Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

This work provides a new potential tool to manipulate Tregs function for therapeutic use. It focuses on the role of PGAM in Tregs differentiation and function. The authors, interrogating publicly available transcriptomic and proteomic data of human regulatory T cells and CD4 T cells, state that Tregs express higher levels of PGAM (at both message and protein levels) compared to CD4 T cells. They then inhibit PGAM by using a known inhibitor ECGC and show that this inhibition affects Tregs differentiation. This result was also observed when they used antisense oligonucleotides (ASOs) to knockdown PGAM1.

PGAM1 catalyzes the conversion of 3PG to 2PG in the glycolysis cascade. However, the authors focused their attention on the additional role of 3PG: acting as starting material for the de novo synthesis of serine.

They hypothesized that PGAM1 regulates Tregs differentiation by regulating the levels of 3PG that are available for de novo synthesis of serine, which has a negative impact on Tregs differentiation. Indeed, they tested whether the effect on Tregs differentiation observed by reducing PGAM1 levels was reverted by inhibiting the enzyme that catalyzes the synthesis of serine from 3PG.

The authors continued by testing whether both synthesized and exogenous serine affect Tregs differentiation and continued with in vivo experiments to examine the effects of dietary serine restriction on Tregs function.

In order to understand the mechanism by which serine impacts Tregs function, the authors assessed whether this depends on the contribution of serine to one-carbon metabolism and to DNA methylation.

The authors therefore propose that extracellular serine and serine whose synthesis is regulated by PGAM1 induce methylation of genes Tregs associated, downregulating their expression and overall impacting Tregs differentiation and suppressive functions.

Strengths:

The strength of this paper is the number of approaches taken by the authors to verify their hypothesis. Indeed, by using both pharmacological and genetic tools in in vitro and in vivo systems they identified a potential new metabolic regulation of Tregs differentiation and function.

We are grateful to the reviewer for their thoughtful and constructive consideration of our work. We appreciate their comment that the number of approaches taken to test our hypothesis represents a strength that increases confidence in the conclusions.

Weaknesses:

Using publicly available transcriptomic and proteomic data of human T cells, the authors claim that both ex vivo and in vitro polarized Tregs express higher levels of PGAM1 protein compared to CD4 T cells (naïve or cultured under Th0 polarizing conditions). The experiments shown in this paper have all been carried out in murine Tregs. Publicly available resources for murine data (ImmGen -RNAseq and ImmPRes - Proteomics) however show that Tregs do not express higher PGAM1 (mRNA and protein) compared to CD4 T cells. It would be good to verify this in the system/condition used in the paper.

This is a fair comment. Although our pharmacologic and genetic studies demonstrated the importance of PGAM in Treg differentiation and suppressive function in murine cells, thereby corroborating the hypothesis formed based on human CD4 cell expression data, we agree that investigating PGAM expression in murine Tregs is important in the context of our work. In reviewing the ImmPres proteomics database, the reviewer is correct that PGAM1 expression was not higher in iTregs compared to other subsets, including Th17 cells. However, when compared to other glycolytic enzymes, expression of PGAM1 increases out of proportion in iTregs. In particular, the ratio of PGAM1 to GAPDH expression is much greater in iTregs compared to Th17 cells. This data is now shown in the revised Figure S5. The disproportionate increase in PGAM1 expression is consistent with the regulatory role of PGAM in the Treg-Th17 axis via modulation of 3PG concentrations, a metabolite that lies between GAPDH and PGAM in the glycolytic pathway. The divergent expression changes between GAPDH and PGAM furthermore support the conclusion that GAPDH and PGAM play opposite roles in Treg differentiation.

It would also be good to assess the levels of both PGAM1 mRNA and protein in Tregs PGAM1 knockdown compared to scramble using different methods e.g. qPCR and western blot. However, due to the high levels of cell death and differentiation variability, that would require cells to be sorted.

We appreciate this comment. As noted by the reviewer, assessing PGAM1 expression via qPCR and Western blot would require cell sorting, which we do not currently have the resources to pursue. However, we measured the effect of ASOs on PGAM1 protein expression using anti-PGAM1 antibody via flow cytometry, which allowed gating on viable cells. As shown in Figure S3A, PGAM-targeted ASOs led to an approximately 40% decrease in PGAM1 expression, as measured by mean fluorescence intensity (MFI). Furthermore, we now show in revised Figure S2 that ASO uptake was near-complete in our cultured CD4 cells.

It is not specified anywhere in the paper whether cells were sorted for bulk experiments. Based on the variability of cell differentiation, it would be good if this was mentioned in the paper as it could help to interpret the data with a different perspective.

Cells were not sorted for bulk experiments. In the revised manuscript, this point is made clear in the text, figure legends, and Methods. It is worth noting that all bulk experiments were conducted on samples with greater than 70% cell viability (greater than 90% for stable isotope tracing studies).

Reviewer #2 (Public review):

Summary:

The authors have tried to determine the regulatory role of Phosphoglycerate mutate (PGAM), an enzyme involved in converting 3-phosphoglycerate to 2-phosphoglycerate in glycolysis, in differentiation and suppressive function of regulatory CD4 T cells through de novo serine synthesis. This is done by contributing one carbon metabolism and eventually epigenetic regulation of Treg differentiation.

Strengths:

The authors have rigorously used inhibitors and antisense RNA to verify the contribution of these pathways in Treg differentiation in-vitro. This has also been verified in an in-vivo murine model of autoimmune colitis. This has further clinical implications in autoimmune disorders and cancer.

We very much appreciate these comments about the rigor of the work and its implications.

Weaknesses:

The authors have used inhibitors to study pathways involved in Treg differentiation. However, they have not studied the context of overexpression of PGAM, which was the actual reason to pursue this study.

We appreciate this comment and agree that overexpression of PGAM would be an excellent way to complement and further corroborate our findings. Unfortunately, despite attempting several methods, we were unable to consistently induce overexpression of PGAM1 in our primary T cell cultures.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I would suggest increasing the font size for flow cytometry gates. Percentages are the focus of the analysis, and it is very hard to read any.

We have increased the font size on all flow cytometry gates, as suggested.

Moreover, most of the flow data show Tregs polarization based on CD25 and FOXP3 expression. However, Figure 3 A, Figure 4D and Figure S3 show Tregs polarization based on FSC and Foxp3. Is there any reason for this?

Antibody staining against CD25 was poor in the experiments noted, which is why Foxp3 alone was used to identify Treg cells in these experiments.

Especially for Figure 3A, other cells could also express Foxp3 making interpretation difficult.

This is a fair comment. With respect to Figures 4D and S3 (now revised Figure S4), these experiments were conducted in isolated CD4 cells, in which the population of CD25-Foxp3+ cells is minimal following Treg polarization (as evident in our other figures). Regarding Figure 3A, previous work has found minimal expression of Foxp3 in circulating non-T cells (Devaud et al., 2014, PMID 25063364), such that we have confidence the identified Foxp3 expressing cells are, in fact, Treg cells. Notably, Figure 3A was already gated on CD4+ T cells, and in the periphery of wild-type mice, these would be reasonably referred to as Tregs, although this does not apply to diseased states or specific cases such as the tumor microenvironment.

The level of murine Tregs differentiation varies a lot among experiments. The % of CD4+CD25+FOXP3+ is ranging from 14% to 77% (controls). It would be good to understand and verify why such differentiation variability.

For most of our Treg polarization experiments, % differentiation in the control group falls within the 35 – 55% range. We found that treatment with ASOs (even scrambled control ASOs) tended to decrease Treg polarization overall, leading to lower numbers of Foxp3 expression in these experiments. Differentiation was similarly low in a few experiments that did not involve the use of ASOs, which we believe was caused by batch variability in the recombinant TGF-b that was used for polarization. Despite this variability, experiments were conducted with sufficient independent experiments and biological replicates to observe consistent trends and to have confidence in the results, as corroborated by statistical testing and the wide variety of experimental approaches used to verify our conclusions. Notably controls were run in every experiment, allowing accurate comparisons to be made in each individual experiment.

Similar comments apply to the level of cell death observed in the cultures of polarizing Tregs.

Although there was some variability in cell viability between experiments, flow cytometry experiments were always gated on live cells, and we believe concerns about reproducibility are substantially mitigated by the number of independent experiments, biological replicates, and distinct experimental approaches used for verification of the experimental findings. For all bulk experiments, cell viability was greater than 70% and equal across samples. For the flux studies, viability was greater than 90% and equal across samples.

Figure 2 B and D: EGCG has been used at two different concentrations. Is it lower in Figure 2D because of one condition being a combination of inhibitors or is it a typo?

The doses stated in the original legend are correct. Yes, drug doses were optimized for combination-treatment experiments. This point is now clarified in the figure legend.

Figure 2G: The description in the results does not match figure legend - Text - serine/glycine-free media or control (serine/glycine-containing) media; figure legend - serine/glycine-free media or media containing 4 mM serine.

We thank the reviewer for pointing out this discrepancy, which was an error in the text. The two conditions used were 1) serine/glycine-free media, and 2) serine/glycine-free media supplemented with 4 mM serine. The text and figure legend have both been updated to clarify this point.

Figure 3 F and G: the graphs do not show the individual points.

Individual points were not shown in these graphs because they are derived from scRNA-seq data, with SCFEA calculated from individual cells. As such, there are far too many data points to display all individual values.

CD4+ T-cell isolation and culture: cells were cultured in 50%RPMI and 50% AIM-V.

I thought that AIM-V medium was intended to be for human cultures. Could some of the conditions explain the low level of differentiation observed in some experiments? If there is such variability it might be because the conditions used are not optimal and therefore not reproducible.

We appreciate this critique. Although AIM-V media is often used for ex vivo human T cell cultures, it can similarly be used for mouse T cell culture with the addition of b-mercaptoethanol, as suggested by ThermoFisher and as used in prior publications, such as PMID 36947105. As outlined in the responses above, the differentiation we observed was consistent in most experiments, with some variability based on experimental conditions (such as lower differentiation in the setting of ASO treatment). Furthermore, we believe the number of independent experiments, biological replicates, and independent experimental approaches used in the study supports the reproducibility of our findings.

Figures S1 A, S2 B, and S4: the flow data are shown using both heights (FSC) and area (zombie NIR dye). It would be better to use areas for both parameters.

In the revised manuscript, areas are now used on both the x- and y-axes for these figures.

Figure S1 B and S2 C: The bar graphs are both showing proliferation index, however, the graphs are labelled differently in the two figures and in the legend (proliferation index -Fig S1 B; division index -Fig S2 C and replication index in the legend of Fig S2 C). The explanation of how the index has been calculated should probably go in the legend of the first figure that shows it.

We thank the reviewer for this comment. In the revised manuscript, we have ensured consistency in the terminology (“proliferation index” is now used consistently), and the explanation of the proliferation index calculation is now included in the legend to Figure S1, where the proliferation index first appears.

Were Tregs PGAM1 KD used for RNAseq sorted or not? Based on the plots shown in Figure S2 B there is ~ 50% death which needs to be taken into consideration for the analysis if not depleted.

Similar question for all bulk experiments. It is not specified in the methods or figure legends.

The cells used for RNAseq and other bulk experiments were not sorted. This point is now made clear in the text, figure legends, and Methods. However, cultures were only used for bulk analyses if the viability in those particular experiments was greater than 70%. Given the sensitivity of stable isotope tracing analyses, cultures were only analyzed for those studies if viability was greater than 90%. In these experiments, viability was similar across samples.

It was mentioned in Figure 1 that the PGAM KD led to transcriptional changes that impacted MYC targets and mTORC1 signalling. It would be good to validate these findings maybe with more targeted experiments.

We appreciate this suggestion and agree that validation and further investigation of these critical targets would be worthwhile. However, because of limitations to resources and the fact that these findings are not critical to the main conclusions of the study, we consider these experiments as future directions beyond the scope of the current work.

Reviewer #2 (Recommendations for the authors):

Here are a few suggestions and recommendations to improve the research study.

(1) The authors have used the word 'vehicle' in most of the figures, however, this word is not explained well in the figure legend. The authors may want to clarify to readers whether vehicle is a plasmid or a solvent for control purposes. For example, in Figure 1D, if vehicle is a plasmid, then another sample for vehicle +/-EGCG should be considered for the rigor in results.

Thank you for identifying this point of confusion. For all drug treatment experiments, vehicle controls consisted of solvent alone without drug. For ASO experiments, the control condition consisted of scrambled ASO. This point is now made clear in the Methods (“Drug and ASO Treatments” section) as well as in the main text. Furthermore, the figure legends and axes have been edited such that “vehicle” is only used to refer to drug experiments (in which solvent vehicle alone was used as control), and “control” is used to refer to ASO experiments (in which scrambled ASO served as control).

(2) Figure 1H represents the RNAseq data for knockdown of PGAM1. It might be interesting to see similar data for the overexpression of PGAM1.

We appreciate this comment and agree that overexpression of PGAM1 would be an excellent way to complement and further corroborate our findings using PGAM1 knockdown and pharmacologic inhibition. Unfortunately, despite attempting several methods, we were unable to consistently induce overexpression of PGAM1 in our primary T cell cultures.

(3) The font in most of the data from flow cytometry experiments (for example 1I) is not legible. Please increase the font size to make it legible.

Font sizes have been increased.

(4) Figure S2, PGAM expression was measured by Flow cytometry experiments. A similar experiment using western Blot, the direct measurement of protein expression, will strengthen the evidence.

We appreciate this comment. As noted in the public reviews, Western blot would require sorting of viable cells, and unfortunately we do not currently have the resources to conduct additional experiments with FACS. However, we respectfully note that assessing protein expression via flow cytometry quantifies protein levels based on antibody binding, similar to Western blot (or in-cell Western blot), while also allowing gating on viable cells. We also note that nearly 100% of cultured CD4 cells took up ASO, as shown in revised Figure S2.

(5) Figure 1J, it is mentioned in the text that 10 datasets were studied. a normalized parameter such as overexpression or suppression could be studied with the variance. It will be good to understand the variability in response among different datasets.

We thank the reviewer for the opportunity to clarify this data. This data was taken from a single published dataset (Dykema et al., 2023, PMID 37713507) in which 10 distinct subsets of tumor-infiltrating Tregs (TIL-Tregs) were identified, rather than from 10 distinct datasets. After identifying the Activated (1)/OX40hiGITRhi cluster of TIL-Tregs as a highly suppressive subset that correlates with resistance to immune checkpoint blockade, Dykema et al. compared gene expression in this subset to the bulked collection of the other 9 subsets, and the data shown in Figure 1J is derived from this analysis. As such, the data in Figure 1J is, indeed, a normalized parameter of overexpression, showing overexpression of PGAM1 in this highly suppressive subset versus other subsets, out of proportion to proximal rate-limiting glycolytic enzymes. The main text and figure/figure legend have been edited to clarify this point.

(6) It will be good to rephrase that the roles of PGAM and GAPDH are opposite, this paragraph is confusing since words such as "supporting Treg differentiation" and "augments Treg differentiation" have been used, although the data in S3 and 1D are opposite. Any possible explanation for the opposing roles of PGAM and GAPDH, despite their involvement in the same pathway of glycolysis, can be added to build up the interest of readers. What is the comparison of the expression of GAPDH and PGAM in Figure 1J?

We thank the reviewer for this comment, as we appreciate that the language used in our initial manuscript was confusing. We have edited the main text, in both the Results and Discussion section, in order to clarify this point and provide explanation as suggested. Indeed, our experimental data indicate that GAPDH and PGAM play opposing roles in Treg differentiation; whereas inhibiting GAPDH activity leads to greater Treg differentiation (shown in revised Figure S4 and our previously published work), similarly inhibiting PGAM leads to diminished Treg differentiation. We view this point (that enzymes within the same glycolytic pathway can have divergent roles in T cells) as a primary implication of these findings, with the explanation that individual enzymes within the same pathway can differentially regulate the concentrations of key immunoactive metabolites. In our study, we identified 3PG as a key immunoactive metabolite whose concentration would be differentially impacted by GAPDH activity versus PGAM activity, since it lies downstream of GAPDH but upstream of PGAM.

To provide further evidence for the opposing roles of GAPDH and PGAM, we analyzed existing datasets. In the revised Figure S5, we show that the PGAM1/GAPDH expression ratio increases in both human and mouse Tregs compared to other CD4 subsets.

(7) Figure 2C, what is M+1, M+2 etc. Does it represent the number of hrs? If so, why are the results for 6 hrs are not shown since the study was for 6 hrs? And what is happening with M+2?

We appreciate the opportunity to clarify this point and apologize for prior confusion. The terminology “M+n” refers to mass-shift produced by incorporation of 13-carbon. When a metabolite incorporates a single 13-carbon atom, it has a mass-shift of one (M+1), whereas incorporation of three 13-carbon atoms produces a mass-shift of three (M+3). Because we used uniformly 13-carbon labeled glucose, 3PG derived from the labeled glucose will have all three carbons labeled (M+3), as will serine that is newly synthesized from 3PG. Because serine can enter the downstream one-carbon cycle and be recycled, we also see the appearance of recycled serine with a single 13-carbon (M+1). The critical point in Figure 2C is that labeled serine is higher in Th17 versus Treg cells, demonstrating that de novo serine synthesis from glycolysis is greater. The main text has been edited to clarify this important point.

(8) Including the quantification of inhibition and rescuing effect of EDCG and NCT will be helpful to readers.

The inhibition and rescuing effects of these drugs are quantified in Figures 2D and 2E as they relate to Treg differentiation. The reviewer may be referring to quantification of relative effects on 3PG levels and serine synthesis. If so, we unfortunately do not have the resources to complete these studies, which would require large-scale quantitative mass spectrometry studies or enzyme activity assays.

(9) Figure 2D and 2E: The authors could also experiment with a dose dependence curve on EGCG and NCT on this phenotype for Treg differentiation. That can help understand the balance between serine pathways and glycolysis pathways. Similarly, the dose dependence of 3PG for Figure 2E and comparing it to the kinetic constants of these enzymes involved and cellular concentrations, these details will be helpful to understand the metabolic dynamics, because this phenotype could be an interplay of both 3PG and serine concentrations.

We appreciate this suggestion and agree that establishing detailed dose-dependence curves and relating these findings to enzyme kinetics would yield additional insights into the biochemical regulation provided by PGAM and PHGDH. Unfortunately we do not have the resources to pursue these additional studies, which therefore lie beyond the scope of our current work.

(10) Figure 4: Explanation for no effect of methionine supplementation?

Thank you for raising this point. We speculate that methionine supplementation had minimal effect because physiologic levels of serine were sufficient to provide basal substrates for the one-carbon cycle. On the other hand, eliminating methionine produced enough of a decrease in one-carbon metabolism to potentiate the effects of excess serine. This point is now briefly addressed in the text.

(11) For direct connection between PGAM and methylation, methylation experiments could be worked out with NCT1 and SHIN1 (as in Figure 4H).

We very much appreciate this suggestion, which we agree would provide a strong complementary approach. Unfortunately we do not have the resources to pursue these studies currently. However, we believe the increased methylation observed following PGAM knockdown (Figure 4G) as strong evidence that PGAM activity directly modulates methylation.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors have assembled a cohort of 10 SiNET, 1 SiAdeno, and 1 lung MiNEN samples to explore the biology of neuroendocrine neoplasms. They employ single-cell RNA sequencing to profile 5 samples (siAdeno, SiNETs 1-3, MiNEN) and single-nuclei RNA sequencing to profile seven frozen samples (SiNET 4-10).

They identify two subtypes of siNETs, characterized by either epithelial or neuronal NE cells, through a series of DE analyses. They also report findings of higher proliferation in non-malignant cell types across both subtypes. Additionally, they identify a potential progenitor cell population in a single-lung MiNEN sample.

Strengths:

Overall, this study adds interesting insights into this set of rare cancers that could be very informative for the cancer research community. The team probes an understudied cancer type and provides thoughtful investigations and observations that may have translational relevance.

Weaknesses:

The study could be improved by clarifying some of the technical approaches and aspects as currently presented, toward enhancing the support of the conclusions:

(1) Methods: As currently presented, it is possible that the separation of samples by program may be impacted by tissue source (fresh vs. frozen) and/or the associated sequencing modality (single cell vs. single nuclei). For instance, two (SiNET1 and SiNET2) of the three fresh tissues are categorized into the same subtype, while the third (SiNET9) has very few neuroendocrine cells. Additionally, samples from patient 1 (SiNET1 and SiNET6) are separated into different subtypes based on fresh and frozen tissue. The current text alludes to investigations (i.e.: "Technical effects (e.g., fresh vs. frozen samples) could also impact the capture of distinct cell types, although we did not observe a clear pattern of such bias."), but the study would be strengthened with more detail.

We thank the reviewer for the thoughtful and constructive review. Due to the difficulty in obtaining enough SiNET samples, we used two platforms to generate data - single cell analysis of fresh samples, and single nuclei analysis of frozen samples. We opted to combine both sample types in our analysis while being fully aware of the potential for batch effects. We therefore agree that this is a limitation of our work, and that differences between samples should be interpreted with caution.

Nevertheless, we argue that the two SiNET subtypes that we have identified are very unlikely to be due to such batch effect. First, the epithelial SiNET subtype was not only detected in two fresh samples but also in one frozen sample (albeit with relatively few cells, as the reviewer correctly noted). Second, and more importantly, the epithelial SiNET subtype was also identified in analysis of an external and much larger cohort of bulk RNA-seq SiNET samples that does not share the issue of two platforms (as seen in Fig. 2f). Moreover, the proportion of samples assigned to the two subtypes is similar between our data and the external data. We therefore argue that the identification of two SiNET subtypes cannot be explained by the use of two data platforms. However, we agree that the results should be further investigated and validated by future studies.

The reviewer also commented that two samples from the same patient which were profiled by different platforms (SiNET1 and SiNET6) were separated into different subtypes. We would like to clarify that this is not the case, since SiNET6 was not included in the subtype analysis due to too few detected Neuroendocrine cells, and was not assigned to any subtype, as noted in the text and as can be seen by its exclusion from Figure 2 where subtypes are defined. We apologize that our manuscript may have given the wrong impression about SiNET6 classification (it was labeled in Fig. 4a in a misleading manner). In the revised manuscript, we corrected the labeling in Fig. 4a and clarified that SiNET6 is not assigned to any subtype. We also further acknowledge the limitation of the two platforms and the arguments in favor of the existence of two SiNET subtypes.     

(Additional specific recommendations for the authors are provided below)

(2) Results:

Heterogeneity in the SiNET tumor microenvironment: It is unclear if the current analysis of intratumor heterogeneity distinguishes the subtypes. It may be informative if patterns of tumor microenvironment (TME) heterogeneity were identified between samples of the same subtype. The team could also evaluate this in an extension cohort of published SiNET tumors (i.e. revisiting additional analyses using the SiNET bulk RNAseq from Alvarez et al 2018, a subset of single-cell data from Hoffman et al 2023, or additional bulk RNAseq validation cohorts for this cancer type if they exist [if they do not, then this could be mentioned as a need in Discussion])

We agree that analysis of an independent cohort will assist in defining the association between TME and the SiNET subtype. However, the sample size required for that is significantly larger than the data available. In the revised manuscript we note that as a direction for future studies.

(3) Proliferation of NE and immune cells in SiNETs: The observed proliferation of NE and immune cells in SiNETs may also be influenced by technical factors (including those noted above). For instance, prior studies have shown that scRNA-seq tends to capture a higher proportion of immune cells compared to snRNA-seq, which should be considered in the interpretation of these results. Could the team clarify this element?

We agree that different platforms could affect the observed proportions of immune cells, and more generally the proportions of specific cell types. However, the low proliferation of Neuroendocrine cells and the higher proliferation of immune cells (especially B cells, but also T cells and macrophages) is consistently observed in both platforms, as shown in Fig. 4a, and therefore appears to be reliable despite the limitations of our work. We clarify this consistency in the revised manuscript. 

(4) Putative progenitors in mixed tumors: As written, the identification of putative progenitors in a single lung MiNEN sample feels somewhat disconnected from the rest of the study. These findings are interesting - are similar progenitor cell populations identified in SiNET samples? Recognizing that ideally additional validation is needed to confidently label and characterize these cells beyond gene expression data in this rare tumor, this limitation could be addressed in a revised Discussion.

We do not find evidence for similar progenitors in the SiNET samples, but they also do not contain two co-existing lineages of cancer cells within the same tumor, so this is harder to define. We agree about the need for additional validation for this specific finding and have noted that in the revised Discussion.

Reviewer #2 (Public review):

Summary:

The research identifies two main SiNET subtypes (epithelial-like and neuronal-like) and reveals heterogeneity in non-neuroendocrine cells within the tumor microenvironment. The study validates findings using external datasets and explores unexpected proliferation patterns. While it contributes to understanding SiNET oncogenic processes, the limited sample size and depth of analysis present challenges to the robustness of the conclusions.

Strengths:

The studies effectively identified two subtypes of SiNET based on epithelial and neuronal markers. Key findings include the low proliferation rates of neuroendocrine (NE) cells and the role of the tumor microenvironment (TME), such as the impact of Macrophage Migration Inhibitory Factor (MIF).

Weaknesses:

However, the analysis faces challenges such as a small sample size, lack of clear biological interpretation in some analyses, and concerns about batch effects and statistical significance.

Reviewer #3 (Public review):

Summary:

In this study, the authors set out to profile small intestine neuroendocrine tumors (siNETs) using single-cell/nucleus RNA sequencing, an established method to characterize the diversity of cell types and states in a tumor. Leveraging this dataset, they identified distinct malignant subtypes (epithelial-like versus neuronal-like) and characterized the proliferative index of malignant neuroendocrine cells versus non-malignant microenvironment cells. They found that malignant neuroendocrine cells were far less proliferative than some of their non-malignant counterparts (e.g., B cells, plasma cells, epithelial cells) and there was a strong subtype association such that epithelial-like siNETs were linked to high B/plasma cell proliferation, potentially mediated by MIF signaling, whereas neuronal-like siNETs were correlated with low B/plasma cell proliferation. The authors also examined a single case of a mixed lung tumor (neuroendocrine and squamous) and found evidence of intermediate/mixed and stem-like progenitor states that suggest the two differentiated tumor types may arise from the same progenitor.

Strengths:

The strengths of the paper include the unique dataset, which is the largest to date for siNETs, and the potentially clinically relevant hypotheses generated by their analysis of the data.

Weaknesses:

The weaknesses of the paper include the relatively small number of independent patients (n = 8 for siNETs), lack of direct comparison to other published single-cell NET datasets, mixing of two distinct methods (single-cell and single-nucleus RNA-seq), lack of direct cell-cell interaction analyses and spatially-resolved data, and lack of in vitro or in vivo functional validation of their findings.

The analytical methods applied in this study appear to be appropriate, but the methods used are fairly standard to the field of single-cell omics without significant methodological innovation. As the authors bring forth in the Discussion, the results of the study do raise several compelling questions related to the possibility of distinct biology underlying the epithelial-like and neuronal-like subtypes, the origin of mixed tumors, drivers of proliferation, and microenvironmental heterogeneity. However, this study was not able to further explore these questions through spatially-resolved data or functional experiments.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Methods:

a) Could the team clarify the discrepancy in subtype assignment between two samples from the same patient? i.e. are these samples from the same tumor? If so, what does the team think is the explanation for the difference in subtype assignment?

As noted above in response to the public review of reviewer #1, SiNET6 was in fact not assigned to any subtype (due to insufficient NE cells) and hence there was no discrepancy. We apologize for the misleading labeling of SiNET6 in the previous version and have corrected this In the revised version of Figure 4.

b) What is the rationale for scoring tumor-derived programs on samples with no tumor cells? For instance, SiNET3 does not contain NE cells, and SiNET9 has a very low fraction of NE cells. Please clarify how the scoring was performed on these samples, as the program assignments may be driven by other cell types in samples with little to no NE cells.

Scoring for tumor-derived programs was done only for the NE cells. Accordingly, SiNET3 was not scored or assigned to any of the programs. SINET9 was included in this analysis - although it had a relatively small fraction of NE cells, the absolute number of profiled cells was particularly high in this sample and therefore the number of NE cells was 130, higher than our cutoff of 100 cells.

c) Given the heterogeneity of cell types within each sample, would there be a way to provide a refined sense of confidence for certain cell type annotations? This would be helpful given the heterogeneity in marker gene expression and the absence of gold-standard markers for fibroblasts and endothelial cells in this cancer type. Additionally, there seems to be an unusually large proportion of NK and T cells - was there selection for this (given that these tumors are largely not immune infiltrated)?

Author Response: Except for the Neuroendocrine cells, there are six TME cell types that we consistently find in multiple SiNET samples: macrophages, T cells, B/plasma cells, fibroblasts, endothelial and epithelial cells. Each of these cell types are identified as discrete clusters in analysis of the respective tumors (as shown in Fig. 1a,b and Fig. S1), and these are exactly the six most common non-malignant cell types that we and others found in single cell analysis across various other tumor types (e.g. see Gavish et al. 2023, ref. #15). The signatures used to annotate these cell types are shown in Table S2, and they primarily consist of classical markers that are traditionally used to define those cell types. We therefore believe that the annotation of these typical tumor-associated cell types is robust and does not include major uncertainties. In addition to these five common cell types, there are three cell types that we find only in 1-2 of the samples – epithelial cells, plasma cells and NK cells. Again, we believe that their annotation is robust, and these cell types are primarily not used for further analysis.

There was no selection for any specific cell types in this study. Nevertheless, single cell (or single nuclei) analysis may lead to biases towards specific cell types, that we cannot evaluate directly from the data. NK cells were detected only in one tumor. T cells were detected in eight of the ten samples; but in four of those samples the frequency of T cells was lower than 5% and only in one sample the frequency was above 20%. Therefore, while we cannot exclude a technical bias towards high frequency of T/NK cells, we do not consider these frequencies as high enough to suggest this specific type of bias. In the revised manuscript, we clarify that the commonly observed cell types in SiNETs are the same as those commonly observed in other tumors and we acknowledge the possibility of a technical bias in cell type capture.  

d) Evaluating the expression of one gene at a time may not effectively demonstrate subtype-specific patterns, particularly when comparing NE cells from one tumor to non-NE cells from another, which may not be an appropriate approach for identifying differentially expressed genes. DE analysis coupled with concordance analysis, for example, could strengthen the results.

We apologize, but we do not fully understand this comment. We note that the initial normalization by non-NE cells was done in order to decrease batch effects when combining the data of the two platforms. We also note that the two subtypes were identified by two distinct approaches, as shown in Fig. 2c and in Fig. 2f.

(2) Results:

See the above public review.

(3) Minor Comments:

a) Results: Single cell and single nuclei RNA-seq profiling of SiNETs

The results say ten primary tumor samples from eight patients. Later in the paragraph it says, "After initial quality controls, we retained 29,198 cells from the ten patients." Please clarify to either ten samples or eight patients.

Indeed these are ten samples rather than ten patients. We corrected that in the revised version and thank the reviewer for noticing our error.

b) Methods:

- Please specify which computational tools were used to perform quality control, signature scoring, etc.

The approaches for quality control, scoring etc. are described in the methods. We implemented these approaches with R code and did not use other computational tools.

- Minor point but be consistent with naming convention (ie, siAdeno vs SiAdeno) throughout the paper. For example, under "Sample Normalization, Filtering and annotations" change "siAdeno" to "SiAdeno."

Thank you for noting this, we corrected that.

- Add processing and analysis of MiNEN sample to the methods section. It is not mentioned in the methods at all.

As noted in the revised manuscript, the MiNEN sample was analyzed in the same way as the SiNET fresh samples.

c) Supplementary Figures:

Figure S1: Change (A-H) to (A-I) to account for all panels in the figure.

Figure S4: Add (C) after "the siAdeno sample" in the legend.

Thank you for noting this, we corrected that.

(4) Font size is quite small in the main figures.

We enlarged the font in selected figure panels.

Reviewer #2 (Recommendations for the authors):

(1) The small number of samples used in some analyses affects the robustness of the findings. Increasing the sample size or including more validation data could improve the statistical reliability and make the results more convincing. The authors should consider expanding the cohort size or integrating additional external datasets to increase statistical power.

We agree with the reviewer that adding more samples would improve the reliability of the results. However, the external data that we found was not comparable enough to enable integration with our data, and we are unable to profile additional SiNET samples in our lab. We hope that future studies would support our results and extend them further.

(2) The biological significance of differentially expressed genes needs more depth, limiting the insights into SiNET biology. The authors should perform a comprehensive pathway enrichment analysis and integrate findings with existing literature. Tools like Gene Set Enrichment Analysis (GSEA) or Overrepresentation Analysis (ORA) could provide a more holistic view of altered biological processes.

We thank the reviewer for this suggestion. We did examine the functional enrichment of differentially expressed genes and did not find additional enrichments that we felt were important to highlight beyond what we described. We report the genes in supplementary tables, enabling other researchers to examine these lists further. 

(3) The unexpected finding of higher proliferation in non-malignant cells requires further investigation and plausible biological explanation. The authors should perform additional analyses to explore potential mechanisms, such as investigating cell cycle regulators or performing in vitro validation experiments. The authors should consider single-cell trajectory analysis to explore these highly proliferative non-malignant cells' potential differentiation or activation states.

We agree that our results are descriptive and that we do not fully explain the mechanism for the high level of non-malignant cell proliferation. We did attempt to perform follow up computational analysis. These analyses raised the hypothesis that high levels of MIF are causing the proliferation of immune cells. Additional analyses that we performed were not sufficient to conclusively identify a mechanism, and we felt that they were not informative enough to be included in the manuscript. Further in vitro (or in vivo) studies are beyond the scope of the current work.

(3) More details are required on methods used for p-value adjustment, and criteria for statistical significance should be clearly defined. Additionally, integrating scRNA-seq and snRNA-seq data needs a more thorough explanation, including batch effect mitigation and more explicit cell clustering representation. The authors should clearly describe p-value adjustments (e.g., FDR) and batch correction methods (e.g., Harmony, FastMNN integration) and include additional figures showing corrected UMAP plots or heatmaps post-batch correction to enhance the confidence in results.

We now clarify in the Methods our use of FDR for p-value adjustments. As for batch correction, we have avoided the use of integration methods as we believe that they tend to distort the data and decrease tumor-specific signals. Instead, we primarily analyzed one tumor at a time and never directly compared cell profiles across distinct tumors but only compared the differences between subpopulations; specifically, we normalized the expression of NE cells by subtracting the expression of reference non-NE cells from the same tumor as a method to decrease batch effects. We now clarify this point in the Methods section.

(4) The lack of analysis of interactions between different cell types limits understanding of tumor microenvironment dynamics. The authors should employ cell-cell interaction analysis tools (e.g., CellPhoneDB, NicheNet) to explore potential communication networks within the tumor microenvironment. This could provide valuable insights into how different cell types influence tumor progression and maintenance.

We thank the reviewer for this suggestion. We have tried to use such methods but found the results difficult to interpret since these approaches generated very long lists of potential cell-cell interactions that are largely not unique to the SiNET context and their relevance remains unclear without follow up experiments, which are beyond the scope of this work. We therefore focused only on ligand/receptors that came up robustly through specific analyses such as the differences between SiNET subtypes. In particular, MIF is highly expressed in the epithelial subtype, and remarkably, MIF upregulation is shared across multiple cell types. Thus, the cell-cell interactions that are suggested by the SiNET data as somewhat unique to this context are those involving MIF and its receptor (CD74 on immune cell types), while other interactions detected by the proposed methods primarily reflect the generic ligand/receptors expressed by corresponding TME cell types.   

Reviewer #3 (Recommendations for the authors):

(1) For a relatively small dataset, the mixing of single-cell versus single-nucleus RNA-seq should be discussed more. It would be nice to have 1-2 tumors that are analyzed by both methods to compare and increase our understanding of how these different approaches may affect the results. This could be accomplished by splitting a fresh tumor into two parts, processing it fresh for single-cell RNA-seq, and freezing the other part for single-nucleus RNA-seq.

We agree with the reviewer that the different techniques may bias our results and we refer to this limitation in the Results and Discussion sections. However, it is important to note that we do not directly integrate the primary data across these modalities, but rather analyze each tumor separately and only combine the results across tumors. For example, we first compare the NE cells from each tumor to control non-NE cells from the same tumor and then only compare the sets of NE-specific genes across tumors. Moreover, the subtypes that we detect cannot be explained by these modalities, as the first subtype contains samples from both methods and these subtypes are further demonstrated in external bulk data. Similarly, the results regarding low proliferation of NE cells and high proliferation of B/plasma cells are observed across both modalities. We therefore argue that while the combination of methods is a limitation of this work it does not account for the main results.  

(2) The authors state that they defined the siNET transcriptomic signature by comparing their siNET single-cell/nucleus data to other NETs profiled by bulk RNA-seq. Some of the genes in the signature, such as CHGA, are widely used as markers for NETs (and not specific for siNET). The authors should address this in more detail.

To define the SiNET transcriptomic signature we first analyzed each tumor separately and compared the expression of Neuroendocrine (NE) cells to that of non-NE cells to detect NE-specific genes. Next, we compared the lists of NE-specific genes across the 8 SiNET patients and found a subset of 26 genes which were shared across most of the analyzed SiNET samples (Fig. 2a). Thus, the signature was defined only from analysis of SiNETs and not based on comparison to other types of NETs and hence it is expected that the signature could contain both SiNET-specific genes and more generic NET genes such as CHGA.

Only after defining this signature, we went on to compare it between SiNETs and other types of NETs (pancreatic and rectal) based on external bulk RNA-seq data. In this comparison, we observed that the signature was clearly higher in SiNETs than in the other NETs (Fig. 2b). This result supports the accuracy of the signature and further suggests that it contains a fraction of SiNET-specific genes and not only generic NET genes such as CHGA. Thus, we would expect this signature to perform well also for distinguishing between SiNET and types of NETs, but it does contain a subset of genes that would be high in the other NETs. Finally, we note that even though CHGA is a generic NET marker, the bulk RNA-seq data would suggest that, at least at the mRNA level, this gene is still higher expressed in SiNETs than in other NETs. To avoid confusion regarding the definition and specificity of the SiNET transcriptomic signature we have extended the description of this section in the revised manuscript.

(3) The authors only compare their data to bulk transcriptomic data on NETs. While in some instances this makes sense given the bulk dataset has >80 tumors, they should at least cite and do some comparison to other published single-cell RNA-seq datasets of NETs (e.g., PMID: 37756410, 34671197). The former study listed has 3 siNETs, 4 pNETs, and 1 gNET. Do the epithelial-like and neuronal-like signatures show up in this dataset too?

We examined these studies but concluded that their data was inadequate to identify the two SiNET subtypes. The latter study was of pNETs, while the former study had 3 SiNET samples but only from 2 patients, and furthermore it was enriching for immune cells with only very low amounts of NE cells. Therefore, we now cite this work in the discussion but cannot use it to extend the results from our work.

(4) How did the authors statistically handle patients with more than one tumor sample (true for n = 2)? These tumor samples would not be truly independent.

In both cases where we had two distinct samples of the same patient, only one sample had sufficient NE cells to be included in NE-related analysis and therefore the other samples (SiNET3 and SiNET6) were excluded from all analysis of NE differential expression and subtypes. These samples were only included in the initial analysis (Fig. 1) and in TME-related analysis (Fig. 3-4) in which there was no statistical analysis of differences between patients and hence no problem with the inclusion of 2 samples for the same patient. We clarified this issue in the revised version.

(5) The association between siNET subtype and B/plasma cell proliferation is very interesting, as is the hypothesis regarding MIF signaling. It would be illuminating for the authors to perform cell-cell interaction analyses with methods such as CellChat in this context rather than just relying on DE. Spatial mapping would be helpful too and while this may be outside the scope of this study, it should at least be expounded upon in the Discussion section.

Indeed, spatial transcriptomic analysis would add interesting insight to our data and to SiNET biology. Unfortunately, this is not within the scope of the current project but we note this interesting possibility in the Discussion. Regarding additional methods for cell-cell interactions, we have performed such analysis but found it not informative as it highlighted a large number of interactions that are not unique SiNETs and are difficult to interpret, and therefore we do not include this in the revised version. 

(6) The authors note that in the mixed lung tumor, the NE component was more proliferative than that observed with siNETs. How does the proliferation compare to pNETs, gNETs, in other published studies? How about assessing the clonality of the SCC and LNET malignant cells with various genomic or combined genomic/transcriptomic methods?

The percentage of proliferating NE cells in the mixed lung tumor was higher than 60%. This is extremely high, approximately four-fold higher than the average that we found in a pan-cancer analysis and higher than the average of any of the >20 cancer types that we analyzed (Gavish et al. 2023, ref. #15). This remarkably high proliferation serves as a control for the low proliferation that we found in SiNET NE cells.

(7) In the Discussion on page 13, the authors write "Second, proliferation of NE cells may be inhibited by prior treatments with somatostatin analogues." How many patients were treated in this manner? This information should be made more explicit in the manuscript.

Details on pretreatment with somatostatin analogues are provided in Table S1. All patients were pre-pretreated with somatostatin analogues, with the possible exception of one patient (P8, SiNET10) for which we could not confidently obtain this information.

(8) On page 5, "bone-fide" is misspelled.

(9) On page 8, "exact identify" is misspelled.

We thank the reviewer and have corrected the typos.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors provide a study among healthy individuals, general medical patients and patients receiving haematopoietic cell transplants (HCT) to study the gut microbiome through shotgun metagenomic sequencing of stool samples. The first two groups were sampled once, while the patients receiving HCT were sampled longitudinally. A range of metadata (including current and previous (up to 1 year before sampling) antibiotic use) was recorded for all sampled individuals. The authors then performed shotgun metagenomic sequencing (using the Illumina platform) and performed bioinformatic analyses on these data to determine the composition and diversity of the gut microbiota and the antibiotic resistance genes therein. The authors conclude, on the basis of these analyses, that some antibiotics had a large impact on gut microbiota diversity, and could select opportunistic pathogens and/or antibiotic resistance genes in the gut microbiota.

Strengths:

The major strength of this study is the considerable achievement of performing this observational study in a large cohort of individuals. Studies into the impact of antibiotic therapy on the gut microbiota are difficult to organise, perform and interpret, and this work follows state-of-the-art methodologies to achieve its goals. The authors have achieved their objectives and the conclusion they draw on the impact of different antibiotics and their impact on the gut microbiota and its antibiotic resistance genes (the 'resistome', in short), are supported by the data presented in this work.

Weaknesses:

The weaknesses are the lack of information on the different resistance genes that have been identified and which could have been supplied as Supplementary Data.

We have now supplied a list of individual resistance genes as supplementary data.

In addition, no attempt is made to assess whether the identified resistance genes are associated with mobile genetic elements and/or (opportunistic) pathogens in the gut. While this is challenging with short-read data, alternative approaches like long-read metagenomics, Hi-C and/or culture-based profiling of bacterial communities could have been employed to further strengthen this work.

We agree this is a limitation, and we now refer to this in the discussion. Unfortunately we did not have funding to perform additional profiling of the samples that would have provided more information about the genetic context of the AMR genes identified.

Unfortunately, the authors have not attempted to perform corrections for multiple testing because many antibiotic exposures were correlated.

The reviewer is correct that we did not perform formal correction for multiple testing. This was because correlation between antimicrobial exposures meant we could not determine what correction would be appropriate and not overly conservative. We now describe this more clearly in the statistical analysis section.

Impact:

The work may impact policies on the use of antibiotics, as those drugs that have major impacts on the diversity of the gut microbiota and select for antibiotic resistance genes in the gut are better avoided. However, the primary rationale for antibiotic therapy will remain the clinical effectiveness of antimicrobial drugs, and the impact on the gut microbiota and resistome will be secondary to these considerations.

We agree that the primary consideration guiding antimicrobial therapy will usually be clinical effectiveness. However antimicrobial stewardship to minimise microbiome disruption and AMR selection is an increasingly important consideration, particularly as choices can often be made between different antibiotics that are likely to be equally clinically effective.

Reviewer #2 (Public Review):

Summary:

In this manuscript by Peto et al., the authors describe the impact of different antimicrobials on gut microbiota in a prospective observational study of 225 participants (healthy volunteers, inpatients and outpatients). Both cross-sectional data (all participants) and longitudinal data (a subset of 79 haematopoietic cell transplant patients) were used. Using metagenomic sequencing, they estimated the impact of antibiotic exposure on gut microbiota composition and resistance genes. In their models, the authors aim to correct for potential confounders (e.g. demographics, non-antimicrobial exposures and physiological abnormalities), and for differences in the recency and total duration of antibiotic exposure. I consider these comprehensive models an important strength of this observational study. Yet, the underlying assumptions of such models may have impacted the study findings (detailed below). Other strengths include the presence of both cross-sectional and longitudinal exposure data and the presence of both healthy volunteers and patients. Together, these observational findings expand on previous studies (both observational and RCTs) describing the impact of antimicrobials on gut microbiota.

Weaknesses:

(1) The main weaknesses result from the observational design. This hampers causal interpretation and corrects for potential confounding necessary. The authors have used comprehensive models to correct for potential confounders and for differences between participants in duration of antibiotic exposure and time between exposure and sample collection. I wonder if some of the choices made by the authors did affect these findings. For example, the authors did not include travel in the final model, but travel (most importantly, south Asia) may result in the acquisition of AMR genes [Worby et al., Lancet Microbe 2023; PMID 37716364). Moreover, non-antimicrobial drugs (such as proton pump inhibitors) were not included but these have a well-known impact on gut microbiota and might be linked with exposure to antimicrobial drugs. Residual confounding may underlie some of the unexplained discrepancies between the cross-sectional and longitudinal data (e.g. for vancomycin).

We agree that the observational design means there is the potential for confounding, which, as the reviewer notes, we attempt to account for as far as possible in the multivariable models presented. We cannot exclude the possibility of residual confounding, and we highlight this as a limitation in the  discussion. We have expanded on this limitation, and mention it as a possible explanation for inconsistencies between longitudinal and cross sectional models. Conducting randomised trials to assess the impacts of multiple antimicrobials in sick, hospitalised patients would be exceptionally difficult, and so it is hard to avoid reliance on observational data in these settings.

We did record participants’ foreign travel and diet, but these exposures were not included in our models as they were not independently associated with an impact on the microbiome and their inclusion did not materially affect other estimates. However, because most participants were recruited from a healthcare setting, few had recent foreign travel and so this study was not well powered to assess the effects of travel on AMR carriage. We have added this as a limitation.

In addition, the authors found a disruption half-life of 6 days to be the best fit based on Shannon diversity. If I'm understanding correctly, this results in a near-zero modelled exposure of a 14-day-course after 70 days (purple line; Supplementary Figure 2). However, it has been described that microbiota composition and resistome (not Shannon diversity!) remain altered for longer periods of time after (certain) antibiotic exposures (e.g. Anthony et al., Cell Reports 2022; PMID 35417701). The authors did not assess whether extending the disruption half-life would alter their conclusions.

The reviewer is correct that the best fit disruption half-life of 6 days means the model assumes near-zero exposure by 70 days. We appreciate that antimicrobials can cause longer-term disruption than is represented in our model, and we refer to this in the discussion (we had cited two papers supporting this, and we are grateful for the additional reference above, which we have added). We agree that it is useful to clarify that the longer term effects may be seen in individual components of the microbiome or AMR genes, but not in overall measures of diversity, so have added this to the discussion.

(2) Another consequence of the observational design of this study is the relatively small number of participants available for some comparisons (e.g. oral clindamycin was only used by 6 participants). Care should be taken when drawing any conclusions from such small numbers.

We agree. Although our participants received a large number of different antimicrobial exposures, these were dependent on routine clinical practice at our centre and we lack data on many potentially important exposures. We had mentioned this in relation to antimicrobials not used at our centre, and have now clarified in the discussion that this also limits reliability of estimates for antimicrobials that were rarely used in study participants.

(3) The authors assessed log-transformed relative abundances of specific bacteria after subsampling to 3.5 million reads. While I agree that some kind of data transformation is probably preferable, these methods do not address the compositional data of microbiome data and using a pseudocount (10-6) is necessary for absent (i.e. undetected) taxa [Gloor et al., Front Microbiol 2017; PMID 29187837]. Given the centrality of these relative abundances to their conclusions, a sensitivity analysis using compositionally-aware methods (such as a centred log-ratio (clr) transformation) would have added robustness to their findings.

We agree that using a pseudocount is necessary for undetected taxa, which we have done assuming undetected taxa had an abundance of 10^-6 (based on the lower limit of detection at the depth we sequenced). We refer to this as truncation in the methods section, but for clarity we have now also described this as a pseudocount.  Because our analysis focusses on major taxa that are almost ubiquitous in the human gut microbiome, a pseudocount was only used for 3 samples that had no detectable Enterobacteriaciae.

We are aware that compositionally-aware methods are often used with microbiome data, and for some analyses these are necessary to avoid introducing spurious correlations. However the flaws in non-compositional analyses outlined in Gloor et al do not affect the analyses in this paper:

(1) The problems related to differing sequence depths or inadequate normalisation do not apply to our dataset, as we took a random subset of 3.5 million reads from all samples (Gloor et al correctly point out that this method has the drawback of losing some information, but it avoids problems related to variable sequencing depth)

(2) The remainder Gloor et al critiques multivariate analyses that assess correlations between multiple microbiome measurements made on the same sample, starting with a dissimilarity matrix. With compositional data these can lead to spurious correlations, as measurements on an individual sample are not independent of other measurements made on the same sample. In contrast, our analyses do not use a dissimilarity matrix, but evaluate the association of multiple non-microbiome covariates (e.g. antibiotic exposures, age) with single microbiome measures. We use a separate model for each of 11 specified microbiome components, and display these results side-by side. This does not lead to the same problem of spurious correlation as analyses of dissimilarity matrices. However, it does mean that estimates of effects on each taxa outcome have to be interpreted in the context of estimates on the other taxa. Specifically, in our models, the associations of antimicrobial exposure with different taxa/AMR genes are not necessarily independent of each other (e.g. if an antimicrobial eradicated only one taxon then it would be associated with an increase in others). This is not a spurious correlation, and makes intuitive sense when using relative abundance as outcome. However, we agree this should be made more explicit.

For these reasons, at this stage we would prefer not to increase the complexity of the manuscript by adding a sensitivity analysis.

(4) An overall description of gut microbiota composition and resistome of the included participants is missing. This makes it difficult to compare the current study population to other studies. In addition, for correct interpretation of the findings, it would have been helpful if the reasons for hospital visits of the general medical patients were provided.

We have added a summary of microbiome and resistome composition in the results section and new supplementary table 2), and we also now include microbiome and resistome profiles of all samples in the supplementary data. We also provide some more detail about the types of general medical patients included. We are not able to provide a breakdown of the initial reason for admission as this was not collected.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Provide a supplementary table with information on the abundance of individual genes in the samples.

This supplementary data is now included.

(2) Engage with an expert in statistics to discuss how statistical analyses can be improved.

A experienced biostatistician has been involved in this study since its conception, and was involved in planning the analysis and in the responses to these comments.

(3) Typos and other minor corrections:

Methods: it is my understanding that litre should be abbreviated with a lowercase l.

Different journals have different house styles: we are happy to follow Editorial guidance.

p. 9: abuindance should be corrected to abundance.

Corrected

p. 9: relative species should be relevant species?  

Yes, corrected. Thank you.

p. 9 - 10: can the apparent lack of effect of beta-lactams on beta-lactamase gene abundance be explained by the focus on a small number of beta-lactamase resistance genes that are found in Enterobacteriaceae and which are not particularly prevalent, while other classes of resistance genes (e.g. Bacteroidal beta-lactamases) were excluded?

It is possible that including other beta-lactamases would have led to different results, but as a small number of beta-lactamases in Enterobacteriaceae are of major clinical importance we decided to focus on these (already justified in the Methods). A full list of AMR genes identified is now provided in the supplementary data.

p. 10: beta-lactamse should be beta-lactamase

Corrected

Figure 3A: could the data shown for tetracycline resistance genes be skewed by tetQ, which is probably one of the most abundant resistance genes in the human gut and acts through ribosome protection?

TetQ was included, but only accounted for 23% of reads assigned to tetracycline resistance genes so is unlikely to have skewed the overall result. We limited the analysis to a few major categories of AMR genes and, other than VanA, have avoided presenting results for single genes to limit the degree of multiple testing. We now include the resistome profile for each sample in the supplementary data so that readers can explore the data if desired.

Reviewer #2 (Recommendations For The Authors):

(1) Given the importance of obligate anaerobic gut microbiota for human health, it might be interesting to divide antibiotics into categories based on their anti-anaerobic activity and assess whether these antibiotics differ in their effects on gut microbiota.

The large majority of antibiotics used in clinical practice have activity against aerobic bacteria and anaerobic bacteria, so it is not possible to easily categorise them this way. There are two main exceptions (metronidazole and aminoglycosides) but there was insufficient use of these drugs to clearly detect or rule out a difference between them, even when categorising antimicrobials by class, so we prefer not to frame the results in these terms. Also see our comments on this categorisation below.

(2) For estimating the abundance of anaerobic bacteria, three major groups were assessed: Bacteroidetes, Actinobacteria and Clostridia. To me, this seems a bit aspecific. For example, the phylum Bacteroidetes contains some aerobic bacteria (e.g. Flavobacteriia). Would it be possible to provide a more accurate estimation of anaerobic bacteria?

We think that an emphasis on a binary aerobic/anaerobic classification is less biologically meaningful that the more granular genetic classification we use, and its use largely reflects the previous reliance on culture-based methods for bacterial identification. Although some important opportunistic human pathogens are aerobic, it is not clear that the benefit or harm of most gut commensals relates to their oxygen tolerance, and all luminal bacteria exist in an anaerobic environment. As such we prefer not to perform an additional analysis using this category. We are also not sure that this could be done reliably, as many of the taxa are characterised poorly, or not at all.

We appreciate that Bacteroidetes, Actinobacteria and Clostridia are diverse taxa that include many different species, so may seem non-specific, but these were chosen because:

i) they are non-overlapping with Enterobacteriaceae and Enterococcus, the major opportunistic pathogens of clinical relevance, so could be used in parallel, and

ii) they make up the large majority of the gut microbiome in most people and most species are of low pathogenicity, so it is plausible that their disruption might drive colonisation with more pathogenic organisms (or those carrying important AMR genes).

We have more clearly stated this rationale.

(3) A statement on the availability of data and code for analysis is missing. I would highly recommend public sharing of raw sequence data and R code for analysis. If possible, it would be very valuable if processed microbiome data and patient metadata could be shared.

We agree, and these have been submitted as supplementary data. We have added the following statement “The data and code used to produce this manuscript are available in the supplementary material, including processed microbiome data, and pseudonymised patient metadata. The sequence data for this study have been deposited in the European Nucleotide Archive (ENA) at EMBL-EBI under accession number PRJEB86785.”

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Cao et al. provides a compelling investigation into the role of mutational input in the rapid evolution of pesticide resistance, focusing on the two-spotted spider mite's response to the recent introduction of the acaricide cyetpyrafen. This well-documented introduction of the pesticide - and thus a clearly defined history of selection - offers a powerful framework for studying the temporal dynamics of rapid adaptation. The authors combine resistance phenotyping across multiple populations, extensive resequencing to track the frequency of resistance alleles, and genomic analyses of selection in both contemporary and historical samples. These approaches are further complemented by laboratory-based experimental evolution, which serves as a baseline for understanding the genetic architecture of resistance across mite populations in China. Their analyses identify two key resistance-associated genes, sdhB and sdhD, within which they detect 15 mutations in wild-collected samples. Protein modeling reveals that these mutations cluster around the pesticide's binding site, suggesting a direct functional role in resistance. The authors further examine signatures of selective sweeps and their distribution across populations to infer the mechanisms - such as de novo mutation or gene flow-driving the spread of resistance, a crucial consideration for predicting evolutionary responses to extreme selection pressure. Overall, this is a well-rounded, thoughtfully designed, and well-written manuscript. It shows significant novelty, as it is relatively rare to integrate broad-scale evolutionary inference from natural populations with experimentally informed bioassays, however, some aspects of the methods and discussion have an opportunity to be clarified and strengthened.

Strengths:

One of the most compelling aspects of this study is its integration of genomic time-series data in natural populations with controlled experimental evolution. By coupling genome sequencing of resistant field populations with laboratory selection experiments, the authors tease apart the individual effects of resistance alleles along with regions of the genome where selection is expected to occur, and compare that to the observed frequency in the wild populations over space and time. Their temporal data clearly demonstrates the pace at which evolution can occur in response to extreme selection. This type of approach is a powerful roadmap for the rest of the field of rapid adaptation.

The study effectively links specific genetic changes to resistance phenotypes. The identification of sdhB and sdhD mutations as major drivers of cyetpyrafen resistance is well-supported by allele frequency shifts in both field and experimental populations. The scope of their sampling clearly facilitated the remarkable number of observed mutations within these target genes, and the authors provide a careful discussion of the likelihood of these mutations from de novo or standing variation. Furthermore, the discovered cross-resistance that these mutations confer to other mitochondrial complex II inhibitors highlights the potential for broader resistance management and evolution.

Weaknesses:

(1) Experimental Evolution:

- Additional information about the lab experimental evolution would be useful in the main text. Specifically, the dose of cyetpyrafen used should be clarified, especially with respect to the LD50 values. How does it compare to recommended field doses? This is expected to influence the architecture of resistance evolution. What was the sample size? This will help readers contextualize how the experimental design could influence the role of standing variation.

The experimental design involved sampling approximately 6,000 individuals from the wild population ZJSX1, which were subsequently divided into two parallel cohorts under controlled laboratory conditions. The selection group (LabR) was subjected to continuous selection pressure using cyetpyrafen, while the control group (LabS) was maintained under identical laboratory conditions without exposure to acyetpyrafen. A dynamic selection regime was implemented wherein the acaricide dosage was systematically adjusted every two generations to maintain a consistent selection intensity, achieving a mortality rate of 60% ± 10% in the LabR population. This adaptive dosage strategy ensured sustained evolutionary pressure while preventing population collapse. The LC₅₀ values were tested at F1, F32, F54, F60, F62, and F66 generations using standardized bioassay protocols to quantify resistance development trajectories and optimize dosage for subsequent selection cycles. We provided the additional information in subsection 4.1 of the materials and methods section.

- The finding that lab-evolved strains show cross-resistance is interesting, but potentially complicates the story. It would help to know more about the other mitochondrial complex II inhibitors used across China and their impact on adaptive dynamics at these loci, particularly regarding pre-existing resistance alleles. For example, a comparison of usage data from 2013, 2017, and 2019 could help explain whether cyetpyrafen was the main driver of resistance or if previous pesticides played a role. What happened in 2020 that caused such rapid evolution 3 years after launch?

Although the introduction of the other two SDHI acaricides complicates the story, we would like to provide a complete background on the usage of acaricides with this mode of action in China. Although cyflumetofen was released in 2013 before cyetpyrafen, and cyenopyrafen was released in 2019 after cyetpyrafen, their market share is minor (about 3.2%) compared to cyetpyrafen (about 96.8%, personal communication). Since cross-resistance is reported among SDHIs, we could not exclude the contribution of cyflumetofen to the initial accumulation of resistance alleles, but the effect should be minor, both because of their minimal market share and because of the independent evolution of resistance in the field as found in our study. Although the contribution of cyflumetofen and cyenopyrafen cannot be entirely excluded, the rapid evolution of resistance seems likely to be mainly explained by the intensive application of cyetpyrafen. To clarify this issue, we added relevant information in the first paragraph of the discussion section.

(2) Evolutionary history of resistance alleles:

- It would be beneficial to examine the population structure of the sampled populations, especially regarding the role of migration. Though resistance evolution appears to have had minimal impact on genome-wide diversity (as shown in Supplementary Figure 2), could admixture be influencing the results? An explicit multivariate regression framework could help to understand factors influencing diversity across populations, as right now much is left to the readers' visual acuity.

The genetic structure of the populations was examined by Treemix analysis. We detected only one migration event from JXNC to SHPD (no resistance data available for these two populations), suggesting a limited role for migration to resistance evolution. The multiple regression analysis revealed that overall genetic diversity and Tajima’s D across the genome were not significantly associated with resistance levels, genetic structure or geographic coordinates (P > 0.05), which all support a limited role of migration in resistance development.

- It is unclear why lab populations were included in the migration/treemix analysis. We might suggest redoing the analysis without including the laboratory populations to reveal biologically plausible patterns of resistance evolution.

Thank you for the constructive suggestion. The Treemix analysis was redone by removing laboratory populations and is now reported.

- Can the authors explore isolation by distance (IBD) in the frequency of resistance alleles?

Thank you for the constructive suggestion. No significant isolation-by-distance pattern was detected for resistance allele frequencies across all surveyed years (2020: P=0.73; 2021: P=0.52; 2023: P=0.16; Mantel test). We added these results to the text.

- Given the claim regarding the novelty of the number of pesticide resistance mutations, it is important to acknowledge the evolution of resistance to all pesticides (antibiotics, herbicides, etc.). ALS-inhibiting herbicides have driven remarkable repeatability across species based on numerous SNPs within the target gene.

We appreciate this comment, which highlights the need to place our findings within the broader evolutionary context of pesticide resistance. We have investigated references relevant to the evolution of resistance to diverse pesticides. As far as we can tell, the 15 target mutations in eight amino acid residues are among the highest number of pesticide resistance mutations detected, especially within the context of animal studies. We have added relevant text to the second paragraph of the discussion.

- Figure 5 A-B. Why not run a multivariate regression with status at each resistance mutation encoded as a separate predictor? It is interesting that focusing on the predominant mutation gives the strongest r2, but it is somewhat unintuitive and masks some interesting variation among populations.

We conducted a multiple regression analysis to explore the influence of multiple mutations on resistance levels of field populations. However of 15 putative resistant mutations, only five were detected in more than three populations where bioassay data are available, i.e. I260T, I260V, D116G, R119C, R119L. The frequency of three of these mutations, I260T (P = 0.00128), I260V (P = 0.00423) and D116G (P = 0.00058), are significantly correlated with the resistance level of field populations. This has been added.

