on previous studies by some of the authors showing similar behavior by a different species of bacteria (Caulobacter) on another polysaccharide (xylan). The conceptual model presented at the end encapsulates the findings and provides an interesting hypothesis. I also find the observation of chemotaxis towards the polysaccharide in the experimental conditions interesting.

Weaknesses:

Much of the genetic analysis, as it stands, is quite speculative and descriptive. I found myself confused about many of the genes (e.g., quorum sensing) that pop up enriched during dispersal quite in contrast to my expectations. While the authors do discuss this in the text as worth following up on, I think the analysis as it stands is speculative about the behaviors observed. In the authors' defense, I acknowledge that it might have the potential to generate hypotheses and thus aid future studies.

Reviewer #2 (Public Review):

Summary:

The paper sets out to understand the mechanisms underlying the colonization and degradation of marine particles using a natural Vibrio isolate as a model. The data are measurements of motility and gene expressing using microfluidic devices and RNA sequencing. The results reveal that degradation products of alginate do stimulate motility but not chemotaxis. In contrast, alginate itself (the polymer) does stimulate chemotaxis. Further, the dispersal from degrading alginate is density dependent, increasing at higher density. The evidence for these claims are strong. From these the authors propose a narrative (Fig. 6) for growth and dispersal cycles in this system. The idea is that cells colonize and degrade alginate, this degradation stimulates motility and dispersal followed by chemotaxis to a new alginate source. This complete narrative has modest support in the data. A quantitative description of these dynamics awaits future studies.

Strengths:

The microfluidic measurements are the central strength of the paper. The density dependence claim is qualitatively supported by the data. The motility and chemotaxis claims are also well supported by the data. The presentation of the experiment and results are well done. The study serves to motivate a unifying picture of growth and dispersal in marine systems. This is a key process in the global carbon cycle.

Weaknesses:

Perhaps not a weakness, but a glimmer that this is not yet the full story. The RNA expression data show alginate lyase expression in response to digested alginate which is unexpected given the narrative articulated above. Why express lyases while leaving the polymer patch via motility? This question is addressed in the Discussion. A holistic and quantitative picture of the proposed process in Figure 6 awaits additional studies.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Stubbusch and coauthors examine the foraging behavior of a marine species consuming an abundant marine polysaccharide. Laboratory experiments in a microfluidic setup are complemented with transcriptomic analyses aiming at assessing the genetic bases of the observed behavior. Bacterial cells consuming the polysaccharide form cohesive aggregates, while start dispersing away when the byproduct of the digestion of the polysaccharide start accumulating. Dispersing cells, tend to be attracted by the polysaccharide. Expression data show that motility genes are enriched during the dispersal phase, as expected. Counterintuitively, in the same phase, genes for transporters and digestions of polysaccharide are also highly expressed.

Strengths:

The manuscript is very well written and easy to follow. The topic is interesting and timely. The genetic analyses provide a new, albeit complex, angle to the study of foraging behaviors in bacteria, adding to previous studies conducted on other species.

Weaknesses:

I find this paper very descriptive and speculative. The results of the genetic analyses are quite counterintuitive; therefore, I understand the difficulty of connecting them to the observations coming from experiments in the microfluidic device. However, they could be better placed in the literature of foraging - dispersal cycles, beyond bacteria. In addition, the interpretation of the results is sometimes confusing.

Reviewer #1 (Public Review):

The authors effectively delineate the differential distribution and behaviour of MNPs within the heart, noting that these cells can be characterised by their expression levels of csf1ra and mpeg1.1. Key findings include the identification of distinct origins for larval macrophage populations and the sustained presence of csf1ra-expressing cells on the surface of the adult heart. The study examines the embryonic development of these MNPs, revealing that csf1ra+ cells begin populating the heart from embryonic day 3, while mpeg1.1+ cells colonise the heart around day 10, with a significant increase by day 17. Given that the emergence of mpeg1.1+ cells coincides with the reported timing for the onset of haematopoietic stem cell-derived haematopoiesis, the authors combined kaede-lineage tracing experiments and mutant backgrounds to conclude that the earliest tissue-resident macrophages in the heart are derived from primitive haematopoiesis.

The authors also note that the spatial distribution of MNPs varies, with csf1ra+ cells found on the atrium and ventricle surfaces, while mpeg1.1+ cells are initially located on the surface but later distributed throughout the cardiac tissue. Notably, the study demonstrates that tissue-resident macrophages proliferate rapidly following cardiac injury. The authors observe an increased number of proliferating csf1ra+ cells, especially in csf1ra mutant zebrafish, which likely correspond to primitive-derived tissue-resident macrophages that rapidly respond to injury and contribute to the reduced scarring observed in these mutants.

This manuscript makes an important contribution to the field by enhancing our understanding of the ontogeny of tissue-resident macrophages in the heart and their cellular behaviour in a vertebrate model capable of heart regeneration.

Strengths:

This work presents a landmark study on the ontogeny and cellular behaviour of macrophages in the zebrafish heart as it comprehensively examines their development and distribution in both embryonic and adult stages.

One of the key strengths of this study is its thorough cellular description using a range of available genetic tools. By employing transgenic lines to differentiate between a few MNP subtypes, the authors provide a detailed and nuanced understanding of these cells' origins, distribution, and behaviour. This approach allows for high-resolution characterisation of MNP populations, revealing significant insights into their potential role in cardiac homeostasis and regeneration.

Furthermore, the study's findings are significant as they parallel those observed in mouse models, thereby reinforcing the validity and relevance of the zebrafish as a model organism for studying macrophage function in the context of cardiac injury. This comparative aspect underscores the evolutionary conservation of these cellular processes and enhances the study's impact.

Another notable strength is the use of ex vivo imaging techniques, which enable the authors to observe and study the dynamic behaviour of MNPs in heart tissue in real-time. This live imaging capability is crucial for understanding how these cells interact with their environment, particularly in response to cardiac injury. The ability to visualise MNP proliferation and movement provides valuable insights into the mechanisms underlying tissue repair and regeneration.

Weaknesses:

While the manuscript offers significant insights into the ontogeny and behaviour of MNPs in the zebrafish heart, a few limitations described below should be considered:

One potential issue lies in the lineage tracing experiments using the photoconversion Tg(csf1ra:Gal4); Tg(UAS:kaede) line. The authors photoconverted all cardiac tissue macrophages present at 2 days post-fertilisation (dpf) and examined the hearts of these fish at 21 dpf. Although photoconverted macrophages were still observed at 21 dpf, the majority of cells present in the heart at that time were non-photoconverted (cyan) csf1ra+ cells. While this suggests that early-seeded embryonic csf1ra+ macrophages are retained during late larval stages, the contribution of macrophages derived from haematopoietic stem cells (HSCs) might be overestimated. An important concern is that the kaede-converted cells could have proliferated during the embryonic timeframe analysed, thereby diluting and extinguishing the converted kaede protein. This dilution effect could lead to an underestimation of the contribution of primitive embryonic macrophages relative to the HSC-derived cells, resulting in an inaccurate assessment of the proportion of embryonic-derived tissue-resident macrophages over time.

Moreover, the study reports no significant difference in immune cell numbers in the hearts of cmyb-/- mutants, which have normal primitive haematopoiesis but lack HSCs, at 5 dpf. Given the authors' suggestion that mpeg+ cells originate from the HSC wave, it is essential to assess the number of mpeg+ cells in these mutants at later stages. This assessment would clarify whether mpeg+ cells are indeed HSC-derived or if csf1ra+ cells later switch on mpeg expression. Without this additional data, conclusions about the origins of mpeg+ cells remain speculative.

The study's reliance on available genetic tools, while a strength, also introduces limitations. The use of only a few transgenic lines will not fully capture the complexity and diversity of MNP populations, leading to an incomplete understanding of their roles and dynamics.

Furthermore, while the use of ex vivo imaging provides dynamic insights into cell behaviour, it may not fully capture the complexity of in vivo conditions, possibly overlooking interactions and influences present in the living organism.

The manuscript would benefit from increasing the sample sizes to ensure the robustness of the findings. The use of Phalloidin staining to delineate single cells more accurately would also enhance the precision of cell counting and improve the overall data quality.

The study could also benefit from a more in-depth exploration of the functional consequences of MNP heterogeneity in the heart. While the cellular characterisations are thorough, the molecular and regulatory insights provided by the study are limited to a couple of RT-PCRs for some known genes.

Overall, the manuscript by Moyse and colleagues significantly advances our understanding of the ontogeny and behaviour of macrophages in the zebrafish heart, revealing important parallels with mammalian models. However, the points above should be carefully considered when interpreting the results presented in this study.

eLife assessment

The manuscript presented by Moyse and colleagues provides valuable insight into the origin, morphology, dynamics, and behavior of several populations of mononuclear phagocytes in the zebrafish heart. The study presents solid evidence through the use of transgenic lines and live imaging, although some limitations related to lineage tracing and molecular profiles should be considered. This work exemplifies the use of zebrafish as a model to study the role of leukocytes in cardiac development and regeneration and potentially draw broader interest to biologists working in immunology fields.

Reviewer #2 (Public Review):

In this manuscript, Moyse et. al. investigated the origins and potential functions of distinct populations of mononuclear phagocytes (MNPS) in the heart of developing and adult zebrafish. First, the authors demonstrate that the embryonic zebrafish heart contains macrophages early in development and that mpeg1.1 and csf1ra expressing macrophages vary across time and location and present that cardiac tissue macrophages (cTMs) in the juvenile heart are derived by primitive hematopoiesis. By combining the two transgenes, the authors demonstrate that there are 3 distinct (later determined to be 4) subpopulations of MNPs in adult hearts and that the distribution of these subtypes is distinct within the heart consistent with differing distributions of primitive and definitive macrophages in mammalian hearts. Further analysis of these populations demonstrates distinct morphologies of the subpopulations and analysis of markers conserved in mammals demonstrates distinct expression profiles as well. The authors go on to demonstrate that these subpopulations also demonstrate distinct behaviors via ex-vivo imaging. Lastly, the authors investigated the roles of these subpopulations in a model of cardiac injury in adult zebrafish and demonstrated that primitive-derived cTMs proliferate after injury consistent with mammalian models and that the proliferation of these macrophages likely results in reduced scarring in csf1ra mutants which have reduced recruitment of pro-inflammatory definitive macrophages. The data presented in this manuscript provides solid evidence that zebrafish MNPs behave consistently with those in mammals and further solidifies the use of zebrafish models as a useful tool in studying the role of these cells in cardiac repair and regeneration.

The data presented in this manuscript strongly supports the conclusions made by the authors and utilizes novel techniques. The authors appear to have achieved the goals they set out to investigate. The use of ex-vivo imaging to visualize the movement of these macrophage populations within the heart is especially compelling. The combined use of commonly used transgenic reporters for zebrafish macrophages is a very nice use of existing tools to address new questions and highlight the distinct populations of macrophages. While the overall manuscript is very strong and is likely to have a great impact on the field, there are a few weaknesses that should be addressed prior to acceptance:

(1) The reasoning for N used in many of these experiments is not addressed, nor is the question of the number of times experiments were performed. For purposes of rigor and reproducibility, these questions should be addressed in the methods.

(2) In investigating homologs of zebrafish and mammalian genes, the inclusion of additional classical markers and novel markers of subpopulations highlighted in numerous recent studies using single-cell RNA sequencing would greatly add to the impact.

(3) The description of the RT-PCR experiment is not included in the methods. Detailed methods should be provided including probe sequences. Additionally, a quantitative method of presenting this data would strengthen the conclusions presented here as well as the inclusion of additional markers as discussed previously.

Reviewer #3 (Public Review):

In this manuscript, Moyse et al. build on previously published data and investigate several subtypes of mononuclear phagocytes within the larval, juvenile, and adult zebrafish heart. Through the use of mpeg1.1 and csfr1a transgenic lines, the authors characterize the seeding of macrophages in the embryonic and larval heart and describe localization, proportions, morphology, and behavior of several subtypes of mpeg1.1 and csfr1a macrophages in the adult uninjured heart. The authors further provide an analysis of marker gene expression in the differing macrophage subtypes in the uninjured adult heart. Lastly, the authors perform analyses of how these populations respond to cardiac injury and show that csfr1a is important for the proportion and proliferation of these different subtypes of macrophages in the heart.

While the presence of cardiac resident macrophages and their importance in heart regeneration and cardiac disease have been extensively studied in the mouse, the same attention has only recently been given to macrophages in the adult zebrafish heart. This study provides insight into many parallels that exist between resident macrophages in the mouse and zebrafish heart, and while not especially novel, this concept is important for the zebrafish cardiac field. Overall, the conclusions of this study are mostly well supported by the data, but further analysis of marker gene expression in the various macrophage subtypes described would be an important and useful addition for zebrafish researchers studying macrophages in heart regeneration. For example, how are markers of cardiac resident macrophages (described in Wei et al, doi: 10.7554/eLife.84679) expressed in the different mpeg1.1 and csfr1a populations?

eLife assessment

This paper explores the relationships among evolutionary and epidemiological quantities in influenza, and presents fundamental findings that substantially advance our understanding of the drivers of influenza epidemics. The authors use a rich set of data sources to gather and analyze compelling evidence on the roles of genetic distance, other influenza dynamics and epidemiological indicators in predicting influenza epidemics. The central findings highlight the significant influence of genetic distance on A(H3N2) virus epidemiology and emphasize the role of A(H1N1) virus incidence in shaping A(H3N2) epidemics, suggesting subtype interference as a key factor. This paper also makes relevant data available to the research community.

Reviewer #1 (Public Review):

Summary:

The authors aimed to investigate the contribution of antigenic drift in the HA and NA genes of seasonal influenza A(H3N2) virus to their epidemic dynamics. Analyzing 22 influenza seasons before the COVID-19 pandemic, the study explored various antigenic and genetic markers, comparing them against indicators characterizing the epidemiology of annual outbreaks. The central findings highlight the significant influence of genetic distance on A(H3N2) virus epidemiology and emphasize the role of A(H1N1) virus incidence in shaping A(H3N2) epidemics, suggesting subtype interference as a key factor.

Major Strengths:

The paper is well-organized, written with clarity, and presents a comprehensive analysis. The study design, incorporating a span of 22 seasons, provides a robust foundation for understanding influenza dynamics. The inclusion of diverse antigenic and genetic markers enhances the depth of the investigation, and the exploration of subtype interference adds valuable insights.

Major Weaknesses:

While the analysis is thorough, some aspects require deeper interpretation, particularly in the discussion of certain results. Clarity and depth could be improved in the presentation of findings, and minor adjustments are suggested. Furthermore, the evolving dynamics of H3N2 predominance post-2009 need better elucidation.

Comments on revised version:

The authors have addressed each of the comments well. I have no further comments.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The authors aimed to investigate the contribution of antigenic drift in the HA and NA genes of seasonal influenza A(H3N2) virus to their epidemic dynamics. Analyzing 22 influenza seasons before the COVID-19 pandemic, the study explored various antigenic and genetic markers, comparing them against indicators characterizing the epidemiology of annual outbreaks. The central findings highlight the significant influence of genetic distance on A(H3N2) virus epidemiology and emphasize the role of A(H1N1) virus incidence in shaping A(H3N2) epidemics, suggesting subtype interference as a key factor. 

Major Strengths: 

The paper is well-organized, written with clarity, and presents a comprehensive analysis. The study design, incorporating a span of 22 seasons, provides a robust foundation for understanding influenza dynamics. The inclusion of diverse antigenic and genetic markers enhances the depth of the investigation, and the exploration of subtype interference adds valuable insights. 

Major Weaknesses: 

While the analysis is thorough, some aspects require deeper interpretation, particularly in the discussion of certain results. Clarity and depth could be improved in the presentation of findings. Furthermore, the evolving dynamics of H3N2 predominance post-2009 need better elucidation.  

Reviewer #2 (Public Review): 

Summary: This paper aims to achieve a better understanding of how the antigenic or genetic compositions of the dominant influenza A viruses in circulation at a given time are related to key features of seasonal influenza epidemics in the US. To this end, the authors analyze an extensive dataset with a range of statistical, data science and machine learning methods. They find that the key drivers of influenza A epidemiological dynamics are interference between influenza A subtypes and genetic divergence, relative to the previous one or two seasons, in a broader range of antigenically related sites than previously thought. 

Strengths: A thorough investigation of a large and complex dataset. 

Weaknesses: The dataset covers a 21 year period which is substantial by epidemiological standards, but quite small from a statistical or machine learning perspective. In particular, it was not possible to follow the usual process and test predictive performance of the random forest model with an independent dataset. 

Reviewer #3 (Public Review): 

Summary: 

This paper explores the relationships among evolutionary and epidemiological quantities in influenza, using a wide range of datasets and features, and using both correlations and random forests to examine, primarily, what are the drivers of influenza epidemics. It's a strong paper representing a thorough and fascinating exploration of potential drivers, and it makes a trove of relevant data readily available to the community. 

Strengths: 

This paper makes links between epidemiological and evolutionary data for influenza. Placing each in the context of the other is crucial for understanding influenza dynamics and evolution and this paper does a thorough job of this, with many analyses and nuances. The results on the extent to which evolutionary factors relate to epidemic burden, and on interference among influenza types, are particularly interesting. The github repository associated with the paper is clear, comprehensive, and well-documented. 

Weaknesses: 

The format of the results section can be hard to follow, and we suggest improving readability by restructuring and simplifying in some areas. There are a range of choices made about data preparation and scaling; the authors could explore sensitivity of the results to some of these. 

Response to public reviews

We appreciate the positive comments from the reviewers and have implemented or responded to all of the reviewers’ recommendations.

In response to Reviewer 1, we expand on the potential drivers and biological implications of the findings pointed out in their specific recommendations. For example, we now explicitly mention that antigenically distinct 3c.2a and 3c.3a viruses began to co-circulate in 2012 and underwent further diversification during subsequent seasons in our study. We note that, after the 2009 A(H1N1) pandemic, the mean fraction of influenza positive cases typed as A(H3N2) in A(H3N2) dominant seasons is lower compared to A(H3N2) dominant seasons prior to 2009. We propose that the weakening of A(H3N2) predominance may be linked to the diversification of A(H3N2) viruses during the 2010s, wherein multiple antigenically distinct clades with similar fitness circulated in each season, as opposed to a single variant with high fitness.

In response to Reviewer 2, we agree that it would be ideal and best practice to measure model performance with an independent test set, but our dataset includes only ~20 seasons. Predictions of independent test sets of 2-3 seasons had unstable performance, which indicates we do not have sufficient power to measure model performance with a test set this small. In the revised manuscript, we provide more justification and clarification of our methodology. Instead of testing model performance on an independent test set, we use leave-one-season-out cross-validation to train models and measure model performance, wherein each “assessment” set contains one season of data (predicted by the model), and the corresponding “analysis” set (“fold”) contains the remaining seasons. This approach is roughly analogous to splitting data into training and test sets, but all seasons are used at some point in the training of the model (Kuhn & Johnson, 2019).

In response to Reviewer 3, we follow the reviewer’s advice to put the Methods section before the Results section. Concerning Reviewer 3’s question about the sensitivity of our results to data preparation and rescaling, we provide more justification and clarification of our methodology in the revised manuscript. In our study, we adjust influenza type/subtype incidences for differences in reporting between the pre- and post-2009 pandemic periods and across HHS regions. We adjust for differences in reporting between the pre- and post-2009 periods because the US CDC and WHO increased laboratory testing capacity in response to the 2009 A(H1N1) pandemic, which led to substantial, long-lasting improvements to influenza surveillance that are still in place today. Figure 1 - figure supplement 2 shows systematic increases in influenza test volume in all HHS regions after the 2009 pandemic. Given the substantial increase in test volume after 2009, we opted to keep the time trend adjustment for the pre- and post-2009 pandemic periods and evaluate whether adjusting for regional reporting differences affects our results. When estimating univariate correlations between various A(H3N2) epidemic metrics and evolutionary indicators, we found qualitatively equivalent results when adjusting for both pre- and post-2009 pandemic reporting and regional reporting versus only adjusting for the pre- and post-2009 pandemic reporting.

Reviewer #1 (Recommendations For The Authors): 

Specific comments: 

(1) Line 155-156. Request for a reference for: "Given that protective immunity wanes after 1-4 years" 

We now include two references (He et al. 2015 and Wraith et al. 2022), which were cited at the beginning of the introduction when referring to the duration of protective immunity for antigenically homologous viruses. (Lines 640-642 in revised manuscript)

(2) Line 162-163: Request a further explanation of the negative correlation between seasonal diversity of HA and NA LBI values and NA epitope distance. Clarify biological implications to aid reader understanding. 

In the revised manuscript we expand on the biological implications of A(H3N2) virus populations characterized by high antigenic novelty and low LBI diversity.

Lines 649-653:

“The seasonal diversity of HA and NA LBI values was negatively correlated with NA epitope distance (Figure 2 – figure supplements 5 – 6), with high antigenic novelty coinciding with low genealogical diversity. This association suggests that selective sweeps tend to follow the emergence of drifted variants with high fitness, resulting in seasons dominated by a single A(H3N2) variant rather than multiple cocirculating clades.”

(3) Figure S3 legend t-2 may be marked as t-1. 

Thank you for catching this. We have fixed this typo. Note: Figure S3 is now Figure 2 – figure supplement 5.

(4) Lines 201-214. The key takeaways from the analysis of subtype dominance are ultimately not clear. It also misses the underlying dynamics that H3N2 predominance following an evolutionary change has waned since 2009.

In the revised manuscript we elaborate on key takeaways concerning the relationship between antigenic drift and A(H3N2) dominance. We also add a caveat noting that A(H3N2) predominance is weaker during the post-2009 period, which may be linked to the diversification of A(H3N2) lineages after 2012. We do not know of a reference that links the diversification of A(H3N2) viruses in the 2010s to a particular evolutionary change. Therefore, we do not attribute the diversification of A(H3N2) viruses to a specific evolutionary change in A(H3N2) variants circulating at the time (A/Perth/16/2009-like strains (PE09)). Instead, we allude to the potential role of A(H3N2) diversification in creating multiple co-circulating lineages that may have less of a fitness advantage.

Lines 681-703:

“We explored whether evolutionary changes in A(H3N2) may predispose this subtype to dominate influenza virus circulation in a given season. A(H3N2) subtype dominance – the proportion of influenza positive samples typed as A(H3N2) – increased with H3 epitope distance (t – 2) (R2 = 0.32, P = 0.05) and N2 epitope distance (t – 1) (R2 = 0.34, P = 0.03) (regression results: Figure 4; Spearman correlations: Figure 3 – figure supplement 1). Figure 4 illustrates this relationship at the regional level across two seasons in which A(H3N2) was nationally dominant, but where antigenic change differed. In 2003-2004, we observed widespread dominance of A(H3N2) viruses after the emergence of the novel antigenic cluster, FU02 (A/Fujian/411/2002-like strains). In contrast, there was substantial regional heterogeneity in subtype circulation during 2007-2008, a season in which A(H3N2) viruses were antigenically similar to those circulating in the previous season. Patterns in type/subtype circulation across all influenza seasons in our study period are shown in Figure 4 – figure supplement 1. As observed for the 2003-2004 season, widespread A(H3N2) dominance tended to coincide with major antigenic transitions (e.g.,

A/Sydney/5/1997 (SY97) seasons, 1997-1998 to 1999-2000; A/California/7/2004 (CA04) season, 20042005), though this was not universally the case (e.g., A/Perth/16/2009 (PE09) season, 2010-2011). 

After the 2009 A(H1N1) pandemic, A(H3N2) dominant seasons still occurred more frequently than A(H1N1) dominant seasons, but the mean fraction of influenza positive cases typed as A(H3N2) in A(H3N2) dominant seasons was lower compared to A(H3N2) dominant seasons prior to 2009. Antigenically distinct 3c.2a and 3c.3a viruses began to co-circulate in 2012 and underwent further diversification during subsequent seasons in our study (https://nextstrain.org/seasonal-

flu/h3n2/ha/12y@2024-05-13) (Dhanasekaran et al., 2022; Huddleston et al., 2020; Yan et al., 2019). The decline in A(H3N2) predominance during the post-2009 period may be linked to the genetic and antigenic diversification of A(H3N2) viruses, wherein multiple lineages with similar fitness co-circulated in each season.”

(5) Line 253-255: It would be beneficial to provide a more detailed interpretation of the statement that "pre-2009 seasonal A(H1N1) viruses may limit the circulation of A(H3N2) viruses to a greater extent than A(H1N1)pdm09 viruses." Elaborate on the cause-and-effect relationship within this statement.

In the revised manuscript we suggest that seasonal A(H1N1) viruses may interfere with the circulation of A(H3N2) viruses to a greater extent than A(H1N1)pdm09 viruses, because seasonal A(H1N1) viruses and A(H3N2) are more closely related, and thus may elicit stronger cross-reactive T cell responses.

Lines 738-745:

“The internal gene segments NS, M, NP, PA, and PB2 of A(H3N2) viruses and pre-2009 seasonal A(H1N1) viruses share a common ancestor (Webster et al., 1992) whereas A(H1N1)pdm09 viruses have a combination of gene segments derived from swine and avian reservoirs that were not reported prior to the 2009 pandemic (Garten et al., 2009; Smith et al., 2009). Non-glycoprotein genes are highly conserved between influenza A viruses and elicit cross-reactive antibody and T cell responses (Grebe et al., 2008; Sridhar, 2016). Because pre-2009 seasonal A(H1N1) viruses and A(H3N2) are more closely related, we hypothesized that seasonal A(H1N1) viruses could potentially limit the circulation of A(H3N2) viruses to a greater extent than A(H1N1)pdm09 viruses, due to greater T cell-mediated cross-protective immunity.”

(6) In the results section, many statements report statistical results of correlation analyses. Consider providing further interpretations of these results, such as the implications of nonsignificant correlations and how they support or contradict the hypothesis or previous studies. For example, the statement on line 248 regarding the lack of significant correlation between influenza B epidemic size and A(H3N2) epidemic metrics would benefit from additional discussion on what this non-significant correlation signifies and how it relates to the hypothesis or previous research. 

In the Discussion section, we suggest that the lack of an association between influenza B circulation and A(H3N2) epidemic metrics is due to few T and B cell epitopes shared between influenza A and B viruses (Terajima et al., 2013).

Lines 1005-1007 in revised manuscript (Lines 513-515 in original manuscript): 

“Overall, we did not find any indication that influenza B incidence affects A(H3N2) epidemic burden or timing, which is not unexpected, given that few T and B cell epitopes are shared between the two virus types (Terajima et al., 2013).”

Minor comments: 

(1) Line 116-122: Include a summary statistical description of all collected data sets, detailing the number of HA and NA sequence data and their sources. Briefly describe subsampled data sets, specifying preferences (e.g., the number of HA or NA sequence data collected from each region). 

In our revised manuscript we now include supplementary tables that summarize the number of A/H3 and

A/N2 sequences in each subsampled dataset, aggregated by world region, for all seasons combined (Figure 2 - table supplements 1 - 2). We also include supplementary figures showing the number of sequences collected in each month and each season in North America versus the other nine world regions combined (Figure 2 - figure supplements 1 - 2). Subsampled datasets are plotted individually in the figures below but individual time series are difficult to discern due to minor differences in sequence counts across the datasets.

(2) Figure 7A: Due to space limitations, consider rounding numbers on the x-axis to whole numbers for clarity. 

Thank you for this suggestion. In the revised manuscript we round numbers in the axes of Figure 7A (Figure 9A in the revised manuscript) so that the axes are less crowded.

(3) Figure 4C & Figure 4D: Note that Region 10 (purple) data were unavailable for seasons before 2009 (lines 1483-1484). Label each region on the map with its respective region number (1 to 10) and indicate this in the legend for easy identification. 

In our original submission, the legend for Figure 4 included “Data for Region 10 (purple) were not available for seasons prior to 2009” at the end of the caption. We have moved this sentence, as well as other descriptions that apply to both C and D, so that they follow the sentence “C-D. Regional patterns of influenza type and subtype incidence during two seasons when A(H3N2) was nationally dominant.”

In our revised manuscript, Figure 4, and Figure 4 - figure supplement 1 (Figure S10 in original submission) include labels for each HHS region.

We did not receive specific recommendations from Reviewer #2. However, our responses to Reviewer #3 addresses the study’s weaknesses mentioned by Reviewer #2.

Reviewer #3 (Recommendations For The Authors): 

This paper explores the relationships among evolutionary and epidemiological quantities in influenza, using a wide range of datasets and features, and using both correlations and random forests to examine, primarily, what are the drivers of influenza epidemics. 

This is a work horse of paper, in the volumes of data that are analyzed and the extensive analysis that is done. The data that are provided are a treasure trove resource for influenza modelers and for anyone interested in seeing influenza surveillance data in the context of evolution, and evolutionary information in the context of epidemiology. 

L53 - end of sentence "and antigenic drift": not sure this fits, explain? I thought this sentence was in contrast to antigenic drift.

Thank you for catching this. We did not intend to include “and antigenic drift” at the end of this sentence and have removed it (Line 59).

Para around L115: would using primarily US data be a limitation, because it's global immunity that shapes success of strains? Or, how much does each country's immunity and vaccination and so on actually shape what strains succeed there, compared to global/international factors? 

The HA and NA phylogenetic trees in our study are enriched with US sequences because our study focuses on epidemiological dynamics in the US, and we wanted to prioritize A(H3N2) viruses that the US human population encountered in each season. We agree with the reviewer that the world population may be the right scale to understand how immunity, acquired by vaccination or natural infection, may shape the emergence and success of new lineages that will go on to circulate globally. However, our study assesses the overall impact of antigenic drift on regional A(H3N2) epidemic dynamics in the US. In other words, our driving question is whether we can predict the population-level impact of an A(H3N2) variant in the US, conditional on this particular lineage having established in the US and circulating at relatively high levels. We do not assess the global or population-level factors that may influence which A(H3N2) virus lineages are successful in a given location or season.

We have added a clarifying sentence to the end of the Introduction to narrow the scope of the paper for the reader. 

Line 114-116: “Rather than characterize in situ evolution of A(H3N2) lineages circulating in the U.S., we study the epidemiological impacts of antigenic drift once A(H3N2) variants have arrived on U.S. soil and managed to establish and circulate at relatively high levels.”

In the Results section, I found the format hard to follow, because of the extensive methodological details, numbers with CIs and long sentences. Sentences sometimes included the question, definitions of variables, and lists. For example at line 215 we have: "Next, we tested for associations between A(H3N2) evolution and epidemic timing, including onset week, defined as the winter changepoint in incidence [16], and peak week, defined as the first week of maximum incidence; spatiotemporal synchrony, measured as the variation (standard deviation, s.d.) in regional onset and peak timing; and epidemic speed, including seasonal duration and the number of weeks from onset to peak (Table 2, Figure S11)". I would suggest putting the methods section first, using shorter sentences, separating lists from the question being asked, and stating what was found without also putting in all the extra detail. Putting the methods section before the results might reduce the sense that you have to explain what you did and how in the results section too.

Thank you for suggesting how to improve the readability of the Results section. In the revised manuscript, we follow the reviewer’s advice to put the Methods section before the Results section. Although eLife formatting requirements specify the order: Introduction, Results, Discussion, and Methods, the journal allows for the Methods section to follow the Introduction when it makes sense to do so. We agree with the reviewer that putting the Methods section before the Results section makes our results easier to follow because we no longer need to introduce methodological details at the beginning of each set of results.

L285 in the RF you remove variables without significant correlations with the target variables, but isn't one of the aims of RF to uncover relationships where a correlation might not be evident, and in part to reveal combinations of features that give the targeted outcome? Also with the RF, I am a bit concerned that you could not use the leave-one-out approach because it was "unstable" - presumably that means that you obtain quite different results if you leave out a season. How robust are these results, and what are the most sensitive aspects? Are the same variables typically high in importance if you leave out a season, for example? What does the scatterplot of observed vs predicted epidemic size (as in Fig 7) look like if each prediction is for the one that was left out (i.e. from a model trained on all the rest)? In my experience, where the RF is "unstable", that can look pretty terrible even if the model trained on all the data looks great (as does Figure 7). In any case I think it's worth discussing sensitivity.

(1) In response to the reviewer’s first question, we explain our rationale for not including all candidate predictors in random forest and penalized regression models. 

Models trained with different combinations of predictors can have similar performance, and these combinations of predictors can include variables that do not necessarily have strong univariate associations with the target variable. The performance of random forest and LASSO regression models are not sensitive to redundant or irrelevant predictors (see Figure 10.2 in Kuhn & Johnson, 2019). However,  if our goal is variable selection rather than strictly model performance, it is considered best practice to remove collinear, redundant, and/or irrelevant variables prior to training models (see section 11.3 in Kuhn & Johnson, 2019). In both random forest and LASSO regression models, if there are highly collinear variables that are useful for predicting the target variable, the predictor chosen by the model becomes a random selection. In random forest models, these highly collinear variables will be used in all splits across the forest of decision trees, and this redundancy dilutes variable importance scores. Thus, failing to minimize multicollinearity prior to model training could result in some variables having low rankings and the appearance of being unimportant, because their importance scores are overshadowed by those of the highly correlated variables. Our rationale for preprocessing predictor data follows the philosophy of Kuhn & Johnson, 2019, who recommend including the minimum possible set of variables that does not compromise model performance. Even if a particular model is insensitive to extra predictors, Kuhn and John explain that “removing predictors can reduce the cost of acquiring data or improve the throughput of the software used to make predictions.”

In the revised manuscript, we include more details about our steps for preprocessing predictor data. We also follow the reviewer’s suggestion to include all evolutionary predictors in variable selection analyses, regardless of whether they have strong univariate correlations with target outcomes, because the performance of random forest and LASSO regression models is not affected by redundant predictors. 

Including additional predictors in our variable selection analyses does not change our conclusions. As reported in our original manuscript, predictors with strong univariate correlations with various epidemic metrics were the highest ranked features in both random forest and LASSO regression models.

Lines 523-563:

“Preprocessing of predictor data: The starting set of candidate predictors included all viral fitness metrics: genetic and antigenic distances between current and previously circulating strains and the standard deviation and Shannon diversity of H3 and N2 LBI values in the current season. To account for potential type or subtype interference, we included A(H1N1) or A(H1N1)pdm09 epidemic size and B epidemic size in the current and prior season and the dominant IAV subtype in the prior season (Lee et al., 2018). We included A(H3N2) epidemic size in the prior season as a proxy for prior natural immunity to A(H3N2). To account for vaccine-induced immunity, we considered four categories of predictors and included estimates for the current and prior seasons: national vaccination coverage among adults (18-49 years coverage × ≥ 65 years coverage), adjusted A(H3N2) vaccine effectiveness (VE), a combined metric of vaccination coverage and A(H3N2) VE (18-49 years coverage × ≥ 65 years coverage × VE), and H3 and N2 epitope distances between naturally circulating A(H3N2) viruses and the U.S. A(H3N2) vaccine strain in each season. We could not include a predictor for vaccination coverage in children or consider cladespecific VE estimates, because these data were not available for most seasons in our study.

Random forest and LASSO regression models are not sensitive to redundant (highly collinear) features (Kuhn & Johnson, 2019), but we chose to downsize the original set of candidate predictors to minimize the impact of multicollinearity on variable importance scores. For both types of models, if there are highly collinear variables that are useful for predicting the target variable, the predictor chosen by the model becomes a random selection (Kuhn & Johnson, 2019). In random forest models, these highly collinear variables will be used in all splits across the forest of decision trees, and this redundancy dilutes variable importance scores (Kuhn & Johnson, 2019). We first confirmed that none of the candidate predictors had zero variance or near-zero variance. Because seasonal lags of each viral fitness metric are highly collinear, we included only one lag of each evolutionary predictor, with a preference for the lag that had the strongest univariate correlations with various epidemic metrics. We checked for multicollinearity among the remaining predictors by examining Spearman’s rank correlation coefficients between all pairs of predictors. If a particular pair of predictors was highly correlated (Spearman’s 𝜌 > 0.8), we retained only one predictor from that pair, with a preference for the predictor that had the strongest univariate correlations with various epidemic metrics. Lastly, we performed QR decomposition of the matrix of remaining predictors to determine if the matrix is full rank and identify sets of columns involved in linear dependencies. This step did not eliminate any additional predictors, given that we had already removed pairs of highly collinear variables based on Spearman correlation coefficients. 

After these preprocessing steps, our final set of model predictors included 21 variables, including 8 viral evolutionary indicators: H3 epitope distance (t – 2), HI log2 titer distance (t – 2), H3 RBS distance (t – 2), H3 non-epitope distance (t – 2), N2 epitope distance (t – 1), N2 non-epitope distance (t – 1), and H3 and N2 LBI diversity (s.d.) in the current season; 6 proxies for type/subtype interference and prior immunity:

A(H1N1) and B epidemic sizes in the current and prior season, A(H3N2) epidemic size in the prior season, and the dominant IAV subtype in the prior season; and 7 proxies for vaccine-induced immunity: A(H3N2) VE in the current and prior season, H3 and N2 epitope distances between circulating strains and the vaccine strain in each season, the combined metric of adult vaccination coverage × VE in the current and prior season, and adult vaccination coverage in the prior season.”

(2) Next, we clarify our model training methodology to address the reviewer’s second point about using a leave-one-out cross-validation approach.

We believe the reviewer is mistaken; we use a leave-one-season-out validation approach which lends some robustness to the predictions. In our original submission, we stated “We created each forest by generating 3,000 regression trees from 10 repeats of a leave-one-season-out (jackknife) cross-validated sample of the data. Due to the small size of our dataset, evaluating the predictive accuracy of random forest models on a quasi-independent test set produced unstable estimates.” (Lines 813-816 in the original manuscript)

To clarify, we use leave-one-season-out cross-validation to train models and measure model performance, wherein each “assessment” set contains one season of data (predicted by the model), and the corresponding “analysis” set (“fold”) contains the remaining seasons. This approach is roughly analogous to splitting data into training and test sets, but all seasons are used at some point in the training of the model (see Section 3.4 in Kuhn & Johnson, 2019). To reduce noise, we generated 10 bootstrap resamples of each fold and averaged the RMSE and R2 values of model predictions from resamples. 

Although it would be ideal and best practice to measure model performance with an independent test set, our dataset includes only ~20 seasons. We found that predictions of independent test sets of 2-3 seasons had unstable performance, which indicates we do not have sufficient power to measure model performance with a test set this small. Further, we suspect that large antigenic jumps in a small subset of seasons further contribute to variation in prediction accuracy across randomly selected test sets. Our rationale for using cross-validation instead of an independent test set is best described in Section 4.3 of Kuhn and Johnson’s book “Applied Predictive Modeling” (Kuhn & Johnson, 2013):

“When the number of samples is not large, a strong case can be made that a test set should be avoided because every sample may be needed for model building. Additionally, the size of the test set may not have sufficient power or precision to make reasonable judgements. Several researchers (Molinaro 2005; Martin and Hirschberg 1996; Hawkins et al. 2003) show that validation using a single test set can be a poor choice. Hawkins et al. (2003) concisely summarize this point: “holdout samples of tolerable size [...] do not match the cross-validation itself for reliability in assessing model fit and are hard to motivate. “Resampling methods, such as cross-validation, can be used to produce appropriate estimates of model performance using the training set. These are discussed in length in Sect.4.4. Although resampling techniques can be misapplied, such as the example shown in Ambroise and McLachlan (2002), they often produce performance estimates superior to a single test set because they evaluate many alternate versions of the data.”

In our revised manuscript, we provide additional clarification of our methods (Lines 574-590):

“We created each forest by generating 3,000 regression trees. To determine the best performing model for each epidemic metric, we used leave-one-season-out (jackknife) cross-validation to train models and measure model performance, wherein each “assessment” set is one season of data predicted by the model, and the corresponding “analysis” set contains the remaining seasons. This approach is roughly analogous to splitting data into training and test sets, but all seasons are used at some point in the training of each model (Kuhn & Johnson, 2019). Due to the small size of our dataset (~20 seasons), evaluating the predictive accuracy of random forest models on a quasi-independent test set of 2-3 seasons produced unstable estimates. Instead of testing model performance on an independent test set, we generated 10 bootstrap resamples (“repeats”) of each analysis set (“fold”) and averaged the predictions of models trained on resamples (Kuhn & Johnson, 2013, 2019). For each epidemic metric, we report the mean root mean squared error (RMSE) and R2 of predictions from the best tuned model. We used permutation importance (N = 50 permutations) to estimate the relative importance of each predictor in determining target outcomes. Permutation importance is the decrease in prediction accuracy when a single feature (predictor) is randomly permuted, with larger values indicating more important variables. Because many features were collinear, we used conditional permutation importance to compute feature importance scores, rather than the standard marginal procedure (Altmann et al., 2010; Debeer & Strobl, 2020; Strobl et al., 2008; Strobl et al., 2007).”

(3) In response to the reviewer’s question about the sensitivity of results when one season is left out, we clarify that the variable importance scores in Figure 8 and model predictions in Figure 9 were generated by models tuned using leave-one-season-out cross-validation. 

As explained above, in our leave-one-season-out cross-validation approach, each “assessment” set contains one season of data predicted by the model, and the corresponding “analysis” set (“fold”) contains the remaining seasons. We generated predictions of epidemic metrics and variable importance rankings by averaging the model output of 10 bootstrap resamples of each cross-validation fold. 

In Lines 791-806, we describe which epidemic metrics have the highest prediction accuracy and report that random forest models tend to underpredict most epidemic metrics in seasons with high antigenic novelty:

“We measured correlations between observed values and model-predicted values at the HHS region level. Among the various epidemic metrics, random forest models produced the most accurate predictions of A(H3N2) subtype dominance (Spearman’s 𝜌 = 0.95, regional range = 0.85 – 0.97), peak incidence (𝜌 = 0.91, regional range = 0.72 – 0.95), and epidemic size (𝜌 = 0.9, regional range = 0.74 – 0.95), while predictions of effective 𝑅! and epidemic intensity were less accurate (𝜌 = 0.81, regional range = 0.65 – 0.91; 𝜌 = 0.78, regional range = 0.63 – 0.92, respectively) (Figure 9). Random forest models tended to underpredict most epidemic targets in seasons with substantial H3 antigenic transitions, in particular the SY97 cluster seasons (1998-1999, 1999-2000) and the FU02 cluster season (2003-2004) (Figure 9). 

For epidemic size and peak incidence, seasonal predictive error – the root-mean-square error (RMSE) across all regional predictions in a season – increased with H3 epitope distance (epidemic size, Spearman’s 𝜌 = 0.51, P = 0.02; peak incidence, 𝜌 = 0.63, P = 0.004) and N2 epitope distance (epidemic size, 𝜌 = 0.48, P = 0.04; peak incidence, 𝜌 = 0.48, P = 0.03) (Figure 9 – figure supplements 1 – 2). For models of epidemic intensity, seasonal RMSE increased with N2 epitope distance (𝜌 = 0.64, P = 0.004) but not H3 epitope distance (𝜌 = 0.06, P = 0.8) (Figure 9 – figure supplements 1 – 2). Seasonal RMSE of effective 𝑅! and subtype dominance predictions did not correlate with H3 or N2 epitope distance (Figure 9 – figure supplements 1 – 2).”

I think the competition (interference) results are really interesting, perhaps among the most interesting aspects of this work. 

Thank you! We agree that our finding that subtype interference has a greater impact than viral evolution on A(H3N2) epidemics is one of the more interesting results in the study.

Have you seen the paper by Barrat-Charlaix et al? They found that LBI was not good predicting frequency dynamics (see https://pubmed.ncbi.nlm.nih.gov/33749787/); instead, LBI was high for sequences like the consensus sequence, which was near to future strains. LBI also was not positively correlated with epidemic impact in Figure S7.

The local branching index (LBI) measures the rate of recent phylogenetic branching and approximates relative fitness among viral clades, with high LBI values representing greater fitness (Neher et al. 2014).

Two of this study’s co-authors (John Huddleston and Trevor Bedford) are also co-authors of BarratCharlaix et al. 2021. Barrat-Charlaix et al. 2021 assessed the performance of LBI in predicting the frequency dynamics and fixation of individual amino acid substitutions in A(H3N2) viruses. Our study is not focused on predicting the future success of A(H3N2) clades or the frequency dynamics or probability of fixation of individual substitutions. Instead, we use the standard deviation and Shannon diversity of LBI values in each season as a proxy for genealogical (clade-level) diversity. We find that, at a seasonal level, low diversity of H3 or N2 LBI values in the current season correlates with greater epidemic intensity, higher transmission rates, and shorter seasonal duration.

In the Discussion we provide an explanation for these correlation results (Lines 848-857): 

“The local branching index (LBI) is traditionally used to predict the success of individual clades, with high LBI values indicating high viral fitness (Huddleston et al., 2020; Neher et al., 2014). In our epidemiological analysis, low diversity of H3 or N2 LBI in the current season correlated with greater epidemic intensity, higher transmission rates, and shorter seasonal duration. These associations suggest that low LBI diversity is indicative of a rapid selective sweep by one successful clade, while high LBI diversity is indicative of multiple co-circulating clades with variable seeding and establishment times over the course of an epidemic. A caveat is that LBI estimation is more sensitive to sequence sub-sampling schemes than strain-level measures. If an epidemic is short and intense (e.g., 1-2 months), a phylogenetic tree with our sub-sampling scheme (50 sequences per month) may not incorporate enough sequences to capture the true diversity of LBI values in that season.”

Figure 1 - LBI goes up over time. Is that partly to do with sampling? Overall how do higher sampling volumes in later years impact this analysis? (though you choose a fixed number of sequences so I guess you downsample to cope with that). I note that LBI is likely to be sensitive to sequencing density. 

Thank you for pointing this out. We realized that increasing LBI Shannon diversity over the course of the study period was indeed an artefact of increasing sequence volume over time. Our sequence subsampling scheme involves selecting a random sample of up to 50 viruses per month, with up to 25 viruses selected from North America (if available) and the remaining sequences evenly divided across nine other global regions. In early seasons of the study (late 1990s/early 2000s), sampling was often too sparse to meet the 25 viruses/month threshold for North America or for the other global regions combined (H3: Figure 2 - figure supplement 1; N2: Figure 2 - figure supplement 2). Ecological diversity metrics are sensitive to sample size, which explains why LBI Shannon diversity appeared to steadily increase over time in our original submission. In our revised manuscript, we correct for uneven sample sizes across seasons before estimating Shannon diversity and clarify our methodology. 

Lines 443-482: 

“Clade growth: The local branching index (LBI) measures the relative fitness of co-circulating clades, with high LBI values indicating recent rapid phylogenetic branching (Huddleston et al., 2020; Neher et al., 2014). To calculate LBI for each H3 and N2 sequence, we applied the LBI heuristic algorithm as originally described by Neher et al., 2014 to H3 and N2 phylogenetic trees, respectively. We set the neighborhood parameter 𝜏 to 0.4 and only considered viruses sampled between the current season 𝑡 and the previous season 𝑡 – 1 as contributing to recent clade growth in the current season 𝑡.  

Variation in the phylogenetic branching rates of co-circulating A(H3N2) clades may affect the magnitude, intensity, onset, or duration of seasonal epidemics. For example, we expected that seasons dominated by a single variant with high fitness might have different epidemiological dynamics than seasons with multiple co-circulating clades with varying seeding and establishment times. We measured the diversity of clade growth rates of viruses circulating in each season by measuring the standard deviation (s.d.) and Shannon diversity of LBI values in each season. Given that LBI measures relative fitness among cocirculating clades, we did not compare overall clade growth rates (e.g., mean LBI) across seasons.

Each season’s distribution of LBI values is right-skewed and does not follow a normal distribution. We therefore bootstrapped the LBI values of each season in each replicate dataset 1000 times (1000 samples with replacement) and estimated the seasonal standard deviation of LBI from resamples, rather than directly from observed LBI values. We also tested the seasonal standard deviation of LBI from log transformed LBI values, which produced qualitatively equivalent results to bootstrapped LBI values in downstream analyses.