(3) Haplotype Reconstruction (Line 271-):

- We are a bit sceptical of the methods taken to reconstruct these haplotypes. It seems as though the authors did so with Sanger sequencing (this should be mentioned in the text), focusing only on homozygous SNPs. How many such SNPs were used to reconstruct haplotypes, along what length of sequence? For how many individuals were haplotypes reconstructed? Nonetheless, I appreciated that the authors looked into the extent to which the reconstructed haplotypes could be driven by recombination. Can the authors elaborate on the calculations in line 296? Is that the census population size estimate or effective?

Because haplotypes could not be determined when more than two loci were heterozygous, we detected haplotypes from sequencing data with at most one heterozygous locus. In total 844 individuals and 696 individuals were used to detect haplotypes of sdhB and sdhD. We detected 11 haplotypes (with 8 SNPs) and 24 haplotypes (with 11 SNPs) along 216 bp of the sdhB and 155 bp of the sdhD genes, respectively. Please see the fifth paragraph of subsection 2.4. We used ρ = 4 × Ne × d (genetic distance) (Li and Stephens, 2003) to calculate the number of effective individuals for one recombination event.

(4) Single Mutations and Their Effect (line 312-):

- It's not entirely clear how the breeding scheme resulted in near-isogenic lines. Could the authors provide a clearer explanation of the process and its biological implications?

To investigate the effect of single mutations or their combination on resistance levels, we isolated the females and males with the same homozygous/ hemizygous genotypes for creating homozygous lines. Females from these lines were not near-isogenic, but homozygous for the critical mutations. We revised the description in the methods section to clearly define these lines.

- If they are indeed isogenic, it's interesting that individual resistance mutations have effects on resistance that vary considerably among lines. Could the authors run a multivariate analysis including all potential resistance SNPs to account for interactions between them? Given the variable effects of the D116G substitution (ranging from 4-25%), could polygenic or epistatic factors be influencing the evolution of resistance?

We couldn’t conduct multivariate analysis because most lines have only one resistant SNP. The four lines homozygous for 116G were from the same population. The variable mortality may reflect other unknown mechanisms but these are beyond the scope of this study.

- Why are there some populations that segregate for resistance mutations but have no survival to pesticides (i.e., the green points in Figure 5)? Some discussion of this heterogeneity seems required in the absence of validation of the effects of these particular mutations. Could it be dominance playing a role, or do the authors have some other explanation?

We didn’t investigate the degree of dominance of each mutation. The mutation I260V shows incompletely dominant inheritance (Sun, et al. 2022). To investigate survival rate of different populations, the two-spotted spider mite T. urticae was exposed to 1000 mg/L of cyetpyrafen, higher than the recommended field dose of 100 mg/L. Such a high concentration may lead to death of an individual heterozygous for certain mutations, such as I260V.

- The authors mention that all resistance mutations co-localized to the Q-site. Is this where the pesticide binds? This seems like an important point to follow their argument for these being resistance-related.

Yes. We revised Fig. 3c to show the Q-site.

(5) Statistical Considerations for Allele Frequency Changes (Figure 3):

- It might be helpful to use a logistic regression model to assess the rate of allele frequency changes and determine the strength of selection acting on these alleles (e.g., Kreiner et al. 2022; Patel et al. 2024). This approach could refine the interpretation of selection dynamics over time.

Thank you for this suggestion. A logistic regression model was used to track allele frequencies trajectories. The selection coefficient of each allele and their joint effects were estimated.

Reviewer #2 (Public review):

Summary:

This paper investigates the evolution of pesticide resistance in the two-spotted spider mite following the introduction of an SDHI acaricide, cyatpyrafen, in China. The authors make use of cyatpyrafen-naive populations collected before that pesticide was first used, as well as more recent populations (both sensitive and resistant) to conduct comparative population genomics. They report 15 different mutations in the insecticide target site from resistant populations, many reported here for the first time, and look at the mutation and selection processes underlying the evolution of resistance, through GWAS, haplotype mapping, and testing for loss of diversity indicating selective sweeps. None of the target site mutations found in resistant populations was found in pre-exposure populations, suggesting that the mutations may have arisen de novo rather than being present as standing variation, unless initially present at very low frequencies; a de novo origin is also supported by evidence of selective sweeps in some resistant populations. Furthermore, there is no significant evidence of migration of resistant genotypes between the sampled field populations, indicating multiple origins of common mutations. Overall, this indicates a very high mutation rate and a wide range of mutational pathways to resistance for this target site in this pest species. The series of population genomic analyses carried out here, in addition to the evolutionary processes that appear to underlie resistance development in this case, could have implications for the study of resistance evolution more widely.

Strengths:

This paper combines phenotypic characterisation with extensive comparative population genomics, made possible by the availability of multiple population samples (each with hundreds of individuals) collected before as well as after the introduction of the pesticide cyatpyrafen, as well as lab-evolved lines. This results in findings of mutation and selection processes that can be related back to the pesticide resistance trait of concern. Large numbers of mites were tested phenotypically to show the levels of resistance present, and the authors also made near-isogenic lines to confirm the phenotypic effects of key mutations. The population genomic analyses consider a range of alternative hypotheses, including mutations arising by de novo mutation or selection from standing genetic variation, and mutations in different populations arising independently or arriving by migration. The claim that mutations most likley arose by multiple repeated de novo mutations is therefore supported by multiple lines of evidence: the direct evidence of none of the mutations being found in over 2000 individuals from naive populations, and the indirect evidence from population genomics showing evidence of selective sweeps but not of significant migration between the sampled populations.

Weaknesses:

As acknowledged within the discussion, whilst evidence supports a de novo origin of the resistance-associated mutations, this cannot be proven definitively as mutations may have been present at a very low frequency and therefore not found within the tested pesticide-naive population samples.

We agree that we could not definitively exclude the presence of a very low incidence of favoured mutations before the introduction of this novel acaricide.

Near-isofemale lines were made to confirm the resistance levels associated with five of the 15 mutations, but otherwise, the genotype-phenotype associations are correlative, as confirmation by functional genetics was beyond the scope of this study.

We hope that future functional studies will validate the effects of these mutations on resistance in both the two-spotted spider mite T. urticae and other spider mite species. This could be done by creating near-isogenic female lines or using CRISPR-Cas9 technology, as gene knockouts have recently been established for T. urticae.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Could the authors elaborate on the environmental context (e.g., climate, geography) of the sampled populations to give more nuance to the analysis of genetic differentiation and resistance evolution?

We have explored the influence of geographic isolation on the frequency of resistance alleles by Mantel tests (isolation by distance). We didn’t investigate the influence of climate, because most of the samples were from greenhouses, where the climate to which the pest is exposed is unclear.

(2) Line 161: is this supposed to be one R and one S?

Yes, we added this information (LabR and LabS).

(3) Line 207: variation is not saturated at the first two sites because the different combinations are not seen. This is a bit misleading.

What we wanted to indicate was that the two codon positions are saturated, rather than their combinations. We revised this sentence by adding “of each codon position”.

(4) Line 376: continuous selection did not "result in a new mutation arising". Rather, the mutation arose and was subsequently selected on.

We revised the expression of this de novo mutation and selection process.

(5) Line 402: can the authors explore what Ne would be necessary to drive the number of mutational origins they observe, as in (Karasov et al. 2010)?

It is challenged to estimate Ne, especially when mutation rate data from the two-spotted spider mite T. urticae is unavailable. We observed 2.7 resistant mutations per population in samples collected in 2024, seven years after the release of cyetpyrafen. The estimated mutation rate (Θ) is  0.0193, given 20 generations per year for T. urticae. An effective population size (Ne) of 2.29*10⁶ would be necessary to reach the number of de novo mutations observed in this study, given Θ  =  3Neμ (haplodiploid sex determination of T. urticae) and a mutation rate of μ  =  2.8*10^-9 per base pair per generation as estimated for Drosophila melanogaster (Keightley et al., 2014). The high reproductive capacity of T. urticae (> 100 eggs per female) and short generation time makes it easier to reach such a population size in the field as we now note.

(6) Line 482: how did the authors precisely kill 60% of samples with their selection? What was the applied rate? In general, listing the rates of insecticide used in dose response would be useful to decipher if LD50s are projected outside of the doses used (seems like they are). In this case, authors should limit their estimates to those > the highest rate used in the dose response.

It is difficult to control mortality precisely. We applied cyetpyrafen every two generations but did not determine the LC₅₀ every two generations. When mortality was lower than 60%, another round of spraying was applied by increasing the dosage of the pesticide. The LC₅₀ values were tested at F₁, F₃₂, F₅₄, F₆₀, F₆₂, and F₆₆ generations to establish the trajectories around resistance.

(7) The light pink genomic region in Figure 2 was distracting. Why is it included if there is no discussion of genomic regions outside the sdh genes? Generally, there was a lot going on in this figure, and some guiding categories (i.e., lab selected vs wild population) on the figure itself could help orient the reader.

We included chromosome 2 colored in light pink/ red to show the selection signal across a wider genomic region. In the figure legend, we added a description of the lab selected, field resistant and field susceptible populations. Very little common selection signal was detected among resistant populations on chromosome 2, indicating this region was less likely to be involved in resistance evolution of T. urticae to cyetpyrafen. We also described the result briefly in the figure legend.

Reviewer #2 (Recommendations for the authors):

(1) The most significant aspect of this study is the use of multiple pest population samples taken before as well as after the introduction of a class of pesticides, allowing a thorough comparative population genomics study in a species where a range of resistance mutations have appeared within a few years. I would prefer to see a title conveying this significance, rather than the current study, which focuses on the total number of mutations and claimed notoriety of the (at that point unnamed) study species. Similarly, I would prefer an abstract that relies less on superlative claims and includes more details: the scientific name of the study species; the number of years in which resistance evolved; the number of historical specimens; how the resistance levels for single mutations were shown.

(1) The title was changed by adding “the two-spotted spider mite Tetranychus urticae” and removing the “unprecedented number” to emphasize that “recurrent mutations drive rapid evolution”, i.e., “Recurrent Mutations Drive the Rapid Evolution of Pesticide Resistance in the Two-spotted Spider Mite Tetranychus urticae.”

(2) The scientific name of the study species was added.

(3) The number of years in which resistance evolved was added.

(4) The number of historical specimens was added (2666).

(5) Because we used homozygous lines but not iso-genic lines or gene-edited lines, our bioassay data could not provide direct evidence on the level of resistance conferred by each mutation. We revised our description of the results and removed this content from the abstract.

Line 29: if you want to claim the number is unprecedented, please specify the context: unprecedented for a pesticide target in an arthropod pest? (more resistance mutations may have been found in bacteria/fungi...).

We revised the sentence by adding “in an arthropod pest”.

Line 30: rather than a claim of notoriety, it may be better to specify what damage this pest causes.

Revised by describing it as an arthropod pest.

Line 34: please clarify, was this all in different haplotypes, or were some mutations found in combination?

Done: We identified 15 target mutations, including six mutations on five amino acid residues of subunit sdhB, and nine mutations on three amino acid residues of subunit sdhD, with as many as five substitutions on one residue.

(2) The introduction begins by framing the context as resistance evolution in invertebrate pests. However, the evolutionary processes examined in the study are applicable to resistance in other systems, and potentially to other cases of rapid contemporary evolution. The authors could show wider significance for their work beyond the subfield of invertebrate pests by including more of this wider context in their introduction and discussion: even if this means they can no longer claim novelty based on the number of mutations alone, the study is a strong example of the use of population genomics combined with functional and phenotypic characterisation to investigate the evolutionary processes underlying the emergence of resistance, so could have wider importance than within its current framing.

The background was revised as mentioned above to take this into account.

For example, in lines 48-50, please clarify what is meant by pesticides here (insects/arthropods? weeds and pathogens too?) In lines 69-73, the opposite is sometimes seen in fungal pathogens, with large numbers of mutations generated in lab-evolved strains.

We extended pesticides to those targeting arthropods, weeds and pathogens. We still emphasize the situation mainly with respect to arthropod pests.

(3) Lines 91-93: how many modes of action? How recently were SDHI acaricides introduced?

Added: at least 11 groups of acaricides based on their modes of action. SDHI was launched in 2007.

(4) Line 98-102: Use in China is a useful background for the study populations, but the global context should be included too.

Yes, four SDHI acaricides developed around the globe were introduced.

(5) Line 113: They show diverse mutations, but all within the mechanism of target-site point mutations.

We agree to your suggestion. This sentence has been removed as it repeats information stated above it.

(6) Line 115-116: Yes, agreed; I think this is the main strength of the current study and should be emphasised sooner.

Thanks.

(7) Line 158: Selective sweep signals were clear in half of the resistant populations but not in the others. The suggestion that the others had undergine soft sweeps, with multiple mutations increasing in frequency simultaneously but no one reaching fixation, seems reasonable; but the authors could compare the populations that did show a sweep with those that did not (for example, was there greater diversity or evenness of genotypes in those that did not?).

Five resistant populations with selection signals identified by PBE analysis (Figure 2b) showed corresponding decreases in π and Tajima’s D near the two SDH genes but not across the genome (Figure S1).

(8) Line 313: please clarify "in combination with other mutations" within a mixed population or combined in one individual/haplotype? Also, the phrase "characterised the function" may be a little misleading, as this is a correlative analysis, not functional confirmation.

None of the combinations of different resistant mutations was observed in a single haplotype. Here, we examine resistance levels associated with a single mutation or two mutations on sdhB and sdhD in one individual, i.e. sdhB_I260V and sdhD_R119C. We revised the sentences to avoid any implication of functional confirmation.

(9) Line 358: again, please clarify the context: among arthropod pests?

Done.

(10) Line 360-363: please give some background on when and where these related compounds were introduced.

Added.

(11) Line 410: yes fitness costs may be a factor, but you could also give an example of a cost expressed in the absence of any pesticides, as well as the given example of negative cross-resistance.

We added the example of the H258Y mutation which causes both fitness costs and negative cross-resistance.

(12) Lines 419-438: this is one aspect where the situation for insecticides is in contrast with some other resistance areas.

Yes, we restricted these statements to arthropod pests.

(13) Line 466: some more detail could be given here: for example, SNP-specific monitoring would be less effective, but amplicon sequencing would be more suitable.

Yes, revised.

(14) Lines 472-475: Please list the numbers of field/lab, pre/post exposure, and sensitive/resistant populations within the main text.

Done. The number of sensitive/resistant populations was reported in the result section.

(15) Line 483: randomly selected individuals?

Yes, added randomly selected individuals.

(16) Line 556: Sanger sequencing to characterise populations? Or a number of individuals from each population?

Revised.

(17) References: there are some duplicate entries, please check this.

Checked.

(18) Figure 1e: consider a log(10) scale to better show large fold changes and avoid multiple axis breaks.

Thanks for your suggestions. However we didn’t scale the LC₅₀ value, because we wanted to show the specific impact of 1,000 mg/L. The breaks in the Y axis around 30 mg/L -1,000 mg/L reveal that the LC50s of the resistant populations were all greater than 1000 mg/L, while those of the susceptible populations were all below 30 mg/L. This justified the use 1000 mg/L as a discriminating dose to investigate resistance status and level in subsequent work.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Azlan et al. identified a novel maternal factor called Sakura that is required for proper oogenesis in Drosophila. They showed that Sakura is specifically expressed in the female germline cells. Consistent with its expression pattern, Sakura functioned autonomously in germline cells to ensure proper oogenesis. In sakura KO flies, germline cells were lost during early oogenesis and often became tumorous before degenerating by apoptosis. In these tumorous germ cells, piRNA production was defective and many transposons were derepressed. Interestingly, Smad signaling, a critical signaling pathway for the GSC maintenance, was abolished in sakura KO germline stem cells, resulting in ectopic expression of Bam in whole germline cells in the tumorous germline. A recent study reported that Bam acts together with the deubiquitinase Otu to stabilize Cyc A. In the absence of sakura, Cyc A was upregulated in tumorous germline cells in the germarium. Furthermore, the authors showed that Sakura co-immunoprecipitated Otu in ovarian extracts. A series of in vitro assays suggested that the Otu (1-339 aa) and Sakura (1-49 aa) are sufficient for their direct interaction. Finally, the authors demonstrated that the loss of otu phenocopies the loss of sakura, supporting their idea that Sakura plays a role in germ cell maintenance and differentiation through interaction with Otu during oogenesis.

Strengths:

To my knowledge, this is the first characterization of the role of CG14545 genes. Each experiment seems to be well-designed and adequately controlled

Weaknesses:

However, the conclusions from each experiment are somewhat separate, and the functional relationships between Sakura's functions are not well established. In other words, although the loss of Sakura in the germline causes pleiotropic effects, the cause-and-effect relationships between the individual defects remain unclear.

Comments on latest version:

The authors have attempted to address my initial concerns with additional experiments and refutations. Unfortunately, my concerns, especially my specific comments 1-3, remain unaddressed. The present manuscript is descriptive and fails to describe the molecular mechanism by which Sakura exerts its function in the germline. Nevertheless, this reviewer acknowledges that the observed defects in sakura mutant ovaries and the possible physiological significance of the Sakura-Out interaction are worth sharing with the research community, as they may lay the groundwork for future research in functional analysis.

We thank the reviewer for valuable comments. We would like to investigate the molecular mechanism by which Sakura exerts its function in the germline in near future studies. 

Reviewer #2 (Public review):

In this study, the authors identified CG14545 (named it sakura), as a key gene essential for Drosophila oogenesis. Genetic analyses revealed that Sakura is vital for both oogenesis progression and ultimate female fertility, playing a central role in the renewal and differentiation of germ stem cells (GSC).

The absence of Sakura disrupts the Dpp/BMP signaling pathway, resulting in abnormal bam gene expression, which impairs GSC differentiation and leads to GSC loss. Additionally, Sakura is critical for maintaining normal levels of piRNAs. Also, the authors convincingly demonstrate that Sakura physically interacts with Otu, identifying the specific domains necessary for this interaction, suggesting a cooperative role in germline regulation. Importantly, the loss of otu produces similar defects to those observed in sakura mutants, highlighting their functional collaboration.

The authors provide compelling evidence that Sakura is a critical regulator of germ cell fate, maintenance, and differentiation in Drosophila. This regulatory role is mediated through modulation of pMad and Bam expression. However, the phenotypes observed in the germarium appear to stem from reduced pMad levels, which subsequently trigger premature and ectopic expression of Bam. This aberrant Bam expression could lead to increased CycA levels and altered transcriptional regulation, impacting piRNA expression. In this revised manuscript, the authors further investigated whether Sakura affects the function of Orb, a binding partner they identified, in deubiquitinase activity when Orb interacts with Bam.

We appreciate the authors' efforts to address all our comments. While these revisions have greatly improved the clarity of certain sections, some of the concerns remain unclear, while details mentioned in the responses about these studies should be incorporated in the manuscript. Specifically, the manuscript still lacks the demonstration that Sakura co-localizes with Orb/Bam despite having the means for staining and visualization. This would bring insight into the selective binding of Orb with Bam vs. Sakura perhaps at different stages of oogenesis. Such analyses would allow for more specific conclusions, further alluding to the underlying mechanism, rather than the general observations currently presented.

This elaborate study will be embraced by both germline-focused scientists and the developmental biology community.

We thank the reviewer for valuable comments. We believe that the author meant Otu, not Orb, for the binding partner of Sakura that we identified. We would like to investigate the colocalization of Sakura with other proteins including Otu and the molecular mechanism by which Sakura exerts its function in the germline in near future studies. 

Reviewer #3 (Public review):

In this very thorough study, the authors characterize the function of a novel Drosophila gene, which they name Sakura. They start with the observation that sakura expression is predicted to be highly enriched in the ovary and they generate an anti-sakura antibody, a line with a GFP-tagged sakura transgene, and a sakura null allele to investigate sakura localization and function directly. They confirm the prediction that it is primarily expressed in the ovary and, specifically, that it is expressed in germ cells, and find that about 2/3 of the mutants lack germ cells completely and the remaining have tumorous ovaries. Further investigation reveals that Sakura is required for piRNA-mediated repression of transposons in germ cells. They also find evidence that sakura is important for germ cell specification during development and germline stem cell maintenance during adulthood. However, despite the role of sakura in maintaining germline stem cells, they find that sakura mutant germ cells also fail to differentiate properly such that mutant germline stem cell clones have an increased number of "GSC-like" cells. They attribute this phenotype to a failure in the repression of Bam by dpp signaling. Lastly, they demonstrate that sakura physically interacts with otu and that sakura and otu mutants have similar germ cell phenotypes. Overall, this study helps to advance the field by providing a characterization of a novel gene that is required for oogenesis. The data are generally high-quality and the new lines and reagents they generated will be useful for the field.

Comments on latest version:

With these revisions, the authors have addressed my main concerns.

We thank the reviewer for valuable comments.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

The manuscript is much improved based on the changes made upon recommendations from the reviewers.

Though most of our comments have been addressed, we have a few more we wish to recommend. For previous points we made, we replied with further clarification for the authors.

Figure 1

(1) B should be the supplemental figure.

We moved the former Fig 1B to Supplemental Figure 1.

• Previous Fig1B (sakura mRNA expression level) is now Fig S2, not S1. Please make this data as Fig S1.

We moved Fig S1 to main Fig7A and renumbered Fig S2-S16 to Fig S1-S15.

(2) C - How were the different egg chamber stages selected in the WB? Naming them 'oocytes' is deceiving. Recommend labeling them as 'egg chambers', since an oocyte is claimed to be just the one-cell of that cyst.

We changed the labeling to egg chambers.

• The labels on lanes for Stages 12-13 and Stage 14, still only say "chambers", not "egg chambers". Also there is no Stage 1-3 egg chamber. More accurately, the label should be "Germarium - Stage 11 egg chambers".

We updated the lables on lanes as suggested by the reviewer.

(3) Is the antibody not detecting Sakura in IF? There is no mention of this anywhere in the manuscript.

While our Sakura antibody detects Sakura in IF, it seems to detect some other proteins as well. Since we have Sakura-EGFP fly strain (which fully rescues sakuranull phenotypes) to examine Sakura expression and localization without such non-specific signal issues, we relied on Sakura-EGFP rather than anti-Sakura antibodies for IF.

• Please put this info into the Methods section.

We added this info into the Methods section.

(4) Expand on the reliance of the sakura-EGFP fly line. Does this overexpression cause any phenotypes?

sakura-EGFP does not cause any phenotypes in the background of sakura[+/+] and sakura[+/-].

• Please add this detail into the manuscript.

We added this info into the Methods section.

Figure 5

(1) D - It might make more sense if this graph showed % instead of the numbers.

We did not understand the reviewer's point. We think using numbers, not %, makes more sense.

• Having a different 'n' number for each experiment does not allow one to compare anything except numbers of the egg chambers. This must be normalized.

We still don’t agree with the reviewer. In Fig 5D, we are showing the numbers of stage 14 oocytes per fly (= per a pair of ovaries). ‘n’ is the number of flies (= number of a pair of ovaries) examined. We now clarified this in the figure legend. Different ‘n’ number does not prevent us from comparing the numbers of stage 14 oocytes per fly. Therefore, we would like to show as it is now.

(2) Line 213 - explain why RNAi 2 was chosen when RNAi 1 looks stronger.

Fly stock of RNAi line 2 is much healthier than RNAi line 1 (without being driven Gal4) for some reasons. We had a concern that the RNAi line 1 might contain an unwanted genetic background. We chose to use the RNAi 2 line to avoid such an issue.

• Please add this information to the manuscript.

We added this info into the Methods section.

Figure 7/8 - can go to Supplemental.

We moved Fig 8 to supplemental. However, we think Fig 7 data is important and therefore we would like to present them as a main figure.

• Current Fig S1 should go to Fig 7, to better understand the relationship between pMad and Bam expression.

We moved Fig S1 to main Fig7A and renumbered Fig S2-S16 to Fig S1-S15.

Figure 9C - Why the switch to S2 cells? Not able to use the Otu antibody in the IP of ovaries?

We can use the Otu antibody in the IP of ovaries. However, in anti-Sakura Western after anti Otu IP, antibody light chain bands of the Otu antibodies overlap with the Sakura band. Therefore, we switched to S2 cells to avoid this issue by using an epitope tag.

• Please add this info to the Methods section.

We added this info into the Methods section.

Figure 10- Some images would be nice here to show that the truncations no longer colocalize.

We did not understand the reviewer's points. In our study, even for the full-length proteins. We have not shown any colocalization of Sakura and Otu in S2 cells or in ovaries, except that they both are enriched in developing oocytes in egg chambers.

• Based on your binding studies, we would expect them to colocalize in the egg chamber, and since there are antibodies and a GFP-line available, it would be important to demonstrate that via visualization.

As we wrote in the response and now in the manuscript, our antibodies are not best for immunostaining. We will try to optimize the experimental conditions in the future studies.

Author response:

The following is the authors’ response to the original reviews

Recommendations for the authors:

Reviewing Editor (Recommendations For The Authors):

There are four main areas that need further clarification:

(1) Further and more complete assessment of senescence and the fibroblasts must be done to support the claims. 

We sincerely appreciate the Reviewing Editor's valuable suggestion regarding the addition of cellular senescence detection markers. In the revised manuscript, we have incorporated additional detection markers for cellular senescence, such as H3K9me3 and SA-β-gal staining, in healthy and periodontitis gingival samples to further validate our findings (Figure 1A, B in revised manuscripts).

(2) Confusion between ageing and senescence throughout the manuscript.

We fully understand the concerns raised by the Reviewing Editor and reviewers regarding the confusion between the concepts of ageing and senescence in the manuscript. Cellular senescence is a manifestation of ageing at the cellular level. In the revised manuscript, we have given priority to the term ‘senescence’ to describe the cell condition instead of ‘aging’.

(3) The lipid metabolism mechanistic claims are very speculative and largely unsupported by experimental data. 

We greatly appreciate the Reviewing Editor and reviewers for pointing out the incorrect statements regarding the role of lipid metabolism in regulating cellular senescence. Since the mechanism by which cellular metabolism regulates cellular senescence is not the core focus of this manuscript, we have moved the results of the metabolic analysis from the sc-RNA sequencing data to the figure supplement (Figure 4-figure supplement 1) and revised the related statements in the revised manuscript (Page 7-8, Line 186-194).

(4) Concerns about the use of Metformin as a senotherapy vs other pleiotropic effects in periodontitis and the suggestion of using an alternative Senolytic drug (Bcl2 inhibitors, etc.). 

We fully understand the concerns of the Reviewing Editor and reviewers regarding metformin as an anti-aging therapy. In the revised manuscript, we have included additional experiments using other senolytic drugs ABT-263, a Bcl2 inhibitor, in the ligature-induced periodontitis mouse model. The corresponding results could be found in the Figure 6. and Page 9-10, Line 248-264 in the revised manuscripts.

Reviewer #1 (Recommendations For The Authors):

While most of the experiments are elegantly designed and the procedures well conducted there are several critical weaknesses that temper my enthusiasm for this solid and timely work. Considering my main points, I would recommend the following:

(1) Potentiate the senescent assessment in vitro and, most importantly, in vivo. E.g. SABgal with fresh tissue, other senescent biomarkers like SAHFs (HP1g or H3K9me3), etc.

We sincerely appreciate the reviewers' suggestion to potentiate the assessment of cellular senescence. In the revised manuscript, we performed SA-β-gal staining on fresh frozen samples, revealing a significantly higher number of SA-β-gal positive cells in the gingival tissue of periodontitis, particularly in the lamina propria, while few SA-β-gal positive cells were observed in healthy gingival tissue (Figure. 1A). Additionally, we assessed the protein level changes of H3K9me3, a marker of senescence-associated heterochromatin foci (SAHF), in gingival tissues from healthy individuals and periodontitis patients. The results showed a notable increase in the number of H3K9me3 positive cells in periodontitis tissues, approximately double that found in healthy gingiva (Figure. 1B). This trend aligns with our previous findings of elevated p16 and p21 levels. Collectively, these results further confirm that periodontitis gingival tissues contain a greater number of senescent cells compared to healthy gingiva.  

(2) Claims on disturbances in lipid metabolism as a driver of CD81+ fibroblast senescence require appropriate functional/mechanistic validations and experiments of metabolism rewiring.

We sincerely appreciate the reviewers' suggestion for more experimental evidence regarding the role of lipid metabolism in driving CD81+ fibroblast senescence. The influence and mechanisms of lipid metabolism on cellular senescence is a complex and important scientific issue, and it is not the central focus of this manuscript. Therefore, to avoid causing confusion for the reviewers and readers, we have removed the metabolism analysis in the Figure 4-figure supplement 1 and revised the presentation of the relevant results in the revised manuscript to ensure a more rigorous interpretation of our findings (Page 7-8, Line 186-194). 

(3) Do LPS-stimulated HGFS implementing the senescent programme secrete C3? Detection of complement C3 at the protein level (e.g. by ELISA) would reinforce the proposed mechanism.

This is indeed a very interesting question. In response to the reviewers' suggestion, we measured the levels of C3 protein secreted by human gingival fibroblasts induced by Pg-LPS, which is one of the markers of the senescence-associated secretory phenotype (SASP). The results indicated that, compared to untreated fibroblasts, those induced by Pg-LPS exhibited significantly higher levels of C3 secretion, approximately 1.5 times that of the control group (Figure. 5G). Additionally, we also found that primary gingival fibroblasts derived from periodontitis tissues secreted more complement C3 compared to those derived from healthy tissues (Figure. 5F). These findings suggest that the increased secretion of complement C3 by gingival fibroblasts in periodontitis tissues may be related to Pg-LPS-induced cellular senescence.

(4) The mechanism of Metformin to impair senescence and/or the SASP is not fully validated and Metformin can produce other pleiotropic effects. A key experiment (including therapeutic implications) is using a senolytic drug (e.g. Navitoclax) to causally connect the eradication of senescent CD81+ fibroblasts with the recruitment of neutrophils. If the hypothesis of the authors is correct this approach should result in reduced levels of gingival CD81 and C3 positivity, prevention of neutrophils infiltration (reduced MPO positivity), and ameliorate bone damage in ligationinduced periodontitis murine models.

We fully understand the reviewers' concerns regarding the role of metformin in alleviating cellular senescence and the possibility of it acting through non-senescent pathways. To clarify the role of cellular senescence in the recruitment of neutrophils by CD81+ fibroblasts through C3 in periodontitis, we treated a ligature-induced periodontitis mouse model with ABT-263, also known as Navitoclax. The results showed that after ABT-263 treatment, the number of p16-positive or H3K9me3-positive senescent cells in the periodontitis mice significantly decreased. Additionally, we observed reductions in the quantities of CD81+ fibroblasts, C3 protein levels, neutrophil infiltration, and osteoclasts to varying degrees in the LIP model after ABT263 treatment (Figure. 6). These results further support our hypothesis that the eradication of senescent CD81+ fibroblasts could reduce neutrophil infiltration and alveolar bone resorption. 

(5) Have the authors considered using any of the available C3/C3aR inhibitors to validate the involvement of neutrophils and the inflammatory response in periodontitis? A C3/C3aR inhibitor would be an elegant treatment group in parallel with the senolytic approach.

Thank you very much for the reviewers' suggestion to investigate neutrophil infiltration and inflammatory responses after treating periodontitis with C3/C3aR inhibitors. In a clinical study by Hasturk et al. in 2021 (Reference 1), it was found that using the C3 inhibitor AMY-101 effectively alleviated gingival inflammation levels in periodontitis patients. This was reflected in significant decreases in clinical indicators such as the modified gingival index and bleeding on probing, as well as a marked reduction in inflammatory tissue destruction markers, including MMP-8 and MMP-9. In addition, Tomoki Maekawa et al. (Reference 2) demonstrated that a peptide inhibitor of complement C3 effectively reduced inflammation levels and the extent of bone resorption in periodontitis. Moreover, research by Guglietta et al. (Reference 3) clarified that the C3 complement promotes neutrophil recruitment and the formation of neutrophil extracellular traps (NETs) via C3aR. And neutrophil extracellular traps are considered key pathological factors in causing sustained chronic inflammation in periodontitis (References 4 and 5). In summary, existing studies have clearly indicated that C3/C3aR inhibitors likely reduce neutrophil recruitment and inflammation in periodontitis. 

Reference

(1) Hasturk, H., Hajishengallis, G., Forsyth Institute Center for Clinical and Translational Research staff, Lambris, J. D., Mastellos, D. C., & Yancopoulou, D. (2021). Phase IIa clinical trial of complement C3 inhibitor AMY-101 in adults with periodontal inflammation. The Journal of clinical investigation, 131(23), e152973.

(2) Maekawa, T., Briones, R. A., Resuello, R. R., Tuplano, J. V., Hajishengallis, E., Kajikawa, T., Koutsogiannaki, S., Garcia, C. A., Ricklin, D., Lambris, J. D., & Hajishengallis, G. (2016). Inhibition of pre-existing natural periodontitis in non-human primates by a locally administered peptide inhibitor of complement C3. Journal of clinical periodontology, 43(3), 238–249.

(3) Guglietta, S., Chiavelli, A., Zagato, E., Krieg, C., Gandini, S., Ravenda, P. S., Bazolli, B., Lu, B., Penna, G., & Rescigno, M. (2016). Coagulation induced by C3aR-dependent NETosis drives protumorigenic neutrophils during small intestinal tumorigenesis. Nature communications, 7, 11037.

(4) Kim, T. S., Silva, L. M., Theofilou, V. I., Greenwell-Wild, T., Li, L., Williams, D. W., Ikeuchi, T., Brenchley, L., NIDCD/NIDCR Genomics and Computational Biology Core, Bugge, T. H., Diaz, P. I., Kaplan, M. J., Carmona-Rivera, C., & Moutsopoulos, N. M. (2023). Neutrophil extracellular traps and extracellular histones potentiate IL-17 inflammation in periodontitis. The Journal of experimental medicine, 220(9), e20221751.

(5) Silva, L. M., Doyle, A. D., Greenwell-Wild, T., Dutzan, N., Tran, C. L., Abusleme, L., Juang, L. J., Leung, J., Chun, E. M., Lum, A. G., Agler, C. S., Zuazo, C. E., Sibree, M., Jani, P., Kram, V., 6 Martin, D., Moss, K., Lionakis, M. S., Castellino, F. J., Kastrup, C. J., … Moutsopoulos, N. M. (2021). Fibrin is a critical regulator of neutrophil effector function at the oral mucosal barrier. Science (New York, N.Y.), 374(6575), eabl5450.

Other comments

(1) Figure 1. The authors report upregulation of the aging pathway in bulk RNAseq analyses. What about the upregulation of senescence-related pathways and differential expression of SASP-related genes in this experiment?

Thanks for this interesting question. Through further analysis of the bulk RNA sequencing results of gingival tissues from LIP mice model, we found significant alterations in multiple senescence-associated secretory phenotype (SASP) genes and several cellular senescencerelated pathways. SASP genes, such as Icam1, Mmp3, Nos3, Igfbp7, Igfbp4, Mmp14, Timp1, Ngf, Il6, Areg, and Vegfa, were markedly upregulated in the periodontitis samples of ligature-induced mice (Figure 1-figure supplement 2A). Moreover, we observed a significant reduction in oxidative phosphorylation levels and the tricarboxylic acid (TCA) cycle in the periodontitis group, suggesting that the occurrence of cellular senescence may be related to mitochondrial dysfunction (Figure 1figure supplement 2B and C.).

Additionally, we noted the activation of the PI3K-AKT and MAPK pathways in LIP model (Figure 1-figure supplement 2D and E), both of which can induce cellular senescence by activating the tumor suppressor pathway TP53/CDKN1A, leading to cell cycle arrest (References 1, 2). Furthermore, the NF-κB signaling pathway was also significantly enriched in LIP model (Figure 1-figure supplement 2F), which is closely associated with the secretion of SASP factors (Reference 3).

In summary, our bulk RNA sequencing results suggest enrichment of cellular senescencerelated pathways in the periodontitis group, including mitochondrial metabolic dysregulation, senescence-related pathways, and alterations in the SASP. Related results were added into Page 56 of the revised manuscripts.

Reference

(1) Tang Q, Markby GR, MacNair AJ, Tang K, Tkacz M, Parys M, Phadwal K, MacRae VE, Corcoran BM. TGF-β-induced PI3K/AKT/mTOR pathway controls myofibroblast differentiation and secretory phenotype of valvular interstitial cells through the modulation of cellular senescence in a naturally occurring in vitro canine model of myxomatous mitral valve disease. Cell Prolif. 2023 Jun;56(6):e13435. doi: 10.1111/cpr.13435.

(2) Sayegh S, Fantecelle CH, Laphanuwat P, Subramanian P, Rustin MHA, Gomes DCO, Akbar AN, Chambers ES. Vitamin D3 inhibits p38 MAPK and senescence-associated inflammatory mediator secretion by senescent fibroblasts that impacts immune responses during ageing. Aging Cell. 2024 Apr;23(4):e14093.

(3) Raynard C, Ma X, Huna A, Tessier N, Massemin A, Zhu K, Flaman JM, Moulin F, Goehrig D, Medard JJ, Vindrieux D, Treilleux I, Hernandez-Vargas H, Ducreux S, Martin N, Bernard D. NF-κB-dependent secretome of senescent cells can trigger neuroendocrine transdifferentiation of breast cancer cells. Aging Cell. 2022 Jul;21(7):e13632.

(2) I wonder whether the authors could clarify how the semi quantifications for p21, p16, Masson's trichrome, C3, or MPO were done in Figures 1, 2, and 6.

Thank you very much for the reviewer's suggestion. We have added the semi-quantitative methods for p21, p16, Masson's trichrome, C3, and MPO in the Methods section. Specifically, for semi-quantification of protein expressions, the mean optical density (MOD) of positive stains for p21, p16, and C3 was measured using the ImageJ2 software (version 2.14.0, National Institutes of Health, Bethesda, MD). The number of MPO-positive cells and collagen volume fractions (stained blue) for individual sections were also measured using the ImageJ2 software. (Page 19, Line 537-541 in the revised manuscripts).  

(3) Figure 2. It is unclear whether N=6 refers to 6 mice, maxilla, or fields per group.

Thank you very much for the reviewer's question. To avoid any misunderstandings for the reviewer and readers, we have added a definition of the sample size in the description of the micro-CT analysis method. Specifically, in the micro-CT quantitative analysis, the sample size n for each group consists of 6 mice, with the average value of the BV/TV of the bilateral maxillary alveolar bone taken as one sample for statistical analysis (Page 17-18, Line 488-490 in the revised manuscripts).  

(4)  igure 4K. Please provide separated staining for p16, VIM, and CD81, and not only the Merge. It is difficult to identify the triple-positive cells. Also, the arrows are difficult to observe.

Thank you very much for the reviewer's suggestion. In the revised manuscript, we have included separated staining for p16, VIM, and CD81, and the triple-positive cells are indicated with white arrows (Figure 5-figure supplement 1). 

(5) Overall, improve the magnifications in the IF experiments and show where the magnified areas come from.

Thank you very much for the reviewer's suggestion. We have enlarged the fluorescence result images.

(6) Refer to the original datasets of the scRNAseq results in figure legends.

Thank you very much for the reviewer's suggestion. We have indicated the source of the raw single-cell sequencing data in the figure legend.

(7) Check English grammar and writing.

Thank you for the reviewer's suggestion. We checked the grammar and writing in the revised manuscript assisted by a native English speaker and AI tools like Chat-GPT.

Reviewer #2 (Recommendations For The Authors):

(1) When the authors refer to accelerated aging and/or senescence, they are doing so in comparison to what?

Thank you for the reviewer's question, which allows me to further clarify the concepts of accelerated aging and/or senescence. In sections 2.1 and Figure 1 of this manuscript, we referred to accelerated aging and/or senescence. This indicates that the gingival tissues of periodontitis patients exhibit a higher number of senescent cells and elevated levels of senescence-related markers compared to healthy gingival tissues. In the title of this manuscript, we describe CD81+ fibroblasts as a unique subpopulation with accelerated cellular senescence. This means that CD81+ fibroblasts display higher expression levels of senescence-related genes, cell cycle inhibitor p16, and SASP factors compared to other fibroblast subpopulations. To avoid any misunderstanding, we have deleted the text ‘accelerated senescence’ in the revised manuscripts. 

(2) In general, the main text does not describe the results using exact and reproducible terminology. Phrases like "X was most active", "a significant increase was observed", "the highest proportion was", and "the level of aging increased" should be supported by adding quantification details and by detailing what these comparisons are made to, to improve the reproducibility of the results.

Thank you for the reviewer's suggestion. To improve the reproducibility of the results, we have added quantification details in the results section and clarified what comparisons are being made through the whole manuscript.

(3) In some sections of the main text and figure legends, it is not entirely clear which sequencing experiments were conducted by the authors, which analyses were conducted by the authors on publicly available sequencing data, and which analyses were conducted on their mouse sequencing data.

Thank you for the valuable feedback from the reviewer. To further clarify the source of the sequencing data, we have clearly indicated the data source in both the results section and the figure legends. 

(4) In Figure 3H, the images showing SA-beta-gal staining on LPS-treated fibroblasts do not show convincingly the difference between treatments that are represented in the graph.

Thank you for the reviewer's suggestion. To further clearly show the differences between treatments, we have enlarged the partial image of SA-β-gal staining shown in Figure 2-figure supplement 2 of the revised manuscripts. 

(5) The choice of colors for Figure 4K is far from ideal as it is very difficult to tell apart red from purple channels and thus to visualize triple positive cells. A different LUT should be chosen, and separate individual channels should be shown to clearly identify triple-positive cells from others. Arrows also do not currently point at triple-positive cells.

Thank you for the reviewer's suggestion. In the revised manuscript, we have included separated staining for p16, VIM, and CD81, and the triple-positive cells are marked with white arrows shown in Figure 5-figure supplement 1 of the revised manuscripts.  

(6) The authors state that treatment with metformin "alleviated.... inflammatory cell infiltration (Figure 2C), and collagen degradation (Figure 2D) as observed through H&E and Masson staining." However, I cannot find a description of how the "relative fraction of collagen" in Figure 2Gc was calculated and how the H&E image they provide shows evidence of a reduction in inflammatory cells at that magnification.

Thank you for the reviewer's suggestion. In the revised manuscript, we have added details in the methods section regarding the calculation of the "relative fraction of collagen" (Page 19, Line 539-541). Specifically, the collagen volume fractions (stained blue) for individual sections were measured using ImageJ2 software. Additionally, we have marked the infiltrating inflammatory cells in the gingiva in the H&E images with black arrows shown in Figure 7-figure supplement 1B of the revised manuscripts.

(7) It appears that the in vivo experiment for metformin treatment was conducted with 6 animals per group, but this is not clear in the figures, main text, and methods.

Thank you for the reviewer's suggestion. In the revised manuscript, we have included the number of mice in each group for the in vivo experiments, specifying that there are 6 mice per group in the figures, main text, and methods sections.

(8) The methodology described for the bulk RNA-sequencing experiment in mice should describe the sequencing library characteristics and some reference to quality control thresholds that were implemented (mapped and aligned reads, sequencing depth and coverage, etc.).

In the bulk RNA-sequencing experiment, the sequencing library characteristics and quality control thresholds were listed as follows:

Sequencing Library Characteristics: We utilized the Illumina TruSeq RNA Library Construction Kit, generating libraries with an insert fragment length of approximately 400-500 bp.

Quality Control Standards include the following:

Alignment and Mapping Rates: The read data for all samples underwent preliminary quality control using FastQC (v0.11.9) and were aligned using HISAT2 (v2.2.1). The average mapping rate for each sample was over 90%.

Sequencing Depth and Coverage: Each sample had a sequencing depth of 30M-40M paired reads to ensure sufficient transcript coverage. Detailed alignment statistics have been provided in the supplementary materials.

Other Quality Control Measures: During the analysis, we also utilized RSeQC (v3.0.1) to evaluate the transcript coverage and GC bias of the sequencing data.

The corresponding method description and reference were added in the Page 19-20, Line 546-558 of the revised manuscripts.

(9) Patients with periodontitis are labeled as diagnosed with "chronic periodontitis". I would like to know how the authors defined this chronic state of the disease in their inclusion criteria.

Thank you very much for the reviewer’s question, which gives us the opportunity to further clarify the definition and diagnosis of chronic periodontitis. The diagnostic criteria for patients with chronic periodontitis in this study are based on the 1999 International Workshop for a Classification of Periodontal Diseases and Conditions (Reference 1). Chronic periodontitis is a type of periodontal disease distinct from aggressive periodontitis, and it is not diagnosed based on the rate of disease progression. Clinically, the diagnosis of chronic periodontitis is primarily based on clinical attachment loss (CAL) ≥ 4 mm or probing depth (PD) ≥ 5 mm as one of the criteria for diagnosis.

Reference

(1) Armitage G. C. (2000). Development of a classification system for periodontal diseases and conditions. Northwest dentistry, 79(6), 31–35.

(10) There is no detail about the age and sex of the donors for the healthy gingival fibroblast experiments. Are they some of the patients mentioned in Supplementary Table 1? Please clarify the source and number of independent primary cultures.

Thank you very much to the reviewer for allowing us to further clarify the source and number of independent primary cultures. In the cell experiments, we used gingival fibroblasts derived from gingival tissue of two healthy volunteers and two patients with periodontitis as experimental subjects. This information has been listed in the Supplementary Table 1. 

(11) Can the authors explain why their age inclusion criteria were different for the healthy and periodontitis groups according to their methods (healthy 18-50 years old: periodontitis 18-35 years old?)

Thank you very much to the reviewer for pointing this out. We noticed that there was an error in the age range indicated for the healthy and periodontitis groups in the inclusion criteria. Based on the original inclusion criteria information, we have corrected the age range of the included population. 18-65 years old individuals were included into the both healthy and periodontitis groups. (Page 14-15, Line 396-404 in the revised manuscripts)

(12) The methodology for inclusion is confusing and does not reflect the actual information of the recruited patients and samples thus analyzed. In the text, the healthy group appears to have included 8 young adult individuals and 8 middle-aged individuals. However, the list of recruited patients shows all healthy patients were in the young adult range (below 35 years of age) while all chronic periodontitis patients were middle-aged (above 50 years of age). Please clarify.

Thank you very much to the reviewer for pointing out the issues in the article. This study included 8 healthy periodontal patients and 8 patients with periodontitis (Page 14, Line 396-398 and Supplementary Table 1 in the revised manuscripts). Since periodontitis has a higher prevalence in middle-aged and elderly populations, the periodontitis samples included in this study were mostly from this demographic. In contrast, the healthy gingival samples were sourced from patients undergoing wisdom tooth extraction, which primarily involves younger individuals. Therefore, due to the limited sample size, we could not enforce strict age matching. To address this, we repeated the relevant experiments in more consistent mouse models, which confirmed the increase in senescent cells in periodontal tissues (Figure 1D in the revised manuscripts). In summary, although the clinical samples were limited, the experimental results from the mouse models still support our conclusions.

(13) The number of biological replicates for each group used in the bulk RNA-sequencing experiment is unclear. The methods state:" For those with biological duplication, we used DESeq2 [8] (version: 1.34.0) to screen differentially expressed gene sets between two biological conditions; for those without biological duplication, we used edgeR". Please clarify the number of mouse samples sequenced and the description of the groups.

Thank you very much to the reviewer for pointing out the errors in the article. In the transcriptome sequencing, we collected gingival tissues from 3 healthy mice and gingival tissues from 3 ligature-induced periodontitis mice. Therefore, we used the DESeq2 (version: 1.34.0) method to filter for differentially expressed genes. The corresponding descriptions were revised in Page 20, Line 554-555 in the revised manuscripts.

(14) Cluster group labels are misaligned in Figure 4C.

Thank you very much for the reviewer's suggestion. The cluster group labels in Figure 3C of the revised manuscripts have been aligned.

Reviewer #3 (Recommendations For The Authors):

Major Comments for the Authors:

(1) I do not find the immunohistochemical staining of p16 and p21 shown in Figures 2E and F to be particularly compelling. Especially as other stains of these markers used later in the manuscript are of higher quality (i.e. Figures 3F and G). Can this staining be improved to better reflect the quantifications in Figure 2G?

Thank you very much for the reviewer's suggestion. In the revised manuscript, we have provided more representative images in Figure 7C in the revised manuscripts to reflect the effect of metformin treatment on the number of p16-positive cells in periodontitis. In Figure 7-figure supplement 1D of the revised manuscripts, we have marked p21-positive cells with black arrows to help readers better identify the p21-positive cells. Additionally, we have also assessed the H3K9me3 marker, which is more specific, and the results similarly indicate that metformin treatment can alleviate the formation of senescent cells in periodontitis (Figure 7-figure supplement 1E of the revised manuscript).

(2) On line 140, Supplementary Figure 2C, D is quoted to show "...an increase in senescence characteristics of fibroblasts with the severity of periodontitis." This figure panel does not appear to support this statement. Please revise.

Thank you very much for pointing out the errors in the manuscript. In the revised version, we have corrected this part of the description and added that “The results showed a decline in fibroblast proportion along with increasing disease severity (Figure 2-figure supplement 1C and D)” (Page 6, Line 153-154 of the revised manuscript)

(3) I do not find the Western Blot experiment in Figure 4L to be particularly convincing. The text states that p21, p16, and CD81 increase in a context-dependent manner upon LPS stimulation, which doesn't appear to be very evident. I recommend repeating this experiment and showing both a representative blot alongside a blot density quantification where the bars have the error shown between experiments.

Thank you very much for the reviewer’s suggestion regarding this result. During subsequent repeated experiments, we found that the result was not reproducible, and we have removed the related results.

(4) The results state that metabolic profiling of senescent fibroblasts shows an increase in the biosynthesis of Linoleic acid, linolenic acid, arachidonic acid, and steroid. However, in Figure 5B only arachidonic acid and steroid biosynthesis appear to be elevated in CD81+ Fibroblasts, while Linoleic and linolenic acid appear to be decreased. Can the authors comment on this discrepancy? Moreover, in Figure 5C steroid biosynthesis is unchanged between healthy and periodontitis samples, contrary to the claimed increased trend in the results text. Please revise this section. Also, in Figures 5 B and C some of the terms are highlighted in a red or blue box. This is not discussed in the figure legend. Could the significance of this be explained or could these highlights be removed from the figure?

Thank you very much for the reviewer’s correction regarding the errors in the manuscript. In the Page 7-8, Line 186-194 of the revised manuscripts, “Pathways related to fatty acid biosynthesis, arachidonic acid metabolism, and steroid biosynthesis were significantly upregulated in CD81+ fibroblasts (Figure 4-figure supplement 1A)” was re-wrote. Moreover, we have removed the results from Figure 5C, and the highlights in Figures 5B and C of the previous manuscripts. Since the mechanism by which cellular metabolism regulates cellular senescence is not the core focus of this manuscript, we have moved the results of the metabolic analysis from the sc-RNA sequencing data to the figure supplement (Figure 4-figure supplement 1) and revised the related statements in the revised manuscript (Page 7-8, Line 186-194).

(5) The authors state that arachidonic acid can be converted to prostaglandins and leukotrienes through COXs (which are expressed in their CD81+ Fibroblasts), accentuating inflammatory responses. Have the authors profiled for the expression of prostaglandins and leukotrienes in their CD81+ Fibroblasts or between healthy and periodontitis samples? Such data would be a great inclusion in the manuscript.

Thank you very much for the reviewer’s suggestion. Our results indicated that CD81+ gingival fibroblasts expressed higher levels of PTGS1 and PTGS2 compared to other fibroblast subpopulations. These genes encode proteins that are COX-1 and COX-2, which are key enzymes in prostaglandin biosynthesis (Figure 4-figure supplement 1 of the revised manuscript). Additionally, previous studies have reported high levels of prostaglandins and leukotrienes in periodontal tissues, and these pro-inflammatory mediators contribute to tissue destruction in periodontitis (Reference 1 and 2).

Reference

(1) Van Dyke, T. E., & Serhan, C. N. (2003). Resolution of inflammation: a new paradigm for the pathogenesis of periodontal diseases. Journal of dental research, 82(2), 82–90.

(2) Hikiji, H., Takato, T., Shimizu, T., & Ishii, S. (2008). The roles of prostanoids, leukotrienes, and platelet-activating factor in bone metabolism and disease. Progress in lipid research, 47(2), 107–126.

(6) Lines 199 and 200 state "...the cellular senescence of CD81+ fibroblasts could be attributed to disturbances in lipid metabolism". While altered lipid metabolic profiles are shown in Figure 5 to correlate with senescent fibroblasts/periodontitis tissue, no evidence is shown to suggest that they are the driver or cause of fibroblast senescence. Could this sentence be amended to better reflect the conclusions that can be drawn from the data presented?

Thank you very much for the reviewer’s suggestion. We have revised the related statements and believed that “lipid metabolism might play a role in cellular senescence of the gingival fibroblasts” in the Page 7, Line 189 of the revised manuscripts.  

Minor Comments for the Authors:

(1) There are some sentences without references that I feel would warrant referencing: - Line 112 - "Metformin, an anti-aging drug has shown potential in inhibiting cell senescence in various disease models (REFERENCE)."

Thank you for the reviewer's suggestion. We have included the relevant references in the Page10, Line 267-271 of the revised manuscripts.

Reference

(1) Soukas, A. A., Hao, H., & Wu, L. (2019). Metformin as Anti-Aging Therapy: Is It for Everyone?. Trends in endocrinology and metabolism: TEM, 30(10), 745–755.

(2) Kodali, M., Attaluri, S., Madhu, L. N., Shuai, B., Upadhya, R., Gonzalez, J. J., Rao, X., & Shetty, A. K. (2021). Metformin treatment in late middle age improves cognitive function with alleviation of microglial activation and enhancement of autophagy in the hippocampus. Aging cell, 20(2), e13277.

- Line 210 - "Previous studies have demonstrated the importance of sustained neutrophil infiltration in the progression of periodontitis (REFERENCE)."

Thank you for the reviewer's suggestion. We have included the relevant references in the Page 8, Line 211-214 of the revised manuscripts.

Reference

(1) Song, J., Zhang, Y., Bai, Y., Sun, X., Lu, Y., Guo, Y., He, Y., Gao, M., Chi, X., Heng, B. C., Zhang, X., Li, W., Xu, M., Wei, Y., You, F., Zhang, X., Lu, D., & Deng, X. (2023). The Deubiquitinase OTUD1 Suppresses Secretory Neutrophil Polarization And Ameliorates Immunopathology of Periodontitis. Advanced science (Weinheim, Baden-Wurttemberg, Germany), 10(30), e2303207.

(2) Kim, T. S., Silva, L. M., Theofilou, V. I., Greenwell-Wild, T., Li, L., Williams, D. W., Ikeuchi, T., Brenchley, L., NIDCD/NIDCR Genomics and Computational Biology Core, Bugge, T. H., Diaz, P. I., Kaplan, M. J., Carmona-Rivera, C., & Moutsopoulos, N. M. (2023). Neutrophil extracellular traps and extracellular histones potentiate IL-17 inflammation in periodontitis. The Journal of experimental medicine, 220(9), e20221751.

(3) Ando, Y., Tsukasaki, M., Huynh, N. C., Zang, S., Yan, M., Muro, R., Nakamura, K., Komagamine, M., Komatsu, N., Okamoto, K., Nakano, K., Okamura, T., Yamaguchi, A., Ishihara, K., & Takayanagi, H. (2024). The neutrophil-osteogenic cell axis promotes bone destruction in periodontitis. International journal of oral science, 16(1), 18.

(2) To improve the quality of several of the authors' claims I would recommend some further quantification of their experimental analyses. Namely:

- Figures 3 F and G

- Figures 4 I, J and K

- Figures 6 F and G

- Supplementary Figures 4 A, B, and C

Thank you for the reviewer's suggestion. We have supplemented the quantitative analysis results for some images based on the reviewer's recommendations, specifically in Figure. 2G, Figure. 3G, Figure 5-figure supplement 1A, B, Figure 5-figure supplement 2A and Figure 7figure supplement 3A-D in the revised manuscripts. 

(3) Figure 1L has missing x-axis annotation.

Thank you for the reminder from the reviewer. The X-axis label has been added in Figure 1-figure supplement 1D for the GO term annotation. 

(4) Line 117 is missing a reference for the experimental schematic shown in Figure 2A.

Thank you for the reminder from the reviewer. The experimental schematic shown in Figure 7A has been referenced in Page 10, Line 275-277.

(5) The "BV/TV ratio" and "CEJ-ABC distance" should be briefly explained in the results test (Lines 118 and 119).

Thank you for the reviewer's suggestion. We have added the explanation of "BV/TV ratio" and "CEJ-ABC distance." In Page 10-11, Line 279-281 in the revised manuscripts.

(6) Figure 2 could be improved by having some annotation for the anatomical regions shown.

Thank you for the reviewer’s valuable suggestion. We have labeled the relevant anatomical structures to enhance clarity in Figure 7 in the revised manuscripts. 

(7) The positive signal for p16 and p21 is difficult to interpret in Figure 2. Could the clarity of this be improved either by using more evident images or annotation with arrowheads indicating positive cells?

Thank you for the reviewer's suggestion. In the revised manuscript, we have provided more representative images in Figure. 7C in the revised manuscripts to reflect the effect of metformin treatment on the number of p16-positive cells in periodontitis. In Figure 7-figure supplement 1D of the revised manuscripts, we have marked p21-positive cells with black arrows to help readers better identify the p21-positive cells. Additionally, we have also assessed the H3K9me3 marker, which is more specific, and the results similarly indicate that metformin treatment can alleviate the formation of senescent cells in periodontitis (Figure 7-figure supplement 1E of the revised manuscript).

(8) Figure 2Gc, d, and e are not mentioned in the results text. Please include references to these panels at the appropriate points.

Thank you for the reminder. In the revised manuscripts, Figures 2G c, d, and e in the previous manuscripts have been mentioned in the text in the Page 11, Line 284-289 of the revised manuscript. 

(9) Scale bars are missing in Supplementary Figure 2E.

Thank you for the suggestion. The scale bar has been added in the Figure 7-figure supplement 2B in the revised manuscripts. 

(10) The order of the figure panels is not always mentioned in the order they are referred to in the text. For example, Figure 3 is presented in the order of A, B, D then C. Could this be changed to reflect the order in the results text?

Thank you for the feedback. We have renumbered the figures according to the order mentioned in the original manuscript (Page 6, Line 146-149, Figure 2 in the revised manuscripts).

(11) To improve reader clarity it would be good to briefly introduce the gene expression datasets analysed, such as GSE152042. I.e. what the experimental condition is from which it is derived.

Thank you for the suggestion. We have included a brief description of the information and sources of the samples from GSE152042 in Page 6, Line 140-142 of the revised manuscripts. 

(12) To improve reader clarity I would recommend signifying clearly in the figure if the data shown is from mouse or human samples. For example in Figure 3F and G.

Thank you for the suggestion. We have moved all the results from the mouse experiments to the figures supplement (Figure 5-figure supplement 1 and 2 in the revised manuscripts).

(13) The images shown in Figure 3H for SA-beta-Gal do not seem very convincing. Could this be improved?

Thank you for the suggestion. To further illustrate the differences in SA-beta-Gal results between the groups, we have provided images at higher magnification in the Figure 2-figure supplement 2 of the revised manuscripts.  

(14) Supplementary Figure 2E would benefit from small experimental schematics that would allow the reader to appreciate the timings of the treatment for this experiment.

Thank you for the suggestion. We have added a schematic diagram in Figure 7-figure supplement 2A of the revised manuscripts to illustrate the LPS treatment, metformin treatment, and the timing of the assessments. 

(15) Figure 4K would benefit from showing the merged image and single channels of each of the stains to better assess the degree of colocalisation.

Thank you for the suggestion. We have included each individual fluorescence channel in Figure 5-figure supplement 1C of the revised manuscripts. 

(16) The writing on the X-axis of Figure 6B is almost illegible to me, although this may just be a compression artefact. This makes the interpretation of the data quite difficult. Also, for Figures 6 B and C, the meaning of the (H) and (P) annotations should be clear on either the figure or figure legend. I surmise that they represent "Healthy" and "Periodontic" samples respectively.

Thank you for the suggestion. In the revised manuscript, we have enlarged Figure 6B in the previous manuscripts to better display the X-axis as shown in the Figure 5B of the revised manuscripts. Additionally, we have fully labeled "Healthy" and "Periodontitis" in Figure 5C of the revised manuscripts.

(17) MPO-positive cells are introduced on line 216, however, no explanation is provided for what population or state the expression of this protein marks. I surmise the authors are using it to detect Neutrophil populations. If so, could the authors briefly state this the first time it is used?

Thank you for the suggestion. In the revised manuscript, we have added an introduction to MPO. MPO, or myeloperoxidase, is considered one of the markers for neutrophils. (Page 9, Line 240-242 of the revised manuscripts)

(18) Supplementary Figure 3D does not appear to be mentioned or discussed in the results text.

Thank you for the reminder. We have referenced Supplementary Figure 3D in the previous manuscripts in Page 9, Line 240-242 shown as Figure 5-figure supplement 2C of the revised manuscript.  

(19) Figure 6E showing increased C3 expression in periodontic samples is not very convincing and differences in expression are not evident. Can the authors provide an image that more convincingly matches their quantification?

Thank you for the suggestion. In the revised manuscript, we have provided more representative images shown in Figure 5E of the revised manuscript.

(20) Figure 6I shows the expression of CD81 and SOD2 in healthy and periodontic tissue. The associated results texts (Lines 220 to 223) discuss the spatial coincidence of CD81 and MPO. Can the authors address this discrepancy in either the results text or the figure panel? Moreover, can Figure 6H and I be annotated to show the location of the gingival lamina propria to improve clarity?