As an alternative measure of seasonal LBI diversity, we binned raw H3 and N2 LBI values into categories based on their integer values (e.g., an LBI value of 0.5 is assigned to the (0,1] bin) and estimated the exponential of the Shannon entropy (Shannon diversity) of LBI categories (Hill, 1973; Shannon, 1948). The Shannon diversity of LBI considers both the richness and relative abundance of viral clades with different growth rates in each season and is calculated as follows:  

where 𝑞 𝐷 is the effective number of categories or Hill numbers of order 𝑞 (here, clades with different growth rates), with 𝑞 defining the sensitivity of the true diversity to rare versus abundant categories (Hill,

1973). exp is the exponential function, 𝑝# is the proportion of LBI values belonging to the 𝑖th category, and 𝑅 is richness (the total number of categories). Shannon diversity 1𝐷 (𝑞 = 1) estimates the effective number of categories in an assemblage using the geometric mean of their proportional abundances 𝑝# (Hill, 1973).  

Because ecological diversity metrics are sensitive to sampling effort, we rarefied H3 and N2 sequence datasets prior to estimating Shannon diversity so that seasons had the same sample size. For each season in each replicate dataset, we constructed rarefaction and extrapolation curves of LBI Shannon diversity and extracted the Shannon diversity estimate of the sample size that was twice the size of the reference sample size (the smallest number of sequences obtained in any season during the study) (iNEXT R package) (Chao et al., 2014). Chao et al. found that their diversity estimators work well for rarefaction and short-range extrapolation when the extrapolated sample size is up to twice the reference sample size. For H3, we estimated seasonal diversity using replicate datasets subsampled to 360 sequences/season; For N2, datasets were subsampled to 230 sequences/season.”

Estimating the Shannon diversity of LBI from datasets with even sampling across seasons removes the previous secular trend of increasing LBI diversity over time (Figure 2 in revised manuscript).

Figure 3 - I wondered what about the co-dominant times? 

In Figure 3, orange points correspond to seasons in which A(H3N2) and A(H1N1) were codominant. We are not sure of the reviewer’s specific question concerning codominant seasons, but if it concerns whether antigenic drift is linked to epidemic magnitude among codominant seasons alone, we cannot perform separate regression analyses for these seasons because there are only two codominant seasons during the 22 season study period.

Figure 4 - Related to drift and epidemic size, dominance, etc. -- when is drift measured, and (if it's measured in season t), would larger populations create more drift, simply by having access to more opportunity (via a larger viral population size)? This is a bit 'devil's advocate' but what if some epidemiological/behavioural process causes a larger and/or later peak, and those gave rise to higher drift?

Seasonal drift is measured as the genetic or antigenic distance between viruses circulating during season t and viruses circulating in the prior season (𝑡 – 1) or two seasons ago (𝑡 – 2).

Concerning the question about whether larger human populations lead to greater rates of antigenic drift, phylogeographic studies have repeatedly found that East-South-Southeast Asia are the source populations for A(H3N2) viruses (Bedford et al., 2015; Lemey et al., 2014), in part because these regions have tropical or subtropical climates and larger human populations, which enable year-round circulation and higher background infection rates. Larger viral populations (via larger host population sizes) and uninterrupted transmission may increase the efficiency of selection and the probability of strain survival and global spread (Wen et al., 2016). After A(H3N2) variants emerge in East-South-Southeast Asia and spread to other parts of the world, A(H3N2) viruses circulate via overlapping epidemics rather than local persistence (Bedford et al., 2015; Rambaut et al., 2008). Each season, A(H3N2) outbreaks in the US (and other temperate regions) are seeded by case importations from outside the US, genetic diversity peaks during the winter, and a strong genetic bottleneck typically occurs at the end of the season (Rambaut et al., 2008).

Due to their faster rates of antigenic evolution, A(H3N2) viruses undergo more rapid clade turnover and dissemination than A(H1N1) and B viruses, despite similar global migration networks across A(H3N2), A(H1N1), and B viruses (Bedford et al., 2015). Bedford et al. speculate that there is typically little geographic differentiation in A(H3N2) viruses circulating in each season because A(H3N2) viruses tend to infect adults, and adults are more mobile than children. Compared to A(H3N2) viruses, A(H1N1) and B viruses tend to have greater genealogical diversity, geographic differentiation, and longer local persistence times (Bedford et al., 2015; Rambaut et al., 2008). Thus, some A(H1N1) and B epidemics are reseeded by viruses that have persisted locally since prior epidemics (Bedford et al., 2015).

Theoretical models have shown that epidemiological processes can influence rates of antigenic evolution (Recker et al., 2007; Wen et al., 2016; Zinder et al., 2013), though the impact of flu epidemiology on viral evolution is likely constrained by the virus’s intrinsic mutation rate. 

In conclusion, larger host population sizes and flu epidemiology can indeed influence rates of antigenic evolution. However, given that our study is US-centric and focuses on A(H3N2) viruses, these factors are likely not at play in our study, due to intrinsic biological characteristics of A(H3N2) viruses and the geographic location of our study.

We have added a clarifying sentence to the end of the Introduction to narrow the scope of the paper for the reader.

Line 114-116: “Rather than characterize in situ evolution of A(H3N2) lineages circulating in the U.S., we study the epidemiological impacts of antigenic drift once A(H3N2) variants have arrived on U.S. soil and managed to establish and circulate at relatively high levels.”

Methods -- 

L 620 about rescaling and pre- vs post-pandemic times : tell us more - how has reporting changed? could any of this not be because of reporting but because of NPIs or otherwise? Overall there is a lot of rescaling going on. How sensitive are the results to it? 

it would be unreasonable to ask for a sensitivity analysis for all the results for all the choices around data preparation, but some idea where there is a reason to think there might be a dependence on one of these choices would be great.

In response to the 2009 A(H1N1) pandemic, the US CDC and WHO increased laboratory testing capacity and strengthened epidemiological networks, leading to substantial, long-lasting improvements to influenza surveillance that are still in place today (https://www.cdc.gov/flu/weekly/overview.htm). At the beginning of the COVID-19 pandemic, influenza surveillance networks were quickly adapted to detect and understand the spread of SARS-CoV-2. The 2009 pandemic occurred over a time span of less than one year, and strict non-pharmaceutical interventions (NPIs), such as lockdowns and mask mandates, were not implemented. Thus, we attribute increases in test volume during the post-2009 period to improved virologic surveillance and laboratory testing capacity rather than changes in care-seeking behavior. In the revised manuscript, we include a figure (Figure 1 - figure supplement 2) that shows systematic increases in test volume in all HHS regions after the 2009 pandemic.

Given the substantial increase in influenza test volume after 2009, we opted to keep the time trend adjustment for the pre- and post-2009 pandemic periods and evaluate whether adjusting for regional reporting differences affects our results. When estimating univariate correlations between various

A(H3N2) epidemic metrics and evolutionary indicators, we found qualitatively equivalent results for Spearman correlations and regression models, when adjusting for the pre- and post-2009 pandemic time periods and regional reporting versus only adjusting for the pre-/post-2009 pandemic time periods. Below, we share adjusted versions of Figure 3 (regression results) and Figure 3 - figure supplement 1 (Spearman correlations). Each figure only adjusts for differences in pre- and post-2009 pandemic reporting.

Author response image 1.

Adjustment for pre- and post-2009 pandemic only

Author response image 2.

Adjustment for pre- and post-2009 pandemic only

L635 - Why discretize the continuous LBI distribution and then use Shannon entropy when you could just use the variance and/or higher moments? (or quantiles)? Similarly, why not use the duration of the peak, rather than Shannon entropy? (though there, because presumably data are already binned weekly, and using duration would involve defining start and stop times, it's more natural than with LBI)

We realize that we failed to mention in the methods that we calculated the standard deviation of LBI in each season, in addition to the exponential of the Shannon entropy (Shannon diversity) of LBI. Both the Shannon diversity of LBI values and the standard deviation of LBI values were negatively correlated with effective Rt and epidemic intensity and positively correlated with seasonal duration. The two measures were similarly correlated with effective Rt and epidemic intensity (Figure 3 - figure supplements 2 - 3), while the Shannon diversity of LBI had slightly stronger correlations with seasonal duration than s.d. LBI (Figure 5). Thus, both measures of LBI diversity appear to capture potentially biologically important heterogeneities in clade growth rates.

Separately, we use the inverse Shannon entropy of the incidence distribution to measure the spread of an A(H3N2) epidemic during the season, following the methods of Dalziel et al. 2018. The peak of an epidemic is a single time point at which the maximum incidence occurs. We have not encountered “the duration of the peak” before in epidemiology terminology, and, to our knowledge, there is not a robust way to measure the “duration of a peak,” unless one were to measure the time span between multiple points of maximum incidence or designate an arbitrary threshold for peak incidence that is not strictly the maximum incidence. Given that Shannon entropy is based on the normalized incidence distribution over the course of the entire influenza season (week 40 to week 20), it does not require designating an arbitrary threshold to describe epidemic intensity.

L642 - again why normalize epidemic intensities, and how sensitive are the results to this? I would imagine given that the RF results were unstable under leave-one-out analysis that some of those results could be quite sensitive to choices of normalization and scaling.

Epidemic intensity, defined as the inverse Shannon entropy of the incidence distribution, measures the spread of influenza cases across the weeks in a season. Following Dalziel et al. 2018, we estimated epidemic intensity from normalized incidence distributions rather than raw incidences so that epidemic intensity is invariant under differences in reporting rates and/or attack rates across regions and seasons. If we were to use raw incidences instead, HHS regions or seasons could have the appearance of greater or lower epidemic intensity (i.e., incidence concentrated within a few weeks or spread out over several weeks), due to differences in attack rates or test volume, rather than fundamental differences in the shapes of their epidemic curves. In other words, epidemic intensity is intended to measure the shape and spread of an epidemic, regardless of the actual volume of cases in a given region or season.

In the methods section, we provide further clarification for why epidemic intensities are based on normalized incidence distributions rather than raw incidences.

Lines 206-209: “Epidemic intensity is intended to measure the shape and spread of an epidemic, regardless of the actual volume of cases in a given region or season. Following the methodology of Dalziel et al. 2018, epidemic intensity values were normalized to fall between 0 and 1 so that epidemic intensity is invariant to differences in reporting rates and/or attack rates across regions and seasons.”  

L643 - more information about what goes into Epidemia (variables, priors) such that it's replicable/understandable without the code would be good. 

We now include additional information concerning the epidemic models used to estimate Rt, including all model equations, variables, and priors (Lines 210-276 in Methods).

L667 did you do breakpoint detection? Why linear models? Was log(incidence) used? 

In our original submission, we estimated epidemic onsets using piecewise regression models (Lines 666674 in original manuscript), which model non-linear relationships with breakpoints by iteratively fitting linear models (Muggeo, 2003). Piecewise regression falls under the umbrella of parametric methods for breakpoint detection.

We did not include results from linear models fit to log(incidence) or GLMs with Gaussian error distributions and log links, due to two reasons. First, models fit to log-transformed data require non-zero values as inputs. Although breakpoint detection does not necessarily require weeks of zero incidence leading up to the start of an outbreak, limiting the time period for breakpoint detection to weeks with nonzero incidence (so that we could use log transformed incidence) substantially pushed back previous more biologically plausible estimates of epidemic onset weeks. Second, as an alternative to limiting the dataset to weeks with non-zero incidence, we tried adding a small positive number to weekly incidences so that we could fit models to log transformed incidence for the whole time period spanning epidemic week 40 (the start of the influenza season) to the first week of maximum incidence. Fitting models to log

transformed incidences produced unrealistic breakpoint locations, potentially because log transformations 1) linearize data, and 2) stabilize variance by reducing the impact of extreme values. Due to the short time span used for breakpoint detection, log transforming incidence diminishes abrupt changes in incidence at the beginning of outbreaks, making it difficult for models to estimate biologically plausible breakpoint locations. Log transformations of incidence may be more useful when analyzing time series spanning multiple seasons, rather than short time spans with sharp changes in incidence (i.e., the exponential growth phase of a single flu outbreak).

As an alternative to piecewise regression, our revised manuscript also estimates epidemic onsets using a Bayesian ensemble algorithm that accounts for the time series nature of incidence data and allows for complex, non-linear trajectories interspersed with change points (BEAST - a Bayesian estimator of Abrupt change, Seasonal change, and Trend; Zhao et al., 2019). Although a few regional onset time times differed across the two methods, our conclusions did not change concerning correlations between viral fitness and epidemic onset timing.

We have rewritten the methods section for estimating epidemic onsets to clarify our methodology and to include the BEAST method (Lines 292-308):

“We estimated the regional onsets of A(H3N2) virus epidemics by detecting breakpoints in A(H3N2) incidence curves at the beginning of each season. The timing of the breakpoint in incidence represents epidemic establishment (i.e., sustained transmission) rather than the timing of influenza introduction or arrival (Charu et al., 2017). We used two methods to estimate epidemic onsets: 1) piecewise regression, which models non-linear relationships with break points by iteratively fitting linear models to each segment (segmented R package) (Muggeo, 2008; Muggeo, 2003), and 2) a Bayesian ensemble algorithm (BEAST – a Bayesian estimator of Abrupt change, Seasonal change, and Trend) that explicitly accounts for the time series nature of incidence data and allows for complex, non-linear trajectories interspersed with change points (Rbeast R package) (Zhao et al., 2019). For each region in each season, we limited the time period of breakpoint detection to epidemic week 40 to the first week of maximum incidence and did not estimate epidemic onsets for regions with insufficient signal, which we defined as fewer than three weeks of consecutive incidence and/or greater than 30% of weeks with missing data. We successfully estimated A(H3N2) onset timing for most seasons, except for three A(H1N1) dominant seasons: 20002001 (0 regions), 2002-2003 (3 regions), and 2009-2010 (0 regions). Estimates of epidemic onset weeks were similar when using piecewise regression versus the BEAST method, and downstream analyses of correlations between viral fitness indicators and onset timing produced equivalent results. We therefore report results from onsets estimated via piecewise regression.”

L773 national indicators -- presumably this is because you don't have regional-level information, but it might be worth saying that earlier so it doesn't read like there are other indicators now, called national indicators, that we should have heard of 

In the revised manuscript, we move a paragraph that was at the beginning of the Results to the beginning of the Methods.

Lines 123-132: 

“Our study focuses on the impact of A(H3N2) virus evolution on seasonal epidemics from seasons 19971998 to 2018-2019 in the U.S.; whenever possible, we make use of regionally disaggregated indicators and analyses. We start by identifying multiple indicators of influenza evolution each season based on changes in HA and NA. Next, we compile influenza virus subtype-specific incidence time series for U.S. Department of Health and Human Service (HHS) regions and estimate multiple indicators characterizing influenza A(H3N2) epidemic dynamics each season, including epidemic burden, severity, type/subtype dominance, timing, and the age distribution of cases. We then assess univariate relationships between national indicators of evolution and regional epidemic characteristics. Lastly, we use multivariable regression models and random forest models to measure the relative importance of viral evolution, heterosubtypic interference, and prior immunity in predicting regional A(H3N2) epidemic dynamics.”

In Lines 484-487 in the Methods, we now mention that measures of seasonal antigenic and genetic distance are at the national level. 

“For each replicate dataset, we estimated national-level genetic and antigenic distances between influenza viruses circulating in consecutive seasons by calculating the mean distance between viruses circulating in the current season 𝑡 and viruses circulating during the prior season (𝑡 – 1 year; one season lag) or two prior seasons ago (𝑡 – 2 years; two season lag).”

L782 Why Beta regression and what is "the resampled dataset" ? 

Beta regression is appropriate for models of subtype dominance, epidemic intensity, and age-specific proportions of ILI cases because these data are continuous and restricted to the interval (0, 1) (Ferrari & Cribari-Neto, 2004). “The resampled dataset” refers to the “1000 bootstrap replicates of the original dataset (1000 samples with replacement)” mentioned in Lines 777-778 of the original manuscript. 

In the revised manuscript, we include more background information about Beta regression models, and explicitly mention that regression models were fit to 1000 bootstrap replicates of the original dataset.

Lines 503-507: 

“For subtype dominance, epidemic intensity, and age-specific proportions of ILI cases, we fit Beta regression models with logit links. Beta regression models are appropriate when the variable of interest is continuous and restricted to the interval (0, 1) (Ferrari & Cribari-Neto, 2004). For each epidemic metric, we fit the best-performing regression model to 1000 bootstrap replicates of the original dataset.”

The github is clear, comprehensive and well-documented, at least at a brief glance. 

Thank you! At the time of resubmission, our GitHub repository is updated to incorporate feedback from the reviewers.

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eLife assessment

This work by Shin et al. demonstrated that a different form of PTH (R25C PTH) generated a comparable anabolic signal to rhPTH 1-34 using a large animal model. This valuable finding may have therapeutic potential in promoting bone formation or the healing process, and the methods seem solid, although there remains a concern regarding the small sample size and surgical procedure.

Reviewer #1 (Public Review):

Summary:

This study, titled "Enhancing Bone Regeneration and Osseointegration using rhPTH(1-34) and Dimeric R25CPTH(1-34) in an Osteoporotic Beagle Model," provides valuable insights into the therapeutic effects of two parathyroid hormone (PTH) analogs on bone regeneration and osseointegration. The research is methodologically sound, employing a robust animal model and a comprehensive array of analytical techniques, including micro-CT, histological/histomorphometric analyses, and serum biochemical analysis.

Strengths:

The use of a large animal model, which closely mimics postmenopausal osteoporosis in humans, enhances the study's relevance to clinical applications. The study is well-structured, with clear objectives, detailed methods, and a logical flow from introduction to conclusion. The findings are significant, demonstrating the potential of rhPTH(1-34) and dimeric R25CPTH(1-34) in enhancing bone regeneration, particularly in the context of osteoporosis.

Weaknesses: There are no major weaknesses.

Reviewer #2 (Public Review):

Summary:

This article explores the regenerative effects of recombinant PTH analogues on osteogenesis.

Strengths:

Although PTH has known to induce the activity of osteoclasts, accelerating bone resorption, paradoxically its intermittent use has become a common treat for osteoporosis. Previous studies successfully demonstrated this phenomenon in vivo, but most of them used rodent animal models, inevitably having a limitation. In this article, the authors tried to address this, using a beagle model, and assessed the osseointegrative effect of recombinant PTH analogues. As a result, the authors clearly observed the regenerative effects of PTH analogues, and compared the efficacy, using histologic, biochemical, and radiologic measurement for surgical-endocrinal combined large animal models. The data seem to be solid, and has potential clinical implications.

Weaknesses:

All the issues that I raised have been resolved in the revision process.

Overall, this paper is well-written and has clarity and consistency for a broader readership.

Reviewer #3 (Public Review):

Summary:

The work submitted by Dr. Jeong-Oh Shin and co-workers aims to investigate the therapeutic efficacy of rhPTH(1-34) and R25CPTH(1-34) on bone regeneration and osseointegration of titanium implants using a postmenopausal osteoporosis animal model.

In my opinion the findings presented are not strongly supported by the provided data since the methods utilized do not allow to significantly support the primary claims.

Strengths:

Strengths include certain good technologies utilized to perform histological sections (i.e. the EXAKT system).

Weaknesses:

Certain weaknesses significantly lower the enthusiasm for this work. Most important: the limited number of samples/group. In fact, as presented, the work has an n=4 for each treatment group. This limited number of samples/group significantly impairs the statistical power of the study. In addition, the implants were surgically inserted following a "conventional implant surgery", implying that no precise/guided insertion was utilized. This weakness is, in my opinion, particularly significant since the amount of bone osteointegration may greatly depend on the bucco-lingual positioning of each implant at the time of the surgical insertion (which should, therefore, be precisely standardized across all animals and for all surgical procedures).

Comments on current version:

As mentioned in my first review, this work is significantly underpowered for the following reasons: 1) n=4 for each treatment group.; 2) no randomization of the surgical sites receiving treatments; 3) implants surgically inserted without precision/guided surgery. The authors have not addressed these concerns.

On a minor note: not sure why the authors present a methodology to evaluate the dynamic bone formation (line 272) but do not present results (i.e. by means of histomorphometrical analyses) utilizing this methodology.

Author response:

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

Response to Reviewer 1

(Cys25)PTH(1-84) does not show efficacy surpassing that of the previously used rhPTH(1-34). This needs to be discussed biologically and clinically.

Thank you very much for your valuable comments for enhancing the manuscript. We appreciate your input and have noted that this aspect was not addressed in the discussion. The authors have included the following paragraph in discussion section.

“This biological difference is thought to be due to dimeric R25CPTH(1-34) exhibiting a more preferential binding affinity for the RG versus R0 PTH1R conformation, despite having a diminished affinity for either conformation. Additionally, the potency of cAMP production in cells was lower for dimeric R25CPTH compared to monomeric R25CPTH, consistent with its lower PTH1R-binding affinity.  (Noh et al., 2024) One of the potential clinical advantages of dimeric R25CPTH(1-34) is its partial agonistic effect in pharmacodynamics. This property may allow for a more fine-tuned regulation of bone metabolism, potentially reducing the risk of adverse effects associated with full agonism, such as hypercalcemia and bone resorption by osteolcast activity. Moreover, the dimeric form may offer a more sustained anabolic response, which could be beneficial in the context of long-term treatment strategies. (Noh et al., 2024) Also, the effects of dimer were prominent, as we mentioned better bone formation than the control group.” (2nd paragraph, Discussion section)

The terms (Cys25)PTH(1-84) and Dimeric R25CPTH(1-34) are being used interchangeably and incorrectly. A unification of these terms is necessary.

We totally agree with the reviewer’s notion. R25CPTH(1-84) represents mutated human PTH, rhPTH(1-34) and dimeric R25CPTH(1-34) are synthesized PTH analogs. To clarified the terminology, we thus have changeed the terminology in the manuscript appear in red.

The figure legend is incorrect. Not all figures are described, and even though there are figures from A to I, only up to E is explained, or the content is different.

We apologize for our negligence. As suggested by a reviewer, we've fixed the figure legends throughout before the list of references in the manuscript as follows.

“Figure legends

Figure 1. Micro-CT analysis (A-D) Experimental design for the controlled delivery of rhPTH(1-34) and dimeric R25CPTH(1-34) in ovariectomized beagle model. Representative images for injection and placement of titanium implant. (E) Micro-CT analysis. bone mineral density (BMD), bone volume (TV; mm3), trabecular number (Tb.N; 1/mm), trabecular thickness (Tb. Th; um), trabecular separation (Tb.sp; ㎛). Error bars indicate standard deviation. Data are shown as mean ± s.d. *p<0.05, **p<0.01, ***p<0.001, n.s., not significant.  P, posterior. R, right

Figure 2. (A-I) Histological analysis of the different groups stained in Goldner’s trichrome. The presence of bone is marked by the green color and soft tissue in red. Red arrows indicate the position with soft tissues without bone around the implant threads. The area of bone formed was the widest in the rhPTH(1-34)-treated group. In the dimeric R25CPTH(1-34)treated group, there is a greater amount of bone than vehicle-treated group. Green arrows represent the bone formed over the implant. blue dotted line, margin of bone and soft tissue; Scale bars: 1mm

Figure 3. Histological analysis using Masson trichrome staining results in the rhPTH(1-34) and dimeric R25CPTH(1-34)-treated group (A-L) Masson trichrome-stained sections of cancellous bone in the mandibular bone. The formed bone is marked by the color red. Collagen is stained blue. Black dotted box magnification region of trabecular bone in the mandible. Scale bars, A-C, G-I: 1mm; D-F, J-L: 200 ㎛

Figure 4. Immunohistochemical analysis using TRAP staining for bone remodeling activity (A-L) TRAP staining is used to evaluate bone remodeling by staining osteoclasts. Osteoclasts is presented by the purple color. Black dotted box magnification region of trabecular bone in the mandible. (M, N) The number of TRAP-positive cells in the mandible of the rhPTH(1-34) and dimeric R25CPTH(1-34)-treated beagles. Scale bars, A-C, G-I: 1mm; D-F, J-L: 200 ㎛. Error bars indicate standard deviation. Data are shown as mean ± s.d. *p<0.05, **p<0.01, n.s., not significant

Figure 5. Measurement of biochemical Marker Dynamics in serum. The serum levels of calcium, phosphorus, P1NP, and CTX across three time points (T0, T1, T2) following treatment with dimeric dimeric R25CPTH(1-34), rhPTH(1-34), or control. (A-B) Calcium and phosphorus levels exhibit an upward trend in response to both PTH treatments compared to control, suggesting enhanced bone mineralization. (C) P1NP levels, indicative of bone formation, remain relatively unchanged across time and treatments. (D) CTX levels, associated with bone resorption, show no significant differences between groups. Data points for the dimeric R25CPTH(1-34), rhPTH(1-34), and control are marked by squares, circles, and triangles, respectively, with error bars representing confidence intervals.

Supplementary Figure. Three-dimensional reconstructed image of the bone surrounding the implants. Three-dimensional reconstructed images of the peri-implant bone depicting the osseointegration after different therapeutic interventions. (A) Represents the bone response to recombinant human parathyroid hormone fragment (rhPTH 1-34) treatment, showing the most robust degree of bone formation around the implant in the three groups. (B) Shows the bone response to a modified PTH fragment (dimeric R25CPTH(1-34)), indicating a similar level of bone growth and integration as seen with rhPTH(1-34), although to a slightly lesser extent. (C) Serves as the control group, demonstrating the least amount of bone formation and osseointegration. The upper panel provides a top view of the bone-implant interface, while the lower panel offers a cross-sectional view highlighting the extent of bony ingrowth and integration with the implant surface.”

In Figure 5, although the descriptions of T0, T1, T2 are mentioned in the method section, it would be more clear if there was a timeline like in Figure 1.

Based on the reviewer’s advice, we have indicated the timing of T0, T1, and T2 in the materials & methods section describing the serum biochemical assay, and we have shown a timeline in figure 5.

In Figure 5, instead of having calcium, phosphorus, P1NP, CTX graphs all under Figure 5, it would be more convenient for referencing in the text to label them as Figure 5A, Figure 5B, Figure 5C, Figure 5D.

We totally understood the reviewer’s comment. As the reviewer’s suggested, we have corrected the labeling in the text for figure 5 as follows.

“The levels of calcium, phosphorus, CTX, and P1NP were analyzed over time using RM-ANOVA (Figure 5). There were no significant differences between the groups for calcium and phosphorus at time points T0 and T1 (Figure 5A). However, after the PTH analog was administered at T2 (Figure 5A), the levels were highest in the rhPTH(1-34) group, followed by the dimeric R25CPTH(1-34) group, and then, lowest in the control group, which was statistically significant (Figure 5B,C). (P < 0.05) The differences between the groups over time for CTX and P1NP were not statistically significant (Figure 5D, E).”

Significance should be indicated in the figure (no asterisk present).

As the reviewer’s comment, we put the asterisk in the figure 5.

Addition of Figures in Text:

Line 112: change from "figure 2" to "figure 1" / Line 115: mention "figure 1. E"

Line 120: refer to "figure 1. E" / Line 123: change from "figure 3" to "figure 2"

Line 128: refer to "figure 2.A-C" / Line 137: mention "figure 3"

Line 138: refer to "figure 3. A-L" / Line 143: mention "figure 3. A-L"

Line 144: refer to "figure 3. E,F,K,L" / Line 148: mention "figure 4"

Line 150: refer to "figure 4 M,N" / Line 152: mention "figure 4. M,N"

Line 155: refer to "figure 5" / Line 157: mention "figure 5"

Line 159: refer to "figure 5" / Line 171: mention "figure 1 E"

Line 175: refer to "figure 2 M, N"/ Line 194: mention "figure 3"

Above all, thank you for the reviewer’s notion. We corrected detailed figure labeling in text to red color.

Response to Reviewer 2

First, the authors should clarify why they compared the effects of rhPTH(1-34) and of dimeric R25C2 PTH(1-34)? In most of the parameters, rhPTH(1-34) seems to be superior to dimeric R25C2 PTH(1-34). Why did the authors insist that the anabolic effects of dimer were prominent? Even though implication of dimeric R25C2 PTH(1-34) was drawn from genetic mutation studies, the authors should describe more clearly in the discussion the potential clinical benefits of the dimeric R25C2 PTH(1-34) compared to rhPTH(1-34), especially if dimeric R25C2 PTH(1-34) has just partial agonistic effect in pharmacodynamics.

Thank you for your insightful comments and questions regarding our results between rhPTH(1-34) and dimeric R25CPTH(1-34). rhPTH(1-34) is a well-characterized therapy for osteoporosis. In this study, rhPTH(1-34) generally showed superior outcomes in most parameters tested, the dimeric R25CPTH(1-34) exhibited specific anabolic effects that are not as pronounced with rhPTH(1-34). We recognized R25CPTH(1-34) as a anabolic effector. One of the potential advantages of dimeric R25CPTH(1-34) is its partial agonistic effect in pharmacodynamics. This property may allow for a more fine-tuned regulation of bone metabolism, potentially reducing the risk of adverse effects associated with full agonism, such as hypercalcemia and bone resorption by osteolast activity. Moreover, the dimeric form may offer a more sustained anabolic response, which could be beneficial in the context of long-term treatment strategies. Also, based on our results, we notes that the effects of dimer were prominent, as we mentioned better bone formation than the control group. We appreciate your input and have noted that this aspect was not addressed in the discussion. As a result, we have included the following paragraph in discussion section.

“This biological difference is thought to be due to dimeric R25CPTH(1-34) exhibiting a more preferential binding affinity for the RG versus R0 PTH1R conformation, despite having a diminished affinity for either conformation. Additionally, the potency of cAMP production in cells was lower for dimeric R25CPTH compared to monomeric R25CPTH, consistent with its lower PTH1R-binding affinity.  (Noh et al., 2024) One of the potential clinical advantages of dimeric R25CPTH(1-34) is its partial agonistic effect in pharmacodynamics. This property may allow for a more fine-tuned regulation of bone metabolism, potentially reducing the risk of adverse effects associated with full agonism, such as hypercalcemia and bone resorption by osteolcast activity. Moreover, the dimeric form may offer a more sustained anabolic response, which could be beneficial in the context of long-term treatment strategies. (Noh et al., 2024) Also, the effects of dimer were prominent, as we mentioned better bone formation than the control group.” (2nd paragraph, Discussion section)

Second, please describe the intermittent and continuous application of PTH analogues. Many of the readers may misunderstand that the authors' daily injection of PTHs were actually to mimic the clinical intermittent application or continuous one. Incorporation of the author's intention for experimental design would be more helpful for readers.

Thank you for your insightful comments regarding the need for clearer differentiation between intermittent and continuous applications of PTH analogs in this study. We appreciate your concern that the readers may not fully grasp whether our daily injection protocol was intended to mimic clinical intermittent or continuous PTH administration. To address this, we have revised the manuscript to explicitly clarify that the daily injections of rhPTH(1-34) and dimeric R25CPTH(1-34) were designed to simulate the intermittent dosing regimen commonly used in clinical practice. This regimen is known to maximize the anabolic effects on bone while minimizing potential catabolic actions associated with more frequent or continuous hormone exposure. We have added detailed explanations in the Introduction, Methods, and Discussion sections to help readers understand our experimental design and its relevance to clinical settings.

Introduction section

“Administration of prathyroid hormone (PTH) analogs can be categorized into two distinct protocols: intermittent and continuous. Intermittent rhPTH(1-34) therapy, typically characterized by daily injections, is clinically used to enhance bone formation and strength. This method leverages the anabolic effects of rhPTH(1-34) without significant bone resorption, which can occur with more frequent or continuous exposure. On the other hand, continuous rhPTH(1-34) exposure, often modeled in research as constant infusion, tends to accelerate bone resorption activities, potentially leading to bone loss (Silva and Bilezikian, 2015; Jilka, 2007). Understanding these differences is crucial for interpreting the therapeutic implications of rhPTH(1-34) in bone health.”

Silva, B. C., & Bilezikian, J. P. (2015). Parathyroid hormone: anabolic and catabolic actions on the skeleton. Current Opinion in Pharmacology, 22, 41-50.

Jilka, R. L. (2007). Molecular and cellular mechanisms of the anabolic effect of intermittent PTH. Bone, 40(6), 1434-1446.

Materials and Methods section

“Each animal received one injection per day, aimed at replicating the intermittent rhPTH(1-34) exposure proven beneficial for bone regeneration and overall skeletal health in clinical settings (Neer et al., 2001; Kendler et al., 2018). This regimen was chosen to investigate the potential anabolic effects of these specific PTH analogs under conditions closely resembling therapeutic use.”

Neer, R. M., Arnaud, C. D., Zanchetta, J. R., Prince, R., Gaich, G. A., Reginster, J. Y., Hodsman, A. B., Eriksen, E. F., Ish-Shalom, S., Genant, H. K., Wang, O., and Mitlak, B. H. (2001). Effect of Parathyroid Hormone (1-34) on Fractures and Bone Mineral Density in Postmenopausal Women with Osteoporosis. The New England Journal of Medicine, 344(19), 1434-1441.

Kendler, D. L., Marin, F., Zerbini, C. A. F., Russo, L. A., Greenspan, S. L., Zikan, V., Bagur, A., Malouf-Sierra, J., Lakatos, P., Fahrleitner-Pammer, A., Lespessailles, E., Minisola, S., Body, J. J., Geusens, P., Moricke, R., & Lopez-Romero, P. (2018). Effects of Teriparatide and Risedronate on New Fractures in Post-Menopausal Women with Severe Osteoporosis (VERO): A Multicenter, Double-Blind, Double-Dummy, Randomized Controlled Trial. The Lancet, 391(10117), 230-240.

Discussion section

“The use of daily injections in this study was intended to simulate intermittent PTH therapy, a well-established clinical approach for managing osteoporosis and enhancing bone regeneration. Intermittent administration of PTH, as opposed to continuous exposure, is critical for maximizing the anabolic response while minimizing the catabolic effects that are associated with higher frequency or continuous hormone levels. Our findings support the notion that even with daily administration, both rhPTH(1-34) and dimeric dimeric R25CPTH(1-34) promote bone formation and osseointegration, consistent with the outcomes expected from intermittent therapy. It’s important for future research to consider the dosage and timing of administration to further optimize the therapeutic benefits of PTH analogs (Dempster et al., 2001; Hodsman et al., 2005).”

Dempster, D. W., Cosman, F., Kurland, E. S., Zhou, H., Nieves, J., Woelfert, L., Shane, E., Plavetic, K., Müller, R., Bilezikian, J., & Lindsay, R. (2001). Effects of Daily Treatment with Parathyroid Hormone on Bone Microarchitecture and Turnover in Patients with Osteoporosis: A Paired Biopsy Study. Journal of Bone and Mineral Research, 16(10), 1846-1853.

Hodsman, A. B., Bauer, D. C., Dempster, D. W., Dian, L., Hanley, D. A., Harris, S. T., Kendler, D. L., McClung, M. R., Miller, P. D., Olszynski, W. P., Orwoll, E., Yuen, C. K. (2005). Parathyroid Hormone and Teriparatide for the Treatment of Osteoporosis: A Review of the Evidence and Suggested Guidelines for Its Use. Endocrine Reviews, 26(5), 688-703.

Third, please unify the nomenclature. Ensure consistency in the nomenclature throughout the article. Unify the naming conventions for PTH analogues, such as rhPTH(1-34) vs teriparatide and (Cys25)PTH(1-84) vs R25CPTH(1-34) vs R25CPTH(1-34) vs (1-84). Choose one nomenclature for each analogue and use it consistently throughout the article.

We totally agree with the reviewer’s notion. R25CPTH(1-84) represents mutated human PTH, rhPTH(1-34) and dimeric R25CPTH(1-34) are synthesized PTH analogs. To clarified the terminology, we thus have changed the terminology in the manuscript appear in red.

Response to Reviewer 3

I would recommend to rewrite the manuscript in a form that is more understandable to the readers. In fact, it appears to me that this work was originally formatted in a way that would need the Materials and Methods to precede the results. As presented (and as requested by the eLife formatting) the Materials and Methods are available only at the end of the reading and, as a consequence, the readers needs to refer to the Materials and Methods to have a general and initial understanding of the study design (i.e. type of treatment for each group, etc are not well specified in the Results section).

Thank you for you constructive comments and suggestions regarding the manuscript. We appreciate your feedback on the organization of the manuscript entirely. As reviewer mentioned, Materials and methods were placed after the discussion section in accordance with the format of the elife journal. For a better and initial understanding, a description of each experimental group has been added to the Results section as follow. Thank you again for your valuable comments.

“To investigate evaluating and comparing the efficacy of rhPTH(1-34) and the dimeric R25CPTH(1-34) in promoting bone regeneration and healing in a clinically relevant animal model. In our study, beagle dogs were selected as the model due to their anatomical similarity to human oral structures, suitable size for surgeries, human-like bone turnover rates, and established oral health profiles, ensuring comparable and ethically sound research outcomes. The normal saline injected-control group, injected with 40ug/day PTH (Forsteo, Eli Lilly) group, and 40ug/day PTH analog-injected group. Animals in each group were injected subcutaneously for 10 weeks.”

eLife assessment

This important paper on measuring molecular connectivity using combined serotonin PET and resting-state fMRI provides both novel methods for studying the brain as well as insights into the effects of ecstasy administration. The methods are solid, with a few doubts that need to be dispelled surrounding the high anaesthetic dose used.

Reviewer #1 (Public Review):

This paper by Ionescu et al. applies novel brain connectivity measures based on fMRI and serotonin PET both at baseline and following ecstasy use in rats. There are multiple strengths to this manuscript. First, the use of connectivity measures using temporal correlations of 11C-DASB PET, especially when combined with resting state fMRI, is highly novel and powerful. The effects of ecstasy on molecular connectivity of the serotonin network and salience network are also quite intriguing.

I would like the authors to discuss and justify their use of high-dose (1.3%) isolfurane. A recent consensus paper on rat fMRI (Grandjean et al., "A Consensus Protocol for Functional Connectivity Analysis in the Rat Brain.") found that medetomidine combined with low dose isoflurane provided optimal control of physiology and fMRI signal. To overcome any doubts about the effects of the high-dose anaesthetic I'd encourage the authors to show the results of their functional connectivity specificity using the same or similar image processing protocol as described in that consensus paper. This is especially true since the fMRI ICs in Figure 2A appear fairly restricted.

I'd also be interested to read more about why the cerebellum was chosen as a reference region, given that serotonin is highly expressed in the cerebellum, and what effects the choice of reference region has on their quantification.

The PET ICs appear less bilateral than the fMRI ICs. Is that simply a thresholding artefact or is it a real signal?

"The data will be made available upon reasonable request" is not sufficient - please deposit the data in an open repository and link to its location.

Reviewer #2 (Public Review):

Summary:

The article aims to describe a novel methodology for the study of brain organization, in comparison to fMRI functional connectivity, under rest vs. controlled pharmacological stimulation.

Strengths:

Solid study design with pharmacological stimulation applied to assess the biological significance of functional and (novel) molecular connectivity estimates.

Provides relevant information on the multivariate organization of serotoninergic system in the brain.

Provides relevant information on the sensitivity of traditional (univariate PET analysis, fMRI functional connectivity) and novel (molecular connectivity) methods in measuring pharmacological effects on brain function.

Weaknesses:

While the study protocol is referenced in the paper, it would be useful to at least report whether the study uses bolus, constant infusion, or a combination of the two and the duration of the frames chosen for reconstruction. Minimal details on anesthesia should also be reported, clarifying whether an interaction between the pharmacological agent for anesthesia and MDMA can be expected (whole-brain or in specific regions).

Some terminology is used in a bit unclear way. E.g. "seed-based" usually refers to seed-to-voxel and not ROI-to-ROI analysis, or e.g. it is a bit confusing to have IC1 called SERT network when in fact all ICs derived from DASB data are SERT networks. Perhaps a different wording could be used (IC1 = SERT xxxxx network; IC2= SERT salience network) .

The limited sample size for the rats undergoing pharmacological stimulation which might make the study (potentially) not particularly powerful. This could not be a problem if the MDMA effect observed is particularly consistent across rats. Information on inter-individual variability of FC, MC, and BPND could be provided in this regard.

eLife assessment

This valuable paper investigates how fish avoid thermal disturbances that occur on fast timescales. The authors use a creative experimental approach that quickly creates a vertical thermal interface, which they combine with careful behavioral analyses. The evidence supporting their results is solid, but there is a potential confounding factor between temperature and vertical positioning, and characterization of the thermal interface would greatly assist in interpreting the results.

Reviewer #1 (Public Review):

Summary:

The experiment is interesting and well executed and describes in high detail fish behaviour in thermally stratified waters. The evidence is strong but the experimental design cannot distinguish between temperature and vertical position of the treatments.

Strengths:

High statistical power, solid quantification of behaviour.

Weaknesses:

A major issue with the experimental design is the vertical component of the experiment. Many thermal preference and avoidance experiments are run using horizontal division in shuttlebox systems or in annular choice flumes. These remove the vertical stratification component so that hot and cold can be compared equally, without the vertical layering as a confounding factor. The method chosen, with its vertical stratification, is inherently unable to control for this effect because warm water is always above, and cold water is always below. This complicates the interpretations and makes firm conclusions about thermal behaviour difficult.

Reviewer #2 (Public Review):

This paper investigates an interesting question: how do fish react to and avoid thermal disturbances from the optimum that occur on fast timescales? Previous work has identified potential strategies for warm avoidance in fish on short timescales while strategies for cold avoidance are far more elusive. The work combines a clever experimental paradigm with careful analysis to show that trout parr avoid cold water by limiting excursions across a warm-cold thermal interface. While I found the paper interesting and convincing overall, there are a few omissions and choices in the presentation that limit interpretability and clarity.

A main question concerns the thermal interface itself. The authors track this interface using a blue dye that is mixed in with either colder or warmer water before a gate is opened that leads to gravitational flow overlaying the two water temperatures. The dye likely allows to identify convective currents which could lead to rapid mixing of water temperatures. However, it is less clear whether it accurately reflects thermal diffusion. This is problematic as the authors identify upward turning behavior around the interface which appears to be the behavioral strategy for avoiding cold water but not warm water. Without knowing the extent of the gradient across the interface, it is hard to know what the fish are sensing. The authors appear to treat the interface as essentially static, leading them to the conclusion that turning away before the interface is reached is likely related to associative learning. However, thermal diffusion could very likely create a gradient across centimeters which is used as a cue by the fish to initiate the turn. In an ideal world, the authors would use a thermal camera to track the relationship between temperature and the dye interface. Absent that, the simulation that is mentioned in passing in the methods section should be discussed in detail in the main text, and results should be displayed in Figure 1. Error metrics on the parameters used in the simulation could then be used to identify turns in subsequent figures that likely are or aren't affected by a gradient formed across the interface.

The authors assume that the thermal interface triggers the upward-turning behavior. However, an alternative explanation, which should be discussed, is that cold water increases the tendency for upward turns. This could be an adaptive strategy since for temperatures > 4C turning swimming upwards is likely a good strategy to reach warmer water.

The paper currently also suffers from a lack of clarity which is largely created by figure organization. Four main and 38 supplemental figures are very unusual. I give some specific recommendations below but the authors should decide which data is truly supplemental, versus supporting important points made in the paper itself. There also appear to be supplemental figures that are never referenced in the text which makes traversing the supplements unnecessarily tedious.<br /> The N that was used as the basis for statistical tests and plots should be identified in the figures to improve interpretability. To improve rigor, the experimental procedures should be expanded. Specifically, the paper uses two thermal models which are not detailed at all in the methods section.

Reviewer #3 (Public Review):

In this study, the authors measured the behavioural responses of brown trout to the sudden availability of a choice between thermal environments. The data clearly show that these fish avoid colder temperatures than the acclimation condition, but generally have no preference between the acclimation condition or warmer water (though I think the speculation that the fish are slowly warming up is interesting). Further, the evidence is compelling that avoidance of cold water is a combination of thermotaxis and thermokinesis. This is a clever experimental approach and the results are novel, interesting, and have clear biological implications as the authors discuss. I also commend the team for an extremely robust, transparent, and clear explanation of the experimental design and analytical decisions. The supplemental material is very helpful for understanding many of the methodological nuances, though I admit that I found it overwhelming at times and wonder if it could be pruned slightly to increase readability. Overall, I think the conclusions are generally well-supported by the data, and I have no major concerns.

eLife assessment

This study describes the development and validation of an Automated Reproducible Mechano-stimulator (ARM), a valuable tool for standardizing and automating somatosensory behavior experiments. The data supporting the use of the ARM system are compelling, though the determination of whether that device emits any sounds, including in the ultrasonic range when in operation or when at rest, would add value to the study. Nevertheless, the ARM system is anticipated to be popular amongst somatosensory and pain researchers.

Reviewer #1 (Public Review):

Allodynia is commonly measured in the pain field using von Frey filaments, which are applied to a body region (usually hindpaw if studying rodents) by a human. While humans perceive themselves as being objective, as the authors noted, humans are far from consistent when applying these filaments. Not to mention, odors from humans, including those of different sexes, can influence animal behavior. There is thus a major unmet need for a way to automate this tedious von Frey testing process and to remove humans from the experiment. I have no major scientific concerns with the study, as the authors did an outstanding job of comparing this automated system to human experimenters in a rigorous and quantitative manner. They even demonstrated that their automated system can be used in conjunction with in vivo imaging techniques.

While it is somewhat unclear how easy and inexpensive this device will be, I anticipate everyone in the pain field will be clamoring to get their hands on a system like this. And given the mechanical nature of the device and the propensity for mice to urinate on things, I also wonder how frequently the device breaks/needs to be repaired. Perhaps some details regarding the cost and reliability of the device would be helpful to include, as these are the two things that could make researchers hesitant to adopt immediately.

The only major technical concern, which is easy to address, is whether the device generates ultrasonic sounds that rodents can hear when idle or operational, across the ultrasonic frequencies that are of biological relevance (20-110 kHz). These sounds are generally alarm vocalizations and can create stress in animals, and/or serve as cues of an impending stimulus (if indeed they are produced by the device).

Reviewer #2 (Public Review):

Summary:

Burdge, Juhmka, et al describe the development and validation of a new automated system for applying plantar stimuli in rodent somatosensory behavior tasks. This platform allows the users to run behavior experiments remotely, removing experimenter effects on animals and reducing variability in the manual application of stimuli. The system integrates well with other automated analysis programs that the lab has developed, providing a complete package for standardizing behavior data collection and analysis. The authors present extensive validations of the system against manual stimulus application. Some proof of concept studies also show how the system can be used to better understand the effect of experimenters on behavior and the effects of how stimuli are presented on the micro features of the animal withdrawal response.

Strengths:

If widely adopted, ARM has the potential to reduce variability in plantar behavior studies across and within labs and provide a means to standardize results. The system is well-validated and results clearly and convincingly presented. Most claims are well supported by experimental evidence.

Weaknesses:

ARM seems like a fantastic system that could be widely adopted, but no details are given on how a lab could build ARM, thus its usefulness is limited.

The ARM system appears to stop short of hitting the desired forces that von Frey filaments are calibrated toward (Figure 2). This may affect the interpretation of results.

The authors mention that ARM generates minimal noise; however, if those sounds are paired with stimulus presentation they could still prompt a withdrawal response. Including some 'catch' trials in an experiment could test for this.

The experimental design in Figure 2 is unclear- did each experimenter have their own cohort of 10 mice, or was a single cohort of mice shared? If shared, there's some concern about repeat testing.

Reviewer #3 (Public Review):

Summary:

This report describes the development and initial applications of the ARM (Automated Reproducible Mechano-stimulator), a programmable tool that delivers various mechanical stimuli to a select target (most frequently, a rodent hindpaw). Comparisons to traditional testing methods (e.g., experimenter application of stimuli) reveal that the ARM reduces variability in the anatomical targeting, height, velocity, and total time of stimulus application. Given that the ARM can be controlled remotely, this device was also used to assess the effect of the experimenter's presence on reflexive responses to mechanical stimulation. Lastly, the ARM was used to stimulate rodent hind paws while measuring neuronal activity in the basolateral nucleus of the amygdala (BLA), a brain region that is associated with the negative effect of pain. This device, and similar automated devices, will undoubtedly reduce experimenter-related variability in reflexive mechanical behavior tests; this may increase experimental reproducibility between laboratories.

Strengths:

Clear examples of variability in experimenter stimulus application are provided and then contrasted with uniform stimulus application that is inherent to the ARM.

Weaknesses:

Limited details are provided for statistical tests and inappropriate claims are cited for individual tests. For example, in Figure 2, differences between researchers at specific forces are reported to be supported by a 2-way ANOVA; these differences should be derived from a post-hoc test that was completed only if the independent variable effects (or interaction effect) were found to be significant in the 2-way ANOVA. In other instances, statistical test details are not provided at all (e.g., Figures 3B, 3C, Figure 4, Figure 6G).

One of the arguments for using the ARM is that it will minimize the effect that the experimenter's presence may have on animal behavior. In the current manuscript, the effects of the experimenter's presence on both habituation time and aspects of the withdrawal reflex are minimal for Researcher 2 and non-existent for Research 1. This is surprising given that Researcher 2 is female; the effect of experimenter presence was previously documented for male experiments as the authors appropriately point out (Sorge et al. PMID: 24776635). In general, this argument could be strengthened (or perhaps negated) if more than N=2 experiments were included in this assessment.

The in vivo BLA calcium imaging data feel out of place in this manuscript. Is the point of Figure 6 to illustrate how the ARM can be coupled to Inscopix (or other external inputs) software? If yes, the following should be addressed: why do the up-regulated and down-regulated cell activities start increasing/decreasing before the "event" (i.e., stimulus application) in Figure 6F? Why are the paw withdrawal latencies and paw distanced travelled values in Figures 6I and 6J respectively so much faster/shorter than those illustrated in Figure 5 where the same approach was used?

Another advance of this manuscript is the integration of a 500 fps camera (as opposed to a 2000 fps camera) in the PAWS platform. To convince readers that the use of this more accessible camera yields similar data, a comparison of the results for cotton swabs and pinprick should be completed between the 500 fps and 2000 fps cameras. In other words, repeat Supplementary Figure 3 with the 2000 fps camera and compare those results to the data currently illustrated in this figure.

eLife assessment

This study makes a valuable contribution to understanding antiviral responses in fish by revealing a role for the cell cycle protein kinase CDK2 in type I interferon signaling. The evidence supporting the authors' claims is solid, including both in vivo and in vitro investigative approaches. However, the mechanisms underlying CDK2 activity are not completely established. This work will be of interest to cell biologists, immunologists, and virologists.

Reviewer #1 (Public Review):

Summary:

The authors set out to evaluate the regulation of interferon (IFN) gene expression in fish, using mainly zebrafish as a model system. Similar to more widely characterized mammalian systems, fish IFN is induced during viral infection through the action of the transcription factor IRF3 which is activated by phosphorylation by the kinase TBK1. It has been previously shown in many systems that TBK1 is subjected to both positive and negative regulation to control IFN production. In this work, the authors find that the cell cycle kinase CDK2 functions as a TBK1 inhibitor by decreasing its abundance through the recruitment of the ubiquitinylation ligase, Dtx4, which has been similarly implicated in the regulation of mammalian TBK1. Experimental data are presented showing that CDK2 interacts with both TBK1 and Dtx4, leading to TBK1 K48 ubiquitinylation on K567 and its subsequent degradation by the proteasome.

Strengths:

The strengths of this manuscript are its novel demonstration of the involvement of CDK2 in a process in fish that is controlled by different factors in other vertebrates and its clear and supportive experimental data.

Weaknesses:

The weaknesses of the study include the following. 1) It remains unclear whether the function described for CDK2 is regulatory, that is, it affects TBK1 levels during physiological responses such as viral infection or cell cycle progression, or if it is homeostatic, governing the basal abundance of TBK1 but not responding to signaling. 2) The authors have not explored whether the catalytic activity of CDK2 is required for TBK1 ubiquitinylation and, if so, what its target specificity is. 3) Given the multitude of CDK isoforms in fish, it remains unexplored whether the identified fish CDK2 homolog is a requisite cell cycle regulator or if its action in the cell cycle is redundant with other CDKs.

Reviewer #2 (Public Review):

Summary:

In this paper, the authors describe a novel function involving the cell cycle protein kinase CDK2, which binds to TBK1 (an essential component of the innate immune response) leading to its degradation in a ubiquitin/proteasome-dependent manner. Moreover, the E3 ubiquitin ligase, Dtx4, is implicated in the process by which CDK2 increases the K48-linked ubiquitination of TBK1. This paper presents intriguing findings on the function of CDK2 in lower vertebrates, particularly its regulation of IFN expression and antiviral immunity.

Strengths:

(1) The research employs a variety of experimental approaches to address a single question. The data are largely convincing and appear to be well executed.

(2) The evidence is strong and includes a combination of in vivo and in vitro experiments, including knockout models, protein interaction studies, and ubiquitination analyses.

(3) This study significantly impacts the field of immunology and virology, particularly concerning the antiviral mechanisms in lower vertebrates. The findings provide new insights into the regulation of IFN expression and the broader role of CDK2 in immune responses. The methods and data presented in this paper are highly valuable for the scientific community, offering new avenues for research into antiviral strategies and the development of therapeutic interventions targeting CDK2 and its associated pathways.

Weaknesses:

(1) While the study focuses on fish, the broader implications for other lower vertebrates and higher vertebrates are not extensively discussed.

(2) The study heavily relies on specific fish models, which may limit the generalizability of the findings across different species.

eLife assessment

This study provides a useful advance in generating mouse oligodendrocytes by direct lineage conversion from cortical astrocytes. The authors demonstrate that Sox10 converts astrocytes to MBP+ oligodendrocytes, whereas Olig2 expression converts astrocytes to PDFRalpha+ oligodendrocyte progenitor cells. The data supporting the conclusions are solid, but there are concerns regarding select figures and the experiments being limited to in vitro studies.

Reviewer #1 (Public Review):

Faiz et al. investigate small molecule-driven direct lineage reprogramming of mouse postnatal mouse astrocytes to oligodendrocyte lineage cells (OLCs). They use a combination of in vitro, in vivo, and computational approaches to confirm lineage conversion and to examine the key underlying transcription factors and signaling pathways. Lentiviral delivery of transcription factors previously reported to be essential in OLC fate determination-Sox10, Olig2, and Nkx2.2-to astrocytes allows for lineage tracing. They found that these transcription factors are sufficient in reprogramming astrocytes to iOLCs, but that the OLCs range in maturity level depending on which factor they are transfected with. They followed up with scRNA-seq analysis of transfected and control cultures 14DPT, confirming that TF-induced astrocytes take on canonical OLC gene signatures. By performing astrocyte lineage fate mapping, they further confirmed that TF-induced astrocytes give rise to iOLCs. Finally, they examined the distinct genetic drivers of this fate conversion using scRNA-seq and deep learning models of Sox10- astrocytes at multiple time points throughout the reprogramming. These findings are certainly relevant to diseases characterized by the perturbation of OLC maturation and/or myelination, such as Multiple Sclerosis and Alzheimer's Disease. Their application of such a wide array of experimental approaches gives more weight to their findings and allows for the identification of additional genetic drivers of astrocyte to iOLC conversion that could be explored in future studies. Overall, I find this manuscript thoughtfully constructed and only have a few questions to be addressed.

(1) The authors suggest that Sox10- and Olig2- transduced astrocytes result in distinct subpopulations iOLCs. Considering it was discussed in the introduction that these TFs cyclically regulate one another throughout differentiation, could they speculate as to why such varying iOLCs resulted from the induction of these two TFs?

(2) In Figure 1B it appears that the Sox10- MBP+ tdTomato+ cells decreases from D12 to D14. Does this make sense considering MBP is a marker of more mature OLCs?

(3) Previous studies have shown that MBP expression and myelination in vitro occurs at the earliest around 4-6 weeks of culturing. When assessing whether further maturation would increase MBP positivity, authors only cultured cells up to 22 DPT and saw no significant increase. Has a lengthier culture timeline been attempted?

(4) Figure S4D is described as "examples of tdTomatonegzsGreen+OLCmarker+ cells that arose from a tdTomatoneg cell with an astrocyte morphology." The zsGreen+ tdTomato- cell is not convincingly of "astrocyte morphology"; it could be a bipolar OLC. To strengthen the conclusions and remove this subjectivity, more extensive characterizations of astrocyte versus OLC morphology in the introduction or results are warranted. This would make this observation more convincing since there is clearly an overlap in the characteristics of these cell types.

Reviewer #2 (Public Review):

The study by Bajohr investigates the important question of whether astrocytes can generate oligodendrocytes by direct lineage conversion (DLR). The authors ectopically express three transcription factors - Sox10, Olig2 and Nkx6.2 - in cultured postnatal mouse astrocytes and use a combination of Aldh1|1-astrocyte fate mapping and live cell imaging to demonstrate that Sox10 converts astrocytes to MBP+ oligodendrocytes, whereas Olig2 expression converts astrocytes to PDFRalpha+ oligodendrocyte progenitor cells. Nkx6.2 does not induce lineage conversion. The authors use single-cell RNAseq over 14 days post-transduction to uncover molecular signatures of newly generated iOLs.

The potential to convert astrocytes to oligodendrocytes has been previously analyzed and demonstrated. Despite the extensive molecular characterization of the direct astrocyte-oligodendrocyte lineage conversion, the paper by Bajohr et al. does not represent significant progress. The entire study is performed in cultured cells, and it is not demonstrated whether this lineage conversion can be induced in astrocytes in vivo, particularly at which developmental stage (postnatal, adult?) and in which brain region. The authors also state that generating oligodendrocytes from astrocytes could be relevant for oligodendrocyte regeneration and myelin repair, but they don't demonstrate that lineage conversion can be induced under pathological conditions, particularly after white matter demyelination. Specific issues are outlined below.

(1) The authors perform an extensive characterization of Sox10-mediated DLR by scRNAseq and demonstrate a clear trajectory of lineage conversion from astrocytes to terminally differentiated MBP+ iOLCs. A similar type of analysis should be performed after Olig2 transduction, to determine whether transcriptomics of OPC induction overlaps with any phase of MBP+ oligodendrocyte induction.

(2) A complete immunohistochemical characterization of the cultures should be performed at different time points after Sox10 and Olig2 transduction to confirm OL lineage cell phenotypes.

Author response:

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

eLife assessment

This work presents valuable information about the specificity and promiscuity of toxic effector and immunity protein pairs. The evidence supporting the claims of the authors is currently incomplete, as there is concern about the methodology used to analyze protein interactions, which did not take potential differences in expression levels, protein folding, and/or transient interaction into account. Other methods to measure the strength of interactions and structural predictions would improve the study. The work will be of interest to microbiologists and biochemists working with toxin-antitoxin and effector-immunity proteins.

We thank the reviewers for considering this manuscript. We agree that this manuscript provides a valuable and cross-discipline introduction to new EI pair protein families where we focus on the EI pair’s flexibility and impacts on community structure. As such, we believe we have provided a solid foundation for future studies to examine non-cognate interactions and their possible effects on microbial communities. This, by definition, leaves some areas “incomplete” and, therefore, open for further investigations. While the methods we show do consider potential differences in binding assays, we have more explicitly addressed how “expression, protein folding, and/or transient binding” may play into this expanded EI pair model. We have also tempered the discussion of the proposed model, while also clearly highlighting other published evidence of non-cognate binding interactions between effector and immunity proteins. We have responded to the reviewers’ public comments (italicized below). 

In this revised manuscript, we have updated the main text, particularly the Discussion section, to include more careful language, explain past research better, and add new references to works showing non-cognate immunity proteins protecting against effectors in other systems. We have also updated the supplemental files with more analyses; the relevant procedures are in the Materials and Methods.

Public Reviews:

Note: Reviewer 1, who appeared to focus on a subset of the manuscript rather than the whole, based their comments on several inaccuracies, which we discuss below. We found the tone in this reviewer's comments to be, at times, inappropriate, e.g., using "harsh" and "simply too drastic" to imply that common structure-function analyses were outside of the field-standard methods. We also note that the reviewer took a somewhat atypical step in reviewing this manuscript by running and analyzing the potential protein-complex data in AlphaFold2 but did not discuss areas of low confidence within that model that may contradict their conclusions. We are concerned their approach muddled valid scientific criticisms with problematic conclusions.

Reviewer #1 (Public Review):

In this manuscript, Knecht, Sirias et al describe toxin-immunity pair from Proteus mirabilis. Their observations suggest that the immunity protein could protect against non-cognate effectors from the same family. They analyze these proteins by dissecting them into domains and constructing chimeras which leads them to the conclusion that the immunity can be promiscuous and that the binding of immunity is insufficient for protective activity.

Strengths:<br />  The manuscript is well written and the data are very well presented and could be potentially interesting. The phylogenetic analysis is well done, and provides some general insights.

Weaknesses:<br /> (1) Conclusions are mostly supported by harsh deletions and double hybrid assays. The later assays might show binding, but this method is not resolutive enough to report the binding strength. Proteins could still bind, but the binding might be weaker, transient, and out-competed by the target binding.

The phrasing of structure-function analyses as “harsh” is a bit unusual, as other research groups regularly use deletions and hybrid studies. Given the known caveats to deletion and domain substitutions, we included point-mutation analyses for both the effector and immunity proteins, as found on lines 105 - 113 and 255 - 261 in the current manuscript. These caveats are also why we coupled the in vitro binding analyses with in vivo protection experiments in two distinct experimental systems (E. coli and P. mirabilis). Based on this manuscript’s introductory analysis (where we define and characterize the genes, proteins, interactions, phylogenetics, and incidences in human microbiomes), the next apparent questions are beyond the scope of this study. Future approaches would include analyzing purified proteins from the effector (E) and immunity (I) protein families using biochemical assays, such as X-ray crystallography, circular dichroism spectroscopy, among others. 

Interestingly, most papers in the EI field do not measure EI protein affinity (Jana et al., 2019, Yadav et al., 2021). Notable exceptions are earlier colicin research (Wallis et al., 1995) and a new T6SS EI paper (Bosch et al., 2023) published as we first submitted this manuscript.

(2) While the authors have modeled the structure of toxin and immunity, the toxin-immunity complex model is missing. Such a model allows alternative, more realistic interpretation of the presented data. Firstly, the immunity protein is predicted to bind contributing to the surface all over the sequence, except the last two alpha helices (very high confidence model, iPTM>0.8). The N terminus described by the authors contributes one of the toxin-binding surfaces, but this is not the sole binding site. Most importantly, other parts of the immunity protein are predicted to interact closer to the active site (D-E-K residues). Thus, based on the AlphaFold model, the predicted mechanism of immunization remains physically blocking the active site. However, removing the N terminal part, which contributes large interaction surface will directly impact the binding strength. Hence, the toxin-immunity co-folding model suggests that proper binding of immunity, contributed by different parts of the protein, is required to stabilize the toxin-immunity complex and to achieve complete neutralization. Alternative mechanisms of neutralization might not be necessary in this case and are difficult to imagine for a DNase.

In response to the reviewer’s comment, we again reviewed the RdnE-RdnI AlphaFold2 complex predictions with the most updated version of ColabFold (1.5.2-patch with PDB100 and MMseq2) and have included them at the end of these responses [1].

However, the literature reports that computational predictions of E-I complexes often do not match experimental structural results (Hespanhol et al., 2022, Bosch et al., 2023). As such, we chose not to include the predicted cognate and non-cognate RdnE-I complexes from ColabFold (which uses AlphaFold2) and have not included this data in the revised manuscript. (It is notable that reviewer 1 found the proposed expanded model and research so interesting as to directly input and examine the AI-predicted RdnE-RdnI protein interactions in AlphaFold2.)

Discussion of the prevailing toxin-immunity complex model is in the introduction (lines 45-48) and Figure 5E. Further, there are various known mechanisms for neutralizing nucleases and other T6SS effectors, which we briefly state in the discussion (lines 359 - 361). More in-depth, these molecular mechanisms include active-site blocking (Benz et al., 2012), allosteric-site binding (Kleanthous et al., 1999 and Lu et al., 2014), enzymatic neutralization of the target (Ting et al., 2021), and structural disruption of both the active and binding sites (Bosch et al., 2023). Given this diversity of mechanisms, we did not presume to speculate on the as-of-yet unknown mechanism of RdnI protection. We have expanded discussion of these items in the revised manuscript.

(3) Dissection of a toxin into two domains is also not justified from a structural point of view, it is probably based on initial sequence analyses. The N terminus (actually previously reported as Pone domain in ref 21) is actually not a separate domain, but an integral part of the protein that is encased from both sides by the C terminal part. These parts might indeed evolve faster since they are located further from the active site and the central core of the protein. I am happy to see that the chimeric toxins are active, but regarding the conservation and neutralization, I am not surprised, that the central core of the protein fold is highly conserved. However, "deletion 2" is quite irrelevant - it deletes the central core of the protein, which is simply too drastic to draw any conclusions from such a construct - it will not fold into anything similar to an original protein, if it will fold properly at all.

The reviewer’s comment highlights why we turned to the chimera proteins to dissect the regions of RdnE (formerly IdrD-CT), as the deletions could result in misfolded proteins. (We initially examined RdnE in the years before the launch of AlphaFold2.) However, the reviewer is incorrect regarding the N-terminus of RdnE. The PoNe domain, while also a subfamily of the PD-(D/E)XK superfamily, forms a distinct clade of effectors from the PD-(D/E)XK domain in RdnE (formally IdrD-CT) as seen in Hespanhol et al., 2022; this is true for other DNase effectors as well. Many studies analyzing effectors within the PD-(D/E)XK superfamily only focus on the PD-(D/E)XK domain, removing just this domain from the context of the whole protein (Hespanhol et al., 2022; Jana et al., 2019). Of note, in RdnE, this region alone (containing the DNA-binding domain) is insufficient for DNase activity (unlike in PoNe). We have clarified this distinction in the results section of the current manuscript, visible in figure 2 .

(4) Regarding the "promiscuity" there is always a limit to how similar proteins are, hence when cross-neutralization is claimed authors should always provide sequence similarities. This similarity could also be further compared in terms of the predicted interaction surface between toxin and immunity.

Reviewer 1 points out a fundamental property of protein-protein interactions that has been isolated away from the impacts of such interactions on bacterial community structure. We have provided the whole protein alignments in figure 3 supplemental figure 3, the summary images in Figure 3D, and the protein phylogenetic trees in Figure 3C. We encourage others to consider the protein alignments as percent amino acid sequence similarity is not necessarily a good gauge for protein function and interactions. These data are publicly available on the OSF website associated with this manuscript https://osf.io/scb7z/, and we hope the community explores the data there.

In consideration of the enthusiasm to deeply dive into the primary research data, we have included the pairwise sequence identities across the entire proteins here: Proteus RdnI vs. Rothia RdnI: 23.6%; Proteus RdnI vs. Prevotella RdnI: 16.3%, Proteus RdnI vs. Pseudomonas RdnI: 14.6%; Rothia RdnI vs. Prevotella RdnI: 22.4%, Rothia RdnI vs. Pseudomonas RdnI: 17.6%; Prevotella RdnI vs. Pseudomonas RdnI: 19.5%. (As stated in response to reviewer 1 comment 2, we did not find it appropriate to make inferences based on AlphaFold2-predicted protein complexes.)

Overall, it looks more like a regular toxin-immunity couple, where some cross-reactions with homologues are possible, depending on how far the sequences have deviated. Nevertheless, taking all of the above into account, these results do not challenge toxin-immunity specificity dogma.

In this manuscript, we did not intend to dismiss the E-I specificity model but rather point out its limitations and propose an important expansion of that model that accounts for cross-protection and survival against attacks from other genera. We agree that it is commonly considered that deviations in amino acid sequence over time could result in cross-binding and protection (see lines 364-368). However, the impacts of such cross-binding on community structure, bacterial survival, and strain evolution were rarely addressed in prior literature, with exceptions such as in Zhang et al., 2013 and Bosch et al., 2023 among others. One key insight we propose and show in this manuscript is that cross-binding can be a fitness benefit in mixed communities; therefore, it could be selected for evolutionarily (lines 378-380), even potentially in host microbiomes.

Reviewer #2 (Public Review):

Summary:

The manuscript by Knecht et al entitled "Non-cognate immunity proteins provide broader defenses against interbacterial effectors in microbial communities" aims at characterizing a new type VI secretion system (T6SS) effector immunity pair using genetic and biochemical studies primarily focused on Proteus mirabilis and metagenomic analysis of human-derived data focused on Rothia and Prevotella sequences. The authors provide evidence that RdnE and RdnI of Proteus constitute an E-I pair and that the effector likely degrades nucleic acids. Further, they provide evidence that expression of non-cognate immunity derived from diverse species can provide protection against RdnE intoxication. Overall, this general line of investigation is underdeveloped in the T6SS field and conceptually appropriate for a broad audience journal. The paper is well-written and, aside from a few cases, well-cited. As detailed below however, there are several aspects of this paper where the evidence provided is somewhat insufficient to support the claims. Further, there are now at least two examples in the literature of non-cognate immunity providing protection against intoxication, one of which is not cited here (Bosch et al PMID 37345922 - the other being Ting et al 2018). In general therefore I think that the motivating concept here in this paper of overturning the predominant model of interbacterial effector-immunity cognate interactions is oversold and should be dialed back.

We agree that analyses focusing on flexible non-cognate interactions and protection are underdeveloped within the T6SS field and are not fully explored within a community structure. These ideas are rapidly growing in the field, as evidenced by the references provided by the reviewer. As stated earlier, we did not intend to overturn the prevailing model but rather have proposed an expanded model that accounts for protection against attacks from foreign genera.

Strengths:

One of the major strengths of this paper is the combination of diverse techniques including competition assays, biochemistry, and metagenomics surveys. The metagenomic analysis in particular has great potential for understanding T6SS biology in natural communities. Finally, it is clear that much new biology remains to be discovered in the realm of T6SS effectors and immunity.

Weaknesses:

The authors have not formally shown that RdnE is delivered by the T6SS. Is it the case that there are not available genetics tools for gene deletion for the BB2000 strain? If there are genetic tools available, standard assays to demonstrate T6SS-dependency would be to interrogate function via inactivation of the T6SS (e.g. by deleting tssC).

Our research group showed that the T6SS secretes RdnE (previously IdrD) in Wenren et al., 2013 (cited in lines 71-73). We later confirmed T6SS-dependent secretion by LC-MS/MS (Saak et al., 2017).  

For swarm cross-phyla competition assays (Figure 4), at what level compared to cognate immunity are the non-cognate immunity proteins being expressed? This is unclear from the methods and Figure 4 legend and should be elaborated upon. Presumably these non-cognate immunity proteins are being overexpressed. Expression level and effector-to-immunity protein stoichiometry likely matters for interpretation of function, both in vitro as well as in relevant settings in nature. It is important to assess if native expression levels of non-cognate cross-phyla immunity (e.g. Rothia and Prevotella) protect similarly as the endogenously produced cognate immunity. This experiment could be performed in several ways, for example by deleting the RdnE-I pair and complementing back the Rothia or Prevotella RdnI at the same chromosomal locus, then performing the swarm assay. Alternatively, if there are inducible expression systems available for Proteus, examination of protection under varying levels of immunity induction could be an alternate way to address this question. Western blot analysis comparing cognate to non-cognate immunity protein levels expressed in Proteus could also be important. If the authors were interested in deriving physical binding constants between E and various cognate and non-cognate I (e.g. through isothermal titration calorimetry) that would be a strong set of data to support the claims made. The co-IP data presented in supplemental Figure 6 are nice but are from E. coli cells overexpressing each protein and do not fully address the question of in vivo (in Proteus) native expression.

P. mirabilis strain ATCC29906 does not encode the rdnE and rdnI genes on the chromosome (NCBI BioSample: SAMN00001486) (line 151). Production of the RdnI proteins, including the cognate Proteus RdnI, comes from equivalent transgenic expression vectors. Specifically, the rdnI genes were expressed under the flaA promoter in P. mirabilis strain ATCC29906 (Table 1) for the swarm competition assays found in Figure 2C and Figure 4. This promoter results in constitutive expression in swarming cells (Belas et al., 1991; Jansen et al., 2003). In the revised manuscript, figure 4 Supplement Figure 2 shows the relative RdnI protein levels in these strains; we also clarified the expression constructs in the text (see reviewer 3, comment 1).

Lines 321-324, the authors infer differences between E and I in terms of read recruitment (greater abundance of I) to indicate the presence of orphan immunity genes in metagenomic samples (Figure 5A-D). It seems equally or perhaps more likely that there is substantial sequence divergence in E compared to the reference sequence. In fact, metagenomes analyzed were required only to have "half of the bases on reference E-I sequence receiving coverage". Variation in coverage again could reflect divergent sequence dipping below 90% identity cutoff. I recommend performing metagenomic assemblies on these samples to assess and curate the E-I sequences present in each sample and then recalculating coverage based on the exact inferred sequences from each sample.

This comment raises the challenges with metagenomic analyses. It was difficult to balance specificity to a particular species’ DNA sequence with the prevalence of any homologous sequence in the sample. Given the distinction in binding interactions among the examined four species, we opted to prioritize specificity, accepting that we were losing access to some rdnE and rdnI sequences in that decision. We chose a 90% identity cutoff, which, through several in silica controls, ensured that each sequence we identified was the rdnE or rdnI gene from that specific species. For the Version of Record, we have included analysis with a 70% cutoff in the supplemental information to try to account for sequence divergence by lowering the identity cutoffs as suggested. The data from the 70% identity cutoff was consistent with the original data from the 90% identity cutoff.

A description of gene-level read recruitment in the methods section relating to metagenomic analysis is lacking and should be provided.

Noted. We included the raw code and sequences on the OSF website associated with this manuscript https://osf.io/scb7z/.

Reviewer #3 (Public Review):

Summary:<br /> The authors discovered that the RdnE effector possesses DNase activity, and in competition, P. mirabilis having RdnE outcompetes the null strain. Additionally, they presented evidence that the RdnI immunity protein binds to RdnE, suppressing its toxicity. Interestingly, the authors demonstrated that the RdnI homolog from a different phylum (i.e., Actinomycetota) provides cross-species protection against RdnE injected from P. mirabilis, despite the limited identity between the immunity sequences. Finally, using metagenomic data from human-associated microbiomes, the authors provided bioinformatic evidence that the rdnE/rdnI gene pair is widespread and present in individual microbiomes. Overall, the discovery of broad protection by non-cognate immunity is intriguing, although not necessarily surprising in retrospect, considering the prolonged period during which Earth was a microbial battlefield/paradise.

Strengths:<br /> The authors presented a strong rationale in the manuscript and characterized the molecular mechanism of the RdnE effector both in vitro and in the heterologous expression model. The utilization of the bacterial two-hybrid system, along with the competition assays, to study the protective action of RdnI immunity is informative. Furthermore, the authors conducted bioinformatic analyses throughout the manuscript, examining the primary sequence, predicted structural, and metagenomic levels, which significantly underscore the significance and importance of the EI pair. 

Weaknesses:<br /> (1) The interaction between RdnI and RdnE appears to be complex and requires further investigation. The manuscript's data does not conclusively explain how RdnI provides a "promiscuous" immunity function, particularly concerning the RdnI mutant/chimera derivatives. The lack of protection observed in these cases might be attributed to other factors, such as a decrease in protein expression levels or misfolding of the proteins. Additionally, the transient nature of the binding interaction could be insufficient to offer effective defenses.

Yes, we agree with the reviewer and hope that grant reviewers’ share this colleague’s enthusiasm for understanding the detailed molecular mechanisms of RdnE-RdnI binding across genera. In the revised manuscript, we have continued to emphasize such caveats as the next frontier is clearly understanding the molecular mechanisms for RdnI cognate or non-cognate protection. In the revised manuscript, figure 4 Supplement Figure 2 shows the RdnI protein levels; we also clarified the expression constructs in the text (see reviewer 2, comment 2).

(2) The results from the mixed population competition lack quantitative analysis. The swarm competition assays only yield binary outcomes (Yes or No), limiting the ability to obtain more detailed insights from the data.

The mixed swam assay is needed when studying T6SS effectors that are primarily secreted during Proteus’ swarming activity (Saak et al. 2017, Zepeda-Rivera et al. 2018). This limitation is one reason we utilize in vitro, in vivo, and bioinformatic analyses. Though the swarm competition assay yields a binary outcome, we are confident that the observed RdnI protection is due to interaction with a trans-cell RdnE via an active T6SS. By contrast, many manuscripts report co-expression of the EI pair (Yadev et al., 2021, Hespanhol et al., 2022) rather than secreted effectors, as we have achieved in this manuscript.

(3) The discovery of cross-species protection is solely evident in the heterologous expression-competition model. It remains uncertain whether this is an isolated occurrence or a common characteristic of RdnI immunity proteins across various scenarios. Further investigations are necessary to determine the generality of this behavior.

We agree, which is why we submitted this paper as a launching point for further investigations into the generality of non-cognate interactions and their potential impact on community structure.

Comments from Reviewing Editor:<br />  - In addition to the references provided by reviewer#2, the first manuscript to show non-cognate binding of immunity proteins was Russell et al 2012 (PMID: 22607806).<br />  - IdrD was shown to form a subfamily of effectors in this manuscript by Hespanhol et al 2022 PMID: 36226828 that analyzed several T6SS effectors belonging to PDDExK, and it should be cited.

We appreciate that the reviewer and eLife staff pointed out missed citations. We have incorporated these studies and cited them in the revised manuscript.

[1] The Proteus RdnE in complex with either the Prevotella or Pseudomonas RdnI showed low confidence at the interface (pIDDT ~50-70%); this AI-predicted complex might support the lack of binding seen in the bacterial two-hybrid assay. On the other hand, the Proteus and Rothia RdnI N-terminal regions show higher confidence at the interface with RdnE. Despite this, the C-terminus of the Proteus RdnI shows especially low confidence (pIDDT ~50%) where it might interact near RdnE’s active site (as suggested by reviewer 1). Given this low confidence and the already stated inaccuracies of AI-generated complexes, we would rather wait for crystallization data to inform potential protection mechanisms of RdnI.

Author response image 1.

eLife assessment

This study provides valuable insights into the specificity and promiscuity of toxic effector and immunity protein pairs. While the work is improved over a previous version, there are still some questions regarding the methodology used to draw certain conclusions, rendering the study somewhat incomplete. Nevertheless, this work will likely be of interest to microbiologists and biochemists working with toxin-antitoxin systems and effector-immunity proteins.

Reviewer #3 (Public Review):

Summary:

The authors discovered that the RdnE effector possesses DNase activity, and in competition, P. mirabilis having RdnE outcompetes the null strain. Additionally, they presented evidence that the RdnI immunity protein binds to RdnE, suppressing its toxicity. Interestingly, the authors demonstrated that the RdnI homolog from a different phylum (i.e., Actinomycetota) provides cross-species protection against RdnE injected from P. mirabilis, despite the limited identity between the immunity sequences. Finally, using metagenomic data from human-associated microbiomes, the authors provided bioinformatic evidence that the rdnE/rdnI gene pair is widespread and present in individual microbiomes. Overall, the discovery of broad protection by non-cognate immunity is intriguing, although not necessarily surprising in retrospect, considering the prolonged period during which Earth was a microbial battlefield/paradise.

Strengths:

The authors presented a strong rationale in the manuscript and characterized the molecular mechanism of the RdnE effector both in vitro and in the heterologous expression model. The utilization of the bacterial two-hybrid system, along with the competition assays, to study the protective action of RdnI immunity is informative. Furthermore, the authors conducted bioinformatic analyses throughout the manuscript, examining the primary sequence, predicted structural, and metagenomic levels, which significantly underscore the significance and importance of the EI pair.

Weaknesses:

(1) The interaction between RdnI and RdnE appears to be complex and requires further investigation. The manuscript's data does not conclusively explain how RdnI provides a "promiscuous" immunity function, particularly regarding the RdnI mutant/chimera derivatives. The lack of protection observed in these cases might be attributed to other factors, such as a decrease in protein expression levels or misfolding of the proteins. Additionally, the transient nature of the binding interaction could be insufficient to offer effective defenses.<br /> (2) The results from the mixed population competition would benefit from quantitative analysis. The swarm competition assays only yield binary outcomes (Yes or No), limiting the ability to obtain more detailed insights from the data.<br /> (3) The discovery of cross-species protection is solely evident in the heterologous expression-competition model. It remains uncertain whether this is an isolated occurrence or a common characteristic of RdnI immunity proteins across various scenarios. Further investigations are necessary to determine the generality of this behavior.

Reviewer #4 (Public Review):

Summary:

Knecht et al. elucidate a Type VI Secretion System (T6SS) effector-immunity pair in Proteus mirabilis. They demonstrate that the effector protein RdnE exhibits DNase activity in vitro and induces toxicity when ectopically expressed in cells, the latter being neutralized by the cognate immunity protein RdnI. The authors identify major regions within RdnI necessary for the interaction and neutralization of RdnE. Notably, they report cross-talk where both cognate and non-cognate RdnI proteins can neutralize RdnE, mitigating its fitness advantage in bacterial co-swarm assays. A comprehensive metagenomic analysis revealed an abundance of rdnI over rdnE genes in most gut samples, suggesting a potential role of rdnI in providing a fitness advantage against bacteria encoding for RdnE effector.

Strengths:

The authors successfully combined biochemical and microbiological experiments with bioinformatics analysis to advance the understanding of the T6SS-mediated population dynamics in bacteria. The co-swarm functional assay is of particular interest as it demonstrates how bacterial strains carrying only rdnI immunity genes could potentially compete in the same niche with other species armed with toxic rdnE effector genes. The manuscript is well-written, and the figures are self-explanatory.

Weaknesses:

(1) How would the authors explain the discrepancy observed in Figure 4 G and Figure 4 S3 B where two RdnI proteins from Prevotella and Pseudomonas genera do not bind to RdnE_Proteus in BACTH, whereas they co-elute with a RdnE_Proteus-FLAG with efficiency comparable to the cross-neutralizing RdnI_Rothia? Similarly, the interaction results obtained in BACTH with RdnI truncate (Figure 4E) or chimeric RdnI (Figure 4I, lane 4) could be a result of an overexpressed T18-fusion variant.<br /> Alternative in vitro protein binding assay would be beneficial.

(2) Based on the bioinformatic analysis the Rothia and Prevotella species harboring rdnE/I genes co-occurred in 5% of metagenomes tested, suggesting that these bacteria could come into contact. The manuscript would benefit greatly if authors demonstrated that RdnI proteins from Rothia or Prevotella could cross-neutralize its own and its 'neighbor' RdnE effectors, for example in an E. coli viability assay. The cross-neutralizing co-swarming results (Figure 4F) could also be further validated in viability assay as shown in Figure 2 S1.

(3) Little is known about whether RdnE is delivered via T6SS as a full-length protein or as the shorter C-terminal fragment. There is a possibility that immunity proteins could recognize RdnE regions beyond the C-terminal 138 amino acids that authors used in their in vitro assays.

Reviewer #5 (Public Review):

This work investigates a T6SS effector-immunity pair from Proteus mirabilis. The authors make several interesting claims, particularly regarding the mechanism of effector inhibition by the immunity protein. However, it appears that these claims are not fully supported by the evidence provided.

I have read the revised manuscript, the public reviews, and the authors' updated responses to these reviews. In my opinion, the concerns raised by the reviewers remain relevant even after the authors' revisions. Since previous reviews have excellently described the strengths and weaknesses of this work, I will focus on my major concerns:

(1) The authors describe RdnE-RdnI, a T6SS effector-immunity pair from Proteus mirabilis. RdnE is actually the C-terminal domain of IdrD, a 1581-amino-acid protein containing PAAR and RHS domains. This work does not provide evidence for T6SS-dependent secretion of the effector, instead supplying references to previous works.

(2) While the authors claim the function of the RdnE domain is unknown, it was previously shown to be evolutionarily related to PoNe and TseV, both of which are known DNA nucleases. Although the authors cite the relevant references, they do not clearly disclose this information.

(3) The authors claim that RdnE contains two different domains: the first is the PD-(D/E)XK domain, and the second, referred to as "region 2," follows it. Unfortunately, no structural evidence is provided to support this claim, not even a predicted model demonstrating that these are indeed separate domains.

(4) One of the major claims made in this work is that RdnI binding to RdnE is not sufficient for RdnE inhibition, suggesting a more sophisticated mechanism. The authors base this theory on differences between the ability of RdnI to bind RdnE (shown using bacterial two-hybrid assays) and the ability to protect against RdnE toxicity in swarm competition assays. Specifically, they show that the first 85 amino acids of RdnI bind to the short RdnE domain in the bacterial two-hybrid assay but do not protect against the full-length effector in the swarm competition assay. They also demonstrate that performing seven mutations in conserved residues in RdnE or replacing parts of RdnI with parts from other RdnI homologs leads to the same phenomenon.

While these findings are interesting and even intriguing, in my opinion, the current evidence does not support their theory. A simple explanation for the differences between the assays is that while the N-terminal domain of RdnI is sufficient for binding to RdnE, inhibition of the active site of RdnE requires binding of a second domain to RdnE. In that sense, it should be noted that while the authors use co-IP assays to show the interaction between RdnE and full-length RdnI, they do not use it to show the interaction between RdnE and the first 85 amino acids of RdnI.

(5) The authors claim that a "conserved motif" within RdnI plays a role in the inhibition of RdnE. To investigate this, they replace this motif with sequences from several RdnI homologs, demonstrating that in one case, it is possible to exchange these conserved motifs between RdnI homologs that inhibit Proteus RdnE. However, they also show that even if the conserved motif is taken from an RdnI homolog that cannot inhibit Proteus RdnE, the hybrid protein can still protect cells in a swarm competition assay. This result raises concerns regarding the relevance of this conserved motif.

(6) Lastly, regarding the theory that immunity proteins can protect against non-cognate effectors, it appears that the authors based their theory on a single case where RdnI from Rothia protected against RdnE from Proteus. In my opinion, a more thorough investigation, involving testing many homologs, is needed to substantiate this theory.

Author response:

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

eLife assessment

In this fundamental study, the authors use innovative fine-scale motion capture technologies to study visual vigilance with high-acuity vision, to estimate the visual fixation of free-feeding pigeons. The authors present convincing evidence for use of the fovea to inspect predator cues, the behavioral state influencing the latency for fovea use, and the use of the fovea decreasing the latency to escape of both the focal individual and other flock members. The work will be of broad interest to behavioral ecologists.

We thank the editor for his interest and feedback on the manuscript. We hereafter addressed the comments of the reviewer.

Reviewer #1 (Public Review):

Summary:

The authors were using an innovative technic to study the visual vigilance based on high-acuity vision, the fovea. Combining motion-capture features and visual space around the head, the authors were able to estimate the visual fixation of free-feeding pigeon at any moment. Simulating predator attacks on screens, they showed that 1) pigeons used their fovea to inspect predators cues, 2) the behavioural state (feeding or head-up) influenced the latency to use the fovea and 3) the use of the fovea decrease the latency to escape of both the individual that foveate the predators cues but also the other flock members.

Strengths:

The paper is very interesting, and combines innovative technic well adapted to study the importance of high-acuity vision for spotting a predator, but also of improving the behavioural response (escaping). The results are strong and the models used are well-adapted. This paper is a major contribution to our understanding of the use of visual adaptation in a foraging context when at risk. This is also a major contribution to the understanding of individual interaction in a flock.

Weaknesses:

I have identified only two weaknesses:

(1) The authors often mixed the methods and the results, Which reduces the readability and fluidity of the manuscript. I would recommend the authors to re-structure the manuscript.<br /> (2) In some parts, the authors stated that they reconstructed the visual field of the pigeon, which is not true. They identified the foveal positions, but not the visual fields, which involve different sectors (binocular, monocular or blind). Similarly, they sometimes mix-up the area centralis and the fovea, which are two different visual adaptations.

Thank you for your positive feedback. We addressed these comments by restructuring the methods and result sections as suggested, and by checking the terminology and specific vocabulary used throughout the manuscript.

Reviewer #1 (Recommendations For The Authors):

First, I would like to say that I really enjoyed the manuscript. This is a great contribution to the field.

Thank you for the positive feedback, we highly appreciate it.

Then, I have some comments that I hope, would help the authors to improve the manuscript.

Major comments :

I would recommend the authors to restructure the methods and the results section. In many parts, the models used are presented in the results section, while this should be presented in the methods section.

Thank you for the suggestion, we now have ensured that the model descriptions are presented in the statistic section of the methods.

To me, the introduction is too long (more than 5 pages). It would be beneficial to reduce it considerably. Furthermore, in the introduction, it misses some information about the visual abilities of your species ((visual acuity, visual field, temporal resolution, contrast sensitivity....).

We agree that the introduction was very long and reduced it by removing the “Methodological issues” as well as strongly reducing the “Experimental rationales” to a minimum. We also added the missing information on the visual abilities of the pigeons in the “Experimental rationales” section (see L135-150). Please note, however, that we refer to the temporal resolution of pigeon vision in the method section, to associate it with the information of the used monitor’s resolution.

Minor comments :

Lines 37-39: This needs a reference.

A reference has been added (McFarland, 1977)

Lines 39-41: But see some papers published recently on Harris's hawks.

Thank you for the references, we added the citation as well as a few more papers (Kane et al., 2015; Kano et al., 2018; Miñano et al., 2023; Yorzinski & Platt, 2014).

Lines 41-43: This sentence needs a reference as well.

A reference has been added (Cresswell, 1994; M. H. R. Evans et al., 2018; Inglis & Lazarus, 1981)

Lines 56-103: In this paragraph, head down and head up also depends from the retinal map of the birds! Some birds have visual streak that allow them to see a potential threats while foraging. Please add more information about the importance of photoreceptors distribution.

Thank you for pointing out this issue. We rewrote the sentence L65-69 as follows to include the importance retinal structures.

“In several species, especially those with a broad visual field and specific retinal structures such as the visual streaks, individuals can simultaneously engage in foraging activities while remaining vigilant (Fernández-Juricic, 2012), likely using peripheral vision to detect approaching threats (Bednekoff & Lima, 2005; Cresswell et al., 2003; Kaby & Lind, 2003; Lima & Bednekoff, 1999).”

Lines 76-79: you wrote : ".... favor alternative hypotheses based on their findings". Which findings? You need to explain.

We rewrote this part as follows (L80-81).

“other studies found evidence for the risk dilution (Beauchamp & Ruxton, 2008) and the edge effect (Inglis & Lazarus, 1981) in their study systems.”

Lines 109-110: It would be good to have a representation of what is an area and a fovea, and how it is placed in the eye, what type of fovea exists and how it is related to visual field. Where does it project?

We now give a better description of the pigeon’s visual field in the experimental rationales section that we hope will help the reader understanding the key features of pigeon’s vision (see L135-150). Specifically, we now say in L137-138:

“they have one fovea centrally located in the retina of each eye, with an acuity of 12.6 c/deg (Hodos et al., 1985). Their fovea projects laterally at ~75° into the horizon in their visual field.”

Lines 109-113: You might need to see some new papers here about the fovea. See for instance Bringmann 2019.

Thank you for the suggestion, we now give a more precise definition of the fovea and refer to Bringmann’s paper for more details (L113-114):

“a pit-like area in the retina with high concentration of cone cells where visual acuity is highest, and is responsible for sharp, detailed, and color vision.”

Lines 113-120: Please explain how the visual field is related to fovea? Where is the fovea project in the visual fields?

Similarly to the question above, we now give a more precise description of the pigeon’s visual field (see L135-150).

Line 131-134: For a non-expert, you would need to explain what is micro, meso and macro scale?

These sentences have been removed when shortening the introduction and we are not referring to micro, meso and macro scales anymore.

Lines 134-136: Please explain in one sentence the technique here.

We now explain in one sentence how motion capture enables the tracking of head and body orientation (L130-132):

“Motion capture cameras track with high accuracy the 3D position of markers, which, when attached to the pigeon’s head and body, enables to reconstruct the rotations of the head and body in all directions.”

Line 140: You presented here for the first time the word "foveation". Has this term been used before? If so, please add a reference. If not, please explain what you mean by foveation precisely.

Thank you for noticing this lack. We are now providing the following definition “directing visual focus to the fovea to achieve the clearest vision” in the first place where we mention the term foveation (L149-150).

Lines 146-148: Please explain why this proves that it is appropriate to not record eyes movements, and is this true for every behaviours?

We acknowledge that some small eye movement might occur and reduce the accuracy of the method. This error is considered in the system using the +-10 degrees range around the foveas. The lines the reviewer referred to were removed when shortening the introduction, but we added an explanation in the paragraph describing pigeon vision to make it clearer (L147-150):

“Yet, it should be noted that their eye movement was not tracked in our system, although it is typically confined within a 5 degrees range (Wohlschläger et al., 1993). We thus considered this estimation error of the foveation (directing visual focus to the fovea to achieve the clearest vision) in our analysis, as a part of the error margin (see Methods).”

Lines 161-163: What is the frontal and binocular field for? You would need to explain the different fields of view and what they are supposed to be for.

Furthermore, does the visual field of pigeon have been studied? If so, you would need to add more information about it.

This information is now given in the new paragraph describing the pigeon’s vision in the  “Experimental rationales” section (see L135-150).

Figure 1: It is not clear here which panels correspond to a, b or c. Please use some boxes to clarify it.

Thank you for the comment, we now have made the figure’s sub-panels clearer.

Lines 193-194: You wrote "... such as foveas (also known as the area centralis). No, this is not the same.

(1) In some species, you have two foveas, one placed centrally in the retina, one place temporally. So the fovea is not the area centralis.

(2) Second, some species do have an area centralis but without a fovea.

Thank you for pointing out the inaccuracy. In this case, we were referring specifically to the pigeon’s fovea which is sometimes referred to as “area centralis”, but we now changed the sentence as follow to avoid any confusion (L174-175):

“The initial two hypotheses (Hypotheses 1 and 2) aim to examine whether foveation correlates with predator detection.”

Lines 192-212: I did not understand the logic of the hypotheses numbers? Why do you have 2.1 but not 3.1 for instance? And if you have two hypotheses for the within a global one (for instance, 2.1 and 2.2), what is the main hypothesis 2? You should explain more here because we get lost here and in the result section as well.

We recognize this section might have appeared confusing to the reader. In short, we had four main hypotheses: 1) the fovea is used to evaluate predator cues, 2) the latency to foveate is related to vigilance behaviors. These first 2 hypotheses aimed to determine if the latency to foveate on the predator cue could be related to the detection. 3) foveation is related to the escape response of the pigeons and 4) there is a collective influence in the escape response. We further divided some of the hypotheses into 2 sub-hypotheses whenever 2 different tests were used to answer the same question. We have modified this section to be clearer.

Lines 224-229: Where are the figures and statistics for these results?

These results are presented in Table S1. We apologize for forgetting to add this reference and have now added it (L211).

Lines 229-231: This should be in the method section.

This model explanation (as well as all other hereafter mentioned) have been moved to the method section as suggested.

Lines 248-252: This should be in the method section. Furthermore, you should better explain the model selection.

Please see earlier comment. Additionally, we are now better explaining how the model has been built.

Figure 2: It is not clear on the figure which letters correspond to which panels. Please improve the readability of the figure.

It was modified accordingly.

Lines 274-278: This should be in the method section.

Please see earlier comment.

Line 281: The "Fig.3" should be mentioned in the previous sentence.

It was modified accordingly.

Figure 3: Please explain why the latency to foveate had negative values in Fig.2 but not here, and not in Fig. 4 as well. This again highlights that we missed a number of information in the methods about the transformation of the data and the model selection.

The variable presented in Fig 2d is not the latency to foveate but the “Normalized frequency at which the object was observed within foveal regions” (hypothesis 1). It represents the amount of time the object was lying within one of the foveal regions of the individual (“how long the pigeons foveated on it”), further normalized to unit sum to make all objects comparable. This variable was indeed logit-transformed (hence the negative value) to improve residual fit in the model, but this information (as well as other transformations) are always clearly stated on the axis caption of the graphs. Additionally, we now have improved the statistical analysis section to make the model used for each hypothesis testing clearer. But please let us know if you have suggestions for a further improvement in terms of presentation.

Lines 297-301: This should be in the method section.