Thank you for the reminder. We have revised the relevant statements in the text: "Interestingly, spatial transcriptomic analysis of gingival tissue revealed that the regions expressing CD81 and SOD2, a neutrophil marker, in periodontitis overlapped in the gingival lamina propria, showing a high spatial correlation" in Page 9, Line 223-226 of the revised manuscripts. Additionally, we have labeled the gingival lamina propria (LP) in Figure 5H of the revised manuscripts.

(21) I am confused about the purpose of Supplementary Figure 3E and what evidence it provides. Can the authors comment on this?

Thank you for the reminder. To avoid any potential misunderstanding by readers, we have deleted Supplementary Figure 3 image in the revised manuscripts

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this paper, Wang et al show that differentiated peridermal cells of the zebrafish epidermis extend cytoneme-like protrusions toward the less differentiated, intermediate layer below. They present evidence that expression of a dominant-negative cdc42, inhibits cytoneme formation and leads to elevated expression of a marker of undifferentiated keratinocytes, krtt1c19e, in the periderm layer. Data is presented suggesting the involvement of Delta-Notch signaling in keratinocyte differentiation. Finally, changes in expression of the inflammatory cytokine IL-17 and its receptors is shown to affect cytoneme number and periderm structure in a manner similar to Notch and cdc42 perturbations.

Strengths:

Overall, the idea that differentiated cells signal to underlying undifferentiated cells via membrane protrusions in skin keratinocytes is interesting and novel, and it is clear that periderm cells send out thin membrane protrusions that contain a Notch ligand. Further, perturbations that affect cytoneme number, Notch signaling, and IL-17 expression clearly lead to changes in periderm structure and gene expression.

Weaknesses:

More work is needed to determine whether the effects on keratinocyte differentiation are due to a loss of cytonemes themselves, or to broader effects of inhibiting cdc42. Moreover, more evidence is needed to support the claim that periderm cytonemes deliver Delta ligands to induce Notch signaling below. Without these aspects of the study being solidified, understanding how IL-17 affects these processes seems premature.

Reviewer #2 (Public Review):

Summary:

The aim of the study was to understand how cells of the skin communicate across dermal layers. The research group has previously demonstrated that cellular connections called airinemes contribute to this communication. The current work builds upon this knowledge by showing that differentiated keratinocytes also use cytonemes, specialized signaling filopodia, to communicate with undifferentiated keratinocytes. They show that cytonemes are the more abundant type of cellular extension used for communication between the differentiated keratinocyte layer and the undifferentiated keratinocytes. Disruption of cytoneme formation led to the expansion of the undifferentiated keratinocytes into the periderm, mimicking skin diseases like psoriasis. The authors go on to show that disruption of cytonemes results in perturbations in Notch signaling between the differentiated keratinocytes of the periderm and the underlying proliferating undifferentiated keratinocytes. Further, the authors show that Interleukin-17, also known to drive psoriasis, can restrict the formation of periderm cytonemes, possibly through the inhibition of Cdc42 expression. This work suggests that cytoneme-mediated Notch signaling plays a central role in normal epidermal regulation. The authors propose that disruption of cytoneme function may be an underlying cause of various human skin diseases.

Strengths:

The authors provide strong evidence that periderm keratinocytes cytonemes contain the notch ligand DeltaC to promote Notch activation in the underlying intermediate layer to regulate accurate epidermal maintenance.

Weaknesses:

The impact of the study would be increased if the mechanism by which Interlukin-17 and Cdc42 collaborate to regulate cytonemes was defined. Experiments measuring Cdc42 activity, rather than just measuring expression, would strengthen the conclusions.

Reviewer #3 (Public Review):

Summary:

Leveraging zebra fish as a research model, Wang et al identified "cytoneme-like structures" as a mechanism for mediating cell-cell communications among skin epidermal cells. The authors further demonstrated that the "cytoneme-like structures" can mediate Notch signaling, and the "cytoneme-like structures" are influenced by IL17 signaling.

Strengths:

Elegant zebrafish genetics, reporters, and live imaging.

Weaknesses: (minor)

This paper focused on characterizing the "cytoneme-like structures" between different layers and the NOTCH signaling. However, these "cytoneme-like structures" observed in undifferentiated KC (Figure 2B), although at a slightly lower frequency, were not interpreted. In addition, it is unclear if these "cytoneme-like structures" can mediate other signaling pathways than NOTCH.

We are currently investigating the role of cytoneme-like protrusions extended from undifferentiated keratinocytes and their role is still under investigation. We believe that addressing the function of undifferentiated keratinocyte cytonemes and exploring whether peridermal cytoneme can mediate other signaling pathways is beyond the scope of the current manuscript. However, we hope to publish our discoveries about them soon. It is worth noting that cytonemes mediate other morphogenetic signals, such as Hh, Wnt, Fgf, and TGFbeta in other contexts.

Overall, this is a solid paper with convincing data reporting the "cytoneme-like structures" in vivo, and with compelling data demonstrating the roles in NOTCH signaling and the regulation by IL17.

These findings provide a foundation for future work exploring the "cytoneme-like structures" in the mammalian system and other epithelial tissue types. This paper also suggests a potential connection between the "cytoneme-like structures" and psoriasis, which needs to be further explored in clinical samples.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major points

- In general, representative images from each experiment should accompany the graphs shown. The inclusion of still frames from time-lapse imaging experiments in the main figures would help the reader understand the morphology and dynamics of these protrusions in control, cdc42, and IL-17 manipulations.

Thank you for the comments. We appreciate your suggestion to include representative images alongside the graphs to better illustrate the morphology and dynamics of these protrusions.

In response, we have made the following additions to our main figures.

Figure 3A now includes still images from time-lapse movies for both control and cdc42 manipulations.

Figure 5A and 6A,C now include still images for il17 manipulations.

- Data in Figure 3 is crucial as it demonstrates that cdc42DN selectively impairs cytoneme extensions without affecting other actin-based structures. It also shows that cdc42DN leads to upregulation of krtt1c19e in periderm. Therefore, these data should be presented in a comprehensive way. Still, frames of high mag views of time-lapse images from control and cdc42DN should be included in the figure. Similarly, a counter label (E-Cadherin, perhaps) showing the presence of all three layers and goblet cells at different focal planes capturing the different layers of the skin should be included. It is stated that the goblet cell number is unaffected, but they seem to be absent in the image shown in Figure 3B.

In this revised version, we have included magnified cross-sectional views. In addition to the images of the peridermal layer from the original version, we have now included the underlying intermediate and basal stem cell layers (Figure 3C-C”). We hope these data convincingly show that peridermal keratinocytes in cytoneme inhibited animals co-express krt4 and krtt1c19e markers, suggesting that peridermal keratinocytes are not fully differentiated.

We agree that the goblet cells in this particular image of experimental group appear largely absent, however, as we quantified many animals, the number of goblet cells was not significantly different between controls and experimental (Figure S2).

- The effects on periderm architecture upon broad cdc42 inhibition may not be directly due to a loss of cytonemes. Performing this experiment in a mosaic manner to determine if the effects are local and in the range of cytoneme protrusion would strengthen the conclusions. Adding a secondary perturbation to inhibit cytoneme formation in periderm cells would also strengthen the conclusions that defects are not related specifically to cdc42 inhibition, but cytonemes themselves.

Thank you for the suggestion. We confirmed that mosaic expression of cdc42DN in peridermal keratinocytes elicited local disorganization, and elevated krtt1c19e expression as we seen in transgenic lines. Also, the cdc42DN expressing cells exhibited significantly lower cytoneme extension frequency.

In addition, we found that like cdc42DN, rac1DN expressing keratinocytes exhibited significant decrease in cytoneme extension frequency, but rhoabDN show no effects (new Figure S3). These data suggest that cytoneme extension is regulated by cdc42 and rac1 but not rhoab. Further investigation is required however, at least these data suggest that the effects we observe is likely the loss of cytonemes not just specifically to cdc42 inhibition.

- Figure 4. The inclusion of an endogenous reporter of Notch activity, like Hes or Hey immunofluorescence, would strengthen the conclusion that the intermediate layer is Notch responsive.

Thank you for the suggestion. In this revised version, we have included immunostaining data in Figure 4D demonstrating that Her6 (the orthologous to human HES1) protein is expressed in the intermediate layer.

- It is not clear where along a differentiation trajectory Notch signaling and cytonemes are needed. What happens to the intermediate layer when Notch signaling or cdc42 is inhibited? Do the cells become more basal-like? Or failing to become periderm? Meaning - is Notch promoting the basal to intermediate fate transition, or the intermediate to periderm transition? A more comprehensive characterization of basal, intermediate, and periderm differentiation with markers selective to each layer would help define which step in the process is being altered.

Notch signaling is known to regulate keratinocyte terminal differentiation. Thus, it requires in the process from intermediate to peridermal transition. We observed peridermal keratinocytes still strongly express krt19 suggesting their terminal differentiation is inhibited when cytoneme mediated Notch signaling is compromised.

As seen on Figure 3C”, peridermal keratinocytes express both krt4 and krtt1c19e markers and they are located at the peridermal layer suggesting that they are not fully differentiated keratinocytes. As we included the images of intermediate and basal layers, we do not observe any noticeable defects in basal stem cells or complete depletion of intermediate keratinocytes (Fig 3C-C”). These observations suggest that notch signaling, activated by cytonemes, is required for the differentiation of undifferentiated intermediate keratinocytes into peridermal keratinocytes.

We included this interpretation in the main text.

- A number of times in the text it is suggested that cytonemes, Notch, and IL-17 signaling are essential for keratinocyte differentiation and proliferation, but proliferation (% cells in S-phase and M-phase) is not measured. Also, #of keratinocytes @ periderm is not an accurate way to report the number of cells in the periderm unless every cell in the larvae has been counted. It should be # cells/unit area.

In this revised version, we confirmed that the number of Edu+ cells among peridermal keratinocytes are significantly increased when cytonemes are inhibited (Figure 3F-G). Also, as indicated in the methods section, we indeed counted the cells in 290um x 200um square. We believe both of the data sufficiently suggest that the number of keratinocytes in periderm is significantly increased due to the lack of proper cytoneme mediated signaling.

- If the model is correct that Delta ligands from the periderm signal to intermediate cells to promote their differentiation and inhibit their proliferation, then depletion of Delta from Krt4 expressing cells should recapitulate the periderm phenotype.

It is a great suggestion. However, zebrafish skin express multiple delta ligands and we do not know what specific combination of Deltas are delivered via cytonemes. In this manuscript we identified Dlc is expressed along the cytonemes and krt4+ cells (revised Figure S4), however we are unsure whether other Delta ligands involve the notch activation. However, cytoneme inhibition is performed specifically in krt4+ cells and the downregulation of Notch activation are observed in krtt1c19e+ undifferentiated keratinocytes. In this revised version, we found that a Notch responsive protein Her6 is exclusively expressed in the cytoneme target keratinocytes, and cytoneme extending cells (krt4+) do not express Notch receptors.

- rtPCR data in Figure S3 is not properly controlled. Each gene should be tested in both krt4 and krtt1c19e expressing cells to determine their relative expression levels in different skin layers that are proposed to signal to one another. Are Notch ligands present in basal cells? These could be activating Notch in the intermediate layer.

Our intention was to merely confirm the Notch signaling components are expressed in cytoneme extending and receiving cells. Based on the new panel of RT-PCRs for notch signaling components, we confirmed again that dlc is expressed in cytoneme extending cells but not in receiving cells. Basal cells are also krtt1c19e+ but we did not detect dlc from them. Interestingly, we found that notch 2 is exclusively expressed in krtt1c19e+ cells but not from krt4+ cytoneme extending cells (now new Figure S4).

- It is not intuitive why NICD (activation) and SuHDN (inhibition) of Notch signaling should result in a similar effect on the periderm. What is the effect of NICD expression on the TP1:H2BGFP reporter? Does it hyperactivate as expected?

We agree reviewer’s concerns. It is well studied that psoriasis patients exhibits either loss or gain of notch signaling (Ota et al., 2014 Acta Histochecm Cytochem, Abdou et al., 2012 Annals of Diagnostic Pathology). However, it remains unknown the underlying mechanisms. We merely intended to showcase our zebrafish experimental manipulations recapitulate human patients’ case. However, we believe this data doesn’t require for drawing the overall conclusion but need further investigation to explain it. Thus, if the reviewers agree we want to omit it in this manuscript and leave it for future studies.

- Due to the involvement of immune signaling in hyperproliferative skin diseases the paper then investigates the role of IL-17 on cytoneme formation by overexpressing two IL-17 receptors in the periderm. Fewer cytonemes were present in the receptor over-expressing periderm cells. The rationale for overexpressing the receptors was unclear. If relevant to endogenous cytokine signaling, the periderm would be expected to express IL-17 receptors normally and respond to elevated levels of IL-17.

The rationale behind the reason of why we overexpress the IL-17 receptors is to test its autonomy of krt4+ peridermal cells. There is a debate that whether the onset of psoriasis is autonomous to keratinocytes or non-autonomous effects of immune malfunction. In addition to the overexpression of IL-17 receptors, we showed that the IL-17 ligand overexpression shows the sample effects on cytoneme extension (Fig. 6A-B).

- Experiments overexpressing IL-17 in macrophages are also suggested to limit cytoneme number whereas heterozygous deletion elevates them. Representative images and movies should be included to support the data. Western blots or immunofluorescence showing that IL-17 and its receptors are indeed overexpressed in the relevant layers/cell types should also be included as controls. Knockout of IL-17 protein in the new Crispr deletion mutant should also be shown.

In response to the reviewer’s comments, we have included representative images of peridermal keratinocytes in IL-17 ligand overexpressed and il17 CRISPR KO animals (Fig. 6A,C).

We have confirmed the overexpression of Il17rd, Il17ra1a and Il17a in the transgenic animals. For the il17 receptors, we FACS-sorted differentiated keratinocytes and performed qRT-PCR. Similarly, for the il17 ligand, we isolated skin tissue and conducted qRT-PCR (new Figure S7).

Additionally, we confirmed that IL-17 protein expression is undetectable in il17a CRISPR KO fish (Fig. S8C).

- Evidence that the effect of IL-17 upregulation on periderm architecture is via cytonemes is suggestive but not conclusive. Can the phenotype be rescued by a constitutively active cdc42?

We appreciate the reviewer’s suggestion. We are unsure whether constitutively active cdc42 expression can rescue IL-17 overexpression mediated reduction of cytoneme extension frequency. It is well expected that cdc42CA will stabilize actin polymerization in turn more cytonemes. However, it is also known sustained cdc42 activation can paradoxically lead to actin depolymerization. Thus, we concern it will be likely uninterpretable. Also, we need to generate a new transgenic line for this experiment and the baseline control experiments and validations take substantial amount of time and efforts with no confidence.

We and others believe that the cdc42 is a final effector molecule to regulate cytoneme extension given its role in actin polymerization. we provided the evidence that IL-17 overexpression significantly reduced cdc42 and rac1 expression (Figure 6E) and co-manipulation with IL17 overexpression and cdc42DN led to further down-regulation of cytoneme extension frequency in peridermal keratinocytes (Figure 6H).

- In a final experiment, the authors mutate a psoriasis-associated gene, clint1a gene and show an effect on cytonemes, Notch output, and periderm structure. More information about what this gene encodes, where the mRNA is expressed, and where the cell the protein should localize would help place this result in context for the reader.

In this revised manuscript we included more information about the clint1.

“The clathrin interactor 1 (clint1), also referred to as enthoprotin and epsinR functions as an adaptor molecule that binds SNARE proteins and play a role in clathrin-mediated vasicular transport (Wasiak, 2002). It has also been reported that clint1 is expressed in epidermis and play an important role in epidermal homeostasis and development in zebrafish (Dodd et al., 2009)”.

Minor points

- The architecture of zebrafish skin is notably distinct from that of humans and other mammals and whether parallels can be drawn with regards to cytoneme mediated signaling requires further investigation. For this reason, I believe the title should include the words 'in zebrafish skin'.

In this version, we changed the title as ‘Cytoneme-mediated intercellular signaling in keratinocytes essential for epidermal remodeling in zebrafish’.

- More details about the timing of cdc42 inhibition should be given in the main text to interpret the data. How many hours of days are the larvae treated? How does this compare to the rate of division and differentiation in the zebrafish larval epidermis?

We apologize for omitting the detailed experimental conditions for cytoneme inhibition. We have revised the main text as follows “Although the cytoneme inhibition is evident after overnight treatment with the inducing drugs, noticeable epidermal phenotypes begin to appear after 3 days of treatment. This reflects the higher cytoneme extension frequency and their potential role during metamorphic stages, which takes a couple of weeks (Figure 1C)”

- What are the genotypes of animals in Figure 4B where 'Notch expression' is being measured upon cdc42DN inhibition? Is this the TP1:H2B-GFP reporter? Again, details of the timing of this experiment are needed to evaluate the results.

We indicated the reference supplement figure for the Notch activity measure in the figure legend S4. And we added the following sentence in the main text. “Similar to the effects on the epidermis after cytoneme inhibition (Figure 3), it takes 3 days to observe a significantly reduction in Notch signal in the undifferentiated keratinocytes.”

Reviewer #2 (Recommendations For The Authors):

- Figure 2B: the authors indicate that the undifferentiated keratinocytes (krtt1c19e+) do extend some cytonemes. Although this behavior is not a focus of the study, it would be helpful to see an image of krtt1c19e:lyn-tdTomato cytonemes. The discussion ends with an interesting statement about downward pointed protrusions coming off the undifferentiated keratinocytes. A representative image of this should be included in Figure 2.

In this revised version, we included an image of krtt1c19e positive cell that extend cytonemes in Figure 2C.

- The evidence for hyperproliferation of the undifferentiated keratinocytes would be strengthened by quantifying proliferation. Most experiments result in increased expression of krtt1c19e in the periderm layer, but it is unclear whether this is invasion, remodeling, or incomplete differentiation of the cells. Notch suppression with krtt1c19e:SuHDN and overactivation with krtt1c19e:NICD phenocopy each other. Are there differences in proliferation vs differentiation rates in these two genotypes that result in a similar phenotype?

We appreciate the reviewer’s comments. In response to the feedback, we included Edu experiments that show increased cell proliferation in keratinocytes in periderm in experimental groups. Additionally, we observed co-expressed of both differentiated marker krt4 and undifferentiated marker krtt1c19e in the keratinocytes in periderm. Since we did not observe depletion of intermediate layer, we believe it is reasonable to conclude that the phenotype represents incomplete differentiation (new Figure 3). For the krtt1c19e:NICD question, please refer to our response to reviewer #1’ comment.

- Do Cdc42DN and il17rd or il17ra1a work in parallel or in a hierarchy of signaling events to regulate cytoneme formation?

Cdc42 is widely recognized as a final effector in cytoneme extension, given its well-established role in actin polymerization, which is critical for cytoneme extension. Our data support a model where il17 signaling acts upstream of cdc42. We showed that the overexpression of il17rd or il17ra1a significantly reduced the expression of Cdc42 (Figure 6E). In double transgenic fish overexpressing il17rd and cdc42DN, we observed a more marked decrease in cytoneme extension compared to single transgenic (Figure 6H). These results collectively indicate that, at least partially, Cdc42 functions downstream of il17 signaling in the context of cytoneme formation. However, we acknowledge that additional regulatory mechanisms may be involved, given the complexity of cellular signaling networks.  

- Figure 6C: Are the effects of overexpression of il17rd specific to Cdc42, or are other Rho family GTPases like Rac and Rho also affected? Is the microridge defect (Figure 6D) also present in Tg(krt4:TetGBDTRE-v2a-cdc42DN) when induced, or could this be regulated by Rho/Rac?

We used the microridge formation as a readout to evaluate the effects of il17receptor overexpression on actin polymerization. In this revision, we demonstrate that the expression of other small GTPases is also decreased in il17rd or il17ra1a overexpressed keratinocytes (Figure 6E). Also, we confirmed that microridges exhibit significantly shorter branch length when cdc42DN or rac1DN is overexpressed (new Figure S9). It is note that we have shown that the effects on cytonemes are regulated by cdc42 and rac1 (new Figure S3).

- Please change the color of the individual data points from black to grey or another color so readers may better visualize the mean and error bars.

We agree with this comment, and in response, we have revised the figures by changing the color of the individual data points to empty circles and now the error bars are better visualized.

- Figure 1: What were the parameters used to identify an extension as a cytoneme? Please include the minimal length and max-width used in the analysis in the methods.

Thank you for the comments. We have now included the method of how we defined cytonemes and measured as follows. In zebrafish keratinocytes, lamellipodial extensions are the dominant extension type, and most filopodial extensions are less than 1µm in length, both are not easily visible at the confocal resolution we used for this study. Thus, it is easy to distinguish filopodia from cytonemes, as cytonemes have a minimum length of 4.36µm in our observations. We did not use the width parameter since there are no other protrusions except cytonemes. We calculated the cytoneme extension frequency by counting how many cytonemes extended from a cell per hour. We analyzed movies with 3-minute intervals over a total of 10 hours, as described in the section above.

- Line 149-150, (Figure S1) ML141 is a Cdc42 inhibitor, please correct the wording. Would the use of an actin polymerization inhibitor like Cytochalasin B or a depolymerizing agent (Latrunculin) increase the reduction in cytoneme formation?

Thank you for pointing it out. We have revised it in this version. We have tried Cytochalasin B or Latrunculin and the treatments killed the animals.

- Figure 2: What is the depth of the Z-axis images? Does the scale bar apply to the cross-sectional images as well? It may be beneficial to readers to expand the Z scale of the cross-section images for Figure 2C.

Sure, we enlarged the cross-sectional images. Yes, the scale bar should apply to the cross-sectional images.

- Figure 3B-B' cross-section images should be added to confirm images shown represent the periderm layer. Are there folds in the epidermis due to cdc42DN expression or are differentiated keratinocytes absent?

In response, we have included z-stack images in the revised figure 3. We found that the epidermal tissue is not flat as compared to controls, presumably due to broad cdc42DN expression (Figure 3C”).

- Figure S3: Do the EGFP+ and tdTomato+ cells have noticeable differential gene expression? The inclusion of RT-PCR analysis of all genes analyzed for both cell populations would bolster statements on lines 230-231 and 254-256.

We agree the reviewer’s comment and we have revised the RT-PCR panel in this revised version (Figure S4).

- Figure 4D-D', Please include cross-section images to indicate the focal plane for analysis.

We included cross-section images in this revised version (Figure 4E-E”).

- Figure 5B: Complimentary images visualizing the reduction of Notch would be helpful.

We are sorry not to include the data. In this revised version, we included notch reporter expression data that comparing WT, Tg(krt4:il17rd), and Tg(krt4:il17ra1a) in Figure S5E.

- Line 432-433: "Moreover, we have demonstrated that IL-17 can influence cytoneme extension by regulating Cdc42 GTPases, ultimately affecting actin polymerization." This claim would be strengthened by assaying for Cdc42 activity.

It is a great idea, and we were trying to address this issue. However, we realized that activity measure with biosensors, especially in vivo, required significant amount of time and effort and validations which seem to take a substantial amount of work needed, and no confidence to work in our end. And, it seems the current methods works for in vitro samples still has many limitations such as sensitivity issues. Although, we agree cdc42 activity measure will bolster our findings, it seems very challenging to apply it to zebrafish in vivo system.

- Line 445-447: "Clint1(Clathrin Interactor 1) plays an important role in vesicle trafficking, and it is well established that endocytic pathways are critical for multiple steps in cytoneme-mediated morphogen delivery (Kalthoff et al., 2002)." Please add references to the "endocytic pathways are critical for multiple steps in cytoneme-mediated morphogen delivery" portion of the sentence.

We revised the sentence. It is “well established” -> it is “suggested”, and added a reference (Daly et al., 2022).

Reviewer #3 (Recommendations For The Authors):

The details of the "cytoneme inhibition" experiments need to be better clarified. How long was the dox treatment? How soon did the cells start to show "disorganization"? How soon did the KC in the periderm start to show increased proliferation?

Thank you for the valuable comment and in response, we have revised the main text as follows “Although the cytoneme inhibition is evident after overnight treatment with the inducing drugs, noticeable epidermal phenotypes begin to appear after 3 days of treatment. This reflects the higher cytoneme extension frequency and their potential role during metamorphic stages, which takes a couple of weeks (Figure 1C)”

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

This manuscript presents a practical modification of the orthogonal hybridization chain reaction (HCR) technique, a promising yet underutilized method with broad potential for future applications across various fields. The authors advance this technique by integrating peptide ligation technology and nanobody-based antibody mimetics - cost-effective and scalable alternatives to conventional antibodies - into a DNA-immunoassay framework that merges oligonucleotide-based detection with immunoassay methodologies. Notably, they demonstrate that this approach facilitates a modified ELISA platform capable of simultaneously quantifying multiple target protein expression levels within a single protein mixture sample.

Strengths:

The hybridization chain reaction (HCR) technique was initially developed to enable the simultaneous detection of multiple mRNA expression levels within the same tissue. This method has since evolved into immuno-HCR, which extends its application to protein detection by utilizing antibodies. A key requirement of immuno-HCR is the coupling of oligonucleotides to antibodies, a process that can be challenging due to the inherent difficulties in expressing and purifying conventional antibodies.

In this study, the authors present an innovative approach that circumvents these limitations by employing nanobody-based antibody mimetics, which recognize antibodies, instead of directly coupling oligonucleotides to conventional antibodies. This strategy facilitates oligonucleotide conjugation - designed to target the initiator hairpin oligonucleotide of HCR -through peptide ligation and click chemistry.

Weaknesses:

The sandwich-format technique presented in this study, which employs a nanobody that recognizes primary IgG antibodies, may have limited scalability compared to existing methods that directly couple oligonucleotides to primary antibodies. This limitation arises because the C-region types of primary antibodies are relatively restricted, meaning that the use of nanobody-based detection may constrain the number of target proteins that can be analyzed simultaneously. In contrast, the conventional approach of directly conjugating oligonucleotides to primary antibodies allows for a broader range of protein targets to be analyzed in parallel.

We would like to clarify that MaMBA was specifically designed to address and overcome the limitations imposed by relying on primary antibodies’ Fc types for multiplexing. MaMBA utilizes DNA oligo-conjugated nanobodies that selectively and monovalently bind to the Fc region of IgG. This key feature allows us to barcode primary IgGs targeting different antigens independently. These barcoded IgGs can then be pooled together after barcoding, effectively minimizing the potential for cross-reactivity or crossover. Therefore, IgGs barcoded using MaMBA are functionally equivalent to those barcoded via conventional direct conjugation approaches with respect to multiplexing capability.

Additionally, in the context of HCR-based protein detection, the number of proteins that can be analyzed simultaneously is inherently constrained by fluorescence wavelength overlap in microscopy, which limits its multiplexing capability. By comparison, direct coupling of oligonucleotides to primary antibodies can facilitate the simultaneous measurement of a significantly greater number of protein targets than the sandwich-based nanobody approach in the barcode-ELISA/NGS-based technique.

As we have responded above, MaMBA barcoding of primary IgGs that target various antigens can be conducted separately. Once barcoded, these IgGs can then be combined into a single pool. Therefore, for BLISA (i.e., the barcode-ELISA/NGS-based technique), IgGs barcoded through MaMBA offer the same multiplexing capability as those barcoded using traditional direct conjugation methods.

In in situ protein imaging, spectral overlap can indeed limit the throughput of multiplexed HCR fluorescent imaging. There are two strategies to address this challenge. As demonstrated in this work with _mis_HCR and _mis_HCRn, removing the HCR amplifiers allows for multiplexed detection using a limited number of fluorescence wavelengths. This is achieved through sequential rounds of HCR amplification and imaging. Alternatively, recent computational approaches offer promising solutions for “one-shot” multiplexed imaging. These include combinatorial multiplexing (PMID: 40133518) and spectral unmixing (PMID: 35513404), which can be applied to _mis_HCR to deconvolute overlapping spectra and increase multiplexing capacity in a single imaging acquisition.

Reviewer #1 (Recommendations for the authors):

(1) The introduction of nanobody and peptide ligation technology is a key highlight of this study. To strengthen the manuscript, the authors should provide a more detailed discussion of the principles and applications of HCR in the Introduction or Discussion sections.

We have added a brief discussion of the HCR reaction to the revised manuscript.

(2) It would also be beneficial to include results and/or discussion on how the affinity of nanobody binding to IgG influences the success and accuracy of the technique.

We have added a brief discussion of the IgG nanobodies we used in MaMBA to the revised manuscript.

(3) Additionally, a more detailed explanation of the recognition specificity of the AEP peptide ligase used in this study should be included in the Discussion section. Prior studies have reported on the specificity of amino acid residues positioned at the C-terminus of target A (-5 to -1) and the N-terminus of target B (1 to 3) in AEP-mediated ligation, and integrating this context would enhance clarity.

We have added a brief discussion of the AEP-mediated ligation to the revised manuscript.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment 

The authors utilize a valuable computational approach to exploring the mechanisms of memorydependent klinotaxis, with a hypothesis that is both plausible and testable. Although they provide a solid hypothesis of circuit function based on an established model, the model's lack of integration of newer experimental findings, its reliance on predefined synaptic states, and oversimplified sensory dynamics, make the investigation incomplete for both memory and internal-state modulation of taxis.  

We would like to express our gratitude to the editor for the assessment of our work. However, we respectfully disagree with the assessment that our investigation is incomplete, if the negative assessment is primarily due to the impact of AIY interneuron ablation on the chemotaxis index (CI) which was reported in Reference [1]. It is crucial to acknowledge that the CI determined through experimental means incorporates contributions from both klinokinesis and klinotaxis [1]. It is plausible that the impact of AIY ablation was not adequately reflected in the CI value. Consequently, the experimental observation does not necessarily diminish the role of AIY in klinotaxis. Anatomical evidence provided by the database (http://ims.dse.ibaraki.ac.jp/ccep-tool/) substantiates that ASE sensory neurons and AIZ interneurons, which have been demonstrated to play a crucial role in klinotaxis [Matsumoto et al., PNAS 121 (5) e2310735121], have the much higher number of synaptic connections with AIY interneurons. These findings provide substantial evidence supporting the validity of the presented minimal neural network responsible for salt klinotaxis.

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

This research focuses on C. elegans klinotaxis, a chemotactic behavior characterized by gradual turning, aiming to uncover the neural circuit mechanism responsible for the context-dependent reversal of salt concentration preference. The phenomenon observed is that the preferred salt concentration depends on the difference between the pre-assay cultivation conditions and the current environmental salt levels. 

We would like to express our gratitude for the time and consideration you have dedicated to reviewing our manuscript.

The authors propose that a synaptic-reversal plasticity mechanism at the primary sensory neuron, ASER, is critical for this memory- and context-dependent switching of preference. They build on prior findings regarding synaptic reversal between ASER and AIB, as well as the receptor composition of AIY neurons, to hypothesize that similar "plasticity" between ASER and AIY underpins salt preference behavior in klinotaxis. This plasticity differs conceptually from the classical one as it does not rely on any structural changes but rather synaptic transmission is modulated by the basal level of glutamate, and can switch from inhibitory to excitatory. 

To test this hypothesis, the study employs a previously established neuroanatomically grounded model [4] and demonstrates that reversing the ASER-AIY synapse sign in the model agent reproduces the observed reversal in salt preference. The model is parameterized using a computational search technique (evolutionary algorithm) to optimize unknown electrophysiological parameters for chemotaxis performance. Experimental validity is ensured by incorporating constraints derived from published findings, confirming the plausibility of the proposed mechanism. 

Finally. the circuit mechanism allowing C. elegans to switch behaviour to an exploration run when starved is also investigated. This extension highlights how internal states, such as hunger, can dynamically reshape sensory-motor programs to drive context-appropriate behaviors.  

We would like to thank the reviewer for the appropriate summary of our work. 

Strengths and weaknesses: 

The authors' approach of integrating prior knowledge of receptor composition and synaptic reversal with the repurposing of a published neuroanatomical model [4] is a significant strength. This methodology not only ensures biological plausibility but also leverages a solid, reproducible modeling foundation to explore and test novel hypotheses effectively.

The evidence produced that the original model has been successfully reproduced is convincing.

The writing of the manuscript needs revision as it makes comprehension difficult.  

We would like to thank the reviewer for recognizing the usefulness of our approach. In the revised version, we improved the explanation according to your suggestions.  

One major weakness is that the model does not incorporate key findings that have emerged since the original model's publication in 2013, limiting the support for the proposed mechanism. In particular, ablation studies indicate that AIY is not critical for chemotaxis, and other interneurons may play partially overlapping roles in positive versus negative chemotaxis. These findings challenge the centrality of AIY and suggest the model oversimplifies the circuit involved in klinotaxis.

We would like to express our gratitude for the constructive feedback we have received. We concur with some of your assertions. In fact, our model is the minimal network for salt klinotaxis, which includes solely the interneurons that are connected to each other via the highest number of synaptic connections. It is important to note that our model does not consider redundant interneurons that exhibit overlapping roles. Consequently, the model is not applicable to the study of the impact of interneuron ablation. In the reference [1], the influence of interneuron ablations on the chemotaxis index (CI) has been investigated. The experimentally determined CI value incorporates the contributions from both klinokinesis and klinotaxis. Consequently, it is plausible that the impact of AIY ablation was not significantly reflected in the CI value. The experimental observation does not necessarily diminish the role of AIY in klinotaxis. 

Reference [1] also shows that ASER neurons exhibit complex, memory- and context-dependent responses, which are not accounted for in the model and may have a significant impact on chemotactic model behaviour. 

As the reviewer has noted, our model does not incorporate the context-dependent response of the ASER. Instead, the impact of the salt concentration-dependent glutamate release from the ASER [S. Hiroki et al. Nat Commun 13, 2928 (2022)] as the result of the ASER responses was in detail examined in the present study.

The hypothesis of synaptic reversal between ASER and AIY is not explicitly modeled in terms of receptor-specific dynamics or glutamate basal levels. Instead, the ASER-to-AIY connection is predefined as inhibitory or excitatory in separate models. This approach limits the model's ability to test the full range of mechanisms hypothesized to drive behavioral switching.  

We would like to express our gratitude to the reviewer for their constructive feedback. As you correctly noted, the hypothesized synaptic reversal between ASER and AIY is not explicitly modeled in terms of the sensitivity of the receptors in the AIY and the glutamate basal levels by the ASER. On the other hand, in the present study, under considering a substantial difference in the sensitivity of the two glutamate receptors on the AIY, we sought to endeavored to elucidate the impact of salt-concentration-dependent glutamate basal levels on klinotaxis. To this end, we conducted a comprehensive examination of the full range gradual change in the ASER-to-AIY connection from inhibitory to excitatory, as illustrated in Figures S4 and S5.

While the main results - such as response dependence on step inputs at different phases of the oscillator - are consistent with those observed in chemotaxis models with explicit neural dynamics (e.g., Reference [2]), the lack of richer neural dynamics could overlook critical effects. For example, the authors highlight the influence of gap junctions on turning sensitivity but do not sufficiently analyze the underlying mechanisms driving these effects. The role of gap junctions in the model may be oversimplified because, as in the original model [4], the oscillator dynamics are not intrinsically generated by an oscillator circuit but are instead externally imposed via $z_¥text{osc}$. This simplification should be carefully considered when interpreting the contributions of specific connections to network dynamics. Lastly, the complex and contextdependent responses of ASER [1] might interact with circuit dynamics in ways that are not captured by the current simplified implementation. These simplifications could limit the model's ability to account for the interplay between sensory encoding and motor responses in C. elegans chemotaxis. 

We might not understand the substance of your assertions. However, we understand that the oscillator dynamics were not intrinsically generated by the oscillator neural circuit that is explicitly incorporated into our modeling. On the other hand, the present study focuses on how the sensory input and resulting interneuron dynamics regulate the oscillatory behavior of SMB motor neurons to generate klinotaxis. The neuron dynamics via gap junctions results from the equilibration of the membrane potential yi of two neurons connected by gap junctions rather than the zi. We added this explanation in the revised manuscript as follows.

“The hyperpolarization signals in the AIZL are transmitted to the AIZR via the gap junction (Figs. S1d and S1f and Fig. 3d). This is because the neuron dynamics via gap junctions results from the equilibration of the membrane potential y_i of two neurons connected by gap junctions rather than the z_i.”

In the limitation, we added the following sentence:

“In the present study, the oscillator components of the SMB are not intrinsically generated by an oscillator circuit but are instead externally imposed via 𝑧_i^OSC. Furthermore, the complex and context-dependent responses of ASER {Luo:2014et} were not taken into consideration. It should be acknowledged as a limitation of this study that these omitted factors may interact with circuit dynamics in ways that are not captured by the current simplified implementation.”

Appraisal: 

The authors show that their model can reproduce memory-dependent reversal of preference in klinotaxis, demonstrating that the ASER-to-AIY synapse plays a key role in switching chemotactic preferences. By switching the ASER-AIY connection from excitatory to inhibitory they indeed show that salt preference reverses. They also show that the curving/turn rate underlying the preference change is gradual and depends on the weight between ASER-AIY. They further support their claim by showing that curving rates also depend on cultivated (set-point).  

We would like to thank the reviewer for assessing our work.

Thus within the constraints of the hypothesis and the framework, the model operates as expected and aligns with some experimental findings. However, significant omissions of key experimental evidence raise questions on whether the proposed neural mechanisms are sufficient for reversal in salt-preference chemotaxis.  

We agree with your opinion. The present hypothesis should be verified by experiments.

Previous work [1] has shown that individually ablating the AIZ or AIY interneurons has essentially no effect on the Chemotactic Index (CI) toward the set point ([1] Figure 6). Furthermore, in [1] the authors report that different postsynaptic neurons are required for movement above or below the set point. The manuscript should address how this evidence fits with their model by attempting similar ablations. It is possible that the CI is rescued by klinokinesis but this needs to be tested on an extension of this model to provide a more compelling argument.  

We would like to express our gratitude for the constructive feedback we have received. In the reference [1], the influence of interneuron ablations on the chemotaxis index (CI) has been investigated. It is important to acknowledge that the experimentally determined CI value encompasses the contributions of both klinokinesis and klinotaxis. It is plausible that the impact of AIY ablation was not reflected in the CI value. Consequently, these experimental observations do not necessarily diminish the role of AIY in klinotaxis. The neural circuit model employed in the present study constitutes a minimal network for salt klinotaxis, encompassing solely interneurons that are connected to each other via the highest number of synaptic connections. Anatomical evidence provided by the database (http://ims.dse.ibaraki.ac.jp/cceptool/) substantiates that ASE sensory neurons and AIZ interneurons, which have been demonstrated to play a crucial role in klinotaxis [Matsumoto et al., PNAS 121 (5) e2310735121], have the much higher number of synaptic connections with AIY interneurons. Our model does not take into account redundant interneurons with overlapping roles, thus rendering it not applicable to the study of the effects of interneuron ablation.

The investigation of dispersal behaviour in starved individuals is rather limited to testing by imposing inhibition of the SMB neurons. Although a circuit is proposed for how hunger states modulate taxis in the absence of food, this circuit hypothesis is not explicitly modelled to test the theory or provide novel insights.  

As the reviewer noted, the experimentally identified neural circuit that inhibits the SMB motor neurons in starved individuals is not incorporated in our model. Instead of incorporating this circuit explicitly, we examined whether our minimal network model could reproduce dispersal behavior under starvation conditions solely due to the experimentally demonstrated inhibitory effect of SMB motor neurons.

Impact: 

This research underscores the value of an embodied approach to understanding chemotaxis, addressing an important memory mechanism that enables adaptive behavior in the sensorimotor circuits supporting C. elegans chemotaxis. The principle of operation - the dependence of motor responses to sensory inputs on the phase of oscillation - appears to be a convergent solution to taxis. Similar mechanisms have been proposed in Drosophila larvae chemotaxis [2], zebrafish phototaxis [3], and other systems. Consequently, the proposed mechanism has broader implications for understanding how adaptive behaviors are embedded within sensorimotor systems and how experience shapes these circuits across species.

We would like to express our gratitude for useful suggestion. We added this argument in Discussion of the revised manuscript as follows.    

“The principle of operation, in which the dependence of motor responses to sensory inputs on the phase of motor oscillation, appears to be a convergent solution for taxis and navigation across species. In fact, analogous mechanisms have been postulated in the context of chemotaxis in Drosophila larvae chemotaxis {Wystrach:2016bt} and phototaxis in zebrafish {Wolf:2017ei}. Consequently, the synaptic reversal mechanism highlighted in this study offers the framework for understanding how the behaviors that are adaptive to the environment are embedded within sensorimotor systems and how experience shapes these neural circuits across species.”

Although the reported reversal of synaptic connection from excitatory to inhibitory is an exciting phenomenon of broad interest, it is not entirely new, as the authors acknowledge similar reversals have been reported in ASER-to-AIB signaling for klinokinesis ( Hiroki et al., 2022). The proposed reversal of the ASER-to-AIY synaptic connection from inhibitory to excitatory is a novel contribution in the specific context of klinotaxis. While the ASER's role in gradient sensing and memory encoding has been previously identified, the current paper mechanistically models these processes, introducing a hypothesis for synaptic plasticity as the basis for bidirectional salt preference in klinotaxis.  

The research also highlights how internal states, such as hunger, can dynamically reshape sensory-motor programs to drive context-appropriate behaviors.  

The methodology of parameter search on a neural model of a connectome used here yielded the valuable insight that connectome information alone does not provide enough constraints to reproduce the neural circuits for behaviour. It demonstrates that additional neurophysiological constraints are required.  

We would like to acknowledge the appropriate recognition of our work.

Additional Context 

Oscillators with stimulus-driven perturbations appear to be a convergent solution for taxis and navigation across species. Similar mechanisms have been studied in zebrafish phototaxis [3], Drosophila larvae chemotaxis [2], and have even been proposed to underlie search runs in ants. The modulation of taxis by context and memory is a ubiquitous requirement, with parallels across species. For example, Drosophila larvae modulate taxis based on current food availability and predicted rewards associated with odors, though the underlying mechanism remains elusive. The synaptic reversal mechanism highlighted in this study offers a compelling framework for understanding how taxis circuits integrate context-related memory retrieval more broadly.  

We would like to express our gratitude for the insightful commentary. In the revised manuscript, we incorporated the argument that the similar oscillator mechanism with stimulus-driven perturbations has been observed for zebrafish phototaxis [3] and Drosophila larvae chemotaxis [2] into Discussion.

As a side note, an interesting difference emerges when comparing C. elegans and Drosophila larvae chemotaxis. In Drosophila larvae, oscillatory mechanisms are hypothesized to underlie all chemotactic reorientations, ranging from large turns to smaller directional biases (weathervaning). By contrast, in C. elegans, weathervaning and pirouettes are treated as distinct strategies, often attributed to separate neural mechanisms. This raises the possibility that their motor execution could share a common oscillator-based framework. Re-examining their overlap might reveal deeper insights into the neural principles underlying these maneuvers. 

We would like to acknowledge your thoughtfully articulated comment. As the reviewer pointed out, the anatomical database (http://ims.dse.ibaraki.ac.jp/ccep-tool/) shows that that the neural circuits underlying weathervaning and pirouettes in C. elegans are predominantly distinct but exhibit partial overlap. When we restrict our search to the neurons that are connected to each other with the highest number of synaptic connections, we identify the projections from the neural circuit of weathervaning to the circuit of pirouettes; however we observed no reversal projections. This finding suggests that the neural circuit of weathervaning, namely, our minimal neural network, is not likely to be affected by that of pirouettes, which consists of AIB interneurons and interneurons and motor neurons the downstream. 

(1) Luo, L., Wen, Q., Ren, J., Hendricks, M., Gershow, M., Qin, Y., Greenwood, J., Soucy, E.R., Klein, M., Smith-Parker, H.K., & Calvo, A.C. (2014). Dynamic encoding of perception, memory, and movement in a C. elegans chemotaxis circuit. Neuron, 82(5), 1115-1128. 

(2) Antoine Wystrach, Konstantinos Lagogiannis, Barbara Webb (2016) Continuous lateral oscillations as a core mechanism for taxis in Drosophila larvae eLife 5:e15504. 

(3) Wolf, S., Dubreuil, A.M., Bertoni, T. et al. Sensorimotor computation underlying phototaxis in zebrafish. Nat Commun 8, 651 (2017). 

(4) Izquierdo, E.J. and Beer, R.D., 2013. Connecting a connectome to behavior: an ensemble of neuroanatomical models of C. elegans klinotaxis. PLoS computational biology, 9(2), p.e1002890. 

Reviewer #2 (Public review): 

Summary: 

This study explores how a simple sensorimotor circuit in the nematode C. elegans enables it to navigate salt gradients based on past experiences. Using computational simulations and previously described neural connections, the study demonstrates how a single neuron, ASER, can change its signaling behavior in response to different salt conditions, with which the worm is able to "remember" prior environments and adjust its navigation toward "preferred" salinity accordingly.  

We would like to express our gratitude for the time and consideration the reviewer has dedicated to reviewing our manuscript.

Strengths: 

The key novelty and strength of this paper is the explicit demonstration of computational neurobehavioral modeling and evolutionary algorithms to elucidate the synaptic plasticity in a minimal neural circuit that is sufficient to replicate memory-based chemotaxis. In particular, with changes in ASER's glutamate release and sensitivity of downstream neurons, the ASER neuron adjusts its output to be either excitatory or inhibitory depending on ambient salt concentration, enabling the worm to navigate toward or away from salt gradients based on prior exposure to salt concentration.

We would like to thank the reviewer for appreciating our research. 

Weaknesses: 

While the model successfully replicates some behaviors observed in previous experiments, many key assumptions lack direct biological validation. As to the model output readouts, the model considers only endpoint behaviors (chemotaxis index) rather than the full dynamics of navigation, which limits its predictive power. Moreover, some results presented in the paper lack interpretation, and many descriptions in the main text are overly technical and require clearer definitions.  

We would like to thank the reviewer for the constructive feedback. As the reviewer noted, the fundamental assumptions posited in the study have yet to be substantiated by biological validation, and consequently, these assumptions must be directly assessed by biological experimentation. The model performance for salt klinotaxis has been evaluated by multiple factors, including not only a chemotaxis index but also the curving rate vs. bearing (Fig. 4a, the bearing is defined in Fig. A3) and the curving rate vs. normal gradient (Fig. 4c). These two parameters work to characterize the trajectory during salt klinotaxis. In the revised version, we meticulously revised the manuscript according to the reviewer’s suggestions. We would like to express our sincere gratitude for your insightful review of our work.

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors): 

An interesting and engaging methodology combining theoretical and computational approaches. Overall I found the manuscript up to discussion a difficult read, and I would suggest revising it. I would also recommend introducing the general operating principle of the oscillator with sensory perturbations before jumping into the implementation details of signal propagation specific to C.

elegans.  

In order to elucidate the relation between the general operating principle of the oscillator with sensory perturbations and the results shown by the two graphs from the bottom in Fig. 3d, the following statement was added on page 12.

“It is remarkable that this regulatory mechanism derived via the optimization of the CI has been observed in the context of chemotaxis in Drosophila larvae chemotaxis {Wystrach:2016bt} and phototaxis in zebrafish {Wolf:2017ei}. The principle of operation, in which the dependence of motor responses to sensory inputs on the phase of motor oscillation, therefore, may serve as a convergent solution for taxis and navigation across species.”

The abstract could benefit from a clarification of terms to benefit a broader audience:  The term "salt klinotaxis" is used without prior introduction or definition. It would be beneficial to briefly explain this term, as it may not be familiar to all readers. 

Due to the limitation of the word number in the abstract, the explanation of salt klinotaxis could not be included.

Although ASER is introduced as a right-side head sensory neuron, AIY neurons are not similarly introduced. It may also benefit to introduce here that ASER integrates memory with current salt gradients, tuning its output to produce context-appropriate behaviour.  

Due to the limitation of the word number in the abstract, we could add no more the explanations. 

"it can be anticipated that the ASER-AIY synaptic transmission will undergo a reversal due to alterations in the basal glutamate Release": Where is this expectation drawn from? Is it derived from biophysical or is it a functional expectation to explain the network's output constraints?  

As delineated before this sentence, it is derived from a comprehensive consideration of the sensitivity of excitatory/inhibitory glutamate receptors expressed on the postsynaptic AIY interneurons, in conjunction with varying the basal level of glutamate transmission from ASER.

The statement that the model "revealed the modular neural circuit function downstream of ASE" could be more explicit. What specific insights about the downstream circuit were uncovered?

Highlighting one or two key findings would strengthen the impact.  

Due to the limitation of the word number in the abstract, no more details could be added here, while the sentence was revised as “revealed that the circuit downstream of ASE functions as a module that is responsible for salt klinotaxis.” This is because the salt-concentration dependent behaviors in klinitaxis can be reproduced through the modulation of the ASRE-AIY synaptic connections alone, despite the absence of alterations in the neural circuit downstream of AIY.

I believe the authors should cite Luo et al. 2014, which also studies how chemotactic behaviours arise from neural circuit dynamics, including the dynamic encoding of salt concentration by ASER, and the crucial downstream interaction with AIY for chemotactic actions. 

We would like to express our gratitude for useful suggestion. We cited Luo et al. 2014 in the discussion on the limitation of our work. 

The introduction could also be improved for clarity. Specifically in the last paragraph authors should clarify how the observed synchrony of ASER excitation to the AIZ (Matsumoto et al., 2024), validates the resulting network.  

We would like to express our gratitude for useful suggestion. We added the following explanation in the last paragraph of the introduction.

“Specifically, the synchrony of the excitation of the ASER and AIZ {Matsumoto:2024ig} taken together with the experimentally identified inhibitory synaptic transmission between the AIY and AIZ revealed that the ASER-AIY synaptic connections should be inhibitory, which was consistent with the network obtained from the most evolved model.”

In addition, we added the following explanation after “It was then hypothesized that the ASER-AIY inhibitory synaptic connections are altered to become excitatory due to a decrease in the baseline release of glutamate from the ASER when individuals are cultured under C_cult < C_test.”

This is due to the substantial difference in the sensitivity of excitatory/inhibitory glutamate receptors expressed on the postsynaptic AIY interneurons.

I would also strongly recommend replacing the term "evolved model", with "Optimized Model" or "Best-Performing Model" to clarify this is a computational optimization process with limitations - optimization through GAs does not guarantee finding global optima.  

We revised "evolved model" as "optimized model" in the main and SI text.

The text overall would benefit from editing for clarity and expression.  

According to the revisions mentioned above, we revised “best optimized model” as “most optimized model” in the main and SI text.

The font size on the plot axis in Figures 3 c&d should be increased for readability on the printed page. Label the left/right panel to indicate unconstrained / constrained evolution.  

As you noted, the font size of the subscript on the vertical axis in Figs 3c and 3d was too small. We have revised the font size of the subscript in Figs. 3c and 3d and also in Fig. 5e. At your suggestion, “unconstrained” and “constrained” have been added as labels to the left and right panels in Fig. 3.

There is no input/transmission to AIYR to step input in either model shown in Figure 3? 

As shown in Fig. S1e and S1f, there are the transmissions to the AIYR from the ASEL and ASER. 

Supplementary Figure 1 attempts to explain the interactions. There are inconsistent symbols used for inhibition and excitation between network schema (colours) and the z response plots (arrows vs circles), combined with different meanings for red/blue making it very confusing. 

We could not address the inconsistency in the color of arrows and lines with an ending between Figs. S1c and S1d and Figs. S1a and S1b. On the other hand, Figs. S1e and S1f were revised so that the consistent symbols were used for inhibition, excitation, and electrical gap connections in Figs. S1c-S1f. The same revisions were made for Fig. S7c-S7f.

Model parameters are given to 15 decimal precision, which seems excessive. Is model performance sensitive to that order? We would expect robustness around those values. The authors should identify relevant orders and truncate parameters accordingly. 

We examined the influence of the parameter truncation on the trajectory and decided that the parameters with four decimal places were appropriate. According to this, we revised Table A4.

Figure 3 caption typo "step changes I the salt concentration".  

The typo was revised in Fig. 3 caption. 

Reviewer #2 (Recommendations for the authors): 

(1) Overall, the language of the paper is not properly organized, making the paper's logic and purpose hard to follow. In the Results Section, many observations or findings lack explicit interpretation. To address this issue, the authors should consider (1) adopting the contextcontent-conclusion scheme, (2) optimizing the logic flow by clearly identifying the context and goals prior to discussing their results and findings, (3) more explicitly interpreting their results, especially in a biological context.  

We would like to express our gratitude for helpful suggestion. According to your suggestion listed below, we revised the main and SI texts.

(2) In Figure 2, trajectories from the model with AIY-AIZ constraints show a faster convergence than those from the constraint-free model. However, in the corresponding texts in the Results section, the authors claimed no significant difference. It seems that the authors made this argument only based on CI (Chemotaxis Index). Therefore, in order to address such inconsistency, the authors need more explanation on why only relying on CI, which is an endpoint metric, instead of the whole navigation.  

I would like to thank you for the helpful comment. In the present study, not only the CI but also the curving rate shown in Fig. 4 were applied to characterize the behavior in klinotaxis.

According to your comments, we revised the related description in the main text as follows:

“The difference between these CI values is slight, while the model optimized with the constraints exhibits a marginally accelerated attainment of the salt concentration peak, as shown by the trajectories. The slightly higher chemotaxis performance observed in the constrained model is not essentially attributed to the introduction of the AIY-AIZ synaptic constraints but rather depends on the specific individuals selected from the optimized individuals obtained from the evolutionary algorithm. In fact, even when the AIY-AIZ constraints are taken into consideration, the model retains a significant degree of freedom to reproduce salt klinotaxis due to the presence of a substantial parameter space. Consequently, the impact of the AIY-AIZ constraints on the optimization of the CI is expected to be negligible.”

(3) In Figures 3a and b, some inter-neuron connections are relatively weak (e.g., AIYR to AIZR in Figure 3a) - thus it is unclear whether the polarity of such synapses would significantly influence the behavioral outcome or not. The authors could consider plotting the change of the connection strengths between neurons over the course of model optimization to get a sense of confidence in each inter-neuron connection. 

In the evolutional algorithm, the parameters of individuals are subject to discontinuous variation due to the influence of selection, crossover, and mutations. Consequently, it is not straightforward to extract information regarding parameter optimization from parameter changes due to the non-systematic nature of parameter variation..

(4) In Figure 3, the order of individual figure panels is incorrect: in the main text, Figure 3 a and b were mentioned after c and d. Also, the caption of Figure 3c "negative step changes I the" should be "in".  

The main text underwent revision, with the description of Figures 3a and 3b being presented prior to that of Figures 3c and 3d. The typo was revised.

(5) In Figure 4, the order of individual figure panels is messed up: in the main text, Figure 4 a was mentioned after b.  

The main text underwent revision, with the description of Figure 4a being presented prior to that of Figure 4b.

(6) Also in Figure 4, the authors need to provide a definition/explanation of "Bearing" and "Translational Gradient". In Figure 4d, the definition of positive and negative components is not clear.  

Normal and Translational Salt Concentration Gradient in METHOD was referenced for the definition and explanation of the bearing and the translational gradient. We added the following explanation on the positive and negative components.

“The positive and negative components of the curving rate are respectively sampled from the trajectory during leftward turns (as illustrated in Fig. 4b) and rightward turns, respectively.”

(7) Figure 5: the authors need to explain why c has an error bar and how they were calculated, as this result is from a computational model. Figure 5d is experimental results - the authors need to add error bars to the data points and provide a sample size. 

As explained in Analysis of the Salt Preference Behavior in Klinotaxis in METHOD, the ensemble average of these quantities was determined by performing 100,000 sets of the simulation with randomized initial orientation for a simulation time of T_sim=200 sec. The error bars for the experimental data were added in Figs. 5c, 6a, and S9a.

(8) On Page 14, the authors said, "To this end, this end, we used the best evolved network with the constraints, in which we varied the synaptic connections between ASER and AIY from inhibitory to excitatory." How did the model change the ASER-AIY signaling specifically? The authors should provide more explanation or at least refer to the Methods Section.  

The caption of Fig. S4 was referred as the explanation on the detailed method. 

(9) Page 15: "a subset a subset exhibited a slight curve...". This observation from the model simulation is contradictory to experiments. However, their explanation of that is hard to understand.  

I would like to thank you for the helpful comment. To improve this, we added the following explanation:

“In the case of step increases in 𝑧OFF as illustrated in the second right panel from the bottom in Fig.3d, the turning angle φ is increased from its ideal oscillatory component to a value close to zero, causing the model worm to deviate from the ideal sinusoidal trajectory and gradually turn toward lower salt concentrations. On the other hand, in the case of step increases in 𝑧ON as illustrated in the second left panel from the bottom in Fig.3d, the turning angle φ is again increased from its ideal oscillatory component to a value close to zero, causing the model worm to deviate from the ideal sinusoidal trajectory and gradually turn toward higher salt concentrations. The behaviors that are consistent with these analyses are observed in the trajectory illustrated in Fig. S8b.”

(10) Last result session: inhibited SMB in starved worms is due to a mechanism unrelated to their neural network model upstream to SMB. Therefore, their results recapitulating the worms' dispersal behaviors cannot strengthen the validity of their model.  

We agree with your opinion. We think that the findings from the study of starved worms do not provide evidence to validate the neural network model upstream of SMB.   

(11) Discussion: "in contrast, the remaining neurons...". This argument lacks evidence or references.  

This argument is based on the results obtained from the present study. This sentence was revised as follows:

“This regulatory process enables the reproduction of salt concentration memory-dependent reversal of preference behavior in klinotaxis, despite the remaining neurons further downstream of the ASER not undergoing alterations and simply functioning as a modular circuit to transmit the received signals to the motor systems. Consequently, the sensorimotor circuit allows a simple and efficient bidirectional regulation of salt preference behavior in klinotaxis.”

(12) To increase the predictive power of their model, can the authors perform simulations on mutant worms, like those with altered glutamate basal level expression in ASER?  

We would like to express our gratitude for useful suggestion. The simulations, in which the weight of the ASER-AIY synaptic connection is increased from negative (inhibitory connection) to positive (excitatory connection), as illustrated in Figure S4, provide valuable insights into the relationship between varying glutamate basal levels from ASER and behavior in klinotaxis, such as the chemotaxis index.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In the present study, Chen et al. investigate the role of Endophilin A1 in regulating GABAergic synapse formation and function. To this end, the authors use constitutive or conditional knockout of Endophilin A1 (EEN1) to assess the consequences on GABAergic synapse composition and function, as well as the outcome for PTZ-induced seizure susceptibility. The authors show that EEN1 KO mice show a higher susceptibility to PTZ-induced seizures, accompanied by a reduction in the GABAergic synaptic scaffolding protein gephyrin as well as specific GABAAR subunits and eIPSCs. The authors then investigate the underlying mechanisms, demonstrating that Endophilin A1 binds directly to gephyrin and GABAAR subunits, and identifying the subdomains of Endophilin A1 that contribute to this effect. Overall, the authors state that their study places Endophilin A1 as a new regulator of GABAergic synapse function.

Strengths:

Overall, the topic of this manuscript is very timely, since there has been substantial recent interest in describing the mechanisms governing inhibitory synaptic transmission at GABAergic synapses. The study will therefore be of interest to a wide audience of neuroscientists studying synaptic transmission and its role in disease. The manuscript is well-written and contains a substantial quantity of data.

Weaknesses:

A number of questions remain to be answered in order to be able to fully evaluate the quality and conclusions of the study. In particular, a key concern throughout the manuscript regards the way that the number of samples for statistical analysis is defined, which may affect the validity of the data analysed. Addressing this weakness will be essential to providing conclusive results that support the authors' claims.

We would like to thank the reviewer for appreciation of the value of our study and careful critics to help us improve the manuscript. We will correct the way that the number of samples for statistical analysis is defined throughout the manuscript as suggested and update figures, figure legends, and Materials and Methods accordingly. For example, we will average the values for all dendritic segments from one neuron, so that each data point represents one neuron in the graphs.

Reviewer #2 (Public review):

Summary:

The function of neural circuits relies heavily on the balance of excitatory and inhibitory inputs. Particularly, inhibitory inputs are understudied when compared to their excitatory counterparts due to the diversity of inhibitory neurons, their synaptic molecular heterogeneity, and their elusive signature. Thus, insights into these aspects of inhibitory inputs can inform us largely on the functions of neural circuits and the brain.

Endophilin A1, an endocytic protein heavily expressed in neurons, has been implicated in numerous pre- and postsynaptic functions, however largely at excitatory synapses. Thus, whether this crucial protein plays any role in inhibitory synapse, and whether this regulates functions at the synaptic, circuit, or brain level remains to be determined.

New Findings:

(1) Endophilin A1 interacts with the postsynaptic scaffolding protein gephyrin at inhibitory postsynaptic densities within excitatory neurons.

(2) Endophilin A1 promotes the organization of the inhibitory postsynaptic density and the subsequent recruitment/stabilization of GABA A receptors via Endophilin A1's membrane binding and actin polymerization activities.

(3) Loss of Endophilin A1 in CA1 mouse hippocampal pyramidal neurons weakens inhibitory input and leads to susceptibility to epilepsy.

(4) Thus the authors propose that via its role as a component of the inhibitory postsynaptic density within excitatory neurons, Endophilin A1 supports the organization, stability, and efficacy of inhibitory input to maintain the excitatory/inhibitory balance critical for brain function.

(5) The conclusion of the manuscript is well supported by the data but will be strengthened by addressing our list of concerns and experiment suggestions.

We would like to thank the reviewer for their favorable impression of manuscript. We also appreciate the great experiment suggestions to help us improve the manuscript.

Weaknesses:

Technical concerns:

(1) Figure 1F and Figure 1H, Figures 7H,J:

Can the authors justify using a paired-pulse interval of 50 ms for eEPSCs and an interval of 200 ms for eIPSCs? Otherwise, experiments should be repeated using the same paired pulse interval.