Please see earlier comment.

Lines 301-305: Fig. 3 b and c only referred to the two first factors. Please add more figures for the other factors. This could be in supp. Mat.

We added the 3 graphs for the proportion of time foveating on the monitor, the saccade rate and the proportion of time foveating on conspecifics in the supplementary (Fig S6).

Lines 306-309: This should be in methods, and you should have explained in methods how you performed your model selection.....

We prefer leaving this paragraph in the result section, as it was intended to give the reader extra information on the predictive power of the different variables (by comparing the effectiveness of the models including one variable at a time, all the rest being equal) and not on the model selection per se. However, we now explain our goal better in the statistics section regarding this analysis (L635-636):

“We further tested the relative predictive power of the different test variables by comparing the resulting models’ efficiency using AIC scores.”

Lines 317-319: This should be in the method section.

Please see earlier comment.

Lines 320-322: This should be in the method section.

Please see earlier comment.

Lines 332-334: This should be in the method section.

Please see earlier comment.

Lines 334-336: Then, if this is not significant, you cannot say that.

Thank you for noticing the inaccuracy, we have now rephrased it as (L298-299):

“Earlier foveation of the first pigeon was not significantly related to an earlier escape responses among the other flock members, although there was a trend (χ2(1) = 3.66, p = 0.0559).”

Line 336: Please explain why you did different models. We missed a lot of information in the method about your strategy for statistics.?

We have now added a lot more information on the models in the statistics section, according to this comment as well as the previous ones. We hope the explanations of the analyses are now clearer to the reader.

Lines 339-349: This should be in the method section.

Please see earlier comment.

Results section: As you may have understood, there are too many sentence that should be moved into the method section. Futhermore, I would recommend to modify the headdings so that they are more biologically speaking. Similarly to what you have done in the discussion section.

Thank you for the comments. We agree with most of them, and have modified the manuscript accordingly. Additionally, we now use the same headings in the results section as the ones used in the discussion to make the text easier to follow.

Lines 500-501: What were the body weight of the pigeon? At which weight of their full weight they were?

This information is now added (492 ± 41g; mean ± SD). We did not control the amount of food during our experiments and only ensured 24h without food by feeding the pigeons after the experiment was completed. This information was added as follows (L454-456):

“On experimental days, they were fed only after the experiments was completed; this ensures 24-hour no feeding at the time of the experiment, although we did not control the amount of the food over the course of the experimental periods.”

Line 522-523: Those screens are very good for pigeons.

Thank you for the positive comment, we indeed tried to match bird vision as close as possible.

Lines 527-528: At which frequency was produced the moving stimulus? Your screen can display up to 144Hz, which is very good. But can your laptop do it? If not, it is important to mention it as pigeons may have a temporal resolution of vision up to 149Hz.

Our laptop indeed supports 144Hz display. In addition, we now mention the temporal resolution of pigeon vision (L480-482).

“We specifically chose a monitor with high temporal resolution to match the pigeon’s Critical Flicker Fusion Frequency (threshold at which a flickering light is perceived by the eye as steady) that reaches up to 143Hz (Dodt & Wirth, 1954).”

Lines 555-572: Did you use a control shape in your experiment? Indeed, they may escape because of a moving pattern but not a predator shape?

We did not use a control shape, as the aim of the experiment was not to directly test the effect of the shape itself. We designed the predator cue to resemble an approaching predator to ensure a response from the pigeons, but it might be that other shapes would have worked as well.

Lines 588-589: Please explain why the coordinate system of the pigeon's head is considered as the visual field?

From what I have understood, you did not reconstruct the visual fields, but only the position of the fovea. This should be noted like this as visual field involves more than a sphere around the head (binocular and monocular sectors, blind sectors, vertical extension....).

Thank you for noticing the inaccuracy, we indeed did not consider other sectors of the visual field and therefore rephrased it as (L551): “the location of the objects and conspecifics from the pigeon’s perspective”.

Lines 601-604: How much does it represent?

As this was estimated by visual inspection, we do not have the exact percentage of data loss that was caused by grooming. However, because of the number of cameras in the SMART BARN motion capture system, it is reliable in detecting markers inside the space in “ideal” conditions (without occlusion). For example, a similar set-up found marker track loss of only <1% using a model bird (Itahara & Kano 2022)

Itahara, A., & Kano, F. (2022). “Corvid Tracking Studio”: A custom-built motion capture system to track head movements of corvids. Japanese Journal of Animal Psychology, 72(1), 1–16. https://doi.org/10.2502/janip.72.1.1

Lines 610-612: You would need to cite Wood 1917 and Hodos et al. 1991 who described the presence of a fovea in this species.

We added both citations to the manuscript.

Line 611: Again, the fovea is not egal to area centralis.

Thank you, we changed it as well.

Lines 625-626: you wrote "... in a few instances....". Please explain more. How many? What proportion?

This happened in 9 observations out of 120. We now specify it in the text as well (L587-589):

“in a few instances (9 out of 120 observations), pigeons foveated on the model predator after the looming stimulus had disappeared, but these cases were excluded from our analysis.”

Lines 640-653: We missed a lot of information in the section "statistical analysis". If you moved most of the sentence from the results that describe the methods in the method section, that would be much better. Furthermore, you would need to explain more what statistics you used, which model selection, what type of data transformation....

We agree this section lacked information, and we moved the information from the result to the statistics section.

Supplmentary materials: boxplots from Fig. S1 and S2 are too small and impossible to read. Please improve the readability.

We now have enlarged these plots to make them more readable.

eLife assessment

In this fundamental study, the authors use innovative fine-scale motion capture technologies to study visual vigilance with high-acuity vision, to estimate the visual fixation of free-feeding pigeons. The authors present compelling evidence for use of the fovea to inspect predator cues, the behavioral state influencing the latency for fovea use, and the use of the fovea decreasing the latency to escape of both the focal individual and other flock members. The work will be of broad interest to behavioral ecologists.

Public Review:

The authors used an innovative technic to study the visual vigilance based on high-acuity vision, the fovea. Combining motion-capture features and visual space around the head, the authors were able to estimate the visual fixation of free-feeding pigeon at any moment. Simulating predator attacks on screens, they showed that 1) pigeons used their fovea to inspect predators cues, 2) the behavioural state (feeding or head-up) influenced the latency to use the fovea and 3) the use of the fovea decrease the latency to escape of both the individual that foveate the predators cues but also the other flock members.

The paper is very interesting, and combines innovative technic well adapted to study the importance of high-acuity vision for spotting a predator, but also of improving the behavioural response (escaping). The results are strong and the models used are well-adapted. This paper is a major contribution to our understanding of the use of visual adaptation in a foraging context when at risk. This is also a major contribution to the understanding of individual interaction in a flock.

Joint Public Review:

The manuscript "Engineering of PAClight1P78A: A High-Performance Class-B1 GPCR-Based Sensor for PACAP1-38" by Cola et al. presents the development of a novel genetically encoded sensor, PAClight1P78A, based on the human PAC1 receptor. The authors provide a thorough in vitro and in vivo characterization of this sensor, demonstrating its potential utility across various applications in life sciences, including drug development and basic research.

The main criticism of this manuscript after initial review is that the PACLight1 sensor has not been shown to detect the release of endogenous PACAP, whether in culture, in vivo, or ex vivo. The authors appear to be cognizant of this significant limitation (for a PACAP sensor) but no significant changes to address this limitation are provided in the revision.

While the sensor that is described here is new and the experimental results support the conclusions, the sensor reported here is not suited for the detection of endogenous PACAP release in vivo. In some respects, this manuscript could be seen as a stepping stone for further development either by the authors or other groups. Indeed, in many cases initial versions of genetically encoded sensors undergo substantial development post-publication, as exemplified by the evolution of GCaMP. However, the situation with the PAClight sensor reported here requires a different approach. Unlike GCaMP, which was one of the first genetically encoded calcium indicators, PAClight is another variant in a series of GPCR-fluorophore conjugates, following methodologies similar to those developed in the Lin Tian lab and the multiple GRAB-based sensors from Yulong Li's lab. These sensors have already demonstrated in vivo applicability, setting a standard that PAClight must meet or exceed to confirm its value and novelty.

Given that the title of the manuscript, "Probing PAC1 receptor activation across species with an engineered sensor," implies broader applicability, it potentially misleads readers about the sensor's utility in vivo, where "in vivo" should be understood as referring to the detection of endogenous PACAP release.

To align the manuscript with the expectations set by its title, it is crucial that the authors either provide substantial in vivo validation (ability to detect endogenous release of PACAP) or revise the title and the text to clarify that the sensor is primarily intended to detect exogenously applied PACAP. This clarification will ensure that the manuscript accurately reflects the sensor's current capabilities and scope of use.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript "Engineering of PAClight1P78A: A High-Performance Class-B1 GPCR-Based Sensor for PACAP1-38" by Cola et al. presents the development of a novel genetically encoded sensor, PAClight1P78A, based on the human PAC1 receptor. The authors provide a thorough in vitro and in vivo characterization of this sensor, demonstrating its potential utility across various applications in life sciences, including drug development and basic research.

The diverse methods to validate PAClight1P78A demonstrate a comprehensive approach to sensor engineering by combining biochemical characterization with in vivo studies in rodent brains and zebrafish. This establishes the sensor's biophysical properties (e.g., sensitivity, specificity, kinetics, and spectral properties) and demonstrates its functionality in physiologically relevant settings. Importantly, the inclusion of control sensors and the testing of potential intracellular downstream effects such as G-protein activation underscore a careful consideration of specificity and biological impact.

Strengths:

The fundamental development of PAClight1P78A addresses a significant gap in sensors for Class-B1 GPCRs. The iterative design process -starting from PAClight0.1 to the final PAClight1P78A variant - demonstrates compelling optimization. The innovative engineering results in a sensor with a high apparent dynamic range and excellent ligand selectivity, representing a significant advancement in the field. The rigorous in vitro characterization, including dynamic range, ligand specificity, and activation kinetics, provides a critical understanding of the sensor's utility. Including in vivo experiments in mice and zebrafish larvae demonstrates the sensor's applicability in complex biological systems.

Weaknesses:

The manuscript shows that the sensor fundamentally works in vivo, albeit in a limited capacity. The titration curves show sensitivity in the nmol range at which endogenous detection might be possible. However, perhaps the sensor is not sensitive enough or there are not any known robust paradigms for PACAP release. A more detailed discussion of the sensors's limitations, particularly regarding in vivo applications and the potential for detecting endogenous PACAP release, would be helpful.

We thank the reviewer for carefully analyzing our in vivo data and highlighting the limitation of our results regarding the sensor’s applicability in detecting endogenous PACAP. We added several sections conversing future possibilities for optimization in the discussion (see paragraphs 2-4). We agree that a more specific discussion of the limitations of our study is an important addition to help design future experiments. 

There are several experiments with an n=1 and other low single-digit numbers. I assume that refers to biological replicates such as mice or culture wells, but it is not well defined. n=1 in experimental contexts, particularly in Figure 1, raises significant concerns about the exact dynamic range of the sensor, data reproducibility, and the robustness of conclusions drawn from these experiments. Also, ROI for cell cultures, like in Figure 1, is not well defined. The methods mentioned ROIs were manually selected, which appears very selective, and the values in Figure 1c become unnecessarily questionable. The lack of definition for "ROI" is confusing. Do ROIs refer to cells, specific locations on the cell membrane, or groups of cells? It would be best if the authors could use unbiased methods for image analysis that include the majority of responsive areas or an explanation of why certain ROIs are included or excluded.

We thank the reviewer for the helpful suggestions. We have increased the number of replicates to n=3 for both HEK293T and neuron data depicted in Fig.1c. Furthermore, we have added Fig.1c’ containing the quantification of the maximum responses obtained in the dataset shown in Fig.1c also depicting the single values for each replicate. To clarify the definition of an ROI in our manuscript, we have detailed the process of ROI selection in the Methods section “Cell culture, imaging and quantification section”. Additionally, we also increased mouse numbers for in vivo PACAP infusions in mice (see Figure 4g).

Reviewer #2 (Public Review):

Summary:

The PAClight1 sensor was developed using an approach successful for the development of other fluorescence-based GPCR sensors, which is the complete replacement of the third intracellular loop of the receptor with a circularly-permuted green fluorescent protein. When expressed in HEK cells, this sensor showed good expression and a weak but measurable response to the extracellular presence of PACAP1-38 (a

F/Fo of 43%). Additional mutation near the site of insertion of the linearized GPF, at the C-terminus of the receptor, and within the second intracellular loop produced a final optimized sensor with F/Fo of >1000%. Finally, screening of mutational libraries that also included alterations in the extracellular ligand-binding domain of the receptor yielded a molecule, PAClight1P78A, that exhibited a high ligand-dependent fluorescence response combined with a high differential sensitivity to PACAP (EC50 30 nM based on cytometric sorting of stably transfected HEK293 cells) compared to its congener VIP, (with which PACAP shares two highly related receptors, VPAC1 and VPAC2) as well as several unrelated neuropeptides, and significantly slowed activation kinetics by PACAP in the presence of a 10-fold molar excess of the PAC1 antagonist PACAP6-38. A structurally highly similar control construct, PAClight1P78Actl, showed correspondingly similar basal expression in HEK293 cells, but no PACAP-dependent enhancement in fluorescent properties.

PAClight1P78A was expressed in neurons of the mouse cortex via AAV9.hSyn-mediated gene transduction. Slices taken from PAClight1P78A-transfected cortex, but not slices taken from PAClight1P78Actl-transfected cortex exhibited prompt and persistent elevation of F/Fo after 2 minutes of perfusion with PACAP1-38 which persisted for up to 14 minutes and was statistically significant after perfusion with 3000, but not 300 or 30 nM, of peptide. Likewise, microinfusion of 200 nL of 300 uM PACAP1-38 into the cortex of optical fiber-implanted freely moving mice elicited a F/Fo (%) of greater than 15, and significantly higher than that elicited by application of similar concentrations of VIP, CRF, or enkephalin, or vehicle alone. In vivo experiments were carried out in zebrafish larvae by the introduction of PAClight1P78A into single-cell stage Danio rerio embryos using a Tol2 transposase-based plasmid with a UAS promoter via injection (of plasmid and transposase mRNA), and sorting of post-fertilization embryos using a marker for transgenesis carried in the UAS :

PAClight1P78A construct. Expression of PAClight1P78A was directed to cells in the olfactory bulb which express the fish paralog of the human PAC1 receptor by using the Tg(GnRH3:gal4ff) line, and fluorescent signals were elicited by intracerebroventricular administration of PACAP1-38 at a single concentration (1 mM), which were specific to PACAP and to the presence of PAClight1P78A per se, as controlled by parallel experiments in which PAClight1P78Actl instead of PAClight1P78A was contained in the transgenic plasmid.

Major strengths and weaknesses of the methods and results

The report represents a rigorous demonstration of the elicitation of fluorescent signals upon pharmacological exposure to PACAP in nervous system tissue expressing PAClight1P78A in both mammals (mice) and fish (zebrafish larvae). Figure 4d shows a change in GFP fluorescence activation by PACAP occurring several seconds after the cessation of PACAP perfusion over a two-minute period, and its persistence for several minutes following. One wonders if one is apprehending the graphical presentation of the data incorrectly, or if the activation of fluorescence efficiency by ligand presentation is irreversible in this context, in which case the utility of the probe as a real-time indicator, in vivo, of released peptide might be diminished.

We thank the reviewer for their careful consideration of our manuscript and agree that the activation of PAClight persisting for several minutes at micromolar concentrations could be a potential limitation for in vivo applications. We added a possible explanation for the persisting sensor activation in response to artificial application of PACAP38 in paragraph 3 of the discussion. We agree that this addition eases the interpretation of PAClight signals detected in vivo. 

Appraisal of achievement of aims, and data support of conclusions:

Small cavils with controls are omitted for clarity; the larger issue of appraisal of results based on the scope of the designed experiments is discussed in the section below. An interesting question related to the time dependence of the PACAP-elicited activation of PAClight1P87A is its onset and reversibility, and additional data related to this would be welcome.

We agree that the reversibility of the sensor’s fluorescence is indeed an important feature especially for detecting endogenous PACAP release. Our data indicate that the sensor’s fluorescence is reversible when detecting small to medium doses of PACAP38 (see Figure 4d – Application of 30-300nM) that are presumably closer to physiological concentrations than the non-reversible concentration of 3000nM. Please, see also our new discussion on peptide concentrations in paragraph 4 of our discussion. For future experiments, it is indeed advisable to adjust the interval of repeated applications to the decay of the response at the respective concentration. Considering, the long-lasting downstream effects of endogenous signaling, longer intervals between ligand applications are generally preferred to match more closely the physiological range in which endogenous PAC1 is most likely affective. 

Discussion of the impact of the work, and utility of the methods and data:

Increasingly, neurotransmitter function may be observed in vivo, rather than by inferring in vivo function from in vitro, in cellular, or ex vivo experimentation. This very valuable report discloses the invention of a genetically encoded sensor for the class B1 GPCR PAC1. PAC1 is the major receptor for the neuropeptide PACAP, which in turn is a major neurotransmitter involved in brain response to psychogenic stress, or threat, in vertebrates as diverse as mammals and fishes. If this sensor possesses the sensitivity to detect endogenously released PACAP in vivo it will indeed be an impactful tool for understanding PACAP neurotransmission (and indeed PACAP action in general, in immune and endocrine compartments as well) in future experiments.

However, the sensor has not yet been used to detect endogenously released PACAP. Until this has been done, one cannot answer the question as to whether the levels of exogenously perfused/administered PACAP used here merely to calibrate the sensor's sensitivity are indeed unphysiologically high. If endogenous PACAP levels don't get that high, then the sensor will not be useful for its intended purpose. The authors should address this issue and allude to what kind of experiments would need to be done in order to detect endogenous PACAP release in living tissue in intact animals. The authors could comment upon the success of other GPCR sensors that have been used to observe endogenous ligand release, and where along the pathway to becoming a truly useful reagent this particular sensor is.

We thank the reviewer for highlighting the lack in clarity that the scope of this paper was not intended to cover the detection of endogenous PACAP release. We therefore expanded our discussion to encompass the intended purpose of detecting artificially infused or applied PAC1 agonists, such as conducting fundamental tests of drug specificity and developing new pharmacological ligands to selectively target PAC1. This includes a more detailed discussion of our in vivo findings and a clearer phrasing that stresses the potential application for applied drugs and not endogenous PACAP (see last paragraph in the discussion).

We also agree that little is known about endogenous concentrations of PACAP in the brain. However, we have supplemented our discussion with several references estimating lower concentrations of PACAP and other peptides in vivo, suggesting average PACAP levels below the detection threshold of the sensor. Importantly, within certain brain regions and in closer proximity to release sites, significantly higher concentrations might be reached. Additionally, our data indicate that the concentrations observed under our current conditions do not saturate the sensor in vivo.  

We therefore acknowledge the reviewer’s comment on the sensor’s potential limitations under our current experimental conditions. Hence, we expanded our discussion and suggest the use of higher resolution imaging to potentially reveal loci of high PACAP concentrations, which should be validated by future studies (see also our added discussion in paragraph 4). 

Reviewer #3 (Public Review):

Summary:

The manuscript introduces PAClight1P78A, a novel genetically encoded sensor designed to facilitate the study of class-B1 G protein-coupled receptors (GPCRs), focusing on the human PAC1 receptor. Addressing the significant challenge of investigating these clinically relevant drug targets, the sensor demonstrates a high dynamic range, excellent ligand selectivity, and rapid activation kinetics. It is validated across a variety of experimental contexts including in vitro, ex vivo, and in vivo models in mice and zebrafish, showcasing its utility for high-throughput screening, basic research, and drug development efforts related to GPCR dynamics and pharmacology.

Strengths:

The innovative design of PAClight1P78A successfully bridges a crucial gap in GPCR research by enabling realtime monitoring of receptor activation with high specificity and sensitivity. The extensive validation across multiple models emphasizes the sensor's reliability and versatility, promising significant contributions to both the scientific understanding of GPCR mechanisms and the development of novel therapeutics. Furthermore, by providing the research community with detailed methodologies and access to the necessary viral vectors and plasmids, the authors ensure the sensor's broad applicability and ease of adoption for a wide range of studies focused on GPCR biology and drug targeting.

Weaknesses

To further strengthen the manuscript and validate the efficacy of PAClight1P78A as a selective PACAP sensor, it is crucial to demonstrate the sensor's ability to detect endogenous PACAP release in vivo under physiological conditions. While the current data from artificial PACAP application in mouse brain slices and microinfusion in behaving mice provide foundational insights into the sensor's functionality, these approaches predominantly simulate conditions with potentially higher concentrations of PACAP than naturally occurring levels.

We thank the reviewer for their valuable comments and agree that the use of PAClight for detecting endogenous PACAP will be of big interest for the scientific community and should be a goal for future research. Considering the time, equipment and additional animal licenses necessary, we are convinced that these questions would go beyond the scope of the current paper and might rather be addressed in a follow-up publication. We therefore rephrased the discussion and added more details to clarify further the intended purpose of the current study. Additionally, we added a paragraph in the discussion suggesting experiments needed to validate PAClight for putative future in vivo applications. 

Although the sensor's specificity for the PAC1 receptor and its primary ligand is a pivotal achievement, exploring its potential application to other GPCRs within the class-B1 family or broader categories could enhance the manuscript's impact, suggesting ways to adapt this technology for a wider array of receptor studies. Additionally, while the sensor's performance is convincingly demonstrated in short-term experiments, insights into its long-term stability and reusability in more prolonged or repeated measures scenarios would be valuable for researchers interested in chronic studies or longitudinal behavioral analyses. Addressing these aspects could broaden the understanding of the sensor's practical utility over extended research timelines.

We extend our gratitude to the reviewer for diligently assessing our results. 

Indeed, the very high level of sensitivity that we could achieve in PAClight leads us to think that potentially a grafting-based approach, such as the one we’ve recently described for class-A GPCR-based sensors (PMID: 37474807) could also work for the direct generation of multiple class-B1 sensors based on the optimized fluorescent protein module present in PAClight. Unfortunately, considering the amount of work that testing this hypothesis would entail, we are not able to perform these experiments in the context of this revision, and would rather pursue them as a future project. Nevertheless, we have expanded the discussion of the manuscript with a paragraph with these considerations.

While we lack comprehensive data on the long-term stability of the sensor, our preliminary findings from photometry recordings optimization indicate consistent baseline expression of PAClight and PACLight ctrl over several weeks. Conducting experiments to systematically assess stability would require several months, which is currently impractical due to limitations in tools and licenses for repeated in vivo infusions. Hence, we intend to include these experiments in potential follow-up studies.

Furthermore, the current in vivo experiments involving microinfusion of PACAP near sensor-expressing areas in behaving mice are based on a relatively small sample size (n=2), which might limit the generalizability of the findings. Increasing the number of subjects in these experimental groups would enhance the statistical power of the results and provide a more robust assessment of the sensor's in vivo functionality. Expanding the sample size will not only validate the findings but also address potential variability within the population, thereby reinforcing the conclusions drawn from these crucial experiments.

We agree with the reviewer that a sample size of N=2 is not sufficient for in vivo recordings. We therefore increased the sample size and now present recordings with 5 PAClight1P78A and 4 PACLight-control mice. Of note, the new data validate our previous findings and conclusions and give a better idea of the variability in vivo that we now discuss in much more detail in the discussion (see paragraph 2). 

Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

The lower potency of maxadilan activation might reflect broader implications for ligand-receptor dynamics. Perhaps the authors could discuss the maxadilan binding from a structural perspective, including AlphaFold models. Also, discussing how these findings might influence sensor application in diverse biological contexts would be insightful. Clear definitions and consistent use of these terms are crucial for ensuring that readers understand the methods and results.

We would like to thank the reviewer for the comments. As part of this work, we did not obtain a dose-response curve for maxadilan peptide, and only reported the maximal response of the sensor to a high concentration of the peptide (10 µM). Thus, our findings would rather inform us on the maximal efficacy of the peptide, as opposed to its potency towards the PAC1R. Furthermore, we would like to point out that due to the lack of structural details for any GPCR-based sensor published to date, we cannot make any molecularly accurate conclusion regarding the precise reasons why a different ligand (in this case the sandfly maxadilan) induces a lower maximal efficacy of the response compared to the endogenous cognate ligand of the receptor. We do not believe that AlphaFold models can accurately replace structural information in this regard, especially given the consideration that the aminoacid linker regions between the GPCR and the fluorescent protein, which are a critical determinant of allosteric chromophore modulation by ligand-induced conformational changes, typically obtain the lowest confidence score in all AlphaFold predicted structural models of GPCR-based sensors. Finally, we would like to refer the reviewer to a very nice recent publication (PMID: 32047270) which resolved the structures of each of these peptides bound to the PAC1 receptor-Gs protein complex, which provides accurate molecular details on the different modalities of receptor binding and activation by PACAP138  versus maxadilan.

Reviewer #2 (Recommendations For The Authors):

The authors are congratulated on the meticulous achievement of their aim, i.e. a fluorescence-based sensor for the detection of PACAP with in vivo utility. Whether or not this sensor will have the requisite sensitivity to detect the release of endogenous PACAP within various regions of the nervous system, in response to specific environmental stimuli or changes in brain or physiological state, remains to be determined.

We thank the reviewer for the very positive evaluation of our manuscript and for the suggested additions that will improve the strength of our arguments.

We agree that the in vivo detection of endogenous PACAP will be an important objective for future studies. Due to time, resource and animal license constraints, we are not able to address this objective in our current study, but we now detail possible future experiments in the discussion section. Please see also our answer to the suggested discussion points previously.

Reviewer #3 (Recommendations For The Authors):

To comprehensively assess the sensor's sensitivity and specificity to endogenous PACAP, I recommend conducting additional in vivo experiments where PAClight1P78A is expressed in neurons that endogenously express the Pac1r receptor (using Adcyap1r1-Cre mouse line). These experiments should involve applying sensory or emotional stimuli known to evoke PACAP release or activating upstream PACAP-expressing neurons. Such studies would offer valuable data on the sensor's performance under natural physiological conditions and its potential utility for exploring PACAP's roles in vivo.

We express our gratitude to the reviewer for providing detailed methodological approaches to examine endogenous PACAP release. These suggestions will prove invaluable for future investigations and are important additions to a follow-up publication. As mentioned earlier, we have incorporated some of these approaches into our discussion. Additionally, we have underscored the existing limitations in detecting endogenous PACAP in vivo and emphasized the relevance of PAClight for drug development purposes.

eLife assessment

This fundamental paper reports a new biosensor to study G protein-coupled receptor activation by the pituitary adenylyl cyclase-activating polypeptide (PACAP) in cell culture, ex vivo (mouse brain slices), and in vivo (zebrafish, mouse). Convincing data are presented that show the new sensor works with high affinity in vitro, while requiring very high (non-physiological) concentrations of exogenous PACAP when applied to intact tissues. The sensor has not yet been used to detect endogenously released PACAP, raising questions about whether the sensor can be used for its intended purpose. While further work must be pursued to achieve broad in vivo applications under physiological conditions, the new tool will be of interest to cell biologists, especially those studying the large and significant GPCR family.

eLife assessment

This useful study describes an antibody-free method to map G-quadruplexes (G4s) in vertebrate cells. While the method might have potential, the current analysis is primarily descriptive and does not add substantial new insights beyond existing data (e.g., PMID:34792172). While the datasets provided might constitute a good starting point for future functional studies, additional data and analyses would be needed to fully support the major conclusions and, at the same time, clarify the advantage of this method over other methods. Specifically, the strength of the evidence for DHX9 interfering with the ability of mESCs to differentiate by regulating directly the stability of either G4s or R-loops is still incomplete.

Reviewer #1 (Public Review):

Summary:

Non-B DNA structures such as G4s and R-loops have the potential to impact genome stability, gene transcription, and cell differentiation. This study investigates the distribution of G4s and R-loops in human and mouse cells using some interesting technical modifications of existing Tn5-based approaches. This work confirms that the helicase DHX9 could regulate the formation and/or stability of both structures in mouse embryonic stem cells (mESCs). It also provides evidence that the lack of DHX9 in mESCs interferes with their ability to differentiate.

Strengths:

HepG4-seq, the new antibody-free strategy to map G4s based on the ability of Hemin to act as a peroxidase when complexed to G4s, is interesting. This study also provides more evidence that the distribution pattern of G4s and R-loops might vary substantially from one cell type to another.

Weaknesses:

This study is essentially descriptive and does not provide conclusive evidence that lack of DHX9 does interfere with the ability of mESCs to differentiate by regulating directly the stability of either G4 or R-loops. In the end, it does not substantially improve our understanding of DHX9's mode of action.

There is no in-depth comparison of the newly generated data with existing datasets and no rigorous control was presented to test the specificity of the hemin-G4 interaction (a lot of the hemin-dependent signal seems to occur in the cytoplasm, which is unexpected).

The authors talk about co-occurrence between G4 and R-loops but their data does not actually demonstrate co-occurrence in time. If the same loci could form alternatively either R-loops or G4 and if DHX9 was somehow involved in determining the balance between G4s and R-loops, the authors would probably obtain the same distribution pattern. To manipulate R-loop levels in vivo and test how this affects HEPG4-seq signals would have been helpful.

This study relies exclusively on Tn5-based mapping strategies. This is a problem as global changes in DNA accessibility might strongly skew the results. It is unclear at this stage whether the lack of DHX9, BLM, or WRN has an impact on DNA accessibility, which might underlie the differences that were observed. Moreover, Tn5 cleaves DNA at a nearby accessible site, which might be at an unknown distance away from the site of interest. The spatial accuracy of Tn5-based methods is therefore debatable, which is a problem when trying to demonstrate spatial co-occurrence. Alternative mapping methods would have been helpful.

Reviewer #2 (Public Review):

Summary:

In this study, Liu et al. explore the interplay between G-quadruplexes (G4s) and R-loops. The authors developed novel techniques, HepG4-seq and HBD-seq, to capture and map these nucleic acid structures genome-wide in human HEK293 cells and mouse embryonic stem cells (mESCs). They identified dynamic, cell-type-specific distributions of co-localized G4s and R-loops, which predominantly localize at active promoters and enhancers of transcriptionally active genes. Furthermore, they assessed the role of helicase Dhx9 in regulating these structures and their impact on gene expression and cellular functions.

The manuscript provides a detailed catalogue of the genome-wide distribution of G4s and R-loops. However, the conceptual advance and the physiological relevance of the findings are not obvious. Overall, the impact of the work on the field is limited to the utility of the presented methods and datasets.

Strengths:

(1) The development and optimization of HepG4-seq and HBD-seq offer novel methods to map native G4s and R-loops.

(2) The study provides extensive data on the distribution of G4s and R-loops, highlighting their co-localization in human and mouse cells.

(3) The study consolidates the role of Dhx9 in modulating these structures and explores its impact on mESC self-renewal and differentiation.

Weaknesses:

(1) The specificity of the biotinylation process and potential off-target effects are not addressed. The authors should provide more data to validate the specificity of the G4-hemin.

(2) Other methods exploring a catalytic dead RNAseH or the HBD to pull down R-loops have been described before. The superior quality of the presented methods in comparison to existing ones is not established. A clear comparison with other methods (BG4 CUT&Tag-seq, DRIP-seq, R-CHIP, etc) should be provided.

(3) Although the study demonstrates Dhx9's role in regulating co-localized G4s and R-loops, additional functional experiments (e.g., rescue experiments) are needed to confirm these findings.

(4) The manuscript would benefit from a more detailed discussion of the broader implications of co-localized G4s and R-loops.

(5) The manuscript lacks appropriate statistical analyses to support the major conclusions.

(6) The discussion could be expanded to address potential limitations and alternative explanations for the results.

Reviewer #3 (Public Review):

Summary:

The authors developed and optimized the methods for detecting G4s and R-loops independent of BG4 and S9.6 antibody, and mapped genomic native G4s and R-loops by HepG4-seq and HBD-seq, revealing that co-localized G4s and R-loops participate in regulating transcription and affecting the self-renewal and differentiation capabilities of mESCs.

Strengths:

By utilizing the peroxidase activity of G4-hemin complex and combining proximity labeling technology, the authors developed HepG4-seq (high throughput sequencing of hemin-induced proximal labelled G4s) , which can detect the dynamics of G4s in vivo. Meanwhile, the "GST-His6-2xHBD"-mediated CUT&Tag protocol (Wang et al., 2021) was optimized by replacing fusion protein and tag, the optimized HBD-seq avoids the generation of GST fusion protein aggregates and can reflect the genome-wide distribution of R-loops in vivo.

The authors employed HepG4-seq and HBD-seq to establish comprehensive maps of native co-localized G4s and R-loops in human HEK293 cells and mouse embryonic stem cells (mESCs). The data indicate that co-localized G4s and R-loops are dynamically altered in a cell type-dependent manner and are largely localized at active promoters and enhancers of transcriptionally active genes.

Combined with Dhx9 ChIP-seq and co-localized G4s and R-loops data in wild-type and dhx9KO mESCs, the authors confirm that the helicase Dhx9 is a direct and major regulator that regulates the formation and resolution of co-localized G4s and R-loops.

Depletion of Dhx9 impaired the self-renewal and differentiation capacities of mESCs by altering the transcription of co-localized G4s and R-loops-associated genes.

In conclusion, the authors provide an approach to studying the interplay between G4s and R-loops, shedding light on the important roles of co-localized G4s and R-loops in development and disease by regulating the transcription of related genes.

Weaknesses:

As we know, there are at least two structure data of S9.6 antibody very recently, and the questions about the specificity of the S9.6 antibody on RNA:DNA hybrids should be finished. The authors referred to (Hartono et al., 2018; Konig et al., 2017; Phillips et al., 2013) need to be updated, and the authors' bias against S9.6 antibodies needs also to be changed. However, as the authors had questioned the specificity of the S9.6 antibody, they should compare it in parallel with the data they have and the data generated by the widely used S9.6 antibody.

Although HepG4-seq is an effective G4s detection technique, and the authors have also verified its reliability to some extent, given the strong link between ROS homeostasis and G4s formation, and hemin's affinity for different types of G4s, whether HepG4-seq reflects the dynamics of G4s in vivo more accurately than existing detection techniques still needs to be more carefully corroborated.

Author response:

eLife assessment

This useful study describes an antibody-free method to map G-quadruplexes (G4s) in vertebrate cells. While the method might have potential, the current analysis is primarily descriptive and does not add substantial new insights beyond existing data (e.g., PMID:34792172). While the datasets provided might constitute a good starting point for future functional studies, additional data and analyses would be needed to fully support the major conclusions and, at the same time, clarify the advantage of this method over other methods. Specifically, the strength of the evidence for DHX9 interfering with the ability of mESCs to differentiate by regulating directly the stability of either G4s or R-loops is still incomplete.

We thank the editors for their helpful comments.

Given that antibody-based methods have been reported to leave open the possibility of recognizing partially folded G4s and promoting their folding, we have employed the peroxidase activity of the G4-hemin complex to develop a new method for capturing endogenous G4s that significantly reduces the risk of capturing partially folded G4s. We will be happy to clarify the advantage of our method.

In the Fig. 7, we applied the Dhx9 CUT&Tag assay to identify the G4s and R-loops directly bound by Dhx9 and further characterized the differential Dhx9-bound G4s and R-loops in the absence of Dhx9. Dhx9 is a versatile helicase capable of directly resolving R-loops and G4s or promoting R-loop formation (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). Furthermore, we showed that depletion of Dhx9 significantly altered the levels of G4s or R-loops around the TSS or gene bodies of several key regulators of mESC and embryonic development, such as Nanog, Lin28a, Bmp4, Wnt8a, Gata2, and Lef1, and also their RNA levels (Fig.7 I). The above evidence is sufficient to support the transcriptional regulation of mESCs cell fate by directly modulating the G4s or R-loops within the key regulators of mESCs.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Non-B DNA structures such as G4s and R-loops have the potential to impact genome stability, gene transcription, and cell differentiation. This study investigates the distribution of G4s and R-loops in human and mouse cells using some interesting technical modifications of existing Tn5-based approaches. This work confirms that the helicase DHX9 could regulate the formation and/or stability of both structures in mouse embryonic stem cells (mESCs). It also provides evidence that the lack of DHX9 in mESCs interferes with their ability to differentiate.

Strengths:

HepG4-seq, the new antibody-free strategy to map G4s based on the ability of Hemin to act as a peroxidase when complexed to G4s, is interesting. This study also provides more evidence that the distribution pattern of G4s and R-loops might vary substantially from one cell type to another.

We appreciate your valuable points.

Weaknesses:

This study is essentially descriptive and does not provide conclusive evidence that lack of DHX9 does interfere with the ability of mESCs to differentiate by regulating directly the stability of either G4 or R-loops. In the end, it does not substantially improve our understanding of DHX9's mode of action.

In this study, we aimed to report new methods for capturing endogenous G4s and R-loops in living cells. Dhx9 has been reported to directly unwind R-loops and G4s or promote R-loop formation (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). To understand the direct Dhx9-bound G4s and R-loops, we performed the Dhx9 CUT&Tag assay and analyzed the co-localization of Dhx9-binding sites and G4s or R-loops. We found that 47,857 co-localized G4s and R-loops are directly bound by Dhx9 in the wild-type mESCs and 4,060 of them display significantly differential signals in absence of Dhx9, suggesting that redundant regulators exist as well. We showed that depletion of Dhx9 significantly altered the RNA levels of several key regulators of mESC and embryonic development, such as Nanog, Lin28a, Bmp4, Wnt8a, Gata2, and Lef1, which coincides with the significantly differential levels of G4s or R-loops around the TSS or gene bodies of these genes (Fig.7). The comprehensive molecular mechanism of Dhx9 action is indeed not the focus of this study. We will work on it in the future studies. Thank you for the comments.

There is no in-depth comparison of the newly generated data with existing datasets and no rigorous control was presented to test the specificity of the hemin-G4 interaction (a lot of the hemin-dependent signal seems to occur in the cytoplasm, which is unexpected).

The specificity of hemin-G4-induced peroxidase activity and self-biotinylation has been well demonstrated in previous studies (PMID: 19618960, 22106035, 28973477, 32329781). In the Fig.1A, we compared the hemin-G4-induced biotinylation levels in different conditions. Cells treated with hemin and Bio-An exhibited a robust fluorescence signal, while the absence of either hemin or Bio-An almost completely abolished the biotinylation signals, suggesting a specific and active biotinylation activity. To identify the specific signals, we have included the non-label control and used this control to call confident HepG4 peaks in all HepG4-seq assays.

The hemin-RNA G4 complex has also been reported to have mimic peroxidase activity and trigger similar self-biotinylation signals as DNA G4s (PMID: 32329781, 31257395, 27422869). Therefore, it is not surprising to observe hemin-dependent signals in the cytoplasm generated by cytoplasmic RNA G4s.

In the revised version, we will include careful comparison between our data and previous datasets.

The authors talk about co-occurrence between G4 and R-loops but their data does not actually demonstrate co-occurrence in time. If the same loci could form alternatively either R-loops or G4 and if DHX9 was somehow involved in determining the balance between G4s and R-loops, the authors would probably obtain the same distribution pattern. To manipulate R-loop levels in vivo and test how this affects HEPG4-seq signals would have been helpful.

Single-molecule fluorescence studies have shown the existence of a positive feedback mechanism of G4 and R-loop formation during transcription (PMID: 32810236, 32636376), suggesting that G4s and Rloops could co-localize at the same molecule. Dhx9 is a versatile helicase capable of directly resolving R-loops and G4s or promoting R-loop formation (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). Although depletion of Dhx9 resulted in 6,171 Dhx9-bound co-localized G4s and R-loops with significantly altered levels of G4s or R-loops, only 276 of them (~4.5%) harbored altered G4s and R-loops, suggesting that the interacting G4s and R-loops are rare in living cells. Nowadays, the genome-wide co-occurrence of two factors are mainly obtained by bioinformatically intersection analysis. We agreed that the heterogenous distribution between cells will give false positive co-occurrence patterns. We will carefully discuss this point in the revised version. At the same time, we will make efforts to develop a new method to map the co-localized G4 and R-loop in the same molecule in the future study.

This study relies exclusively on Tn5-based mapping strategies. This is a problem as global changes in DNA accessibility might strongly skew the results. It is unclear at this stage whether the lack of DHX9, BLM, or WRN has an impact on DNA accessibility, which might underlie the differences that were observed. Moreover, Tn5 cleaves DNA at a nearby accessible site, which might be at an unknown distance away from the site of interest. The spatial accuracy of Tn5-based methods is therefore debatable, which is a problem when trying to demonstrate spatial co-occurrence. Alternative mapping methods would have been helpful.

In this study, we used the recombinant streptavidin monomer and anti-GP41 nanobody fusion protein (mSA-scFv) to specifically recognize hemin-G4-induced biotinylated G4 and then recruit the recombinant GP41-tagged Tn5 protein to these G4s sites. Similarly, the recombinant V5-tagged N-terminal hybrid-binding domain (HBD) of RNase H1 specifically recognizes R-loops and recruit the recombinant protein G-Tn5 (pG-Tn5) with the help of anti-V5 antibody. Therefore, the spatial distance of Tn5 to the target sites is well controlled and very short, and also the recruitment of Tn5 is specifically determined by the existence of G4s in HepG4-seq and R-loops in HBD-seq.

Reviewer #2 (Public Review):

Summary:

In this study, Liu et al. explore the interplay between G-quadruplexes (G4s) and R-loops. The authors developed novel techniques, HepG4-seq and HBD-seq, to capture and map these nucleic acid structures genome-wide in human HEK293 cells and mouse embryonic stem cells (mESCs). They identified dynamic, cell-type-specific distributions of co-localized G4s and R-loops, which predominantly localize at active promoters and enhancers of transcriptionally active genes. Furthermore, they assessed the role of helicase Dhx9 in regulating these structures and their impact on gene expression and cellular functions.

The manuscript provides a detailed catalogue of the genome-wide distribution of G4s and R-loops. However, the conceptual advance and the physiological relevance of the findings are not obvious. Overall, the impact of the work on the field is limited to the utility of the presented methods and datasets.

Strengths:

(1) The development and optimization of HepG4-seq and HBD-seq offer novel methods to map native G4s and R-loops.

(2) The study provides extensive data on the distribution of G4s and R-loops, highlighting their co-localization in human and mouse cells.

(3) The study consolidates the role of Dhx9 in modulating these structures and explores its impact on mESC self-renewal and differentiation.

We appreciate your valuable points.

Weaknesses:

(1) The specificity of the biotinylation process and potential off-target effects are not addressed. The authors should provide more data to validate the specificity of the G4-hemin.

The specificity of hemin-G4-induced peroxidase activity and self-biotinylation has been well demonstrated in previous studies (PMID: 19618960, 22106035, 28973477, 32329781). In the Fig.1A, we compared the hemin-G4-induced biotinylation levels in different conditions. Cells treated with hemin and Bio-An exhibited a robust fluorescence signal, while the absence of either hemin or Bio-An almost completely abolished the biotinylation signals, suggesting a specific and active biotinylation activity.

(2) Other methods exploring a catalytic dead RNAseH or the HBD to pull down R-loops have been described before. The superior quality of the presented methods in comparison to existing ones is not established. A clear comparison with other methods (BG4 CUT&Tag-seq, DRIP-seq, R-CHIP, etc) should be provided.

Thank you for the suggestions. We will include the comparisons in the revised version.

(3) Although the study demonstrates Dhx9's role in regulating co-localized G4s and R-loops, additional functional experiments (e.g., rescue experiments) are needed to confirm these findings.

Dhx9 has been demonstrate as a versatile helicase capable of directly resolving R-loops and G4s or promoting R-loop formation in previous studies (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). We believe that the current new dataset and previous studies are enough to support the capability of Dhx9 in regulating co-localized G4s and R-loops.

(4) The manuscript would benefit from a more detailed discussion of the broader implications of co-localized G4s and R-loops.

Thank you for the suggestions. We will include a more detailed discussion in the revised version.

(5) The manuscript lacks appropriate statistical analyses to support the major conclusions.

We apologized for this point. Whereas we have applied careful statistical analyses in this study, lacking of some statistical details make people hard to understand some conclusions. We will carefully add details of all statistical analysis.

(6) The discussion could be expanded to address potential limitations and alternative explanations for the results.

Thank you for the suggestions. We will include a more detailed discussion about this point in the revised version.

Reviewer #3 (Public Review):

Summary:

The authors developed and optimized the methods for detecting G4s and R-loops independent of BG4 and S9.6 antibody, and mapped genomic native G4s and R-loops by HepG4-seq and HBD-seq, revealing that co-localized G4s and R-loops participate in regulating transcription and affecting the self-renewal and differentiation capabilities of mESCs.

Strengths:

By utilizing the peroxidase activity of G4-hemin complex and combining proximity labeling technology, the authors developed HepG4-seq (high throughput sequencing of hemin-induced proximal labelled G4s), which can detect the dynamics of G4s in vivo. Meanwhile, the "GST-His6-2xHBD"-mediated CUT&Tag protocol (Wang et al., 2021) was optimized by replacing fusion protein and tag, the optimized HBD-seq avoids the generation of GST fusion protein aggregates and can reflect the genome-wide distribution of R-loops in vivo.

The authors employed HepG4-seq and HBD-seq to establish comprehensive maps of native co-localized G4s and R-loops in human HEK293 cells and mouse embryonic stem cells (mESCs). The data indicate that co-localized G4s and R-loops are dynamically altered in a cell type-dependent manner and are largely localized at active promoters and enhancers of transcriptionally active genes.

Combined with Dhx9 ChIP-seq and co-localized G4s and R-loops data in wild-type and dhx9KO mESCs, the authors confirm that the helicase Dhx9 is a direct and major regulator that regulates the formation and resolution of co-localized G4s and R-loops.

Depletion of Dhx9 impaired the self-renewal and differentiation capacities of mESCs by altering the transcription of co-localized G4s and R-loops-associated genes.

In conclusion, the authors provide an approach to studying the interplay between G4s and R-loops, shedding light on the important roles of co-localized G4s and R-loops in development and disease by regulating the transcription of related genes.

We appreciate your valuable points.

Weaknesses:

As we know, there are at least two structure data of S9.6 antibody very recently, and the questions about the specificity of the S9.6 antibody on RNA:DNA hybrids should be finished. The authors referred to (Hartono et al., 2018; Konig et al., 2017; Phillips et al., 2013) need to be updated, and the authors' bias against S9.6 antibodies needs also to be changed. However, as the authors had questioned the specificity of the S9.6 antibody, they should compare it in parallel with the data they have and the data generated by the widely used S9.6 antibody.

Thank you for the updating information about the structure data of S9.6 antibody. We politely disagree the specificity of the S9.6 antibody on RNA:DNA hybrids. The structural studies of S9.6 (PMID: 35347133, 35550870) used only one RNA:DNA hybrid to show the superior specificity of S9.6 on RNA:DNA hybrid than dsRNA and dsDNA. However, Fabian K. et al has reported that the binding affinities of S9.6 on RNA:DNA hybrid exhibits obvious sequence-dependent bias from null to nanomolar range (PMID: 28594954). We will include the comparison between S9.6-derived data and our HBD-seq data in the revised version.

Although HepG4-seq is an effective G4s detection technique, and the authors have also verified its reliability to some extent, given the strong link between ROS homeostasis and G4s formation, and hemin's affinity for different types of G4s, whether HepG4-seq reflects the dynamics of G4s in vivo more accurately than existing detection techniques still needs to be more carefully corroborated.

Thank you for pointing out this issue. In the in vitro hemin-G4 induced self-biotinylation assay, parallel G4s exhibit higher peroxidase activities than anti-parallel G4s. Thus, the dynamics of G4 conformation could affect the HepG4-seq signals (PMID: 32329781). In the future, people may need to combine HepG4-seq and BG4s-eq to carefully explain the endogenous G4s. We will carefully discuss this point in the revised version.

eLife assessment

This valuable paper compares blood gene signature responses between small cohorts of individuals with mild and severe COVID-19. The authors provide solid evidence for distinct transcriptional profiles during early COVID-19 infections that may be predictive of severity, within the limitations of studying human patients displaying heterogeneity in infection timelines and limited cohort size.