We apologize for the confusion. As illustrated by the schematic current traces, the decay time constants of eEPSCs and eIPSCs in hippocampal CA1 neurons are different. The eEPSCs exhibit a faster channel closing rate, corresponding to a smaller time constant Tau. Thus, a shorter inter-stimulus interval (50 ms) was chosen for paired-pulse ratio recordings. In contrast, the eIPSCs display a slower channel closing rate, with a Tau value larger than that of eEPSCs, so a longer inter-stimulus interval (200 ms) was used for PPR. This protocol has been long-established and adopted in previous studies (please see below for examples).

Contractor, A., Swanson, G. & Heinemann, S. F. Kainate receptors are involved in short- and long-term plasticity at mossy fiber synapses in the hippocampus. Neuron 29, 209-216, doi:10.1016/s0896-6273(01)00191-x (2001).

Babiec, W. E., Jami, S. A., Guglietta, R., Chen, P. B. & O'Dell, T. J. Differential Regulation of NMDA Receptor-Mediated Transmission by SK Channels Underlies Dorsal-Ventral Differences in Dynamics of Schaffer Collateral Synaptic Function. Journal of neuroscience 37, 1950-1964, doi:10.1523/JNEUROSCI.3196-16.2017 (2017).

(2) Figures 3G,H,I:

While 3D representations of proteins of interest bolster claims made by superresolution microscopy, SIM resolution is unreliable when deciphering the localization of proteins at the subsynaptic level given the small size of these structures (<1 micrometer). In order to determine the actual location of Endophilin A1, especially given the known presynaptic localization of this protein, the authors should complete SIM experiments with a presynaptic marker, perhaps an active zone protein, so that the relative localization of Endophilin A1 can be gleaned. Currently, overlapping signals could stem from the presynapse given the poor resolution of SIM in this context.

Thanks for your suggestions. It is certainly preferable to investigate the relative localization of endophilin A1 using both presynaptic and postsynaptic markers. For SIM imaging in Figure 3G-I, to visualize neuronal morphology, we immunostained GFP as cell fill, leaving two other channels for detection of immunofluorescent signals of endophilin A1 and another protein. We will try co-immunostaining of endophilin A1, the active zone protein bassoon (presynaptic marker) and gephyrin without morphology labeling. Alternatively, we will do co-staining of endophilin A1 and bassoon in GFP-expressing neurons. We agree that overlapping signals or proximal localization of presynaptic endophilin A1 with gephyrin or GABA_AR γ2 could not be ruled out. To note, if image resolution is improved with the use of a more advanced imaging system, the overlap between two proteins will become smaller or even disappear. With the ~110 nm lateral resolution of SIM microscopy, the degree of overlap between the two proteins of interest is much lower than in confocal microscopy. Given the presynaptic localization of endophilin, most likely we will observe a small overlap (presynatpic) or proximal localization (postsynaptic) of endophilin A1 with bassoon. Nevertheless, we will complete the SIM experiments as suggested to improve the manuscript.

Manuscript consistency:

(1) Figure 2:

The authors looked at VGAT and noticed a reduction of signals in hippocampal regions in their P21 slices, indicating that the proposed postsynaptic organization/stabilization functions of Endophilin A1 extend to the inhibitory presynapse, perhaps via Neuroligin 2-Neurexin. Simultaneously, hippocampal regions in P21 slices showed a reduction in PSD-95 signals, indicating that excitatory synapses are also affected. It would be crucial to also look at excitatory presynapses, via VGLUT staining, to assess whether EndoA1 -/- also affects presynapses. Given the extensive roles of Endophilin A1 in presynapses, especially in excitatory presynapses, this should be investigated.

Thanks for the thoughtful comments. Given that the both VGAT and PSD95 signals are reduced in hippocampal regions in P21 slices, it is conceivable that the proposed postsynaptic organization/stabilization functions of endophilin A1 extend to the inhibitory presynapse via Neuroligin-2-Neurexin and the excitatory presynapse as well during development. Of note, endophilin A1 knockout did not impair the distribution of Neuroligin-2 in inhibitory postsynapses (immunoisolated with anti-GABA_AR α1) in mature mice (Figure 3K), and endophilin A1 did not bind to Neuroligin-2 (Figure 4D), suggesting that endophilin A1 might function via other mechanisms. Nevertheless, as functions of endophilin A family members at the presynaptic site are well-established, the reduction of presynaptic signals in developmental hippocampal regions of EndoA^-/- mice might result from the depletion of presynaptic endophilin A1. The presynaptic deficits can be compensatory by other mechanisms as neurons mature. Certainly, we will do VGLUT staining of EndoA1^-/- brain slices as suggested to assess the role of endophilin A1 in excitatory presynapses in vivo.

(2) Figure 7C:

The authors do not assess whether p140Cap overexpression rescues GABAAR receptor loss exhibited in Endophilin A1 KO, as they did for Gephryin. This would be an important data point to show, as p140Cap may somehow rescue receptor loss by another pathway. In fact, it is mentioned in the text that this experiment was done, "Consistently, neither p140Cap nor the endophilin A1 loss-of-function mutants could rescue the GABAAR clustering phenotype in EEN1 KO neurons (Figure 7C, D)" yet the data for p140Cap overexpression seem to be missing. This should be remedied.

Thanks a lot for the thoughtful comment. We will determine whether p140Cap overexpression also rescues the GABA_AR clustering phenotype in EndoA1^-/- neurons by surface GABA_AR γ2 staining in our revised manuscript.

Reviewer #3 (Public review):

Summary:

Chen et al. identify endophilin A1 as a novel component of the inhibitory postsynaptic scaffold. Their data show impaired evoked inhibitory synaptic transmission in CA1 neurons of mice lacking endophilin A1, and an increased susceptibility to seizures. Endophilin can interact with the postsynaptic scaffold protein gephyrin and promote assembly of the inhibitory postsynaptic element. Endophilin A1 is known to play a role in presynaptic terminals and in dendritic spines, but a role for endophilin A1 at inhibitory postsynaptic densities has not yet been described.

Strengths:

The authors used a broad array of experimental approaches to investigate this, including tests of seizure susceptibility, electrophysiology, biochemistry, neuronal culture, and image analysis.

Weaknesses:

Many results are difficult to interpret, and the data quality is not always convincing, unfortunately. The basic premise of the study, that gephyrin and endophilin A1 interact, requires a more robust analysis to be convincing.

We greatly appreciate the positive comment on our study and the very valuable feedback for us to improve the manuscript. We will conduct additional experiments to improve our data quality and strengthen our evidences according to these great constructive suggestions. To gain strong evidence for the interaction between endophilin A1 and gephyrin, we will perform in vitro pull-down assay with recombinant proteins from bacterial expression system.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) For all of the electrophysiology experiments, only the number of neurons recorded is stated, but not the number of independent animals that these neurons were obtained from. The number of independent animals used should be stated for each panel. At least 3 independent animals should be used in each group, otherwise, more data needs to be added.

We apologize for missing the information in the original manuscript. For all electrophysiological experiments, data were obtained from more than 3 experimental animals. The figure legends were updated to include the number of independent animals used for each panel.

(2) For the cell culture experiments analyzing dendritic puncta at GABAergic synapses, the number of data points analysed appears to be the number of dendritic segments quantified, regardless of whether they originate from the same neuron or not. This analysis method is not valid, since dendritic segments from the same neuron cannot be counted as statistically independent samples. The authors need to average the values for all dendritic segments from one neuron, such that one neuron equals one data point. This alteration should be made for Figures 2B, 2D, 4H, 4J, 5B, 5C, 5E, 5J, 5L, 6B, 6D, 6F, 6H, 6J, 6K,7B, and 7D. In addition, the number of independent cultures from which the neurons were obtained should be stated for each panel. At least 3 independent cultures should be used in each group, otherwise, more data need to be added.

Thanks for the criticism. We reanalyzed the data throughout the manuscript as suggested and updated the figure legends accordingly. Moreover, we increased the number of neurons from independent experiments to further confirm the results in our revised manuscript.

In the revised manuscript, we averaged the values for all dendritic segments from a single neuron and updated the data in Figure 3B, 3D, 4H, 4J, 5B, 5C, 5E, 5K, 5M, 6B, 6D, 6F, 6H, 6J, 6K,7B, and 7D.

Neurons analyzed in each group were derived from at least 3 independent cultures. Due to very low efficiency of sparse transfection in primary cultured hippocampal neurons, multiple experimental repetitions were necessary to obtain the sufficient number of neurons for analysis. We described statistical analysis in “Material and Methods” section in the original manuscript as follows:

“For all biochemical, cell biological and electrophysiological recordings, at least three independent experiments were performed (independent cultures, transfections or different mice).”

(3) Individual data points should be shown on all graphs, particularly in Figures 2C, 2F, 2I, 3F, 3K, and 3L.

Thank you for the suggestion. We replaced the original graphs with scatterplots and mean ± S.E.M. in new Figures.

(4) For each experiment, the authors should state explicitly in the methods section whether that experiment was conducted blind to genotype.

Thank you for the suggestion. We have modified the description of blind analysis for each experiment in methods section to “Seizure susceptibility was measured blindly by rating seizures on a scale of 0 to 7 as follows…”, “Quantification of immunostaining were carried out blindly…” in our revised manuscript.

(5) For each experiment, the authors should state whether they used male or female mice, and what age the mice were at the time of the experiment

Thanks a lot for the suggestion. We usually use male and female mice for neuron culture and behavioral test. We observed no sex-related differences in PTZ-induced behaviors, so the results were pooled together.

For mice ages, P0 pups were used for hippocampal neuron cultures and virus injection in electrophysiological recording assays or FingR probes assays. P14-21 mice were used for electrophysiological recording, immunofluorescent staining and FingR probes detection in brain slice, while adult mice (P60) for behavioral tests, immunofluorescent staining in brain slice and biochemical assays. We have modified the description in genders and ages of mice in methods section to “To evaluate seizure susceptibility, 8-10-week-old male and female EndoA1^+/+ or EndoA1^-/- littermates or EndoA1^fl/fl littermates were intraperitoneally administered… ”, “For virus injection, 8-9-week-old naive male and female littermates were anesthetized…”, “Male and female littermates (P21 or P60) were anesthetized and immediately perfused…”, “Hippocampi of female or male pups (P0) were rapidly dissected under sterile conditions…”, “PSD fractions from adult mouse brain were prepared as previously described…”, “Newborn EndoA1^fl/fl littermates (male or female) were anesthetized on ice for 4-5 min…” in our revised manuscript.

(6) For each experiment involving WT and KO mice, please state whether WTs and KOs were bred as littermates from heterozygous breeders

Sorry for the confusion. In our study, EndoA1^+/+ and EndoA1^-/- mice were bred as littermates from heterozygous breeders. We added the information in methods section as follows in our revised manuscript, “EndoA1^+/+ and EndoA1^-/- mice were bred as littermates from heterozygous breeders…”, “To evaluate seizure susceptibility, 8-10-week-old male and female EndoA1^+/+ or EndoA1^-/- littermates or EndoA1^fl/fl littermates…”, “For virus injection, 8-9-week-old naive male and female littermates were anesthetized…”, “Male and female littermates (P21 or P60) were anesthetized and immediately perfused…”, “For co-IP from brain lysates, the whole brain from 8-10-week-old WT and KO littermates were dissected…”, “Newborn EndoA1^fl/fl littermates (male or female) were anesthetized on ice for 4-5 min…”.

(7) For experiments comparing three or more groups, the authors claim in the methods section to have used a one-way ANOVA for statistical analysis. However, no ANOVA values are given, only the post-hoc tests. Please add the ANOVA values for each experiment before stating the values of the post-hoc analysis.

Sorry for the missing information. We used one-way ANOVA for comparing three or more groups in the original manuscript and have changed to two-way ANOVA for behavior data analysis in our revised manuscript as suggested in Recommendations (18). We added the ANOVA values (F & p values) for each experiment in new figures. For example, see Figure 1C.

(8) In Figure 1A-C, seizure susceptibility was compared in EEN+/+ and EEN-/- mice, but the methods section states that seizure susceptibility was evaluated in 8-10-week-old male C57BL/6N mice (line 513). Was this meant to indicate that the EEN+/+ and EEN-/- mice were on a C57BL/6N background? How does this match with the statement that EEN1 -/- mice were generated on a C57BL/6J background (line 467)?

We apologize for the mistake. In our study, EEN1^-/- mice were generated on a C57BL/6J background, as stated in our previously published papers (Yang et al., 2021; Yang et al., 2018) and in “Animals” in Material and Methods of our original manuscript. We had corrected the statement to “To evaluate seizure susceptibility, 8-10-week-old male and female EndoA1^+/+ or EndoA1^-/- littermates…” in Material and Methods of the revised manuscript.

(9) In the electrophysiology experiments in Figure 1E-O, it is not clear to me which neurons were recorded in the control group. The methods section states that "Whole-cell recordings were performed on an AAV-infected neuron and a neighboring uninfected neuron" (line 736). However, the figure legends states that recordings were obtained from "10 control (Ctrl, mCherry alone) and 10 EEN1 KO (mCherry and Cre) pyramidal neurons" (line 1079), which would indicate that the controls are not uninfected neurons from the same animal, but AAV-mCherry infected neurons from a different animal. Please clarify which of the two descriptions is accurate.

Thanks for catching the error! In all electrophysiological experiments, a neighboring uninfected neuron was used as the control in Figure 1E-O. This was incorrectly stated in the figure legend of the original manuscript. In the revised manuscript, the information has been corrected in figure legends of new Figure 1 (E-F).

(10) The authors show that in Endophilin A1 KO animals, eIPSCs are reduced, but mIPSC frequency and amplitude are unaltered. How do they explain this finding in the context of the fact that gephyrin and GABAAR1.

We apologize for the confusion about the data of electrophysiological recording. Compared with eIPSC, which are recorded in the presence of electrically evoked action potential that elicited a substantial release of neurotransmitter, mIPSCs are small, spontaneous currents recorded in the presence of TTX during patch-clamp experiments, resulting from the release of neurotransmitters from presynaptic terminals in the absence of action potential. The amplitude of mIPSCs typically reflects the quantal release of neurotransmitters, while their frequency can vary depending on synaptic activity and the state of the neuron.

A number of molecules fine-tune presynaptic neurotransmitter release and functions of inhibitory postsynaptic receptors. In our study, inhibitory postsynapses were partially affected in endophilin A1 knockout neurons, while presynaptic endophilin A1 remained intact during electrophysiological recordings. Conceivably, the observed deficits in endophilin A1 knockout mice were mild. Following endophilin A1 depletion, inhibitory postsynaptic receptors appeared sufficient to respond to spontaneous neurotransmitter release but may be inadequate to large amounts of neurotransmitter release evoked by action potential. Meanwhile, spontaneous synaptic activity and the state of the neuron were not obviously affected under basic state by endophilin A1 depletion during postnatal stages. Consequently, mIPSC frequency and amplitude remain unaltered but eIPSCs were reduced compared to the control neurons. This finding was consistent with behavioral experiments, where aggressive epileptic behaviors were induced by PTZ rather than spontaneous epilepsy in endophilin A1 knockout mice.

(11) Distribution of gephyrin, VGAT, and GABAARg2 differs substantially between the different layers of hippocampal area CA1, and the same goes for the other regions of the hippocampus. However, in Figure 2, it is not clear to me from the sample images which layers of each subregion the authors quantified, or indeed whether they paid attention to which layers they included in their analysis. This can lead to a substantial skewing of the data if different layers were preferentially included in the two genotypes. Please clarify which layers were analysed, and how comparability between WTs and KOs was ensured. This is particularly important given the authors' claim that Endophilin A1 acts equally at all subtypes of GABAergic synapses (lines 373- 376).

Thanks for the cautiousness! We distinguished each hippocampal subregion based on the anatomical structure in brain slices. Quantification of fluorescent mean intensity of each synaptic protein in all layers of each subregion, as shown in new Figure 2 and Figure S2A-F, revealed that GABAergic synaptic proteins were impaired in both P21 and P60 KO mice.

We further analyzed the fluorescent signal of core postsynaptic component, gephyrin, in individual layers of each subregion in the hippocampus of mature WT and KO mice, as presented in new Figures S2G-H. Our findings demonstrated a decrease in gephyrin levels across all layers of each subregion in KO mice. Additionally, we examined gephyrin clustering across the soma, axon initial segment (AIS), and dendrites in cultured mature endophilin A1 knockout hippocampal neurons, as shown in new Figure S5E-H. The results showed that gephyrin was affected in all subcellular regions following endophilin A1 knockout.

Collectively, these data suggest that endophilin A1 functions across all subtypes of GABAergic postsynapses.

(12) In Figure 3E-F, the authors state that there was no change in the total level of synaptic neurons in EEN1 KO neurons (line 188). However, there is no quantification of the total level of synaptic neurons shown, and based on the immunoblot in Figure 3E, it looks like there is a substantial reduction in NR1, NL2, and g2. The authors should present a quantification of the total levels of these proteins and adjust their statement accordingly if necessary.

Thanks a lot for your comments. We quantified the total protein levels in Figure 3E and added the result to new Figure 3F, showing that total protein levels were not obviously affected in cultured KO neurons. When normalized to total protein levels, the surface levels of GABA_A receptors were significantly compromised compared to surface GluN1 and NL2. Furthermore, the total protein levels were not affected in brains of KO mice, as shown in Figures 3K (input) and 3L (S1). Collectively, there was no change in the total level of synaptic proteins in KO neurons.

(13) In Figure 3G-I, the authors claim, based on super-resolution images as presented here, that Endophilin A1 colocalizes with gephyrin and g2. However, no quantification of this colocalization is presented. The authors should add this quantification to support their claim and indicate how many GABAergic synapses contain Endophilin A1.

Thank you for the thoughtful comments. The resolution of the images is significantly improved by super-resolution microscopy. As a result, the overlap between the two proteins will become smaller or even disappear. Since no two proteins can occupy the same physical space, they would show lower colocalization and instead exhibit proximal localization. As expected, in Figures 3G and 3H, we observed only small overlap or proximal localization of endophilin A1 with gephyrin or GABA_AR γ2. To further confirm the localization of endophilin A1 in inhibitory synapses, we co-stained endophilin A1 with both pre- and post-synaptic proteins, gephyrin and Bassoon. Then we quantified the colocalization of endophilin A1 with gephyrin or with Bassoon using the method for super-resolution images described in the reference (Andrew D. McCall. Colocalization by cross-correlation, a new method of colocalization suited for super-resolution microscopy. McCall BMC Bioinformatics (2024) 25:55). The percentage of gephyrin or Bassoon puncta that were in close proximity with endophilin A1 was also calculated, as shown in new video 5 and new Figure S4B-G. These data have been added in the revised manuscript as follows, “We further detected the localization of endophilin A1 to inhibitory synapses by co-immunostaining with both pre- and post-synaptic markers (Figure. S4B and Video 5). Quantitative analysis of super-resolution localization maps revealed that ~ 47 % puncta of gephyrin or Bassoon were proximal to endophilin A1 (Figure. S4G, n \= 14), with a mean distance between endophilin A1- and gephyrin-positive pixels of ∼ 120 nm, or between endophilin A1- and Bassoon-positive pixels of ∼ 130 nm (Figure. S4C-F).”

(14) In the quantification shown in Figure 3K-L, there are no error bars in the WT data sets. This presumably means that all values were normalized to WT. However, since this artificially eliminates the variance in the WT group, a t-test is no longer valid, since this assumes a normal distribution and normal variance, which are no longer given. The authors should either change the way they normalize their data to maintain the variance in the WT group or perform a different statistical test that can account for the artificial lack of variance in one of the groups.

Thank you for the suggestions! We modified our analysis approach. Specifically, we used mean value of WTs to normalize data to preserve the variance in the WT group and performed unpaired t-tests to assess statistical significance in Figure 3K-L. Additionally, we replaced the bar graphs with modified graphs showing individual data points. Please see Response to Recommendation (12).

(15) What is the difference between the coIP experiment in Figure 4E and 3J, right panel? In both cases, an Endophilin A1 IP is performed, and gephyrin, GABAARg2, and GABAARa1 are assessed. However, Figure 3J's right panel indicates that Endophilin A1 does interact with the GABAAR subunits, whereas Figure 4E shows that it does not. How do the authors explain this discrepancy? Were these experiments performed more than once?

Sorry for the confusion. Figure 3J and Figure 4E show data from immunoisolation assay and conventional co-immunoprecipitation (co-IP), respectively. Immunoisolation allows for the rapid and efficient separation of subcellular membrane compartments using antibodies conjugated to magnetic beads. In Figure 3J, we used antibodies against GABA_AR α1 subunit or endophilin A1 to isolate the inhibitory postsynaptic membranes or endophilin A1-associated membranous compartments. In contrast, co-immunoprecipitation detects direct protein-protein interactions in detergent-solubilized lysates. For Figure 4E, we applied antibodies against endophilin A1 to precipitate its interaction partners. The results in Figure 3J and Figure 4E demonstrate that endophilin A1 is localized in the inhibitory postsynaptic compartment and directly interacts with gephyrin, but not with GABA_ARs. Detailed information regarding the methods used for co-IP and immunoisolation can be found in “GST-pull down, co-immunoprecipitation (IP), and immunoisolation” in the “Material and Methods” section of original manuscript.

These experiments were repeated multiple times to ensure reliability. In fact, consistent data showing endophilin A1 localization in the inhibitory postsynaptic compartment were observed in Figure 3K, showing the quantified data as well.

(16) For the colocalization analysis in Figure 5A-C, what percentage of gephyrin puncta contain g2 in the WT and Endophilin A1 KO? Currently, only a correlation coefficient is provided, but not the degree of overlap. Please add this information to the figure.

Thanks for the comments on the colocalization analysis. We analyzed the percentage of gephyrin puncta overlapping with GABA_AR γ2 and added the graphs in new Figure 5C.

(17) Figure 6 investigates how actin depolarization affects GABAergic synapse function, but does not assess how Endophilin A1 contributes to this process. The authors then provide an extremely short statement in the discussion, stating that their data are contradictory to a previous study (lines 412 - 417). This section of the discussion should be expanded to address the specific role of Endophilin A1 in the consequences of actin depolymerization.

Thanks a lot for the advice. In the original manuscript, we discussed the specific role of endophilin A1 at inhibitory postsynapses as follows in Discussion:

“As membrane-binding and actin polymerization-promoting activities of endophilin A1 are both required for its function in enhancing iPSD formation and g2–containing GABA_AR clustering to iPSD, we propose that membrane-bound endophilin A1 promotes postsynaptic assembly by coordinating the plasma membrane tethering of the postsynaptic protein complex and its stabilization with the actin cytomatrix”

Following your advice, we added a statement in the revised manuscript addressing the role of endophilin A1 in actin polymerization at inhibitory postsynapses, shown as follows, “In the present study, the impaired clustering of gephyrin and GABA_A γ2 by F-actin depolymerization underscores the essential role of F-actin in the assembly and stabilization of the inhibitory postsynaptic machinery. Membrane-bound endophilin A1 promotes F-actin polymerization beneath the plasma membrane through its interaction with p140Cap, an F-actin regulatory protein, thereby facilitating and/or stabilizing the clustering of gephyrin and γ2-containing GABA_A ​receptors at postsynapses.”

(18) Which statistical analysis was conducted in Figure 7F? Given the nature of the data, a repeated measures ANOVA would be necessary to accurately assess the statistical accuracy.

Sorry for the confusion. We conducted one-way ANOVA followed by Tukey post hoc test at each time point in original Figure 7F. We have employed the method of repeated measures ANOVA followed by Tukey post hoc test as suggested in new Figure 7F. Meanwhile, we reanalyzed data in new Figure 1C with the same method. We also modified the description in “Statistical analysis” and Figure legends for new Figure1C and 7F in revised manuscript.

Reviewer #2 (Recommendations for the authors):

Data presentation:

(1) Figures 2A, B, D, E, G, H. Figures S2A, B, D:

Add P21 or P60 labels to these figures so that the difference between similarly stained samples (e.g. Figures 2A, B) is obvious to the reader.

Thanks! We added “P21” or “P60” labels in new Figure 2 and Figure S2 as suggested.

(2) Figures 4C, D:

The authors must make their coIP data annotation consistent. In Figure 4C, they use actual microgram amounts when, e.g., describing how much input was present, yet in Figure 4D they use + and -. The authors should pick one.

Thanks for the comments. We labeled the consistent data annotation in new Figure 4C and 4D, we also changed the label in 4F for the consistent data annotation.

(3) Figure 5A

GFP is gray in this figure, but in all other figures, it is blue. Consider changing for presentation reasons.

Thanks a lot for pointing out the problem. We replaced gray with blue color to indicate GFP in new Figure 5A.

(4) Figures 6A, C, E, G

Label graphs as either short-term or long-term drug treatment.

Thanks for the suggestion. We labeled the graphs as 60 min for short-term or 120 min for long-term drug treatment in new Figure 6A, C, E, G for convenient reading.

Annotation, grammar, spelling, typing errors:

(1) Figure 4G:

Merge and GFP labels are seemingly swapped.

Thanks a lot for sharp eye. We corrected the labels in new Figure 4G.

(2) Fig 4I:

The authors use "Gephryin" instead of GPN. They should be consistent and choose one.

Sorry for the mistake. We changed the label consistent with other figures in new Figure 4I and rearranged the images in figures for good looking.

(3) "One-hour or two-hour treatment of mature neurons with nocodazole..."

Thanks for your advice. We modified the sentence to “Treatment of mature neurons with nocodazole, a microtubule depolymerizing reagent, for one hour (short-term) or two hours (long-term), caused…”.

(4) The authors should indicate that one-hour is their short-term treatment and that two-hour is their long-term treatment so that when these terms are used later to describe LatA experiments, it is clearer to the reader.

Thanks for your comments. We modified the statement as seen in Response to Recommendation (3), it is clearer to the reader.

(5) EEA1. The authors should use a more conventional term EndoA1 so that the manuscript can be searched easily.

Thanks a lot for the suggestion. We replaced all of the term “EEN1” with “EndoA1” in the revised manuscript.

Reviewer #3 (Recommendations for the authors):

Major Points

(1) The number of observations for the electrophysiology experiments in Figure 1 (dots are neurons) is very low and it is not clear whether the data shown is derived from different mice. The same criticism applies to the data shown in Figures 7G-K.

We apologize for the low neuron number in electrophysiology experiments. In the patch-clamp experiments, the number of neurons recorded was higher than what is shown in the figures. However, neurons with a membrane resistance (Rm) below 500 MΩ, indicating unstable seals or poor conditions, were excluded from the analysis. Additionally, we added the number of mice from which the data derived in each group in the figure legends for Figure 1, 7 and S1, this point was also raised by Reviewer #1 (Please see Response to Recommendation (1)).

(2) Images in Figure 2 are shown at low magnification, statements on changes in intensity of inhibitory synaptic markers in the hippocampal region are impossible to interpret. Analysis of inhibitory synapses in vivo would require sparse neuronal labeling and 3D reconstruction, for instance using gephyrin-FingRs (Gross et al., Neuron 2013).

Thanks for your insightful suggestion. We obtained pCAG_PSD95.FingR-eGFP-CCR5TC and pCAG_GPN.FingR-eGFP-CCR5TC constructs from Addgene (plasmid # 46295 & #46296). We attempted in utero electroporation (IUE) to introduce the DNAs into cortical neurons or hippocampal neurons at E14.5, unfortunately with no success. Following the repetitive operation for numerous times, we could eventually obtain newborn pups of ICR mice after IUE. However, we failed to obtain any newborn pups of C57BL/6J mice due to abortion following the procedure. Furthermore, pregnant C57BL/6J mice (WTs or KOs) did not survive or remained in a poor state of health after surgery. Therefore, we were unable to analyze synapses through sparse labeling and 3D reconstruction by IUE. Alternatively, we obtained commercial AAVs carrying rAAV-EF1a-PSD95.FingR-eGFP-CCR5TC and rAAV-EF1a-mRuby2-Gephyrin.FingR-IL2RGTC, then injected into the CA1 region of EndoA1^fl/fl mice at P0. Mice were fixed and detected the fluorescent signals in CA1 regions at P21. Consistent with immunostaining with antibodies, decreased mRuby2-Gephyrin.FingR or PSD95.FingR-eGFP was observed in dendrites of KO neurons at P21, as shown in new Figure S3. In combination with electrophysiological recording, PSD fractionation and immunoisolation from brains, these data support our conclusion regarding the effects of endophilin A1 knockout on the inhibitory synapses.

Additionally, we transfected DIV12 cultured hippocampal neurons with pCAG_PSD95.FingR-eGFP-CCR5TC or pCAG_GPN.FingR-eGFP-CCR5TC and observed fluorescent signals on DIV16. Both the signal intensity and number of GPN.FingR-eGFP clusters were also significantly attenuated, with no obvious changes in PSD95.FingR-eGFP clusters in dendrites of mature neurons, as shown in new Figure S5A-D. We are very pleased that the result further strengthened our original conclusion. We have added the new pieces of data in our revised manuscript.

(3) Figure 3: surface labeling of GluA1 or the GABAAR gamma 2 subunit is difficult to interpret: the patterns are noisy and the numerous puncta appear largely non-synaptic although this is difficult to judge in the absence of additional synaptic markers. It appears statistics are done on dendritic segments rather than the number of neurons. The legend does not mention how many independent cultures this data is derived from. In their previous study (Yang et al., Front Mol Neurosci 2018), the authors noted a decrease in surface GluA1 levels in the absence of endophilin A1. How do they explain the absence of an effect on surface GluA1 levels in the current study?

Sorry for the concern and thanks for your comments. First, we assessed changes in the surface levels of excitatory and inhibitory receptors by co-immunostaining in cultured WT and KO hippocampal neurons. Given the very low transfection efficiency of neurons in high density culture, numerous puncta of receptors from adjacent non-transfected neurons were also detected. This approach may contribute to the noisy pattern observed in Figure 3A. Besides, the projections of z-stack for higher magnified dendrites may likely introduced higher background signals. We have now replaced the original images with the newest repeat in new Figure 3A. Moreover, we confirmed a decrease in the surface expression of GABA_AR γ2 by the biotinylation assay, as shown in Figure 3E. Indeed, we agree that some puncta for surface labeling of receptors seemed to be non-synaptic localization. In order to reflect the decrease in synaptic proteins at synapses, we isolated PSD fraction by biochemical assay and found that gephyrin and GABA_AR γ2, two major inhibitory postsynaptic components, were reduced in the PSD fraction from KO brains, as shown in Figure 3L. Their colocalization was also attenuated in the absence of endophilin A1, as shown in Figure 5A-C. Combined with electrophysiological recording, these data from multiple assays indicate GluA1 at synapses was not obviously affected but GABA_AR γ2 at synapses was impaired in endophilin A1 KO neurons in the present study.

We have corrected the way that the number of samples is defined for statistical analysis as suggested. This point was also raised by Reviewer #1 (Recommendation (2)). We averaged the values from all dendritic segments of a single neuron, such that one neuron equaled one data point. We had replaced the original Figure 3B and 3D (please see Response to Recommendation (2) by Reviewer #1). Additionally, we added the number of independent cultures these data were derived from to figure legends in revised manuscript.

Previously, we observed a small decrease in surface GluA1 levels in spines under basal conditions and a more pronounced suppression of surface GluA1 accumulation in spines upon chemical LTP in endophilin A1 KO neurons from EndoA1^-/- mice that knockout endophilin A1 since embryonic development stages (Figure 5C,H. Yang et al., Front Mol Neurosci, 2018). In Figure 3A and B in current study, we analyzed surface receptor levels in GFP-positive dendrites, rather than spines, under basal conditions when endophilin A1 was depleted at the later developmental stage. We found a decrease in surface GABA_AR γ2 levels but no significant effects on surface GluA1 levels in dendrites. These findings indicate that endophilin A1 primarily affects excitatory synaptic proteins in spines during synaptic plasticity and inhibitory synaptic proteins in dendrites under basal conditions in mature neurons.

(4) Super-resolution images in Figure 3G, H, I: endophilin A1 puncta look different in panel 3I compared to 3G and 3H, which are very noisy. It is difficult to interpret how specific these EEN1 puncta are. Previous images showing EEN1 distribution in dendrites look different (Yang et al., Front Mol Neurosci 2018); is the same KO-verified antibody being used here? Colocalization of EEN1 with gephyrin or the GABAAR gamma 2 subunit is difficult to interpret; gephyrin mostly does not seem to colocalize with EEN1 in the example shown.

Sorry for your concerns. As stated previously in Major Points (3), transfection efficiency was very low in cultured neurons and our cultured neurons were at relative high density. As a result, numerous puncta of proteins located in the adjacent non-transfected neurons were also detected, which may contribute to noisy signals observed in Figure 3G-I.

In our previous paper, we confirmed the specificity of the antibody against endophilin A1 (5A,B. Yang et al., Front Mol Neurosci, 2018). We used the same antibody (rabbit anti-endophilin A1, Synaptic Systems GmbH, Germany) in the current study. While the previous images were obtained using confocal microscopy, the current images in Figures 3G, H, and I were acquired using super-resolution microscopy (SIM). The different patterns observed in the dendrites may be attributed to the difference in image resolution, antibodies dilution and reaction time.

Reviewer #1 also points out the quantification of colocalization of gephyrin and GABA_AR γ2 with endophilin A1. Please see Response to Recommendation (13) by Reviewer #1.

(5) The interaction of gephyrin and endophilin A1 is based on coIP experiments in cells and brain tissue. To convincingly demonstrate that these proteins interact, biophysical experiments with purified proteins are necessary.

Thanks a lot for your great suggestions on the interaction of endophilin A1 with gephyrin. To convincingly demonstrate their interaction, we performed pull-down assay with purified recombinant proteins and the result shows that both G and E domains of gephyrin were involved in the interaction with endophilin A1. The data has been added to the revised manuscript as new Figure 5I. We also modified the statement about the data and figure legends in the revised manuscript.

(6) Figure 4G: the gephyrin images are not convincing; the inhibitory postsynaptic element typically looks somewhat elongated; these puncta are very noisy and do not appear to represent iPSDs. The same criticism applies to the images shown in Figures 5 and 7.

Thanks for the comment. The gephyrin puncta in our images exhibited heterogeneous shapes and sizes, with some appearing somewhat elongated. To address this, we compared the puncta pattern of gephyrin with that shown in the reference. As illustrated in the figure from the reference, gephyrin puncta also displayed distinct shapes and sizes, Figure 3A-F, Neuron 78, 971–985, June 19, 2013). Please note that the images were z-stack projections at higher magnification, as described in the "Materials and Methods" section. This approach may likely introduce higher background signals and may contribute to the much more heterogeneous appearance of the puncta in Figures 4, 5, and 7. As mentioned previously, the numerous gephyrin puncta located in the adjacent non-transfected neurons may also contribute to some of the noisy signals observed. We have replaced the original images with new images in new Figure 4G, 5 and 7.

Moreover, in order to confirm the effects of endophilin A1 KO on the gephyrin clustering, we also detected the endogenous clusters of gephyrin or PSD95 visualized by GPN.FingR-eGFP or PSD95.FingR-eGFP in cultured mature neurons. The results were consistent with immunostaining with antibodies against gephyrin. Please see Response to Recommendation (2)

(7) Figure 7E, F: the rescue (Cre + WT) appears to perform better than the control (mCherry + GFP) in the PTZ condition; how do the authors explain this? Mixes of viral vectors were injected, would this approach achieve full rescue?

Thanks for the thoughtful comment. Mixed viruses were injected bilaterally into the hippocampal CA1 regions. The results showed a full rescue effect by WT endophilin A1 in knockout mice during the early days, with even a little bit better rescue effect than the control group in the later days under the PTZ condition, as shown in Figures 7E and 7F. In the current study, overexpression of endophilin A1 increased the clustering of gephyrin and GABA_AR γ2 in cultured neurons, as shown in Figures 4I-J and 5D-E. Presumably, the slightly better rescue effects observed in the behavioral tests was likely attributed to the enhanced clustering and/or stabilization of gephyrin/GABA_AR γ2 by WT endophilin A1 expression in KO neurons in vivo. Moreover, the electrophysiological recording also showed full rescue effects on eIPSC by WT endophilin A1 in KO neurons (Figure 7G-K).

Minor Points

(1) The authors mention that they previously found a decrease in eEPSC amplitude in EEN1 KO mice (Yang et al., Front Mol Neurosci 2018). The data in Fig. 1E suggests a decrease in eEPSC amplitude but is not significant here, likely due to the small number of observations. If both eEPSC and iEPSC amplitude are reduced in the absence of EEN1. Would the E/I ratio still be significantly changed?

We apologize for the confusion. In our previous study, AMPAR-mediated excitatory postsynaptic currents (eEPSCs) were found to be slightly but significantly reduced compared to the control group, while NMDAR-mediated excitatory postsynaptic currents showed no significant difference (Figure 4N,O. Yang et al., Front Mol Neurosci, 2018). In the current study, we adopted a different recording protocol, simultaneously measuring eEPSCs and eIPSCs from the same neuron to calculate the E/I ratio. Unlike previous studies, we did not use inhibitors to suppress GABA receptor activity. As a result, the recorded signals did not distinguish AMPAR-mediated or NMDAR-mediated excitatory postsynaptic currents to reflect total eEPSCs, which may explain the non-significant reduction observed compared to control neurons in this study.

It is possible that the eEPSC amplitude would show a significant reduction if a larger number of neurons were recorded. Nevertheless, the larger suppression of eIPSCs in the absence of endophilin A1 indicates that the E/I ratio is significantly altered.

(2) Page 7: the authors mention they aim to exclude effects on presynaptic terminals of deleting endophilin A1 in cultured neurons, is this because of a sparse transfection approach?

Please clarify.

Sorry for the confusion. In cultured neurons, we always observed sparse transfection due to the very low transfection efficiency (~ 0.5%). Therefore, we could examine the effects of endophilin A1 knockout specifically in the specific CamKIIa promoter-driven Cre-expressing postsynaptic neurons, while endophilin A1 remained intact in the non-transfected presynaptic neurons.

(3) The representative blot of the surface biotinylation experiment (Figure 3E) suggests that loss of endophilin A1 also affects GluN1 and Nlgn2 levels, and error bars in panel 3F (lacking individual data points) suggest these experiments were highly variable.

Sorry for the confusion. Reviewer #1 also raised the question and we quantified the total level of GluN1 and NL2 in Figure 3E. And we replaced the original graphs with scatterplots and means ± S.E.M. Please see the Response to Recommendation (3) & (12) by Reviewer #1.

(4) Have other studies analyzing inhibitory synapse composition identified endophilin A1 as a component? The rationale for this study seems to be primarily based on the presence of epileptic seizures and E/I imbalance.

Thank you for your questions. To date, no other studies investigated endophilin A1 as an inhibitory postsynaptic component. We observed the proximal localization of endophilin A1 with inhibitory postsynaptic proteins using super-resolution microscopy (SIM) and quantification results showed ~ 47% puncta of gephyrin correlated with endophilin A1 (Figure 3G-I and S4B-G). We further immunoisolated the inhibitory postsynaptic fraction using GABA_A receptors and found that endophilin A1 was present in the isolated fraction, and vice versa (Figure 3J). Additionally, we demonstrated that endophilin A1 directly interacted with gephyrin through co-IP and pull-down assays (Figure 5J-I). Together with data from immunolabeling, biochemical assays, electrophysiological recordings, and behavioral tests, these results identified endophilin A1 as an inhibitory postsynaptic component.

(5) Figure 3J: what are S100 and P100 labels? Is Nlgn2 part of the EEN1 complex? If it is, why are Nlgn2 surface levels not affected by EEN1 loss (Figure 3E, F, K)? Why does EEN1 not interact with Nlgn2 in HEK cells (Figure 4D)?

Sorry for the confusion. The detailed information regarding S100 and P100 can be found in the “GST-pull down, co-immunoprecipitation (IP), and immunoisolation” in the “Materials and Methods” section. S100 contains soluble proteins, while P100 refers to the membrane fraction after high speed (100,000xg) centrifugation.

Figures 3J-K and 4C-F showed the data from immunoisolation and conventional co-immunoprecipitation assays, respectively. Immunoisolation, which uses antibodies coupled to magnetic beads, allows for the rapid and efficient separation of subcellular membrane compartments. In Figure 3J-K, we used antibodies against GABA_AR α1 to isolate membrane protein complexes from the inhibitory postsynaptic fraction. In contrast, co-immunoprecipitation typically detects direct interactions between proteins solubilized by detergent treatment. For Figure 4C-F, FLAG beads were used in HEK293 lysates, or antibodies against endophilin A1 were employed in brain lysates to precipitate direct interaction partners. Combined with the results from Figure 3J-L, the data in 4C-F indicated that endophilin A1 was localized in the inhibitory postsynaptic compartment and directly bound to gephyrin but not to either GABA_A receptors or Nlgn2 (NL2). This binding promoted the clustering of gephyrin and GABA_AR γ2 at synapses, facilitating GABA_AR assembly.

Nlgn2 (NL2) is a key inhibitory postsynaptic component but does not directly bind to endophilin A1. Consequently, endophilin A1 failed to co-immunoprecipitate with NL2 in the presence of detergent in HEK293 cell lysates (Figure 4D). Furthermore, the surface levels of NL2 or its distribution in PSD fraction were unaffected by the loss of endophilin A1 (Figure 3E, F, K, L). This suggests that mechanisms independent of endophilin A1 orchestrate the surface expression and synaptic distribution of NL2.

(6) How do the authors interpret the finding that endophilin A1, but not A2 or A3, binds gephyrin? What could explain these differences?

Thanks for the thoughtful comment. Endophilin As contain BAR and SH3 domains. While the amino acid sequences in the BAR and SH3 domains are highly conserved, the intrinsically disordered loop region between BAR and SH3 domains is highly variable. A study by the Verstreken lab revealed that a human mutation in the unstructured loop region of endophilin A1 increases the risk of Parkinson's disease. They also demonstrated that the disordered loop region controls protein flexibility, which fine-tunes protein-protein and protein-membrane interactions critical for endophilin A1 function (Bademosi et al., Neuron 111, 1402–1422, May 3, 2023). Our previous study showed that endophilin A1 and A3, but not A2, bind to p140Cap through their SH3 domains, despite the high sequence homology in the SH3 domains among these proteins (Figure2A,B. Yang et al., Cell Research, 2015). These findings indicate that each endophilin A likely interacts with specific partners due to distinct key amino acids.

Additionally, endophilin A1 is expressed at much higher levels than A2 and A3 in neurons, with distinct distribution of them across different brain regions. Our lab demonstrated that the function of A1 at postsynapses (both excitatory and inhibitory synapses) cannot be compensated by A2 or A3. Therefore, it is reasonable that endophilin A1, rather than A2 or A3, binds to gephyrin, even though the underlying mechanisms remain unclear.

(7) Figure 4G: panels are mislabeled (GFP vs merge).

Thanks for careful reading and sorry for the mistake. We corrected the label in new Figure 4G. Please see Response to Annotation, grammar, spelling, typing errors:(1) by Reviewer #2.

Author response:

Reviewer #1 (Public review):

Summary:

The manuscript by Ross, Miscik, and others describes an intriguing series of observations made when investigating the requirement for podxl during hepatic development in zebrafish. Podxl morphants and CRISPants display a reduced number of hepatic stellate cells (HSCs), while mutants are either phenotypically wild type or display an increased number of HSCs.

The absence of observable phenotypes in genetic mutants could indeed be attributed to genetic compensation, as the authors postulate. However, in my opinion, the evidence provided in the manuscript at this point is insufficient to draw a firm conclusion. Furthermore, the opposite phenotype observed in the two deletion mutants is not readily explainable by genetic compensation and invokes additional mechanisms.

Major concerns:

(1) Considering discrepancies in phenotypes, the phenotypes observed in podxl morphants and CRISPants need to be more thoroughly validated. To generate morphants, authors use "well characterized and validated ATG Morpholino" (lines 373-374). However, published morphants, in addition to kidney malformations, display gross developmental defects including pericardial edema, yolk sack extension abnormalities, and body curvature at 2-3 dpf (reference 7 / PMID: 24224085). Were these gross developmental defects observed in the knockdown experiments performed in this paper? If yes, is it possible that the liver phenotype observed at 5 dpf is, to some extent, secondary to these preceding abnormalities? If not, why were they not observed? Did kidney malformations reproduce? On the CRISPant side, were these gross developmental defects also observed in sgRNA#1 and sgRNA#2 CRISPants? Considering that morphants and CRISPants show very similar effects on HSC development and assuming other phenotypes are specific as well, they would be expected to occur at similar frequencies. It would be helpful if full-size images of all relevant morphant and CRISPant embryos were displayed, as is done for tyr CRISPant in Figure S2. Finally, it is very important to thoroughly quantify the efficacy of podxl sgRNA#1 and sgRNA#2 in CRISPants. The HRMA data provided in Figure S1 is not quantitative in terms of the fraction of alleles with indels. Figure S3 indicates a very broad range of efficacies, averaging out at ~62% (line 100). Assuming random distribution of indels among cells and that even in-frame indels result in complete loss of function (possible for sgRNA#1 due to targeting the signal sequence), only ~38% (.62*.62) of all cells will be mutated bi-allelically. That does not seem sufficient to reliably induce loss-of-function phenotypes. My guess is that the capillary electrophoresis method used in Figure S3 underestimates the efficiency of mutagenesis, and that much higher mutagenesis rates would be observed if mutagenesis were assessed by amplicon sequencing (ideally NGS but Sanger followed by deconvolution analysis would suffice). This would strengthen the claim that CRISPant phenotypes are specific.

The reviewer points out some excellent caveats regarding the morphant experiments. We agree that at least some of the effects of the podxl morpholino may be related to its effects on kidney development and/or gross developmental defects that impede liver development. Because of these limitations, we focused our experiments on analysis of CRISPant and mutant phenotypes, including showing that podxl (Ex1(p)_Ex7Δ) mutants are resistant to CRISPant effects on HSC number when injected with sgRNA#1. We did not observe any gross morphologic defects in podxl CRISPants. Liver size was not significantly altered in podxl CRISPants (Figure 2A). We will add brightfield images of podxl CRISPant larvae to the supplemental data for the revised manuscript.

We agree with the reviewer that HRMA is not quantitative with respect to the fraction of alleles with indels and that capillary electrophoresis likely underestimates mutagenesis efficiency. Nonetheless, even with 100% mutation efficiency, podxl CRISPant knockdown, like most CRISPR knockdowns, would not represent complete loss of function:  ~1/3 of alleles will contain in-frame mutations and likely retain at least some gene function, so ~1/3*1/3 = 1/9 of cells will have no out-of-frame indels and contain two copies of at least partially functional podxl and ~2/3*2/3 = 4/9 of cells will have one out-of-frame indel and one copy of at least partially functional podxl. Thus, the decreased HSCs we observe with podxl CRISPant likely represents a partial loss-of-function phenotype in any case.

(2) In addition to confidence in morphant and CRISPant phenotypes, the authors' claim of genetic compensation rests on the observation that podxl (Ex1(p)_Ex7Δ) mutants are resistant to CRISPant effect when injected with sgRNA#1 (Figure 3L). Considering the issues raised in the paragraph above, this is insufficient. There is a very straightforward way to address both concerns, though. The described podxl(-194_Ex7Δ) and podxl(-319_ex1(p)Δ) deletions remove the binding site for the ATG morpholino. Therefore, deletion mutants should be refractive to the Morpholino (specificity assessment recommended in PMID: 29049395, see also PMID: 32958829). Furthermore, both deletion mutants should be refractive to sgRNA#1 CRISPant phenotypes, with the first being refractive to sgRNA#2 as well.

The reviewer proposes elegant experiments to address the specificity of the morpholino. For the revision, we plan to perform additional morpholino studies, including morpholino injections of podxl mutants and assessment of tp53 and other immune response/cellular stress pathway genes in podxl morphants.

Reviewer #2 (Public review):

In this manuscript, Ross and Miscik et. al described the phenotypic discrepancies between F0 zebrafish mosaic mutant ("CRISPants") and morpholino knockdown (Morphant) embryos versus a set of 5 different loss-of-function (LOF) stable mutants in one particular gene involved in hepatic stellate cells development: podxl. While transient LOF and mosaic mutants induced a decrease of hepatic stellate cells number stable LOF zebrafish did not. The authors analyzed the molecular causes of these phenotypic differences and concluded that LOF mutants are genetically compensated through the upregulation of the expression of many genes. Additionally, they ruled out other better-known and described mechanisms such as the expression of redundant genes, protein feedback loops, or transcriptional adaptation.

While the manuscript is clearly written and conclusions are, in general, properly supported, there are some aspects that need to be further clarified and studied.

(1) It would be convenient to apply a method to better quantify potential loss-of-function mutations in the CRISPants. Doing this it can be known not only percentage of mutations in those embryos but also what fraction of them are actually generating an out-of-frame mutation likely driving gene loss of function (since deletions of 3-6 nucleotides removing 1-2 aminoacid/s will likely not have an impact in protein activity, unless that this/these 1-2 aminoacid/s is/are essential for the protein activity). With this, the authors can also correlate phenotype penetrance with the level of loss-of-function when quantifying embryo phenotypes that can help to support their conclusions.

Reviewer #2 raises an excellent point that is similar to Reviewer #1’s first concern. Please see our response above. In general, we agree that correlating phenotype penetrance with level of loss-of-function is a very good way to support conclusions regarding specificity in knockdown experiments. Unfortunately, because the phenotype we are examining (HSC number) has a relatively large standard deviation even in control/wildtype larvae (for example, 63 ± 19 (mean ± standard deviation) HSCs per liver in uninjected control siblings in Figure 1) it would be technically very difficult to do this experiment for podxl.

(2) It is unclear that 4.93 ng of morpholino per embryo is totally safe. The amount of morpholino causing undesired effects can differ depending on the morpholino used. I would suggest performing some sanity check experiments to demonstrate that morpholino KD is not triggering other molecular outcomes, such as upregulation of p53 or innate immune response.

Reviewer #2 raises an excellent point that is similar to Reviewer #1’s second concern. Please see our response above. We acknowledge that some of the effects of the podxl morpholino may be non-specific. To address this concern in the revised manuscript, we plan to perform additional morpholino studies, including morpholino injections of podxl mutants and assessment of tp53 and other immune response/cellular stress pathway genes in podxl morphants.

(3) Although the authors made a set of controls to demonstrate the specificity of the CRISPant phenotypes, I believe that a rescue experiment could be beneficial to support their conclusions. Injecting an mRNA with podxl ORF (ideally with a tag to follow protein levels up) together with the induction of CRISPants could be a robust manner to demonstrate the specificity of the approach. A rescue experiment with morphants would also be good to have, although these are a bit more complicated, to ultimately demonstrate the specificity of the approach.

(4) In lines 314-316, the authors speculate on a correlation between decreased HSC and Podxl levels. It would be interesting to actually test this hypothesis and perform RT-qPCR upon CRISPant induction or, even better and if antibodies are available, western blot analysis.

We appreciate the reviewer’s acknowledgement of the controls we performed to demonstrate the specificity of the CRISPant phenotypes. The proposed experiments (rescue, assessment of Podxl levels) would help bolster our conclusions but are technically difficult due to the relatively large standard deviation for the HSC number phenotype even in wildtype larvae and the lack of well-characterized zebrafish antibodies against Podxl.

(5) Similarly, in lines 337-338 and 342-344, the authors discuss that it could be possible that genes near to podxl locus could be upregulated in the mutants. Since they already have a transcriptomic done, this seems an easy analysis to do that can address their own hypothesis.

Thank you for this suggestion. We were referring in these sections to genes that are near the podxl locus with respect to three-dimensional chromatin structure; such genes would not necessarily be near the podxl locus on chromosome 4. We will clarify the text in this paragraph for the revised manuscript. At the same time, we will examine our transcriptomic data to check expression of mkln1, cyb5r3, and other nearby genes on chromosome 4 as suggested and include this analysis in the revised manuscript.

(6) Figures 4 and 5 would be easier to follow if panels B-F included what mutants are (beyond having them in the figure legend). Moreover, would it be more accurate and appropriate if the authors group all three WT and mutant data per panel instead of showing individual fish? Representing technical replicates does not demonstrate in vivo variability, which is actually meaningful in this context. Then, statistical analysis can be done between WT and mutant per panel and per set of primers using these three independent 3-month-old zebrafish.

Thank you for this suggestion. We will modify these figures to clarify our results.

Reviewer #3 (Public review):

Summary:

Ross et al. show that knockdown of zebrafish podocalyxin-like (podxl) by CRISPR/Cas or morpholino injection decreased the number of hepatic stellate cells (HSC). The authors then generated 5 different mutant alleles representing a range of lesions, including premature stop codons, in-frame deletion of the transmembrane domain, and deletions of the promoter region encompassing the transcription start site. However, unlike their knockdown experiment, HSC numbers did not decrease in podxl mutants; in fact, for two of the mutant alleles, the number of HSCs increased compared to the control. Injection of podxl CRISPR/Cas constructs into these mutants had no effect on HSC number, suggesting that the knockdown phenotype is not due to off-target effects but instead that the mutants are somehow compensating for the loss of podxl. The authors then present multiple lines of evidence suggesting that compensation is not exclusively due to transcriptional adaptation - evidence of mRNA instability and nonsense-mediated decay was observed in some but all mutants; expression of the related gene endoglycan (endo) was unchanged in the mutants and endo knockdown had no effect on HSC numbers; and, expression profiling by RNA sequencing did not reveal changes in other genes that share sequence similarity with podxl. Instead, their RNA-seq data showed hundreds of differentially expressed genes, especially ECM-related genes, suggesting that compensation in podxl mutants is complex and multi-genic.

Strengths:

The data presented is impressively thorough, especially in its characterization of the 5 different podxl alleles and exploration of whether these mutants exhibit transcriptional adaptation.

Thank you very much for appreciating the hard work that went into this manuscript.

Weaknesses:

RNA sequencing expression profiling was done on adult livers. However, compensation of HSC numbers is apparent by 6 dpf, suggesting compensatory mechanisms would be active at larval or even embryonic stages. Although possible, it's not clear that any compensatory changes in gene expression would persist to adulthood.

This reviewer makes an excellent point. Our finding that the largest changes in gene expression were in extracellular matrix (ECM) genes and ECM modulation is a major function of HSCs supports the hypothesis that genetic compensation is occurring in adults. Nonetheless, we agree that compensatory changes in adults may not fully reflect the compensatory changes during development, so it would bolster the conclusions of the paper to perform the RNA sequencing and qPCR experiments on zebrafish larval livers.

We tried very hard to do this experiment proposed by Reviewer #3. In our hands, obtaining sufficient high-quality RNA for robust gene expression analysis typically requires pooling of ~10-15 larval livers. These larvae need to be obtained from a heterozygous in-cross in order to have matched wildtype sibling controls. Livers must be dissected from freshly euthanized (not fixed) zebrafish. Thus, this experiment requires genotyping live, individual larvae from a small amount of tissue (without sacrificing the larvae) before dissecting and pooling the livers. Unfortunately we were unable to confidently and reproducibly genotype individual live podxl larvae with these small amounts of tissue despite trying multiple approaches. Therefore we were not able to perform gene expression analysis on podxl mutant larval livers.

Author response:

Reviewer #1 (Public review):

Summary:

The study investigated how individuals living in urban slums in Salvador, Brazil, interact with environmental risk factors, particularly focusing on domestic rubbish piles, open sewers, and a central stream. The study makes use of the step selection functions using telemetry data, which is a method to estimate how likely individuals move towards these environmental features, differentiating among groups by gender, age, and leptospirosis serostatus. The results indicated that women tended to stay closer to the central stream while avoiding open sewers more than men. Furthermore, individuals who tested positive for leptospirosis tended to avoid open sewers, suggesting that behavioral patterns might influence exposure to risk factors for leptospirosis, hence ensuring more targeted interventions.

Strengths:

(1) The use of step selection functions to analyze human movement represents an innovative adaptation of a method typically used in animal ecology. This provides a robust quantitative framework for evaluating how people interact with environmental risk factors linked to infectious diseases (in this case, leptospirosis).

(2) Detailed differentiation by gender and serological status allows for nuanced insights, which can help tailor targeted interventions and potentially improve public health measures in urban slum settings.

(3) The integration of real-world telemetry data with epidemiological risk factors supports the development of predictive models that can be applied in future infectious disease research, helping to bridge the gap between environmental exposure and health outcomes.

Weaknesses:

(1) The sample size for the study was not calculated, although it was a nested cohort study.

We thank Reviewer #1 for highlighting this weakness. We will make sure that this is explained in the next version of the manuscript. At the time of recruiting participants, we found no literature on how to perform a sample size calculation for movement studies involving GPS loggers and associated methods of analysis. Therefore, we aimed to recruit as many individuals as possible within the resource constraints of the study.

(2) The step‐selection functions, though a novel method, may face challenges in fully capturing the complexity of human decision-making influenced by socio-cultural and economic factors that were not captured in the study.

We agree with Reviewer #1 that this model may fail to capture the full breadth of human decision-making when it comes to moving through local environments. We included a section discussing the aspect of violence and how this influences residents’ choices, along with some possibilities on how to record and account for this. Although it is outside of the scope of this study, we believe that coupling these quantitative methods with qualitative studies would provide a comprehensive understanding of movement in these areas.

(3) The study's context is limited to a specific urban slum in Salvador, Brazil, which may reduce the generalizability of its findings to other geographical areas or populations that experience different environmental or socio-economic conditions.

(4) The reliance on self-reported or telemetry-based movement data might include some inaccuracies or biases that could affect the precision of the selection coefficients obtained, potentially limiting the study's predictive power.

We agree that telemetry data has inherent inaccuracies, which we have tried to account for by using only those data points within the study areas. We would like to clarify that there is no self-reported movement data used in this study. All movement data was collected using GPS loggers.

(5) Some participants with less than 50 relocations within the study area were excluded without clear justification, see line 149.

We found that the SSF models would not run properly if there weren’t enough relocations. Therefore, we decided to remove these individuals from the analysis. They are also removed from any descriptive statistics presented.

(6) Some figures are not clear (see Figure 4 A & B).

We will be trying to improve the quality of this image in the next version of the manuscript.

(7) No statement on conflict of interest was included, considering sponsorship of the study.

The conflict-of-interest forms for each author were sent to eLife separately. I believe these should be made available upon publication, but please reach out if these need to be re-sent.

Reviewer #2 (Public review):

Summary:

Pablo Ruiz Cuenca et al. conducted a GPS logger study with 124 adult participants across four different slum areas in Salvador, Brazil, recording GPS locations every 35 seconds for 48 hours. The aim of their study was to investigate step-selection models, a technique widely used in movement ecology to quantify contact with environmental risk factors for exposure to leptospires (open sewers, community streams, and rubbish piles). The authors built two different types of models based on distance and based on buffer areas to model human environmental exposure to risk factors. They show differences in movement/contact with these risk factors based on gender and seropositivity status. This study shows the existence of modest differences in contact with environmental risk factors for leptospirosis at small spatial scales based on socio-demographics and infection status.

Strengths:

The authors assembled a rich dataset by collecting human GPS logger data, combined with field-recorded locations of open sewers, community streams, and rubbish piles, and testing individuals for leptospirosis via serology. This study was able to capture fine-scale exposure dynamics within an urban environment and shows differences by gender and seropositive status, using a method novel to epidemiology (step selection).

Weaknesses:

Due to environmental data being limited to the study area, exposure elsewhere could not be captured, despite previous research by Owers et al. showing that the extent of movement was associated with infection risk. Limitations of step selection for use in studying human participants in an urban environment would need to be explicitly discussed.

The environmental factors used in the study required research teams to visit the sites and map the locations. Given that individuals travelled throughout the city of Salvador, performing this task at a large scale would be unachievable. Therefore, we limited the data to only those points within the study area boundaries to avoid any biases from interactions with unrecorded environmental factors. We will be including a more explicit discussion of the limitations of SSF in urban environmental settings with human participants in the next version of the manuscript.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Diarrheal diseases represent an important public health issue. Among the many pathogens that contribute to this problem, Salmonella enterica serovar Typhimurium is an important one. Due to the rise in antimicrobial resistance and the problems associated with widespread antibiotic use, the discovery and development of new strategies to combat bacterial infections is urgently needed. The microbiome field is constantly providing us with various health-related properties elicited by the commensals that inhabit their mammalian hosts. Harnessing the potential of these commensals for knowledge about host-microbe interactions as well as useful properties with therapeutic implications will likely to remain a fruitful field for decades to come. In this manuscript, Wang et al use various methods, encompassing classic microbiology, genomics, chemical biology, and immunology, to identify a potent probiotic strain that protects nematode and murine hosts from S. enterica infection. Additionally, authors identify gut metabolites that are correlated with protection, and show that a single metabolite can recapitulate the effects of probiotic administration.

We gratefully appreciate your positive and professional comments.

Strengths:

The utilization of varied methods by the authors, together with the impressive amount of data generated, to support the claims and conclusions made in the manuscript is a major strength of the work. Also, the ability the move beyond simple identification of the active probiotic, also identifying compounds that are at least partially responsible for the protective effects, is commendable.

We gratefully appreciate your positive and professional comments.

Weaknesses:

No major weaknesses noted.

We gratefully appreciate your positive comments.

Reviewer #2 (Public review):

Summary:

In this work, the investigators isolated one Lacticaseibacillus rhamnosus strain (P118), and determined this strain worked well against Salmonella Typhimurium infection. Then, further studies were performed to identify the mechanism of bacterial resistance, and a list of confirmatory assays were carried out to test the hypothesis.

We gratefully appreciate your positive and professional comments.

Strengths:

The authors provided details regarding all assays performed in this work, and this reviewer trusted that the conclusion in this manuscript is solid. I appreciate the efforts of the authors to perform different types of in vivo and in vitro studies to confirm the hypothesis.

We gratefully appreciate your positive and professional comments.

Weaknesses:

I have mainly two questions for this work.

Main point-1:

The authors provided the below information about the sources from which Lacticaseibacillus rhamnosus was isolated. More details are needed. What are the criteria to choose these samples? Where were these samples originate from? How many strains of bacteria were obtained from which types of samples?

Lines 486-488: Lactic acid bacteria (LAB) and Enterococcus strains were isolated from the fermented yoghurts collected from families in multiple cities of China and the intestinal contents from healthy piglets without pathogen infection and diarrhoea by our lab.

Sorry for the ambiguous and limited information, previously, more details had been added in Materials and methods section in the revised manuscript (see Line 482-493) (Manuscript with marked changes are related to “Related Manuscript File” in submission system). We gratefully appreciate your professional comments.

Line 482-493: “Lactic acid bacteria (LAB) and Enterococcus strains were isolated from 39 samples: 33 fermented yoghurts samples (collected from families in multiple cities of China, including Lanzhou, Urumqi, Guangzhou, Shenzhen, Shanghai, Hohhot, Nanjing, Yangling, Dali, Zhengzhou, Shangqiu, Harbin, Kunming, Puer), and 6 healthy piglet rectal content samples without pathogen infection and diarrhea in pig farm of Zhejiang province (Table 1). Ten isolates were randomly selected from each sample. De Man-Rogosa-Sharpe (MRS) with 2.0% CaCO₃ (is a selective culture medium to favor the luxuriant cultivation of Lactobacilli) and Brain heart infusion (BHI) broths (Huankai Microbial, Guangzhou, China) were used for bacteria isolation and cultivation. Matrix-Assisted Laser Desorption Ionization-Time of Flight Mass Spectrometry (MALDI-TOF MS, Bruker Daltonik GmbH, Bremen, Germany) method was employed to identify of bacterial species with a confidence level ≥ 90% (He et al., 2022).”

Lines 129-133: A total of 290 bacterial strains were isolated and identified from 32 samples of the fermented yoghurt and piglet rectal contents collected across diverse regions within China using MRS and BHI medium, which consist s of 63 Streptococcus strains, 158 Lactobacillus/ Lacticaseibacillus Limosilactobacillus strains and 69 Enterococcus strains.

Sorry for the ambiguous information, we had carefully revised this section and more details had been added in this section (see Line 129-133). We gratefully appreciate your professional comments.

Line 129-133: “After identified by MALDI-TOF MS, a total of 290 bacterial isolates were isolated and identified from 33 fermented yoghurts samples and 6 healthy piglet rectal content samples. Those isolates consist of 63 Streptococcus isolates, 158 Lactobacillus/Lacticaseibacillus/Limosilactobacillus isolates, and 69 Enterococcus isolates (Figure 1A, Table 1).”

Main-point-2:

As probiotics, Lacticaseibacillus rhamnosus has been widely studied. In fact, there are many commercially available products, and Lacticaseibacillus rhamnosus is the main bacteria in these products. There are also ATCC type strain such as 53103.

I am sure the authors are also interested to know if P118 is better as a probiotics candidate than other commercially available strains. Also, would the mechanism described for P118 apply to other Lacticaseibacillus rhamnosus strains?

It would be ideal if the authors could include one or two Lacticaseibacillus rhamnosus which are currently commercially used, or from the ATCC. Then, the authors can compare the efficacy and antibacterial mechanisms of their P118 with other strains. This would open the windows for future work.

We gratefully appreciate your professional comments and valuable suggestions. We deeply agree that it will be better and make more sense to include well-known/recognized/commercial probiotics as a positive control to comprehensively evaluate the isolated P118 strain as a probiotic candidate, particularly in comparison to other well-established probiotics, and also help assess whether the mechanisms described for P118 are applicable to other L. rhamnosus strains or lactic acid bacteria in general. Those issues will be fully taken into consideration and included in the further works. Nonetheless, the door open for future research had been left in Conclusion section (see Line 477-479) “Further investigations are needed to assess whether the mechanisms observed in P118 are strain-specific or broadly applicable to other L. rhamnosus strains, or LAB species in general.”.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Minor comments:

This reviewer appreciates the efforts from the authors to provide the details related to this work. In the meantime, the manuscript shall be written in a way which is easy for the readers to follow.

We had tried our best to revise and make improve the whole manuscript to make it easy for the readers to follow (e.g., see Line 27-30, Line 115-120, Line 129-133, Line 140-143, Line 325-328, Line 482-493, Line 501-502, Line 663-667, Line 709-710, Line 1003-1143). We gratefully appreciate your valuable suggestions.

For example, under the sections of Materials and Methods, there are 19 sub-titles. The authors could consider combining some sections, and/or cite other references for the standard procedures.

We gratefully appreciate your professional comments and valuable suggestions. Some sections had been combined according to the reviewer’s suggestions (see Line 501-710).

Another example: the figures have great resolution, but they are way too busy. The figures 1 and 2 have 14-18 panels. Figure 5 has 21 panels. Please consider separating into more figures, or condensing some panels.

We deeply agree with you that some submitted figures are way too busy, but it’s not easy for us to move some results into supplementary information sections, because all of them are essential for fully supporting our hypothesis and conclusions. Nonetheless, some panels had been combined or condensed according to the reviewer’s suggestions (see Line 1003-1024, Line 1056-1075). We gratefully appreciate your professional comments and valuable suggestions.

More minor comments:

line 30: spell out "C." please.

Done as requested (see Line 29, Line 31). We gratefully appreciate your valuable suggestions.

Author response:

The following is the authors’ response to the original reviews

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

Walton et al. set out to isolate new phages targeting the opportunistic pathogen Pseudomonas aeruginosa. Using a double ∆fliF ∆pilA mutant strain, they were able to isolate 4 new phages, CLEW-1. -3, -6, and -10, which were unable to infect the parental PAO1F Wt strain. Further experiments showed that the 4 phages were only able to infect a ∆fliF strain, indicating a role of the MS-protein in the flagellum complex. Through further mutational analysis of the flagellum apparatus, the authors were able to identify the involvement of c-di-GMP in phage infection. Depletion of c-di-GMP levels by an inducible phosphodiesterase renders the bacteria resistant to phage infection, while elevation of c-di-GMP through the Wsp system made the cells sensitive to infection by CLEW-1. Using TnSeq, the authors were able to not only reaffirm the involvement of c-di-GMP in phage infection but also able to identify the exopolysaccharide PSL as a downstream target for CLEW-1. C-di-GMP is a known regulator of PSL biosynthesis. The authors show that CLEW-1 binds directly to PSL on the cell surface and that deletion of the pslC gene resulted in complete phage resistance. The authors also provide evidence that the phage-PSL interaction happens during the biofilm mode of growth and that the addition of the CLEW-1 phage specifically resulted in a significant loss of biofilm biomass. Lastly, the authors set out to test if CLEW-1 could be used to resolve a biofilm infection using a mouse keratitis model. Unfortunately, while the authors noted a reduction in bacterial load assessed by GFP fluorescence, the keratitis did not resolve under the tested parameters. 

Strengths: 

The experiments carried out in this manuscript are thoughtful and rational and sufficient explanation is provided for why the authors chose each specific set of experiments. The data presented strongly supports their conclusions and they give present compelling explanations for any deviation. The authors have not only developed a new technique for screening for phages targeting P. aeruginosa, but also highlight the importance of looking for phages during the biofilm mode of growth, as opposed to the more standard techniques involving planktonic cultures. 

Weaknesses: 

While the paper is strong, I do feel that further discussions could have gone into the decision to focus on CLEW-1 for the majority of the paper. The paper also doesn't provide any detailed information on the genetic composition of the phages. It is unclear if the phages isolated are temperate or virulent. Many temperate phages enter the lytic cycle in response to QS signalling, and while the data as it is doesn't suggest that is the case, perhaps the paper would be strengthened by further elimination of this possibility. At the very least it might be worth mentioning in the discussion section. 

Thank you for your review. The genomes of all Clew phages and Ocp-2 have been uploaded [Genbank accession# PQ790658.1, PQ790659.1, PQ790660.1, PQ790661.1, and PQ790662.1]. It turns out that the Clew phage are highly related, which is highlighted by the genomic comparison in the supplementary figure S1. It therefore made sense to focus our in-depth analysis on one of the phage. We have included a supplementary figure (S1A), demonstrating that the other Clew phage also require an intact psl locus for infection, to make that logic clearer. The phage are virulent (there is apparently a bit of a debate about this with regard to Bruynogheviruses, but we have not been able to isolate lysogens). This is now mentioned in the discussion.  

Reviewer #2 (Public review): 

This manuscript by Walton et al. suggests that they have identified a new bacteriophage that uses the exopolysaccharide Psl from Pseudomonas aeruginosa (PA) as a receptor. As Psl is an important component in biofilms, the authors suggest that this phage (and others similarly isolated) may be able to specifically target biofilm-growing bacteria. While an interesting suggestion, the manner in which this paper is written makes it difficult to draw this conclusion. Also, some of the results do not directly follow from the data as presented and some relevant controls seem to be missing. 

Thank you for your review. We would argue that the combination of demonstrating Psl-dependent binding of Clew-1 to P. aeruginosa, as well as demonstration of direct binding of Clew-1 to affinity-purified Psl, indicates that the phage binds directly to Psl and uses it as a receptor. In looking at the recommendations, it appears that the remark about controls refers to not using the ∆pslC mutant alone (as opposed to the ∆fliF2 ∆pslC double mutant) as a control for some of the binding experiments. However, since the ∆fliF2 mutant is more permissive for phage infection, analyzing the effect of deleting pslC in the context of the ∆fliF2 mutant background is the more stringent test. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

First off, I would like to congratulate the authors on this study and manuscript. It is very well executed and the writing and flow of the paper are excellent. The findings are intriguing and I believe the paper will be very well received by both the phage, Pseudomonas, and biofilm communities. 

Thank you for your kind review of our work!

I have very little to critique about the paper but I have listed a few suggestions that I believe could strengthen the paper if corrected: 

Comments and suggestions: 

(1) The paper initially describes 4 isolated phages but no rationale is given for why they chose to continue with CLEW-1, as opposed to CLEW-3, -6, and -10. The paper would benefit from going into more detail with phage genomics and perhaps characterize the phage receptor binding to PSL. 

Clew-1, -3, -6, and -10 are actually quite similar to one another. The genomes are now uploaded to Genbank [accession# PQ790658.1, PQ790659.1, PQ790660.1, and PQ790661.1]. They all require an intact Psl locus for infection, we have updated Fig. S1 to show this for the remaining Clew phage. In the end, it made sense to focus on one of these related phage and characterize it in depth.

(2) PA14 was used in some experiments but not listed in the strain table. 

Thank you, this has been added in the resubmission.

(3) Would have been good to see more strains/isolates used.

We are currently characterizing the host range of Clew-1. It appears to be pretty limited, but this will likely be included in another paper that will focus on host range, not only of Clew-1, but other biofilm-tropic phage that we have isolated since then.

(4) Could purified PSL be added to make non-PSL strain (like PA14) susceptible? 

We have tried adding purified Psl to a psl mutant strain, but this does not result phage sensitivity. Further characterization of the Psl receptor, is something we are currently working on, but will likely be a much bigger story than can be easily accommodated in a revised manuscript.

(5) No data on resistance development. 

We have not done this as yet.

(6) Alternative biofilm models. Both in vitro and in vivo. 

We agree that exploring the interaction of Clew-1 with biofilms in greater detail is a logical next step. The revised manuscript does have data on the viability of P. aeruginosa biofilm bacteria after Clew-1 infection using either a bead biofilm model or LIVE/DEAD staining of static biofilms. However, expanding on this further (setting up flow-cell biofilms, developing reporters to monitor phage infection, etc.) is beyond the scope of this initial report and characterization of Clew-1.

(7) There is a mistake in at least one reference. An unknown author is listed in reference 48. DA Garsin is not part of the paper. Might be worth looking into further mistakes in the reference list as I suspect this might be an issue related to the citation software.

Thank you. Yes, odd how that extra author got snuck in. This has been corrected.

(8) I don't seem to be able to locate a Genbank file or accession number. If it wasn't performed how was evolutionary relatedness data generated?

The genomes of all Clew phages and Ocp-2 have been uploaded [Genbank accession# PQ790658.1, PQ790659.1, PQ790660.1, PQ790661.1, and PQ790662.1]

(9) No genomic information about the isolated phages. Are they temperate or virulent? This would be important information as only strictly lytic phages are currently deemed appropriate for phage therapy. 

These phage are virulent. We have only been able to isolate resistant bacteria from plaques, but they do not harbor the phage (as detected by PCR). This matches what other researchers have found for Bruynogheviruses.

Reviewer #2 (Recommendations for the authors): 

Others have used different PA mutants lacking known phage receptors to pan for new phages. However, it is not totally clear how the screen here was selected for the Psl-specific phage. The authors used flagella and pili mutants and found Clew-1, -3, -6, and -10. These were all Bruynogheviruses. They also isolated a phage that uses the O antigen as a receptor. The family of this latter phage and how it is known to use this as a receptor is not described. 

Phage Ocp-2 is a Pbunavirus. We added new supplementary figure S3, addressing the O-antigen receptor.

The authors focused on Clew-1, but the receptor for these other Clew phages is not presented. For Clew-1 the phage could plaque on the fliF deletion mutant but not the wild-type strain. The reason for this never appears to be addressed. The authors leap to consider the involvement of c-di-GMP, but how this relates to fliF appears to be lacking. 

We have included a supplementary figure demonstrating that all the Clew phage require Psl for infection (Fig. S1A). As noted above, we have uploaded the genomic data that underpins the comparison in our supplementary figure. The phage are all closely related. It therefore made sense to focus on one of the phage for the analysis.  

It is particularly unclear why this phage doesn't plaque on PAO1 as this strain does make Psl. Related to this, it actually looks like something is happening to PAO1 in Figure S4 (although what units are on the x-axis is not entirely clear).

We hypothesize that the fraction of susceptible cells in the population dictates whether the phage can make overt plaques. The supplementary figure S4 indicates that a subpopulation of the wild-type culture is susceptible and this is borne out by the fraction of wild type cells that the phage can bind to (~50%). The fliF mutation increases this frequency of susceptible cells to 80-90% (Fig. 3).

The Tnseq screen to identify receptors is clever and identifies additional phosphodiesterase genes, the deletion of which makes PAO1 susceptible. And the screen to find resistant fliF mutants identified genes involved in Psl. However, the link between the phosphodiesterase mutants and the amount of Psl produced never appears to be established. And the statement that Psl is required for infection (line 130) is never actually tested.

The link between c-di-GMP and Psl production is well-established in the literature. I think the requirement for Psl in infection is demonstrated multiple ways, including lack of plaque formation on psl mutant strains and lack of phage binding to strains that do not produce Psl, direct binding of the phage to affinity purified Psl.

Figure 2C describes using a ∆fliF2 strain but how this is different (or if it is different) from ∆fliF described in the text is never explained.

The difference in the deletions is explained in table S1, in the description for the deletion constructs used in their construction, pEXG2-∆fliF and pEXG2-∆fliF2 (∆fliF2 is smaller than ∆fliF and can be complemented completely with our complementing plasmid, pP37-fliF, which is the reason why we used the ∆fliF2 mutation going forward, rather than the ∆fliF mutation on which the phage was originally isolated).

Similarly, there is a sentence (line 138) that "Attachment of Clew-1 is Psl-dependent" but this would appear to have no context.

The relevant figure, Fig. 3, is cited in the next sentence and is the subject of the remaining paragraphs in this section of the manuscript.

For Figure 3B, why wasn't the single ∆pslC mutant visualized in this analysis? Similar questions relate to the data in Figure 4.

Analyzing the effect of the pslC deletion in the context of the ∆fliF2 mutant background, which is more permissive for phage infection, is the more stringent test.  

The efficacy of Clew-1 in the mouse keratitis model is intriguing but it is unclear why the CFU/eye are so variable. The description of how the experiment was actually carried out is not clear. Was only one eye scratched or both? Were controls included with a scratch and no bacteria ({plus minus} phage)?

One eye was infected. We did not conduct a no-bacteria control (just scratching the cornea is not sufficient to cause disease). The revised manuscript has an updated animal experiment in which we carried the infection forward to 72h with two phage treatments. Following this regiment, there is a significant decrease in CFU, as well as corneal opacity (disease). Variability of the data is a fairly common feature in animal experiments. There are a number of factors, such as does the mouse blink and remove some of the inoculum shortly after deposition of the bacteria or the phage after each treatment that could explain this variability.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

The revised manuscript has gained much clarity and consistency. One previous criticism, however, has in my opinion not been properly addressed. I think the problem boils down to not clearly distinguishing between orthologs and paralogs/homologs. As this problem affects a main conclusion - the prevalence of deletions over insertions in the MTBC - it should be addressed, if not through additional analyses, then at least in the discussion.

Insertions and deletions are now distinguished in the following way: "Accessory regions were further classified as a deletion if present in over 50% of the 192 sub-lineages or an insertion/duplication if present in less than 50% of sub-lineages." The outcome of this classification is suspicious: not a single accessory region was classified as an insertion/duplication. As a check of sanity, I'd expect at least some insertions of IS6110 to show up, which has produced lineage- or sublineage-specific insertions (Roychowdhury et al. 2015, Shitikov et al. 2019). Why, for example, wouldn't IS6110 insertions in the single L8 strain show up here?

In a fully clonal organism, any insertion/duplication will be an insertion/duplication of an existing sequence, and thus produce a paralog. If I'm correctly understanding your methods section, paralogs are systematically excluded in the pangraph analysis. Genomic blocks are summarized at the sublineage levels as follows (l.184 ): "The DNA sequences from genomic blocks present in at least one sub-lineage but completely absent in others were extracted to look for long-term evolution patterns in the pangenome." I presume this is done using blastn, as in other steps of the analysis.

So a sublineage-specific copy of IS6110 would be excluded here, because IS6110 is present somewhere in the genome in all sublineages. However, the appropriate category of comparison, at least for the discussion of genome reduction, is orthology rather than homology: is the same, orthologous copy of IS6110, at the same position in the genome, present or absent in other sublineages? The same considerations apply to potential sublineage-specific duplicates of PE, PPE, and Esx genes. These gene families play important roles in host-pathogen interactions, so I'd argue that the neglect of paralogs is not a finicky detail, but could be of broader biological relevance.

Within the analysis we undertook we did look at paralogous blocks in pangraph, based on copy number per genome. However, this could have been clearer in the text and we will rectify this. We also focussed on duplicated/deleted blocks that were present in two of more sub-lineages. This is noted in figure 4 legend but we will make this clearer in other sections of the manuscript.

We agree that indeed the way paralogs are handled could still be optimised, and that gene duplicates of some genes could have biological importance. The reviewer is suggesting that a synteny analysis between genomes would be best for finding specific regions that are duplicated/deleted within a genome, and if those sections are duplicated/deleted in the same regions of the genome. Since Pangraph does not give such information readily, a larger amount of analysis would be required to confirm such genome position-specific duplications. While this is indeed important, we deem this to be out of scope for the current publication, but will note this as a limitation in the discussion. However, this does not fundamentally change the main conclusions of our analysis.

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this paper, Behruznia and colleagues use long-read sequencing data for 335 strains of the Mycobacterium tuberculosis complex to study genome evolution in this clonal bacterial pathogen. They use both a "classical" pangenome approach that looks at the presence and absence of genes, and a more general pangenome graph approach to investigate structural variants also in non-coding regions. The two main results of the study are that (1) the MTBC has a small pangenome with few accessory genes, and that (2) pangenome evolution is driven by deletions in sublineage-specific regions of difference. Combining the gene-based approach with a pangenome graph is innovative, and the former analysis is largely sound apart from a lack of information about the data set used. The graph part, however, requires more work and currently fails to support the second main result. Problems include the omission of important information and the confusing analysis of structural variants in terms of "regions of difference", which unnecessarily introduces reference bias. Overall, I very much like the direction taken in this article, but think that it needs more work: on the one hand by simply telling the reader what exactly was done, on the other by taking advantage of the information contained in the pangenome graph.

Strengths:

The authors put together a large data set of long-read assemblies representing most lineages of the Mycobacterium tuberculosis context, covering a large geographic area. State-of-the-art methods are used to analyze gene presence-absence polymorphisms (Panaroo) and to construct a pangenome graph (PanGraph). Additional analysis steps are performed to address known problems with misannotated or misassembled genes in pangenome analysis.

Weaknesses:

The study does not quite live up to the expectations raised in the introduction. Firstly, while the importance of using a curated data set is emphasized, little information is given about the data set apart from the geographic origin of the samples (Figure 1). A BUSCO analysis is conducted to filter for assembly quality, but no results are reported. It is also not clear whether the authors assembled genomes themselves in the cases where, according to Supplementary Table 1, only the reads were published but not the assemblies. In the end, we simply have to trust that single-contig assemblies based on long-reads are reliable.

We have now added a robust overview of the dataset to supplementary file 1. This is split into 3 sections: public genomes, which were assembled by others; sequenced genomes, which were created and assembled by us; the BUSCO information for all the genomes together. We did not assemble any public data ourselves but retrieved these from elsewhere. We have modified the text to be more specific on this (Line 114 onwards) and the supplementary file is updated to better outline the data.

One issue with long read assemblies could be that high rates of sequencing errors result in artificial indels when coverage is low, which in turn could affect gene annotation and pangenome inference (e.g. Watson & Warr 2019, https://doi.org/10.1038/s41587-018-0004-z). Some of the older long-read data used by the authors could well be problematic (PacBio RSII), but also their own Nanopore assemblies, six of which have a mean coverage below 50 (Wick et al. 2023 recommend 200x for ONT, https://doi.org/ 10.1371/journal.pcbi.1010905). Could the results be affected by such assembly errors? Are there lineages, for example, for which there is an increased proportion of RSII data? Given the large heterogeneity in data quality on the NCBI, I think more information about the reads and the assemblies should be provided.

We have now included an analysis where we looked to see if the sequencing platform influenced the resulting accessory genome size and the pseudogene count. The details of this are included in lines 207-219, and the results are outlined in lines 251-258. Essentially, we found no correlation between sequencing platform and genome characteristics, although less stringent cut-offs did suggest that PacBio SMRT-only assembled genomes may have larger accessory genomes. We do not believe this is enough to influence our larger inferences from this data. It should be noted that complete genomes, in general, give a better indication of pangenome size compared to draft genomes, as has been shown previously (e.g. Marin et al., 2024). Even with some small potential bias, this makes our analysis more robust than any previously published.

In relation to the sequencing depth of our own data, all genomes had coverage above 30x, which Sanderson et al. (2024) has shown to be sufficient for highly accurate sequence recovery. We fixed an issue with the L9 isolate from the previous submission, which resulted in a better BUSCO score and overall quality of that isolate and the overall dataset.

The part of the paper I struggled most with is the pangenome graph analysis and the interpretation of structural variants in terms of "regions of difference". To start with, the method section states that "multiple whole genomes were aligned into a graph using PanGraph" (l.159/160), without stating which genomes were for what reason. From Figure 5 I understand that you included all genomes, and that Figure 6 summarizes the information at the sublineage level. This should be stated clearly, at present the reader has to figure out what was done. It was also not clear to me why the authors focus on the sublineage level: a minority of accessory genes (107 of 506) are "specific to certain lineages or sublineages" (l. 240), so why conclude that the pangenome is "driven by sublineage-specific regions of difference", as the title states? What does "driven by" mean? Instead of cutting the phylogeny arbitrarily at the sublineage level, polymorphisms could be described more generally by their frequencies.

We apologise for the ambiguity in the methodology. All the isolates were inputted to Pangraph to create the pangenome using this method. This is now made clearer in lines 175-177. Standard pangenome statistics (size, genome fluidity, etc.) derived from this Pangraph output are now present in the results section as well (lines 301-320).

We then only looked at regions of difference at the sub-lineage level, meaning we grouped genomes by sub-lineage within the resulting graph and looked for blocks common between isolates of the same sub-lineage but absent from one or more other sub-lineages. We did this from both the Panaroo output and the Pangraph output and then retained only blocks found by both. The results of this are now outlined in lines 351-383.

We focussed on these sub-lineage-specific regions to focus on long-term evolution patterns and not be influenced by single-genome short-term changes. We do not have enough genomes of closely related isolates to truly look at very recent evolution, although the small accessory genome indicates this is not substantial in terms of gene presence/absence. We also did not want potential mis-annotations in a single genome to heavily influence our findings due to the potential issues pointed out by the reviewer above. We state this more clearly in the introduction (lines 106-108), methods (lines 184-186) and results (345-347), and we indicate the limitations in the Discussion, lines 452-457 and 471-473. We also changed the title to ‘shaped’ instead of ‘driven by’.

I fully agree that pangenome graphs are the way to go and that the non-coding part of the genome deserves as much attention as the coding part, as stated in the introduction. Here, however, the analysis of the pangenome graph consists of extracting variants from the graph and blasting them against the reference genome H37Rv in order to identify genes and "regions of difference" (RDs) that are variable. It is not clear what the authors do with structural variants that yield no blast hit against H37Rv. Are they ignored? Are they included as new "regions of difference"? How many of them are there? etc. The key advantage of pangenome graphs is that they allow a reference-free, full representation of genetic variation in a sample. Here reference bias is reintroduced in the first analysis step.

We apologise for the confusion here as indeed the RDs terminology is very MTBC-specific. Current RDs are always relevant to H37Rv, as that is how original discovery of these regions was done and that is how RDScan works. We clarify this in the introduction (lines 67-68). If we found a large sequence polymorphism (e.g. by Pangraph) and searched for known RDs using RDScan, we then assigned a current RD name to this LSP. This uses H37Rv as a reference. If we did not find a known RD, we then classified the LSP as a new RD if it is present in H37Rv, or left the designation as an LSP if not in H37Rv, thus expanding the analysis beyond the H37Rv-centric approaches used by others previously. This is hopefully now made clearer in the methods, lines 187-194.

Along similar lines, I find the interpretation of structural variants in terms of "regions of difference" confusing, and probably many people outside the TB field will do so. For one thing, it is not clear where these RDs and their names come from. Did the authors use an annotation of RDs in the reference genome H37Rv from previously published work (e.g. Bespiatykh et al. 2021)? This is important basic information, its lack makes it difficult to judge the validity of the results. The Bespiatykh et al. study uses a large short-read data (721 strains) set to characterize diversity in RDs and specifically focuses on the sublineage-specific variants. While the authors cite the paper, it would be relevant to compare the results of the two studies in more detail.

We have amended the introduction to explain this terminology better (lines 67-68). Naming of the RDs here came from using RDScan to assign current names to any accessory regions we found and if such a region was not a known RD, we gave it a lineage-related name, allowing for proper RD naming later (lines 187-194). Because the Bespiatyk paper is the basis for RDScan, our work implicitly compares to this throughout, as any RDs we find which were not picked up by RDScan are thus novel compared to that paper.

As far as I understand, "regions of difference" have been used in the tuberculosis field to describe structural variants relative to the reference genome H37Rv. Colloquially, regions present in H37Rv but absent in another strain have been called "deletions". Whether these polymorphisms have indeed originated through deletion or through insertion in H37Rv or its ancestors requires a comparison with additional strains. While the pangenome graph does contain this information, the authors do not attempt to categorize structural variants into insertions and deletions but simply seem to assume that "regions of difference" are deletions. This, as well as the neglect of paralogs in the "classical" pangenome analysis, puts a question mark behind their conclusion that deletion drives pangenome evolution in the MTBC.

We have now amended the analysis to specifically designate a structural variant as a deletion if present in the majority of strains and absent in a minority, or an insertion/duplication if present in a minority and absent in a majority (lines 191-192). We also ran Panaroo without merging paralogs to examine duplication in this output; Pangraph implicitly includes paralogs already.

From all these analyses we did not find any structural variants classed as insertions/duplications and did not find paralogs to be a major feature at the sub-lineage level (lines 377-383). While these features could be important on shorter timescales, we do not have enough closed genomes to confidently state this (limitation outlined in lines 452-457). Therefore, our assertion that deletions are a primary force shaping the long-term evolution in this group still holds.

Reviewer #2 (Public Review):

Summary:

The authors attempted to investigate the pangenome of MTBC by using a selection of state-of-the-art bioinformatic tools to analyse 324 complete and 11 new genomes representing all known lineages and sublineages. The aim of their work was to describe the total diversity of the MTBC and to investigate the driving evolutionary force. By using long read and hybrid approaches for genome assembly, an important attempt was made to understand why the MTBC pangenome size was reported to vary in size by previous reports.

Strengths:

A stand-out feature of this work is the inclusion of non-coding regions as opposed to only coding regions which was a focus of previous papers and analyses which investigated the MTBC pangenome. A unique feature of this work is that it highlights sublineage-specific regions of difference (RDs) that were previously unknown. Another major strength is the utilisation of long-read whole genomes sequences, in combination with short-read sequences when available. It is known that using only short reads for genome assembly has several pitfalls. The parallel approach of utilizing both Panaroo and Pangraph for pangenomic reconstruction illuminated the limitations of both tools while highlighting genomic features identified by both. This is important for any future work and perhaps alludes to the need for more MTBC-specific tools to be developed.

Weaknesses:

The only major weakness was the limited number of isolates from certain lineages and the over-representation others, which was also acknowledged by the authors. However, since the case is made that the MTBC has a closed pangenome, the inclusion of additional genomes would not result in the identification of any new genes. This is a strong statement without an illustration/statistical analysis to support this.

We have included a Heaps law and genome fluidity calculation for each pangenome estimation to demonstrate that the pangenome is closed. This is detailed in lines 225-228 with results shown in lines 274-278 and 316- 320 and Supplementary Figure 2. We agree that more closely related genomes would benefit a future version of this analysis and indicate we indicate the limitations in the Discussion, lines 452-457 and 471-473.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Abstract

l. 24, "with distinct genomic features". I'm not sure what you are referring to here.

We refer to the differences in accessory genome and related functional profiles but did not want to bloat the abstract with such additional details

Introduction

l. 40, "L1 to L9". A lineage 10 has been described recently: https://doi.org/10.3201/eid3003.231466.

We have updated the text and the reference. Unfortunately, no closed genome for this lineage exists so we have not included it in the analyses. We note this in the results, like 232

l.62/3, "caused by the absence of horizontal gene transfer, plasmids, and recombination". Recombination is not absent in the MTBC, only horizontal gene transfer seems to be, which is what the cited studies show. Indeed a few sentences later homologous recombination is mentioned as a cause of deletions.

This has now been removed from the introduction

l. 67, "within lineage diversity is thought to be mostly driven by SNPs". Again I'm not sure what is meant here with "driven by". Point mutations are probably the most common mutational events, but duplications, insertions, deletions, and gene conversion also occur and can affect large regions and possibly important genes, as shown in a recent preprint (https://doi.org/10.1101/2024.03.08.584093).

We have changed the text to say ‘mostly composed of’. While indeed other SNVs may be contributing, the prevailing thought at lineage level is that SNPs are the primary source of diversity. The linked pre-print is looking at within transmission clusters and this has not been described at the lineage level, which could be done in a future work.

l. 100/1. "that can account for variations in virulence, metabolism, and antibiotic resistance". I would phrase this conservatively since the functional inferences in this study are speculative.

This has now been tempered to be less specific.

Methods

l. 108. That an assembly has a single contig does not mean that it is "closed". Many single contig assemblies on NCBI are reference-guided short-read assemblies, that is, fragments patched together rather than closed assemblies. The same could be true for long-read assemblies.

We specifically chose those listed as closed on NCBI so rely on their checks to ensure this is true. We have stated this better in the paper, line 117.

l. 111. From Supplementary Table 1 understand that for many genomes only the reads were available (no ASM number). Did you assemble these genomes? If yes, how? The assembly method is not indicated in the supplement, contrary to what is written here.

All public genomes were downloaded in their assembled forms from the various sources. This is specified better in the text (line 118) and the supplementary table 1 now lists the accessions for all the assemblies.

l. 113. How many assemblies passed this threshold? And is BUSCO actually useful to assess assembly quality in the MTBC? I assume the dynamic, repetitive gene families that cause problems for assembly and mapping in TB (PE, PPE, ESX) do not figure in the BUSCO list of single-copy orthologs.

All assemblies passed the BUSCO thresholds for high-quality genomes as laid out in Supplementary Table 1. While indeed this does not include multi-copy genes such as PE/PPE we focussed on regions of difference at the sub-lineage level where two or more genomes represent that sub-lineage. This means any assembly issues in a single genome would need to be exactly the same in another of the same sub-lineage to be included in our results. Through this, we aimed to buffer out issues in individual assemblies.

l. 147: Why is Panaroo used with -merge-paralogs? I understand that near-identical genes may not be too interesting from a functional perspective, but if the aim of the analysis is to make broad claims about processes driving genome evolution, paralogs should be considered.

We chose to do so with merged paralogs to look for larger patterns of diversity beyond within-genome paralogs. Additionally, this was required to build the core phylogenetic tree. However, as the reviewer points out, this may bias our findings towards deletions and away from duplications as a primary evolutionary force.

We repeated this without the merged paralogs option and indeed found a larger pangenome, as outlined in Table 1. However, at the sub-lineage level, this did not result in any new presence/absence patterns (lines 381-383). This means the paralogs tended to be in single genomes only. This still indicates that deletions are the primary force in the longer-term evolution of the complex but indeed on shorter spans this may be different.

l. 153: remove the comment in brackets.

This has been fixed and the proper URL placed in instead.

l. 159: which genomes, and why those?

This is now clarified to state all genomes were used for this analysis.

l. 161, "gene blocks": since this analysis is introduced as capturing the non-coding part of the genome, maybe just call them "blocks"?

All references to gene blocks are now changed to genomic blocks to be more specific.

l. 162: what happens with blocks that yield no hits against RvD1, TbD1, and H37Rv?

We named these with lineage-specific names (supplementary table 4) but did not assign RD names specifically.

l. 164: where does the information about the regions of difference come from? How exactly were these regions determined?

Awe have expanded this section to be more specific on the use of RDScan and new naming, along with how we determine if something is an RD/LSP.

Results

l. 185ff: This paragraph gives many details about the geographic origin of the samples, but what I'd expect here is a short description of assembly qualities, for example, the results of the BUSCO analysis, a description of your own Nanopore assemblies, or a small analysis of the number of indels/pseudogenes relative to sequencing technology or coverage (see comment in the public review).

This section (lines 231-258) has been expanded considerably to give a better overview of the dataset and any potential biases. Supplementary table 1 has also been expanded to include more information on each strain.

l. 187, "324 genomes published previously": 322 according to the methods section.

The number has been fixed throughout to the proper total of public genomes (329).

l. 201: define the soft core, shell, and cloud genes.

This is now defined on line 262

l. 228, "defined primarily by RD105 and RD207 deletions": this claim seems to come from the analysis of variable importance (Factoextra), which should be made clear here.

This has been clarified on line 333.

l. 237, "L8, serving as the ancestor of the MTBC": this is incorrect, equivalent to saying that the Chimpanzee is the ancestor of Homo sapiens.

We have changed this to basal to align with how it is described in the original paper.

l. 239, "The accessory genome of the MTBC". It is a bit confusing that the same term, 'accessory genome', is used here for the graph-based analysis, which is presented as a way to look at the non-coding part of the genome.

We have clarified the terminology on line 347 and improved consistency throughout.

l. 240/1, "specific to certain lineages and sublineages". What exactly do you mean by "specific" to? Present only in members of a certain lineage/sublineage? In all members of a certain lineage/sublineage? Maybe an additional panel in Figure 5, showing examples of lineage- and sublineage-specific variants, would help the reader grasp this key concept.

We have clarified this on line 349 and the legend of what is now figure 4.

l. 241/2, "82 lineage and sublineage-specific genomic regions ranging from 270 bp to 9.8 kb". Were "gene blocks" filtered for a minimum size, or why are there no variants smaller than 270 bp? A short description of all the blocks identified in the graph could be informative (their sizes, frequencies ...).

Yes, a minimum of 250bp was set for the blocks to only look at larger polymorphisms. This is clarified on line 177 and 304.

A second point: It is not entirely clear to me what Figure 6 is showing. Are you showing here a single representative strain per sublineage? Or have you somehow summarized the regions of difference shown in Figure 5 at the sublineage level? What is the tree on the left? This should be made clear in the legend and maybe also in the methods/results.

In figure 4 (which was figure 6), because each RD is common to all members of the same sub-lineage, we have placed a single branch for each sub-lineage. This is has been clarified in the legend.

l. 254, "this gene was classified as being in the core genome": why should a partially deleted gene not be in the core genome?

You are correct, we have removed that statement.

l. 258/259, "The Pangraph alignment approach identified partial gene deletion and non-coding regions of the DNA that were impacted by genomic deletion". I do not understand how you classify a structural variant identified in the pangenome graph as a deletion or an insertion.

This has been clarified as relative to H37Rv, as this is standard practice for RDs and general evolutionary analyses in MTBC, as outlined above.

l. 262/263 , "the accessory genome of the MTBC is small and is acquired vertically from a common ancestor within the lineage". If deletion is the main process involved here, "acquired" seems a bit strange.

We agree and changed the header to better reflect the discussion on mis-annotation issues

Figure 1: Good to know, but not directly relevant for the rest of the paper. Maybe move it to the supplement?

This has been moved to Supplementary figure 1

Figure 2: the y-axis is labeled 'Variable genome size', but from the text and the legend I figure it should be 'Number of accessory genes'?

This has been changed to ‘accessory genes’ in Figure 1 (which was figure 2 in previous version).

Figure 4: too small.

We will endeavour to ensure this is as large as possible in the final version.

Discussion

l. 271, "MTBC accessory genome is ... acquired vertically". See above.

Changed, as outlined above.

l. 292, "appeared to be fragmented genes caused by misassemblies". Is there a way to distinguish "true" pseudogenes from misassemblies? This could be a relevant issue for low-coverage long-read assemblies (see public review).

Not that we are currently aware of, but we do know other groups which are working on this issue.

l. 300/1, "the whole-genome approach could capture higher genetic variations". Do you mean the graph approach? I'm not sure that comparing the two approaches here makes sense, as they serve different purposes. A pangenome graph is a summary of all genetic variation, while the purpose of Panaroo is to study gene absence/presence. So by definition, the graph should capture more genetic variation.

This statement was specifically to state that much genetic variation in MTBC is outside the coding genes and so traditional “pangenome’ analyses are actually not looking at the full genomic variation.

l. 302/3, "this method identified non-coding regions of the genome that were affected by genomic deletions". See the comments above regarding deletions versus insertions. I'd say this method identifies coding and non-coding regions that were affected by genomic deletions and insertions.

We have undertaken additional analyses to be sure these are likely deletions, as outlined above.

l. 305: what are "lineage-independent deletions"?

We labelled these as convergent evolution, now clarified on line 443.

l. 329: How is RD105 "caused" by the insertion of IS6110? I did not find RD105 mentioned in the Alonso et al. paper. Similarly below, l. 331, how is RD207 "linked" to IS6110?

The RD105 connection was misattributed as IS6110 insertion is related to RD152, not RD105. This has now been removed.

RD207 is linked to IS6110 as its deletion is due to recombination between two such elements. This is now clarified on line 486.

l. 345, "the growth advantage gene group": not quite sure what this is.

We have fixed this on line 499 to state they are genes which confer growth advantages.

l. 373ff: The role of genetic drift in the evolution of the MTBC is an open question, other studies have come to different conclusions than Hershberg et al. (this has been recently reviewed: https://doi.org/10.24072/pcjournal.322).

We have outlined this debate better in lines 527-531

l. 375/6, "Gene loss, driven by genetic drift, is likely to be a key contributor to the observed genetic diversity within the MTBC." This sentence would need some elaboration to be intelligible. How does genetic drift drive gene loss?

We have removed this.

l. 395/6, "... predominantly driven by genome reduction. This observation underlines the importance of genomic deletions in the evolution of the MTBC." See comments above regarding deletions. I'm not convinced that your study really shows this, as it completely ignores paralogs and the processes counteracting reductive genome evolution: duplication and gene amplification.

As outlined above, we have undertaken additional analyses to more strongly support this statement.

l. 399, "the accessory genome of MTBC is a product of gene deletions, which can be classified into lineage-specific and independent deletions". Again, I'm not sure what is meant by lineage-independent deletions.

We have better defined this in the text, line 443, to be related to convergent evolution.

Reviewer #2 (Recommendations For The Authors):

Suggestions for improved or additional experiments, data, or analyses.

In lines 120-121, it is mentioned that TB-profiler v4.4.2 was used for lineage classification, but this version was released in February 2023. As I understand there have been some changes (inclusion/exclusion) of certain lineage markers. Would it not be appropriate to repeat lineage classification with a more recent version? This would of course require extensive re-analysis, so could the lineage marker database perhaps also be cited.

We have rerun all the genomes through TB-Profiler v6.5 and updated the text to state this; the exact database used is also now stated.

Could the authors perhaps include the sequencing summary or quality of the nanopore sequences? The L9 (Mtb8) sample had a relatively lower depth and resulted in two contigs. Yet one contig was the initial inclusion criteria. It is unclear whether these samples were excluded from some of the analyses. Mtb6 also has relatively low coverage. Was the sequencing quality adequate to accurately identify all the lineage markers, in particular those with a lower depth of coverage? Could a hybrid approach be an inexpensive way to polish these assemblies?

We reanalysed the L9 sample and, with some better cleaning, got it to a single contig with better depth and overall score. This is outlined in the Supplementary table 1 sheets. While depth is average, it is still above the recommended 30x, which is needed for good sequence recovery (Sanderson et al., 2024). We did indeed recover all lineage markers from these assemblies.

Recommendations for improving the writing and presentation.

The introduction is well-written and recent MTBC pangenomic studies have been incorporated, but I am curious as to why this paper was not referred to: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC6922483/ I believe this was the first attempt to study the pangenome, albeit with a different research question. Nearly all previous analyses largely focused on utilizing the pangenome to investigate transmission.

Indeed this study did look at a pangenome of sorts, but specifically SNPs and not genes or regions. Since the latter is the main basis for pangenome work these days, we chose not to include this paper.

Minor corrections to the text and figures.

In line 129, it is explained that DNA was extracted to be suitable for PacBio sequencing, but ONT sequencing was used for the 11 new sequences. Is this a minor oversight or do the authors feel that DNA extracted for PacBio would be suitable for ONT sequencing? It is a fair assumption.

We apologise, this is a long-read extraction approach and not specific to PacBio. We have amended the text to state this.

In line 153, this should be removed: (Conor, could you please add the script to your GitHub page?).

This has been fixed now.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study by Seo et al highlights knowledge gaps regarding the role of cerebellar complex spike (CS) activity during different phases of learning related to optokinetic reflex (OKR) in mice. The novelty of the approach is twofold: first, specifically perturbing the activity of climbing fibers (CFs) in the flocculus (as opposed to disrupting communication between the inferior olive (IO) and its cerebellar targets globally); and second, examining whether disruption of the CS activity during the putative "consolidation phase" following training affects OKR performance.

The first part of the results provides adequate evidence supporting the notion that optogenetic disruption of normal CF-Purkinje neuron (PN) signaling results in the degradation of OKR performance. As no effects are seen in OKR performance in animals subjected to optogenetic irradiation during the memory consolidation or retrieval phases, the authors conclude that CF function is not essential beyond memory acquisition. However, the manuscript does not provide a sufficiently solid demonstration that their long-term activity manipulation of CF activity is effective, thus undermining the confidence of the conclusions.

Strengths:

The main strength of the work is the aim to examine the specific involvement of the CF activity in the flocculus during distinct phases of learning. This is a challenging goal, due to the technical challenges related to the anatomical location of the flocculus as well as the IO. These obstacles are counterbalanced by the use of a well-established and easy-to-analyse behavioral model (OKR), that can lead to fundamental insights regarding the long-term cerebellar learning process.

Weaknesses:

The impact of the work is diminished by several methodological shortcomings.

Most importantly, the key finding that prolonged optogenetic inhibition of CFs (for 30 min to 6 hours after the training period) must be complemented by the demonstration that the manipulation maintains its efficacy. In its current form, the authors only show inhibition by short-term optogenetic irradiation in the context of electrical-stimulation-evoked CSs in an ex vivo preparation. As the inhibitory effect of even the eNpHR3.0 is greatly diminished during seconds-long stimulations (especially when using the yellow laser as is done in this work (see Zhang, Chuanqiang, et al. "Optimized photo-stimulation of halorhodopsin for long-term neuronal inhibition." BMC biology 17.1 (2019): 1-17), we remain skeptical of the extent of inhibition during the long manipulations. In short, without a demonstration of effective inhibition throughout the putative consolidation phase (for example by showing a significant decrease in CS frequency throughout the irradiation period), the main claim of the manuscript of phase-specific involvement of CF activity in OKR learning can not be considered to be based on evidence.

Second, the choice of viral targeting strategy leaves gaps in the argument for CF-specific mechanisms. CaMKII promoters are not selective for the IO neurons, and even the most precise viral injections always lead to the transfection of neurons in the surrounding brainstem, many of which project to the cerebellar cortex in the form of mossy fibers (MF). Figure 1Bii shows sparsely-labelled CFs in the flocculus, but possibly also MFs. While obtaining homogenous and strong labeling in all floccular CFs might be impossible, at the very least the authors should demonstrate that their optogenetic manipulation does not affect simple spiking in PNs.

Finally, while the paper explicitly focuses on the effects of CF-evoked complex spikes in the PNs and not, for example, on those mediated by molecular layer interneurons or via direct interaction of the CF with vestibular nuclear neurons, it would be best if these other dimensions of CF involvement in cerebellar learning were candidly discussed.

Reviewer #2 (Public Review):

Summary:

The authors aimed to explore the role of climbing fibers (CFs) in cerebellar learning, with a focus on optokinetic reflex (OKR) adaptation. Their goal was to understand how CF activity influences memory acquisition, memory consolidation, and memory retrieval by optogenetically suppressing CF inputs at various stages of the learning process.

Strengths:

The study addresses a significant question in the cerebellar field by focusing on the specific role of CFs in adaptive learning. The authors use optogenetic tools to manipulate CF activity. This provides a direct method to test the causal relationship between CF activity and learning outcomes.

Weaknesses:

Despite shedding light on the potential role of CFs in cerebellar learning, the study is hampered by significant methodological issues that question the validity of its conclusions. The absence of detailed evidence on the effectiveness of CF suppression and concerns over tissue damage from optogenetic stimulation weakens the argument that CFs are not essential for memory consolidation. These challenges make it difficult to confirm whether the study's objectives were fully met or if the findings conclusively support the authors' claims. The research commendably attempts to unravel the temporal involvement of CFs in learning but also underscores the difficulties in pinpointing specific neural mechanisms that underlie the phases of learning. Addressing these methodological issues, investigating other signals that might instruct consolidation, and understanding CFs' broader impact on various learning behaviors are crucial steps for future studies.

We appreciate the editors and reviewers for their constructive feedback and careful consideration of our manuscript. Despite their acknowledgment of the potential of our study to yield valuable insights into the role of CF activity in cerebellar learning and its phase-specific involvement, we have meticulously addressed all the methodological concerns raised by providing additional clarifications and explanations in this letter.

In response to concerns regarding the efficacy of long-term optogenetic inhibition, we conducted additional in vivo monitoring of CF activity during the irradiation period, confirming sustained inhibition of complex spikes throughout the consolidation phase (Figure 2, lines 112-139). Although stable single-unit recording beyond 40 minutes was not feasible due to technical challenges, the robust suppression of CF-evoked complex spikes we observed during this period (Figure 2, lines 112–139) provides strong evidence that halorhodopsin-mediated inhibition persists over the longer irradiation intervals employed in our behavioral assays.

Moreover, given that there is a concern regarding the CaMKII promoter also inducing expression in neighboring mossy fibers, potentially affecting simple spike activity, we have presented data in Figure 2C, which illustrates that PC simple spike firing rates remain unchanged during prolonged illumination. This finding confirms that our optogenetic manipulation selectively disrupts CF-mediated complex spikes without influencing mossy fiber to PC transmission. We have elucidated these results further in lines 128 to 136.

Lastly, we have broadened our Discussion to consider alternative mechanisms of CF involvement in cerebellar learning, including the modulation of molecular layer interneurons (Rowan et al., 2018) and direct CF interactions with vestibular nuclear neurons (Balaban et al., 1981), thereby offering a more comprehensive perspective on the multifaceted role of CF signaling. Specific clarifications regarding these points are articulated from lines 222 to 242 and 243 to 254 in the manuscript. We are confident that these revisions adequately address the reviewers' concerns and further substantiate the specificity and significance of our study findings

(1) Rowan, Matthew JM, et al. "Graded control of climbing-fiber-mediated plasticity and learning by inhibition in the cerebellum." Neuron 99.5 (2018): 999-1015.

(2) Balaban, Carey D., Yasuo Kawaguchi, and Eiju Watanabe. "Evidence of a collateralized climbing fiber projection from the inferior olive to the flocculus and vestibular nuclei in rabbits." Neuroscience letters 22.1 (1981): 23-29.

Author response:

The following is the authors’ response to the original reviews

Life Assessment

The authors use a synthetic approach to introduce synaptic ribbon proteins into HEK cells and analyze the ability of the resulting assemblies to cluster calcium channels at the active zone. The use of this ground-up approach is valuable as it establishes a system to study molecular interactions at the active zone. The work relies on a solid combination of super-resolution microscopy and electrophysiology, but would benefit from: (i) additional ultrastructural analysis to establish ribbon formation (in the absence of which the claim of these being synthetic ribbons might not be supported; (ii) data quantification (to confirm colocalization of different proteins); (iii) stronger validation of impact on Ca2+ function; (iv) in depth discussion of problems derived from the use of an over-expression approach.

We thank the editors and the reviewers for the constructive comments and appreciation of our work. Please find a detailed point-to-point response below. In response to the critique received, we have now (i) included an ultrastructural analysis of the SyRibbons using correlative light microscopy and cryo-electron tomography, (ii) performed quantifications to confirm the colocalisation of the various proteins, (iii) discussed and carefully rephrased our interpretation of the role of the ribbon in modulating Ca²⁺ channel function and (iv) discussed concerns regarding the use of an overexpression system. 

Public Reviews:

Reviewer #1 (Public Review):

We would like to thank the reviewer for the comments and advice to further improve our manuscript. We have completely overhauled the manuscript taking the suggestions of the reviewer into account.

(1) Are these truly "synthetic ribbons". The ribbon synapse is traditionally defined by its morphology at the EM level. To what extent these structures recapitulate ribbons is not shown. It has been previously shown that Ribeye forms aggregates on its own. Do these structures look any more ribbonlike than ribeye aggregates in the absence of its binding partners?

We thank reviewer 1 for their constructive feedback and critique of the work. 

We agree that traditionally, ribbon synapses have always been defined by the distinct morphology observed at the EM level. However, since the discovery of the core-components of ribbons (RIBEYE and Piccolino) confocal and super-resolution imaging of immunofluorescently labelled ribbons have gained importance for analysing ribbon synapses. A correspondence of RIBEYE immunofluorescent structures at the active zone to electron microscopy observations of ribbons has been established in numerous studies (Wong et al, 2014; Michanski et al, 2019, 2023; Maxeiner et al, 2016; Jean et al, 2018) even though direct correlative approaches have yet to be performed to our knowledge. We have now analysed SyRibbons using cryo-correlative electron-light microscopy. We observe that GFPpositive RIBEYE spots corresponded well with electron-dense structures, as is characteristic for synaptic ribbons (Robertis & Franchi, 1956; Smith & Sjöstrand, 1961; Matthews & Fuchs, 2010). We could also observe SyRibbons within 100 nm of the plasma membrane (see Fig. 3). We have now added this qualitative ultrastructural analysis of SyRibbons in the main manuscript (lines 272 - 294, Fig. 3 and Supplementary Fig. 3).

(2) No new biology is discovered here. The clustering of channels is accomplished by taking advantage of previously described interactions between RBP2, Ca channels and bassoon. The localization of Ribeye to bassoon takes advantage of a previously described interaction between the two. Even the membrane localization of the complexes required the introduction of a membraneanchoring motif.

We respectfully disagree with the overall assessment. Our study emphasizes the synthetic establishment of protein assemblies that mimic key aspects of ribbon-type active zone, defining minimum molecular requirements. Numerous previous studies have described the role of the synaptic ribbon in organising the spatial arrangement of Ca²⁺ channels, regulating their abundance and possibly also modulating their physiological properties (Maxeiner et al, 2016; Frank et al, 2010; Jean et al, 2018; Wong et al, 2014; Grabner & Moser, 2021; Lv et al, 2016). We would like to highlight that there remain major gaps between existing in vitro and in vivo data; for instance, no evidence for direct or indirect interactions between Ca²⁺ channels and RIBEYE have been demonstrated so far. While we do indeed take advantage of previously known interactions between RIBEYE and Bassoon (tom Dieck et al, 2005); between Bassoon, RBP2 and P/Q-type Ca²⁺ channels (Davydova et al, 2014); and between RBP2 and Ltype Ca²⁺ channels (Hibino et al, 2002), our study tries to bridge these gaps by establishing the indirect link between the synaptic ribbon (RIBEYE) and L-type CaV1.3 Ca²⁺ channels using a bottom-up approach, which has previously just been speculative. Our data shows how even in a synapse-naive heterologous expression system, ribbon synapse components assemble Ca²⁺ channel clusters and even show a partial localisation of Ca²⁺ signal. Moreover, we argue that the established reconstitution approach provides other interesting insights such as laying ground-up evidence supporting the anchoring of the synaptic ribbon by Bassoon. Finally, we expect that the established system will serve future studies aimed at deciphering the role of putative CaV1.3 or CaV1.4 interacting proteins in regulating Ca²⁺ channels of ribbon synapses by providing a more realistic Ca²⁺ channel assembly that has been available in heterologous expression systems used so far. In response to the reviewers comment we have augmented the discussion accordingly.  

(3) The only thing ribbon-specific about these "syn-ribbons" is the expression of ribeye and ribeye does not seem to participate in the localization of other proteins in these complexes. Bsn, Cav1.3 and RBP2 can be found in other neurons.

The synaptic ribbon made of RIBEYE is the key molecular difference in the molecular AZ ultrastructure of ribbon synapses in the eye and the ear. We hypothesize the ribbon to act as a superscaffold that enables AZ with large Ca²⁺ channel assemblies and readily releasable pools. In further support of this hypothesis, the present study on synthetic ribbons shows that CaV1.3 Ca²⁺ channel clusters are larger in the presence of SyRibbons compared to SyRibbon-less CaV1.3 Ca²⁺ channel clusters in tetratransfected HEK cells (Ca²⁺ channels, RBP, membrane-anchored Bassoon, and RIBEYE, Fig. 6). In response to the reviewers comment we now added an analysis of triple-transfected HEK cells (Ca²⁺ channels, RBP, membrane-anchored Bassoon), in which CaV1.3 Ca²⁺ channel clusters again are significantly smaller than at the SyRibbons and indistinguishable from SyRibbon-less CaV1.3 Ca²⁺ channel clusters (Fig. 6E, F).

(4) As the authors point out, RBP2 is not necessary for some Ca channel clustering in hair cells, yet seems to be essential for clustering to bassoon here.

Here we would like to clarify that RBP2 is indeed important in inner hair cells for promoting a larger complement of CaV1.3 and RBP2 KO mice show smaller CaV1.3 channel clusters and reduced whole cell and single-AZ Ca²⁺ influx amplitudes (Krinner et al, 2017). However, a key point of difference we emphasize on is that even though CaV1.3 clusters appeared smaller, they did not appear broken or fragmented as they do upon genetic perturbation of Bassoon (Frank et al, 2010), RIBEYE (Jean et al, 2018) or Piccolino (Michanski et al, 2023). This highlights how there may be a hierarchy in the spatial assembly of CaV1.3 channels at the inner hair cell ribbon synapse (also described in the discussion section “insights into presynaptic Ca²⁺ channel clustering and function”) with proteins like RBP2 regulating abundance of CaV1.3 channels at the synapse and organising them into smaller clusters – what we have termed as “nanoclustering”; while Bassoon and RIBEYE may serve as super-scaffolds further organizing these CaV1.3 nanoclusters into “microclusters”. Observations of fragmented Ca²⁺ channel clusters and broader spread of Ca²⁺ signal seen upon Ca²⁺ imaging in RIBEYE and Bassoon mutants (Jean et al, 2018; Frank et al, 2010; Neef et al, 2018), and the absence of such a phenotype in RBP2 mutants (Krinner et al, 2017) may be explained by such a differential role of these proteins in organising Ca²⁺ channel spatial assembly. The data of the present study on reconstituted ribbon containing AZs are in line with these observations in inner hair cells: RBP2 appears important to tether Ca²⁺ channels to Bassoon and these AZ-like assemblies are organised to their full extent by the presence of RIBEYE. As mentioned in the response to point 3 of the reviewer, we have now further strengthened this point by adding the analysis of SyRibbon-less CaV1.3 Ca²⁺ channel clusters in tripletransfected HEK cells (Ca²⁺ channels, RBP, membrane-anchored Bassoon, Fig. 6E, F). Moreover, we have revised the discussion accordingly. 

(5) The difference in Ca imaging between SyRibbons and other locations is extremely subtle.

We agree with the reviewer on the modest increase in Ca²⁺ signal amplitude seen in the presence of  SyRibbons and provide the following reasoning for this observation: 

(i) It is plausible that due to the overexpression approach, Ca²⁺ channels (along with RBP2 and PalmBassoon) still show considerably high expression throughout the membrane even in regions where SyRibbons are not localised. Indeed, this is evident in the images shown in the lower panel in Fig. 6B, where Ca²⁺ channel immunofluorescence is distributed across the plasma membrane with larger clusters formed underneath SyRibbons (for an opposing scenario, please see the cell in Fig. 6B upper panel with very localised CaV1.3 distribution underneath SyRibbons). This would of course diminish the difference in the Ca²⁺ signals between membrane regions with and without SyRibbons. We note that while the contrast is greater for native synapses, extrasynaptic Ca²⁺ channels have been described in numerous studies alone for hair cells (Roberts et al, 1990; Brandt, 2005; Zampini et al, 2010; Wong et al, 2014).

(ii) Nevertheless, we do not expect a remarkably big difference in Ca²⁺ influx due to the presence of SyRibbons in the first place. Ribbon-less AZs in inner hair cells of RIBEYE KO mice showed normal Ca²⁺ current amplitudes at the whole-cell and the single-AZ level (Jean et al, 2018). However, it was the spatial spread of the Ca2+ signal at the single-AZ level which appeared to be broader and more diffuse in these mutants in the absence of the ribbon, in contrast to the more confined Ca2+ hotspots seen in the wild-type controls. 

So, in agreement with these published observations – it appears that presence of SyRibbons helps in spatially confining the Ca²⁺ signal by super scaffolding nanoclusters into microclusters (see also our response to points 3 and 4 of the reviewer): this is evident from seeing some spatial confinement of Ca²⁺ signals near SyRibbons on top of the diffuse Ca²⁺ signal across the rest of the membrane as a result of overexpression in HEK cells. 

We have now carefully rephrased our interpretation throughout the manuscript and added further explanation in the discussion section.   

(6) The effect of the expression of palm-Bsn, RBP2 and the combination of the two on Ca-current is ambiguous. It appears that while the combination is larger than the control, it probably isn't significantly different from either of the other two alone (Fig 5). Moreover, expression of Ribeye + the other two showed no effect on Ca current (Figure 7). Also, why is the IV curve right shifted in Figure 7 vs Figure 5?

We agree with the reviewer that co-expression of palm-Bassoon and RBP2 seems to augment Ca²⁺ currents, while the additional expression of RIBEYE results in no change when compared to wild-type controls. We currently do not have an explanation for this observation and would refrain from making any claims without concrete evidence. As the reviewer also correctly pointed out, while the expression of the combination of palm-Bassoon and RBP2 raises Ca²⁺ currents, current amplitudes are not significantly different when compared to the individual expression of the two proteins (P > 0.05, Kruskal-Wallis test). In light of this, we have now carefully rephrased our MS. Moreover, we would like to thank reviewer 1 for pointing out the right shift in the IV curve which was due to an error in the values plotted on the x-axis. This has been corrected in the updated version of the manuscript. 

(7) While some of the IHC is quantified, some of it is simply shown as single images. EV2, EV3 and Figure 4a in particular (4b looks convincing enough on its own, but could also benefit from a larger sample size and quantification)

We have now added quantifications for the colocalisations of the various transfection combinations depicted in the above-mentioned figures collectively in Supplementary Figure 7 and added the corresponding results and methods accordingly. 

Reviewer #2 (Public Review):

We would like to thank the reviewer for the comments and advice to further improve our manuscript.

(1) Relies on over-expression, which almost certainly diminishes the experimentally-measured parameters (e.g. pre-synapse clustering, localization of Ca2+ entry).

We acknowledge this limitation highlighted by the reviewer arising from the use of an overexpression system and have carefully rephrased our interpretation and discussed possible caveats in the discussion section. 

(2) Are HEK cells the best model? HEK cells secrete substances and have a studied-endocytitic pathway, but they do not create neurosecretory vesicles. Why didn't the authors try to reconstitute a ribbon synapse in a cell that makes neurosecretory vesicles like a PC12 cell?

This is a valid point for discussion that we also had here extensively. We indeed did consider pheochromocytoma cells (PC12 cells) for reconstitution of ribbon-type AZs and also performed initial experiments with these in the initial stages of the project. PC12 cells offer the advantage of providing synaptic-like microvesicles and also endogenously express several components of the presynaptic machinery such as Bassoon, RIM2, ELKS etc (Inoue et al, 2006) such that overexpression of exogenous AZ proteins would have to be limited to RIBEYE only. 

However, a major drawback of PC12 cells as a model is the complex molecular background of these cells. We have also briefly described this in the discussion section (line 615 – 619). Naïve, undifferentiated PC12 cells show highly heterogeneous expression of various CaV channel types (Janigro et al, 1989); however, CaV1.3, the predominant type in ribbon synapses of the ear, does not seem to express in these cells (Liu et al, 1996). Furthermore, our attempts at performing immunostainings against CaV1.3 and at overexpressing CaV1.3 in PC12 cells did not prove successful and we decided on refraining from pursuing this further (data not shown). 