Reviewer #1 (Public Review):

Summary:

Medina et al, 2023 investigated the peripheral blood transcriptional responses in patients with diversifying disease outcomes. The authors characterized the blood transcriptome of four non-hospitalized individuals presenting mild disease and four patients hospitalized with severe disease. These individuals were observed longitudinally at three timepoints (0-, 7-, and 28-days post recruitment), and distinct transcriptional responses were observed between severe hospitalized patients and mild non-hospitalized individuals, especially during 0- and 7-day collection timepoints. Particularly, the authors found that increased expression of genes associated with NK cell cytotoxicity is associated with mild outcomes. Additional co-regulated gene network analyses positively correlates T cell activity with mild disease and neutrophil degranulation with severe disease.

Strengths:

The longitudinal measurements in individual participants at consistent collection intervals can offer an added dimension to the dataset that involves temporal trajectories of genes associated with disease outcomes and is a key strength of the study. The use of co-expressed gene networks specific to the cohort to complement enrichment results obtained from pre-determined gene sets can offer valuable insights into new associations/networks associated with disease progression and warrants further analyses on the biological functions enriched within these co-expressed network modules.

Weaknesses:

There is a large difference in the infection timeline (onset of symptom to recruitment) between mild and severe patient cohort. As immune responses during early infection can be highly dynamic, the differences in infection timeline may bias transcriptional signatures observed between the groups. The study is also limited by a small cohort size.

Comments on revised version:

The authors have addressed the specific concerns brought forth by the reviewers.

Reviewer #2 (Public Review):

In their manuscript, Medina and colleagues investigate transcriptional differences between mild and severe SARS-CoV-2 infections. Their analyses are very comprehensive incorporating a multitude of bioinformatics tools ranging from PCA plots, GSEA and DEG analysis, protein-protein interaction network, and weighted correlation network analyses. They conclude that in mild COVID-19 infection NK cell functionality is compromised and this is connected to cytokine interactions and Th1/Th2 cell differentiation pathways cross-talk, bridging the innate and the adaptive arms of the immune system. The authors successfully recruited participants with both mild and severe COVID-19 between November 2020 to May 2021. The analyzed cohort is gender and acceptably age-matched and the results reported are promising. Signatures associated with NK cell cytotoxicity in mild and neutrophil functions in the severe group during acute infection are the chief findings reported in this manuscript.

Comments on revised version:

The authors responded appropriately to the previous review critiques.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

(1) Due to the significant difference between the infection timeline of mild (1 day post symptom onset) and severe (10 days post symptom onset) cohort at enrollment, an informative analysis to consider is to compare timepoint 2 from the mild cohort to timepoint 1 from the severe cohort.

In agreement with what the reviewer noted on his comment, to be more helpful we completed the analysis comparing timepoint 2 from the mild cohort to timepoint 1 from severe cohort, which is now included as Figure 4-figure supplement 5. The new text added is on pages 13-14, lines 346-355 explaining this analysis. We also included a paragraph in the discussion on page 22, lines 595-604. We have resolved to show this comparison to enforce the main observation related to Natural Killer Cytotoxicity pathways enriched in all analyses of this work.

(2) Alternatively, as this information is available, the authors may group the samples based on the individual's infection timeline as opposed to the recruitment timeline.

Patients in both groups were enrolled at the peak of their symptoms. According to this criterion, we grouped the patients to generate more significant results. Since these infections occurred naturally, we have no accurate information regarding the infection timing of patients. However, if the samples were grouped in order of individual infection timeline, the analysis would be statistically weak to make conclusions about the course of COVID-19, as disease progression would not be coordinated. Our grouping approach provided us a good confidence range, despite the tiny population evaluated.

(3) The authors selected three co-regulated network modules based on the size of module membership genes, selecting the three modules containing the largest gene membership. Small co-regulated networks can also offer important biological insights into specific molecular machinery associated with disease outcomes.

Figure 5 was updated including two more networks (besides blue), for brown and turquoise modules (5E and 5F). This new information allowed us to understand deeply the three larger modules with the most significant results, due to the number of genes they included (blue: 704, brown: 508, and turquoise: 712). The new text describing this analysis is included in page 15 lines 388-396. The remaining 7 modules were also analyzed, and the Gene Ontology/Pathways enrichment were included in 2 new supplemental figures (Figure 5 - figure supplement 1 and 2). The new text describing this analysis is included on page 15, lines 397-401.

(4) An alternative selection criterion that can inform biological associations between module genes and disease severity is the strength of the correlation coefficients. It seems from Figure 5B, that yellow, turquoise, and green modules have a moderate positive correlation with severe patients, while brown, blue, and gray modules show a slight positive correlation with mild outpatients. A recommendation for the authors is to consider revising Figure 5C to include the enrichment of these additional modules and include these modules in the interpretation of the results.

The correlations between cohorts and the modules (blue, brown and turquoise) are clearly identified for severe or mild patients. However, for several smaller modules, correlations are heterogenous for different patients of the cohorts, making it hard to gain a clear conclusion related to severity groups. In this sense, the 7 modules were analyzed as is indicated in the previous response number #3, and the results offer an idea of the different transcriptional programs present at different patients in different stages of disease. However, the small number of genes in some modules brings weak results of GO and enriched pathways, making it difficult to interpretation. The text describing this figure is included in page 15 lines 397-401. Also, the network analyses for brown and turquoise modules were included in figure 5 as 5E-F and the text detailing these figures was included on page 15 lines 388-396.

(5) In Figures 3E and 3F, the authors present enrichment analyses of differentially expressed genes from day 28. However, earlier in the results (lines 226-228), the authors reported no differentially expressed genes observed between the mild and severe participant cohort at this time point. Can the authors clarify which comparison was performed to obtain the list of differentially expressed genes used in the enrichment analyses in Figures 3E and 3F?

The discrepancy in this case stems from separate criteria employed for comparison in each case. At the pairwise comparison, DEGs list is different from the longitudinal comparison mentioned afterwards, as for this later analysis we selected only the genes with different trajectories throughout the study (Figure 3). To clarify this point, we included a new paragraph on page 11, lines 278-285.

Original:

“We detected 828 genes that exhibited temporal and quantitative expression level differences during the progression of disease. We discovered additional biological processes and KEGG pathways that were differentially enriched during the COVID-19 progression in mild and severe patients (Figure 3) using the Enrichr platform (G. Chen et al., 2020)”

Changed to:

“To do so, we first identified genes that were differentially expressed between severity groups, and second, we chose only those that also showed changes in their trajectories across sampling times. In doing so, we found 828 genes that exhibited temporal differences in expression level during disease progression. Then using the Enrichr platform (G. Chen et al., 2020), we discovered additional biological processes and KEGG pathways that were differentially enriched during the COVID-19 progression in mild and severe patients (Figure 3).”

(6) Additionally, the authors refer to specific enriched genes in Figure 3 (lines 298-302), but Figure 3 only displays the enriched terms. Can the authors include the results from the enrichment analysis that include gene membership for each enriched term in the supplement?

Certainly, there is no figure or table in the initial version that includes the gene list for this analysis. We have now included a supplement table 1 and 2 that details each pathway, along with its gene list.

(7) In line 104, can the authors clarify the parameters used to define well-matched samples?

Based on the observations made by the reviewers, we decided to change the wording to make it more obvious about the message of this paper. The update was included on page 5, line  as follows:

Original:

“Here, we designed a longitudinal investigation using well-matched samples to study how changes in gene expression in distinct immune effector cells changed during the earliest time points after diagnosis and during progression of clinical disease”,

Changed to:

“Here, we designed a longitudinal comparison between mild and severe patients, choosing the appropriate samples according to the clinical progression and the unbiased gene expression profile”

(8) In lines 113-116, can the authors clarify how their approach mitigates noise/potential biases and very briefly, describe what the nature of noise/biases could be?

The main goal of this paragraph is to show that, while there are several pathways with statistical significance in our analyses, the focus was on NK cell cytotoxicity because this molecular pathway showed bridges between other relevant immune responses; thus, the pathways chosen to respond to its intricated transcriptional program instead of a biased interest. The text was edited and included on page 6, line 111-131 as follows:

Original:

“We used a pairwise comparison of gene expression, gene set enrichment, and weight-correlated gene network analyses to detect differential expression of genes involved with the cytotoxic signaling pathway of Natural Killer (NK) cells in mild verses severe progression of disease. We promoted a broad and integrated point of view throughout the transcriptomic analysis of functional pathways to mitigate noise and potential biases (Bastard et al., 2020; Delorey et al., 2021; Schultze & Aschenbrenner, 2021; S. Zhang et al., 2022). We found close connectivity between NK signaling pathway genes and those of cytokine-cytokine receptor signaling pathways, along with Th1/Th2 cell differentiation genes, as part of the transcriptional circuit executed preferentially among mildly ill patients. Our results detected transcriptional circuits engaging multiple regulatory checkpoints. These findings indicated that the innate NK signaling pathway (cell cytotoxic activity) is beneficial, perhaps a critically-necessary activity needed to effectively eradicate coronavirus. We interpreted that an adaptive immune response that included early cell-mediated immunity was important for reducing disease severity in mild patients. This balance between humoral- and cell-mediated immunity appeared to be less robust in patients presenting with severe COVID-19. These results detected components of the immune response that were significantly associated with the differences in symptom severity observed between mild and severely ill COVID-19 patients.”

Changed to:

“Briefly, to gain more insights into our findings and complement their functional context, we used a pairwise comparison of gene expression, gene set enrichment, and weight-correlated gene network analyses. By doing so, we identified pathways of genes involved with the NK cell cytotoxicity enriched in mild patients when compared to severe. Besides focusing on a particular molecular pathway, we investigated the interactions to better comprehend the underlying phenomena of a successful immune response, contributing to an integrated point of view throughout the transcriptomic analyses of functional pathways to mitigate potential biases attributed to focusing the study on a single pathway. In this regard, we revealed that the NK signaling pathway was intricately related to other transcriptional circuits, such as those governing Th1/Th2 cell differentiation and cytokine-cytokine receptor signaling pathways. These interactions highlight the importance of these pathways as bridges between the innate and adaptive immune responses throughout the disease, implying that the innate NK signaling pathway (cell cytotoxic activity) is beneficial, and possibly a critical activity required to effectively eradicate coronavirus. We also concluded that an adaptive immune response including early cell-mediated immunity was significant in lowering disease severity. The link between the primary innate NK cell activity and the transcriptional priming of adaptive Th1 and Th2 cell responses appears to be more robust in mild patients than in severe.”

(9) In line 120, can the authors clarify which regulatory checkpoints were being referred to?

The concept of “checkpoint” was changed to “bridges” (line 124), because offers a clearer idea about the molecular interaction displayed across the different enriched pathways described in our study. In this sense, the bridges show the connection between innate immune response by NK cell and the adaptive immune response by Th1/Th2 cells

(10) In lines 125-126, can the authors refer to specific results to support this observation?

Lines 111 to 129 summarize the results of the analysis that support the aforementioned phrase. However, the original sentence referred was modified for better comprehension on page 6, lines 129-131 as follows:

Original:

“This balance between humoral- and cell-mediated immunity appeared to be less robust in patients presenting with severe COVID-19”

Changed to:

“The link between the primary innate NK cell activity and the transcriptional priming of adaptive Th1 and Th2 cell responses appears to be more robust in mild patients than in severe.”

(11) In lines 184-185, can the authors clarify what the term "mixed" specifically refers to?

The original text was modified for better comprehension on page 8, lines 177-179 as follows:

Original:

“Interestingly, on day-28, when the majority of patients had recovered, samples from severely ill patients were still mixed compared to those with mild symptoms.”

Changed to:

“Interestingly, on day-28, when the majority of patients had recovered, samples from severely ill patients were pooled together with those mild patients who had already recovered”.

(12) In line 286, can the authors clarify how quantitative expression level differences are distinct from temporal expression level differences?

Despite the differences in the enrollment time between mild and severe cohorts, it was made precisely during COVID-19 symptoms peaks, as illustrated in figure 1B. Also supporting this criterion, the longitudinal analysis outlined in figure 3 was performed taking into account the changes in gene expression trajectories along all sampling times. This point has significance because the results obtained from it exposed several transcriptional programs that were dynamically executed along disease progression, even independently of the pairwise comparison approaches carried out previously.

(13) In Figure 1C, there seemed to be two data points associated with "M1 0 days" and "M4 28 days" with distinct PC projections. Could these samples be mislabeled?

The figure was revised and completed. The hexagon symbol for day-28 was changed for a star symbol. The “M1 0 days” and “M4 28 days” samples were labeled correctly.  See below figure 1C with changes as follows:  

(14) In Figure 1D caption: could authors clarify if the ranking of 100 genes was based on the log2FC or adjusted p-values?

The criteria considered was Fold Change ≥ 2 and the FDR ≤ 0.05 which is included in the methodology on page 23, lines 657-660

(15) In Figure 4D, can the authors include the expression z score for the healthy participants?

We could include this information, but we consider that it would not help for the understanding of this figure because in this way we put the focus on the differential trajectories between mild and severe patients. Also, DEGs from mild and severe cohorts from this analysis or any other in this work were obtained relatively to healthy donors.

(16) Related to this, can the authors clarify if the expression z scores were computed using the mean and standard deviations of all samples within the study or relative to a specific participant cohort?

The z-score was used considering the mild and severe patients to calculate mean and then the standard deviation of each group. A new paragraph was included in material and methods on page 24, lines 662-664.

(17) In Figure 5B, can the authors include column annotations for participants and sampling time points?

The figure 5B was updated and completed with the suggested information.

(18) In Figure 1 - Figure Supplement 2, can the authors include the volcano plot from the pairwise comparison for day 28 showing no differentially expressed genes between mild and severe participants as reported in the results (lines 226-228)?

The third volcano plot for day 28 was included in the updated figure 1 supplement 2.

Reviewer #2 (Recommendations For The Authors):

The manuscript is generally very well-constructed and well-written. However, the following are the major concerns mostly regarding the study design and participant selection.

(1) The authors have used enrolment day as D0 which is not reflective of the immune response timeline. Especially when the designated 'D0' for the severe group is 10.0 + 1.8 days post symptom (DPS) onset while the 'D0' for the mild group is 1.2 + 1.3 DPS. In the context of an acute infection discussed herewith, this difference is critical.

As tempting as it is to conduct longitudinal studies on COVID-19, the authors might do better focusing on specific acute time points (within 10 days post-symptom onset) and convalescent time points (beyond 28 days post-symptom). A better comparison would be D0 severe with D7 mild (aligning the DPS to be between 7-10 days in both groups).

Despite the differences in the enrolment time between mild and severe cohorts, it was made precisely during COVID-19 symptoms peaks, as illustrated in figure 1B. Also supporting this criterion, the longitudinal analysis outlined in figure 3 was performed taking into account the changes in gene expression trajectories along all sampling times. This point has significance because the results obtained from it exposed several transcriptional programs that were dynamically executed along disease progression, even independently of the pairwise comparison approaches carried out previously. Likewise, we agree with the observation of the reviewer, because as we mentioned in the article, it is difficult to properly compare disease progression between naturally infected patients. So, to better support our findings, we complemented them throughout a pairwise comparison between day-7 samples from mild and day-0 samples from severely ill individuals, finding GO terms and enriched pathways related to NK cell function across the mild cohort, as seen in Figure 4-figure supplement 5. This result enforced the main findings gained from the different analyses carried out in this work, highlighting the relevance of the innate immune response of Natural Killer cells, which correlated with a mild progression of disease. The new paragraph describing this analysis was included in pages 13-14, lines 346-355. We also included a paragraph in the discussion on page 22, lines 595-604.

(2) Though there are four participants within each group, one of the participants with severe infection (S1) only has the D0 time point which probably undermines the statistical significance of the results.

This is an accurate observation, as the statistical weight will allow the deeper alterations to be evaluated while the more subtle ones will most likely be excluded from this study. In our analyses, we focused on variations with high statistical significance, which led to the discovery of a distinct Natural Killer response between mild and severe cohorts.

(3) The authors should also account for any medications administered to the severe group in the ICU before enrolment in the study -immune-dampening drugs or steroids which may alter neutrophil recruitment or other immune functions.

Only one severe patient received medication both prior to and during the COVID-19 disease. Even though several medications were administered to this patient, their effects have not been found to increase the neutrophil response.

(4) What was the viral load status at the different time points analyzed - how does this relate to the immune and clinical findings?

In this recruitment the viral load status was not measured.

(5) Was any complete blood count or basic immune phenotyping conducted on these samples? Important to know the various cell frequencies in the PBMC mix sent for sequencing to account for contamination of lymphocytes with RBCs/monocytes/neutrophils as well as any lymphopenia.

This measurement was not done for these samples. However, our protocol of PBMC purification has been tested before and showed small quantities of red blood cell contamination in the process. Furthermore, in all analysis of Gene Ontology or Enriched Pathways, there is not any related to red blood cell genes that could generate noise in the interpretation of our results.

(6) The neutrophil/lymphocyte ratio is already skewed during SARS-CoV-2 infection - which could be the reason for higher readings in severe participants? - speculate?

Effectively, the ratio in several cell types is changed during SARS-CoV-2 infection. However, despite this noise in the proportion of immune cells, different functions in our study are more represented in cells with less count as Natural Killer cells. The modules of co-expression analysis support the notion that despite the number of cells being in different proportions, a transcriptional program is being executed differentially in the cohorts.

(7) CD247/ZAP70 also influences the CD16-mediated NK cell ADCC activity which the authors can add to the innate-adaptive bridging section.

NK CD16a is more highly expressed in NK cells. The circuit involving CD247/ZAP70 and CD16 could explain the cytotoxicity of these cells and how they contribute to the establishment of a response to fight the viral infection of SARS-CoV-2. In our study, CD16a (FcgammaRIIIa) expression was similar in both mild and severe cohorts. Because our methodology only counts transcriptional changes, genes that did not change were excluded from our discussion. However, our group's research focuses on this node or bridge between innate and adaptive immune responses, with a particular emphasis on fc-antibodies functions, being a topic of interest for future research.

(8) Some of the figures lacked clarity making it difficult to review. (Eg. Fig 4 A, Fig 4 - supplement 1 A&B, Fig 5).

Figure 4A was redesigned, Figure 4-figure supplement 1 was presented in a full page for better resolution.

Specific Comments:

(1) Consider changing "covid-19" in the title of the manuscript to "COVID-19"

Probably the journal platform changes the letters. The original title is in capital letters according to the observation. In the clinical table “COVID-19” was changed to capital letters.

(2) Page 2: Line 24 - Consider revising this line. Not sure what the authors mean by 'early compromise'

The paragraph was revised and rewritten.

Original:

“Mild COVID-19 patients presented an early compromise with NK cell function, whereas severe patients do so with neutrophil function”

Changed to:

”Mild COVID-19 patients displayed an early transcriptional commitment with NK cell function, whereas severe patients do so with neutrophil function”

(3) Page 4: Lines 57 & 58 - Verify the reference. The paper referenced was published in 2016 and is in regard to SARS-CoV, MERS-CoV, and enterovirus D68.

Effectively, this reference was appropriate for drawing parallels with other respiratory viruses. Due to the emphasis on SARS-CoV-2, the paragraph has been strengthened with two additional references: Shen 2023, and Wauters 2022.

(4) Page 10: Lines 229 - 234 - Consider referring to the appropriate figure (i.e., Figure Supplement 2 A or B). The figure associated with D28 DEGs (Volcano plot) is missing in the supplementary. Erroneously referred here as Figure 1C which is a PCA plot?

The original text was changed because the figure referenced was correct but misunderstood. The final sentence is on page 9, lines 220-223.

(5) Page 10: Line 224 - Change the sentence to " We found upregulated.." instead of " We found regulated..".

The text was edited in accordance with this recommendation, which is currently found in line 232.

(6) Page 13: Line 326 - Figure 4A referenced here is not clear - unable to review.

Figure 4A was updated for a better resolution and included in the manuscript.

(7) Page 15: Line 398 - Consider rewording "after diagnosis" since the days here are "after enrolment".

This recommendation was considered and the text was rewritten on page 15, lines 404-406:

Original:

“We systematically analyzed transcriptomic features of PBMCs from COVID-19 patients with mild and severe symptoms at three sequential time-points (D0, D7, and D28) after diagnosis”

Changed to:

“We systematically analyzed transcriptomic features of PBMCs from COVID-19 patients with mild and severe symptoms at three sequential time-points (D0, D7, and D28) during the peak of the symptoms”

(8) Page 17: Move text from the next page to eliminate blank space.

Resolved

(9) Page 32: Figure 1C - Consider changing the symbol for D28 since it looks very similar to the D0 symbol. Use the colors consistently instead of different shades for each group.

The hexagon symbol was changed by a star symbol for D28 in figure 1C.  In this figure each color indicates the three different groups, and the transparent color was used to differentiate the symbols when are close together.

(10) Page 36: Figure 4A - Unable to review.

This figure was resized for better resolution.

(11) Page 42-49: Consider relabeling and renumbering the Supplementary figures for consistency and reference the modified numbers in the appropriate location in the main text.

The supplementary figures were relabeling for consistency and better understanding.

(12) Pages 44 & 48: Unable to review the figures.

The figures indicated were resized for better resolution.

Examples of consistency review:

(1) Use of D0,D7 / D-0, D-7 throughout the manuscript

The selected format for the final version of the manuscript is D0, D7, and D28.

(2) Reporting the source of reagents consistently (Name, Place, Country, Catalog number)

The source reagents were reformatted for consistency in lines 626-628-632-642.

eLife assessment

The authors performed extensive coarse-grained molecular dynamics simulations of 140 different prion-like domain variants to interrogate how specific amino acid substitutions determine the driving forces for phase separation. The analyses are solid, and the predictive scaling laws can aid in identifying potential phase-separating regions in uncharacterized proteins. Overall, this is a valuable contribution to the field of biomolecular condensates. It exemplifies how data-driven methodologies can uncover new insights into complex biological phenomena.

Reviewer #1 (Public Review):

Summary:

In this preprint, the authors systematically and rigorously investigate how specific classes of residue mutations alter the critical temperature as a proxy for the driving forces for phase separation. The work is well executed, the manuscript well-written, and the results reasonable and insightful.

Strengths:

The introductory material does an excellent job of being precise in language and ideas while summarizing the state of the art. The simulation design, execution, and analysis are exceptional and set the standard for these types of large-scale simulation studies. The results, interpretations, and Discussion are largely nuanced, clear, and well-motivated.

Weaknesses:

This is not exactly a weakness, but I think it would future-proof the authors' conclusions to clarify a few key caveats associated with this work. Most notably, given the underlying implementation of the Mpipi model, temperature dependencies for intermolecular interactions driven by solvent effects (e.g., hydrophobic effect and charge-mediated interactions facilitated by desolvation penalties) are not captured. This itself is not a "weakness" per se, but it means I would imagine CERTAIN types of features would not be well-captured; notably, my expectation is that at higher temperatures, proline-rich sequences drive intermolecular interactions, but at lower temperatures, they do not. This is likely also true for the aliphatic residues, although these are found less frequently in IDRs. As such, it may be worth the authors explicitly discussing.

Similarly, prior work has established the importance of an alpha-helical region in TDP-43, as well as the role of aliphatic residues in driving TDP-43's assembly (see Schmidt et al 2019). I recognize the authors have focussed here on a specific set of mutations, so it may be worth (in the Discussion) mentioning [1] what impact, if any, they expect transient or persistent secondary structure to have on their conclusions and [2] how they expect aliphatic residues to contribute. These can and probably should be speculative as opposed to definitive.

Again - these are not raised as weaknesses in terms of this work, but the fact they are not discussed is a minor weakness, and the preprint's use and impact would be improved on such a discussion.

Reviewer #2 (Public Review):

This is an interesting manuscript where a CA-only CG model (Mpipi) was used to examine the critical temperature (Tc) of phase separation of a set of 140 variants of prion-like low complexity domains (PLDs). The key result is that Tc of these PLDs seems to have a linear dependence on substitutions of various sticker and space residues. This is potentially useful for estimating the Tc shift when making novel mutations of a PLD. However, I have strong reservations about the significance of this observation as well as some aspects of the technical detail and writing of the manuscript.

(1) Writing of the manuscript: The manuscript can be significantly shortened with more concise discussions. The current text reads as very wordy in places. It even appears that the authors may be trying a bit too hard to make a big deal out of the observed linear dependence.

The manuscript needs to be toned done to minimize self-promotion throughout the text. Some of the glaring examples include the wording "unprecedented", "our research marks a significant milestone in the field of computational studies of protein phase behavior ..", "Our work explores a new framework to describe, quantitatively, the phase behavior ...", and others.

There is really little need to emphasize the need to manage a large number of simulations for all 140 variants. Yes, some thoughts need to go into designing and managing the jobs and organizing the data, but it is pretty standard in computational studies. For example, large-scale protein ligand-free energy calculations can require one to a few orders of magnitude larger number of runs, and it is pretty routine.

When discussing the agreement with experimental results on Tm, it should be noted that the values of R > 0.93 and RMSD < 14 K are based on only 16 data points. I am not sure that one should refer to this as "extended validation". It is more like a limited validation given the small data size.

Results of linear fitting shown in Eq 4-12 should be summarized in a single table instead of scattering across multiple pages.

The title may also be toned down a bit given the limited significance of the observed linear dependence.

(2) Significance and reliability of Tc: Given the simplicity of Mpipi (a CA-only model that can only describe polymer chain dimension) and the low complexity nature of PLDs, the sequence composition itself is expected to be the key determinant of Tc. This is also reflected in various mean-field theories. It is well known that other factors will contribute, such as patterning (examined in this work as well), residual structures, and conformational preferences in dilute and dense phases. The observed roughly linear dependence is a nice confirmation but really unsurprising by itself. It appears how many of the constructs deviate from the expected linear dependence (e.g., Figure 4A) may be more interesting to explore.

The assumption that all systems investigated here belong to the same universality class as a 3D Ising model and the use of Eqn 20 and 21 to derive Tc is poorly justified. Several papers have discussed this issue, e.g., see Pappu Chem Rev 2023 and others. Muthukumar and coworkers further showed that the scaling of the relevant order parameters, including the conserved order parameter, does not follow the 3D Ising model. More appropriate theoretical models including various mean field theories can be used to derive binodal from their data, such as using Rohit Pappu's FIREBALL toolset. Imposing the physics of the 3D Ising model as done in the current work creates challenges for equivalence relationships that are likely unjustified.

While it has been a common practice to extract Tc when fitting the coexistence densities, it is not a parameter that is directly relevant physiologically. Instead, Csat would be much more relevant to think about if phase separation could occur in cells.

Reviewer #3 (Public Review):

Summary:

"Decoding Phase Separation of Prion-Like Domains through Data-Driven Scaling Laws" by Maristany et al. offers a significant contribution to the understanding of phase separation in prion-like domains (PLDs). The study investigates the phase separation behavior of PLDs, which are intrinsically disordered regions within proteins that have a propensity to undergo liquid-liquid phase separation (LLPS). This phenomenon is crucial in forming biomolecular condensates, which play essential roles in cellular organization and function. The authors employ a data-driven approach to establish predictive scaling laws that describe the phase behavior of these domains.

Strengths:

The study benefits from a robust dataset encompassing a wide range of PLDs, which enhances the generalizability of the findings. The authors' meticulous curation and analysis of this data add to the study's robustness. The scaling laws derived from the data provide predictive insights into the phase behavior of PLDs, which can be useful in the future for the design of synthetic biomolecular condensates.

Weaknesses:

While the data-driven approach is powerful, the study could benefit from more experimental validation. Experimental studies confirming the predictions of the scaling laws would strengthen the conclusions. For example, in Figure 1, the Tc of TDP-43 is below 300 K even though it can undergo LLPS under standard conditions. Figure 2 clearly highlights the quantitative accuracy of the model for hnRNPA1 PLD mutants, but its applicability to other systems such as TDP-43, FUS, TIA1, EWSR1, etc., may be questionable.

The authors may wish to consider checking if the scaling behavior is only observed for Tc or if other experimentally relevant quantities such as Csat also show similar behavior. Additionally, providing more intuitive explanations could make the findings more broadly accessible.

The study focuses on a particular subset of intrinsically disordered regions. While this is necessary for depth, it may limit the applicability of the findings to other types of phase-separating biomolecules. The authors may wish to discuss why this is not a concern. Some statements in the paper may require careful evaluation for general applicability, and I encourage the authors to exercise caution while making general conclusions. For example, "Therefore, our results reveal that it is almost twice more destabilizing to mutate Arg to Lys than to replace Arg with any uncharged, non-aromatic amino acid..." This may not be true if the protein has a lot of negative charges.

I am surprised that a quarter of a million CPU hours are described as staggering in terms of computational requirements.

eLife assessment

This valuable study tests the functional role of food-washing behavior in removing tooth-damaging sand and grit in long-tailed macaques and whether dominance rank predicts the level of investment in the behavior. The evidence that food-washing is deliberate is compelling, but the evidence for variable and adaptive investment depending on rank is incomplete given confounding between sex and rank and limited sample size. A more careful and perhaps restrained interpretation of the findings, as well as a connection to the existing literature on optimal foraging theory, would increase the value of the study to its intended audience, i.e. researchers interested in foraging behavior, cognition, and primate evolution.

Reviewer #1 (Public Review):

Summary:

In this paper, the authors had 2 aims:

(1) Measure macaques' aversion to sand and see if its' removal is intentional, as it is likely in an unpleasurable sensation that causes tooth damage.

(2) Show that or see if monkeys engage in suboptimal behavior by cleaning foods beyond the point of diminishing returns, and see if this was related to individual traits such as sex and rank, and behavioral technique.

They attempted to achieve these aims through a combination of geochemical analysis of sand, field experiments, and comparing predictions to an analytical model.

The authors' conclusions were that they verified a long-standing assumption that monkeys have an aversion to sand as it contains many potentially damaging fine-grained silicates and that removing it via brushing or washing is intentional.

They also concluded that monkeys will clean food for longer than is necessary, i.e. beyond the point of diminishing returns, and that this is rank-dependent.

High and low-ranking monkeys tended not to wash their food, but instead over-brushed it, potentially to minimize handling time and maximize caloric intake, despite the long-term cumulative costs of sand.

This was interpreted through the *disposable soma hypothesis*, where dominants maximize immediate needs to maintain rank and increase reproductive success at the potential expense of long-term health and survival.

Strengths:

The field experiment seemed well-designed, and their quantification of physical and mineral properties of quartz particles (relative to human detection thresholds) seemed good relative to their feret diameter and particle circularity (to a reviewer who is not an expert in sand). The *Rank Determination* and *Measuring Sand* sections were clear.

In achieving Aim 1, the authors validated a commonly interpreted, but unmeasured function, of macaque and primate behavior-- a key study/finding in primate food processing and cultural transmission research.

I commend their approach in developing a quantitative model to generate predictions to compare to empirical data for their second aim.

This is something others should strive for.

I really appreciated the historical context of this paper in the introduction, and found it very enjoyable and easy to read.

I do think that interpreting these results in the context of the *disposable soma hypothesis* and the potential implications in the *paleolithic matters* section about interpreting dental wear in the fossil record are worthwhile.

Weaknesses:

Most of the weaknesses in this paper lie in statistical methods, visualization, and a missing connection to the marginal value theorem and optimal foraging theory.

I think all of these weaknesses are solvable.

The data and code were not submitted. Therefore I was unable to better understand the simulation or to provide useful feedback on the stats, the connection between the two, and its relevance to the broader community.

(1) Statistics:

(a) AIC and outcome distributions

The use of AIC for hierarchical models, and models with different outcome distributions brought up several concerns.

The authors appear to use AIC to help inform which model to use for their primary analyses in Tables S1 and S2. It is unclear which of these models are analyzed in Tables S3 and S4.

AIC should not be used on hierarchical models, and something like WAIC (or DIC which has other caveats) would be more appropriate.

Also, using information criteria on Mixture Models like Negative Binomials (aka Gamma-Poisson) should be done with extreme caution, or not at all, as the values are highly sensitive to the data structure.

Some researchers also say that information criteria should not be used to compare models with different outcome distributions - although this might be slightly less of a concern as all of your models are essentially variations on a Poisson GLM.

Discussion on this can be found in McElreath Statistical Rethinking (Section 12.1.3) and Gelman et al. BDA3 (Chapter 7).

Choosing an outcome distribution, based on your understanding of the data generating process is a better approach than relying on AIC, especially in this context where it can be misleading.

(b) Zeros

I also had some concerns about how zeros were treated in the models.

In lines 217-218, they mentioned that "if a monkey consumed a cucumber slice without brushing or washing it, the zero-second duration was included in both GLMMs."

This zero implies no processing and should not be treated as a length 0 duration of processing.

This suggests to me that a zero-inflated poisson or zero-inflated negative binomial, would be the best choice for modelling the data as it is essentially a 2-step process:<br /> (i) Do they process the cucumber at all?<br /> (ii) If so do they wash or brush, and how is this predicted by rank and treatment?

(2) Absence of Links to Foraging Theory

Optimal cleaning time model: the optimality model was not well described including how it was programmed. Better description and documentation of this model, along with code (Mathematica judging from the plot?) is needed.

There seems to be much conceptual and theoretical overlap with foraging theory models that were not well described - namely the *marginal value theorem (Charnov (1976), Krebs et al. (1974),) and its subsequent advances* (see https://doi.org/10.1016/j.jaa.2016.03.002 and https://doi.org/10.1086/283929 for examples).

In the suggestions, I attached the R code where I replicated their model to show that it is *mathematically identical to the marginal value theorem*. This was not mentioned at all in the text or citations.

This is a well-studied literature since the 1970's and there is a history of studies that compare behavior to an optimality model and fail (or do find) instances where animals conform or diverge with its predictions (https://doi.org/10.1146/annurev.es.15.110184.002515). This link should be highlighted, and interpreting it in that theoretical context will make it more broadly applicable to behavioral ecologists.

The data was subsetted to include instances where there were < 3 monkeys present to avoid confounds of rank, but it is important to know that optimal behavior might vary by individual, and can change in a social context depending on rank (see https://doi.org/10.1016/j.tree.2022.06.010). Discussion of this, and further exploration of it in the data would strengthen the overall contribution of this manuscript to the field, but I understand that the researchers wish to avoid that in this paper for it is a complex topic, which this dataset is uniquely suited to address.

(3) Interpretation and validity of model relative to data

In lines 92-102, they present summary statistics (I think) showing that time spent brushing and washing is consistent with washing or brushing to remove sand.

In the **mitigating tooth wear** section (line 73) and corresponding Figure S1 showing surface sand removed, more detail about how these numbers were acquired, and statistical modelling, is needed.

This is important as uncertainty and measurement error around these metrics are key to the central finding and interpretation of Aim 2 in this paper.

It appears that the researchers simulated the monkey's brushing and washing behaviors (similar to https://doi.org/10.1007/s10071-009-0230-3).

How many researchers simulated monkey behavior and how many times?

What are the repeat points in Figure S1?

What is the number of trials or number of people?

This effect appears stronger for washing than brushing as well - if so, why?

More info about this data, and the uncertainty in this is important, as it is key to the second central claim of this paper.

The estimates of removing between 76% +/- 7 and 93% +/- 4 of sand (visualized in Figure S1), are statistical estimates.

I would find the argument more convincing if after propagating for the uncertainty in handling in sand removal rates, and the corresponding half-saturation constants, if this processing for food is too long, after accounting for diminishing returns held true.<br /> It is very possible that after accounting for uncertainty and variation in handling time and removal rates, the second result may not hold true.

I was not able to convince myself of this via reanalysis as the description of the data in the text was not enough to simulate it myself.

Essentially, this would imply that in Figure 3 the predicted value would have some variation around it (informed by boundary conditions of time being positive, and percents having floors and ceilings) and that a range of predicting cleaning times (optimal give-up times) would be plotted in Figure 3.

This could be accomplished in a Bayesian approach, Or by simply plotting multiple predictions given some confidence interval around, c and h.

Reviewer #2 (Public Review):

Summary:

This field experiment aimed to assess what motivates macaque monkeys to clean food items prior to consumption and the relative costs and benefits of different cleaning approaches (manually brushing sand from food versus dousing food items in water). The experiment teases apart if/how the benefits of these approaches are mediated by the amount of debris on food and the monkeys' rank in terms of the costs of consuming sand versus the time and energy required to remove it. The authors not only examined the behavioral responses of wild macaques to three conditions of food sand contamination but also tested the relative costs of consuming different levels and sizes of sand particulates. Through this, the authors propose considerations of the macaques' motivations to clean food and the balance they take in energetic gains from consuming food versus the costs of cleaning food and consuming sand. Their data reveal that food washing is more effective in removing sand, but more costly than manually brushing off sand. This study also revealed that only mid-ranked monkeys washed their food, while high and low-ranked monkeys were more likely to remove sand via brushing it off food with their hands.

Strengths:

This study provides a very in-depth consideration of the motivations of macaques to clean their food, and the relative costs and benefits of different food cleaning techniques. Not only did the study test the behavior of wild macaques via a simple yet elegant field study, but they also performed a detailed analysis of the sand particulates to understand the level of potential tooth wear that consuming it could result in. By relying on a wild group of macaques that have been part of a long-term study site, the team also had detailed behavioral data on the population to allow for rank assessments of the animals. This comprehensive study provides important foundational information for a better understanding of how and why macaques clean food, that inform existing and future considerations of this as a potential cultural behavior.

Weaknesses:

As currently written, the paper does not provide sufficient background on this population of animals and their prior demonstrations of food-cleaning behavior or other object-handling behaviors (e.g., stone handling). Moreover, the authors' conclusions focus on the behavior of high-ranked animals, but subordinate animals also showed similar behavioral patterns and they should be considered in more detail too.

Reviewer #3 (Public Review):

This paper provides evidence that food washing and brushing in wild long-tailed macaques are deliberate behaviors to remove sand that can damage tooth enamel. The demonstration of the immediate functional importance of these behaviors is nicely done. However, the paper also makes the claim that macaques systematically differ in their investment in food cleaning because of rank-dependent differences in their costs and benefits. This latter conclusion is not, in my view, well-supported, for several reasons.

First, as is typical in many primate studies, the authors construct sex-specific ordinal rank hierarchies. This makes sense since hierarchies for males and hierarchies for females are determined by different processes and have different consequences. However, if I understand it correctly, they are then lumped together in all statistical analyses of rank, which makes the apparent rank effect very difficult to understand. The challenge of interpretation is increased because there are twice as many adult females in the group as adult males, so the rank is confounded by sex (because all low-rank values are adult females).

Second, because only one social group is being studied, the conclusions about rank may be heavily driven by individual identity, not rank per se. An analysis involving replicate social groups (which granted, may be impossible here) or longitudinal data showing a change in behavior following a change in rank would be much more compelling.

Third, there is no evidence presented on the actual fitness-related costs of tooth wear or the benefits of slightly faster food consumption. Support for these arguments is provided based on other papers, some of which come from highly resource-limited populations (and different species). But this is a population that is supplemented by tourists with melons, cucumbers, and pineapples! In the absence of more direct data on fitness costs and benefits, the paper makes overly strong claims about the ability to explain its observations based on "immediate energetic requirements" (abstract), "difference...freighted with fitness consequences" (line 80), and "pressing energetic needs"/"live fast, die young" (lines 121-122--there is no evidence that tooth wear is associated with morbidity or mortality here). The idea that high-ranking animals are "sacrificing their teeth at the altar of high rank" seems extreme.

eLife assessment

The present paper describes an important methodological development that combines light (confocal) microscopy with scanning and transmission EM and EM tomography. The method expands the level of structural detail accessible to large-volume EM studies and thus represents an approach to integrate analyses of cellular and sub-cellular structures in biological samples. The study, which provides a compelling proof-of-principle, will be of particular value to cell biologists interested in the in-depth interpretation of high-resolution ultrastructural information from sparsely distributed targets - at multiple scales and in diverse biological structures.

Reviewer #1 (Public Review):

The present paper presents a new, simple, and cost-effective technique for multimodal EM imaging that combines the strengths of volume scanning electron microscopy (SEM) and electron microscopic tomography. The novel ATUM-Tomo approach enables the consecutive inspection of selected areas of interest by correlated serial SEM and TEM, optionally in combination with CLEM, as demonstrated. The most important finding of ATUM-Tomo and particularly correlative ATUM-Tomo is that it can bridge several scales from the cellular to the high-resolution subcellular scale, from the micrometer to low nanometer resolution, which is particularly important for the ultrastructural analysis of biological regions of interest as demonstrated here by focal pathologies or rare cellular and subcellular structures. Both imaging modalities are non-destructive, thus allowing re-imaging and hierarchical imaging at the SEM and TEM levels, which is particularly important for precious samples, such as human biopsies or specimens from complex CLEM experiments. The paper demonstrates that the new approach is very helpful in analyses of pathologically altered brains, including humans brain tissue samples, that require high-resolution SEM and TEM in combination with immunohistochemistry for analysis. Even the combination with tracers would be possible. In sum, ATUM-Tomo opens up new possibilities in multimodal volume EM imaging for diverse biological areas of research.

Strengths

This paper is a very nice piece of work. It combines modern, high-end, state-of-the-art technology that allows to investigate diverse biological questions in different fields and at multiple scales. The paper is clear and well-written. It is accompanied by excellent figures, supplementals, and colored 3D-reconstructions that make it easy for the reader to follow the experimental procedure and the scientific context alike.

Weaknesses

There is a bit of an imbalance between the description of the state-of-the-art methodology and the scientific context. The discussion of the latter could be expanded.

Reviewer #2 (Public Review):

Kislinger et al. present a method permitting a targeted, multi-scale ultrastructural imaging approach to bridge the resolution gap between large-scale scanning electron microscopy (SEM) and transmission electron microscopy (TEM). The key methodological development consists of an approach to recover sections of resin-embedded material produced by Automated Tape Collecting Ultramicrotomy (ATUM), thereby permitting regions of interest identified by serial section SEM (ATUM-SEM) screening to be subsequently re-examined at higher resolution by TEM tomography (ATUM-Tomo). The study shows that both formvar and permanent marker coatings are in principle compatible with solvent-based release of pre-screened sections from ATUM tape (carbon nanotubule or Kapton tape). However, a comparative analysis of potential limitations and artifacts introduced by these respective coatings revealed permanent marker to provide a superior coating; permanent marker coatings are more easily and reliably applied to tape with only minor contaminants affecting the recovered section-tape interface with negligible influence on tomogram interpretation. Convincing proof-of-principle is provided by integrating this novel ATUMTomo technique into a technically impressive correlated light and electron microscopy (CLEM) approach specifically tailored to investigate ultrastructural manifestations of trauma-induced changes in blood-brain barrier permeability.

Strengths

Schematics and figures are very well-constructed, illustrating the workflow in a logical and easily interpretable manner. Light and electron microscope image data are of excellent quality, and the efficacy of the ATUM-Tomo approach is evidenced by a qualitative assessment of ATUM-SEM performance using coated tape variants and a convincing correlation between scanning and transmission electron microscopy imaging modalities. Potential ultrastructural artifacts induced via solvent exposure and any subsequent mechanical stress incurred during section detachment were thoroughly and systematically investigated using appropriate methods and reported with commendable transparency. In summary, the presented data convincingly support the claims of the study. A major strength of this work includes its general applicability to a broad range of biological questions and ultrastructural targets demanding resolutions exceeding that obtained via serial section and destructive block-face imaging approaches alone. The level of methodological detail provided is sufficient for replication of the ATUM-Tomo technique in other laboratories. Consequently, this relatively simple and cost-effective technique is widely adoptable by electron microscopy laboratories, and its integration into existing ATUM-SEM workflows supports a versatile and non-destructive imaging regime enabling high-resolution details of targeted structures to be interpreted within anatomical and subcellular contexts.

Weaknesses

I find no significant weaknesses in the current version of the manuscript.

Author response:

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

Reviewer #1: The authors may consider moving the supplemental figures into the main body of the paper since they finally would end up with a total of eight figures.

As we added two more supplementary figures, we left them separated from the main part of the manuscript in the supplement. All of them describe important experimental details but we believe that it is easier to follow if there is a focus on the key results.

Reviewer #1: In general, the methods and techniques used here are beside some required but important additions described in sufficient detail.

Reviewer #2: Given the identified importance of glow-discharge treatment of precoated tape to the flat deposition of sections during ATUM, a corresponding schematic or appropriate reference(s) providing more information about the custom-built tape plasma device would likely be a prerequisite for effective reproduction of this technique in other laboratories.

Thank you for the valuable comments on the missing experimental details, which could affect the ease of establishing ATUM-Tomo in other labs. We will clearly highlight the ATUM-Tomo-specific vs. some general EM processing steps of the workflow in the proposed way. A detailed description of the custom-built tape plasma device will be added to the methods section. In addition, we will reference more explicitly our published protocols, which describe the standard electron microscopy embedding steps in great detail (Kislinger et al., STAR protocols, 2020; Kislinger et al., Meth Cell Biol, 2023).

Reviewer #1: Concerning the results section: In my opinion, the results section is a bit unbalanced. There is a mismatch between the detailed description of the methodology (experimental approach) and the scientific findings of the paper. The reviewer can see the enormous methodological impact of the paper, which on the other hand is the major drawback of the paper. To my opinion, the authors should also give a more detailed description of their scientific results.

Concerning the discussion: It would have been nice to give a perspective to which the described methodology can be used not only to describe diverse biological aspects that can be addressed and answered by this experimental approach. For example, how could this method be used to address various questions about the normal and pathologically altered brain?

In my opinion, the paper has one major drawback which is that it is more methodologically based although the authors included a scientific application of the method. The question here is to balance the methodology vs. the scientific achievement of this paper, a decision hard to take. In other words, one could recommend this paper to more methodologically based journals, for example, Nature Methods.

Balancing the technological and biological parts is indeed a difficult issue. We agree that this manuscript mainly describes a technical advancement and demonstrates its power to answer previously unsolved scientific questions. We exemplify this in our model system, neuropathology of the blood-brain barrier. The biological impact of ATUM-SEM has been described in detail in Khalin et al., Small, 2022, and is referenced accordingly. Here we describe how ATUM-Tomo can be applied to reveal biological insights exceeding the capabilities of ATUM-SEM and other volume electron microscopy techniques. However, the description of the methodological development outweighs by far the one of the biological details. We consider eLife‘s Tools and Resources (which, in our view, is in scope similar to Nat Methods) an ideal format for this technically focused manuscript while targeting eLife’s readership with diverse biological fields of interest for potential applications of the method. We suggested the application in connectomics (for chemical synapses), the study of endocytosis and the detection of virus particles in the discussion. Hopefully, this accommodates the Reviewer’s concern that having only a single application might seem arbitrary or even suggest a very narrow utility of the technique.

“While we demonstrate a neuropathology-related application, further biological targets that require high-resolution isotropic voxels and the spatial orientation within a larger ultrastructural context can potentially be studied by ATUM-Tomo. This includes the detection of gap junctions for connectomics or for the study of long-range projections (Holler et al., 2021) and the subcellular location of virus particles (Wu et al., 2022, Roingeard, 2008, Pelchen-Matthews and Marsh, 2007). Thus, ATUM-Tomo opens up new avenues for multimodal volume EM imaging of diverse biological research areas.”

Reviewer #2: Is the separation of sections from permanent marker-treated tape sensitive to the time interval between deposition/SEM imaging and acetone treatment?

Thank you for pointing out this important methodological aspect. We have not systematically investigated whether there is a critical time window between microtomy, SEM, and detachment. From the samples generated for this study, we assessed the importance of timing in retrospect:

“The sections could be recovered even four months after collection and nine months after SEM imaging.”

Reviewer #2: To what extent is slice detachment from permanent marker-treated tape resin-dependent [i.e. has ATUM-Tomo been tested on resin compositions beyond LX112 (LADD)]?

We appreciate this comment addressing the broader technical applicability of ATUM-Tomo. We tested the general workflow with tissue embedded in other commonly used resin types (epon, durcupan).

Reviewer #2: Minor corrections to the text and figures.