On the contrary, HEK293 cells being “synapse-naïve” provide the advantage of serving as a “blank canvas” for performing such reconstitutions, e.g. they lack voltage-gated Ca²⁺ channels and multidomain proteins of the active zone. Moreover, an important practical aspect for our choice was the availability of the HEK293 cell line with stable (and inducible) expression of the CaV1.3 Ca²⁺ channel complex. Finally, as described in lines 613 – 614 of the discussion section, even though HEK293 cells lack SVs and the molecular machinery required for their release, our work paves way for future studies which could employ delivery of SV machinery via co-expression (Park et al, 2021) which could then be analyzed by the correlative light and electron microscopy workflow we worked out and added during revision. 

(3) Related to 1 and 2: the Ca channel localization observed is significant but not so striking given the presence of Cav protein and measurements of Ca2+ influx distributed across the membrane. Presumably, this is the result of overexpression and an absence of pathways for pre-synaptic targeting of Ca channels. But, still, it was surprising that Ca channel localization was so diffuse. I suppose that the authors tried to reduce the effect of over-expression by using an inducible Cav1.3? Even so, the accessory subunits were constitutively over-expressed.

We agree with the reviewer on the modest increase in Ca²⁺ signal amplitude seen in the presence of SyRibbons. Yes, we employed inducible expression of the CaV1.3a subunit and tried to reduce the effect of overexpression by testing different induction times. However, we did not observe any major differences in expression and observed large variability in CaV1.3 expression across cells irrespective of induction duration. At all time points, there were cells with diffuse CaV1.3 localisation also in regions without SyRibbons which likely reduced the contrast of the Ca²⁺ signal we observe. We provide the following reasoning for this observation: 

(i) It is plausible that due to the overexpression approach, Ca²⁺ channels (along with RBP2 and PalmBassoon) still show considerable expression along the membrane also in regions where SyRibbons are not localised. Indeed, this is evident in the images shown in the lower panel in Fig. 6B where Ca²⁺ channel immunofluorescence is distributed across the plasma membrane with larger clusters formed underneath SyRibbons. This would of course diminish the difference in the Ca²⁺ signals between membrane regions with and without SyRibbons. We note that while the contrast is greater for native synapses, extrasynaptic Ca²⁺ channels have been described in numerous studies alone for hair cells (Roberts et al, 1990; Brandt, 2005; Zampini et al, 2010; Wong et al, 2014).

(ii) Nevertheless, we do not expect a striking difference in Ca²⁺ influx amplitude due to the presence of SyRibbons in the first place. Ribbon-less AZs in inner hair cells of RIBEYE KO mice showed normal Ca²⁺ current amplitudes at the whole-cell and the single-AZ level (Jean et al, 2018). Instead, it was the spatial spread of the Ca²⁺ signal at the single-AZ level which appeared to be broader and more diffuse in these mutants in the absence of the ribbon, in contrast to the more confined Ca²⁺ hotspots seen in the wildtype controls. 

So, in agreement with these published observations – it appears that presence of SyRibbons helps in spatially confining the Ca²⁺ signal by super scaffolding nanoclusters into microclusters: this is evident from seeing some spatial confinement of Ca²⁺ signals near SyRibbons on top of the diffuse Ca²⁺ signal across the rest of the membrane as a result of overexpression in HEK cells. 

We have now carefully rephrased our interpretation throughout the manuscript and added further explanation in the discussion section.   

Reviewer #3 (Public Review):

We would like to thank the reviewer for the comments and advice to further improve our manuscript.

(1) The results obtained in a heterologous system (HEK293 cells) need to be interpreted with caution. They will importantly speed the generation of models and hypothesis that will, however, require in vivo validation.

We acknowledge this limitation highlighted by Reviewer 3 arising from the use of an overexpression system and have carefully rephrased our interpretation and discussed possible caveats in the discussion section. We employed inducible expression of the CaV1.3a subunit and tried to reduce the effect of overexpression by testing different induction times. However, we did not observe any major differences in expression and observed large variability in CaV1.3 expression across cells irrespective of induction duration. At all time points, there were cells with diffuse CaV1.3 localisation, even in regions without SyRibbons and this could reduce the contrast of the Ca²⁺ signal we observe. We provide the following reasoning for this observation: 

(i) It is plausible that due to the overexpression approach, Ca²⁺ channels (along with RBP2 and PalmBassoon) still show considerable expression along the membrane also in regions where SyRibbons are not localised. Indeed, this is evident in the images shown in the lower panel in Fig. 6B where Ca²⁺ channel immunofluorescence is distributed across the plasma membrane with larger clusters formed underneath SyRibbons. This would of course diminish the difference in the Ca²⁺ signals between membrane regions with and without SyRibbons. We note that while the contrast is greater for native synapses, extrasynaptic Ca²⁺ channels have been described in numerous studies alone for hair cells (Roberts et al, 1990; Brandt, 2005; Zampini et al, 2010; Wong et al, 2014).

(ii) Nevertheless, we do not expect a striking difference in Ca²⁺ influx amplitude due to the presence of SyRibbons in the first place. Ribbon-less AZs in inner hair cells of RIBEYE KO mice showed normal Ca²⁺ current amplitudes at the whole-cell and the single-AZ level (Jean et al, 2018). Instead, it was the spatial spread of the Ca²⁺ signal at the single-AZ level which appeared to be broader and more diffuse in these mutants in the absence of the ribbon, in contrast to the more confined Ca²⁺ hotspots seen in the wildtype controls. 

So, in agreement with these published observations – it appears that presence of SyRibbons helps in spatially confining the Ca²⁺ signal by super scaffolding nanoclusters into microclusters: this is evident from seeing some spatial confinement of Ca²⁺ signals near SyRibbons on top of the diffuse Ca²⁺ signal across the rest of the membrane as a result of overexpression in HEK cells. 

(2) The authors analyzed the distribution of RIBEYE clusters in different membrane compartments and correctly conclude that RIBEYE clusters are not trapped in any of those compartments, but it is soluble instead. The authors, however, did not carry out a similar analysis for Palm-Bassoon. It is therefore unknown if Palm-Bassoon binds to other membrane compartments besides the plasma membrane. That could occur because in non-neuronal cells GAP43 has been described to be in internal membrane compartments. This should be investigated to document the existence of ectopic internal Synribbons beyond the plasma membrane because it might have implications for interpreting functional data in case Ca2+-channels become part of those internal Synribbons.

In response to this valid concern, we have now included the suggested experiment in Supplementary Figure 1. We investigated the subcellular localisation of Palm-Bassoon and did not find Palm-Bassoon puncta to colocalise with ER, Golgi, or lysosomal markers, suggesting against a possible binding with membrane compartments inside the cell. We have added the following sentence in the results section, line 145 : “Palm-Bassoon does not appear to localize in the ER, Golgi apparatus or lysosomes (Supplementary Fig 1 D, E and F).”

(3) The co-expression of RBP2 and Palm-Bassoon induces a rather minor but significant increase in Ca2+-currents (Figure 5). Such an increase does not occur upon expression of (1) Palm-Bassoon alone, (2) RBP2 alone or (3) RIBEYE alone (Figure 5). Intriguingly, the concomitant expression of PalmBassoon, RBP2 and RIBEYE does not translate into an increase of Ca2+-currents either (Figure 7).

We agree with the reviewer that co-expression of palm-Bassoon and RBP2 seems to augment Ca²⁺ currents, while the additional expression of RIBEYE results in no change when compared to wild-type controls. We currently do not have an explanation for this observation and would refrain from making any claims without concrete evidence. We also highlight that, while the expression of the combination of palm-Bassoon and RBP2 raises Ca²⁺ currents, current amplitudes are not significantly different when compared to the individual expression of the two proteins (P > 0.05, Kruskal-Wallis test). In light of this, we have now carefully rephrased our MS. 

(4) The authors claim that Ca2+-imaging reveals increased CA2+-signal intensity at synthetic ribbontype AZs. That claim is a subject of concern because the increase is rather small and it does not correlate with an increase in Ca2+-currents.

Thanks for the comment: please see our response to your first comment and the lines 585 – 610 in the discussion section.

Recommendations for the authors:  

Reviewer #2 (Recommendations For The Authors):

(1) The authors should have a better discussion of problems derived from over-expression.

Done. Please see above. 

(2) Ideally, the authors would repeat the study using a secretory cell line, but this is of course not possible. The idea could be brought forth, though.

As described above in our response to the public review of reviewer 2, we have discussed this idea in the discussion section (refer to lines 615 – 619), emphasizing on both the advantages and the limitations of using a secretory cell line (e.g. PC12 cells) instead of HEK293 cells as a model for performing such reconstitutions. 

Reviewer #3 (Recommendations For The Authors):

(1) There are several figures in which colocalization between different proteins is studied only displaying images but without any quantitative data. This should be corrected by providing such a quantitative analysis.

We have now added quantifications for the colocalisations of the various transfection combinations depicted in the above-mentioned figures collectively in Supplementary Figure 7 and added the corresponding results and methods accordingly. 

(2) The little increase in Ca2+-currents and Ca2+-influx associated to the clustering of Ca2+-channels to Synribbons is a concern. The authors should discuss if such a minor increase (found only when Palm-Bassoon and RBP2 ae co-expressed) would have or not physiological consequences in an actual synapse. They might discuss the comparison of those results and compare with results obtained in genetically modified mice in which Ca2+-currents are affected upon the removal of AZs proteins. On the other hand, they should explain why Ca2+-currents do not increase when the Synribbons are formed by RIBEYE, Palm-Bassoon and RBP2.

Done. Please see above. 

(3) The description of the patch-clamp experiments should be enriched by including representative currents. Did the authors measure tail currents?

We would like to thank the reviewer for the valuable suggestion and have now added representative currents to the figures (see Supplementary Figure 5B). We agree with the reviewer on the importance of further characterizing the Ca²⁺ currents in the presence and absence of SyRibbons by analysis of tail currents for counting the number of Ca²⁺ channels by non-stationary fluctuation analysis but consider this to be out of scope of the current study and an objective for future studies. 

(4) The current displayed in Figure 7 E should be explained better.

Previous studies have shown that Ca²⁺-binding proteins (CaBPs) compete with Calmodulin to reduce Ca²⁺-dependent inactivation (CDI) and promote sustained Ca²⁺ influx in Inner Hair Cells (Cui et al, 2007; Picher et al, 2017). In the absence of CaBPs, CaV1.3-mediated Ca²⁺ currents show more rapid CDI as in the case here upon heterologous expression in HEK cells ((Koschak et al, 2001), see also Picher et al 2017 where co-expression of CaBP2 with CaV1.3 inhibits CDI in HEK293 cells). The inactivation kinetics of CaV1.3 are also regulated by the subunit composition (Cui et al, 2007) along with the modulation via interaction partners and given the reconstitution here we do not find the currents very surprising. 

(5) Is the difference in Ca2+-influx still significantly higher upon the removal of the maximum value measured in positive Syribbons spots (Figure 7, panel K)?

Yes, on removing the maximum value, the P value increases from 0.01 to 0.03 but remains statistically significant. 

(6) In summary, although the approach pioneered by the authors is exciting and provides relevant results, there is a major concern regarding the interpretation of the modulation of Ca2+ channels.

We have now carefully rephrased our interpretation on the modulation of Ca²⁺ channels.  

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Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors, Dalal, et. al., determined cryo-EM structures of open, closed, and desensitized states of the pentameric ligand-gated ion channel ELIC reconstituted in liposomes, and compared them to structures determined in varying nanodisc diameters. They argue that the liposomal reconstitution method is more representative of functional ELIC channels, as they were able to test and recapitulate channel kinetics through stopped-flow thallium flux liposomal assay. The authors and others have described channel interactions with membrane scaffold proteins (MSP), initially thought to be in a size-dependent manner. However, the authors reported that their cryo-EM ELIC structure interacts with the large nanodisc spNW25, contrary to their original hypotheses. This suggests that the channel's interactions with MSPs might alter its structure, possibly not accurately representing/reflecting functional states of the channel.

Strengths:

Cryo-EM structural determination from proteoliposomes is a promising methodology within the ion channel field due to their large surface area and lack of MSP or other membrane mimetics that could alter channel structure. Comparing liposomal ELIC to structures in various-sized nanodiscs gives rise to important discussions for other membrane protein structural studies when deciding the best method for individual circumstances.

Weaknesses:

The overarching goal of the study was to determine structural differences of ELIC in detergent nanodiscs and liposomes. Including comparisons of the results to the native bacterial lipid environment would provide a more encompassing discussion of how the determined liposome structures might or might not relate to the native receptor in its native environment. The authors stated they determined open, closed, and desensitized states of ELIC reconstituted in liposomes and suggest the desensitization gate is at the 9' region of the pore. However, no functional studies were performed to validate this statement.

The goal of this study was to determine structures of ELIC in the same lipid environment in which its function is characterized. However, it is also worth noting that phosphatidylethanolamine and phosphatidylglyerol, two lipids used for the liposome formation, are necessary for ELIC function (PMID 36385237) and principal lipid components of gram-negative bacterial membranes in which ELIC is expressed.

The desensitized structure of ELIC in liposomes shows a pore diameter at the hydrophobic L240 (9’) residue of 3.3 Å, which is anticipated to pose a large energetic barrier to the passage of ions due to the hydrophobic effect. We have included a graphical representation of pore diameters from the HOLE analysis for all liposome structures in Supplementary Figure 6B. While we have not tested the role of L240 in desensitization with functional experiments, it was shown by Gonzalez-Gutierrez and colleagues (PMID 22474383) that the L240A mutation apparently eliminates desensitization in ELIC. This finding is consistent with L240 (9’) being the desensitization gate of ELIC. We have referenced this study when discussing the desensitization gate in the Results.

Reviewer #2 (Public review):

Summary

The report by Dalas and colleagues introduces a significant novelty in the field of pentameric ligand-gated ion channels (pLGICs). Within this family of receptors, numerous structures are available, but a widely recognised problem remains in assigning structures to functional states observed in biological membranes. Here, the authors obtain both structural and functional information of a pLGIC in a liposome environment. The model receptor ELIC is captured in the resting, desensitized, and open states. Structures in large nanodiscs, possibly biased by receptor-scaffold protein interactions, are also reported. Altogether, these results set the stage for the adoption of liposomes as a proxy for the biological membranes, for cryoEM studies of pLGICs and membrane proteins in general.

Strengths

The structural data is comprehensive, with structures in liposomes in the 3 main states (and for each, both inward-facing and outward-facing), and an agonist-bound structure in the large spNW25 nanodisc (and a retreatment of previous data obtained in a smaller disc). It adds up to a series of work from the same team that constitutes a much-needed exploration of various types of environment for the transmembrane domain of pLGICs. The structural analysis is thorough.

The tone of the report is particularly pleasant, in the sense that the authors' claims are not inflated. For instance, a sentence such as "By performing structural and functional characterization under the same reconstitution conditions, we increase our confidence in the functional annotation of these structures." is exemplary.

Weaknesses

Core parts of the method are not described and/or discussed in enough detail. While I do believe that liposomes will be, in most cases, better than, say, nanodiscs, the process that leads from the protein in its membrane down to the liposome will play a big role in preserving the native structure, and should be an integral part of the report. Therefore, I strongly felt that biochemistry should be better described and discussed. The results section starts with "Optimal reconstitution of ELIC in liposomes [...] was achieved by dialysis". There is no information on why dialysis is optimal, what it was compared to, the distribution of liposome sizes using different preparation techniques, etc... Reading the title, I would have expected a couple of paragraphs and figure panels on liposome reconstitution. Similarly, potential biochemical challenges are not discussed. The methods section mentions that the sample was "dialyzed [...] over 5-7 days". In such a time window, most of the members of this protein family would aggregate, and it is therefore a protocol that can not be directly generalised. This has to be mentioned explicitly, and a discussion on why this can't be done in two days, what else the authors tested (biobeads? ... ?) would strengthen the manuscript.

To a lesser extent, the relative lack of both technical details and of a broad discussion also pertains to the cryoEM and thallium flux results. Regarding the cryoEM part, the authors focus their analysis on reconstructions from outward-facing particles on the basis of their better resolutions, yet there was little discussion about it. Is it common for liposome-based structures? Are inward-facing reconstructions worse because of the increased background due to electrons going through two membranes? Are there often impurities inside the liposomes (we see some in the figures)? The influence of the membrane mimetics on conformation could be discussed by referring to other families of proteins where it has been explored (for instance, ABC transporters, but I'm sure there are many other examples). If there are studies in other families of channels in liposomes that were inspirational, those could be mentioned. Regarding thallium flux assays, one argument is that they give access to kinetics and set the stage for time-resolved cryoEM, but if I did not miss it, no comparison of kinetics with other techniques, such as electrophysiology, nor references to eventual pioneer time-resolved studies are provided.

Altogether, in my view, an updated version would benefit from insisting on every aspect of the methodological development. I may well be wrong, but I see this paper more like a milestone on sample prep for cryoEM imaging than being about the details of the ELIC conformations.

Additions have been made to the Results and Discussion sections elaborating on the following points: 1) reconstitution of ELIC in liposomes using dialysis, the advantage of this over other methods such as biobeads, and whether the dialysis protocol can be shortened for other less stable proteins; 2) the issue of separating outward- and inward-facing channels; 3) referencing the effect of nanodiscs on ABC transporters, structures of membrane proteins in liposomes, and pioneering time-resolved cryo-EM studies; and 4) comparison of the kinetics of ELIC gating kinetics with electrophysiology measurements. With regards to the first point, it should be noted that all necessary details are provided in the Methods to reproduce the experiments including the reconstitution and stopped-flow thallium flux assay. It is also important to note that the same preparation for making proteoliposomes was used for assessing function using the stopped-flow thallium flux assay and for determining the structure by cryo-EM. This is now stated in the Results.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major revisions:

(1) The authors suggest that the desensitization gate is located at the 9' region within the pore. However, as stated by the authors, the 2' residues function as the desensitization gate in related channels. In a few of their HOLE analyzed structures (e.g. Figure 2B and 4B), there seems to be a constriction also at 2', but this finding is not discussed in the context of desensitization. Further functional testing of mutated 9' and/or 2' gates would bolster the argument for the location of the desensitization gate.

As stated above, we have included HOLE plots of pore radius in Supplementary Fig. 6B and referenced the study showing that the L240A mutation (9’) in ELIC (PMID 22474383) appears to eliminate desensitization. This result along with the narrow pore diameter at 9’ in the desensitized structure suggests that 9’ is likely a desensitization gate in ELIC. In contrast, mutation of Q233 (2’) to a cysteine in a previous study produced a channel that still desensitizes (PMID 25960405). Since Q233 is a hydrophilic residue in contrast to L240, Q233 probably does not pose the same energetic barrier to ion translocation as L240 based on the structure.

(2) In discussing functional states of ELIC and ELIC5 in different reconstitution methods, the authors reference constriction sites determined by HOLE analysis software. These constriction sites were key evidence for the authors to determine functional state, however, it is difficult to discern pore sizes based on the figures. Pore diameters and clear color designation (ie, green vs orange) with the figures would greatly aid their discussions.

HOLE plots are displayed in Supplementary Fig. 6B and pore diameters are not provided in the text.

(3) The authors had an intriguing finding that ELIC dimers are found in spNW25 scaffolds. Is there any functional evidence to suggest they could be functioning as dimers?

There is no evidence that the function of ELIC or other pLGICs is altered by the formation of dimers of pentamers. Therefore, while this result is intriguing and likely facilitated by concentrating multiple ELIC pentamers within the nanodisc, it is not clear if these interactions have any functional importance. We have stated this in the Results.

(4) Thallium flux assay to validate channel function within proteoliposomes. Proteoliposomes are known to be generally very leaky membranes, would be good to have controls without ELIC added to determine baseline changes in fluorescence.

We have established from multiple previous studies that liposomes composed of 2:1:1 POPC:POPE:POPG (PMID 36385237 and 31724949) do not show significant thallium flux as measured by the stopped-flow assay (PMID 29058195) in the absence of ELIC activity. Furthermore, in the present study, the data in Fig. 1A of WT ELIC shows a low thallium flux rate 60 seconds after exposure to agonist when the ion channel has mostly desensitized. Therefore, this data serves also as a control indicating that the high thallium flux rates in response to agonist (at earlier delay times) are not due to leak, but rather due to ELIC channel activity.

Minor revisions:

(1) Abstract and introduction. 'Liganded' should be ligand

We removed this word and changed it to “agonist-bound” for consistency throughout the manuscript.

(2) Inconsistent formatting of FSC graphs in Supplemental Figure 4

The difference is a consequence of the different formatting between cryoSPARC and Relion FSC graphs.

Reviewer #2 (Recommendations for the authors):

Minor writing remarks:

The present report builds on previous work from the same team, and to my eye it would be a plus if this were conveyed more explicitly. I see it as a strength to explore various developments in several papers that complement each other. E.g in the introduction when citing reference 12 (Dalal 2024), later in introducing ref 15 (Petroff 2022), I wish I was reminded of the main findings and how they fit with the new results.

We have expanded on the Results and Discussion detailing key findings from these studies that are relevant to the current study.

Suggestions for analysis:

Data treatment. Maybe I missed it, but I wondered if C1 vs C5 treatment of the liposome data showed any interesting differences? When I think about the biological membrane, I picture it as a very crowded place with lots of neighbouring proteins. I would not be surprised if, similarly to what they do in discs, the receptor would tend to stick to, or bump into, anything present also in liposomes (a neighboring liposome, some undefined density inside the liposome).

We attempted to perform C1 heterogeneous refinement jobs in cryoSPARC and C1 3D classification in Relion5. For the WT datasets, these did not produce 3D reconstructions that were of sufficient quality for further refinement. For ELIC5 with agonist, the C1 reconstructions were not different than the C5 reconstructions. Furthermore, there was no evidence of dimers of pentamers from the 2D or 3D treatments, unlike what was observed in the spNW25 nanodiscs. This is likely because the density of ELIC pentamers in the liposomes was too low to capture these transient interactions. We have included this information in the Methods.

In data treatment, we sometimes find only what we're looking for. I wondered if the authors tried to find, for instance, the open and D conformations in the resting dataset during classifications.

This is an interesting question since some population of ELIC channels could visit a desensitized conformation in the absence of agonist and this would not be detected in our flux assay. After extensive heterogeneous refinement jobs in cryoSPARC and 3D classification jobs in Relion5, we did not detect any unexpected structures such as open/desensitized conformations in the apo dataset.

In the analysis of the M4 motions, is there info to be gained by looking at how it interacts with the rest of the TMD? For instance, I wondered if the buried surface area between M4 and the rest was changed. Also one could imagine to look at that M4 separately in outward-facing and inward-facing conformations (because the tension due to the bilayer will not be the same in the outer layer in both orientations - intuitively, I'd expect different levels of M4 motions)

We have expanded our analysis of the structures as recommended. We determined the buried surface area between M4 and the rest of the channel in the liganded WT and ELIC5 structures in liposomes and nanodiscs, as well as the area between the TMD interfaces for these structures. There appears to be a pattern where liposome structures show less buried surface area between M4 and the rest of the channel, and less area at the TMD interfaces. Overall, this suggests that the liposome structures of ELIC in the open-channel or desensitized conformations are more loosely packed in the TMD compared to the nanodisc structures.

We have also further discussed the issue of separating outward- and inward-facing conformations in the Results. The problem with classifying outward- and inward-facing orientations is that top/down or tilted views of the particles cannot be easily distinguished as coming from channels in one orientation or the other, unless there are conformational differences between outward- and inward-facing channels that would allow for their separation during 3D heterogeneous refinement or 3D classification. Furthermore, since the inward-facing reconstructions are of much lower resolution than the outward-facing reconstructions, we suspect that these particles are more heterogeneous possibly containing junk, multiple conformations, or particles that are both inward- and outward-facing. On the other hand, the outward-facing structures are of good quality, and therefore we are more confident that these come from a more homogeneous set of particles that are likely outward-facing (Note that most particles are outward facing based on side views of the 2D class averages). That said, when examining the conformation of M4 in outward- and inward-facing structures, we do not see any significant differences with the caveat that the inward-facing structures are of poor quality and that inward- and outward-facing particles may not have been well-separated.

Author response:

The following is the authors’ response to the original reviews

Summary of our revisions

(1) We have explained the reason why the untrained RNN with readout (value-weight) learning only could not well learn the simple task: it is because we trained the models continuously across trials with random inter-trial intervals rather than separately for each episodic trial and so it was not trivial for the models to recognize that cue presentation in different trials constitutes a same single state since the activities of untrained RNN upon cue presentation should differ from trial to trial (Line 177-185).

(2) We have shown that dimensionality was higher in the value-RNNs than in the untrained RNN (Fig. 2K,6H).

(3) We have shown that even when distractor cue was introduced, the value-RNNs could learn the task (Fig. 10).

(4) We have shown that extended value-RNNs incorporating excitatory and inhibitory units and conforming to the Dale's law could still learn the tasks (Fig. 9,10-right column).

(5) In the original manuscript, the non-negatively constrained value-RNN showed loose alignment of value-weight and random feedback from the beginning but did not show further alignment over trials. We have clarified its reason and found a way, introducing a slight decay (forgetting), to make further alignment occur (Fig. 8E,F).

(6) We have shown that the value-RNNs could learn the tasks with longer cue-reward delay (Fig. 2M,6J) or action selection (Fig. 11), and found cases where random feedback performed worse than symmetric feedback.

(7) We compared our value-RNNs with e-prop (Bellec et al., 2020, Nat Commun). While e-prop incorporates the effects of changes in RNN weights across distant times through "eligibility trace", our value-RNNs do not. The reason why our models can still learn the tasks with cue-reward delay is considered to be because our models use TD error and TD learning itself, even TD(0) without eligibility trace, is a solution for temporal credit assignment. In fact, TD error-based e-prop was also examined, but for that, result with symmetric feedback, but not with random feedback, was shown (their Fig. 4,5) while for another setup of reward-based e-prop without TD error, result with random feedback was shown (their SuppFig. 5). We have noted these in Line 695-711 (and also partly in Line 96-99).

(8) In the original manuscript, we emphasized only the spatial locality (random rather than symmetric feedback) of our learning rule. But we have now also emphasized the temporal locality (online learning) as it is also crucial for bio-plausibility and critically different from the original value-RNN with BPTT. We also changed the title.

(9) We have realized that our estimation of true state values was invalid (as detailed in page 34 of this document). Effects of this error on performance comparisons were small, but we apologize for this error.

Reviewer #1 (Public review):

Summary:

Can a plastic RNN serve as a basis function for learning to estimate value. In previous work this was shown to be the case, with a similar architecture to that proposed here. The learning rule in previous work was back-prop with an objective function that was the TD error function (delta) squared. Such a learning rule is non-local as the changes in weights within the RNN, and from inputs to the RNN depends on the weights from the RNN to the output, which estimates value. This is non-local, and in addition, these weights themselves change over learning. The main idea in this paper is to examine if replacing the values of these non-local changing weights, used for credit assignment, with random fixed weights can still produce similar results to those obtained with complete bp. This random feedback approach is motivated by a similar approach used for deep feed-forward neural networks.

This work shows that this random feedback in credit assignment performs well but is not as well as the precise gradient-based approach. When more constraints due to biological plausibility are imposed performance degrades. These results are not surprising given previous results on random feedback. This work is incomplete because the delay times used were only a few time steps, and it is not clear how well random feedback would operate with longer delays. Additionally, the examples simulated with a single cue and a single reward are overly simplistic and the field should move beyond these exceptionally simple examples.

Strengths:

• The authors show that random feedback can approximate well a model trained with detailed credit assignment.

• The authors simulate several experiments including some with probabilistic reward schedules and show results similar to those obtained with detailed credit assignments as well as in experiments.

• The paper examines the impact of more biologically realistic learning rules and the results are still quite similar to the detailed back-prop model.

Weaknesses:

*please note that we numbered your public review comments and recommendations for the authors as Pub1 and Rec1 etc so that we can refer to them in our replies to other comments.

Pub1. The authors also show that an untrained RNN does not perform as well as the trained RNN. However, they never explain what they mean by an untrained RNN. It should be clearly explained.

These results are actually surprising. An untrained RNN with enough units and sufficiently large variance of recurrent weights can have a high-dimensionality and generate a complete or nearly complete basis, though not orthonormal (e.g: Rajan&Abbott 2006). It should be possible to use such a basis to learn this simple classical conditioning paradigm. It would be useful to measure the dimensionality of network dynamics, in both trained and untrained RNN's.

We have added an explanation of untrained RNN in Line 144-147:

“As a negative control, we also conducted simulations in which these connections were not updated from initial values, referring to as the case with "untrained (fixed) RNN". Notably, the value weights w (i.e., connection weights from the RNN to the striatal value unit) were still trained in the models with untrained RNN.”

We have also analyzed the dimensionality of network dynamic by calculating the contribution ratios of each principal component of the trajectory of RNN activities. It was revealed that the contribution ratios of later principal components were smaller in the cases with untrained RNN than in the cases with trained value RNN. We have added these results in Fig. 2K and Line 210-220 (for our original models without non-negative constraint):

“In order to examine the dimensionality of RNN dynamics, we conducted principal component analysis (PCA) of the time series (for 1000 trials) of RNN activities and calculated the contribution ratios of PCs in the cases of oVRNNbp, oVRNNrf, and untrained RNN with 20 RNN units. Figure 2K shows a log of contribution ratios of 20 PCs in each case. Compared with the case of untrained RNN, in oVRNNbp and oVRNNrf, initial component(s) had smaller contributions (PC1 (t-test p = 0.00018 in oVRNNbp; p = 0.0058 in oVRNNrf) and PC2 (p = 0.080 in oVRNNbp; p = 0.0026 in oVRNNrf)) while later components had larger contributions (PC3~10,15~20 p < 0.041 in oVRNNbp; PC5~20 p < 0.0017 in oVRNNrf) on average, and this is considered to underlie their superior learning performance. We noticed that late components had larger contributions in oVRNNrf than in oVRNNbp, although these two models with 20 RNN units were comparable in terms of cue~reward state values (Fig. 2J-left).”

and Fig. 6H and Line 412-416 (for our extended models with non-negative constraint):

“Figure 6H shows contribution ratios of PCs of the time series of RNN activities in each model with 20 RNN units. Compared with the cases with naive/shuffled untrained RNN, in oVRNNbp-rev and oVRNNrf-bio, later components had relatively high contributions (PC5~20 p < 1.4×10,sup>−6</sup> (t-test vs naive) or < 0.014 (vs shuffled) in oVRNNbp-rev; PC6~20 p < 2.0×10⁻⁷ (vs naive) or PC7~20 p < 5.9×10⁻¹⁴ (vs shuffled) in oVRNNrf-bio), explaining their superior value-learning performance.”

Regarding the poor performance of the model with untrained RNN, we would like to add a note. It is sure that untrained RNN with sufficient dimensions should be able to well represent just <10 different states, and state values should be able to be well learned through TD learning regardless of whatever representation is used. However, a difficulty (nontriviality) lies in that because we modeled the tasks in a continuous way, rather than in an episodic way, the activity of untrained RNN upon cue presentation should generally differ from trial to trial. Therefore, it was not trivial for RNN to know that cue presentation in different trials, even after random lengths of inter-trial interval, should constitute a same single state. We have added this note in Line 177-185:

“This inferiority of untrained RNN may sound odd because there were only four states from cue to reward while random RNN with enough units is expected to be able to represent many different states (c.f., [49]) and the effectiveness of training of only the readout weights has been shown in reservoir computing studies [50-53]. However, there was a difficulty stemming from the continuous training across trials (rather than episodic training of separate trials): the activity of untrained RNN upon cue presentation generally differed from trial to trial, and so it is non-trivial that cue presentation in different trials should be regarded as the same single state, even if it could eventually be dealt with at the readout level if the number of units increases.”

The original value RNN study (Hennig et al., 2023, PLoS Comput Biol) also modeled tasks in a continuous way (though using backprop-through-time (BPTT) for training) and their model with untrained RNN also showed considerably larger RPE error than the value RNN even when the number of RNN units was 100 (the maximum number plotted in their Fig. 6A).

Pub2. The impact of the article is limited by using a network with discrete time-steps, and only a small number of time steps from stimulus to reward. What is the length of each time step? If it's on the order of the membrane time constant, then a few time steps are only tens of ms. In the classical conditioning experiments typical delays are of the order to hundreds of milliseconds to seconds. Authors should test if random feedback weights work as well for larger time spans. This can be done by simply using a much larger number of time steps.

In the revised manuscript, we examined the cases in which the cue-reward delay (originally 3 time steps) was elongated to 4, 5, or 6 time-steps. Our online value RNN models with random feedback could still achieve better performance (smaller squared value error) than the models with untrained RNN, although the performance degraded as the cue-reward delay increased. We have added these results in Fig. 2M and Line 223-228 (for our original models without non-negative constraint)

“We further examined the cases with longer cue-reward delays. As shown in Fig. 2M, as the delay increased, the mean squared error of state values (at 3000-th trial) increased, but the relative superiority of oVRNNbp and oVRNNrf over the model with untrained RNN remained to hold, except for cases with small number of RNN units (5) and long delay (5 or 6) (p < 0.0025 in Wilcoxon rank sum test for oVRNNbp or oVRNNrf vs untrained for each number of RNN units for each delay).”

and Fig. 6J and Line 422-429 (for our extended models with non-negative constraint):

“Figure 6J shows the cases with longer cue-reward delays, with default or halved learning rates. As the delay increased, the mean squared error of state values (at 3000-th trial) increased, but the relative superiority of oVRNNbp-rev and oVRNNrf-bio over the models with untrained RNN remained to hold, except for a few cases with 5 RNN units (5 delay oVRNNrf-bio vs shuffled with default learning rate, 6 delay oVRNNrf-bio vs naive or shuffled with halved learning rate) (p < 0.047 in Wilcoxon rank sum test for oVRNNbp-rev or oVRNNrf-bio vs naive or shuffled untrained for each number of RNN units for each delay).”

Also, we have added the note about our assumption and consideration on the time-step that we described in our provisional reply in Line 136-142:

“We assumed that a single RNN unit corresponds to a small population of neurons that intrinsically share inputs and outputs, for genetic or developmental reasons, and the activity of each unit represents the (relative) firing rate of the population. Cortical population activity is suggested to be sustained not only by fast synaptic transmission and spiking but also, even predominantly, by slower synaptic neurochemical dynamics [46] such as short-term facilitation, whose time constant can be around 500 milliseconds [47]. Therefore, we assumed that single time-step of our rate-based (rather than spike-based) model corresponds to 500 milliseconds.”

Pub3. In the section with more biologically constrained learning rules, while the output weights are restricted to only be positive (as well as the random feedback weights), the recurrent weights and weights from input to RNN are still bi-polar and can change signs during learning. Why is the constraint imposed only on the output weights? It seems reasonable that the whole setup will fail if the recurrent weights were only positive as in such a case most neurons will have very similar dynamics, and the network dimensionality would be very low. However, it is possible that only negative weights might work. It is unclear to me how to justify that bipolar weights that change sign are appropriate for the recurrent connections and inappropriate for the output connections. On the other hand, an RNN with excitatory and inhibitory neurons in which weight signs do not change could possibly work.

We examined extended models that incorporated inhibitory and excitatory units and followed Dale's law with certain assumptions, and found that these models could still learn the tasks. We have added these results in Fig. 9 and subsection “4.1 Models with excitatory and inhibitory units” and described the details of the extended models in Line 844-862:

Pub4. Like most papers in the field this work assumes a world composed of a single cue. In the real world there many more cues than rewards, some cues are not associated with any rewards, and some are associated with other rewards or even punishments. In the simplest case, it would be useful to show that this network could actually work if there are additional distractor cues that appear at random either before the CS, or between the CS and US. There are good reasons to believe such distractor cues will be fatal for an untrained RNN, but might work with a trained RNN, either using BPPT or random feedback. Although this assumption is a common flaw in most work in the field, we should no longer ignore these slightly more realistic scenarios.

We examined the performance of the models in a task in which distractor cue randomly appeared. As a result, our model with random feedback, as well as the model with backprop, could still learn the state values much better than the models with untrained RNN. We have added these results in Fig. 10 and subsection “4.2 Task with distractor cue”

Reviewer #1 (Recommendations for the authors):

Detailed comments to authors

Rec1. Are the untrained RNNs discussed in methods? It seems quite good in estimating value but has a strong dopamine response at time of reward. Is nothing trained in the untrained RNN or are the W values trained. Untrained RNN are not bad at estimating value, but not as good as the two other options. It would seem reasonable that an untrained RNN (if I understand what it is) will be sufficient for such simple Pavlovian conditioning paradigms. This is provided that the RNN generates a complete, or nearly complete basis. Random RNN's provided that the random weights are chosen properly can indeed generate a nearly complete basis. Once there is a nearly complete temporal basis, it seems that a powerful enough learning rule will be able to learn the very simple Pavlovian conditioning. Since there are only 3 time-steps from cue to reward, an RNN dimensionality of 3 would be sufficient. A failure to get a good approximation can also arise from the failure of the learning algorithm for the output weights (W).

As we mentioned in our reply to your public comment Pub1 (page 3-5), we have added an explanation of "untrained RNN" (in which the value weights were still learnt) (Line 144-147). We also analyzed the dimensionality of network dynamics by calculating the contribution ratios of principal components of the trajectory of RNN activities, showing that the contribution ratios of later principal components were smaller in the cases with untrained RNN than in the cases with trained value RNN (Fig. 2K/Line 210-220, Fig.6H/Line 412-416). Moreover, also as we mentioned in our reply to your public comment Pub1, we have added a note that even learning of a small number of states was not trivially easy because we considered continuous learning across trials rather than episodic learning of separate trials and thus it was not trivial for the model to know that cue presentation in different trials after random lengths of inter-trial interval should still be regarded as a same single state (Line 177-185).

Rec2. For all cases, it will be useful to estimate the dimensionality of the RNN. Is the dimensionality of the untrained RNN smaller than in the trained cases? If this is the case, this might depend on the choice of the initial random (I assume) recurrent connectivity matrix.

As mentioned above, we have analyzed the dimensionality of the network dynamics, and as you said, the dimensionality of the model with untrained RNN (which was indeed the initial random matrix as you said, as we mentioned above) was on average smaller than the trained value RNN models (Fig. 2K/Line 210-220, Fig.6H/Line 412-416).

Rec3. It is surprising that the error starts increasing for more RNN units above ~15. See discussion. This might indicate a failure to adjust the learning parameters of the network rather than a true and interesting finding.

Thank you very much for this insightful comment. In the original manuscript, we set the learning rate to a fixed value (0.1), without normalization by the squared norm of feature vector (as we mentioned in Line 656-7 of the original manuscript) because we thought such a normalization could not be locally (biologically) implemented. However, we have realized that the lack of normalization resulted in excessively large learning rate when the number of RNN units was large and it could cause instability and error increase as you suggested. Therefore, in the revised manuscript, we have implemented a normalization of learning rate (of value weights) that does not require non-local computations, specifically, division by the number of RNN units. As a result, the error now monotonically decreased, as the number of RNN units increased, in the non-negatively constrained models (Fig. 6E-left) and also largely in the unconstrained model with random feedback, although still not in the unconstrained model with backprop or untrained RNN (Fig. 2J-left)

Rec4. Not numbering equations is a problem. For example, the explanations of feedback alignment (lines 194-206) rely on equations in the methods section which are not numbered. This makes it hard to read these explanations. Indeed, it will also be better to include a detailed derivation of the explanation in these lines in a mathematical appendix. Key equations should be numbered.

We have added numbers to key equations in the Methods, and references to the numbers of corresponding equations in the main text. Detailed derivations are included in the Methods.

Rec5. What is shown in Figure 3C? - an equation will help.

We have added an explanation using equations in the main text (Line 256-259).

Rec6. The explanation of why alignment occurs is not satisfactory, but neither is it in previous work on feedforward networks. The least that should be done though

Regarding why alignment occurs, what remained mysterious (to us) was that in the case of nonnegatively constrained model, while the angle between value weight vector (w) and the random feedback vector (c) was relatively close (loosely aligned) from the beginning, it appeared (as mentioned in the manuscript) that there was no further alignment over trials, despite that the same mechanism for feedback alignment that we derived for the model without non-negative constraint was expected to operate also under the non-negative constraint. We have now clarified the reason for this, and found a way, introduction of slight decay (forgetting) of value weights, by which feedback alignment came to occur in the non-negatively constraint model. We have added these in the revised manuscript (Line 463-477):

“As mentioned above, while the angle between w and c was on average smaller than 90° from the beginning, there was no further alignment over trials. This seemed mysterious because the mechanism for feedback alignment that we derived for the models without non-negative constraint was expected to work also for the models with non-negative constraint. As a possible reason for the non-occurrence of feedback alignment, we guessed that one or a few element(s) of w grew prominently during learning, and so w became close to an edge or boundary of the non-negative quadrant and thereby angle between w and other vector became generally large (as illustrated in Fig. 8D). Figure 8Ea shows the mean±SEM of the elements of w ordered from the largest to smallest ones after 1500 trials. As conjectured above, a few elements indeed grew prominently.

We considered that if a slight decay (forgetting) of value weights (c.f., [59-61]) was assumed, such a prominent growth of a few elements of w may be mitigated and alignment of w to c, beyond the initial loose alignment because of the non-negative constraint, may occur. These conjectures were indeed confirmed by simulations (Fig. 8Eb,c and Fig. 8F). The mean squared value error slightly increased when the value-weightdecay was assumed (Fig. 8G), however, presumably reflecting a decrease in developed values and a deterioration of learning because of the decay.”

Rec7. I don't understand the qualitative difference between 4G and 4H. The difference seems to be smaller but there is still an apparent difference. Can this be quantified?

We have added pointers indicating which were compared and statistical significance on Fig. 4D-H, and also Fig. 7 and Fig. 9C.

Rec8. More biologically realistic constraints.

Are the weights allowed to become negative? - No.

Figure 6C - untrained RNN with non-negative x_i. Again - it was not explained what untrained RNN is. However, given my previous assumption, this is probably because the units developed in an untrained RNN is much further from representing a complete basis function. This cannot be done with only positive values. It would be useful to see network dynamics of units for untrained RNN. It might also be useful in all cases to estimate the dimensionality of the RNN. For 3 time-steps, it needs to be at least 3, and for more time steps as in Figure 4, larger.

As we mentioned in our reply to your public comment Pub3 (page 6-8), in the revised manuscript we examined models that incorporated inhibitory and excitatory units and followed Dale's law, which could still learn the tasks (Fig. 9, Line 479-520). We have also analyzed the dimensionality of network dynamics as we mentioned in our replies to your public comment Pub1 and recommendations Rec1 and Rec2.

Rec9. A new type of untrained RNN is introduced (Fig 6D) this is the first time an explanation of of the untrained RNN is given. Indeed, the dimensionality of the second type of untrained RNN should be similar to the bioVRNNrf. The results are still not good.

In the model with the new type of untrained RNN whose elements were shuffled from trained bioVRNNrf, contribution ratios of later principal components of the trajectory of RNN activities (Fig. 6H gray dotted line) were indeed larger than those in the model with native untrained RNN (gray solid line) but still much smaller than those in the trained value RNN models with backprop (red line) or random feedback (blue line). It is considered that in value RNN, RNN connections were trained to realize high-dimensional trajectory, and shuffling did not generally preserve such an ability.

Rec10. The discussion is too long and verbose. This is not a review paper.

We have made the original discussion much more compact (from 1686 words to 940 words). We have added new discussion, in response to the review comments, but the total length remains to be shorter than before (1589 words).

Reviewer #2 (Public review):

Summary:

Tsurumi et al. show that recurrent neural networks can learn state and value representations in simple reinforcement learning tasks when trained with random feedback weights. The traditional method of learning for recurrent network in such tasks (backpropagation through time) requires feedback weights which are a transposed copy of the feed-forward weights, a biologically implausible assumption. This manuscript builds on previous work regarding "random feedback alignment" and "value-RNNs", and extends them to a reinforcement learning context. The authors also demonstrate that certain nonnegative constraints can enforce a "loose alignment" of feedback weights. The author's results suggest that random feedback may be a powerful tool of learning in biological networks, even in reinforcement learning tasks.

Strengths:

The authors describe well the issues regarding biologically plausible learning in recurrent networks and in reinforcement learning tasks. They take care to propose networks which might be implemented in biological systems and compare their proposed learning rules to those already existing in literature. Further, they use small networks on relatively simple tasks, which allows for easier intuition into the learning dynamics.

Weaknesses:

The principles discovered by the authors in these smaller networks are not applied to deeper networks or more complicated tasks, so it remains unclear to what degree these methods can scale up, or can be used more generally.

We have examined extended models that incorporated inhibitory and excitatory units and followed Dale's law with certain assumptions, and found that these models could still learn the tasks. We have added these results in Fig. 9 and subsection “4.1 Models with excitatory and inhibitory units”.

We have also examined the performance of the models in a task in which distractor cue randomly appeared, finding that our models could still learn the state values much better than the models with untrained RNN. We have added these result in Fig. 10 and subsection “4.2 Task with distractor cue”.

Regarding the depth, we continue to think about it but have not yet come up with concrete ideas.

Reviewer #2 (Recommendations for the authors):

(1) I think the work would greatly benefit from more proofreading. There are language errors/oddities throughout the paper, I will list just a few examples from the introduction:

Thank you for pointing this out. We have made revisions throughout the paper.

line 63: "simultaneously learnt in the downstream of RNN". Simultaneously learnt in networks downstream of the RNN? Simulatenously learn in a downstream RNN? The meaning is not clear in the original sentence.

We have revised it to "simultaneously learnt in connections downstream of the RNN" (Line 67-68).

starting in line 65: " A major problem, among others.... value-encoding unit" is a run-on sentence and would more readable if split into multiple sentences.

We have extensively revised this part, which now consists of short sentences (Line 70-75).

line 77: "in supervised learning of feed-forward network" should be either "in supervised learning of a feed-forward network" or "in supervised learning of feed-forward networks".

We have changed "feed-forward network" to "feed-forward networks" (Line 83).

(2) Under what conditions can you use an online learning rule which only considers the influence of the previous timestep? It's not clear to me how your networks solve the temporal credit assignment problem when the cue-reward delay in your tasks is 3-5ish time steps. How far can you stretch this delay before your networks stop learning correctly because of this one-step assumption? Further, how much does feedback alignment constrain your ability to learn long timescales, such as in Murray, J.M. (2019)?

The reason why our models can solve the temporal credit assignment problem at least to a certain extent is considered to be because temporal-difference (TD) learning, which we adopted, itself has a power to resolve temporal credit assignment, as exemplified in that TD(0) algorithms without eligibility trance can still learn the value of distant rewards. We have added a discussion on this in Line 702-705:

“…our models do not have "eligibility trace" (nor memorable/gated unit, different from the original value-RNN [26]), but could still solve temporal credit assignment to a certain extent because TD learning is by itself a solution for it (notably, recent work showed that combination of TD(0) and model-based RL well explained rat's choice and DA patterns [132]).”

We have also examined the cases in which the cue-reward delay (originally 3 time steps) was elongated to 4, 5, or 6 time-steps, and our models with random feedback could still achieve better performance than the models with untrained RNN although the performance degraded as the cue-reward delay increased. We have added these results in Fig. 2M and Line 223-228 (for our original models without non-negative constraint)

“We further examined the cases with longer cue-reward delays. As shown in Fig. 2M, as the delay increased, the mean squared error of state values (at 3000-th trial) increased, but the relative superiority of oVRNNbp and oVRNNrf over the model with untrained RNN remained to hold, except for cases with small number of RNN units (5) and long delay (5 or 6) (p < 0.0025 in Wilcoxon rank sum test for oVRNNbp or oVRNNrf vs untrained for each number of RNN units for each delay).”

and Fig. 6J and Line 422-429 (for our extended models with non-negative constraint):

“Figure 6J shows the cases with longer cue-reward delays, with default or halved learning rates. As the delay increased, the mean squared error of state values (at 3000-th trial) increased, but the relative superiority of oVRNNbp-rev and oVRNNrf-bio over the models with untrained RNN remained to hold, except for a few cases with 5 RNN units (5 delay oVRNNrf-bio vs shuffled with default learning rate, 6 delay oVRNNrf-bio vs naive or shuffled with halved learning rate) (p < 0.047 in Wilcoxon rank sum test for oVRNNbp-rev or oVRNNrf-bio vs naive or shuffled untrained for each number of RNN units for each delay).”

As for the difficulty due to random feedback compared to backprop, there appeared to be little difference in the models without non-negative constraint (Fig. 2M), whereas in the models with nonnegative constraint, when the cue-reward delay was elongated to 6 time-steps, the model with random feedback performed worse than the model with backprop (Fig. 6J bottom-left panel).

(3) Line 150: Were the RNN methods trained with continuation between trials?

Yes, we have added

“The oVRNN models, and the model with untrained RNN, were continuously trained across trials in each task, because we considered that it was ecologically more plausible than episodic training of separate trials.” in Line 147-150. This is considered to make learning of even the simple cue-reward association task nontrivial, as we describe in our reply to your comment 9 below.

(4) Figure 2I, J: indicate the statistical significance of the difference between the three methods for each of these measures.

We have added statistical information for Fig. 2J (Line 198-203):

“As shown in the left panel of Fig. 2J, on average across simulations, oVRNNbp and oVRNNrf exhibited largely comparable performance and always outperformed the untrained RNN (p < 0.00022 in Wilcoxon rank sum test for oVRNNbp or oVRNNrf vs untrained for each number of RNN units), although oVRNNbp somewhat outperformed or underperformed oVRNNrf when the number of RNN units was small (≤10 (p < 0.049)) or large (≥25 (p < 0.045)), respectively.”

and also Fig. 6E (for non-negative models) (Line 385-390):

“As shown in the left panel of Fig. 6E, oVRNNbp-rev and oVRNNrf-bio exhibited largely comparable performance and always outperformed the models with untrained RNN (p < 2.5×10⁻¹² in Wilcoxon rank sum test for oVRNNbp-rev or oVRNNrf-bio vs naive or shuffled untrained for each number of RNN units), although oVRNNbp-rev somewhat outperformed or underperformed oVRNNrf-bio when the number of RNN units was small (≤10 (p < 0.00029)) or large (≥25 (p < 3.7×10⁻⁶)), respectively…”

Fig. 2I shows distributions, whose means are plotted in Fig. 2J, and we did not add statistics to Fig. 2I itself.

(5) Line 178: Has learning reached a steady state after 1000 trials for each of these networks? Can you show a plot of error vs. trial number?

We have added a plot of error vs trial number for original models (Fig. 2L, Line 221-223):

“We examined how learning proceeded across trials in the models with 20 RNN units. As shown in Fig. 2L, learning became largely converged by 1000-th trial, although slight improvement continued afterward.”

and non-negatively constrained models (Fig. 6I, Line 417-422):

“Figure 6I shows how learning proceeded across trials in the models with 20 RNN units. While oVRNNbp-rev and oVRNNrf-bio eventually reached a comparable level of errors, oVRNNrf-bio outperformed oVRNNbp-rev in early trials (at 200, 300, 400, or 500 trials; p < 0.049 in Wilcoxon rank sum test for each). This is presumably because the value weights did not develop well in early trials and so the backprop-type feedback, which was the same as the value weights, did not work well, while the non-negative fixed random feedback worked finely from the beginning.”

As shown in these figures, learning became largely steady at 1000 trials, but still slightly continued, and we have added simulations with 3000 trials (Fig. 2M and Fig. 6J).

(6) Line 191: Put these regression values in the figure caption, as well as on the plot in Figure 3B.

We have added the regression values in Fig. 3B and its caption.

(7) Line 199: This idea of being in the same quadrant is interesting, but I think the term "relatively close angle" is too vague. Is there another more quantatative way to describe this what you mean by this?

We have revised this (Line 252-254) to “a vector that is in a relatively close angle with c , or more specifically, is in the same quadrant as (and thus within at maximum 90° from) c (for example, [c₁  c₂  c₃]^T and [0.5c₁ 1.2c₂ 0.8c₃]T) “

(8) Line 275: I'd like to see this measure directly in a plot, along with the statistical significance.

We have added pointers indicating which were compared and statistical significance on Fig. 4D-H, and also Fig. 7 and Fig. 9C.

(9) Line 280: Surely the untrained RNN should be able to solve the task if the reservoir is big enough, no? Maybe much bigger than 50 units, but still.

We think this is not sure. A difficulty lies in that because we modeled the tasks in a continuous way rather than in an episodic way (as we mentioned in our reply to your comment 3), the activity of untrained RNN upon cue presentation should generally differ from trial to trial. Therefore, it was not trivial for RNN to know that cue presentation in different trials, even after random lengths of inter-trial interval, should constitute a same single state. We have added this note in Line 177-185:

“This inferiority of untrained RNN may sound odd because there were only four states from cue to reward while random RNN with enough units is expected to be able to represent many different states (c.f., [49]) and the effectiveness of training of only the readout weights has been shown in reservoir computing studies [50-53]. However, there was a difficulty stemming from the continuous training across trials (rather than episodic training of separate trials): the activity of untrained RNN upon cue presentation generally differed from trial to trial, and so it is non-trivial that cue presentation in different trials should be regarded as the same single state, even if it could eventually be dealt with at the readout level if the number of units increases.”

The original value RNN study (Hennig et al., 2023, PLoS Comput Biol) also modeled tasks in a continuous way (though using BPTT for training) and their model with untrained RNN also showed considerably larger RPE error than the value RNN even when the number of RNN units was 100 (the maximum number plotted in their Fig. 6A).

(10) It's a bit confusing to compare Figure 4C to Figure 4D-H because there are also many features of D-H which do not match those of C (response to cue, response to late reward in task 1). It would make sense to address this in some way. Is there another way to calculate the true values of the states (e.g., maybe you only start from the time of the cue) which better approximates what the networks are doing?

As we mentioned in our replies to your comments 3 and 9, our models with RNN were trained continuously across trials rather than separately for each episodic trial, and whether the models could still learn the state representation is a key issue. Therefore, starting learning from the time of cue would not be an appropriate way to compare the models, and instead we have made statistical comparison regarding key features, specifically, TD-RPEs at early and late rewards, as indicated in Fig. 4D-H.

(11) Line 309: Can you explain why this non-monotic feature exists? Why do you believe it would be more biologically plausible to assume monotonic dependence? It doesn't seem so straightforward to me, I can imagine that competing LTP/LTD mechanisms may produce plasticity which would have a non-monotic dependence on post-synaptic activity.

Thank you for this insightful comment. As you suggested, non-monotonic dependence on the postsynaptic activity (BCM rule) has been proposed for unsupervised learning (cortical self-organization) (Bienenstock et al., 1982 J Neurosci), and there were suggestions that triplet-based STDP could be reduced to a BCM-like rule and additional components (Gjorgjieva et al., 2011 PNAS; Shouval, 2011 PNAS). However, the non-monotonicity appeared in our model, derived from the backprop rule, is maximized at the middle and thus opposite from the BCM rule, which is minimized at the middle (i.e., initially decrease and thereafter increase). Therefore we consider that such an increase-then-decreasetype non-monotonicity would be less plausible than a monotonic increase, which could approximate an extreme case (with a minimum dip) of the BCM rule. We have added a note on this point in Line 355-358:

“…the dependence on the post-synaptic activity was non-monotonic, maximized at the middle of the range of activity. It would be more biologically plausible to assume a monotonic increase (while an opposite shape of nonmonotonicity, once decrease and thereafter increase, called the BCM (Bienenstock-Cooper-Munro) rule has actually been suggested [56-58]).”

(12) Line 363: This is the most exciting part of the paper (for me). I want to learn way more about this! Don't hide this in a few sentences. I want to know all about loose vs. feedback alignment. Show visualizations in 3D space of the idea of loose alignment (starting in the same quadrant), and compare it to how feedback alignment develops (ending in the same quadrant). Does this "loose" alignment idea give us an idea why the random feedback seems to settle at 45 degree angle? it just needs to get the signs right (same quadrant) for each element?

In reply to this encouraging comment, we have made further analyses of the loose alignment. By the term "loose alignment", we meant that the value weight vector w and the feedback vector c are in the same (non-negative) quadrant, as you said. But what remained mysterious (to us) was while the angle between w and c was relatively close (loosely aligned) from the beginning, it appeared (as mentioned in the manuscript) that there was no further alignment over trials (and the angle actually settled at somewhat larger than 45°), despite that the same mechanism for feedback alignment that we derived for the model without non-negative constraint was expected to operate also under the nonnegative constraint. We have now clarified the reason for this, and found a way, introduction of slight decay (forgetting) of value weights, by which feedback alignment came to occur in the non-negatively constraint model. We have added this in Line 463-477:

“As mentioned above, while the angle between w and c was on average smaller than 90° from the beginning, there was no further alignment over trials. This seemed mysterious because the mechanism for feedback alignment that we derived for the models without non-negative constraint was expected to work also for the models with non-negative constraint. As a possible reason for the non-occurrence of feedback alignment, we guessed that one or a few element(s) of w grew prominently during learning, and so w became close to an edge or boundary of the non-negative quadrant and thereby angle between w and other vector became generally large (as illustrated in Fig. 8D). Figure 8Ea shows the mean±SEM of the elements of w ordered from the largest to smallest ones after 1500 trials. As conjectured above, a few elements indeed grew prominently.

We considered that if a slight decay (forgetting) of value weights (c.f., [59-61]) was assumed, such a prominent growth of a few elements of w may be mitigated and alignment of w to c, beyond the initial loose alignment because of the non-negative constraint, may occur. These conjectures were indeed confirmed by simulations (Fig. 8Eb,c and Fig. 8F). The mean squared value error slightly increased when the value-weightdecay was assumed (Fig. 8G), however, presumably reflecting a decrease in developed values and a deterioration of learning because of the decay.”

As for visualization, because the model's dimension was high such as 12, we could not come up with better ways of visualization than the trial versus angle plot (Fig. 3A, 8A,F). Nevertheless, we would expect that the abovementioned additional analyses of loose alignment (with graphs) are useful to understand what are going on.

(13) Line 426: how does this compare to some of the reward modulated hebbian rules proposed in other RNNs? See Hoerzer, G. M., Legenstein, R., & Maass, W. (2014). Put another way, you arrived at this from a top-down approach (gradient descent->BP->approximated by RF->non-negativity constraint>leads to DA dependent modulation of Hebbian plasticity). How might this compare to a bottom up approach (i.e. starting from the principle of Hebbian learning, and adding in reward modulation)

The study of Hoerzer et al. 2014 used a stochastic perturbation, which we did not assume but can potentially be integrated. On the other hand, Hoerzer et al. trained the readout of untrained RNN, whereas we trained both RNN and its readout. We have added discussion to compare our model with Hoerzer et al. and other works that also used perturbation methods, as well as other top-down approximation method, in Line 685-711 (reference 128 is Hoerzer et al. 2014 Cereb Cortex):

“As an alternative to backprop in hierarchical network, aside from feedback alignment [36], Associative Reward-Penalty (A_R-P) algorithm has been proposed [124-126]. In A_R-P, the hidden units behave stochastically, allowing the gradient to be estimated via stochastic sampling. Recent work [127] has proposed Phaseless Alignment Learning (PAL), in which high-frequency noise-induced learning of feedback projections proceeds simultaneously with learning of forward projections using the feedback in a lower frequency. Noise-induced learning of the weights on readout neurons from untrained RNN by reward-modulated Hebbian plasticity has also been demonstrated [128]. Such noise- or perturbation-based [40] mechanisms are biologically plausible because neurons and neural networks can exhibit noisy or chaotic behavior [129-131], and might improve the performance of value-RNN if implemented.

Regarding learning of RNN, "e-prop" [35] was proposed as a locally learnable online approximation of BPTT [27], which was used in the original value RNN 26. In e-prop, neuron-specific learning signal is combined with weight-specific locally-updatable "eligibility trace". Reward-based e-prop was also shown to work [35], both in a setup not introducing TD-RPE with symmetric or random feedback (their Supplementary Figure 5) and in another setup introducing TD-RPE with symmetric feedback (their Figure 4 and 5). Compared to these, our models differ in multiple ways.

First, we have shown that alignment to random feedback occurs in the models driven by TD-RPE. Second, our models do not have "eligibility trace" (nor memorable/gated unit, different from the original valueRNN [26]), but could still solve temporal credit assignment to a certain extent because TD learning is by itself a solution for it (notably, recent work showed that combination of TD(0) and model-based RL well explained rat's choice and DA patterns [132]). However, as mentioned before, single time-step in our models was assumed to correspond to hundreds of milliseconds, incorporating slow synaptic dynamics, whereas e-prop is an algorithm for spiking neuron models with a much finer time scale. From this aspect, our models could be seen as a coarsetime-scale approximation of e-prop. On top of these, our results point to a potential computational benefit of biological non-negative constraint, which could effectively limit the parameter space and promote learning.”

Related to your latter point (and also replying to other reviewer's comment), we also examined the cases where the random feedback in our model was replaced with uniform feedback, which corresponds to a simple bottom-up reward-modulated triplet plasticity rule. As a result, the model with uniform feedback showed largely comparable, but somewhat worse, performance than the model with random feedback. We have added the results in Fig. 2J-right and Line 206-209 (for our original models without non-negative constraint):

“The green line in Fig. 2J-right shows the performance of a special case where the random feedback in oVRNNrf was fixed to the direction of (1, 1, ..., 1)^T (i.e., uniform feedback) with a random coefficient, which was largely comparable to, but somewhat worse than, that for the general oVRNNrf (blue line).”

and Fig. 6E-right and Line 402-407 (for our extended models with non-negative constraint):

“The green and light blue lines in the right panels of Figure 6E and Figure 6F show the results for special cases where the random feedback in oVRNNrf-bio was fixed to the direction of (1, 1, ..., 1) ^T (i.e., uniform feedback) with a random non-negative magnitude (green line) or a fixed magnitude of 0.5 (light blue line). The performance of these special cases, especially the former (with random magnitude) was somewhat worse than that of oVRNNrf-bio, but still better than that of the models with untrained RNN. and also added a biological implication of the results in Line 644-652:

We have shown that oVRNNrf and oVRNNrf-bio could work even when the random feedback was uniform, i.e., fixed to the direction of (1, 1, ..., 1) ^T, although the performance was somewhat worse. This is reasonable because uniform feedback can still encode scalar TD-RPE that drives our models, in contrast to a previous study [45], which considered DA's encoding of vector error and thus regarded uniform feedback as a negative control. If oVRNNrf/oVRNNrf-bio-like mechanism indeed operates in the brain and the feedback is near uniform, alignment of the value weights w to near (1, 1, ..., 1) is expected to occur. This means that states are (learned to be) represented in such a way that simple summation of cortical neuronal activity approximates value, thereby potentially explaining why value is often correlated with regional activation (fMRI BOLD signal) of cortical regions [113].”

Reviewer #3 (Public review):

Summary:

The paper studies learning rules in a simple sigmoidal recurrent neural network setting. The recurrent network has a single layer of 10 to 40 units. It is first confirmed that feedback alignment (FA) can learn a value function in this setting. Then so-called bio-plausible constraints are added: (1) when value weights (readout) is non-negative, (2) when the activity is non-negative (normal sigmoid rather than downscaled between -0.5 and 0.5), (3) when the feedback weights are non-negative, (4) when the learning rule is revised to be monotic: the weights are not downregulated. In the simple task considered all four biological features do not appear to impair totally the learning.

Strengths:

(1) The learning rules are implemented in a low-level fashion of the form: (pre-synaptic-activity) x (post-synaptic-activity) x feedback x RPE. Which is therefore interpretable in terms of measurable quantities in the wet-lab.

(2) I find that non-negative FA (FA with non negative c and w) is the most valuable theoretical insight of this paper: I understand why the alignment between w and c is automatically better at initialization.

(3) The task choice is relevant since it connects with experimental settings of reward conditioning with possible plasticity measurements.

Weaknesses:

(4) The task is rather easy, so it's not clear that it really captures the computational gap that exists with FA (gradient-like learning) and simpler learning rule like a delta rule: RPE x (pre-synpatic) x (postsynaptic). To control if the task is not too trivial, I suggest adding a control where the vector c is constant c_i=1.

We have examined the cases where the feedback was uniform, i.e., in the direction of (1, 1, ..., 1) in both models without and with non-negative constraint. In both models, the models with uniform feedback performed somewhat worse than the original models with random feedback, but still better than the models with untrained RNN. We have added the results in Fig. 2J-right and Line 206-209 (for our original models without non-negative constraint):

“The green line in Fig. 2J-right shows the performance of a special case where the random feedback in oVRNNrf was fixed to the direction of (1, 1, ..., 1) ^T (i.e., uniform feedback) with a random coefficient, which was largely comparable to, but somewhat worse than, that for the general oVRNNrf (blue line).”

and Fig. 6E-right and Line 402-407 (for our extended models with non-negative constraint):

“The green and light blue lines in the right panels of Figure 6E and Figure 6F show the results for special cases where the random feedback in oVRNNrf-bio was fixed to the direction of (1, 1, ..., 1) ^T (i.e., uniform feedback) with a random non-negative magnitude (green line) or a fixed magnitude of 0.5 (light blue line). The performance of these special cases, especially the former (with random magnitude) was somewhat worse than that of oVRNNrf-bio, but still better than that of the models with untrained RNN.”

We have also added a discussion on the biological implication of the model with uniform feedback mentioned in our provisional reply in Line 644-652:

“We have shown that oVRNNrf and oVRNNrf-bio could work even when the random feedback was uniform, i.e., fixed to the direction of (1, 1, ..., 1) ^T, although the performance was somewhat worse. This is reasonable because uniform feedback can still encode scalar TD-RPE that drives our models, in contrast to a previous study [45], which considered DA's encoding of vector error and thus regarded uniform feedback as a negative control. If oVRNNrf/oVRNNrf-bio-like mechanism indeed operates in the brain and the feedback is near uniform, alignment of the value weights w to near (1, 1, ..., 1) is expected to occur. This means that states are (learned to be) represented in such a way that simple summation of cortical neuronal activity approximates value, thereby potentially explaining why value is often correlated with regional activation (fMRI BOLD signal) of cortical regions [113].”

In addition, while preparing the revised manuscript, we found a recent simulation study, which showed that uniform feedback coupled with positive forward weights was effective in supervised learning of one-dimensional output in feed-forward network (Konishi et al., 2023, Front Neurosci).

We have briefly discussed this work in Line 653-655:

“Notably, uniform feedback coupled with positive forward weights was shown to be effective also in supervised learning of one-dimensional output in feed-forward network [114], and we guess that loose alignment may underlie it.”

(5) Related to point 3), the main strength of this paper is to draw potential connection with experimental data. It would be good to highlight more concretely the prediction of the theory for experimental findings. (Ideally, what should be observed with non-negative FA that is not expected with FA or a delta rule (constant global feedback) ?).

We have added a discussion on the prediction of our models, mentioned in our provisional reply, in Line 627-638:

“oVRNNrf predicts that the feedback vector c and the value-weight vector w become gradually aligned, while oVRNNrf-bio predicts that c and w are loosely aligned from the beginning. Element of c could be measured as the magnitude of pyramidal cell's response to DA stimulation. Element of w corresponding to a given pyramidal cell could be measured, if striatal neuron that receives input from that pyramidal cell can be identified (although technically demanding), as the magnitude of response of the striatal neuron to activation of the pyramidal cell. Then, the abovementioned predictions could be tested by (i) identify cortical, striatal, and VTA regions that are connected, (ii) identify pairs of cortical pyramidal cells and striatal neurons that are connected, (iii) measure the responses of identified pyramidal cells to DA stimulation, as well as the responses of identified striatal neurons to activation of the connected pyramidal cells, and (iv) test whether DA→pyramidal responses and pyramidal→striatal responses are associated across pyramidal cells, and whether such associations develop through learning.”

Moreover, we have considered another (technically more doable) prediction of our model, and described it in Line 639-643:

“Testing this prediction, however, would be technically quite demanding, as mentioned above. An alternative way of testing our model is to manipulate the cortical DA feedback and see if it will cause (re-)alignment of value weights (i.e., cortical striatal strengths). Specifically, our model predicts that if DA projection to a particular cortical locus is silenced, effect of the activity of that locus on the value-encoding striatal activity will become diminished.”

(6a) Random feedback with RNN in RL have been studied in the past, so it is maybe worth giving some insights how the results and the analyzes compare to this previous line of work (for instance in this paper [1]). For instance, I am not very surprised that FA also works for value prediction with TD error. It is also expected from the literature that the RL + RNN + FA setting would scale to tasks that are more complex than the conditioning problem proposed here, so is there a more specific take-home message about non-negative FA? or benefits from this simpler toy task? [1] https://www.nature.com/articles/s41467-020-17236-y

As for a specific feature of non-negative models, we did not describe (actually did not well recognize) an intriguing result that the non-negative random feedback model performed generally better than the models without non-negative constraint with either backprop or random feedback (Fig. 2J-left versus Fig. 6E-left (please mind the difference in the vertical scales)). This suggests that the non-negative constraint effectively limited the parameter space and thereby learning became efficient. We have added this result in Line 392-395:

“Remarkably, oVRNNrf-bio generally achieved better performance than both oVRNNbp and oVRNNrf, which did not have the non-negative constraint (Wilcoxon rank sum test, vs oVRNNbp : p < 7.8×10,sup>−6</sup> for 5 or ≥25 RNN units; vs oVRNNrf: p < 0.021 for ≤10 or ≥20 RNN units).”

Also, in the models with non-negative constraint, the model with random feedback learned more rapidly than the model with backprop although they eventually reached a comparable level of errors, at least in the case with 20 RNN units. This is presumably because the value weights did not develop well in early trials and so the backprop-based feedback, which was the same as the value weights, did not work well, while the non-negative fixed random feedback worked finely from the beginning. We have added this result in Fig. 6I and Line 417-422:

“Figure 6I shows how learning proceeded across trials in the models with 20 RNN units. While oVRNNbp-rev and oVRNNrf-bio eventually reached a comparable level of errors, oVRNNrf-bio outperformed oVRNNbp-rev in early trials (at 200, 300, 400, or 500 trials; p < 0.049 in Wilcoxon rank sum test for each). This is presumably because the value weights did not develop well in early trials and so the backprop-type feedback, which was the same as the value weights, did not work well, while the non-negative fixed random feedback worked finely from the beginning.”

We have also added a discussion on how our model can be positioned in relation to other models including the study you mentioned (e-prop by Bellec, ..., Maass, 2020) in subsection “Comparison to other algorithms” of the Discussion):

Regarding the slightly better performance of the non-negative model with random feedback than that of the non-negative model with backprop when the number of RNN units was large (mentioned in our provisional reply), state values in the backprop model appeared underdeveloped than those in the random feedback model. Slightly better performance of random feedback than backprop held also in our extended model incorporating excitatory and inhibitory units (Fig. 9B).

(6b) Related to task complexity, it is not clear to me if non-negative value and feedback weights would generally scale to harder tasks. If the task in so simple that a global RPE signal is sufficient to learn (see 4 and 5), then it could be good to extend the task to find a substantial gap between: global RPE, non-negative FA, FA, BP. For a well chosen task, I expect to see a performance gap between any pair of these four learning rules. In the context of the present paper, this would be particularly interesting to study the failure mode of non-negative FA and the cases where it does perform as well as FA.

In the cue-reward association task with 3 time-steps delay, the non-negative model with random feedback performed largely comparably to the non-negative model with backprop, and this remained to hold in a task where distractor cue, which was not associated with reward, appeared in random timings. We have added the results in Fig. 10 and subsection “4.2 Task with distractor cue”.

We have also examined the cases where the cue-reward delay was elongated. In the case of longer cue-reward delay (6 time-steps), in the models without non-negative constraint, the model with random feedback performed comparably to (and slightly better than when the number of RNN units was large) the model with backprop (Fig. 2M). In contrast, in the models with non-negative constraint, the model with random feedback underperformed the model with backprop (Fig. 6J, left-bottom). This indicates a difference between the effect of non-negative random feedback and the effect of positive+negative random feedback.

We have further examined the performance of the models in terms of action selection, by extending the models to incorporate an actor-critic algorithm. In a task with inter-temporal choice (i.e., immediate small reward vs delayed large reward), the non-negative model with random feedback performed worse than the non-negative model with backprop when the number of RNN units was small. When the number of RNN increased, these models performed more comparably. These results are described in Fig. 11 and subsection “4.3 Incorporation of action selection”.

(7) I find that the writing could be improved, it mostly feels more technical and difficult than it should. Here are some recommendations:

7a) for instance the technical description of the task (CSC) is not fully described and requires background knowledge from other paper which is not desirable.

7b) Also the rationale for the added difficulty with the stochastic reward and new state is not well explained.

7c) In the technical description of the results I find that the text dives into descriptive comments of the figures but high-level take home messages would be helpful to guide the reader. I got a bit lost, although I feel that there is probably a lot of depth in these paragraphs.

As for 7a), 'CSC (complete serial compound)' was actually not the name of the task but the name of the 'punctate' state representation, in which each state (timing from cue) is represented in a punctate manner, i.e., by a one-hot vector such as (1, 0, ..., 0), (0, 1, ..., 0), ..., and (0, 0, ..., 1). As you pointed out, using the name of 'CSC' would make the text appearing more technical than it actually is, and so we have moved the reference to the name of 'CSC' to the Methods (Line 903-907):

“For the agents with punctate state representation, which is also referred to as the complete serial compound (CSC) representation [1, 48, 133], each timing from a cue in the tasks was represented by a 10-dimensional one-hot vector, starting from (1 0 0 ... 0)^T for the cue state, with the next state (0 1 0 ... 0) ^T and so on.”

and in the Results we have instead added a clearer explanation (Line 163-165):

“First, for comparison, we examined traditional TD-RL agent with punctate state representation (without using the RNN), in which each state (time-step from a cue) was represented in a punctate manner, i.e., by a one-hot vector such as (1, 0, ..., 0), (0, 1, ..., 0), and so on.”

As for 7b), we have added the rationale for our examination of the tasks with probabilistic structures (Line 282-294):

“Previous work [54] examined the response of DA neurons in cue-reward association tasks in which reward timing was probabilistically determined (early in some trials but late in other trials). There were two tasks, which were largely similar but there was a key difference that reward was given in all the trials in one task whereas reward was omitted in some randomly determined trials in another task. Starkweather et al. [54] found that the DA response to later reward was smaller than the response to earlier reward in the former task, presumably reflecting the animal's belief that delayed reward will surely come, but the opposite was the case in the latter task, presumably because the animal suspected that reward was omitted in that trial. Starkweather et al.[54] then showed that such response patterns could be explained if DA encoded TD-RPE under particular state representations that incorporated the probabilistic structures of the task (called the 'belief state'). In that study, such state representations were 'handcrafted' by the authors, but the subsequent work [26] showed that the original value-RNN with backprop (BPTT) could develop similar representations and reproduce the experimentally observed DA patterns.”

As for 7c), we have extensively revised the text of the results, adding high-level explanations while trying to reduce the lengthy low-level descriptions (e.g., Line 172-177 for Fig2E-G).

(8) Related to the writing issue and 5), I wished that "bio-plausibility" was not the only reason to study positive feedback and value weights. Is it possible to develop a bit more specifically what and why this positivity is interesting? Is there an expected finding with non-negative FA both in the model capability? or maybe there is a simpler and crisp take-home message to communicate the experimental predictions to the community would be useful?

There is actually an unexpected finding with non-negative model: the non-negative random feedback model performed generally better than the models without non-negative constraint with either backprop or random feedback (Fig. 2J-left versus Fig. 6E-left), presumably because the nonnegative constraint effectively limited the parameter space and thereby learning became efficient, as we mentioned in our reply to your point 6a above (we did not well recognize this at the time of original submission).

Another potential merit of our present work is the simplicity of the model and the task. This simplicity enabled us to derive an intuitive explanation on why feedback alignment could occur. Such an intuitive explanation was lacking in previous studies while more precise mathematical explanations did exist. Related to the mechanism of feedback alignment, one thing remained mysterious to us at the time of original submission. Specifically, in the non-negatively constraint random feedback model, while the angle between the value weight (w) and the random feedback (c) was relatively close (loosely aligned) from the beginning, it appeared (as mentioned in the manuscript) that there was no further alignment over trials (and the angle actually settled at somewhat larger than 45°), despite that the same mechanism for feedback alignment that we derived for the model without non-negative constraint was expected to operate also under the non-negative constraint. We have now clarified the reason for this, and found a way, introduction of slight decay (forgetting) of value weights, by which feedback alignment came to occur in the non-negatively constraint model. We have added this in Line 463-477:

“As mentioned above, while the angle between w and c was on average smaller than 90° from the beginning, there was no further alignment over trials. This seemed mysterious because the mechanism for feedback alignment that we derived for the models without non-negative constraint was expected to work also for the models with non-negative constraint. As a possible reason for the non-occurrence of feedback alignment, we guessed that one or a few element(s) of w grew prominently during learning, and so w became close to an edge or boundary of the non-negative quadrant and thereby angle between w and other vector became generally large (as illustrated in Fig. 8D). Figure 8Ea shows the mean±SEM of the elements of w ordered from the largest to smallest ones after 1500 trials. As conjectured above, a few elements indeed grew prominently.

We considered that if a slight decay (forgetting) of value weights (c.f., [59-61]) was assumed, such a prominent growth of a few elements of w may be mitigated and alignment of w to c, beyond the initial loose alignment because of the non-negative constraint, may occur. These conjectures were indeed confirmed by simulations (Fig. 8Eb,c and Fig. 8F). The mean squared value error slightly increased when the value-weightdecay was assumed (Fig. 8G), however, presumably reflecting a decrease in developed values and a deterioration of learning because of the decay.”

Correction of an error in the original manuscript

In addition to revising the manuscript according to your comments, we have made a correction on the way of estimating the true state values. Specifically, in the original manuscript, we defined states by relative time-steps from a reward and estimated their values by calculating the sums of discounted future rewards starting from them through simulations. However, we assumed variable inter-trial intervals (ITIs) (4, 5, 6, or 7 time-steps with equal probabilities), and so until receiving cue information, agent should not know when the next reward will come. Therefore, states for the timings up to the cue timing cannot be defined by the upcoming reward, but previously we did so (e.g., state of "one timestep before cue") without taking into account the ITI variability.

We have now corrected this issue, having defined the states of timings with respect to the previous (rather than upcoming) reward. For example, when ITI was 4 time-steps and agent existed in its last time-step, agent will in fact receive a cue at the next time-step, but agent should not know it until actually receiving the cue information and instead should assume that s/he was at the last time-step of ITI (if ITI was 4), last − 1 (if ITI was 5), last − 2 (if ITI was 6), or last − 3 (if ITI was 7) with equal probabilities (in a similar fashion to what we considered when thinking about state definition for the probabilistic tasks). We estimated the true values of states defined in this way through simulations. As a result, the corrected true value of the cue-timing has become slightly smaller than the value described in the original manuscript (reflecting the uncertainty about ITI length), and consequently small positive TD-RPE has now appeared at the cue timing.

Because we measured the performance of the models by squared errors in state values, this correction affected the results reporting the performance. Fortunately, the effects were relatively minor and did not largely alter the results of performance comparisons. However, we sincerely apologize for this error. In the revised manuscript, we have used the corrected true values throughout the manuscript, and we have described the ways of estimating these values in Line 919-976.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

MHC (Major Histocompatibility Complex) genes have long been mentioned as cases of trans-species polymorphism (TSP), where alleles might have their most recent common ancestor with alleles in a different species, rather than other alleles in the same species (e.g., a human MHC allele might coalesce with a chimp MHC allele, more recently than the two coalesce with other alleles in either species). This paper provides a more complete estimate of the extent and ages of TSP in primate MHC loci. The data clearly support deep TSP linking alleles in humans to (in some cases) old world monkeys, but the amount of TSP varies between loci.

Strengths:

The authors use publicly available datasets to build phylogenetic trees of MHC alleles and loci. From these trees they are able to estimate whether there is compelling support for Trans-species polymorphisms (TSPs) using Bayes Factor tests comparing different alternative hypotheses for tree shape. The phylogenetic methods are state-of-the-art and appropriate to the task.

The authors supplement their analyses of TSP with estimates of selection (e.g., dN/dS ratios) on motifs within the MHC protein. They confirm what one would suspect: classical MHC genes exhibit stronger selection at amino acid residues that are part of the peptide binding region, and non-classical MHC exhibit less evidence of selection. The selected sites are associated with various diseases in GWAS studies.

Weaknesses:

An implication drawn from this paper (and previous literature) is that MHC has atypically high rates of TSP. However, rates of TSP are not estimated for other genes or gene families, so readers have no basis of comparison. No framework to know whether the depth and frequency of TSP is unusual for MHC family genes, relative to other random genes in the genome, or immune genes in particular. I expect (from previous work on the topic), that MHC is indeed exceptional in this regard, but some direct comparison would provide greater confidence in this conclusion.

We agree that context is important! Although we expected to get the most interesting results from studying the classical genes, we did include the non-classical genes specifically for comparison. They are located in the same genomic region, have multiple sequences catalogued in different species (although they are less diverse), and perform critical immune functions. We think this is a more appropriate set to compare with the classical MHC genes than, say, a random set of genes. Interestingly, we did not detect TSP in these non-classical genes. This likely means that the classical MHC genes are truly exceptional, but it could also mean that not enough sequences are available for the non-classical genes to detect TSP. 

It would be very interesting to repeat this analysis for another gene family to see whether such deep TSP also occurs in other immune or non-immune gene families. We are lucky that decades of past work and a dedicated database exists for cataloging MHC sequences. When this level of sequence collection is achieved for other highly polymorphic gene families, it will be possible to do a comparable analysis.  

Given the companion paper's evidence of genic gain/loss, it seems like there is a real risk that the present study under-estimates TSP, if cases of TSP have been obscured by the loss of the TSP-carrying gene paralog from some lineages needed to detect the TSP. Are the present analyses simply calculating rates of TSP of observed alleles, or are you able to infer TSP rates conditional on rates of gene gain/loss?

We were not able to infer TSP rates conditional on rates of gene gain/loss. We agree that some cases of TSP were likely lost due to the loss of a gene paralog from certain species. Furthermore, the dearth of MHC whole-region and allele sequences available for most primates makes it difficult to detect TSP, even if the gene paralog is still present. Long-read sequencing of more primate genomes should help with this. We agree that it would also be very interesting to study TSPs that were maintained for millions of years but were lost recently.

Figure 5 (and 6) provide regression model fits (red lines in panel C) relating evolutionary rates (y axis not labeled) to site distance from the peptide binding groove, on the protein product. This is a nice result. I wonder, however, whether a linear model (as opposed to non-linear) is the most biologically reasonable choice, and whether non-linear functions have been evaluated. The authors might consider generalized additive models (GAMs) as an alternative that relaxes linearity assumptions.

We agree that a linear model is likely not the most biologically reasonable choice, as protein interactions are complex. However, we made the choice to implement the simplest model because the evolutionary rates we inferred were relative, making parameters relatively meaningless. We were mainly concerned with positive or negative slopes and we leave the rest to the protein interaction experts.

The connection between rapidly evolving sites, and disease associations (lines 382-3) is very interesting. However, this is not being presented as a statistical test of association. The authors note that fast-evolving amino acids all have at least one association: but is this really more disease-association than a random amino acid in the MHC? Or, a randomly chosen polymorphic amino acid in MHC? A statistical test confirming an excess of disease associations would strengthen this claim.

To strengthen this claim, we added Figure 6 - Figure Supplement 7 (NOTE: this needs to be renamed as Table 1 - Figure Supplement 1, which the eLife template does not allow). Here, we plot the number of associations for each amino acid against evolutionary rate, revealing a significant positive slope in Class I. We also added explanatory text for this figure in lines 400-404.

Reviewer #2 (Public review):

Summary

In this study, the authors characterized population genetic variation in the MHC locus across primates and looked for signals of long-term balancing selection (specifically trans-species polymorphism, TSP) in this highly polymorphic region. To carry out these tasks, they used Bayesian methods for phylogenetic inference (i.e. BEAST2) and applied a new Bayesian test to quantify evidence supporting monophyly vs. transspecies polymorphism for each exon across different species pairs. Their results, although mostly confirmatory, represent the most comprehensive analyses of primate MHC evolution to date and novel findings or possible discrepancies are clearly pointed out. However, as the authors discuss, the available data are insufficient to fully capture primates' MHC evolution.

Strengths of the paper include: using appropriate methods and statistically rigorous analyses; very clear figures and detailed description of the results methods that make it easy to follow despite the complexity of the region and approach; a clever test for TSP that is then complemented by positive selection tests and the protein structures for a quite comprehensive study.

That said, weaknesses include: lack of information about how many sequences are included and whether uneven sampling across taxa might results in some comparisons without evidence for TSP; frequent reference to the companion paper instead of summarizing (at least some of) the critical relevant information (e.g., how was orthology inferred?); no mention of the quality of sequences in the database and whether there is still potential effects of mismapping or copy number variation affecting the sequence comparison.

To address these comments, we added Tables 2-4 to allow readers to more readily understand the data we included in each group. We refer to these tables in the introduction (line 95), in the “Data” section of the results (lines 128-129), and the “Data” section of the methods (lines 532-534).  We also added text (lines 216-219 and 250-252) to more explicitly point out that our method is conservative when few sequences are available.

We also added a paragraph to the discussion which addresses data quality and mismapping issues (lines 473-499).

We clarified the role of our companion paper (line 49-50) by changing “In our companion paper, we explored the relationships between the different classical and non-classical genes” to “In our companion paper, we built large multi-gene trees to explore the relationships between the different classical and non-classical genes.” We also changed the text in lines 97-99 from “In our companion paper, we compared genes across dozens of species and learned more about the orthologous relationships among them” to “In our companion paper, we built trees to compare genes across dozens of species. When paired with previous literature, these trees helped us infer orthology and assign sequences to genes in some cases.”

Reviewer #3 (Public review):

Summary

The study uses publicly available sequences of classical and non-classical genes from a number of primate species to assess the extent and depth of TSP across the primate phylogeny. The analyses were carried out in a coherent and, in my opinion, robust inferential framework and provided evidence for ancient (even > 30 million years) TSP at several classical class I and class II genes. The authors also characterise evolutionary rates at individual codons, map these rates onto MHC protein structures, and find that the fastest evolving codons are extremely enriched for autoimmune and infectious disease associations.

Strengths

The study is comprehensive, relying on a large data set, state-of-the-art phylogenetic analyses and elegant tests of TSP. The results are not entirely novel, but a synthesis and re-analysis of previous findings is extremely valuable and timely.

Weaknesses

I've identified weaknesses in several areas (details follow in the next section):

-  Inadequate description and presentation of the data used

-  Large parts of the results read like extended figure captions, which breaks the flow. - Older literature on the subject is duly cited, but the authors don't really discuss their findings in the context of this literature.

-  The potential impact of mechanisms other than long-term maintenance of allelic lineages by balancing selection, such as interspecific introgression and incorrect orthology assessment, needs to be discussed.

We address these comments in the more detailed section below.

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors):

The abstract could benefit from being sharpened. A personal pet peeve is a common habit of saying we don't know everything about a topic (line 16 - "lack a full picture of primate MHC evolution"); We never know everything on a topic, so this is hardly a strong rationale to do more work on it. This is followed by "to start addressing this gap" - which is vague because you haven't explicitly stated any gap, you simply said we are not yet omniscent on the topic. Please clearly identify a gap in our knowledge, a question that you will be able to answer with this paper.

That makes sense! We added another sentence to the abstract to make the specific gap clearer. Inserted “In particular, we do not know to what extent genes and alleles are retained across speciation events” in lines 16-17.

Reviewer #2 (Recommendations for the authors):

- Some discussion of alternative explanations when certain comparisons were not found to have TSP - is this consistent with genetic drift sometimes leading to lineage loss, or does it suggest that the proposed tradeoff between autoimmunity and pathogen recognition might differ depending on primates' life history and/or exposure to similar pathogens? Could the trade-off of pathogen to self-recognition not be as costly in some species?

This is consistent with genetic drift, as no lineages are expected to be maintained across these distantly-diverged primates under neutral selection. These ideas are certainly possible, but our Bayes Factor test only reveals evidence (or lack thereof) for deviations from the species tree and cannot provide reasons why or why not.

- It would be interesting to put these results on very long-term balancing selection in the context of what has been reported at the region for shorter term balancing selection. The discussion compares findings of previous genes in the literature but not regarding the time scale.

Indeed, there is some evidence for the idea of “divergent allele advantage”, in which MHC-heterozygous individuals have a greater repertoire of peptides that they can present, leading to greater resistance against pathogens and greater fitness. This heterozygote advantage thus leads to balancing selection (Pierini and Lenz, 2018; Chowell et al., 2019). Our discussion mentions other time scales of balancing selection across the primates at the MHC and other loci, but we choose to focus more on long-term than short-term balancing selection.

- Lines 223-226 - how is the difference in BF across exons in MHC-A to be interpreted? The paragraph is about MHC-A, but then the explanation in the last sentence is for when similar BF are observed which is not the case for MHC-A. Is this interpreted as lack of evidence for TSP? Or something about recombination or gene conversion? Or that one exon may be under balancing selection but not the other?

Thank you for pointing out the confusing logic in this paragraph. 

Previous: “For MHC-A, Bayes factors vary considerably depending on exon and species pair. Many sequences had to be excluded from MHC-A comparisons because they were identified as gene-converted in the \textit{GENECONV} analysis or were previously identified as recombinants \citep{Hans2017,Gleimer2011,Adams2001}. Importantly, for MHC-A we do not see concordance in Bayes factors across the different exons, whereas we do for the other gene groups. Similar Bayes factors across all exons for a given comparison is thus evidence in favor of TSP being the primary driver of the observed deep coalescence structure (rather than recombination or gene conversion).” Current (lines 228-238): 

“For MHC-A, Bayes factors vary considerably depending on exon and species pair. Past work suggests that this gene has had a long history of gene conversion affecting different exons, resulting in different evolutionary histories for different parts of the gene \citep{Hans2017,Gleimer2011,Adams2001}. Indeed, we excluded many MHC-A sequences from our Bayes factor calculations because they were identified as gene-converted in our \textit{GENECONV} analysis or were previously suggested to be recombinants. As shown in \FIG{bayes_factors_classI}, the lack of concordance in Bayes factors across the different exons for MHC-A is evidence for gene conversion, rather than balancing selection, being the most important factor in this gene's evolution. In contrast, the other gene groups generally show concordance in Bayes factors across exons. We interpret this as evidence in favor of TSP being the primary driver of the observed deep coalescence structure for MHC-B and -C (rather than recombination or gene conversion).”

- In Figures 5C and 6C, the points sometimes show a kind of smile pattern of possibly higher rates further from the peptide. Did authors explore other fits like a polynomial? Or, whether distance only matters in close proximity to the peptide? Out of curiosity, is it possible to map substitution time/branch into the distance to the peptide binding region for each substitution? Is there any pattern with distance to interacting proteins in non-peptide binding MHC proteins like MHC-DOA? Although they don't have a PBR they do interact with other proteins.

Thank you for these ideas! We did not explore other fits, such as a polynomial, because we wanted to implement the simplest model. Our evolutionary rates are relative, making parameters relatively meaningless. We were mainly concerned with positive or negative slopes and we leave the rest to the protein interaction experts.

There is most likely a relationship between evolutionary rate and the distance to interacting proteins in the non-peptide-binding molecules MHC-DM and -DO. However, there are few currently available models and it is difficult to determine which residues in these models are actually interacting. However, researchers with more experience in protein interactions would be able to undertake such an analysis. 

- How biased is the database towards human alleles? Could this affect some of the analyses, including the coincidence of rapidly evolving sites with associations? Are there more associations than expected under some null model?

While the database is indeed biased toward human alleles, we included only a small subset of these in order to create a more balanced data set spanning the primates. This is unlikely to affect the coincidence of rapidly-evolving sites with associations; however, we note that there are no such association studies meeting our criteria in other species, meaning the associations are only coming from studies on humans.

- To this reader, it is unnecessary and distracting to describe the figures within the text; there are frequent sentences in the text that belongs in the figure legend instead (e.g., lines 139-143, 208-211, 214-215, 328-330, etc). It would be better to focus on the results from the figures and then cite the figure, where the colors and exactly what is plotted can be in the figure legend.

We appreciate these comments on overall flow. We removed lines 139-143 and lengthened the Figure 2 caption (and associated supplementary figure captions) to contain all necessary detail. We removed lines 208-211 and 214-215 and lengthened the captions for Figure 3, Figure 4, and associated supplementary figures. We removed a sentence from lines 303-304.  

- I'm still concerned that the poor mappability of short-read data is contributing in some ways. Were the sequences in the database mostly from long-reads? Was nucleotide diversity calculated directly from the sequences in the database or from another human dataset? Is missing data at some sites accounted for in the denominator?

The sequences in the database are mostly from short reads and come from a wide array of labs. We have added a paragraph to the discussion to explain the limitations of this (lines 473-499). However, the nucleotide diversity calculations shown in Figure 1 do not rely on the MHC database; rather, they are calculated from the human genomes in the 1000 Genomes project. Nucleotide diversity would be calculable for other species, but we did not do so for exactly the reason you mention–too much missing data.

- The Figure 2 and Figure 3 supplements took me a little bit to understand - is it really worth pointing out the top 5 Bayes-factor comparisons when there is no evidence for TSP? A lot of the colored squares are not actually supporting TSP but in the grids you can't see which are and which aren't without looking at the Bayes Factor. I wonder if it would help if only those with BF > 100 were shown? Or if these were marked some other way so that it was easy to see where TSPs are supported.

Thank you for your perspective on these figures! We initially limited them to only show >100 Bayes factors for each gene group and region, but some gene groups have no high Bayes factors. Additionally, the “summary” tree pictured in these figures is necessarily a simplification of the full space of posterior trees. We felt that showing low Bayes factor comparisons could help readers understand this relationship. For example, allele sets that look non-monophyletic on the summary tree may still have a low Bayes factor, showing that they are generally monophyletic throughout the larger (un-visualizable) space of trees.

Reviewer #3 (Recommendations for the authors):

Specific comments

Abstract

I think the abstract would benefit from some editing. For example, one might get the impression that you equate allele sharing, which would normally be understood as sharing identical sequences, with sharing ancestral allelic lineages. This distinction is important because you can have many TSPs without sharing identical allele sequences. In l. 20 you write about "deep TSP", which requires either definition of reformulation. In l. 21-23 you seem to suggest that long-term retention of allelic lineages is surprising in the light of rapid sequence evolution - it may be, depending on the evolutionary scenarios one is willing to accept, but perhaps it's not necessary to float such a suggestion in the abstract where it cannot be properly explained due to space constraints? The last sequence needs a qualifier like "in some cases".

Thank you for catching these! For clarity, we changed several words:

● “alleles” to “allelic lineages” in line 13

● “deep” to “ancient” in line 21

● “Despite” to “in addition to” in line 22

● Added “in some cases” to line 28

Results - Overall, parts of the results read like extended figure captions. I understand that the authors want to make the complex figures accessible to the reader. However, including so much information in the text disrupts the flow and makes it difficult to follow what the main findings and conclusions are.

We appreciate these comments on overall flow. We removed lines 139-143 and lengthened the Figure 2 caption (and associated supplementary figure captions) to contain all necessary detail. We removed lines 208-211 and 214-215 and lengthened the captions for Figure 3, Figure 4, and associated supplementary figures. We removed a sentence from lines 303-304.  

l. 37-39 such a short sentence on non-classical MHC is necessarily an oversimplification, I suggest it be expanded or deleted.

There is certainly a lot to say about each of these genes! While we do not have space in this paper’s introduction to get into these genes’ myriad functions, we added a reference to our companion paper in lines 40-41:

“See the appendices of our companion paper \citep{Fortier2024a} for more detail.”

These appendices are extensive, and readers can find details and references for literature on each specific gene there. In addition, several genes are mentioned in analyses further on in the results, and their specific functions are discussed in more detail when they arise.

l. 47 -49 It would be helpful to briefly outline your criteria for selecting these 17 genes, even if this is repeated later.

Thank you! For greater clarity, we changed the text (lines 50-52) from “Here, we look within 17 specific genes to characterize trans-species polymorphism, a phenomenon characteristic of long-term balancing selection.” to “Here, we look within 17 specific genes---representing classical, non-classical, Class I, and Class II ---to characterize trans-species polymorphism, a phenomenon characteristic of long-term balancing selection.“  

l.85-87 I may be completely wrong, but couldn't problems with establishing orthology in some cases lead to false inferences of TSP, even in primates? Or do you think the data are of sufficient quality to ignore such a possibility? (you touch on this in pp. 261-264)

Yes, problems with establishing orthology can lead to false inferences of TSP, and it has happened before. For example, older studies that used only exon 2 (binding-site-encoding) of the MHC-DRB genes inferred trees that grouped NWM sequences with ape and OWM sequences. Thus, they named these NWM genes MHC-DRB3 and -DRB5 to suggest orthology with ape/OWM MHC-DRB3 and -DRB5, and they also suggested possible TSP between the groups. However, later studies that used non-binding-site-encoding exons or introns noticed that these NWM sequences did not group with ape/OWM sequences (which now shared the same name), providing evidence against orthology. This illustrates that establishing orthology is critical before assessing TSP (as is comparing across regions). This is part of the reason we published a companion paper (https://doi.org/10.7554/eLife.103545.1), which clears up questions of orthology and supports the analyses we did in this paper. In cases where orthology was ambiguous, this also helped us to be conservative in our conclusions here. The problems with ambiguous gene assignment are also discussed in lines 488-499.

l. 88-93 is the first place (others are pp. 109-118 and 460-484) where a fuller description of the data used would be welcome. It's clear that the amount of data from different species varies enormously, not only in the number of alleles per locus, but also in the loci for which polymorphism data are available. In such a synthesis study, one would expect at least a tabulation of the data used in the appendices and perhaps a summary table in the main article.

l. 109-118 Again, a more quantitative summary of the data used, with reference to a table, would be useful.

Thank you! To address these comments, we added Tables 2-4 to allow readers to more readily understand the data we included in each group. We refer to these tables in the introduction (line 95), in the “Data” section of the results (lines 128-129), and the “Data” section of the methods (lines 532-534). Supplementary Files listing the exact alleles and sequences used in each group are also included in the resubmission.

l. 123-124 here you say that the definition of the "16 gene groups" is in the methods (probably pp. 471-484), but it would be useful to present an informative summary of your rationale in the introduction or here

Thank you! We agree that it is helpful to outline these groups earlier. We have changed the paragraph in lines 123-135 from: 

“We considered 16 gene groups and two or three different genic regions for each group: exon 2 alone, exon 3 alone, and/or exon 4 alone. Exons 2 and 3 encode the peptide-binding region (PBR) for the Class I proteins, and exon 2 alone encodes the PBR for the Class II proteins. For the Class I genes, we also considered exon 4 alone because it is comparable in size to exons 2 and 3 and provides a good contrast to the PBR-encoding exons. See the Methods for more detail on how gene groups were defined. Because few intron sequences were available for non-human species, we did not include them in our analyses.” To: 

“We considered 16 gene groups spanning MHC classes and functions. These include the classical Class I genes (MHC-A-related, MHC-B-related, MHC-C-related), non-classical Class I genes (MHC-E-related, MHC-F-related, MHC-G-related), classical Class IIA genes (MHC-DRA-related, MHC-DQA-related, MHC-DPA-related), classical Class IIB genes (MHC-DRB-related, MHC-DQB-related, MHC-DPB-related), non-classical Class IIA genes (MHC-DMA-related, MHC-DOA-related, and non-classical Class IIB genes (MHC-DMB-related, MHC-DOB-related). We studied two or three different genic regions for each group: exon 2 alone, exon 3 alone, and (for Class I) exon 4 alone. Exons 2 and 3 encode the peptide-binding region (PBR) for the Class I proteins, and exon 2 alone encodes the PBR for the Class II proteins. For the Class I genes, we also considered exon 4 alone because it is comparable in size to exons 2 and 3 and provides a good contrast to the PBR-encoding exons. Because few intron sequences were available for non-human species, we did not include them in our analyses.”

l. 100 "alleles" -> "allelic lineages"

Thank you for catching this. We have changed this language in line 104.

l. 227-238 it's important to discuss the possible effect of the number of sequences available on the detectability of TSP - this is particularly important as the properties of MHC genealogies may differ considerably from those expected for neutral genealogies.

This is a good point that may not be obvious to readers. We have added several sentences to clarify this:

Line 193-194: “In a neutral genealogy, monophyly of each species' sequences is expected.”

Line 213-219: “Note that the number of sequences available for comparison also affects the detectability of TSP. For example, if the only sequences available are from the same allelic lineage, they will coalesce more recently in the past than they would with alleles from a different lineage and would not show evidence for TSP. This means our method is well-suited to detect TSP when a diverse set of allele sequences are available, but it is conservative when there are few alleles to test. There were few available alleles for some non-classical genes, such as MHC-F, and some species, such as gibbon.”

Line 244-246: “However, since there are fewer alleles available for the non-classical genes, we note that our method is likely to be conservative here.”

l. 301 and 624-41 it's been difficult for me to understand the rationale behind using rates at mostly gap positions as the baseline and I'd be grateful for a more extensive explanation

Normalizing the rates posed a difficult problem. We couldn’t include every single sequence in the same alignment because BEAST’s computational needs scale with the number of sequences. Therefore, we had to run BEAST separately on smaller alignments focused on a single group of genes at a time. We still wanted to be able to compare evolutionary rates across genes, but because of the way SubstBMA is implemented, evolutionary rates are relative, not absolute. Recall that to help us compare the trees, we included a common set of “backbone” sequences in all of the 16 alignments. This set included some highly-diverged genes. Initially, we planned to use 4-fold degenerate sites as the baseline sites for normalization, but there simply weren’t enough of them once we included the “backbone” set on top of the already highly diverse set of sequences in each alignment. This diversity presented an opportunity.  In BEAST, gaps are treated as missing and do not contribute any probability to the relevant branch or site (https://groups.google.com/g/beast-users/c/ixrGUA1p4OM/m/P4R2fCDWMUoJ?pli=1). So, we figured that sites that were “mostly gap” (a gap in all the human backbone sequences but with an insertion in some sequence) were mostly not contributing to the inference of the phylogeny or evolutionary rates. Because the “backbone” sequences are common to all alignments, making the “mostly gap” sites somewhat comparable across sets while not affecting inferred rates, we figured they would be a reasonable choice for the normalization (for lack of a better option).

We added text to lines 680 and 691-693 to clarify this rationale.

l. 380-84 this overview seems rather superficial. Would it be possible to provide a more quantitative summary?

To make this more quantitative, we plotted the number of associations for each amino acid against evolutionary rate, shown in Figure 6 - Figure Supplement 7 (NOTE: this needs to be renamed as Table 1 - Figure Supplement 1, which the template does not allow). This reveals a significant positive slope for the Class I genes, but not for Class II. We also added explanatory text for this figure in lines 400-404.

Discussion - your approach to detecting TSP is elegant but deserves discussion of its limitations and, in particular, a clear explanation of why detecting TSP rather than quantifying its extent is more important in the context of this work. Another important point for discussion is alternative explanations for the patterns of TSP or, more broadly, gene tree - species tree discordance. Although long-term maintenance of allelic lineages due to long-term balancing selection is probably the most convincing explanation for the observed TSP, interspecific introgression and incorrect orthology assessment may also have contributed, and it would be good to see what the authors think about the potential contribution of these two factors.

Overall, our goal was to use modern statistical methods and data to more confidently assess how ancient the TSP is at each gene. We have added several lines of text (as noted elsewhere in this document) to more clearly illustrate the limitations of our approach. We also agree that interspecific introgression and incorrect orthology assessment can cause similar patterns to arise. We attempted to minimize the effect of incorrect orthology assessment by creating multi-gene trees and exploring reference primate genomes, as described in our companion paper (https://doi.org/10.7554/eLife.103545.1), but cannot eliminate it completely. We have added a paragraph to the discussion to address this (lines 488-499). Interspecific introgression could also cause gene tree-species tree discordance, but we are not sure about how systematic this would have to be to cause the overall patterns we observe, nor about how likely it would have been for various clades of primates across the world.

l. 421 -424 A more nuanced discussion distinguishing between positive selection, which facilitates the establishment of a mutation, and directional selection, which leads to its fixation, would be useful here.

We added clarification to this sentence (line 443-445), from “Indeed, within the phylogeny we find that the most rapidly-evolving codons are substituted at around 2--4-fold the baseline rate.” to “Indeed, within the phylogeny we find that the most rapidly-evolving codons are substituted at around 2--4-fold the baseline rate, generating ample mutations upon which selection may act.”

l. 432-434 You write here about the shaping of TCR repertoires, but I couldn't find any such information in the paper, including Table 1.

We did not include a separate column for these, so they can be hard to spot. They take the form of “TCR 𝛽 Interaction Probability >50%”, “TCR Expression (TRAV38-1)”, or “TCR 𝛼 Interaction Probability >50%” and can be found in Table 1.

l. 436-442 Here a more detailed discussion in the context of divergent allelic advantage and even the evolution of new S-type specificities in plants would be valuable.

We added an additional citation to a review article to this sentence (lines 438-439).  

l. 443 The use of the word "training" here is confusing, suggesting some kind of "education" during the lifetime of the animal.

We agree that “train” is not an entirely appropriate term, and have changed it to “evolve” (line 465).

489-491 What data were used for these calculations?

Apologies for missing this citation! We used the 1000 genomes project data, and the citation has been updated (line 541-542).

Author response:

Reviewer 1:

Concern 1: Figures 1I, 1J, and the whole of Figure 2 could be placed as supplementary figures. Also, for Figure 3E, it would be preferable to show the percentage of cells expressing cytokines rather than their absolute numbers. In fact, the drop in the numbers of cytokine-producing cells is probably due solely to the drop in total cell numbers and not to a decrease in the proportion of cells expressing cytokines. If this is the case, these data should be shown in supplementary figures. Finally, Figures 4 and 5 could be merged.

We thank you for your recommendations. As rearranging figures is not critical to convey the data, we have decided to keep the figures and supplemental figures as they are currently presented.

Concern 2a: It would be important to show the proportion of Treg, Tconv, and CD8 expressing Layilin in healthy skin and in patients developing psoriasis, as well as in the blood of healthy subjects.

This data is published in a previous manuscript from our group. Please see Figure 1 in “Layilin Anchors Regulatory T Cells in Skin” (PMID: 34470859)

Concern 2b: We lack information to be convinced that there is enrichment for migration and adhesion genes in Layilin+ Tregs in the GSEA data. The authors should indicate what geneset libraries they used. Indeed, it is tempting to show only the genesets that give results in line with the message you want to get across. If these genesets come from public banks, the bank used should be indicated, and the results of all gene sets shown in an unbiased way. In addition, it should be indicated whether the analyses were performed on untransformed or pseudobulk scRNAseq data analyses. Finally, it would be preferable to confirm the GSEA data with z-score analyses, as Ingenuity does, for example. Indeed, in GSEA-type analyses, there are genes that have activating but also inhibiting effects on a pathway in a given gene set.

Given that we have already shown that layilin plays a major role in Treg and CD8+ T cell adhesion in tissues, we used a candidate approach for our GSEA. We tested the hypothesis that adhesion and motility pathways are enriched in Layilin-expressing Tregs. There was a statistically significant enrichment for these genes in Layilin+ Tregs compared to Layilin- Tregs, which we feel adequately tests our hypothesis.

Concern 2c: For all FACS data, the raw data should be shown as histograms or dot plots for representative samples.

We respect this concern. We omit these secondary to space constraints.

Concern 2d: For Figure 5B, the number of samples analyzed is insufficient to draw clear conclusions.

We respectfully disagree. Three doners were used in a paired fashion (internally controlled) achieving statistical significance.

Concern 3: For Figs. 4 and 5, the design of the experiment poses a problem. Indeed, the comparison between Layn+ and Layn- cells may, in part, not be directly linked to the expression or absence of expression of this protein. Indeed, Layn+ and Layn- Tregs may constitute populations with different biological properties, beyond the expression of Layn. However, in the experiment design used here, a significant fraction of the sorted Layn- Tregs will be cells belonging to the population that has never expressed this protein. It would have been preferable to sort first the Layn+ Tregs, then knock down this protein and re-sort the Layn- Tregs and Layn+ Tregs. If this experiment is too cumbersome to perform, I agree that the authors should not do it. However, it would be important to mention the point I have just made in the text.

We agree. However, as the reviewer points out, these experiments are not logistically and practically feasible at this point. We do perform several experiments in this manuscript in which layilin is reduced via gene editing with results supporting our hypotheses.

Reviewer 2:

Some of the conclusions drawn by the authors must be treated with caution, as the experimental conditions were not always appropriate, leading to a risk of misinterpretation.

We have been transparent with all our methods and data. We will leave this to the reader to determine level of rigor and the robustness of the data.

Reviewer 3:

Weaknesses:

It is not clear that the assays used for functional analysis of the patient samples were optimal. (2) Several conclusions are not fully substantiated. (3) The report is lacking some experimental details.

We have tried to be as comprehensive and thorough as possible. We feel that the data supports our conclusions. We will leave this to the reader to interpret and conclude.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Aicardi-Goutières Syndrome (AGS) is a genetic disorder that primarily affects the brain and immune system through excessive interferon production. The authors sought to investigate the role of microglia in AGS by first developing bone-marrow-derived progenitors in vitro that carry the estrogen-regulated (ER) Hoxb8 cassette, allowing them to expand indefinitely in the presence of estrogen and differentiate into macrophages when estrogen is removed. When injected into the brains of Csf1r-/- mice, which lack microglia, these cells engraft and resemble wild-type (WT) microglia in transcriptional and morphological characteristics, although they lack Sall1 expression. The authors then generated CRISPR-Cas9 Adar1 knockout (KO) ER-Hoxb8 macrophages, which exhibited increased production of inflammatory cytokines and upregulation of interferon-related genes. This phenotype could be rescued using a Jak-Stat inhibitor or by concurrently mutating Ifih1 (Mda5). However, these Adar1-KO macrophages fail to successfully engraft in the brain of both Csf1r-/- and Cx3cr1-creERT2:Csf1rfl/fl mice. To overcome this, the authors used a mouse model with a patient-specific Adar1 mutation (Adar1 D1113H) to derive ER-Hoxb8 bone marrow progenitors and macrophages. They discovered that Adar1 D1113H ER-Hoxb8 macrophages successfully engraft the brain, although at lower levels than WT-derived ER-Hoxb8 macrophages, leading to increased production of Isg15 by neighboring cells. These findings shed new light on the role of microglia in AGS pathology.

Strengths:

The authors convincingly demonstrate that ER-Hoxb8 differentiated macrophages are transcriptionally and morphologically similar to bone marrow-derived macrophages. They also show evidence that when engrafted in vivo, ER-Hoxb8 microglia are transcriptomically similar to WT microglia. Furthermore, ER-Hoxb8 macrophages engraft the Csf1r-/- brain with high efficiency and rapidly (2 weeks), showing a homogenous distribution. The authors also effectively use CRISPR-Cas9 to knock out TLR4 in these cells with little to no effect on their engraftment in vivo, confirming their potential as a model for genetic manipulation and in vivo microglia replacement.

Weaknesses:

The robust data showing the quality of this model at the transcriptomic level can be strengthened with confirmation at protein and functional levels. The authors were unable to investigate the effects of Adar1-KO using ER-Hoxb8 cells and instead had to rely on a mouse model with a patient-specific Adar1 mutation (Adar1 D1113H). Additionally, ER-Hoxb8-derived microglia do not express Sall1, a key marker of microglia, which limits their fidelity as a full microglial replacement, as has been rightfully pointed out in the discussion.

Overall, this paper demonstrates an innovative approach to manipulating microglia using ER-Hoxb8 cells as surrogates. The authors present convincing evidence of the model's efficacy and potential for broader application in microglial research, given its ease of production and rapid brain engraftment potential in microglia-deficient mice. While Adar1-KO macrophages do not engraft well, the success of TLR4-KO line highlights the model's potential for investigating other genes. Using mouse-derived cells for transplantation reduces complications that can come with the use of human cell lines, highlighting the utility of this system for research in mouse models.

Thank you for this thoughtful and balanced assessment. The major suggestion from Reviewer 1 was that confirmation of RNAseq data with protein or functional studies would add strength.  We provided protein staining by IHC for IBA1 in vivo, as well as protein staining by FACS for CD11B, CD45, and TMEM119 in vitro and in vivo.  For TLR4, we showed successful protein KO and blunted response to LPS (a TLR4 ligand) challenge, which we believe provides some protein and functional data to support the approach.  To bolster these data, we added staining for P2RY12 on brain-engrafted ER-Hoxb8s.

Regarding the Adar1 KO phenotypes showing non-engraftment. Because ADAR1 KO mice are embryonically lethal due to hematopoietic failure, we see the health impacts of Adar1 KO on ER-Hoxb8s as a strength of the transplantation model, enabling the assessment of ADAR1 global function in macrophages and microglia-like cells without generation of a transgenic mouse line. In addition, it was a surprise that the health impact occurs at the macrophage and not the progenitor stage, perhaps providing insight for future studies of ADAR1’s role in hematopoiesis. Instead, we were able to show a significant impact of complete loss of Adar1 on survival and engraftment, suggesting an important biological function of ADAR1. Macrophage-specific D1113H mutation, which affects part of the deaminase domain, shows that when the RNA deamination (but not the RNA binding) function of ADAR1 is disrupted, we find brain-wide interferonopathy. This is very exciting to our group and hopefully the community as astrocytes are thought to be a major driver of brain interferonopathy in patients with ADAR1 mutations. Instead, this suggests that disruption of brain macrophages is also a major contributor. 

Reviewer #2 (Public review):

Summary:

Microglia have been implicated in brain development, homeostasis, and diseases. "Microglia replacement" has gained traction in recent years, using primary microglia, bone marrow or blood-derived myeloid cells, or human iPSC-induced microglia. Here, the authors extended their previous work in the area and provided evidence to support: (1)

Estrogen-regulated (ER) homeobox B8 (Hoxb8) conditionally immortalized macrophages from bone marrow can serve as stable, genetically manipulated cell lines. These cells are highly comparable to primary bone marrow-derived (BMD) macrophages in vitro, and, when transplanted into a microglia-free brain, engraft the parenchyma and differentiate into microglia-like cells (MLCs). Taking advantage of this model system, the authors created stable, Adar1-mutated ER-Hoxb8 lines using CRISPR-Cas9 to study the intrinsic contribution of macrophages to the Aicardi-Goutières Syndrome (AGS) disease mechanism.

Strengths:

The studies are carefully designed and well-conducted. The imaging data and gene expression analysis are carried out at a high level of technical competence and the studies provide strong evidence that ER-Hoxb8 immortalized macrophages from bone marrow are a reasonable source for "microglia replacement" exercise. The findings are clearly presented, and the main message will be of general interest to the neuroscience and microglia communities.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

This is an elegant study, demonstrating both the utility and limitations of ER-Hoxb8 technology as a surrogate model for microglia in vivo. The manuscript is well-designed and clearly written, but authors should consider the following suggestions:

(1) Validation of RNA hits at the protein level: To strengthen the comparison between ER-Hoxb8 macrophages and WT bone marrow-derived macrophages, validating several RNA hits at the protein level would be beneficial. As many of these hits are surface markers, flow cytometry could be employed for confirmation (e.g., Figure 1D, Figure 3E).

In vitro, we show protein levels by flow cytometry for CD11B (ITGAM) and CD45 (PTPRC; Figure 1C), as well as TMEM119 (Supplemental Figure 2A) and TLR4 (Supplemental Figure 3C/D). In vivo, we show TMEM119 protein levels by flow cytometry (Figure 3A), as well as their CD11B/CD45 pregates (Supplemental Figure 2C), plus immunostaining for IBA1 (AIF1; Figure 2D). We now provide additional data showing P2RY12 immunostaining in brain-engrafted cells (Supplemental Figure 2B). 

(2) The authors should consider testing the phagocytic capacity of ER-Hoxb8-derived macrophages to further validate their functionality.

Thank you for the suggestion. We measured ER-Hoxb8 macrophage ability to engulf phosphatidylserine-coated beads that mimic apoptotic cells, compared with phosphatidylcholine-coated beads, now as new Supplemental Figure 1C/D. This agrees with existing literature showing efficient engulfment/phagocytosis by ER-Hoxb8-derived cells (Elhag et al., 2021).

(3) For Figure 3E, incorporating a wild-type (WT) microglia reference would be beneficial to establish a baseline for comparison (e.g. including WT microglia data in the graph or performing a ratio analysis against WT expression levels).

We agree - we now include bars representing our sequenced primary microglia data in Figure 3E as a comparison.  

(4) Some statistical analyses may require refinement. Specifically, for Figure 4J, where the effects of Adar1 KO and Adar1 KO with Bari are compared, it would be more appropriate to use a two-way ANOVA.

Thank you for noting it. We have now done more appropriate two-way ANOVA and included the updated results in Figure 4J and the corresponding Supplemental Figure 4G. Errors in figure legend texts have also been corrected to reflect the statistical tests used.

(5) Cx3cr1-creERT2 pups injected with tamoxifen: The authors could clarify the depletion ratio in these experiments before the engraftment and assess whether the depletion is global or regional. In comparison to Csf1r-/-, where TLR4-KO ER-Hoxb8 engraft globally, in Cx3cr1-creERT2, the engraftment seems more regional (Figure 5A vs Supplementary Figure 5B); is this due to the differences in depletion efficiency?

This is an excellent question and observation, and one that we are very interested in, though that finding does not change the conclusions of this particular study.  We find some region-specific differences in depletion early after tamoxifen injection, but that all brain regions are >95% depleted by P7. For instance, in a recently published manuscript (Bastos et al., 2025) we find some differences in the depletion kinetics in the genetic model. By P3, we find 90% depletion in cortex with 50-60% in thalamus and hippocampus. In other studies, we typically deliver primary monocytes, and this is the first study where we report engraftment of ER-Hoxb8 cells in the inducible model.  In this sense, it is possible that depletion kinetics may regionally affect engraftment, but future studies are required to more finely assess this point with ER-Hoxb8s, as it may change how these models are used in the future.

Bastos et al., Monocytes can efficiently replace all brain macrophages and fetal liver monocytes can generate bonafide SALL1+ microglia, Immunity (2025), https://doi.org/10.1016/j.immuni.2025.04.006

(6) It would be helpful for the authors to clarify whether Adar1 is predominantly expressed by microglia, especially since the study aims to show its role in dampening the interferon response.

That’s a wonderful point. Adar1 is expressed by all brain cells, with highest transcript level in some neurons, astrocytes, and oligodendrocytes. It is an interferon-stimulated gene, and mutation itself leads to interferonopathy, we believe, due to poor RNA editing and detection of endogenous RNA as non-self by MDA5. We hope it can dampen the interferon response, but in the case of mutation, Adar1 is probably causal of interferonopathy.  It is induced in microglia upon systemic inflammatory challenge (LPS). We have edited the text to highlight its expression pattern.  See BrainRNAseq.org (Zhang*, Chen*, Sloan*, et al., 2014 and Bennett et al., 2016)

Reviewer #2 (Recommendations for the authors):

(1) There appears to be a morphological difference between wt and Adar1/Ifih1 double KO (dKO) cells in the engrafted brains (Figure 5). It would be good if the authors could systematically compare the morphology (e.g., soma size, number, and length of branches) of the engrafted MLCs between the wt and mutant cells.

We agree. While cells did not differ in branch number or length, engrafted dKO cells had significantly larger somas compared with controls, which we now present in Figure S5A.

(2) To fully appreciate the extent of how those engrafted ER-Hoxb8 immortalized macrophages resemble primary, engrafted yolk sac-myeloid cells, vs engrafted iPSC-induced microglia, it would be informative to provide a comparison of their RNAseq data derived from the engrafted ER-Hoxb8 immortalized macrophages with published data transcriptomic data sets (e.g. Bennett et al. Neuron 2018; Chadarevian et al. Neuron 2024; Schafer et al. Cell 2023).

Thank you for this suggestion. To address this, we provide our full dataset for additional experiments. To compare with a similar non-immortalized model, we compared top up- and down-regulated genes from our data to those of ICT yolk sac progenitor cells from our previous work (Bennett et al., 2018). We find overlap between brain-engrafted ER-Hoxb8-, bone marrow-, and yolk sac-derived cells (Supplemental Figure 2F, Supplemental Table 3).  

Minor comments:

Figure 6C: red arrow showing zoom in regions are not matchable. It might be beneficial to provide bigger images with each channel for C and D as a Supplemental Figure.

We fixed this in Figure 6C to show areas of interest in the cortex for both conditions. Figure S7A shows intermediate power images to aid in interpretation.

Author response:

The following is the authors’ response to the original reviews

Reviewer 1 (Public review):

Weaknesses:

While the data generally supports the authors' conclusions, a weakness of this manuscript lies in their analytical approach where EEG feature-space comparisons used the number of spontaneous or evoked seizures as their replicates as opposed to the number of IHK mice; these large data sets tend to identify relatively small effects of uncertain biological significance as being highly statistically significant. Furthermore, the clinical relevance of similarly small differences in EEG feature space measurements between seizure-naïve and epileptic mice is also uncertain.

In this work, we used linear mixed effect model to address two levels of variability –between animals and within animals. The interactive linear mixed effect model shows that most (~90%) of the variability in our data comes from within animals (Residual), the random effect that the model accounts for, rather than between animals. Since variability between animals are low, the model identifies common changes in seizure propagation across animals, while accounting for the variability in seizures within each animal. Therefore, the results we find are of changes that happen across animals, not of individual seizures. We made text edits to clarify the use of the linear mixed effect model. (page6, second paragraph and page 11, first paragraph)

Finally, the multiple surgeries and long timetable to generate these mice may limit the value compared to existing models in drug-testing paradigms.

Thank you for the suggestion. We added a discussion in the ‘Comparison to other seizure models…’ section on pages 15 and 16. In an existing model investigating spontaneous tonic-clonic seizures (such as the intra-amygdala kainate injection model), the time investment is back-loaded, requiring two to three weeks per condition while counting spontaneous seizures, which may occur only once a day. In contrast, our model requires a front-loaded time investment. Once the animals are set up, we can test multiple drugs within a few weeks, providing significant time savings. Additionally, we did not pre-screen animals in our study. Existing models often pre-select mice with high rates of spontaneous seizures, whereas in our model, seizures can be induced even in animals with few spontaneous seizures. We believe that bypassing the need for pre-screening also is a key advantage of our induced seizure model.  

Reviewer 1 (Recommendations for the authors):

(1) Address why the EEG data comparisons were performed between seizures and not between animals (as explicitly described in the public review). Further, a discussion of the biological significance (or lack thereof) of the effect size differences observed is warranted. This is especially concerning when the authors make the claim that spontaneous and induced seizures are essentially the same while their analysis shows all evaluated feature space parameters were significantly difference in the initial 1/3 of the EEG waveforms.

We made text edits to clarify the use of the linear mixed effects model (page 6, second paragraph, and page 11, first paragraph)

(2) The authors place great emphasis on the use of clinically/etiologically relevant epilepsy models in drug discovery research. There is discussion criticizing the time points required to enact kindling and the artificial nature of acute seizure induction methods. However, the combination IHK-opto seizure induction model also requires a lengthy timeline. A more tempered discussion of this novel model's strengths may benefit readers.

Thank you for the suggestion. We added a discussion in the ‘Comparison to other seizure models…’ section on pages 15 and 16.