Line 83: ((Khalin et al., 2022) should read (Khalin et al., 2022)

Line 86 : 30nm should read 30 nm

Line 139: "...morphological normal tight junctions..." should read "...morphologically normal tight junctions..."

Line 283: "....despite glutaraldehyde fixation, a prerequisite for optimal ultrastructural preservation...".

Line 295: "In contrast, our CLEM approach provides high ultrastructural quality by optimal chemical fixation".

The concepts of optimal preservation and optimal fixation are arguably context- and application-dependent. These statements should be toned down or their context explicitly stated.

Thank you for the detailed corrections. We have applied them accordingly.

eLife assessment

The study presents valuable findings on compensatory mechanisms in response to glycosuria. The evidence supporting the claims is solid, although a causal relationship is somewhat uncertain and the addition of a more clinically relevant model would have strengthened the findings. The work will be of interest to diabetes investigators.

Reviewer #1 (Public Review):

Summary:

In this study, Faniyan and colleagues build on their recent finding that renal Glut2 knockout mice display normal fasting blood glucose levels despite massive glucosuria. Renal Glut2 knockout mice were found to exhibit increased endogenous glucose production along with decreased hepatic metabolites associated with glucose metabolism. Crh mRNA levels were higher in the hypothalamus while circulating ACTH and corticosterone was elevated in this model. While these mice were able to maintain normal fasting glucose levels, ablating afferent renal signals to the brain caused low fasting blood glucose levels. In addition, the higher CRH and higher corticosterone levels of the knockout mice were lost following this denervation. Finally, acute phase proteins were altered, plasma Gpx3 was lower, and major urinary protein MUP18 and its gene expression were higher in renal Glut2 knockout mice. Overall, the main conclusion that afferent signaling from the kidney is required for renal glut2 dependent increases in endogenous glucose production is well supported by these findings.

Strengths:

An important strength of the paper is the novelty of the identification of kidney to brain communication as being important for glucose homeostasis. Previous studies had focused on other functions of the kidney modulated by or modulating brain function. This work is likely to promote interest in CNS pathways that respond to afferent renal signals and the response of the HPA axis to glucosuria. Additional strengths of this paper stem from the use of incisive techniques. Specifically, the authors use isotope enabled measurement of endogenous glucose production by GC-MS/MS, capsaicin ablation of afferent renal nerves, and multifiber recording from the renal nerve. The authors also paid excellent attention to rigor in the design and performance of these studies. For example, they used appropriate surgical controls, confirmed denervation through renal pelvic CGRP measurement, and avoided the confounding effects of nerve regrowth over time. These factors strengthen confidence in their results. Finally, humans with glucose transporter mutations and those being treated with SGLT2 inhibitors show a compensatory increase in endogenous glucose production. Therefore, this study strengthens the case for using renal Glut2 knockout mice as a model for understanding the physiology of these patients.

Comments on latest version:

My concerns have been addressed.

Author response:

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

Reviewer #1 (Public Review):

Summary:

In this study, Faniyan and colleagues build on their recent finding that renal Glut2 knockout mice display normal fasting blood glucose levels despite massive glucosuria. Renal Glut2 knockout mice were found to exhibit increased endogenous glucose production along with decreased hepatic metabolites associated with glucose metabolism. Crh mRNA levels were higher in the hypothalamus while circulating ACTH and corticosterone was elevated in this model. While these mice were able to maintain normal fasting glucose levels, ablating afferent renal signals to the brain caused low fasting blood glucose levels. In addition, the higher CRH and higher corticosterone levels of the knockout mice were lost following this denervation. Finally, acute phase proteins were altered, plasma Gpx3 was lower, and major urinary protein MUP18 and its gene expression were higher in renal Glut2 knockout mice. Overall, the main conclusion that afferent signaling from the kidney is required for renal glut2 dependent increases in endogenous glucose production is well supported by these findings.

Strengths:

An important strength of the paper is the novelty of the identification of kidney to brain communication as being important for glucose homeostasis. Previous studies had focused on other functions of the kidney modulated by or modulating brain function. This work is likely to promote interest in CNS pathways that respond to afferent renal signals and the response of the HPA axis to glucosuria. Additional strengths of this paper stem from the use of incisive techniques. Specifically, the authors use isotope enabled measurement of endogenous glucose production by GC-MS/MS, capsaicin ablation of afferent renal nerves, and multifiber recording from the renal nerve. The authors also paid excellent attention to rigor in the design and performance of these studies. For example, they used appropriate surgical controls, confirmed denervation through renal pelvic CGRP measurement, and avoided the confounding effects of nerve regrowth over time. These factors strengthen confidence in their results. Finally, humans with glucose transporter mutations and those being treated with SGLT2 inhibitors show a compensatory increase in endogenous glucose production. Therefore, this study strengthens the case for using renal Glut2 knockout mice as a model for understanding the physiology of these patients.

Weaknesses:

A few weaknesses exist. Most concerns relate to the interpretation of this study's findings. The authors state that loss of glucose in urine is sensed as a biological threat based on the HPA axis activation seen in this mouse model. This interpretation is understandable but speculative. Importantly, whether stress hormones mediate the increase in endogenous glucose production in this model and in humans with altered glucose transporter function remains to be demonstrated conclusively. For example, the paper found several other circulating and local factors that could be causal. This model is also unable to shed light on how elevated stress hormones might interact with insulin resistance, which is known to increase endogenous glucose production. That issue is of substantial clinical relevance for patients with T2D and metabolic disease. Finally, how these findings can contribute to improving the efficiency of drugs like SGLT2 inhibitors remains to be seen.

-  We agree with the reviewer’s overall assessment of this manuscript.

- Confirming the contribution of each secreted protein shown in Fig. 4, whose levels were changed between the two groups of mice, toward causing a compensatory increase in glucose production in response to elevated glycosuria is beyond the scope of this manuscript.

Reviewer #2 (Public Review):

Summary:

The authors previously generated renal Glut2 knockout mice, which have high levels of glycosuria but normal fasting glucose. They use this as an opportunity to investigate how compensatory mechanisms are engaged in response to glycosuria. They show that renal and hepatic glucose production, but not metabolism, is elevated in renal Glut2 male mice. They show that renal Glut2 male mice have elevated Crh mRNA in the hypothalamus, and elevated plasma levels of ACTH and corticosterone. They also show that temporary denervation of renal nerves leads to a decrease in fasting and fed blood glucose levels in female renal Glut2 mice, but not control mice. Finally, they perform plasma proteomics in male mice to identify plasma proteins that are changed (up or down) between the knockouts and controls.

Strengths:

The question that is trying to be addressed is clinically important: enhancing glycosuria is a current treatment for diabetes, but is limited in efficacy because of compensatory increases in glucose production.

Weaknesses:

(1) Although I appreciate that the initial characterization of the mice in another publication showed that both males and females have glycosuria, this does not mean that both sexes have the same mechanisms giving rise to glycosuria. There are many examples of sex differences in HPA activation in response to threat, for example. There is an unfounded assumption here that males and females have the same underlying mechanisms of glycosuria that undermines the significance of the findings.

- We agree with the reviewer that although we didn’t observe sex differences in renal Glut2 KO mice in the context of glucose homeostasis, their response (or mechanisms) to elevated glycosuria in enhancing compensatory glucose production may be different between the sexes. Therefore, we have included this limitation in discussion section.

(2) The authors state that they induced the Glut2 knockout with taxomifen as in their previous publication. The methods of that publication indicate that all experiments were completed within 14 days of inducing the Glut2 knockout. This means that the last dose of tamoxifen was delivered 14 days prior to the experimental endpoint of each experiment. This seems like an important experimental constraint that should be discussed in this manuscript. Is the glycosuria that follows Glut2 knockout only a temporary change? If so, then the long-term change in glycosuria that follows SGLT2 inhibition in humans might not be best modelled by this knockout. Please specify when the surgeries to implant a jugular catheter or ablate the renal nerves performed relative to the Glut2 knockout in the Methods.

- The reviewer’s statement ‘The methods of that publication indicate that all experiments were completed within 14 days of inducing the Glut2 knockout’ is incorrect. In the referred publication, we had explicitly mentioned in methods, ‘All of the experiments, except those using a diet-induced obesity mouse model or noted otherwise, were completed within 14 days of inducing the Glut2 deficiency.’ Please see figures 5h-l and 6 in the cited publication, which demonstrate that all the experiments were not completed within 14 days of inducing renal Glut2 deficiency. Per the reviewer’s advice, in the present manuscript we have include the timeline (which in some cases is 4 months beyond inducing glycosuria) in all the figure legends. In addition, for a separate project (which is unpublished) we have measured glycosuria up to 1 year after inducing renal Glut2 deficiency. Therefore, the glycosuria observed in the renal Glut2 KO mice is not temporary.

(3) I am still unclear what group was used for controls. Are these wild-type mice who receive tamoxifen? Are they KspCadCreERT2;Glut2loxP/loxP mice who do not receive tamoxifen? This is important and needs to be specified.

- In our previous response to the reviewer, we had already mentioned which control group was used in this study. Please see our response to the second reviewer’s point 3. As mentioned to the reviewer, we had used Glut2loxp/loxp mice as the control group, which is also described multiple times in the figure legends of our previous paper that reported the phenotype of renal Glut2 KO mice. Per the reviewer’s advice, we have provided the information again in a revised version of this manuscript.

(4) The authors should report some additional control measures for the renal denervation that could also impact blood glucose and perhaps some of their other measures. The control measures, which one would like to see unimpacted by renal denervation, include body weights, food consumption and water intake, and glycosuria itself.

- Please also see fig. 3 in the present manuscript that demonstrates renal afferent denervation doesn’t influence baseline blood glucose or plasma insulin levels. We have now also mentioned in the text that the denervation doesn’t affect food intake or bodyweight.

(5) The graphical abstract shows a link between the hypothalamus and the liver that is completely unsupported by any of the current findings. That arrow should be removed.

- Because we observed an increase in hepatic glucose production in renal Glut2 KO mice (Fig. 1) - which was reduced by 50% after selective afferent renal denervation (Fig. 3) - in the graphical abstract we are suggesting a neural connection between the kidney-brain-liver or an endocrine factor(s) to account for these changes in blood glucose levels as also described in the discussion section. We can include a question mark ‘?’ in the graphical abstract to show that further studies are need to validate these proposed mechanisms; however, we cannot just remove the arrow as advised by the reviewer.

(6) Though the authors have toned down their language implying a causal link between the HPA measures and compensatory elevation of blood glucose in the face of glycosuria, the title still implies this causal link. It is still the case that their data do not support causation. There are many potential ways to establish a causal link but those experiments are not performed here. The renal afferents are correlated with Crh content of the PVN, but nothing has been done to show that the Crh content is important for elevating blood glucose. In light of this, the title should be toned down. Perhaps something like "Renal nerves maintain blood glucose production and elevated HPA activity in response to glycosuria". The link between HPA and glucose is not shown in this paper.

- We request the reviewer to take a look at figure 1, showing an increase in glucose production in renal Glut2 KO mice and figure 3, which demonstrates that an afferent renal denervation reduces blood glucose levels by 50%. The afferent renal denervation (ablation of afferent renal nerves) does reduce blood glucose levels in renal Glut2 KO mice. Therefore, the use of the word ‘promote’ in the title is accurate and appropriate to reflect the role of the afferent renal nerves in contributing to about 50% increase in blood glucose levels in renal Glut2 KO mice.

- Regarding the reviewer's comment on changes in Crh gene expression, please look at figure 3. Ablation of renal afferent nerves decreases hypothalamic Crh gene expression and other mediators of the HPA axis by 50%. Therefore, the afferent renal nerves do contribute to regulating blood glucose levels, at least in part, by the HPA axis (which is widely known to change blood glucose levels). The use of words such as ‘required’ or ‘necessary’ in the title may have indicated causal role or could have been misleading here; therefore, we have purposely used ‘promote’ in the title to accurately reflect the findings of this study.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I have only minor text corrections to add:

- line 223 "A list"

- line 253 "independent"

- line 271 "the body's"

- line 304 "do not"

Yes, we have corrected these errors in a revised version of this manuscript.

Reviewer #2 (Recommendations For The Authors):

(1) Please report the dilutions used, if any, for the ELISAs. If the samples were run neat, please report this. Many manufacturer's instructions say that the user must determine the correct dilution to use for the samples collected. Also, sometimes when small blood volumes are collected, samples must be diluted to achieve the minimum volume collected for the assay. It is not sufficient to indicate that a reader refers to the manufacturer's instructions.

- Per the reviewer’s advice, we have included the dilutions used for each assay in the methods.

Author response:

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

Reviewer #1:

Point 1: The authors have demonstrated that Cs9g12620 contains the EBE of PthA4 in the promoter region, to show that PthA4 controls Cs9g12620, the authors need to compare to the wild type Xcc and pthA4 mutant for Cs9g12620 expression. The data in Figure 1 is not enough.

The data in Figure 1 D and E show a pthA4 Tn5 insertion mutant Mxac126-80 and the expression level of Cs9g12620 in citrus inoculated with the pthA4 mutant.

Point 2: The authors confirmed the interaction between PthA4 and the EBE in the promoter of Cs9g12620 using DNA electrophoretic mobility shift assay (EMSA). However, Figure 2B is not convincing. The lane without GST-PthA4 also clearly showed a mobility shift. For the EMSA assay, the authors need also to include a non-labeled probe as a competitor to verify the specificity. The description of the EMSA in this paper suggests that it was not done properly. It is suggested the authors redo this EMSA assay following the protocol: Electrophoretic mobility shift assay (EMSA) for detecting protein-nucleic acid interactions PMID: 17703195.

Thank you very much for your comments. We have re-conducted the EMSA analysis based on your suggestion. The DNA probe was labeled with Cy5, included a non-labeled probe as a competitor. (Figure 3 B and D; Figure 4B and E)

Point 3: The authors also claimed that PthA4 suppresses the promote activity of Cs9g12620. The data is not convincing and also contradicts with their own data that overexpression of Cs9g12620 causes canker and silencing of it reduces canker considering PthA4 is required for canker development. The authors conducted the assays using transient expression of PthA4. It should be done with Xcc wild type, pthA4 mutant, and negative control to inoculate citrus plants to check the expression of Cs9g12620.

We have detected Cs9g12620 expression in silencing citrus plants inoculated wild type Xcc 29-1. (Figure 7F)

Point 4: Figure 6 AB is not convincing. There are no apparent differences. The variations shown in B are common in different wild-type samples. It is suggested that the authors conduct transgenic instead of transient overexpression.

It has been proven that transient expression of PthA4 leads to canker-like phenotype, suggesting that this experiment is effective. However, it will be more confident if conduct transgenic plant overexpressing pthA4 and Cs9g12620. We’ll create the plants in our following research to confirm the phenotype.

Point 5: Gene silencing data needs more appropriate controls. Figure D seems to suggest canker symptoms actually happen for the RNAi treated. The authors need to make sure the same amount of Xcc was used for both CTV empty vector and the RNAi. It is suggested a blink test is needed here.

We used the same amount of Xcc to inoculate CTV empty vector and the RNAi. In either inoculation, the cultured Xcc cells were suspended in sterile distilled water to a final concentration of 108 CFU/mL (OD600 = 0.3).

Point 6: Figure 1. Please draw a figure to clearly show the location of the EBE in the promoter of Cs9g12620, including the transcription start site, and translational start site.

The EBE in Cs9g12620 promoter was indicated by underlined in Figure supplement 1. We did not sure about the translation start site, but the translation start site was labelled.

eLife assessment

This valuable study provides new insight into potential subtle dynamics in effector biology. The data presented generally support the claims, but in some cases, significant controls are missing and so the overall work is currently incomplete. If the limitations can be addressed, this work should be of broad relevance for biologists interested in molecular plant-microbe interactions.

Reviewer #1 (Public Review):

Previous Review:

The authors have identified the predicted EBE of PthA4 in the promoter of Cs9g12620, which is induced by Xcc. The authors identified a homolog of Cs9g12620, which has variations in the promoter region. The authors show PthA4 suppresses Cs9g12620 promoter activity independent of the binding action. The authors also show that CsLOB1 binds to the promoter of Cs9g12620. Interestingly, the authors show that PthA4 interacts with CsLOB1 at protein level. Finally, it shows that Cs9g12620 is important for canker symptoms. Overall, this study has reported some interesting discoveries and the writing is generally well done. However, the discoveries are affected by the reliability of the data and some flaws of the experimental designs.

Here are some major issues:

The authors have demonstrated that Cs9g12620 contains the EBE of PthA4 in the promoter region, to show that PthA4 controls Cs9g12620, the authors need to compare to the wild type Xcc and pthA4 mutant for Cs9g12620 expression. The data in Figure 1 is not enough.

The authors confirmed the interaction between PthA4 and the EBE in the promoter of Cs9g12620 using DNA electrophoretic mobility shift assay (EMSA). However, Fig. 2B is not convincing. The lane without GST-PthA4 also clearly showed mobility shift. For EMSA assay, the authors need also to include non-labeled probe as competitor to verify the specificity. The description of the EMSA in this paper suggests that it was not done properly. It is suggested the authors to redo this EMSA assay following the protocol: Electrophoretic mobility shift assay (EMSA) for detecting protein-nucleic acid interactions PMID: 17703195.

The authors also claimed that PthA4 suppresses the promote activity of Cs9g12620. The data is not convincing and also contradicts with their own data that overexpression of Cs9g12620 causes canker and silencing of it reduces canker considering PthA4 is required for canker development. The authors conducted the assays using transient expression of PthA4. It should be done with Xcc wild type, pthA4 mutant and negative control to inoculate citrus plants to check the expression of Cs9g12620.

Fig. 6 AB is not convincing. There are no apparent differences. The variations shown in B is common in different wild type samples. It is suggested that the authors to conduct transgenic instead of transient overexpression.

Gene silencing data needs more appropriate controls. Fig. D. seems to suggest canker symptoms actually happen for the RNAi treated. The authors need to make sure same amount of Xcc was used for both CTV empty vector and the RNAi. It is suggested a blink test is needed here.

Comments on revised version:

Point 1: Addressed well.

Point 2: The EMSA was reconducted with adding unlabeled DNA, however, the results are still not convincing. Firstly, in fig.3D lane 5, with the absence of unlabeled DNA, the shifted bound signal wasn't reduced significantly. Secondly, still in fig.3D lane 5, the free labeled DNA probe at the bottom of the gel didn't increase. Which together mean that the unlabeled DNA was unable to compete with the labeled DNA and the "bound" shifted bands might not be true positive.

Point 3: The authors didn't address the question clearly regarding the connection between the inhibition of Cs9g12620 promoter by PthA4 and the positive function of Cs9g12620 on citrus canker.

Point 4: The comment was not addressed. Fig.7A and B are not convincing. Firstly, no evidence shows the expression of transiently expressed genes. Secondly, hard to tell the difference in 7A. Thirdly, since CsLOB1 positively regulates Cs9g12620, why expressing of CsLOB1 is unable to cause phenotype, while expression of PthA4 does?

Point 5: addressed.

Reviewer #1 (Public Review):

Summary:

Authors explore how sex-peptide (SP) affects post-mating behaviours in adult females, such as receptivity and egg laying. This study identifies different neurons in the adult brain and the VNC that become activated by SP, largely by using an intersectional gene expression approach (split-GAL4) to narrow down the specific neurons involved. They confirm that SP binds to the well-known Sex Peptide Receptor (SPR), initiating a cascade of physiological and behavioural changes related to receptivity and egg laying.

Areas of improvement and suggestions:

(1) "These results suggest the SP targets interneurons in the brain that feed into higher processing centers from different entry points likely representing different sensory input" and "All together, these data suggest that the abdominal ganglion harbors several distinct type of neurons involved in directing PMRs"<br /> The characterization of the post-mating circuitry has been largely described by the group of Barry Dickson and other labs. I suggest ruling out a potential effect of mSP in any of the well-known post-mating neuronal circuitry, i.e: SPSN, SAG, pC1, vpoDN or OviDNs neurons. A combination of available split-Gal4 should be sufficient to prove this.

(2) Authors must show how specific is their "head" (elav/otd-flp) and "trunk" (elav/tsh) expression of mSP by showing images of the same constructs driving GFP.

(3) VT3280 is termed as a SAG driver. However, VT3280 is a SPSN specific driver (Feng et al., 2014; Jang et al., 2017; Scheunemann et al., 2019; Laturney et al., 2023). The authors should clarify this.

(4) Intersectional approaches must rule out the influence of SP on sex-peptide sensing neurons (SPSN) in the ovary by combining their constructs with SPSN-Gal80 construct. In line with this, most of their lines targets the SAG circuit (4I, J and K). Again, here they need to rule out the involvement of SPSN in their receptivity/egg laying phenotypes. Especially because "In the female genital tract, these split-Gal4 combinations show expression in genital tract neurons with innervations running along oviduct and uterine walls (Figures S3A-S3E)".

(5) The authors separate head (brain) from trunk (VNC) responses, but they don't narrow down the neural circuits involved on each response. A detailed characterization of the involved circuits especially in the case of the VNC is needed to (a) show that the intersectional approach is indeed labelling distinct subtypes and (b) how these distinct neurons influence oviposition.

Reviewer #3 (Public Review):

Summary:

This paper reports new findings regarding neuronal circuitries responsible for female post-mating responses (PMRs) in Drosophila. The PMRs are induced by sex peptide (SP) transferred from males during mating. The authors sought to identify SP target neurons using a membrane-tethered SP (mSP) and a collection of GAL4 lines, each containing a fragment derived from the regulatory regions of the SPR, fru, and dsx genes involved in PMR. They identified several lines that induced PMR upon expression of mSP. Using split-GAL4 lines, they identified distinct SP-sensing neurons in the central brain and ventral nerve cord. Analyses of pre- and post-synaptic connection using retro- and trans-Tango placed SP target neurons at the interface of sensory processing interneurons that connect to two common post-synaptic processing neuronal populations in the brain. The authors proposed that SP interferes with the processing of sensory inputs from multiple modalities.

Strengths:

Besides the main results described in the summary above, the authors discovered the following:

(1) Reduction of receptivity and induction of egg-laying are separable by restricting the expression of membrane-tethered SP (mSP): head-specific expression of mSP induces reduction of receptivity only, whereas trunk-specific expression of mSP induces oviposition only. Also, they identified a GAL4 line (SPR12) that induced egg laying but did not reduce receptivity.

(2) Expression of mSP in the genital tract sensory neurons does not induce PMR. The authors identified three GAL4 drivers (SPR3, SPR 21, and fru9), which robustly expressed mSP in genital tract sensory neurons but did not induce PMRs. Also, SPR12 does not express in genital tract neurons but induces egg laying by expressing mSP.

Weaknesses:

(1) Intersectional expression involving ppk-GAL4-DBD was negative in all GAL4AD lines (Supp. Fig.S5). As the authors mentioned, ppk neurons may not intersect with SPR, fru, dsx, and FD6 neurons in inducing PMRs by mSP. However, since there was no PMR induction and no GAL4 expression at all in any combination with GAL4-AD lines used in this study, I would like to have a positive control, where intersectional expression of mSP in ppk-GAL4-DBD and other GAL4-AD lines (e.g., ppk-GAL4-AD) would induce PMR.

(2) The results of SPR RNAi knock-down experiments are inconclusive (Figure 5). SPR RNAi cancelled the PMR in dsx ∩ fru11/12 and partially in SPR8 ∩ fru 11/12 neurons. SPR RNAi in dsx ∩ SPR8 neurons turned virgin females unreceptive; it is unclear whether SPR mediates the phenotype in SPR8 ∩ fru 11/12 and dsx ∩ SPR8 neurons.

SPR RNAi knock-down experiments may also help clarify whether mSP worked autocrine or juxtacrine to induce PMR. mSP may produce juxtacrine signaling, which is cell non-autonomous.

eLife assessment

This valuable study provides new insights into the neural circuits involved in post-mating responses in Drosophila females. It presents convincing evidence that the circuits for mating receptivity and egg-laying are distinct. A more thorough discussion regarding the integration of the new findings into the current understanding of post-mating behavior as well as clarification of some experimental details would further improve the manuscript.

Reviewer #2 (Public Review):

Sex peptide (SP) transferred during mating from male to female induces various physiological responses in the receiving female. Among those, the increase in oviposition and decrease in sexual receptivity are very remarkable. Naturally, a long standing and significant question is the identity of the underlying sex peptide target neurons that express the SP receptor and are underlying these responses. Identification of these neurons will eventually lead to the identification of the underlying neuronal circuitry.

The Soller lab has addressed this important question already several years ago (Haussmann et al. 2013), using relevant GAL4-lines and membrane-tethered SP. The results already showed that the action of SP on receptivity and oviposition is mediated by different neuronal subsets and hence can be separated. The GAL4-lines used at that time were, however, broad, and the individual identity of the relevant neurons remained unclear.

In the present paper, Nallasivan and colleagues carried this analysis one step further, using new intersectional approaches and transsynaptic tracing.

Strength:

The intersectional approach is appropriate and state-of-the art. The analysis is a very comprehensive tour-de-force and experiments are carefully performed to a high standard. The authors also produced a useful new transgenic line (UAS-FRTstopFRT mSP). The finding that neurons in the brain (head) mediate the SP effect on receptivity, while neurons in the abdomen and thorax (ventral nerve cord or peripheral neurons) mediate the SP effect on oviposition, is a significant step forward in the endavour to identify the underlying neuronal networks and hence a mechanistic understanding of SP action. Though this result is not entirely unexpected, it is novel as it was not shown before.

Weakness:

Though the analysis identifies a small set of neurons underlying SP responses, it does not go the last step to individually identify at least a few of them. The last paragraph in the discussion rightfully speculates about the neurochemical identity of some of the intersection neurons (e.g. dopaminergic P1 neurons, NPF neurons). At least these suggested identities could have been confirmed by straight-forward immunostainings agains NPF or TH, for which antisera are available. Moreover, specific GAL4 lines for NPF or P1 or at least TH neurons are available which could be used to express mSP to test whether SP activation of those neurons is sufficient to trigger the SP effect.

Author response:

Reviewer #1 (Public Review):

Areas of improvement and suggestions:

(1) "These results suggest the SP targets interneurons in the brain that feed into higher processing centers from different entry points likely representing different sensory input" and "All together, these data suggest that the abdominal ganglion harbors several distinct type of neurons involved in directing PMRs"

The characterization of the post-mating circuitry has been largely described by the group of Barry Dickson and other labs. I suggest ruling out a potential effect of mSP in any of the well-known post-mating neuronal circuitry, i.e: SPSN, SAG, pC1, vpoDN or OviDNs neurons. A combination of available split-Gal4 should be sufficient to prove this.

Indeed, we have tested drivers for some of these neurons already and agree that this information is important to distinguish neurons which are direct SP target from neurons which are involved in directing reproductive behaviors.

(2) Authors must show how specific is their "head" (elav/otd-flp) and "trunk" (elav/tsh) expression of mSP by showing images of the same constructs driving GFP.

The expression pattern for tshGAL, which expresses in the trunk is already published (Soller et al., 2006). We will add images for “head” expression.

(3) VT3280 is termed as a SAG driver. However, VT3280 is a SPSN specific driver (Feng et al., 2014; Jang et al., 2017; Scheunemann et al., 2019; Laturney et al., 2023). The authors should clarify this.

According to the reviewers suggestion, we will clarify the specificity of VT3280.

(4) Intersectional approaches must rule out the influence of SP on sex-peptide sensing neurons (SPSN) in the ovary by combining their constructs with SPSN-Gal80 construct. In line with this, most of their lines targets the SAG circuit (4I, J and K). Again, here they need to rule out the involvement of SPSN in their receptivity/egg laying phenotypes. Especially because "In the female genital tract, these split-Gal4 combinations show expression in genital tract neurons with innervations running along oviduct and uterine walls (Figures S3A-S3E)".

We agree with this reviewer that we need a higher resolution of expression to only one cell type. However, this is a major task that we will continue in follow up studies.

In principal, use of GAL80 is a valid approach to restrict expression, if levels of GAL80 are higher than those of GAL4, because GAL80 binds GAL4 to inhibit its activity. Hence, if levels of GAL80 are lower, results could be difficult to interpret.

(5) The authors separate head (brain) from trunk (VNC) responses, but they don't narrow down the neural circuits involved on each response. A detailed characterization of the involved circuits especially in the case of the VNC is needed to (a) show that the intersectional approach is indeed labelling distinct subtypes and (b) how these distinct neurons influence oviposition.

Again, we agree with this reviewer that we need a higher resolution of expression to only one cell type. However, this is a major task that we will continue in follow up studies.

Reviewer #2 (Public Review):

Strength:

The intersectional approach is appropriate and state-of-the art. The analysis is a very comprehensive tour-de-force and experiments are carefully performed to a high standard. The authors also produced a useful new transgenic line (UAS-FRTstopFRT mSP). The finding that neurons in the brain (head) mediate the SP effect on receptivity, while neurons in the abdomen and thorax (ventral nerve cord or peripheral neurons) mediate the SP effect on oviposition, is a significant step forward in the endavour to identify the underlying neuronal networks and hence a mechanistic understanding of SP action. Though this result is not entirely unexpected, it is novel as it was not shown before.

We thank reviewer 2 for recognizing the advance of our work.

Weakness:

Though the analysis identifies a small set of neurons underlying SP responses, it does not go the last step to individually identify at least a few of them. The last paragraph in the discussion rightfully speculates about the neurochemical identity of some of the intersection neurons (e.g. dopaminergic P1 neurons, NPF neurons). At least these suggested identities could have been confirmed by straight-forward immunostainings agains NPF or TH, for which antisera are available. Moreover, specific GAL4 lines for NPF or P1 or at least TH neurons are available which could be used to express mSP to test whether SP activation of those neurons is sufficient to trigger the SP effect.

We appreciate this reviewers recognition of our previous work showing that receptivity and oviposition are separable. As pointed out we have now gone one step further and identified in a tour de force approach subsets of neurons in the brain and VNC.

We agree with this reviewer that we need a higher resolution of expression to only one cell type. As pointed out by this reviewer, the neurochemical identity is an excellent suggestions and will help to further restrict expression to just one type of neuron. However, this is a major task that we will continue in follow up studies.

Reviewer #3 (Public Review):

Strengths:

Besides the main results described in the summary above, the authors discovered the following:

(1) Reduction of receptivity and induction of egg-laying are separable by restricting the expression of membrane-tethered SP (mSP): head-specific expression of mSP induces reduction of receptivity only, whereas trunk-specific expression of mSP induces oviposition only. Also, they identified a GAL4 line (SPR12) that induced egg laying but did not reduce receptivity.

(2) Expression of mSP in the genital tract sensory neurons does not induce PMR. The authors identified three GAL4 drivers (SPR3, SPR 21, and fru9), which robustly expressed mSP in genital tract sensory neurons but did not induce PMRs. Also, SPR12 does not express in genital tract neurons but induces egg laying by expressing mSP.

We thank reviewer 3 for recognizing these two important points regarding the SP response that point to a revised model for how the underlying circuitry induces the post-mating response.

Weaknesses:

(1) Intersectional expression involving ppk-GAL4-DBD was negative in all GAL4AD lines (Supp. Fig.S5). As the authors mentioned, ppk neurons may not intersect with SPR, fru, dsx, and FD6 neurons in inducing PMRs by mSP. However, since there was no PMR induction and no GAL4 expression at all in any combination with GAL4-AD lines used in this study, I would like to have a positive control, where intersectional expression of mSP in ppk-GAL4-DBD and other GAL4-AD lines (e.g., ppk-GAL4-AD) would induce PMR.

We will add positive controls of for ppk-DBD expression and expand the discussion section.

(2) The results of SPR RNAi knock-down experiments are inconclusive (Figure 5). SPR RNAi cancelled the PMR in dsx ∩ fru11/12 and partially in SPR8 ∩ fru 11/12 neurons. SPR RNAi in dsx ∩ SPR8 neurons turned virgin females unreceptive; it is unclear whether SPR mediates the phenotype in SPR8 ∩ fru 11/12 and dsx ∩ SPR8 neurons.

We agree with this reviewer that the interpretation of the SPR RNAi results are complicated by the fact that SP has additional receptors (Haussmann et al 2013). The results are conclusive for all three intersections when expressing UAS mSP in SPR RNAi with respect to oviposition, e.g. egg laying is not induced in the absence of SPR. For receptivity, the results are conclusive for dsx ∩ fru11/12 and partially for SPR8 ∩ fru 11/12.

Potentially, SPR RNAi knock-down does not sufficiently reduce SPR levels to completely reduce receptivity in some intersection patterns, likely also because splitGal4 expression is less efficient.

Why SPR RNAi in dsx ∩ SPR8 neurons turned virgin females unreceptive is unclear, but we anticipate that we need a higher resolution of expression to only one cell type to resolve this unexpected result. However, this is a major task that we will continue in follow up studies.

SPR RNAi knock-down experiments may also help clarify whether mSP worked autocrine or juxtacrine to induce PMR. mSP may produce juxtacrine signaling, which is cell non-autonomous.

Whether membrane-tethered SP induces the response in a autocrine manner is an import aspect in the interpretation of the results from mSP expression.

Removing SPR by SPR RNAi and expression of mSP in the same neurons did not induce egg laying for all three intersection and did not reduce receptivity for dsx ∩ fru11/12 and for SPR8 ∩ fru 11/12. Accordingly, we can conclude that for these neurons the response is induced in an autocrine manner.

We will add this aspect to the discussion section.

eLife assessment

This study highlights an important discovery: a bacterial pathogen's effector influences plant responses that in turn affect how the leafhopper insect vector for the bacteria is attracted to the plants in a sex-dependent manner. The research is backed by convincing physiological and transcriptome analyses. This study unveils a complex interdependence between the pathogen effector, male leafhoppers, and a plant transcription factor in modulating female attraction to the plant, shedding light on previously unexplored aspects of plant-bacteria-insect interactions.

Reviewer #1 (Public Review):

Summary:

Orlovski and his colleagues revealed an interesting phenomenon that SAP54-overexpressing leaf exposure to leafhopper males is required for the attraction of followed females. By transcriptomic analysis, they demonstrated that SAP54 effectively suppresses biotic stress response pathways in leaves exposed to the males. Furthermore, they clarified how SAP54, by targeting SVP, heightens leaf vulnerability to leafhopper males, thus facilitating female attraction and subsequent plant colonization by the insects.

Strengths:

The phenomenon of this study is interesting and exciting.

Weaknesses:

The underlying mechanisms of this phenomenon are not convincing.

Reviewer #2 (Public Review):

Summary:

In this study, the authors show that leaf exposure to leafhopper males is required for female attraction in the SAP54-expressing plant. They clarify how SAP54, by degrading SVP, suppresses biotic stress response pathways in leaves exposed to the males, thus facilitating female attraction and plant colonization.

Strengths:

This study suggests the possibility that the attraction of insect vectors to leaves is the major function of SAP54, and the induction of the leaf-like flowers may be a side-effect of the degradation of MTFs and SVP. It is a very surprising discovery that only male insect vectors can effectively suppress the plant's biotic stress response pathway. Although there has been interest in the phyllody symptoms induced by SAP54, the purpose, and advantage of secreting SAP54 were unknown. The results of this study shed light on the significance of secreted proteins in the phytoplasma life cycle and should be highly evaluated.

Weaknesses:

One weakness of this study is that the mechanisms by which male and female leafhoppers differentially affect plant defense responses remain unclear, although I understand that this is a future study.

The authors show that female feeding suppresses female colonization on SAP54-expressing plants. This is also an intriguing phenomenon but this study doesn't explain its molecular mechanism (Figure 7).

eLife assessment

This important body of work uses state-of-the-art quantitative methods to characterize and compare behaviors across five different fish species to understand which features are conserved and which ones are differentiated. The results from this study will potentially be of interest to ethologists and also have potential utility in understanding the neural mechanisms leading to these behaviors. While some claims are supported with compelling evidence, there are a few results that need further justification or qualification.

Reviewer #1 (Public Review):

Summary:

The authors used video tracking of 4 larval cichlid species and medaka to quantify prey-capture behaviors.

Strengths:

Comparing these behaviors is in principle an interesting question, and helps to address the typicality of the much better-understood zebrafish model. The authors make a good effort to analyze their data quantitatively.

Weaknesses:

(1) The overall conclusion, as summarized in the abstract as "Together, our study documents the diversification of locomotor and oculomotor adaptations among hunting teleost larvae" is not that compelling. What would be much more interesting would be to directly relate these differences to different ecological niches (e.g. different types of natural prey, visual scene conditions, height in water column etc), and/or differences in neural circuit mechanisms. While I appreciate that this paper provides a first step on this path, by itself it seems on the verge of stamp collecting, i.e. collecting and cataloging observations without a clear, overarching hypothesis or theoretical framework.

(2) The data to support some of the claims is either weak or lacking entirely.

Reviewer #2 (Public Review):

Summary:

This is a fascinating study about the behavioral kinematics of prey capture in larvae of several fish species (zebrafish, four cichlid species, and medaka). The authors describe in great detail swimming kinematics, hunting movement, eye movement as well as prey capture kinematics across these species. One striking finding is that cichlids and zebrafish use binocular vision to hunt for prey whereas medaka uses a monocular hunting style with a sideways motion to capture prey. The behavioral variation described in this study forms a strong foundation for future studies on the mechanisms underlying variation in hunting styles.

Strengths:

In general, the paper is well-written and documents very interesting data. The authors used sophisticated analyses that help appreciate the complexity of the behaviors examined. The discussion attempts to place the paper in a broader, comparative context. Overall, this paper reveals novel insight into an important behavior across different teleost species and lays a foundation for future studies on the neural and genetic basis of these distinct swimming and hunting behaviors.

Weaknesses:

The paper is rather descriptive in nature, although more context is provided in the discussion. Most figures are great, but I think the authors could add a couple of visual aids in certain places to explain how certain components were measured.

Reviewer #3 (Public Review):

Summary:

This paper uses 2D pose estimation and quantitative behavioral analyses to compare patterns of prey capture behavior used by six species of freshwater larval fish, including zebrafish, medaka, and four cichlids. The convincing comparison of tail and eye kinematics during hunts reveals that cichlids and zebrafish use binocular vision and similar hunting strategies, but that cichlids make use of an expanded set of action types. The authors also provide convincing evidence that medaka instead use monocular vision during hunts. This finding has important implications for the evolution of distinct distance estimation algorithms used by larval teleost fish species during prey capture.

Strengths:

The quality of the behavioral data is solid and the high frame rate allowed for careful quantification and comparison of eye and tail dynamics during hunts. The statistical approach to assess eye vergence states (Figure 2B) is elegant, the cross-species comparison of prey location throughout each hunt phase is well done (Figure 3B-D), and the demonstration that swim bout tail kinematics from diverse species can be embedded in a shared "canonical" principal component space to explain most of the variance in 2D postural dynamics for each species (Figure 4A-C) provides a simple and powerful framework for future studies of behavioral diversification across fish species.

Weaknesses:

More evidence is needed to assess the types of visual monocular depth cues used by medaka fish to estimate prey location, but that is beyond the scope of this compelling paper. For example, medaka may estimate depth through knowledge of expected prey size, accommodation, defocus blur, ocular parallax, and/or other possible algorithms to complement cues from motion parallax.

eLife assessment

This is a valuable paper that identifies a potential challenge for embryos during fertilization: holding sperm contents in the fertilized embryos away from the oocyte meiotic spindle so that they don't get ejected into the polar body during meiotic chromosome segregation. The authors identify proteins involved in cytoplasmic streaming and maintaining the grouping of paternal organelles as being critical for this process. There remain minor weaknesses in the data presented but the paper provides solid evidence for the majority of its claims, and while the findings may pertain to a narrow audience the tools used and basic characterization shown will likely be relied upon by many in the community and therefore is of high value.

Joint Public Review:

Summary:

This paper by Beath et. al. identifies a potential regulatory role for proteins involved in cytoplasmic streaming and maintaining the grouping of paternal organelles: holding sperm contents in the fertilized embryos away from the oocyte meiotic spindle so that they don't get ejected into the polar body during meiotic chromosome segregation. The authors show that by time-lapse video, paternal mitochondria (used as a readout for sperm and its genome) is excluded from yolk granules and maternal mitochondria, even when moving long distances by cytoplasmic streaming. To understand how this exclusion is accomplished, they first show that it is independent of both internal packing and the engulfment of the paternal chromosomes by the maternal endoplasmic reticulum creating an impermeable barrier. They then test whether the control of cytoplasmic steaming affects this exclusion by knocking down two microtubule motors, Katanin and kinesis I. They find that the ER ring, which is used as a proxy for paternal chromosomes, undergoes extensive displacement with these treatments during anaphase I and interacts with the meiotic spindle, supporting their hypothesis that the exclusion of paternal chromosomes is regulated by cytoplasmic streaming. Next, they test whether a regulator of maternal ER organization, ATX-2, disrupts sperm organization so that they can combine the double depletion of ATX-2 and KLP-7, presumably because klp-7 RNAi (unlike mei-1 RNAi) does not affect polar body extrusion and they can report on what happens to paternal chromosomes. They find that the knockdown of both ATX-2 and KLP-7 produces a higher incidence of what appears to be the capture of paternal chromosomes by the meiotic spindle (5/24 vs 1/25). However, this capture event appears to halt the cell cycle, preventing the authors from directly observing whether this would result in the paternal chromosomes being ejected into the polar body.

The authors addressed the vast majority of the Reviewer's comments including the addition of new figures, re-wording of data interpretation and discussion points to better reflect the claims of the paper. There remain a few outstanding points which were not addressed.

In many cases the number of embryos analyzed or events capture remains low and the authors conclude that these sample sizes prevented statistical significance. It's not clear if more embryos were analyzed or if more capture would lead to statistical significance. Language capturing this caveat should also be included in the manuscript. A specific example of this is given below:

In the double knockdown of ATX-2 and KLP-7, there was no significant difference between single and double knockdowns and the ER ring displacement was not analyzed in this double mutant. Further, there was no difference in the frequency of sperm capture between single and double ATX-2 and KLP-7 due to low sample size, the the strength of the conclusion of this manuscript would be greatly improved if both of these results were further explored.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

This paper by Beath et. al. identifies a potential regulatory role for proteins involved in cytoplasmic streaming and maintaining the grouping of paternal organelles: holding sperm contents in the fertilized embryos away from the oocyte meiotic spindle so that they don't get ejected into the polar body during meiotic chromosome segregation. The authors show that by time-lapse video, paternal mitochondria (used as a readout for sperm and its genome) is excluded from yolk granules and maternal mitochondria, even when moving long distances by cytoplasmic streaming. To understand how this exclusion is accomplished, they first show that it is independent of both internal packing and the engulfment of the paternal chromosomes by maternal endoplasmic reticulum creating an impermeable barrier. They then test whether the control of cytoplasmic steaming affects this exclusion by knocking down two microtubule motors, Katanin and kinesis I. They find that the ER ring, which is used as a proxy for paternal chromosomes, undergoes extensive displacement with these treatments during anaphase I and interacts with the meiotic spindle, supporting their hypothesis that the exclusion of paternal chromosomes is regulated by cytoplasmic streaming. Next, they test whether a regulator of maternal ER organization, ATX-2, disrupts sperm organization so that they can combine the double depletion of ATX-2 and KLP-7, presumably because klp-7 RNAi (unlike mei-1 RNAi) does not affect polar body extrusion and they can report on what happens to paternal chromosomes. They find that the knockdown of both ATX-2 and KLP-7 produces a higher incidence of what appears to be the capture of paternal chromosomes by the meiotic spindle (5/24 vs 1/25). However, this capture event appears to halt the cell cycle, preventing the authors from directly observing whether this would result in the paternal chromosomes being ejected into the polar body. 

Strengths: 

This is a useful, descriptive paper that highlights a potential challenge for embryos during fertilization: when fertilization results in the resumption of meiotic divisions, how are the paternal and maternal genomes kept apart so that the maternal genome can undergo chromosome segregation and polar body extrusion without endangering the paternal genome? In general, the experiments are well-executed and analyzed. In particular, the authors' use of multiple ways to knock down ATX-2 shows rigor. 

Weaknesses: 

The paper makes a case that this regulation may be important but the authors should do some additional work to make this case more convincing and accessible for those outside the field. In particular, some of the figures could include greater detail to support their conclusions, they could explain the rationale for some experiments better and they could perform some additional control experiments with their double depletion experiments to better support their interpretations. Also, the authors' inability to assess the functional biological consequences of the capture of the sperm genome by the oocyte spindle should be discussed, particularly in light of the cell cycle arrest that they observe. 

These general comments are addressed in the more specific critiques below.

Reviewer #2 (Public Review): 

Summary 

In this manuscript, Beath et al. use primarily C. elegans zygotes to test the overarching hypothesis that cytoplasmic mechanisms exit to prevent interaction between paternal chromosomes and the meiotic spindle, which are present in a shared zygotic cytoplasm after fertilization. Previous work, much of which by this group, had characterized cytoplasmic streaming in the zygote and the behavior of paternal components shortly after fertilization, primarily the clustering of paternal mitochondria and membranous organelles around the paternal chromosomes. This work set out to identify the molecular mechanisms responsible for that clustering and test the specific hypothesis that the "paternal cloud" helps prevent the association of paternal chromosomes with the meiotic spindle. 

Strengths 

This work is a collection of technical achievements. The data are primarily 3- and 4-channel time-lapse images of zygotes shortly after fertilization, which were performed inside intact animals. There are many instances in which the experiments show extreme technical skill, such as tracking the paternal chromosomes over large displacements throughout the volume of the embryo. The authors employ a wide variety of fluorescent reporters to provide a remarkably clear picture of what is going on in the zygote. These reagents and the novel characterization of these stages that they provide will be widely beneficial to the community. 

The data provide direct visualization of what had previously been a mostly hypothetical structure, the "paternal cloud," using simultaneous labeling of paternal DNA and mitochondria in combination with a variety of maternal proteins including maternal mitochondria, yolk granules, tubulin, and plasma membrane. Together, these images provided convincing evidence of the existence of this specified cytoplasmic domain. They go on to show that the knockdown of the ataxin-2 homolog ALX-2, a protein previously shown to affect ER dynamics, disrupted the paternal cloud, identifying a role for ER organization in this structure. 

The authors then used the system to test the functional consequences of perturbing the cytoplasmic organization. Consistent with the paternal cloud being a stable structure, it stayed intact during large movements the authors generated using previously published knockdowns (of mei-1/katanin and kinesin-13/kpl-7) that increased cytoplasmic streaming. They used this data to document instances in which the paternal chromosomes were likely to have been attached to the spindle. They concluded with direct evidence of spindle fibers connecting to the paternal chromatin upon knockdown of ATX-2 in combination with increased cytoplasmic streaming, providing strong, direct support for their overarching hypothesis. 

Weaknesses 

While the data is convincing, the narrative of the paper could be streamlined to highlight the novelty of the experiments and better articulate the aims. For example, the cloud of paternal mitochondria and membranous organelles was previously shown, but Figures 1-2 largely reiterate that observation. The innovation seems to be that the combination of ER, yolk, and maternal mitochondrial markers makes the existence of a specified domain more concrete. There are also some instances where more description is needed to make the conclusions from the images clear. 

These general comments are addressed in the more specific critiques below.

The manuscript intersperses what read like basic characterizations of fluorescent markers that, as written, can distract from the main story. The authors characterized the dynamics of ER organization throughout the substages of meiosis and the permeability of the envelope of ER that surrounds the paternal chromatin, but it could be more clearly established how the ability to visualize these structures allowed them to address their aims.

We have added the following after the initial description of ER morphology changes: (ER morphology was used to determine cell-cycle stages during live imaging reported below in Fig. 6.)

More background on what was previously known about ER organization in M-phase and the role of ataxin proteins specifically may help provide more continuity. 

We have added references to transitions to ER sheets during mitotic M-phase in HeLa cells and Xenopus extracts.

Reviewer #3 (Public Review): 

Summary: 

This study by Beath et al. investigated the mechanisms by which sperm DNA is excluded from the meiotic spindle after fertilization. Time-lapse imaging revealed that sperm DNA is surrounded by paternal mitochondria and maternal ER that is permeable to proteins. By increasing cytoplasmic streaming using kinesin-13 or katanin RNAi, the authors demonstrated that limiting cytoplasmic streaming in the embryo is an important step that prevents the capture of sperm DNA by the oocyte meiotic spindle. Further experiments showed that the Ataxin-2 protein is required to hold paternal mitochondria together and close to the sperm DNA. Finally, double depletion of kinesin-13 and Ataxin-2 suggested an increased risk of meiotic spindle capture of sperm DNA. 

Overall, this is an interesting finding that could provide a new understanding of how meiotic spindle capture of sperm DNA and its accidental expulsion into the polar body is prevented. However, some conceptual gaps need to be addressed and further experiments and improved data analyses would strengthen the paper. 

- It would be helpful if the authors could discuss in good detail how they think maternal ER surrounds the sperm DNA

We have added 2 references to papers about nuclear envelope re-assembly from Shirin Bahmanyar’s lab and suggest the ER envelope is a halted intermediate in nuclear envelope reassembly.

and why is it not disrupted following Ataxin disruption. 

We have been attempting to disrupt ER structures in the meiotic embryo for the last 5 years by depleting profilin, BiP, atlastin, ATX-2 and by optogenetically packing ER into a ball in the middle of the oocyte.  None of these treatments prevent envelopment of the sperm DNA by maternal ER.  None of these treatments remove ER from the spindle envelope and none remove ER from the plasma membrane.  These treatments mostly result in “large aggregates” of ER that we have not examined by EM.  Wild speculation: any disruption of the ER strong enough to prevent ER envelopment around chromatin would be sterile because the M to S transition in the mitotic zone of the germline would be blocked.  Rapid depletion of ATX-2 to the extent shown by rigorous data in this manuscript does not prevent ER envelopment around chromatin.  We chose not to speculate about the reasons for this because we do not know why.

- Since important phenotypes revealed in RNAi experiments (e.g. kinesin-13 and ataxin-2 double depletion) are not very robust, the authors should consider toning down their conclusions and revising some of their section headings. I appreciate that they are upfront about some limitations, but they do nonetheless make strong concluding sentences. 

We have changed the discussion of the klp-7 atx-2 double depletion to: “The capture of the sperm DNA by the meiotic spindle in ATX-2 KLP-7 double depleted embryos suggests that the integrity of the exclusion zone around the sperm DNA might insulate the sperm DNA from spindle microtubules.  However, a much larger number of klp-7(RNAi) singly depleted and atx-2(degron) singly depleted time-lapse sequences are needed to rigorously support this idea. “

- The discussion section could be improved further to present the authors' findings in the larger context of current knowledge in the field. 

We have expanded the discussion as suggested.

- The authors previously demonstrated that F-actin prevents meiotic spindle capture of sperm DNA in this system. However, the current manuscript does not discuss how the katanin, kinesin-13 and Ataxin-2 mechanisms could work together with previously established functions of F-actin in this process. 

We have added pfn-1(RNAi) to the discussion section.

- How can the authors exclude off-target effects in their RNAi depletion experiments? Can kinesin-13, katanin, and Ataxin phenotypes be rescued for instance? 

For ataxin-2 phenotypes, two completely independent controls for off target effects are shown.  GFP(RNAi) on a strain with and endogenous ATX-2::GFP tag vs GFP(RNAi) on a strain with no tag on the ATX-2.  ATX-2::AID with or without auxin.  For kinesin-13 and katanin, we did not do a rigorous control for off-target effects of RNAi.  However, the effects of these depletions on cytoplasmic microtubules have been previously reported by others

- How are the authors able to determine if the paternal genome was actually captured by the spindle? Does lack of movement definitively suggest capture without using a spindle marker? 

mKate::tubulin labels the spindle in each capture event.  This can be seen in Video S3. for mei-1(RNAi) and Figure 9 for atx-2 klp-7 double depletions.

(1) Major issues: 

The images provided are not convincing that mitochondria are entirely excluded from the regions with yolk granules from the images provided. Please provide insets of magnified images of the paternal mitochondria in Figure 1E to more clearly show the exclusion even when paternal mitochondria are streaming. Providing grayscale images, individual z-sections and/or some quantification of this data might also be more convincing to this reviewer. 

We have modified Fig. 1 by adding single wavelength magnified insets to more clearly show that paternal mitochondria are in a “black hole” in the maternal yolk granules during  cytoplasmic streaming.

Figure 2 -This figure can be retitled to highlight that the paternal organelle cloud is impermeable to mitochondria and conserved. 

The legend has been re-titled as suggested.

Figure 3B, An image of the DNA within the ring of maternal ER especially since the maternal ER ring is used as a proxy for the paternal chromosomes in later figures would strengthen the authors' claims.

We have added a panel showing DAPI-stained DNA in the center of the ER ring and paternal mitochondria cloud. 

Why is the faster time scale imaging significant? I think this could be more clearly set up in the paper. Perhaps rapid imaging of maternal mito-labeled kca-1(RNAi) embryos would better show the difference in time scale, with the expectation that the paternal cloud forms and persists while the ER invades. 

We are not sure what the reviewer means.  5 sec time intervals were used throughout the paper.  We are also not sure how kca-1(RNAi) would help.  Movement of the entire oocyte into and out of the spermatheca is what limits the ability to keep a fusing sperm in focus.  kca-1(RNAi) would prevent cytoplasmic streaming but not ovulation movements.

Figure 4 - The question about the permeability of the ER envelope seems to come out of nowhere as written. It isn't clear how it contributes to the larger story about preventing sperm incorporation in the spindle.

This section of the results is introduced with: “If the maternal ER envelope around sperm DNA was sealed and impermeable during meiosis, this could both prevent the sperm DNA from inducing ectopic spindle assembly and prevent the sperm DNA from interacting with meiotic spindle microtubules.” 

The data in Figure 4 would probably not be expected to be in this paper based on the paper title. Maybe the title needs something about ER dynamics? "eg. ATX-2 but not an ER envelope" isolates the paternal chromatin? 

In Figure 5, it seems that RNAi of klp-7 and Mei-1 had slightly different effects on short-axis displacement of the ER envelope (klp-7 affecting it more dramatically than mei-1) and slightly different effects on interaction with the meiotic spindle (capture vs streaming past the spindle). The authors mention in their discussion that the difference in the interaction with the meiotic spindle might reflect the effects that loss of Mei-1 may have on the spindle but could it also be a consequence of the differences in cytoplasmic streaming observed?

With our current data, the only statistically significant difference between cytoplasmic streaming of the sperm contents in mei-1(RNAi) vs klp-7(RNAi) is that excessive streaming persists longer into metaphase II in klp-7(RNAi).  We have added a sentence describing this difference to the results.  If differences in streaming were the cause of different capture frequencies, then klp-7(RNAi) would cause more capture events than mei-1(RNAi) but the opposite was observed.  We have avoided too much discussion here because the frequency of capture events is too low to demonstrate statistically significant differences between mei-1(RNAi), klp-7(RNAi), and atx-2(degron) + klp-7(RNAi) without a very large increase in the number of time-lapse sequences.  

Also, the authors should find a way to represent this interaction with the meiotic spindle in a quantitative or table form to allow the reader to observe some of the patterns they report more easily.

We have added a table to Fig. 9 that summarizes capture data.

Finally, can the authors report when they observe the closest association with the meiotic spindle: Does it correlate with the period of greatest displacement (AI) or are they unlinked? 

The low frequency of capture events makes it difficult to test this rigorously.

Figure 6- 'Endogenously tagged ATX-2 was observed throughout oocytes and meiotic embryos without partial co-localization with ER.' How can the authors exclude co-localization with ER? 

We have changed the wording to: “Endogenously tagged ATX-2 was observed throughout oocytes and meiotic embryos (Fig. 6A; Fig. S2).  ATX-2 did not uniquely  co-localize with ER (Fig. S2).“

The rationale for why the authors think that the integrity of sperm organelles is important to keep the genomes apart is not clear to this reviewer and needs to be explained better. Moving the discussion of the displacement experiments in Figure S3 from the end of the results section to the ATX-2 knockdown section would help accomplish this. 

We have added the sentence: “The frequency of sperm capture by the meiotic spindle (Fig. 9D) was significantly higher than wild-type controls in klp-7(RNAi) atx-2(AID) double depleted embryos (p=0.011 Fisher’s exact test).   Although the number of single mutant embryos analyzed was too low to demonstrate a significant difference between single and double mutant embryos,  these results qualitatively support the hypothesis that limiting cytoplasmic streaming and maintaining the integrity of the ball of paternal mitochondria are both important for preventing capture events between the meiotic spindle and sperm DNA.”

It looks like, in the double knockdown of ATX-2 and KLP-7, the spread of paternal mitochondria is less affected than when only ATX-2 is depleted. What effect does this result have on the observation that the incidence of sperm capture appears to increase in the double depletion? What does displacement of the ER ring look like in the double depletion? Is it additive, consistent with their interpretation that both limiting cytoplasmic streaming and maintaining the integrity of the ball of paternal mitochondria is required to keep the genomes separate? 

We cannot show a significant difference between single a double knockdowns without increasing n by alot.  We did not analyze ER ring displacement in the double mutant.

Is the increased incidence of capture in the double-depleted embryos significant? 

We have added the sentence: “The frequency of sperm capture by the meiotic spindle (Fig. 9D) was significantly higher than wild-type controls in klp-7(RNAi) atx-2(AID) double depleted embryos (p=0.011 Fisher’s exact test).   Although the number of single mutant embryos analyzed was too low to demonstrate a significant difference between single and double mutant embryos,  these results qualitatively support the hypothesis that limiting cytoplasmic streaming and maintaining the integrity of the ball of paternal mitochondria are both important for preventing capture events between the meiotic spindle and sperm DNA.”

What do the authors make of the cell cycle arrest observed when paternal chromosomes are captured? Is there an argument to be made that this arrest supports the idea that preventing this capture is actively regulated and therefore functionally important? 

We chose not to discuss the mechanism of this arrest because considerably more work would be required to prove that it is not caused by a combination of imaging conditions and genotype.  The low frequency of these capture + arrest events would make it very difficult to show that the arrest does not occur after depleting a checkpoint protein.

(2) Minor concerns: 

Top of page 4: "streaming because depletion tubulin stops cytoplasmic streaming (7)" should be "streaming because depletion of tubulin stops cytoplasmic streaming (7)" 

The ”of” has been inserted.

Page 6: "This result indicated that the volume of paternal mitochondria excludes maternal mitochondria and yolk granules but not maternal ER." The authors have only shown this for maternal mitochondria, not yolk granules. 

We have deleted the mention of yolk granules here.

Page 7: "These results suggest that all maternal membranes are initially excluded from the sperm at fusion." Should be "These results show that maternal ER are initially excluded from the sperm at fusion. Since maternal mitochondria and yolk granules are excluded later, this suggests that all maternal membranes are initially excluded from the sperm at fusion." 

We have changed this sentence as suggested.

It's not clear why the authors show other types of movement that might be quantified when cytoplasmic streaming is affected in Figure 5A and only quantify long-axis and short-axis displacement. 

We have deleted the other types of movement from the schematic.  Although these parameters were quantified, we did not include this data in the results so it would be confusing for the reader to have them in the schematic.

Bottom of page 7: Mention that the GFP::BAF-1 was maternally provided. 

We have added “Maternally provided..”

Missing an Arrow on Figure 1A 9:20. 

We removed the text citation to an arrow in Fig. 1A because we moved most of the description of the ER ring to Fig. 3 to address other reviewer suggestions.

Supplemental videos should be labeled appropriately to indicate what structures are labeled. It is currently difficult to understand what is being shown. 

(3) Issues with the Discussion section: 

"The simplest explanation is that cytoplasm does not mix during the 45 min from GVBD to pronucleus formation due to the high viscosity of cytoplasm." - Citation page 12. 

We have changed the sentence to: “The simplest hypothesis is that maternal and paternal cytoplasm might not mix during the 45 min from GVBD to pronucleus formation due to the high viscosity of cytoplasm.” 

"The higher frequency of capture of the sperm DNA by the meiotic spindle in ATX-2 KLP-7 double depleted embryos compared with either single depletion suggests that the integrity of the exclusion zone around the sperm DNA may insulate the sperm DNA from spindle microtubule" - Pages 12-13 reference the figures. 

This sentence has been rewritten in response to other comments but the new sentence now references revised Fig. 9.

"ATX-2 is required to maintain the integrity of the ball of paternal mitochondria around the sperm DNA, but the mechanism is unknown." - Page 13 reference figure. 

A reference to Figs 7 and 8 has been inserted.

" In control embryos, the sperm contents rarely came near the meiotic spindle in agreement with a previous study that found that male and female pronuclei rarely form next to each other (6). Streaming of the sperm contents was most commonly restricted to a jostling motion with little net displacement, circular streaming in the short axis of the embryo, or long axis streaming in which the sperm turned away from the spindle before the halfway point of the embryo. Depletion of MEI-1 or KLP-7 resulted in longer excursions of the sperm contents in the long axis of the embryo toward the spindle but frequent capture of the sperm by the spindle was only observed in mei-1(RNAi)." - Page 13, the corresponding figures need to be referenced for these sentences. 

We have inserted figure references.

"In capture events observed after double depletion of ATX-2 and KLP-7, a bundle of microtubules was discernible extending from the spindle into the ER envelope surrounding the sperm DNA. Such bundles were not observed in mei-1(RNAi) capture events, likely because of the previously reported low density of microtubules in mei-1(RNAi) spindles (36, 37)." - Pages 13-14 references figures here. 

We have inserted figure references.

"The higher frequency of capture of the sperm DNA by the meiotic spindle in ATX-2 KLP-7 double depleted embryos compared with either single depletion suggests that the integrity of the exclusion zone around the sperm DNA may insulate the sperm DNA from spindle microtubules." - This should be toned down since this phenotype is not robust. 

We have changed this to: “The capture of the sperm DNA by the meiotic spindle in ATX-2 KLP-7 double depleted embryos suggests that the integrity of the exclusion zone around the sperm DNA might insulate the sperm DNA from spindle microtubules.  However, a much larger number of klp-7(RNAi) singly depleted and atx-2(degron) singly depleted time-lapse sequences are needed to rigorously support this idea. “

ATX-2 depletion alters ER morphology but does not impact the maternal ER envelope - could the authors provide a potential explanation for this? 

In the discussion, we cite papers showing that ATX-2 depletion affects many different cellular processes so the effect we see on paternal mitochondria might have nothing to do with the ER ring.   We have been attempting to disrupt ER structures in the meiotic embryo for the last 5 years by depleting profilin, BiP, atlastin, ATX-2 and by optogenetically packing ER into a ball in the middle of the oocyte.  None of these treatments prevent envelopment of the sperm DNA by maternal ER.  None of these treatments remove ER from the spindle envelope and none remove ER from the plasma membrane.  These treatments mostly result in “large aggregates” of ER that we have not examined by EM.  Wild speculation: any disruption of the ER strong enough to prevent ER envelopment around chromatin would be sterile because the M to S transition in the mitotic zone of the germline would be blocked.  Rapid depletion of ATX-2 to the extent shown by rigorous data in this manuscript does not prevent ER envelopment around chromatin.  We chose not to speculate about the reasons for this because we do not know why.

It would be good to have representative images of what the altered spindle looks like in MEI-1-depleted oocytes. 

The structure of MEI-1-depleted spindles has been described in the cited references.

"Depletion of MEI-1 or KLP-7 resulted in longer excursions of the sperm contents in the long axis of the embryo toward the spindle but frequent capture of the sperm by the spindle was only observed in mei-1(RNAi)" - It is intriguing that this does not happen in the double depletion experiments of kinesin-13 and ATX-2. The authors should perhaps discuss this. 

This does happen in KLP-7 ATX-2 double depleted embryos as shown in Fig. 9.

(4) Missing citations: 

"This analysis was restricted to embryos from anaphase I through anaphase II because our streaming data and that of Kimura 2020 indicate that the sperm contents have not moved significantly before anaphase I." - This needs an appropriate citation. Page 10. 

We have inserted citations here.

" The simplest explanation is that cytoplasm does not mix during the 45 min from GVBD to pronucleus formation due to the high viscosity of cytoplasm." - Citation page 12. Not referencing figures in the discussion. 

We have changed the sentence to: “The simplest hypothesis is that maternal and paternal cytoplasm might not mix during the 45 min from GVBD to pronucleus formation due to the high viscosity of cytoplasm.” 

"The higher frequency of capture of the sperm DNA by the meiotic spindle in ATX-2 KLP-7 double depleted embryos compared with either single depletion suggests that the integrity of the exclusion zone around the sperm DNA may insulate the sperm DNA from spindle microtubule" - Pages 12-13 reference the figures. 

A reference to the revised Fig. 9 has been inserted in the revised version of this sentence.

"ATX-2 is required to maintain the integrity of the ball of paternal mitochondria around the sperm DNA, but the mechanism is unknown." 

References to Figs. 7 and 8 have been inserted.

Page 13 reference figure 

" In control embryos, the sperm contents rarely came near the meiotic spindle in agreement with a previous study that found that male and female pronuclei rarely form next to each other (6). Streaming of the sperm contents was most commonly restricted to a jostling motion with little net displacement, circular streaming in the short axis of the embryo, or long axis streaming in which the sperm turned away from the spindle before the halfway point of the embryo. Depletion of MEI-1 or KLP-7 resulted in longer excursions of the sperm contents in the long axis of the embryo toward the spindle but frequent capture of the sperm by the spindle was only observed in mei-1(RNAi)." Page 13, the corresponding figures need to be referenced for these sentences. 

We have inserted citations here.

"In capture events observed after double depletion of ATX-2 and KLP-7, a bundle of microtubules was discernible extending from the spindle into the ER envelope surrounding the sperm DNA. Such bundles were not observed in mei-1(RNAi) capture events, likely because of the previously reported low density of microtubules in mei-1(RNAi) spindles (36, 37)." Pages 13-14 references figures here. 

We have inserted citations here.

(5) Referencing wrong figures in the text: 

Figure 5 - In the figure legend there is a 5C but there is no 5C panel in the figure. 

A C has been inserted in Fig. 5.

Figure 6A - "Dark holes were observed suggesting exclusion from the lumens of larger membranous organelles (Fig. 6A; Fig. S2)." Page 10. 

6A has been changed to 6C.

Figure 6A is showing background autofluorescence in WT oocytes so I am not certain why it is cited here. 

The Figure citation has been corrected to 6B, C.

Figure 8 - I could not find the supplemental data file with the individual mitochondria distance measurements. 

We are including the Excel file with the revised submission.

The last sentence of the first paragraph should be re-worded to be more concise ". In C. elegans, the nucleus is positioned away from the site of future fertilization so that the meiosis I spindle assembles at the opposite end of the ellipsoid zygote from the site of fertilization (2-4). " 

Every word of this sentence is important.

Last sentence second paragraph typo "These microtubules are thought to drive meiotic cytoplasmic streaming because depletion tubulin stops cytoplasmic streaming (7) and depletion of the microtubule-severing protein katanin by RNAi results in an increased mass of cortical microtubules and an increase in cytoplasmic streaming (8)." Pages 3-4. 

“of” has been inserted.

(6) Typos in the introduction should be corrected: 

Ataxin or kinesin-13 are not mentioned in the introduction but these are a big focus of the paper. 

Gong et al 2024 written instead of number citation (page 5), no citation in References.

This has been corrected. 

Supplemental videos should be labeled appropriately to indicate what structures are labeled. It is currently difficult to understand what is being shown.

eLife assessment

This fundamental study provides a near-comprehensive anatomical description and annotation of neurons in a male Drosophila ventral nerve cord, based on large-scale circuit reconstruction from electron microscopy. This connectome resource will be of substantial interest to neuroscientists interested in sensorimotor control, neural development, and analysis of brain connectivity. However, although the evidence is extensive and compelling, the presentation of results in this very large manuscript lacks clarity and concision.

Reviewer #1 (Public Review):

Summary: The authors present a close to complete annotation of the male Drosophila ventral nerve cord, a critical part of the fly's central nervous system.

Strengths: The manuscript describes an enormous amount of work that takes the first steps towards presenting and comprehending the complexity and organization of the ventral nerve cord. The analysis is thorough and complete. It also makes the effort to connect this EM-centric view of the nervous system to more classical analyses, such as the previously defined hemilineages, that also describe the organization of the fly nervous system. There are many, many insights that come from this work that will be valuable to the field for the foreseeable future.

Weaknesses: With more than 60 primary figures, the paper is overwhelming and cannot be read and digested in a single sitting. The result is more like a detailed resource rather than a typical research paper.

Reviewer #2 (Public Review):

Summary and strengths:<br /> This massive paper describes the identity and connectivity of neurons reconstructed from a volumetric EM image volume of the ventral nerve cord (VNC) of a male fruit fly. The segmentation of the EM data was described in one companion paper; the classification of the neurons entering the VNC from the brain (descending neurons or DNs) and the motor neurons leaving the VNC was described in a second companion paper. Here, the authors describe a system for annotating the remaining neurons in the VNC, which include intrinsic neurons, ascending neurons, and sensory neurons, representing the vast majority of neurons in the dataset. Another fundamental contribution of this paper is the identification of the developmental origins (hemilineage) of each intrinsic neuron in the VNC. These comprehensive hemilineage annotations can be used to understand the relationship between development and circuit structure, provide insight into neurotransmitter identity, and facilitate comparisons across insect species.Many sensory neurons are also annotated by comparison to past literature. Overall, defining and applying this annotation system provides the field with a standard nomenclature and resource for future studies of VNC anatomy, connectivity, and development. This is a monumental effort that will fundamentally transform the field of Drosophila neuroscience and provide a roadmap for similar connectomic studies in other organisms.

Weaknesses:<br /> Despite the significant merit of these contributions, the manuscript is challenging to read and comprehend. In some places, it seems to be attempting to comprehensively document everything the authors found in this immense dataset. In other places, there are gaps in scholarship and analysis. As it is currently constructed, I worry that the manuscript will intimidate general readers looking for an entry point to the system, and ostracize specialized readers who are unable to use the paper as a comprehensive reference due to its confusing organization.

The bulk of the 559 pages of the submitted paper is taken up by a set of dashboard figures for each of ~40 hemilineages. Formatting the paper as an eLife publication will certainly help condense these supplemental figures into a more manageable format, but 68 primary figures will remain, and many of these also lack quality and clarity. Without articulating a clear function for each plot, it is hard to know what the authors missed or chose not to show. As an example, many of the axis labels indicate the hemilineage of a group of neurons, but are ordered haphazardly and so small as to be illegible; if the hemilineage name is too small, and in a bespoke order for that data, then is the reader meant to ignore the specific hemilineage labels?

The text has similar problems of emphasis. It is often meandering and repetitive. Overlapping information is found in multiple places, which causes the paper to be much longer than it needs to be. For example, the concept of hemilineages is introduced three times before the subtitle "Introduction to hemilineage-based organisation". When cell typing is introduced, it is unclear how this relates to serial motif, hemilineage, etc; "Secondary hemilineages" follow the Cell typing title. Like the overwhelming number of graphical elements, this gives the impression that little attention has been paid to curating and editing the text. It is unclear whether the authors intend for the paper to be read linearly or used as a reference. In addition, descriptions of the naming system are often followed by extensive caveats and exceptions, giving the impression that the system is not airtight and possibly fluid. At many points, the text vacillates between careful consideration of the dataset's limitations and overly grandiose claims. These presentation flaws overshadow the paper's fundamental contribution of describing a reasonable and useful cell-typing system and placing intrinsic neurons within this framework.

References to past Drosophila literature are inconsistent and references to work from other insects are generally not included; for example, the extensive past work on leg sensory neurons in locusts, cockroaches, and stick insects. Such omissions are understandable in a situation where brevity is paramount. However, this paper adopts a comprehensive and authoritative tone that gives the reader an impression of completeness that does not hold up under careful scrutiny.

The paper accompanies the release of the MANC dataset (EM images, segmentation, annotations) through a web browser-based tool: clio.janelia.org. The paper would be improved by distilling it down to its core elements, and then encouraging readers to explore the dataset through this interactive interface. Streamlining the paper by removing extraneous and incomplete analyses would provide the reader with a conceptual or practical framework on which to base their own queries of the connectome.

Author response:

eLife assessment

This fundamental study provides a near-comprehensive anatomical description and annotation of neurons in a male Drosophila ventral nerve cord, based on large-scale circuit reconstruction from electron microscopy. This connectome resource will be of substantial interest to neuroscientists interested in sensorimotor control, neural development, and analysis of brain connectivity. However, although the evidence is extensive and compelling, the presentation of results in this very large manuscript lacks clarity and concision.

We thank the reviewers for their detailed and thoughtful feedback and the time that they invested to provide it. Organising this manuscript (which is clearly not a standard research article) was quite challenging as it had to fulfil a number of functions: presenting a guide to the system of annotations and the associated online resources; providing an atlas for the annotated cell types; and showcasing various analyses to illustrate the value of the dataset as well as just a few of the many questions it can be used to address. We gave careful consideration to its structure and attempted to signpost the sections that would be most useful to particular types of readers. Nevertheless we can see that this was not completely successful and we thank the reviewers for their suggestions for improvement.

We acknowledge that the resulting manuscript was very large and will endeavour to streamline our text in the revision without compromising the accessibility of the data. We do note that there is some precedent for comprehensive and lengthy connectome papers going all the way back to White et al. 1986 which took 340 pages to describe the 302 neurons of the C. elegans connectome. More recently, we can compare the “hemibrain papers” published in eLife: Scheffer et al., 2020, Li et al., 2020, Schlegel et al., 2021, Hulse et al., 2021. These papers would also be difficult to digest at a single sitting but were game-changing for the Drosophila neuroscience field and have already been cited hundreds of times, a testament to their utility. In the same way that these papers provided the first comprehensively proofread and annotated EM connectome for (a large part of) the adult fly brain, our work now provides the first fully proofread and annotated EM connectome for the nerve cord. Given the pioneering nature of this dataset we feel that the lengthy but highly structured atlas sections of the paper are justified and will prove impactful in the long term.

Whilst no EM dataset is perfect, we have endeavoured to make this one as comprehensive as possible. We found 74.4 million postsynapses and 15,765 neurons of VNC origin, all of which have been carefully proofread, reviewed, annotated and typed. For comparison, the female adult nerve cord dataset (FANC, Azevedo et al., Nature, 2024) contains roughly 45 million synapses and 14,600 neuronal cell bodies of which at the time of writing 5576 have received preliminary proofreading and 222 high quality proofreading. We emphasise that these are highly complementary datasets, given the difference in sex and the fact that each dataset has different artefacts (MANC has poorer preservation of neurons in the leg nerves; FANC is missing part of the abdominal ganglion and has lower synapse recovery). We reconstructed 5484 sensory neurons from the thoracic nerves, 84% of the ~6500 estimated from FANC. The overall recovery rate was ~86.5% if we include the ~1100 sensory neurons from abdominal nerves, which were in excellent condition.

Reviewer #1 (Public Review):

Summary:

The authors present a close to complete annotation of the male Drosophila ventral nerve cord, a critical part of the fly's central nervous system.

Strengths:

The manuscript describes an enormous amount of work that takes the first steps towards presenting and comprehending the complexity and organization of the ventral nerve cord. The analysis is thorough and complete. It also makes the effort to connect this EM-centric view of the nervous system to more classical analyses, such as the previously defined hemilineages, that also describe the organization of the fly nervous system. There are many, many insights that come from this work that will be valuable to the field for the foreseeable future.

We thank the reviewer for acknowledging the enormous collaborative effort represented by this manuscript. We tried to synthesise decades of light-level work by neuroscientists and developmental biologists working in Drosophila and other insects in order to create a standard, systematic nomenclature for >22,000 neurons, most of which had not been typed at light level. We hope that the MANC dataset and this guide to its contents will prove to be useful resources to Drosophila neurobiologists and the wider neuroscience field.

Weaknesses:

With more than 60 primary figures, the paper is overwhelming and cannot be read and digested in a single sitting. The result is more like a detailed resource rather than a typical research paper.

In writing this paper, we had two aims: first, to describe and validate our extensive biological annotation of the connectome and second, to provide interesting illustrative examples of the many analyses that could be carried out on this dataset using the atlas we generated. The resulting paper is intended primarily as a detailed reference rather than a typical research paper. At the end of the Introduction, we outline the structure of the paper and explicitly direct non-specialist readers to focus on the initial and concluding sections for orientation to the dataset so that they would not get bogged down in the details. We will review our section organisation and headings to try to make the paper more straightforward to navigate, and we will add specific figure numbers to the outline.

Reviewer #2 (Public Review):

Summary and strengths:

This massive paper describes the identity and connectivity of neurons reconstructed from a volumetric EM image volume of the ventral nerve cord (VNC) of a male fruit fly. The segmentation of the EM data was described in one companion paper; the classification of the neurons entering the VNC from the brain (descending neurons or DNs) and the motor neurons leaving the VNC was described in a second companion paper. Here, the authors describe a system for annotating the remaining neurons in the VNC, which include intrinsic neurons, ascending neurons, and sensory neurons, representing the vast majority of neurons in the dataset. Another fundamental contribution of this paper is the identification of the developmental origins (hemilineage) of each intrinsic neuron in the VNC. These comprehensive hemilineage annotations can be used to understand the relationship between development and circuit structure, provide insight into neurotransmitter identity, and facilitate comparisons across insect species.Many sensory neurons are also annotated by comparison to past literature. Overall, defining and applying this annotation system provides the field with a standard nomenclature and resource for future studies of VNC anatomy, connectivity, and development. This is a monumental effort that will fundamentally transform the field of Drosophila neuroscience and provide a roadmap for similar connectomic studies in other organisms.

We thank the reviewer for acknowledging the enormous collaborative effort represented by this manuscript. We tried to synthesise decades of light-level work by neuroscientists and developmental biologists working in Drosophila and other insects in order to create a standard, systematic nomenclature for >22,000 neurons, most of which had not been typed at light level. We hope that the MANC dataset and this guide to its contents will prove to be useful resources to Drosophila neurobiologists and the wider neuroscience field.

Weaknesses:

Despite the significant merit of these contributions, the manuscript is challenging to read and comprehend. In some places, it seems to be attempting to comprehensively document everything the authors found in this immense dataset. In other places, there are gaps in scholarship and analysis. As it is currently constructed, I worry that the manuscript will intimidate general readers looking for an entry point to the system, and ostracize specialized readers who are unable to use the paper as a comprehensive reference due to its confusing organization.

In writing this paper, we had two aims: first, to describe and validate our extensive biological annotation of the connectome and second, to provide interesting illustrative examples of the many analyses that could be carried out on this dataset using the atlas we generated. The resulting paper is intended primarily as a detailed reference rather than a typical research paper. At the end of the Introduction, we outline the structure of the paper and explicitly direct non-specialist readers to focus on the initial and concluding sections for orientation to the dataset so that they would not get bogged down in the details. We will review our section organisation and headings to try to make the paper more straightforward to navigate, and we will add specific figure numbers to the outline.

The bulk of the 559 pages of the submitted paper is taken up by a set of dashboard figures for each of ~40 hemilineages. Formatting the paper as an eLife publication will certainly help condense these supplemental figures into a more manageable format, but 68 primary figures will remain, and many of these also lack quality and clarity. Without articulating a clear function for each plot, it is hard to know what the authors missed or chose not to show. As an example, many of the axis labels indicate the hemilineage of a group of neurons, but are ordered haphazardly and so small as to be illegible; if the hemilineage name is too small, and in a bespoke order for that data, then is the reader meant to ignore the specific hemilineage labels?

We will contact eLife professional editing staff to determine whether the paper can be streamlined by moving more material to supplemental without making it difficult to locate the detailed catalogues of neurons that will be of interest to specialist readers. Based on the typical eLife format, we suspect that retaining the dashboard main figures for each hemilineage will be necessary to maintain its utility as a reference. We will, however, shorten the associated main text by, for example, moving background material used to assign the hemilineages to the Methods section and moving specific results to the figure legends where possible.

We articulated the function for each plot as follows: "Below we describe in more depth every hemilineage that produces more than one or two secondary neurons. For each of these 35 hemilineages, we show (A) the overall morphology of the secondary population, (B) representative individual neurons (as estimated by highest average NBLAST score to other members of the hemilineage), and (C) specific notable examples (which in some cases are primary). We then report (D) the locations of their connectors (postsynapses and presynapses), (E) their upstream and downstream partners by class, and (F) their upstream and downstream partners by finer subdivisions corresponding to their systematic types (secondary hemilineage, target, or sensory modality). We also provide supplementary figures showing the morphology and normalised up- and downstream connectivity of all systematic types for each hemilineage."

We have plotted every secondary neuron in each hemilineage, every predicted synapse for those neurons with confidence >0.5, every connection to partner neurons by class (no threshold applied), and then the same information organised by hemilineage in a heatmap (and including partners from all birthtimes and partners of unknown hemilineage). Then the supplementary figures show all connectivity, organised in the same way, for every individual cell type assigned to the hemilineage, including both primary and early secondary neurons. We will add more detail to the figure legends to clarify these points.

We apologise that you were unable to read some of the axis labels in the review copy of the manuscript; we did submit high resolution versions of the figures as a supplemental file, but perhaps this did not reach you; they can also be found at https://www.biorxiv.org/content/10.1101/2023.06.05.543407v2.supplementary-material. The hemilineages are in a conserved (alphanumerical) order for all hemilineage-specific plots and many others. The exceptions arise when neurons are clustered based on their connectivity to hemilineages, in which case the order of the labels necessarily follows the structure of the resulting clusters.

The text has similar problems of emphasis. It is often meandering and repetitive. Overlapping information is found in multiple places, which causes the paper to be much longer than it needs to be. For example, the concept of hemilineages is introduced three times before the subtitle "Introduction to hemilineage-based organisation". When cell typing is introduced, it is unclear how this relates to serial motif, hemilineage, etc; "Secondary hemilineages" follow the Cell typing title. Like the overwhelming number of graphical elements, this gives the impression that little attention has been paid to curating and editing the text. It is unclear whether the authors intend for the paper to be read linearly or used as a reference. In addition, descriptions of the naming system are often followed by extensive caveats and exceptions, giving the impression that the system is not airtight and possibly fluid. At many points, the text vacillates between careful consideration of the dataset's limitations and overly grandiose claims. These presentation flaws overshadow the paper's fundamental contribution of describing a reasonable and useful cell-typing system and placing intrinsic neurons within this framework.

Because we intended this paper to be read primarily as a reference, we tried to make each section stand on its own, which we agree resulted in some redundancy (with more details appearing where relevant). However, we will do our best to tighten the text for the version of record.

Our description immediately under the Cell typing title includes the use of hemilineage, serial (not serial motif, which was not used), and laterality (left-right homologues) in the procedure to assign cell types. We will change this to “Cell typing of intrinsic, ascending, and efferent neurons” for clarity. The “Secondary hemilineages” title marks the start of a new section that serves as a reference for each of the secondary hemilineages; we will change this to “Secondary hemilineage catalogue” or similar for clarity.

References to past Drosophila literature are inconsistent and references to work from other insects are generally not included; for example, the extensive past work on leg sensory neurons in locusts, cockroaches, and stick insects. Such omissions are understandable in a situation where brevity is paramount. However, this paper adopts a comprehensive and authoritative tone that gives the reader an impression of completeness that does not hold up under careful scrutiny.

We did not attempt to review the sensory neuron literature in this manuscript but rather cited those specific papers which included the axon morphology data that informed our modality, peripheral origin, and cell type assignments. Most of these came from the Drosophila literature due to the availability of genetic tools used for sparse labelling of specific populations as well as the greatly increased likelihood of conserved morphology. However we certainly agree that decades of sensory neuron work in larger insects were foundational for this subfield and will add a sentence to this effect in the introduction to our sensory neuron typing.

The paper accompanies the release of the MANC dataset (EM images, segmentation, annotations) through a web browser-based tool: clio.janelia.org. The paper would be improved by distilling it down to its core elements, and then encouraging readers to explore the dataset through this interactive interface. Streamlining the paper by removing extraneous and incomplete analyses would provide the reader with a conceptual or practical framework on which to base their own queries of the connectome.

We certainly hope that this paper will encourage readers to explore the MANC dataset. Indeed, as we state in the Discussion, "Moreover, its ultimate utility depends on how widely it is leveraged in the future experimental and computational work of the entire neuroscience community. We have only revealed the tip of the iceberg in this report, with a wealth of opportunities now available in this publicly available dataset for forthcoming connectomic analyses that will feed into testable functional hypotheses." In the first few sections of the Results, we include a visual introduction to annotated features, a glossary of annotation terms, a visual guide to our cell typing nomenclature, and two video tutorials on the use of Clio Neuroglancer to query the dataset. To further encourage exploration, we have also included illustrative examples of just a few of the many analyses that can now be performed with this comprehensive and publicly available dataset.

Reviewer #2 (Public Review):

Summary:<br /> The authors used four datasets spanning 30 countries to examine funding success and research quality score for various disciplines. They examined whether funding or research quality score were influenced by majority gender of the discipline and whether these affected men, women, or both within each discipline. They found that disciplines dominated by women have lower funding success and research quality score than disciplines dominated by men. These findings are surprising because even the men in women-dominated fields experienced lower funding success and research quality score.

Strengths:<br /> - The authors utilized a comprehensive dataset covering 30 countries to explore the influence of the majority gender in academic disciplines on funding success and research quality scores.<br /> - Findings suggest a systemic issue where disciplines with a higher proportion of women have lower evaluations and funding success for all researchers, regardless of gender.<br /> - The manuscript is notable for its large sample size and the diverse international scope, enhancing the generalizability of the results.<br /> - The work accounts for various factors including age, number of research outputs, and bibliometric measures, strengthening the validity of the findings.<br /> - The manuscript raises important questions about unconscious bias in research evaluation and funding decisions, as evidenced by lower scores in women-dominated fields even for researchers that are men.<br /> - The study provides a nuanced view of gender bias, showing that it is not limited to individuals but extends to entire disciplines, impacting the perception and funding and quality or worth of research.<br /> - This work underscores the need to explore motivations behind gender distribution across fields, hinting at deep-rooted societal and institutional barriers.<br /> - The authors have opened a discussion on potential solutions to counter bias, like adjusting funding paylines or anonymizing applications, or other practical solutions.<br /> - While pointing out limitations such as the absence of data from major research-producing countries, the manuscript paves the way for future studies to examine whether its findings are universally applicable.<br /> - The study carefully uses the existing data (including PBRF funding panel gender diversity) to examine gender bias. These types of datasets are often not readily accessible for analysis. Here, the authors have used the available data to the fullest extent possible.

The authors have addressed the concerns I had about the original version.

Author response:

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

Public Reviews:

Reviewer #2 (Public Review):

Summary:

The authors used four datasets spanning 30 countries to examine funding success and research quality score for various disciplines. They examined whether funding or research quality score were influenced by majority gender of the discipline and whether these affected men, women, or both within each discipline. They found that disciplines dominated by women have lower funding success and research quality score than disciplines dominated by men. These findings, are surprising because even the men in women-dominated fields experienced lower funding success and research quality score.

Strengths:

- The authors utilized a comprehensive dataset covering 30 countries to explore the influence of the majority gender in academic disciplines on funding success and research quality scores.

- Findings suggest a systemic issue where disciplines with a higher proportion of women have lower evaluations and funding success for all researchers, regardless of gender.

- The manuscript is notable for its large sample size and the diverse international scope, enhancing the generalizability of the results.

- The work accounts for various factors including age, number of research outputs, and bibliometric measures, strengthening the validity of the findings.

- The manuscript raises important questions about unconscious bias in research evaluation and funding decisions, as evidenced by lower scores in women-dominated fields even for researchers that are men.

- The study provides a nuanced view of gender bias, showing that it is not limited to individuals but extends to entire disciplines, impacting the perception and funding and quality or worth of research.

- This work underscores the need to explore motivations behind gender distribution across fields, hinting at deep-rooted societal and institutional barriers.

- The authors have opened a discussion on potential solutions to counter bias, like adjusting funding paylines or anonymizing applications, or other practical solutions.

- While pointing out limitations such as the absence of data from major research-producing countries, the manuscript paves the way for future studies to examine whether its findings are universally applicable.

Weaknesses:

- The study does not provide data on the gender of grant reviewers or stakeholders, which could be critical for understanding potential unconscious bias in funding decisions. These data are likely not available; however, this could be discussed. Are grant reviewers in fields dominated by women more likely to be women?

- There could be more exploration into whether the research quality score is influenced by inherent biases towards disciplines themselves, rather than only being gender bias.

- The manuscript should discuss how non-binary gender identities were addressed in the research. There is an opportunity to understand the impact on this group.

- A significant limitation is absence of data from other major research-producing countries like China and the United States, raising questions about the generalizability of the findings. How comparable are the findings observed to these other countries?

- The motivations and barriers that drive gender distribution in various fields could be expanded on. Are fields striving to reach gender parity through hiring or other mechanisms?

- The authors could consider if the size of funding awards correlates with research scores, potentially overlooking a significant factor in the evaluation of research quality. Presumably there is less data on smaller 'pilot' funds and startup funds for disciplines where these are more common. Would funding success follow the same trend for these types of funds?

- The language used in the manuscript at times may perpetuate bias, particularly when discussing "lower quality disciplines," which could influence the reader's perception of certain fields.

- The manuscript does not clarify how many gender identities were represented in the datasets or how gender identity was determined, potentially conflating gender identity with biological sex.

Reviewer #3 (Public Review):

This study seeks to investigate one aspect of disparity in academia: how gender balance in a discipline is valued in terms of evaluated research quality score and funding success. This is important in understanding disparities within academia.

This study uses publicly available data to investigate covariation between gender balance in an academic discipline and:

i) Individual research quality scores of New Zealand academics as evaluated by one of 14 broader subject panels.

ii) Funding success in Australia, Canada, Europe, UK.

The study would benefit from further discussion of it limitations, and from the clarification of some technical points (as described in the recommendations for the authors).

Recommendations For The Authors:

Reviewer #2 (Recommendations For The Authors):

This is a very nice study as-is. In the following comments, I have mainly put my thoughts as I was reading the manuscript. If there are practical ways to answer my questions, I think they could improve the manuscript but the data required for this may not be available.

Are there any data on the gender of grant reviewers or stakeholders who make funding decisions?

The research quality score metrics seem to be more related to unconscious bias. The funding metrics may also, but there are potentially simple fixes (higher paylines for women or remove gender identities from applications).

We have included some details about PBRF funding panel gender diversity. These panels are usually more gender balanced than the field they represent, but in the extreme cases (Engineering, Education, Mathematics) they are skewed as would be expected. Panels for other award decision makers was not available.

I wonder if the research score metric isn't necessarily reflecting on the gender bias in the discipline but rather on the discipline itself? Terms like "hard science" and "soft science" are frequently used and may perpetuate these biases. This is somewhat supported by the data - on line 402-403 the authors state that women in male-dominated fields like Physics have the same expected score as a man. Could it be that Physics has a higher score than Education even if Physics was woman-dominated and Education was man-dominated? Are there any instances in the data where traditionally male- or female-dominated disciplines are outliers and happen to be the opposite? If so, in those cases, do the findings hold up?

Overall we would love to answer this question! But our data is not enough. We mention these points in the Discussion (Lines 472-466). We have extended this a little to cover the questions raised here.

How are those with non-binary gender identities handled in this article? If there is any data on the subject, I would be curious to know how this effects research score and funding success.

These data were either unavailable or the sample size was too small to be considered anonymously (Mentioned on Lines 74-76).

A limitation of the present article is a lack of data on major research-producing countries like China and the United States. Is there any data relevant to these or other countries? Is there reason to believe the findings outlined in this manuscript would apply or not apply to those countries also?

We would be very excited to see if the findings held up in other countries, particularly any that were less European based. Unfortunately we could not find any data to include. Maybe one day!

What are the motivations or other factors driving men to certain fields and women to certain fields over others? What are the active barriers preventing all fields from 50% gender parity?

Field choice is a highly studied area and the explanations are myriad we have included a few references in the discussion section on job choice. I usually recommend my students read the blog post at

https://www.scientificamerican.com/blog/hot-planet/the-people-who-could-have-done-science-didnt/

It is very thoughtful but unfortunately not appropriate to reference here.

The authors find very interesting data on funding rates. Have you considered funding rates and the size of funding awards as a factor in research score? Some disciplines like biomedical science receive larger grants than others like education.

A very interesting thought for our next piece of work. We would definitely like to explore our hypothesis further.

There are instances where the authors writing may perpetuate bias. If possible these should be avoided. One example is on line 458-459 where the authors state "...why these lower quality disciplines are more likely..." This could be re-written to emphasize that some disciplines are "perceived" as lower quality. Certainly those in these discipline would not characterize their chosen discipline as "low quality".

Well-spotted! Now corrected as you suggest.

Similar to the preceding comment, the authors should use care with the term "gender". In the datasets used, how many gender identities were captured? How many gender identity options were given in the surveys or data intake forms? Could individuals in these datasets have been misgendered? Do the data truly represent gender identity or biological sex?

We know that in the PBRF dataset gender was a binary choice and transgender individuals were able to choose which group they identified with. There was no non-binary option (in defence the latest dataset there is from 2018 and NZ has only recently started updating official forms to be more inclusive) and individuals with gender not-stated (a very small number) were excluded. ARC did mention that a small number of individuals were either non-binary or gender not stated, again these are not included here for reasons of anonymity. This is now mentioned on Lines 74-76. The effects on this group are important and understudied likely because, as here, the numbers are too small to be included meaningfully.

Reviewer #3 (Recommendations For The Authors):

Major revisions:

Could you add line numbers to the Supplementary Materials for the next submission?

Yes! Sorry for the omission.

(1) In the main text L146 and Figure 1, it is not clear why the expected model output line is for a 50 year old male from University of Canterbury only, but the data points are from disciplines in all eight universities in New Zealand. I think it would be more clear and informative to report the trend lines that represent the data points. At the moment it is hard to visualise how the results apply to other age groups or universities.

As age and institution are linear variables with no interactions they are only a constant adjustment above or below this line and the adjustment is small in comparison to the linear trend. Unfortunately, if they were included graphically they do not aid understanding. We agree that indluded raw data with an adjusted trend line can be confusing buy after a lor of between-author discussion this was the most informative compromise we could find (many people like raw data so we included it).

(2) Does your logistic regression model consider sample size weighting in pmen? Weighting according to sample sizes needs to be considered in your model. At the moment it is unclear and suggests a proportion between 0 and 1 only is used, with no weighting according to sample size. If using R, you can use glm(cbind(nFem, nMalFem).

Yes. All data points were weighted by group size exactly as you suggest. We have updated the text on Lines 317 to make this clear.

(3) For PBRF, I think it is useful to outline the 14 assessment panels and the disciplines they consider. Did you include the assessment panel as an explanatory variable in your model too to investigate whether quality is assessed in the same manner between panels? If not, then suggest reasons for not doing so.

We have now included more detail in main text on the gender split of the panels. They were not included as an explanatory variable. In theory there was some cross-referencing of panel scores to ensure consistency as part of the PBRF quality assurance guidelines.

(4) There are several limitations which should be discussed more openly:

Patterns only represent the countries studied, not necessarily academia worldwide.

Mentioned on Line 485-487.

Gender is described as a binary variable.

Discussed on Line 74-76.

The measure of research evaluation as a reflection of academic merit.

This is acknowledged in the data limitations paragraph in the discussion, at the end of the discussion

Minor revisions:

(1) L186. Why do you analyse bibliometric differences between individuals from University of Canterbury only? It would be helpful to outline your reasons.

Although bibliometric data is publicly available it is difficult to collect for a large number of individuals. You also need some private data to match bibliometrics with PBRF data which is anonymous. We were only able to do this for our own institution with considerable internal support.

(2) How many data records did you have to exclude in L191 because they could not be linked? This is helpful to know how efficient the process was, should anyone else like to conduct similar studies.

We matched over 80% of available records (384 individuals). We have mentioned this on Line 194.

(3) Check grammar in the sentence beginning in L202.

Thank-you. Corrected.

(4) Please provide a sample size gender breakdown for "University of Canterbury (UC) bibliometric data", as you do for the preceding section. A table format is helpful.

Included on Line 194.

(5) L377 I think this sentence needs revision.

Thank you, we have reworked that paragraph.

(6) L389-392 Is it possible evaluation panels can score women worse than men and that because more women are present in female-biassed disciplines, the research score in these are worse? Women scoring worse between fields, may be a result of some scaling to the mean score.

No.  This is not possible because women in male-dominated fields score higher.

(7) L393 Could you discuss explanations for why men outperform women in research evaluation scores more when disciplines are female dominated?

Unfortunately, we don’t have an explanation for this and can’t get one from our data. We hope it will be an interesting for future work.

(8) Could the figures be improved by having the crosses, x and + scaled, for example, in thickness corresponding to sample size? Alternatively, some description of the sample size variation? Sorting the rows by order of pmen in Table E1 would also be helpful for the reader.

As with the previous figure we have tried many ways of presenting it (including tis one). Unfortunately nothing helped.

We have provided Table E1 as a spreadsheet to allow readers to do this themselves.

(9) Please state in your methods section the software used to aid repeatability.

This is now in Supplementary Materials (Matlab 2022b).

(10) It is great to report your model findings into real terms for PBRF and ARC. Please can you extend this to CIHR and EIGE. i.e. describing how a gender skew increase of x associates with a y increase in funding success chance.

We have added similar explanations for both these datasets comparing the advantage of being male with the advantage of working in a male dominated discipline.

(11) I would apply care to using pronouns "his" and "her" in L322-L324 and avoid if at all possible, instead, replacing them with "men" and "women".

We have updated the text to avoid there pronouns in most places.

The article in general would benefit from a disclosure statement early on conceding that gender investigated here is only as a binary variable, discounting its spectrum.

See Line 74-76.

Please also report how gender balance is defined in the datasets as in the data summary in supplementary materials, within the main text.

Our definition of gender balance (proportion of researchers who are men, ) is given on Line 103.

(12) The data summary Table S1 could benefit from explaining the variables in the first column. It is currently unclear how granularity, size of dataset and quotas/pre-allocation? are defined.

These lines have been removed as they information they contained is included elsewhere in the table with far better explanations!

(13) There are only 4 data points for investigating covariation between gender balance and funding success in CIHR. This should be discussed as a limitation.

The small size of the dataset is now mentioned on Line 348.

(14) L455 "Research varies widely across disciplines" in terms of what?

This sentence has been extended

.

(15) L456 Maybe I am missing something but I don't understand the relevance of "Physicists' search for the grand unified theory" to research quality.

Removed.

(16) Can you provide more discussion into the results of your bibliographic analysis and Figure 2? An explanation into the relationships seen in the figure at least would be helpful.

Thank you we have clarified the relationships seen in each of figures 2A (Lines 226-235), 2B (Lines 236-252), and 2C (lines  260-268).

(17) It would be helpful to include in the discussion a few more sentences outlining:

- Potential future research that would help disentangle mechanisms behind the trends you find.

- How this research could be applied. Should there be some effort to standardise?

We have added a short paragraph to the discussion about implications/applications, and future research (Lines 481-484).

(18) The introduction could benefit from discussing and explaining their a priori hypotheses for how research from female-biassed disciplines may be evaluated differently.

While not discussed in the introduction, possible explanations for why and how research in female dominated fields might be evaluated differently are explored in some detail in the Discussion.  We think once is enough, and towards the end is more effective than at the beginning.

(19) L16 "Our work builds on others' findings that women's work is valued less, regardless of who performs that work." I find this confusing because in your model, there is a significant interaction effect between gender:pmen. This suggests that for female-biassed disciplines, there is even more of a devaluation for women, which I think your lines in figure 1 suggest.

Correct but men are still affected, so the sentence is correct.  What is confusing is that the finding is counter to what we might expect.

eLife Assessment

This study provides convincing evidence that the quality of research in female-dominated fields of research is systematically undervalued by the research community. The authors' findings are based on analyses of data from a research assessment exercise in New Zealand and data on funding success rates in Australia, Canada, the European Union and the United Kingdom. This work is an important contribution to the discourse on gender biases in academia, underlining the pervasive influence of gender on whole fields of research, as well as on individual researchers.

Reviewer #3 (Public Review):<br /> This study seeks to investigate one aspect of disparity in academia: how gender balance in a discipline is valued in terms of evaluated research quality score and funding success. This is important in understanding disparities within academia.<br /> This study uses publicly available data to investigate covariation between gender balance in an academic discipline and:<br /> individual research quality scores of New Zealand academics as evaluated by one of 14 broader subject panels.<br /> [ii] funding success in Australia, Canada, Europe, UK.

The authors have addressed the concerns I had about the original version

eLife assessment

This study presents a valuable development of endometrial organoid culture methodology that mimics the window of implantation. Functional validation to demonstrate its robustness is lacking; therefore, the study is considered incomplete. The data may be interesting to embryologists and investigators working on reproductive biology and medicine.

Reviewer #1 (Public Review):

This study generated 3D cell constructs from endometrial cell mixtures that were seeded in the Matrigel scaffold. The cell assemblies were treated with hormones to induce a "window of implantation" (WOI) state.

The authors did their best to revise their study according to the reviewers' comments. However, the study remains unconvincing and at the same time too dense and not focused enough.

(1) The use of the term organoids is still confusing and should be avoided. Organoids are epithelial tissue-resembling structures. Hence, the multiple-cell aggregates developed here are rather "co-culture models" (or "assembloids"). It is still unexpected (unlikely) that these structures containing epithelial, stromal and immune cells can be robustly passaged in the epithelial growth conditions used. All other research groups developing real organoids from endometrium have shown that only the epithelial compartment remains in culture at passaging (while the stromal compartment is lost). If authors keep to their idea, they should perform scRNA-seq on both early and late (passage 6-10) "organoids". And they should provide details of culturing/passaging/plating etc that are different with other groups and might explain why they keep stromal and immune cells in their culture for such a long time. In other words, they should then in detail compare their method to the standard method of all other researchers in the field, and show the differences in survival and growth of the stromal and immune cells.<br /> (2) The paper is still much too dense, touching upon all kind of conclusions from the manifold bioinformatic analyses. The latter should be much clearer and better described, and then some interesting findings (pathways/genes) should be highlighted without mentioning every single aspect that is observed. The paper needs a lot of editing to better focus and extract take-home messages, not bombing the reader with a mass of pathways, genes etc which makes the manuscript just not readable or 'digest-able'. There is no explanation whatever and no clear rationale why certain genes are included in a list while others are not. There is the impression that mass bioinformatics is applied without enough focus.<br /> (3) The study is much too descriptive and does not show functional validation or exploration (except glycogen production). Some interesting findings extracted from the bioinformatics must be functionally tested.<br /> (4) In contrast to what was found in vivo (Wang et al. 2020), no abrupt change in gene expression pattern is mentioned here from the (early-)secretory to the WoI phase. Should be discussed. Although the bioinformatic analyses point into this direction, there are major concerns which must be solved before the study can provide the needed reliability and credibility for revision.<br /> (5) All data should be benchmarked to the Wang et al 2020 and Garcia-Alonso et al. 2021 papers reporting very detailed scRNA-seq data, and not only the Stephen R. Quake 2020 paper.<br /> (6) Fig. 2B: Vimentin staining is not at all clear. F-actin could be used to show the typical morphology of the stromal cells?<br /> (7) Where does the term "EMT-derived stromal cells" come from? On what basis has this term been coined?<br /> (8) CD44 is shown in Fig. 2D but the text mentions CD45 (line 159)?<br /> (9) All quantification experiments (of stainings etc) should be in detail described how this was done. It looks very difficult (almost not feasible) when looking at the provided pictures to count the stained cells.<br /> (10) Fig. 3C: it is unclear how quantification can be reliably done. Moreover, OLFM4 looks positive in all cells of Ctrl, but authors still see an increase?<br /> (11) Fig. 3F: Met is downregulated which is not in accordance with the mentioned activation of the PI3K-AKT pathway.<br /> (12) Lines 222-226: transcriptome and proteome differences are not significant; so, how meaningful are the results then? Then, it is very hard to conclude an evolution from secretory phase to WoI.<br /> (13) WoI organoids show an increased number of cilia. However, some literature shows the opposite, i.e. less ciliated cells in the endometrial lining at WoI (to keep the embryo in place). How to reconcile?<br /> (14) How are pinopodes distinguished from microvilli? Moreover, Fig. 3 does not show the typical EM structure of cilia.<br /> (15) There is a recently published paper demonstrating another model for implantation. This paper should be referenced as well (Shibata et al. Science Advances, 2024).<br /> (16) Line 78: two groups were the first here (Turco and Borreto) and should both be mentioned.<br /> (17) Line 554: "as an alternative platform" - alternative to what? Authors answer reviewers' comments by just changing one word, but this makes the text odd.

Reviewer #2 (Public Review):

In this research, Zhang et al. have pioneered the creation of an advanced organoid culture designed to emulate the intricate characteristics of endometrial tissue during the crucial Window of Implantation (WOI) phase. Their method involves the incorporation of three distinct hormones into the organoid culture, coupled with additives that replicate the dynamics of the menstrual cycle. Through a series of assays, they underscore the striking parallels between the endometrial tissue present during the WOI and their crafted organoids. Through a comparative analysis involving historical endometrial tissue data and control organoids, they establish a system that exhibits a capacity to simulate the intricate nuances of the WOI.

The authors made a commendable effort to address the majority of the statements. Developing an endometrial organoid culture methodology that mimics the window of implantation is a game-changer for studying the implantation process. However, the authors should strive to enhance the results to demonstrate how different WOI organoids are from SEC organoids, ensuring whether they are worth using in implantation studies, or a proper demonstration using implantation experiments.

Author response:

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

Reviewer #1 (Public Review): 

Q1: First of all, the term organoid must be discarded. The authors just seed the endometrial cell mixture which assembles and aggregates into a 3D structure which is then immediately used for analysis. Organoids grow from tissue stem cells and must be passage-able (see their own description in lines 69-71). So, the term organoid must be removed everywhere, to not confuse the organoid field. It is not shown that the whole 3D assembly is passageable, which would be very surprising given the fact that immune and stromal cells do not grow in Matrigel because of the unfavorable growing conditions (which are targeted to epithelial cell growth).

We appreciate for your highlighting concerns regarding our organoid construction.

(1) The organoids in our system were originated from tissue stem cells.

We induced adult stem cells derived from endometrial tissue to construct organoids in vitro by various small molecules (such as Noggin, EGF, FGF2, WNT-3A and R-Spondin1), which involves a complex self-assembly process rather than a mere cellular assembly. Initially, there are single cells and small cell clusters in the system two days after the planting. On the fourth day, the glandular epithelial cells gradually assembled to glands, while the stromal cells spontaneously organized themselves around the glands.  On the eleventh day, the endometrial glands enlarged, epithelial cells organized in a paving stone arrangement, and stromal cells established an extensive network. (Author response image1) (Figure 1C)

(2) The organoids we constructed are passage-able.  

Most organoids were used for experiments up to the fifth generation, while some are extended to the 10th generation and cryopreserved. (Response Figure 1B, C)

(3) Immune and stromal cells are present in our system from the primary to the fourth generation. In our study, immune and stromal cells were identified not only from scRNA-seq data (third generation of organoids) (Figure 2A), but also from the morphology using 3D transparent staining and light sheet microscopy imaging (third generation of organoids), with Vimentin marking stromal cells, CD45 designating immune cells, and FOXA2 identifying glands. Further, flow cytometric analysis was applied to verify immune cells within the organoids (third generation of organoids). (Response Figure 1D, E, F)  

Moreover, Immune cells and stromal cells can grow in Matrigel, which was also found in the study of organoid pioneer Hans Clevers (Hans Clevers et al., Nature Reviews Immunology 2019).

Author response image 1.

(A) The growth condition of endometrial cells was observed from day2 to day11 after plating under an inverted microscope. Scale bar = 200 μm. (B) The endometrial organoids of different passages were observed from P1 to P5. Scale bar = 200 μm. (C) Stromal cells formed an extensive network (down). The arrowhead indicates dendritic stromal cells. Scale bar = 100 μm (left), Scale bar = 50 μm (right). (D) Exhibition of stromal cells marked by vimentin. Nuclei were counterstained with DAPI. The arrow indicates stromal cells. Scale bar = 40 μm (up), Scale bar = 30 μm (down). (E)Exhibition of immune cells marked by CD45 and endometrial gland marked by FOXA2. Nuclei were counterstained with DAPI. The arrow indicates immune cells. Scale bar = 50 μm. (F) Flow cytometric analysis of T cells and macrophages in the endometrial organoid. Gating strategy used for determining white blood cells (CD45+ cells), T cells (CD45+CD3+ cells) and macrophages (CD45+CD68+CD11b+ cells).

Q2: Second, the study remains fully descriptive, bombing the reader with a mass of bioinformatic analyses without clear descriptions and take-home messages. The paper is very dense, meaning readers may give up. Moreover, functional validation, except for morphological and immunostaining analyses (which are posed as "functional" but actually are only again expression) is missing, such as in vivo functionality (after transplantation e.g.) and embryo interaction. Importantly, the 3D structure misses the right architecture with a lining luminal epithelium which is present in the receptive endometrium in vivo and needed as the first contact site with the embryo. So, in contrast to what the authors claim, this is not the best model to study embryo interaction, or the closest model to the in vivo state (line 318, line 326).

Thank you.

(1) We have made the following improvements. Firstly, we have conducted additional experiments to validate the bioinformatics analysis. Secondly, the structure of the manuscript has been refined to ensure logical coherence and clear transitions between paragraphs. Thirdly, important findings have been emphasized to ensure readers’ comprehension and inspiration. Furthermore, the manuscript was revised by both domestic and international experts to enhance the readability and clarity.

(2)  For the functional validation, in vivo transfer could not be carried out so far due to ethical limitation. But human embryos are able to develop and grow more efficiently in combining with the receptive endometrial organoids we generated (unpublished data).

(3) As you suggested, we replaced the “closest” with “closer”. It is undeniable that the model cannot completely simulate the in vivo implantation process that the luminal epithelium of the endometrium contacts the embryo first.  

Q3: Third, receptive endometrial organoids (assembloids; Rawlings et al., eLife 2021) and receptive organoid-derived "open-faced endometrial layer" (Kagawa et al., Nature 2022) have already been described, which is in contrast to what the authors claim in several places that "they are the first" (e.g. lines 87-88, 316-319, etc). These studies used real organoids to achieve their model (and even showed embryo interaction), while in the present study, different cell types are just seeded and assembled. Hence, logically, immune cells are present which are never found in real organoid models. The only original aspect in the present study is the use of hormones to enhance the WOI phenotype. However, crucial information on this original aspect is missing such as concentration of the hormones, refreshment schedule, all 3 hormones added together or separately, and all 3 required?

Thank you for pointing out these researches referring to endometrial organoids.

(1) While we didn’t explicitly state "the first", we should be careful to use the expressions similar to "the first". It has been changed to a gentle and modest expression, as follows “we are far from understanding how embryo implantation occurs during the WOI due to ethical limitations and fewer in vitro receptive endometrial model” and “which confirms that they are closer to the in vivo state”.

(2) The definition of organoids and the existence of immune cells have been detailed addressed in the first question.

(3) In terms of hormone scheme, hormone concentrations have been detailed in Table S2 of Supplementary. Estrogen was supplemented to the basal medium for the initial two days, after which a combination treatment of MPA, cAMP, PRL, hPL, and HCG was administered for the subsequent six days. The medium was refreshed every two days.

All three hormones were deemed necessary, which was validated by multiple group comparisons. Only the organoids treated with all six hormones together exhibited an endometrial receptivityrelated gene expression profile. (Author response image 2).

Author response image 2.

Heatmap showing receptivity related gene expression profile of organoids in each hormone regimen.  

Q4: Moreover, it is not a "robust" model at all as the authors claim, given the variability of the initial cell mixture (varying from patient to patient). Actually, the reproducibility is not shown. The proportions of the different cell types seeded in the Matrigel droplet will be different with every endometrial biopsy. It would be much better to recombine epithelial (passageable) organoids with stromal and immune cells in a quantified, standardized manner to establish a "robust" model.

Thanks for your suggestion.  

Firstly, the constructed endometrial organoids generally consist of epithelial, stromal, and immune cells. However, it is undeniable that the cell proportions may vary slightly among different patients. Secondly, the term "robust" is intended to convey strong support for embryo development, which will be supported by our next study (unpublished data). Therefore, robust is replaced here as alternative. Thirdly, as for "reproducibility", the hormone-treated organoids from different women exhibited similarity to the in vivo receptive endometrium through multi-omics analysis, ERT, and various other experiments.  

Reviewer #2 (Public Review):

Q1: With endometrial receptivity analysis, they suggest a successful formation of the implantation window in vitro, but this result is difficult to interpret.

Thanks for your question.  

We understand that the most effective way to demonstrate endometrial receptivity is embryo implantation, which was conducted simultaneously and will be presented in our next study. In this study, we validated the receptivity based on the current researches.

(1) At the single-cell transcriptome level, the cellular composition and function of the receptive endometrial organoids were similar to those of the in vivo implantation window (Stephen R. Quake et al, 2020).

(2) At the whole organoids level, the receptive endometrial organoids exhibited the similar characteristics in transcriptome and proteome to the in vivo mid-secretory endometrium (Andres Salumets 2017, Qi Yu 2018, Triin Laisk 2018, Edson Guimarães Lo Turco 2018, Xiaoyan Chen 2020, Francisco Domínguez 2020, DavidW. Greening 2021, Norihiro Sugino 2023). The receptive endometrial organoids were also validated by endometrial receptivity test (ERT), which utilized high-throughput sequencing and machine learning to assess endometrial receptivity (Yanping Li et al., 2021).  

(3) At the microstructural level under electron microscope, the receptive endometrial organoids exhibited characteristics of the implantation window, such as pinopodes, glycogen particles, microvilli, and cilia.

Overall, the receptive organoids we constructed closely resemble the in vivo implantation window at the single-cell, organoids, and microstructural levels based on existing researches.

Q2: Analyzing transcriptome and proteome information of WOI organoids, authors demonstrate a strong response to estrogen and progesterone, but some comparisons are made with CTRL and SEC, and others only with CTRL, which limits the power of some results. In the same way, some genes related to Cilia and pinopodes appear dominant in WOI organoids, but the comparison by electron microscopy is made only against CTRL organoids.  

In subsequent analysis, WOI organoids showed a marked differentiation from proliferative to secretory epithelium, and from proliferative epithelium to EMT-derived stromal cells than SEC organoids. These statements are based on their upregulation of monocarboxylic acid and lipid metabolism, their enhanced peptide metabolism and mitochondrial energy metabolism, or their pseudotime trajectories. However, other analyses (such as the accumulation of secretory epithelium or decreased proliferative epithelium, the increased ciliated epithelium after hormonal treatment, or the presence of EMT-derived stromal cells) show only small differences between SEC and WOI organoids.

Thank you for raising these important questions.

(1) At the organoid level, the differences in transcriptome and proteome between SEC and WOI organoids are not significant. This is understandable because WOI organoids are further induced towards the implantation window based on the secretory phase (i.e. SEC organoids), and both are similar at the overall organoid level.  

(2) At the single-cell level, the accumulation of secretory epithelium, decreased proliferative epithelium, increased ciliated epithelium post hormonal treatment, or the presence of EMTderived stromal cells are the fundamental features of the secretory endometrium. Therefore, these features are present in both WOI and SEC organoids. However, the most notable differences lie in the more comprehensive differentiation and varied cellular functions exhibited by WOI organoids compared to SEC organoids.

(3) Regarding electron microscopy, we have now quantitatively compared the presence of various characteristic structures such as microvilli, cilia, pinopodes and glycogen in the CTRL, SEC and WOI groups. It has been observed that WOI organoids possess longer microvilli and increased cilia, glycogen, and pinopodes compared to SEC organoids (Fig2H).

Reviewer #1 (Recommendations For The Authors):

Q1: Several of the key methods are performed by companies, hence not in detail described and therefore not verifiable which is essential for reviewers and readers.

We are grateful for the suggestion. Specific methods have now been incorporated into the "Supporting Information" section. (Line91~102, Line 107~123, Line 132~139)

Q2 - Line 49: It is not shown in the present study whether the WOI organoids are a 'robust' platform.

- Line 76: There is a study (Dolat L., Valdivia RH., Journal of Cell Science, 2021) that developed a co-culture with endometrial organoids and immune cells (neutrophils) which should be mentioned.:

We have reweighed the word and now replace 'robust' with 'alternative' (Line 54).  We have considered the reviewer's suggestion and added this citation (Line 82-83) about the cocultivation of immune cells with endothelial organoids, which was not previously cited mainly because the research model was mouse.

Q3: Figure 1: Endometrial organoids possess endometrial morphology and function. - The authors should further explain their decision to add PRL, hCG, and hPL to the organoid culture. Why these particular compounds? What is their specific role during the WOI?

In terms of hormone scheme, estrogen and progesterone promote the transition of endometrial organoids into the secretory phase, and on this basis, pregnancy hormones can further promote their differentiation. PRL promotes immune regulation and angiogenesis during implantation, HCG improves endometrial thickness and receptivity, and HPL promotes the development and function of endometrial glands. Our constructed WOI organoid is in a state conducive to embryo implantation. We aim to develop an in vitro model for embryo implantation study. The detailed explanation of this aspect was initially provided in the Discussion section (Lines 298–313). To enhance the clarity for reviewers and readers regarding the selection of the hormonal regimen, we have now articulated it in the Results section (Lines 124–130).

When selecting hormone formulations, multiple group comparisons were made. It was found that the number, area, and average intensity of organoids in these groups were similar over time. But the WOI organoids showed endometrial receptivity related gene expression profile, which highly expressed genes positively correlated with endometrial receptivity, and lowly expressed genes negatively correlated with receptivity, compared to the other hormone formulations (added to Figure S1E, S1F). Hormone dosage was primarily based on peri-pregnant maternal body or localized endometrium levels (Margherita Y. Turco et al., Nature Cell Biology 2017).

-  Line 108: "the endometrial cells" instead of "endometrial organoid"? Because the authors also refer to the stromal cells.

You should be referring to this sentence “The endometrial organoid, consisting of vesicle-like glands, fibrous stromal cells, and other surrounding cells, developed into a 3D structure with the support of Matrigel”. Organoid, a self-assembled 3D structure, consists of multiple cells and closely resembles in vivo tissue or organ. It offers high expansibility, phenotypic, and functional properties. Here, we aim to delineate the endometrial organoid, comprising epithelial cells, stromal cells, and other cellular components that assemble to form intricate 3D structures. Hence, the term "endometrial organoid" is more appropriate.

-  Line 110: "the endometrial glands", do the authors mean the endometrial organoids? The authors also mention they enlarge, which must be quantified.

You should be referring to this sentence “As the organoids grew and differentiated, the endometrial glands enlarged, epithelial cells adopted a paving stone arrangement, and stromal cells formed an extensive network”. Here, we mean the “endometrial glands” grow progressively in the organoids. We agree with your suggestion to quantify the change of organoids’ area over time, and found that they increased progressively in all three groups (shown as follows) (Fig.S1E) (Line130-131) 

Author response image 3.

The dynamic changes of the area of organoids over time in the CTRL, SEC and WOI organoids.

-  Line 112: E-cadherin is a general epithelial marker, not a glandular marker.

We agree with your suggestion and now change to ‘The epithelium marker E-cadherin’ (Line110).

-  Line 116: Which group was used for KI67 and CC3 staining?

The CTRL organoids were used for Ki67 and CC3 staining. We have modified this expression in the Figure 1E Legend.

-  Line 123: Organoid size (diameter or area) needs to be quantified to claim that WOI organoids grow slower than SEC/CTRL organoids. The same goes for Ki67+ cells for proliferation. In the legend of Fig 1B, the authors in contrast state that the organoids show a similar growth pattern.

We are extremely grateful to you for pointing out this problem. We quantitatively analyzed the size of organoids in the three groups. The area was found to be increasing over time, with the three groups growing the most vigorously in the CTRL group, followed by the SEC group and the WOI group, but the differences were not statistically significant. Relevant results have been added to Figure S1E (Line130-131). There were no significant differences in Ki67 expression of these organoids. Therefore, the three groups of organoids showed a similar growth pattern. We decided to delete the statement “Following hormonal stimulation, WOI organoids exhibited slower growth than SEC and CTRL organoids, while CTRL organoids maintained robust proliferative activity (Fig. 1B)”.

Author response image 4.

The dynamic changes of the area of organoids over time in the CTRL, SEC and WOI organoids.

-  Line 126: Fourteen days of organoid treatment is a very long time. Growing organoids may already be dying which should be checked by CC3 staining to prove that organoids are still fully viable.

Endometrial organoids are vigorous in proliferation and have a long survival period due to the presence of adult stem cells. To address your queries effectively, we conducted CC3 staining on the organoids treated for 14 days, revealing negligible expression levels (shown as below).

Author response image 5.

Figure note: The Ki67 and CC3 immunostaining on the organoids after 14-day hormone treatment.

-  Line 128: Changes in hormone receptors should be supported by RT-qPCR data to be more convincing

We agree with your suggestion. Here we supplemented the RT-PCR results of hormone receptors as follows (Figure S1D) (Line119-121). PAEP and PGR are associated with progesterone, and OLFM4 and EGR1 are associated with estrogen.

-  1A: Are authors able to see and characterize decidualized stromal cells as indicated in the illustration?

Upon the reviewer's inquiry, we carefully observed the morphology of stromal cells in hormone-treated organoids. Regrettably, the morphology of decidualized stromal cells was not ascertainable through light microscopy in our endometrial organoids.

-  1C: Which treatment condition are the organoids in these images?

This figure showed the bright-field morphology of the CTRL organoids, which is now noted in the Figure 1C legend.

-  1D: PAS staining should be quantified to support the claims.

We agree with your suggestion. The quantitative comparison of PAS staining was conducted in these three groups of organoids (Figure S1G) (Line142-143)

-  1D: Where are the stromal cells in the model? There should be vimentin-positive cells outside of the glands.

The figure 1D illustrates the outcomes of section staining, which owned limitation to displaying stromal cells around the gland. Considering the 3D structure of organoids, we conducted organoid clearing and staining, and observed stromal cells (marked by Vimentin) under light sheet microscope (shown as below). The stromal cells were also presented using this method in the original Figure 2B.

Author response image 6.

Exhibition of stromal cell marked by vimentin of CTRL organoid through whole-mount clearing, immunostaining and light sheet microscopy imaging. Nuclei were counterstained with DAPI. The arrowhead indicates stromal cells. Scale bar = 70 μm.

Figure 2: Developing receptive endometrial organoids in vitro mimicking the implantation window endometrium.

-  Line 142: CD44 is not an exclusive marker for immune cells. It has been shown to be expressed in glandular secretory epithelial cells (Fonseca et al., 2023). The authors also mention that CD44 is expressed in stromal cells (line 265). Staining for CD45 (or another immune-specific marker) is needed to demonstrate the presence of immune cells. 

We appreciated your suggestions. We demonstrated the distribution of immune cells in organoids using the organoid clearing technique in combination with light-sheet microscopy imaging, using CD45 as a marker (Figure 2C).

-  Line 144: What are the proportions of the immune cells? What is the variation between patient samples?

We assessed the proportion of immune cells with the help of flow cytometry and analyzed the proportion of Macrophages and T cells in organoids derived from 8 patients. The proportion of WBC in organoids was about 3%~4% (Figure 2D), among which macrophages were less than 1% and T cells less than 2% (Figure S2E). There existed a very few patients with large heterogeneity, and the proportion of immune cells in most patients was

relatively stable.

-  Line 161: What is the endometrial receptivity test (ERT)? Not explained at all.

Endometrial Receptivity Test (ERT) is a kind of gene analysis-based method for detecting endometrial receptivity, which combines high-throughput sequencing and machine learning to analyze the expression of endometrial receptivity-related genes, allowing for a relatively accurate assessment of endometrial receptivity. It is currently used in clinical practice to determine endometrial receptivity and guide personalized embryo transfer (Yanping Li et al., J Transl Med 2021). (line179-183)

-  2A: The authors' dataset is compared to a published dataset. How were they combined? Were they merged, mapped on each other, or integrated? Were all cells employed from the published dataset or specific cell types? Much detail to evaluate the analysis is missing.

We are very grateful for your comments.  

(1) The four raw datasets (CTRL, SEC and WOI organoids, and mid-secretory endometrium) underwent batch correction and integration using Harmony. Subsequently, the integrated dataset underwent dimensionality reduction via  PCA. The soft k-means clustering algorithm was employed to address batch effects and clustering, utilizing a clustering parameter resolution of 0.5. Finally, the clustering results were visualized using tSNE based on the cell subpopulation classification. (“Methods” Line164-175)

(2) The Figure 2A displayed comparison of glandular and luminal epithelium, secretory epithelium, LGR5 epithelium, EMT-derived stromal cells, ciliated epithelium, and glandular secretory epithelium (shown as Figure S2C~S2D) (Line150-154)

- 2E: Please add the cell type names above the heatmaps to improve readability.

Thanks to your suggestion, we have added the cell type names above the heatmaps.

- 2G: The difference between the left and right graphs is not clear from the figure itself. Improve by adding a title and more explanation.

Thanks for your careful review. We have added the title to the left and right graphs.

Supplementary Figure 3 is referenced with Figure 2. Supplementary Figure 2 is referenced with Figure 3. The order needs to be changed.

Thanks for your careful review. We have changed the order.

- S3B: Typical markers for annotation of the different cell clusters are not included and therefore it is not convincing enough that annotations are correct. E.g. Epithelial markers (EPCAM, CDH1), Stromal cells (VIM, PDGFRA), SOX9+LGR5+ cells (SOX9, LGR5). How were the EMT-derived stromal cells designated? It is not clear from the data whether they are in fact EMT-derived or whether they show epithelial markers as well (stated in line 246).

We deeply appreciate your suggestion. We provided more details to describe the cell clustering as the following. Single-cell transcriptomics analysis referred to CellMarker, PanglaoDB, Human Cell Atlas, Human Cell Landscape, and scRNASeqDB, and previous endometrium related studies. (W. Wang et al., Nat Med 2020, P. D. Harriet C. Fitzgerald et al., PNAS 2019, K. M. Thomas, M Rawlings et al., eLife 2021, L. Garcia-Alonso et al., Nat Genet 2021) 

(1) SOX9+LGR5+ cells: SOX9 and LGR5 are both proliferative markers. SOX9 is expressed in all clusters dispersedly. LGR5 is mainly expressed in two clusters, one of which is stem derived epithelium, and the other cluster expresses LGR5 in a scattered manner. Refer to the markers of SOX9+LGR5+ cells, SOX9+LGR5- cells, and SOX9+ proliferative cells in 2021 Nature Genetics (L. Garcia-Alonso et al., Nat Genet 2021), the cells in this cluster expressed high levels of NUAK2, CNKSR3, FOS and LIF, which was consistent with the expression profiles of SOX9+LGR5+ cells and SOX9+ proliferative cells. However, considering that the number of cells expressing LGR5 was relatively small, this cluster of cells was renamed SOX9+ proliferative epithelium.

Figure 3: Receptive endometrial organoids recapitulate WOI-associated biological characteristics. - Line 173-174: The WOI organoids should be compared in detail to the SEC organoids in addition to the CTRL organoids, to show that this WOI model and new hormonal treatment is providing better results compared to the SEC organoids and the results obtained in previous studies.

Thanks for your suggestion. At the organoid level, the differences in transcriptome and proteome between SEC and WOI organoids are not significant. This is understandable because WOI organoids are further induced towards the implantation window based on the secretory phase (i.e. SEC organoids), which prompted us to continue exploring at the single-cell level.

- Line 190: Quantification of pinopodes is required to claim that they are more densely arranged in WOI organoids. 

- Line 190-191: Again, is there a difference in pinopode presence between the WOI and SEC organoids to show that the WOI organoids are really distinct and a better model?

We agree with the reviewer’s suggestion and quantified the pinopodes. The CTRL, SEC and WOI organoids were found to have increasing numbers of pinopodes, with WOI organoid owning the most abundant pinopodes under electron microscope. (Figure 2H) (Line184-186)

- Line 194: Also here, quantification of the glycogen particles is missing.

We agree with your suggestion. We have quantified the area of glycogen particles under electron microscope in the CTRL, SEC and WOI organoids. It was found that WOI organoid had the most glycogen particles. (Figure 2H) (Line184-186)

- 3C: There is no difference between SEC and WOI organoids condition for OLFM4 and PRA/B. What is the purpose then of adding extra hormones if no difference is present?

The figure 3C indicated that there was no significant difference in OLFM4 and PRA/B level (reflecting estrogen and progesterone responsiveness) in SEC and WOI organoids at the organoids level. It is understandable because WOI organoids are induced further into the implantation window on the basis of the secretory phase (i.e., SEC organoids), and both are similar at the overall level of organoids. Based on this, we further explored the differences between WOI organoids and SEC organoids at the single-cell level.

- 3G: A higher magnification is necessary to evaluate cilia staining. From these images, it seems like CTRL organoids also express acetyl-a-tubulin.

Thanks for your suggestion. The figure has been enlarged and shown as below. The acetyl-a-tubulin of WOI organoids is different from that of CTRL organoids in morphology and expression level. The glands of WOI organoids have small green tips (expressing acetyl-α-tubulin) convex toward the lumen. WOI organoids expressed higher level of acetyl-α-tubulin than CTRL organoids. (Now replaced with Figure 3G in the revised draft).

Figure 4: Structural cells construct WOI with functionally dynamic changes

- Line 211: To which figure are these claims referring to?

You should be referring to this sentence “In terms of energy metabolism, the WOI organoids exhibited upregulation of monocarboxylic acid and lipid metabolism, and hypoxia response”. Up-regulation of monocarboxylic acid and lipid metabolism in WOI organoids is reflected in Figure 3B, and up-regulation of hypoxia responses is reflected in Figure S3F.

- In general, it should be stated in the text that CellPhoneDB is a useful tool to investigate ligandreceptor interactions, however, it only proposes potential interactions. To validate such interactions, stainings and functional assays are required.

Thanks for your suggestion. The CellphoneDB was briefly introduced in the "Methods" section of "Supporting information" originally. Now it has been explained in the line 256-257 of main text.

We agree that staining and functional assays are required to validate the ligand-receptor interactions. Therefore, we used the proximity ligation assay (PLA) to verify the trend of interaction. (Figure S2J, Line259-261, Line 277-279, Line 285-288）

- Line 243: Please describe the process of EMT in the endometrium more specifically.

EMT is a common and crucial biological event in the endometrium during the implantation window. During the EMT process, epithelial cells lose their epithelial characteristics while gaining migratory and invasive properties of fibroblasts.

During the attachment and adhesion phases of embryo implantation, interaction mediated by trophoblastic factors (e.g. integrins) and maternal ECM factors (e.g. fibronectin) induce the eventual EMT in the trophectoderm. During the peri-implantation period, microRNAs, (e.g. miR429 and miR-126a-3p) which regulate EMT, are expressed in the maternal luminal epithelium to different degrees, mediating its transformation process as the blastocyst invades the maternal decidua. The epithelium of endometrium transforms to epithelioid stromal cells with increased migratory and invasive capacities through the EMT process. The decidual stromal cells migrate away from the implantation site, having acquired increased motility. (Line 265-267)

- Lines 247-251 and 313-316: the claim that proliferative epithelium transforms into EMT derived stromal cells by pseudotime trajectory is too bold and must be underpinned by other means. Pseudotime analysis only suggests and is by definition biased since the first/originating population must be defined by the operator.

In addition to pseudotime analysis based on monocle, RNA rate analysis based on scVelo is also used for cell evolution analysis. They can prove each other if both analyses indicate the transformation from proliferative epithelium to EMT-derived stromal cell. RNA rate analysis automatically determines the direction of differentiation, which can be used as evidence to determine the starting point of pseudotime analysis.

RNA rate analysis showed that the EMT derived stromal cell was most closely connected to the proliferative epithelium. Besides, the pseudotime point plot inferred that the proliferative epithelium was the root cell. It can be mutually proved with pseudotime analysis that the transformation from proliferative epithelium to EMT-derived stromal cell.

Author response image 7.

RNA rate junction diagram (To infer intercellular connectivity)

Author response image 8.

Time differentiation of cells

Discussion

- Line 300-302: It would be interesting to investigate ATP production and IL8 release in the WOI organoids to validate with findings from in vivo.

To answer this point of your interest, we purposely examined ATP production and IL8 release. It was found that WOI organoids indeed produced much more ATP and IL8 than CTRL and

SEC organoids (Figure S3L) (Line323-324)

- Line 313-316: Do the WOI organoids lose polarity and cell-to-cell junctions?

Transcriptome sequencing revealed downregulation of cell adhesion and RHO GTPase signaling in WOI organoids (Figure 3B). Electron microscopy revealed that the cellular arrangement of WOI organoids was slightly looser than that of CTRL organoids, but the microvilli were still oriented toward the medial side of the glands and did not undergo polarity reversal (shown as below).

Author response image 9.

Electron micrograph of the CTRL (left), and WOI (right) endometrial organoid. Scale bar = 5 μm.  

- Line 322: Where is the data that shows that 'a decreased abundance of immune cells', is observed?  

A decreased abundance of immune cells was observed through single-cell transcriptome sequencing and flow cytometry. The number of immune cells was reduced in WOI organoids compared to CTRL organoids in single-cell sequencing results (Figure 4A). Besides, flow cytometry also showed that the percentage of WBCs in WOI organoids was lower than that in CTRL organoids (Figure S2F).  

- Line 324: Elaborate more on how the immune cell composition differs from the endometrium.

The differences of immune cell composition between organoids and endometrium were mainly reflected in the proportion of WBC, the proportion of immune cell subtypes and the changes of T cells after entering the implantation window.

Firstly, the proportion of WBCs in organoids was lower than that in endometrium. Flow cytometry showed that the proportion of WBC in organoids was about 3%~4% (Figure 2D), but the proportion of WBCs in endometrium was about 8% (W. Wang et al., Nat Med 2020). Secondly, the proportions of T cells and macrophages in organoids were about 2%~3% and 1% (Figure 2D), respectively, but the proportions of lymphocytes and macrophages in endometrium were 7%~8% and 0.6%~0.7% (W. Wang et al., Nat Med 2020). Besides, after entering the implantation window, T cells in WOI organoids decreased (Figure S2F), while T cells in endometrium increased (W. Wang et al., Nat Med 2020). These three aspects have differences in vivo and in vitro. (Line347353)

Material and Methods

-  What are the concentrations of all medium components?

Thanks to your suggestions. The concentrations of all medium components have now been refined in Table S1.

-  Authors mention 10x while Smartseq2 is mentioned in Dataset S7?

Thanks for your careful review. Single cell transcriptome sequencing in this study was done using 10X Genomics. Smartseq2 was used to sequence the transcriptome of a gland and its surrounding cells, which can be regarded as small bulk RNA sequencing. A small number of cells are utilized in Smartseq2 to construct a full-length mRNA library with enhanced transcript sequencing coverage, making it particularly well-suited for small-scale samples such as organoids.

The data in Dataset S7 are acquired from small bulk RNA-seq with Smartseq2.  

Reviewer #2 (Recommendations For The Authors):

Q1: The theoretical choice of extra reagents added to the WOI organoids culture (PRL, hCG, and hPL) is theoretically justified, but not experimentally. On what previous studies, or performed experiments, are the choice of conditions used based?

When selecting hormone formulations, multiple group comparisons were made. It was found that the number, area, and average intensity of organoids in these groups were similar over time. But the WOI organoids showed endometrial receptivity related gene expression profile, which highly expressed genes positively correlated with endometrial receptivity, and lowly expressed genes negatively correlated with receptivity, compared to the other hormone formulations (added to Figure S1E, S1F). Hormone dosage was primarily based on peri-pregnant maternal body or localized endometrium levels (Margherita Y. Turco et al., Nature Cell Biology 2017).

Q2: Text in line 111 indicates that "stromal cells formed an extensive network", but vimentin fluorescence is not present on any image surrounding organoids in that figure. This assertion could only be supported by the subsequent results in Figure 2B. In addition, it is not indicated what kind of organoids have been used for these experiments

The stromal cells arranged around the glands in the 3D structure (as shown in Figure 1C and Figure 2B), where bright-field high magnification photography, clearing staining of the organoids, and light microscopy imaging were used, respectively. However, there are many steps of fixation, embedding, staining and elution during the immunostaining of sections. It is difficult to preserve the arrangement and morphology of the stromal cells in the slice, so the stromal cells were not intentionally captured in the other images.  

Figure 1C and Figure 2B are both CTRL organoids, which are now noted in the corresponding figure legend section.  

Q3: It is not clear how glycogen secretion into the lumen is assessed in Figure 1D.

Glycogen from the subnuclear region of the glandular cells gradually reaches the top of the cells, i.e., the supranuclear region, and is discharged into the glandular lumen as parietal plasma secretion. Glycogen-containing eosinophilic secretion can be seen in the glandular lumen in Figure1D.

Q4: Assertions about differences in proliferation between groups are purely subjective; some kind of measurement and analysis would be necessary to be sure that there is differential proliferation based on Figure 1B.

We are extremely grateful to you for pointing out this problem. We quantitatively analyzed the size of organoids in the three groups. The area was found to be increasing over time, with the three groups growing the most vigorously in the CTRL group, followed by the SEC group and the WOI group, but the differences were not statistically significant. Relevant results have been added to Figure S1E (Line130-131).

Q5: For progesterone receptor expression analysis organoids are cultured for fourteen days. What is the basis for this change in culture time? 

The choice of time point here is based on the secretary period of 14 days in the female menstrual cycle, when the endometrium is stimulated by estrogen and progesterone to maximized

level.

Q6: "n" number of individuals analysed through single-cell transcriptomics is not indicated.

One patient's endometrium was simultaneously constructed into CTRL, SEC and WOI organoids, which were then subjected to single-cell transcriptome sequencing. This is described in the Supporting Information (Line 141-142).

Q7: Where does the classification of EMT-derived stromal cells come from?

EMT is a common and crucial biological event in the endometrium during the implantation window. During the EMT process, epithelial cells lose their epithelial characteristics while gaining migratory and invasive properties of fibroblasts.

This cluster of cells expresses both epithelium markers CDH1 and EPCAM, and specifically expresses high levels of the EMT-related stromal cell markers AURKB, HJURP and UBE2C. During endometrial EMT, AURKB upregulates MMP2, VEGFA/Akt/mTOR and Wnt/β-catenin/Myc pathways to induce EMT (Zhen Wang et al., Cancer Manag Res 2020). HJURP also activates Wnt/β-catenin signaling to promote EMT (Y Wei et al., Eur Rev Med Pharmacol Sci 2019, Tianchi Chen et al., Int J Biol Sci 2019). UBE2C is upregulated by estrogen to promote EMT (Yan Liu et al., Mol Cancer Res 2020). Therefore, this cluster was defined as "EMT-derived stromal cells”.

Q8: In the endometrial receptivity test (ERT), endometrium sample data matches with prereceptive endometrium and WOI organoids data matches with a receptive endometrium, but why there is no information about CTRL and SEC organoids?

We performed ERT on these samples at a time when our hospital has a cooperative project with Yikon Genomics (Jiangsu, China). However, only endometrium and WOI organoids were sent for testing due to the limited quotas. Considering the end of cooperation and batch effect, no more CTRL and SEC organoids were tested. Moreover, the current ERT is a machine learning model based on the sequencing data of endometrium samples. But there are still differences in cellular composition between endometrial organoids and endometrium. Thus, the results need to be interpreted in conjunction with other results.

Q9: When analysing the transcriptome and proteome, some comparisons are made between WOI vs CTRL and SEC, or just WOI vs CTRL. It would be interesting to have all the comparisons since the power of WOI organoids lies in their differences with SEC organoids.

Thanks for your suggestion. At the organoid level, the differences in transcriptome and proteome between SEC and WOI organoids are not significant. This is understandable because WOI organoids are further induced towards the implantation window based on the secretory phase (i.e. SEC organoids), which prompted us to continue exploring at the single-cell level.

Q10: Electron microscopy comparisons with respect to pinopods, cilia, and microvilli are only performed between WOI and CTRL. It would be interesting to check it with SEC.

We now quantitatively compared the presence of various characteristic structure like microvilli, cilia, pinopodes and glycogen in the CTRL, SEC and WOI organoids. It was found that WOI organoid had longer microvilli and increased cilia, glycogen, and pinopodes (Figure 2H).

Q11: Line 190 states that pinopods are arranged more densely in WOI organoids than in CTRL organoids. Seems to be a subjective observation. Is there an objective method to quantify this?

We agree with the reviewer’s suggestion and quantified the pinopodes. The CTRL, SEC and WOI organoids were found to have increasing numbers of pinopodes, with WOI organoid owning the most abundant pinopodes. (Figure 2H) (Line184-186)

Q12: Some characteristics are very similar between WOI and SEC organoids (such as the accumulation of secretory epithelium or decreased proliferative epithelium, the increased ciliated epithelium after hormonal treatment, or the presence of EMT-derived stromal cells). The authors should complement the discussion by objectively justifying the use of WOI versus SEC organoids. Would they be useful in more specific cases or at a general level when studying implementation?

Thanks for your comments. WOI organoids are differentiated from SEC organoids towards the implantation window. Therefore, WOI organoids are suitable for studying periimplantation physiological changes or exploring pathological mechanisms. SEC organoids can be used when studying only a range of pathological problems such as endometrial secretory phase changes or hormone reactivity. (Line 365-368)

Q13：ExM media is described in Table S1, but it does not include the concentration of the different reagents in the culture medium, which is the most interesting data about the ExM medium.

Thanks to your suggestions. The concentrations of all medium components have now been refined in Table S1.

Q14: It is not specified which organoid pass is used in each experiment. Is it always the same pass?

Our experiments were conducted using P1~P3 generation endometrial organoids, as specified in the “Supporting Information” Line 54~55.

Q15: As a protocol for freezing organoids is included in materials and methods, do the authors use freshly cultured organoids or do they cryopreserve them and thaw them for culturing?

Thanks for your question. We used freshly cultured organoids in the manuscript. We listed the freezing protocol to illustrate that the constructed organoids can be frozen and recovered for special experimental needs and the establishment of sample banks.

Q16: The most important point: Neither of the two studies that developed human endometrial organoids from tissue biopsies (Boretto et al. 2017 and Turco et al. 2017), observed stromal cell growth in culture. They disappeared between the first and second pass (as indicated by Turco et al. 2017). How do the authors justify the presence of stromal cells in their organoid culture if they rely on the protocols previously described by these research groups? If it is the case that they can only use the initial pass (freshly planted cells from endometrium), it does not make sense to include the freezing of the different passes in materials and methods, since the expansion capacity of the culture would be lost, which implies a major limitation of the model.

Thanks for your question.  

(1) We did not completely follow the protocols of these research groups. To maximize the recovery of both epithelial and stromal cells, we optimized key steps such as tissue digestion and cell strainer filtration. We shortened the digestion time to 20 minutes to protect cells from the digestion solution and retain some cell aggregates, which are beneficial for maintaining cell stemness and preserving stromal and immune cells cluster. The 40 μm filter membrane was used to isolate the endometrial cells, which may acquire both epithelial, and stromal cells.

(2) Our experiments were conducted using P1~P3 generation of freshly constructed organoids. However, we also used recovered organoids when fresh endometrial samples were not available due to the COVID-19 epidemic. It was found that the organoids (e.g., P0~P5) still exhibited vigorous growth condition after recovery and could continue to be cultured by passaging (shown as below).

The recovered organoids can be used for special experiments and biobank establishment.

Author response image 10.

The endometrial organoids of different passages were observed before cryopreservation and after recovery. Scale bar = 200 μm.

Q17: It is not clear which organoids include Figure S2F. Does it include the three types of organoids or just WOI organoids?

This circle diagram showed the functions of upregulated genes in the WOI group compared to CTRL group from combined transcriptome and proteome analysis, which has been labeled in the figure legend section.