(3) The authors should further emphasize the benefit of having an inducible seizure model of focal epilepsy since other mouse models (e.g., genetic or TBI models) may have superior etiological relevance (construct and face validity) but may not be amenable to their optogenetic stimulation approach.

Thank you for the suggestion. We revised the manuscript to better emphasize the potential significance of our approach. We added a discussion in the 'Application of Models...' section on page 15, second paragraph. The on-demand seizure model can be applied to address biologically and clinically relevant questions beyond its utility in drug screening. For example, crossing the Thy1-ChR2 mouse line with genetic epilepsy models, such as Scn1a mutants, could reveal how optogenetic stimulation differentially induces seizures in mutant versus non-mutant mice, providing insights into seizure generation and propagation in Dravet syndrome. Due to the cellular specificity of optogenetics, we also envision this approach being used to study circuit-specific mechanisms of seizure generation and propagation.

(4) Suggestion: Provide immunolabeled imagery demonstrating ChR2 presence in Thy1 cells.

Thank you for the suggestion. We added a fluorescence image showing ChR2 expression in Fig. 2A

(5) It might be prudent to mention any potential effects of laser heat on hippocampal cell damage, although the 10 Hz, ~10 mW, and 6 s stim is unlikely to cause any substantial burns. Without knowing the diameter and material of the optic fiber, this is left up to some interpretation.

Thank you for the comments. In the Methods section, we listed the optical fiber diameter as 400 microns (page 17, EEG and Fiber Implantation section). Using 5–18 mW laser power with a relatively large fiber diameter of 400 microns, the power density falls within the range of commonly employed channelrhodopsin activation conditions in vivo. That said, we would like to investigate potential heat effects or cell damage in a follow-up study.

(6) There are instances in the manuscript where the authors describe experimental and analytical parameters vaguely (e.g. "Seizures were induced several times a day", "stimulation was performed every 1 - 3 hours over many days"). These descriptions can and should be more precise.

Thank you for the comments. To enhance clarity, we added the stimulation protocol in a flowchart format in Fig. S2A, describing how we determined the threshold and proceeded to the drug test. Following this protocol, there was variability in the number of stimulations per day.

(7) In the second to last paragraph of the discussion, the authors state "However, HPDs are not generalizable across species - they are specific to the mouse model (55)." This statement is inaccurate. The paper cited comes from Dr. Corrine Roucard's lab at Synapcell. In fact, Dr. Rouchard argues the opposite (See Neurochem Res (2017) 42:1919-1925).

Thank you for pointing out the mistake. On page 16, in the first paragraph, reference 55 (now 58 in the revised version) was intended to refer to 'quickly produce dose-response curves with high confidence.' In the revision, we cited another paper reporting that hippocampal spikes were not reproduced in the rat IHK model. R. Klee, C. Brandt, K. Töllner, W. Löscher, Various modifications of the intrahippocampal kainate model of mesial temporal lobe epilepsy in rats fail to resolve the marked rat-to-mouse differences in type and frequency of spontaneous seizures in this model. Epilepsy Behav. 68, 129–140 (2017).

(8) In the discussion, Levetiracetam is highlighted as an ASM that would not be detected in acute induced seizure models; the authors point out its lack of effect in MES and PTZ. However, LEV is effective in the 6Hz test (also an acute-induced seizure model). This should be stated.

Thank you for the comments. We highlighted the discussion on LEV in the 'Application of Model to Testing Multiple Classes of ASMs...' section on page 14.

(9) The results text indicates that 9 epileptic mice were used to test LEV and DZP. However, the individual data points illustrated in Figure 5B show N=8 mice. Please correct.

Thank you for the comments. A total of nine epileptic mice were used to assess two drugs, with the animals being re-used as indicated in the schematic. A total of eight assessments were conducted for DZP with six mice and eight assessments for LEV with five mice. Each assessment included hourly ChR2 activations without an ASM and hourly ChR2 activations after ASM injection.

(10) Figure 4D: Naïve mice are labeled as solid blue circles in the legend while the data points are solid blue triangles. Please correct.

Thank you. We corrected the marker in Fig.4D.

Reviewer 2 (Public Review):

Weaknesses:

(1) Although the figures provide excellent examples of individual electrographic seizures and compare induced seizures in epileptic and naïve animals, it is unclear which criteria were used to identify an actual seizure induced by the optogenetic stimulus, versus a hippocampal paroxysmal discharge (HPD), an "afterdischarge", an "electrophysiological epileptiform event" (EEE, Ref #36, D'Ambrosio et al., 2010 Epilepsy Currents), or a so-called "spike-wave-discharge" (SWD). Were HPDs or these other non-seizure events ever induced using stimulation in animals with IH-KA? A critical issue is that these other electrical events are not actual seizures, and it is unclear whether they were included in the column showing data on "electrographic afterdischarges" in Figure 5 for the studies on ASDs. This seems to be a problem in other areas of the paper, also.

Thank you for pointing out the unclear definition of the seizures analyzed. We added sentences at the beginning of the Results section (page 3) to clarify the terminology we used. We analyzed animal behavior during evoked events, and a high percentage of induced electrographic events were accompanied by behavioral seizures with a Racine scale of three or above. We added Supplemental Figure S9, which shows behavioral seizure severity scores observed before and during ASM testing. We hope these changes address the reviewer’s concern and improve the clarity of the manuscript.

(2) The differences between the optogenetically evoked seizures in IH-KA vs naïve mice are interpreted to be due to the "epileptogenesis" that had occurred, but the lesion from the KA-induced injury would be expected to cause differences in the electrically and behaviorally recorded seizures - even if epileptogenesis had not occurred. This is not adequately addressed.

Thank you for the comments. IHK-injected mice had spontaneous tonic-clonic seizures before the start of optical stimulation, as shown in Figure S1.

(3) The authors offer little mention of other research using animal models of TLE to screen ASDs, of which there are many published studies - many of them with other strengths and/or weaknesses. For example, although Grabenstatter and Dudek (2019, Epilepsia) used a version of the systemic KA model to obtain dose-response data on the effects of carbamazepine on spontaneous seizures, that work required use of KA-treated rats selected to have very high rates of spontaneous seizures, which requires careful and tedious selection of animals. The ETSP has published studies with an intra-amygdala kainic acid (IA-KA) model (West et al., 2022, Exp Neurol), where the authors claim that they can use spontaneous seizures to identify ASDs for DRE; however, their lack of a drug effect of carbamazepine may have been a false negative secondary to low seizure rates. The approach described in this paper may help with confounds caused by low or variable seizure rates. These types of issues should be discussed, along with others.

We appreciate the reviewer’s insights. We added a discussion comparing our model with other existing models in the Discussion section (pages 15 and 16, 'Comparison to Other Seizure Models Used in Pharmacologic Screening' section). In an existing model investigating spontaneous tonic-clonic seizures (such as the intra-amygdala kainate injection model), the time investment is back-loaded, requiring two to three weeks per condition while counting spontaneous seizures, which may occur only once a day. In contrast, our model requires a front-loaded time investment. Once the animals are set up, we can test multiple drugs within a few weeks, providing significant time savings. Additionally, we did not pre-screen animals in our study. Existing models often pre-select mice with high rates of spontaneous seizures, whereas in our model, seizures can be induced even in animals with few spontaneous seizures. We believe that bypassing the need for pre-screening is a key advantage of our induced seizure model.

(4) The outcome measure for testing LEV and DZP on seizures was essentially the fraction of unsuccessful or successful activations of seizures, where high ASD efficacy is based on showing that the optogenetic stimulation causes fewer seizures when the drug is present. The final outcome measure is thus a percentage, which would still lead to a large number of tests to be assured of adequate statistical power. Thus, there is a concern about whether this proposed approach will have high enough resolution to be more useful than conventional screening methods so that one can obtain actual dose-response data on ASDs.

Thank you for the comments. In this revision, we added Supplemental Figure S9, showing the severity of behavioral seizures observed before and during ASM testing for each animal. We observed a reduction in behavioral seizure severity for each subject. We would like to explore using behavioral severity as an outcome measure in a follow-up study.

(5) The authors state that this approach should be used to test for and discover new ASDs for DRE, and also used for various open/closed loop protocols with deep-brain stimulation; however, the paper does not actually discuss rigorously or critically the background literature on other published studies in these areas or how this approach will improve future research for a broader audience than the ETSP and CROs. Thus, it is not clear whether the utility will apply more widely and how extensive a readership will be attracted to this work.

We appreciate the reviewer’s insights. We revised the manuscript to better emphasize the potential significance of our approach (page 15, second paragraph). The on-demand seizure model can be applied to address biologically and clinically relevant questions beyond its utility in drug screening. For example, crossing the Thy1-ChR2 mouse line with genetic epilepsy models, such as Scn1a mutants, could reveal how optogenetic stimulation differentially induces seizures in mutant versus non-mutant mice, providing insights into seizure generation and propagation in Dravet syndrome. Due to the cellular specificity of optogenetics, we also envision this approach being used to study circuit-specific mechanisms of seizure generation and propagation. Regarding drug-resistant epilepsy (DRE) and anti-seizure drug (ASD) screening, we agree with the reviewer that probing new classes of ASDs for DRE represents a critical goal. However, we believe that a full exploration of additional ASD classes and/or modeling DRE lies outside the scope of this manuscript, and we would like to explore it in a follow-up study.

Reviewer 2 (Recommendations for the authors):

(1) The authors should explain why 10 Hz was chosen as the stimulation frequency.

Thank you for the comment. A frequency of 10 Hz was determined based on previous work using anesthetized animals prepared in an acute in vivo setting. To simplify the paper and avoid confusion, we did not include a discussion on how we determined the frequency. Instead, we added a detailed description of how we optimized the power in a flowchart format in Supplemental Figure S2. We hope this improves reproducibility.

(2) After micro-injection of KA, morphological changes were observed in the hippocampus, but no comparison of Chr2 expression was made in naïve animals vs KA-injected animals. Presumably, the Thy1-Chr2 mouse expresses GFP in cells that express Chr2. Thus, it may be useful to show the expression of Chr2 in animals with hippocampal sclerosis. This may explain the lack of dramatic difference between stimulation parameters in naïve vs epileptic animals, as shown in supplemental Figure S2.

Thank you for the suggestion. We added a fluorescence image of ChR2 expression in CA1, ipsilateral to the KA-injected site, in Fig. 2A.

(3) The authors state that "During epileptogenesis, neural networks in the brain undergo various changes ranging from modification of membrane receptors to the formation of new synapses" and that these changes are critical for successful "on-demand" seizure induction. However, it is not clear or well-discussed whether changes in neuronal cell densities that occur during sclerosis are important for "on-demand" seizure induction as well. Also, the authors showed that naïve animals exhibit a kindling-like effect, but it was unclear whether a similar effect was present in epileptic animals (i.e. do stimulation thresholds to seizure induction change as the animal gets more induction stimulations)? If present, would the secondary kindling affect drug-testing studies (e.g., would the drug effect be different on induced seizure #2 vs induced seizure #20)?

Thank you for the suggestion. Since this is an important aspect of the model, we would like to address the kindling effect, the secondary kindling effect, and histopathology in a longer-term setting (several weeks) in a follow-up study.

(4) The authors show that in their model, LEV and DZP were both efficacious. The authors do not seem to mention that, over 25 years ago, LEV was originally missed in the standard ETSP screens; and, it was only discovered outside of the ETSP with the kindling model. The kindling model is now used to screen ASDs. The authors should consider adding this point to the Discussion. It remains unclear, however, if the author's screening strategy shows advantages over kindling and other such approaches in the field.

Thank you for the suggestion. We added a discussion on LEV in the 'Application of Model to Testing Multiple Classes of ASMs...' section on page 14.

(5) P8 paragraph 2. The authors state values for naïve animals, but they should also provide values for epileptic animals since they state that the groups were not significantly different (p>0.05). It would be useful to show values for both and state the actual p-value from the test. This issue of stating mean/median values with SD and sample size should be addressed for all data throughout the paper. Additionally, Figure S2 should be added to the manuscript and discussed, as it has data that may be valuable for the reproducibility of the paper.

Thank you for the suggestion. Figure S2 shows the threshold power required to induce electrographic activity for n = 10 epileptic animals (9.14 ± 4.75 mW) and n = 6 naïve animals (6.17 ± 1.58 mW) (Wilcoxon rank-sum test, p = 0.137). The threshold duration was comparable between the same epileptic animals (6.30 ± 1.64 s) and naïve animals (5.67 ± 1.03 s) (Wilcoxon rank-sum test, p = 0.7133). 

(6) In addition to the other stated references on synaptic reorganization in the CA1 area, the authors should mention similar studies from Esclapez et al. (1999, J Comp Neurol).

Thank you. We have included the reference in the revision.

(7) All of the raw EEG data on the seizures should be accessible to the readers.

Thank you for the suggestion. We will consider depositing EEG data in a publicly accessible site.

Reviewer 3 (Public review):

Weaknesses:

(1) Evaluation of seizure similarity using the SVM modeling and clustering is not sufficiently explained to show if there are meaningful differences between induced and spontaneous seizures. SVM modeling did not include analysis to assess the overfitting of each classifier since mice were modeled individually for classification.”

Thank you for the comment. We made text edits to clarify the purpose of the SVM analysis. It was not intended to identify meaningful differences between induced and spontaneous seizures. Rather, it was used to classify EEG epochs as 'seizures' based on spontaneous seizures as the training set, demonstrating the gross similarity between induced and spontaneous seizures.

(2) The difference between seizures and epileptiform discharges or trains of spikes (which are not seizures) is not made clear.

Thank you for pointing out the unclear definition of the seizures analyzed. We added sentences at the beginning of the Results section (page 3) to clarify the terminology we used. We analyzed animal behavior during evoked events, and a high percentage of induced electrographic events were accompanied by behavioral seizures with a Racine scale of three or above. We added Supplemental Figure S9 to show the types of seizures observed before and during ASM testing. We hope these changes address the reviewer’s concern and improve the clarity of the manuscript.

(3) The utility of increasing the number of seizures for enhancing statistical power is limited unless the sample size under evaluation is the number of seizures. However, the standard practice is for the sample size to be the number of mice.

In this work, we used a linear mixed-effects model to address two levels of variability—between animals and within animals. The interactive linear mixed-effects model shows that most (~90%) of the variability in our data comes from within animals (residual), the random effect that the model accounts for, rather than between animals. Since variability between animals is low, the model identifies common changes in seizure propagation across animals while accounting for the variability in seizures within each animal. Therefore, the results we find reflect changes that occur across animals, not individual seizures. We made text edits to clarify the use of the linear mixed-effects model.

(4) Seizure burden is not easily tested.

Thank you for the comment. We added Supplemental Figure S9 to summarize the severity of behavioral seizures before and during ASM testing. This addresses the reviewer’s comment on seizure burden. In a follow-up study, we would like to explore this type of outcome measure for drug screening.

Reviewer 3 (Recommendations for the authors):

(1) Provide a stronger rationale to use area CA1. For example, the authors mention that CA1 is active during seizure activity, but can seizures originate from CA1? That would make the approach logical and also explain why induced and spontaneous seizures are similar.

Thank you for the comment. We discussed it in the Discussion section (page 14, first and second paragraphs).

(2) Explain the use of SVM classifiers so it is more convincing that induced and spontaneous seizures are similar. Or, if they are not similar, explain that this is a limitation.

We made text edits to clarify the purpose of the SVM analysis. It was not intended to identify meaningful differences between induced and spontaneous seizures. Rather, it was used to classify EEG epochs as 'seizures' based on spontaneous seizures as the training set, demonstrating the gross similarity between induced and spontaneous seizures.

(3)If feasible, extend the duration over which seizure induction reliability is assessed so that the long-term utility of the model can be demonstrated.

Thank you for the suggestion. We would like to assess long-term utility in a follow-up study.

(4) The GitHub link is not yet active. The authors will be required to supply their relevant code for peer evaluation as well as publication.

Thank you. The GitHub repository is now active.

(5) State and assess the impacts of sex as a biological variable.

Thank you for pointing this out. Both female and male animals were included in this study: Epileptic cohort: 7 males, 3 females; Naïve cohort: 3 males, 4 females.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public Review):

This work adds another mouse model for LAMA2-MD that re-iterates the phenotype of previously published models. Such as dy3K/dy3K; dy/dy and dyW/dyW mice. The phenotype is fully consistent with the data from others.

Thank you for the valuable comments and good suggestions you have proposed, and we have added information and analysis of another mouse model for LAMA2-MD in the updated version 2 of this manuscript.

One of the major weaknesses of the manuscript initially submitted was the overinterpretation and the overstatements. The revised version is clearly improved as the authors toned-down their interpretation and now also cite the relevant literature of previous work.

Thank you for the good comments you have proposed, and we have carefully corrected the overinterpretation and overstatements in the previous updated version.

Unfortunately, the data on RNA-seq and scRNA-seq are still rather weak. scRNA-seq was conducted with only one mouse resulting in only 8000 nuclei. I am not convinced that the data allow us to interpret them to the extent of the authors. Similar to the first version, the authors infer function by examining expression. Although they are a bit more cautious, they still argue that the BBB is not functional in dy^H/dy^H mice without showing leakiness. Such experiments can be done using dyes, such as Evans-blue or Cadaverin. Hence, I would suggest that they formulate the text still more carefully.

Thank you for the valuable suggestions. We also agree that we should perform more related functional experiments such as Evans-blue or Cadaverin to confirm the impaired BBB. However, the related functional experiments haven’t been done due to the first author has been working in clinic. While, we have added the "Limitations" part, and made statements in the Limitations part with "Even though RNA-seq and scRNA-seq have been performed, the data of scRNA-seq are still insufficient due to the limited number of mouse brains. This study has provided potentially important information for the molecular pathogenetic mechanisms of muscular dystrophy and brain dysfunction for LAMA2-CMD, however, some related functional experiments have not been further performed".

A similar lack of evidence is true for the suggested cobblestone-like lissencephaly of the mice. There is no strong evidence that this is indeed occurring in the mice (might also be a problem because mice die early). Hence, the conclusions need to be formulated in such a way that readers understand that these are interpretations and not facts.

Thank you for the valuable suggestions. We do agree with this comment, and have made statement in the Limitations with "This study has provided potentially important information for the molecular pathogenetic mechanisms of muscular dystrophy and brain dysfunction for LAMA2-CMD, however, some related functional experiments have not been further performed". Also, for the cobblestone-like lissencephaly which was showed in LAMA2-CMD patients while not found in the mouse model, we have added the discussion as "Though the cortical malformations were not found in the dy H/dy H brains by MRI analysis probably due to the small volume in within 1 month old, Thus, the changes in transcriptomes and protein levels provided potentially useful data for the hypothesis of the impaired gliovascular basal lamina of the BBB, which might be associated with occipital pachygyria in LAMA2-CMD patients."

Finally, I am surprised that the only improvement in the main figures is the Western blot for laminin-alpha2. The histology of skeletal muscle still looks rather poor. I do not know what the problems are but suggest that the authors try to make sections from fresh-frozen tissue. I anticipate that the mice were eventually perfused with PFA before muscles were isolated. This often results in the big gaps in the sections.

Thank you for the valuable suggestions. We do agree with this comment and we should make sections from fresh-frozen tissue. Therefore, we have made statement in the Limitations with "Moreover, due to making sections with PFA before muscles isolated, and not from fresh-frozen tissue, there have been big gaps in the sections which do affect the histology of skeletal muscle to some extent."

Overall, the work is improved but still would need additional experiments to make it really an important addition to the literature in the LAMA-MD field.

Thank you for all your good comments and the valuable suggestions.

Reviewer #2 (Public Review):

This revised manuscript describes the production of a mouse model for LAMA2- Related Muscular Dystrophy. The authors investigate changes in transcripts within the brain and blood barrier. The authors also investigate changes in the transcriptome associated with the muscle cytoskeleton. Strengths: (1) The authors produced a mouse model of LAMA2-CMD using CRISPR-Cas9. (2) The authors identify cellular changes that disrupted the blood-brain barrier.

Thank you for your good comments.

Weaknesses:

The authors throughout the manuscript overstate "discoveries" which have been previously described, published and not appropriately cited.

Thank you for your great suggestion. We have toned-down the interpretations and overstatements throughout the manuscript, and added words such as "potentially", "possible", "some potential clues", "was speculated to probably", and so on.

Alternations in the blood brain barrier and in the muscle cell cytoskeleton in LAMA2-CMD have been extensively studied and published in the literature and are not cited appropriately.

Thank you for your great suggestion. We do agree with that alternations in the muscle cell cytoskeleton in LAMA2-CMD have been extensively studied and published, and the related literatures have been cited in the updated version 2.0. However, alternations in the blood brain barrier in LAMA2-CMD haven’t been extensively studied, only some papers (such as PMID: 25392494, PMID: 32792907) have investigated or discussed this issue.

The authors have increased animal number to N=6, but this is still insufficient based on Power analysis results in statistical errors and conclusions that may be incorrect.

Thank you for your great suggestion. We do agree that the animal number should be increased for Power analysis, and we have added statements in the Limitations with "Finally, due to the limited number of animal samples for the Power analysis, the statistical errors and conclusions might be affected."

The use of "novel mouse model" in the manuscript overstates the impact of the study.

Thank you for your great suggestion. We have changed the statement "novel mouse model" throughout the manuscript except the title.

All studies presented are descriptive and do not more to the field except for producing yet another mouse model of LAMA2-CMD and is the same as all the others produced.

Thank you for your comment. We do agree that further functional experiments have not been performed to reveal and confirm the pathogenesis. However, the analysis of phenotype was systematic and comprehensive, including survival time, motor function, serum CK, muscle MRI, muscle histopathology in different stages, and brain histopathology. Moreover, RNA-seq and scRNA-seq in LAMA2-CMD have been seldom performed before, and the data in this study could provide potentially important information for the molecular pathogenetic mechanisms of muscular dystrophy and brain dysfunction for LAMA2-CMD.

Grip strength measurements are considered error prone and do not give an accurate measurement of muscle strength, which is better achieved using ex vivo or in vivo muscle contractility studies.

Thank you for your great suggestion. We do agree that grip strength measurements are considered error prone and do not give an accurate measurement of muscle strength. And we have added related statement in the Limitations with "Grip strength measurements used in this study are considered error prone and do not give an accurate measurement of muscle strength, which would be better achieved using ex vivo or in vivo muscle contractility studies."

A lack of blinded studies as pointed out of the authors is a concern for the scientific rigor of the study.

Thank you for your great suggestion. We performed the studies with those scoring outcome measures not blinded to the groups. Actually, it was very easy to discriminate the dy^H/dy^H groups from the WT/Het mice due to that the dy^H/dy^H mice showed much smaller body shape than other groups from as early as P7 .

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

There are multiple grammatical errors throughout the manuscript which should be corrected.

Thank you for your recommendation. We have carefully corrected the grammatical errors within the manuscript.

The authors mention no changes in intestinal muscles, but it is unclear if they are referring to skeletal or smooth muscle.

Thank you for your good comment. The intestinal muscles with no changes in this study are referring to smooth muscle, and we have changes the description into intestinal smooth muscles.

Author response:

The following is the authors’ response to the original reviews

We thank the Reviewers for their constructive comments and the Editor for the possibility to address the Reviewers’ points in this rebuttal. We 

(1) Conducted new experiments with NP6510-Gal4 and TH-Gal4 lines to address potential behavioral differences due to targeting dopaminergic vs. both dopaminergic and serotonergic neurons

(2) Conducted novel data analyses to emphasize the strength of sampling distributions of behavioral parameters across trials and individual flies

(3) Provided Supplementary Movies

(4) Calculated additional statistics

(5) Edited and added text to address all points of the Reviewers.

Please see our point-by-point responses below.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Translating discoveries from model organisms to humans is often challenging, especially in neuropsychiatric diseases, due to the vast gaps in the circuit complexities and cognitive capabilities. Kajtor et al. propose to bridge this gap in the fly models of Parkinson's disease (PD) by developing a new behavioral assay where flies respond to a moving shadow by modifying their locomotor activities. The authors believe the flies' response to the shadow approximates their escape response to an approaching predator. To validate this argument, they tested several PD-relevant transgenic fly lines and showed that some of them indeed have altered responses in their assay.

Strengths:

This single-fly-based assay is easy and inexpensive to set up, scalable, and provides sensitive, quantitative estimates to probe flies' optomotor acuity. The behavioral data is detailed, and the analysis parameters are well-explained.

We thank the Reviewer for the positive assessment of our study.

Weaknesses:

While the abstract promises to give us an assay to accelerate fly-to-human translation, the authors need to provide evidence to show that this is indeed the case. They have used PD lines extensively characterized by other groups, often with cheaper and easier-to-setup assays like negative geotaxis, and do not offer any new insights into them. The conceptual leap from a low-level behavioral phenotype, e.g. changes in walking speed, to recapitulating human PD progression is enormous, and the paper does not make any attempt to bridge it. It needs to be clarified how this assay provides a new understanding of the fly PD models, as the authors do not explore the cellular/circuit basis of the phenotypes. Similarly, they have assumed that the behavior they are looking at is an escape-from-predator response modulated by the central complex- is there any evidence to support these assumptions? Because of their rather superficial approach, the paper does not go beyond providing us with a collection of interesting but preliminary observations.

We thank the Reviewer for pointing out some limitations of our study. We would like to emphasize that what we perceive as the main advantage of performing single-fly and single-trial analyses is the access to rich data distributions that provide more fine-scale information compared to bulk assays. We think that this is exactly going one step closer to ‘bridging the enormous conceptual leap from a low-level behavioral phenotype, e.g. changes in walking speed, to recapitulating human PD progression’, and we showcase this in our study by comparing the distributions over the entire repertoire of behavioral responses across fly mutants. Nevertheless, we agree with the Reviewer that many more steps in this direction are needed to improve translatability. Therefore, we toned down the corresponding statements in the Abstract and in the Introduction. Moreover, to further emphasize the strength of sampling distributions of behavioral parameters across trials and individual flies, we complemented our comparisons of central tendencies with testing for potential differences in data dispersion, demonstrated in the novel Supplementary Figure S4.

Looming stimuli have been used to characterize flies’ escape behaviors. These studies uncovered a surprisingly rich behavioral repertoire (Zacarias et al., 2018), which was modulated by both sensory and motor context, e.g. walking speed at time of stimulus presentation (Card and Dickinson, 2008; Oram and Card, 2022; Zacarias et al., 2018). The neural basis of these behaviors was also investigated, revealing loom-sensitive neurons in the optic lobe and the giant fiber escape pathway (Ache et al., 2019; de Vries and Clandinin, 2012). Although less frequently, passing shadows were also employed as threat-inducing stimuli in flies (Gibson et al., 2015). We opted for this variant of the stimulus so that we could ensure that the shadow reached the same coordinates in all linear track concurrently, aiding data analysis and scalability. Similar to the cited study, we found the same behavioral repertoire as in studies with looming stimuli, with an equivalent dependence on walking speed, confirming that looming stimuli and passing shadows can both be considered as threat-inducing visual stimuli. We added a discussion on this topic to the main text.

Reviewer #2 (Public Review):

In this study, Kajtor et al investigated the use of a single-animal trial-based behavioral assay for the assessment of subtle changes in the locomotor behavior of different genetic models of Parkinson's disease of Drosophila. Different genotypes used in this study were Ddc-GAL4>UASParkin-275W and UAS- α-Syn-A53T. The authors measured Drosophila's response to predatormimicking passing shadow as a threatening stimulus. Along with these, various dopamine (DA) receptor mutants, Dop1R1, Dop1R2 and DopEcR were also tested.

The behavior was measured in a custom-designed apparatus that allows simultaneous testing of 13 individual flies in a plexiglass arena. The inter-trial intervals were randomized for 40 trials within 40 minutes duration and fly responses were defined into freezing, slowing down, and running by hierarchical clustering. Most of the mutant flies showed decreased reactivity to threatening stimuli, but the speed-response behavior was genotype invariant.

These data nicely show that measuring responses to the predator-mimicking passing shadows could be used to assess the subtle differences in the locomotion parameters in various genetic models of Drosophila.

The understanding of the manifestation of various neuronal disorders is a topic of active research. Many of the neuronal disorders start by presenting subtle changes in neuronal circuits and quantification and measurement of these subtle behavior responses could help one delineate the mechanisms involved. The data from the present study nicely uses the behavioral response to predator-mimicking passing shadows to measure subtle changes in behavior. However, there are a few important points that would help establish the robustness of this study.

We thank the Reviewer for the constructive comments and the positive assessment of our study.

(1) The visual threat stimulus for measuring response behavior in Drosophila is previously established for both single and multiple flies in an arena. A comparative analysis of data and the pros and cons of the previously established techniques (for example, Gibson et al., 2015) with the technique presented in this study would be important to establish the current assay as an important advancement.

We thank the Reviewer for this suggestion. We included the following discussion on measuring response behavior to visual threat stimuli in the revised manuscript.

Many earlier studies used looming stimulus, that is, a concentrically expanding shadow, mimicking the approach of a predator from above, to study escape responses in flies (Ache et al., 2019; Card and Dickinson, 2008; de Vries and Clandinin, 2012; Oram and Card, 2022; Zacarias et al., 2018) as well as rodents (Braine and Georges, 2023; Heinemans and Moita, 2024; Lecca et al., 2017). These assays have the advantage of closely resembling naturalistic, ecologically relevant threatinducing stimuli, and allow a relatively complete characterization of the fly escape behavior repertoire. As a flip side of their large degree of freedom, they do not lend themselves easily to provide a fully standardized, scalable behavioral assay. Therefore, Gibson et al. suggested a novel threat-inducing assay operating with moving overhead translational stimuli, that is, passing shadows, and demonstrated that they induce escape behaviors in flies akin to looming discs (Gibson et al., 2015). This assay, coined ReVSA (repetitive visual stimulus-induced arousal) by the authors, had the advantage of scalability, while constraining flies to a walking arena that somewhat restricted the remarkably rich escape types flies otherwise exhibit. Here we carried this idea one step further by using a screen to present the shadows instead of a physically moving paddle and putting individual flies to linear corridors instead of the common circular fly arena. This ensured that the shadow reached the same coordinates in all linear tracks concurrently and made it easy to accurately determine when individual flies encountered the stimulus, aiding data analysis and scalability. We found the same escape behavioral repertoire as in studies with looming stimuli and ReVSA (Gibson et al., 2015; Zacarias et al., 2018), with a similar dependence on walking speed (Oram and Card, 2022; Zacarias et al., 2018), confirming that looming stimuli and passing shadows can both be considered as threat-inducing visual stimuli.  

(2) Parkinson's disease mutants should be validated with other GAL-4 drivers along with DdcGAL4, such as NP6510-Gal4 (Riemensperger et al., 2013). This would be important to delineate the behavioral differences due to dopaminergic neurons and serotonergic neurons and establish the Parkinson's disease phenotype robustly.

We thank the Reviewer for point out this limitation. To address this, we repeated our key experiments in Fig.3. with both TH-Gal4 and NP6510-Gal4 lines, and their respective controls. These yielded largely similar results to the Ddc-Gal4 lines reported in Fig.3., reproducing the decreased speed and decreased overall reactivity of PD-model flies. Nevertheless, TH-Gal4 and NP6510-Gal4 mutants showed an increased propensity to stop. Stop duration showed a significant increase not only in α-Syn but also in Parkin fruit flies. These novel results have been added to the text and are demonstrated in Supplementary Figure S3.

(3) The DopEcR mutant genotype used for behavior analysis is w1118; PBac{PB}DopEcRc02142TM6B, Tb1. Balancer chromosomes, such as TM6B,Tb can have undesirable and uncharacterised behavioral effects. This could be addressed by removing the balancer and testing the DopEcR mutant in homozygous (if viable) or heterozygous conditions.

We appreciate the Reviewer's comment and acknowledge the potential for the DopEcR balancer chromosome to produce unintended behavioral effects. However, given that this mutant was not essential to our main conclusions, we opted not to repeat the experiment. Nevertheless, we now discuss the possible confounds associated with using the PBac{PB}DopEcRc02142 mutant allele over the balancer chromosome. “We recognize a limitation in using PBac{PB}DopEcRc02142 over the  TM6B, Tb¹ balancer chromosome, as the balancer itself may induce behavioral deficits in flies. We consider this unlikely, as the PBac{PB}DopEcRc02142 mutation demonstrates behavioral effects even in heterozygotes (Ishimoto et al., 2013). Additionally, to our knowledge, no studies have reported behavioral deficits in flies carrying the TM6B, Tb¹ balancer chromosome over a wild-type chromosome.”

(4) The height of the arena is restricted to 1mm. However, for the wild-type flies (Canton-S) and many other mutants, the height is usually more than 1mm. Also, a 1 mm height could restrict the fly movement. For example, it might not allow the flies to flip upside down in the arena easily. This could introduce some unwanted behavioral changes. A simple experiment with an arena of height at least 2.5mm could be used to verify the effect of 1mm height.

We thank the Reviewer for this comment, which prompted us to reassess the dimensions of the apparatus. The height of the arena was 1.5 mm, which we corrected now in the text. We observed that the arena did not restrict the flies walking and that flies could flip in the arena. We now include two Supplementary Movies to demonstrate this.

(5) The detailed model for Monte Carlo simulation for speed-response simulation is not described. The simulation model and its hyperparameters need to be described in more depth and with proper justification.

We thank the Reviewer for pointing out a lack of details with respect to Monte Carlo simulations. We used a nested model built from actual data distributions, without any assumptions. Accordingly, the stimulation did not have hyperparameters typical in machine learning applications, the only external parameter being the number of resamplings (3000 for each draw). We made these modeling choices clearer and expanded this part as follows.

“The effect of movement speed on the distribution of behavioral response types was tested using a nested Monte Carlo simulation framework (Fig. S5). This simulation aimed to model how different movement speeds impact the probability distribution of response types, comparing these simulated outcomes to empirical data. This approach allowed us to determine whether observed differences in response distributions are solely due to speed variations across genotypes or if additional behavioral factors contribute to the differences. First, we calculated the probability of each response type at different specific speed values (outer model). These probabilities were derived from the grand average of all trials across each genotype, capturing the overall tendency at various speeds. Second, we simulated behavior of virtual flies (n = 3000 per genotypes, which falls within the same order of magnitude as the number of experimentally recorded trials from different genotypes) by drawing random velocity values from the empirical velocity distribution specific to the given genotype and then randomly selecting a reaction based on the reaction probabilities associated with the drawn velocity (inner model). Finally, we calculated reaction probabilities for the virtual flies and compared it with real data from animals of the same genotype.

Differences were statistically tested by Chi-squared test.”

(6) The statistical analysis in different experiments needs revisiting. It wasn't clear to me if the authors checked if the data is normally distributed. A simple remedy to this would be to check the normality of data using the Shapiro-Wilk test or Kolmogorov-Smirnov test. Based on the normality check, data should be further analyzed using either parametric or non-parametric statistical tests. Further, the statistical test for the age-dependent behavior response needs revisiting as well. Using two-way ANOVA is not justified given the complexity of the experimental design. Again, after checking for the normality of data, a more rigorous statistical test, such as split-plot ANOVA or a generalized linear model could be used.

We thank the Reviewer for this comment. We performed Kolmogorov-Smirnov test for normality on the data distributions underlying Figure 3, and normality was rejected for all data distributions at p = 0.05, which justifies the use of the non-parametric Mann-Whitney U-test. Regarding ANOVA, we would like to point out that the ANOVA hypothesis test design is robust to deviations from normality (Knief and Forstmeier, 2021; Mooi et al., 2018). While the Kruskal-Wallis test is considered a reasonable non-parametric alternative of one-way ANOVA, there is no clear consensus for a non-parametric alternative of two-way ANOVA. Therefore, we left the two-way ANOVA for Figure 5 in place; however, to increase the statistical confidence in our conclusions, we performed Kruskal-Wallis tests for the main effect of age and found significant effects in all genotypes in accordance with the ANOVA, confirming the results (Stop frequency, DopEcR p = 0.0007; Dop1R1, p = 0.004; Dop1R2, p = 9.94 × 10^-5; w¹¹¹⁸, p = 9.89 × 10^-13; y¹ w⁶⁷c²³, p = 2.54 × 10^-5; Slowing down frequency, DopEcR, p = 0.0421; Dop1R1, p = 5.77 x 10^-6; Dop1R2, p = 0.011; w¹¹¹⁸, p = 2.62 x 10^-5; y¹ w⁶⁷c²³, p = 0.0382; Speeding up frequency, DopEcR, p = 0.0003; Dop1R1, p = 2.06 x 10^-7; Dop1R2, p = 2.19 x 10^-6; w¹¹¹⁸, p = 0.0044; y¹ w⁶⁷c²³, p = 1.36 x 10^-5). We also changed the post hoc Tukey-tests to post hoc Mann-Whitney tests in the text to be consistent with the statistical analyses for Figure 3. These resulted in very similar results as the Tukey-tests. Of note, there isn’t a straightforward way of correcting for multiple comparisons in this case as opposed to the Tukey’s ‘honest significance’ approach, we thus report uncorrected p values and suggest considering them at p = 0.01, which minimizes type I errors. These notes have been added to the ‘Data analysis and statistics’ Methods section.

(7) The dopamine receptor mutants used in this study are well characterized for learning and memory deficits. In the Parkinson's disease model of Drosophila, there is a loss of DA neurons in specific pockets in the central brain. Hence, it would be apt to use whole animal DA receptor mutants as general DA mutants rather than the Parkinson's disease model. The authors may want to rework the title to reflect the same.

We thank the Reviewer for this comment, which suggests that we were not sufficiently clear on the Drosophila lines with DA receptor mutations. We used Mi{MIC} random insertion lines for dopamine receptor mutants, namely y¹ w^*1; Mi{MIC}Dop1R1^MI04437 (BDSC 43773), y¹ w^*1; Mi{MIC}Dop1R2^MI08664 (BDSC 51098) (Harbison et al., 2019; Pimentel et al., 2016), and w¹¹¹⁸; PBac{PB}DopEcR^c02142/TM6B, Tb¹ (BDSC 10847) (Ishimoto et al., 2013; Petruccelli et al., 2020, 2016). These lines carried reported mutations in dopamine receptors, most likely generating partial knock down of the respective receptors. We made this clearer by including the full names at the first occurrence of the lines in Results (beyond those in Methods) and adding references to each of the lines.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Please think about focusing the manuscript either on the escape response or the PD pathology and provide additional evidence to demonstrate that you indeed have a novel system to address open questions in the field.

As detailed above, we now emphasize more that the main advantage of our single-trial-based approach lies in the appropriate statistical comparison of rich distributions of behavioral data. Please see our response to the ‘Weaknesses’ section for more details.

(2) Please explain the rationale for choosing the genetic lines and provide appropriate genetic controls in the experiments, e.g. trans-heterozygotes. Why use Ddc-Gal4 instead of TH or other specific Split-Gal4 lines?

We thank the Reviewer for this suggestion. We repeated our key experiments with TH-Gal4 and NP6510-Gal4 lines. Please see our response to Point #2 of Reviewer #2 for details.

(3) Please proofread the manuscript for ommissions. e.g. there's no legend for Fig 4b.

We respectfully point out that the legend is there, and it reads “b, Proportion of a given response type as a function of average fly speed before the shadow presentation. Top, Parkin and α-Syn flies. Bottom, Dop1R1, Dop1R2 and DopEcR mutant flies.”

Reviewer #2 (Recommendations For The Authors):

(1) In figure 2(c), representing the average walking speed data for different mutants would be useful to visually correlate the walking differences.

We thank the Reviewer for this suggestion. The average walking speed was added in a scatter plot format, as suggested in the next point of the Reviewer. 

(2) The data could be represented more clearly using scatter plots. Also, the color scheme could be more color-blindness friendly.

We thank the Reviewer for this suggestion. We added scatter plots to Fig.2c that indeed represent the distribution of behavioral responses better. We also changed the color scheme and removed red/green labeling.

(3) The manuscript should be checked for typos such as in line 252, 449, 484.

Thank you. We fixed the typos.

References

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Knief U, Forstmeier W. 2021. Violating the normality assumption may be the lesser of two evils. Behav Res Methods 53:2576–2590. doi:10.3758/s13428-021-01587-5

Lecca S, Meye FJ, Trusel M, Tchenio A, Harris J, Schwarz MK, Burdakov D, Georges F, Mameli M. 2017. Aversive stimuli drive hypothalamus-to-habenula excitation to promote escape behavior. Elife 6:1–16. doi:10.7554/eLife.30697

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Petruccelli E, Lark A, Mrkvicka JA, Kitamoto T. 2020. Significance of DopEcR, a G-protein coupled dopamine/ecdysteroid receptor, in physiological and behavioral response to stressors. J Neurogenet 34:55–68. doi:10.1080/01677063.2019.1710144

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Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Recommendations for the authors):

The authors have done an impressive job in responding to the previous critique and even gone beyond what was asked. I have only very minor comments on this excellent manuscript. The manuscript also needs some light editing for grammar and readability.

We have worked to improve the grammar and readability of the manuscript.

Comments:

Lines 227-234: At what age was tamoxifen administered to the various CreERTM mice?

We have updated the ages of the mice used in this study in the methods sections.

UMAP in Figure 5A is missing label for cluster 19.

The UMAP in Figure 5A has the label for cluster 19 at the center-bottom of the image.

Supplement Figure 6: Cluster 10 seems to be separate from the other AdvC clusters, and it includes some expression of Myh11 and Notch3. Further, there is low expression of Pdgfra in this cluster, which can be seen in panel B and panels D-I. Are the Pdgfra negative cells in the pie charts from cluster 10? Could the cells in this cluster by more LMC like than AdvC like?

We agree with the reviewer that the subcluster 10 of the fibroblasts cells are intriguing if only a minor population. When assessing just this population of cells, which is 77 cells out of 2261 total, 40 of the 77 were Pdgfra+ and of the 37 remaining Pdgfra- but 11 of those were still CD34+. Thus at least half of these cells could be expected to have the PdgfraCreERTM. Only 8 of the 37 were Pdgfra-Notch3+ while 12 cells were Pdgfra+Notch3+, and only 3 were Pdgfra-Myh11+ while 3 were Pdgfra+Myh11+. 26 of 77 cells were Pdgfra+Pdgfrb+ double positive, while 12 of 37 Pdgfra- cells were still Pdgfrb+. Additionally, within the 77 cells of subcluster 10 17 were positive for Scn3a (Nav1.3), 21were positive for Kcnj8 (Kir6.1), and 33 were positive for Cacna1c (Cacna1c) which are typically LMC markers would support the reviewers thinking that this group contains a fibroblast-LMC transitional cell type. Only 2 of 77 cells were positive for the BK subunit (Kcnma1), which is a classic smooth muscle marker. Another possibility is this population represents the Pdgfra+Pdgfrb+ valve interstitial cells we identified in our IF staining and in our reporter mice. Of note almost all cells in this cluster were Col3a1+ and Vim+. Even though we performed QC analysis to remove doublets, it is also possible some of these cells could represent doublets or contaminants, however the low % of Myh11 expression, a very highly expressed gene in LMCs especially compared to ion channels, would suggest this is less likely. Assessing the presence of this particular cell cluster in future RNAseq or with spatial transcriptomics will be enlightening.

Line 360. Proofread section title.

We have simplified this title to read “Optogenetic Stimulation of iCre-driven Channel Rhodopsin 2”

Lines 370-371. Are the length units supposed to be microns or millimeters?

We have corrected this to microns as was intended. Thank you for catching this error.

The resolution for each UMAP analysis should be stated, particularly for the identification of subclusters. How was the resolution chosen?

To select the optimal cluster resolution, we used Clustree with various resolutions. We examined the resulting tree to identify a resolution where the clusters were well-separated and biologically meaningful, ensuring minimal merging or splitting at higher resolutions. Our goal was to find a resolution that captures relevant cell subpopulations while maintaining distinct clusters without excessive fragmentation. We have now stated the resolution for the subclustering of the LECs, LMCs, and fibroblasts. We have also added greater detail regarding the total number of cells, QC analysis, and the marker identification criteria used to the methods sections. We used resolution of 0.5 for sub-clustering LMCs, 0.87 for LECs, and 1.0 for fibroblasts.  These details are now added to the manuscript.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This important work advances our understanding of the impact of malnutrition on hematopoiesis and subsequently infection susceptibility. Support for the overall claims is convincing in some respects and incomplete in others as highlighted by reviewers. This work will be of general interest to those in the fields of hematopoiesis, malnutrition, and dietary influence on immunity.

We would like to thank the editors for agreeing to review our work at eLife. We greatly appreciate them assessing this study as important and of general interest to multiple fields, as well as the opportunity to respond to reviewer comments. Please find our responses to each reviewer below.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, the authors used a chronic murine dietary restriction model to study the effects of chronic malnutrition on controls of bacterial infection and overall immunity, including cellularity and functions of different immune cell types. They further attempted to determine whether refeeding can revert the infection susceptibility and immunodeficiency. Although refeeding here improves anthropometric deficits, the authors of this study show that this is insufficient to recover the impairments across the immune cell compartments.

Strengths:

The manuscript is well-written and conceived around a valid scientific question. The data supports the idea that malnutrition contributes to infection susceptibility and causes some immunological changes. The malnourished mouse model also displayed growth and development delays. The work's significance is well justified. Immunological studies in the malnourished cohort (human and mice) are scarce, so this could add valuable information.

Weaknesses:

The assays on myeloid cells are limited, and the study is descriptive and overstated. The authors claim that "this work identifies a novel cellular link between prior nutritional state and immunocompetency, highlighting dysregulated myelopoiesis as a major." However, after reviewing the entire manuscript, I found no cellular mechanism defining the link between nutritional state and immunocompetency.

We thank the reviewer for deeming our work significant and noting the importance of the study. We appreciate the referee’s point regarding the lack of specific cellular functional data for innate immune cells and have modified the conclusions stated in text to more accurately reflect the results presented.

Reviewer #2 (Public review):

Summary:

Sukhina et al. use a chronic murine dietary restriction model to investigate the cellular mechanisms underlying nutritionally acquired immunodeficiency as well as the consequences of a refeeding intervention. The authors report a substantial impact of undernutrition on the myeloid compartment, which is not rescued by refeeding despite rescue of other phenotypes including lymphocyte levels, and which is associated with maintained partial susceptibility to bacterial infection.

Strengths:

Overall, this is a nicely executed study with appropriate numbers of mice, robust phenotypes, and interesting conclusions, and the text is very well-written. The authors' conclusions are generally well-supported by their data.

Weaknesses:

There is little evaluation of known critical drivers of myelopoiesis (e.g. PMID 20535209, 26072330, 29218601) over the course of the 40% diet, which would be of interest with regard to comparing this chronic model to other more short-term models of undernutrition.

Further, the microbiota, which is well-established to be regulated by undernutrition (e.g. PMID 22674549, 27339978, etc.), and also well-established to be a critical regulator of hematopoiesis/myelopoiesis (e.g. PMID 27879260, 27799160, etc.), is completely ignored here.

We thank the reviewer for agreeing that the data presented support the stated conclusions and noting the experimental rigor.  The referee highlights two important areas for future mechanistic investigation that we agree are of great importance and relevant to the submitted study. We have included further discussion of the potential role cytokines and the microbiota might play in our model.

Reviewer #3 (Public review):

Summary:

Sukhina et al are trying to understand the impacts of malnutrition on immunity. They model malnutrition with a diet switch from ad libitum to 40% caloric restriction (CR) in post-weaned mice. They test impacts on immune function with listeriosis. They then test whether re-feeding corrects these defects and find aspects of emergency myelopoiesis that remain defective after a precedent period of 40% CR. Overall, this is a very interesting observational study on the impacts of sudden prolonged exposure to less caloric intake.

Strengths:

The study is rigorously done. The observation of lasting defects after a bout of 40% CR is quite interesting. Overall, I think the topic and findings are of interest.

Weaknesses:

While the observations are interesting, in this reviewer's opinion, there is both a lack of mechanistic understanding of the phenomena and also some lack of resolution/detail about the phenomena itself. Addressing the following major issues would be helpful towards aspects of both:

(1) Is it calories, per se, or macro/micronutrients that drive these phenotypes observed with 40% CR. At the least, I would want to see isocaloric diets (primarily protein, fat, or carbs) and then some of the same readouts after 40% CR. Ie does low energy with relatively more eg protein prevent immunosuppression (as is commonly suggested)? Micronutrients would be harder to test experimentally and may be out of the scope of this study. However, it is worth noting that many of the malnutrition-associated diseases are micronutrient deficiencies.

(2) Is immunosuppression a function of a certain weight loss threshold? Or something else? Some idea of either the tempo of immunosuppression (happens at 1, in which weight loss is detected; vs 2-3, when body length and condition appear to diverge; or 5 weeks), or grade of CR (40% vs 60% vs 80%) would be helpful since the mechanism of immunosuppression overall is unclear (but nailing it may be beyond the scope of this communication).

(3) Does an obese mouse that gets 40% CR also become immunodeficient? As it stands, this ad libitum --> 40% CR model perhaps best models problems in the industrial world (as opposed to always being 40% CR from weaning, as might be more common in the developing world), and so modeling an obese person losing a lot of weight from CR (like would be achieved with GLP-1 drugs now) would be valuable to understanding generalizability.

(4) Generalizing this phenomenon as "bacterial" with listeriosis, which is more like a virus in many ways (intracellular phase, requires type I IFN, etc.) and cannot be given by the natural route of infection in mice, may not be most accurate. I would want to see an experiment with E.Coli, or some other bacteria, to test the statement of generalizability (ie is it bacteria, or type I IFN-pathway dominant infections, like viruses). If this is unique listeriosis, it doesn't undermine the story as it is at all, but it would just require some word-smithing.

(5) Previous reports (which the authors cite) implicate Leptin, the levels of which scale with fat mass, as "permissive" of a larger immune compartment (immune compartment as "luxury function" idea). Is their phenotype also leptin-mediated (ie leptin AAV)?

(6) The inability of re-feeding to "rescue" the myeloid compartment is really interesting. Can the authors do a bone marrow transplantation (CR-->ad libitum) to test if this effect is intrinsic to the CR-experienced bone marrow?

(7) Is the defect in emergency myelopoiesis a defect in G-CSF? Ie if the authors injected G-CSF in CR animals, do they equivalently mobilize neutrophils? Does G-CSF supplementation (as one does in humans) rescue host defense against Listeria in the CR or re-feeding paradigms?

We thank the reviewer for considering our work of interest and noting the rigor with which it was conducted. The referee raises several excellent mechanistic hypotheses and follow-up studies to perform. We agree that defining the specific dietary deficiency driving the phenotypes is of great interest. The relative contribution of calories versus macro- and micronutrients is an area we are interested in exploring in future studies, especially given the literature on the role of micronutrients in malnutrition driven wasting as the referee notes. We also agree that it will be key to determine whether non-hematopoietic cells contribute as well as the role of soluble factors such G-CSF and Leptin in mediating the immunodeficiency all warrant further study. Likewise, it will be important to evaluate how malnutrition impacts other models of infection to determine how generalizable these phenomena are. We have added these points to the discussion section as limitations of this study.

Regarding how the phenotypes correspond to the timing of the immunosuppression relative to weight loss, we have performed new kinetics studies to provide some insight into this area. We now find that neutropenia in peripheral blood can be detected after as little as one week of dietary restriction, with neutropenia continuing to decline after prolonged restriction. These findings indicate that the impact on myeloid cell production are indeed rapid and proceed maximum weight loss, though the severity of these phenotypes does increase as malnutrition persists. We wholeheartedly agree with the reviewer that it will be interesting to explore whether starting weight impacts these phenotypes and whether similar findings can be made in obese animals as they are treated for weight loss.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

In this study, the authors used a chronic murine dietary restriction model to study the effects of chronic malnutrition on controls of bacterial infection and overall immunity, including cellularity and functions of different immune cell types. They further attempted to determine whether refeeding can revert the infection susceptibility and immunodeficiency. Although refeeding here improves anthropometric deficits, the authors of this study show that this is insufficient to recover the impairments across the immune cell compartments. The authors claim that "this work identifies a novel cellular link between prior nutritional state and immunocompetency, highlighting dysregulated myelopoiesis as a major." However, after reviewing the entire manuscript, I could not find any cellular mechanism defining the link between nutritional state and immunocompetency. The assays on myeloid cells are limited, and the study is descriptive and overstated.

Major concerns:

(1) Malnutrition has entirely different effects on adults and children. In this study, 6-8 weeks old C57/Bl6 mice were used that mimic adult malnutrition. I do not understand then why the refeeding strategy for inpatient treatment of severely malnourished children was utilized here.

(2) Figure 1g shows BM cellularity is reduced, but the authors claim otherwise in the text.

(3) What is the basis of the body condition score in Figure 1d? It will be good to have it in the supplement.

(4) Listeria monocytogenes cause systemic infection, so bioload was not determined in tissues beyond the liver.

(5) Figure 3; T cell functional assays were limited to CD8 T cells and lymphocytes isolated from the spleen.

(6) Why was peripheral cell count not considered? Discrepancies exist with the absolute cell number and relative abundance data, except for the neutrophil and monocyte data, which makes the data difficult to interpret. For example, for B cells, CD4 and CD8 cells.

(7) Also, if mice exhibit thymic atrophy, why does % abundance data show otherwise? Overall, the data is confusing to interpret.

(8) No functional tests for neutrophil or monocyte function exist to explain the higher bacterial burden in the liver or to connect the numbers with the overall pathogen load

The rationale for examining both innate and adaptive immunity is not clear-it is even more unclear since the exact timelines for examining both innate and adaptive immunity (D0 and D5) were used.

(9) Figure 2e doesn't make sense - why is spleen cellularity measured when bacterial load is measured in the liver?

(10) Although it is claimed that emergency myelopoiesis is affected, no specific marker for emergency myelopoiesis other than cell numbers was studied.

(11) I suggest including neutrophil effector functions and looking for real markers of granulopoiesis, such as Cebp-b. Since the authors attempted to examine the entirety of immune responses, it is better to measure cell abundance, types, and functions beyond the spleen. Consider the systemic spread of m while measuring bioload.

(12) Minor grammatical errors - please re-read the entire text and correct grammatical errors to improve the flow of the text.

(13) Sample size details missing

(14) Be clear on which marks were used to identify monocytes. Using just CD11b and Ly6G is insufficient for neutrophil quantification.

(15) Also, instead of saying "undernourished patients," say "patients with undernutrition" - change throughout the text. I would recommend numbering citations (as is done for Nature citations) to ease in following the text, as there are areas when there are more than ten citations with author names.

(16) No line numbers are provided

(17) Abstract

-  What does accelerated contraction mean?

-  "In" is repeated in a sentence

-  Be clear that the study is done in a mouse model - saying just "animals" is not sufficient

-  Indicate how malnutrition is induced in these mice

(18) Introduction

-  "restriction," "immune organs," - what is this referring to?

-  You mention lymphoid tissue and innate and adaptive immunity, which doesn't make sense.

Please correct this.

-  You mention a lot of lymphoid tissues, i.e. lymphoid mass gain, but how about the bone marrow and spleen, which are responsible for most innate immune compartments?

(19) Results

a) Figure 1

-  Why 40% reduced diet?

-  It would be interesting to report if the organs are smaller relative to body weight. It makes sense that the organ weight is lower in the 40RD mice, especially since they are smaller, so the novelty of this data is not apparent (Figure 1f).

-  You say, "We observed a corresponding reduction in the cellularity of the spleen and thymus, while the cellularity of the bone marrow was unaffected (Fig. 1g)." however, your BM data is significant, so this statement doesn't reflect the data you present, please correct.

b) Figure 2

- Figure 2d - what tissue is this from, mentioned in the figure? And measure cellularity there. The rationale for why you look only at the spleen here is weak. Also, we would benefit from including the groups without infection here for comparison purposes.

c) Figure 3

- The rationale for why you further looked at T cells is weak, mainly because of the following sentence. "Despite this overall loss in lymphocyte number, the relative frequency of each population was either unchanged or elevated, indicating that while malnutrition leads to a global reduction in immune cell numbers, lymphocytes are less impacted than other immune cell populations (Supplemental 1)." Please explain in the main text.

d) Figure 4

-  You say the peak of the adaptive immune response, but you never looked at the peak of adaptive immune - when is this? If you have the data, please show it. You also only show d0 and d5 post-infection data for adaptive immunity, so I am unsure where this statement comes from.

-  How did you identify neutrophils and monocytes through flow cytometry? Indicate the markers used. Also, your text does not match your data; please correct it. i.e. monocyte numbers reduced, and relative abundance increased, but your text doesn't say this.

-  Show the flow graph first then, followed by the quantification.

-  The study would benefit from examining markers of emergency myelopoiesis such as Cebpb through qPCR.

-  Although the number of neutrophils is lower in the BM and spleen, how does this relate to increased bacterial load in the liver? This is especially true since you did not quantify neutrophil numbers in the liver.

e) Figure 6

-  Some figures are incorrectly labelled.

-  For the refeeding data, also include the data from the 40RD group to compare the level of recovery in the outcome measures.

(20) Discussion

-  You claim that monocytes are reduced to the same extent as neutrophils, but this is not true.

Please correct.

-  Indicate some limitations of your work.

We thank the reviewer for offering these recommendations and the constructive comments. 

Several comments raised concerns over the rationale or reasoning behind aspects of the experimental design or the data presented, which we would like to clarify:

• Regarding the refeeding protocol, we apologize for the confusion for the rationale. We based our methodology on the general guidelines for refeeding protocols for malnourished people. We elected to increase food intake 10% daily to avoid risk of refeeding syndrome or other complications. Our method is by no means replicates the administration of specific vitamins, minerals, electrolytes, nor precise caloric content as would be given to a human patient. The citation provided offers information from the WHO regarding the complications that can arise during refeeding syndrome, which while it is from a document on pediatric care, we did not mean to imply that our method modeled refeeding intervention for children. We have modified the text to avoid this confusion.

• The reviewer requested more clarity on why we studied both the innate and adaptive immune system as well as why we chose the time points studied. As referenced in the manuscript, prior work has observed that caloric restriction, fasting, and malnutrition all can impact the adaptive immune system. Given these previous findings, we felt it important to evaluate how malnutrition affected adaptive immune cell populations in our model. To this end, we provide data tracking the course of T-cell responses from the start of infection through day 14 at the time that the response undergoes contraction. However, since we find that bacterial burden is not properly controlled at earlier time points (day 5), when it is understood the innate immune system is more critical for mediating pathogen clearance, we elected to better characterize the effect malnutrition had on innate immune populations, something less well described in the literature. As phenotypes both in bacterial burden and within innate immune populations were observable as early as day 5, we chose to focus on that time point rather than later time points when readouts could be further confounded by secondary or compounding effects by the lack of early control of infection. We have tried to make this rationale clear in the text and have made changes to further emphasize this reasoning.

• The reviewer also requested an explaination over why bacterial burden was measured in the liver and the immune response was measured in the spleen. While the reviewer is correct that our model is a systemic infection, it is well appreciated that bacteria rapidly disseminate to the liver and spleen and these organs serve as major sites of infection. Given the central role the spleen plays in organizing both the innate and adaptive immune response in this model, it is common practice in the field to phenotype immune cell populations in the spleen, while using the liver to quantify bacterial burden (see PMID: 37773751 as one example of many). We acknowledge this does not provide the full scope of bacterial infection or the immune response in every potentially affected tissue, but nonetheless believe the interpretation that malnourished and previously malnourished animals do not properly control infection and their immune responses are blunted compared to controls still stands.

The reviewer raised several points about di3erences in the results for cell frequency and absolute number and why these may deviate in some circumstances. For example, the reviewer notes that we observe thymic atrophy yet the frequency of peripheral T-cells does not decline. It should be noted that absolute number can change when frequency does not and vice versa, due to changes in other cell types within the studied population of cells. As in the case of peripheral lymphocytes in our study, the frequency can stay the same or even increase when the absolute number declines (Supplemental 1). This can occur if other populations of cells decrease further, which is indeed the case as the loss of myeloid cells is greater than that of lymphocytes. Hence, we find that the frequency of T and B cells is unchanged or elevated, despite the loss in absolute number of peripheral cell, which is our stated interpretation. We believe this is consistent with our overall observations and is why it is important to report both frequency and absolute number, as we have done. 

We have made the requested changes to the text to address the reviewers concerns as noted to improve clarity and accuracy for the description of experiments, results, and overall conclusions drawn in the manuscript. We have also included a discussion of the limitations of our work as well as additional areas for future investigation that remain open. 

Reviewer #2 (Recommendations for the authors):

Regarding the known drivers of myelopoiesis, can the authors quantify circulating levels of relevant immune cytokines (e.g. type I and II IFNs, GM-CSF, etc.)?

Regarding the microbiota (point #2), how dramatically does this undernutrition modulate the microbiota both in terms of absolute load and community composition, and how effectively/quickly is this rescued by refeeding?

We thank the reviewer for raising these recommendations. We agree that the role of circulating factors like cytokines and growth factors in contributing to the defects in myelopoiesis is of interest and is the focus of future work. Similarly, the impact of malnutrition on the microbiota is of great interest and has been evaluated by other groups in separate studies. How the known impact of malnutrition on the microbiota affects the phenotypes we observe in myelopoiesis is unclear and warrants future investigation. We have added these points to the discussion section as limitations of this study.

Author Response:

In the Weaknesses, Reviewer 3 suggests that in the Discussion, we comment upon whether WRN ATPase/3’-5’ helicase and WRNIP1 ATPase work on Y-family Pols additively or synergistically to raise fidelity. However, in the Discussion on page 20, we do comment on the role of WRN and WRNIP1 ATPase activities in conferring an additive increase in the fidelity of TLS by Y-family Pols.

Author Response:

We thank the reviewers for their thoughtful feedback and appreciate their recognition of the value of our findings. In response, we are refining the manuscript to clarify key terminology, more clearly describe our image analysis workflows, and temper the interpretation of our results where appropriate. We are planning to perform additional experiments to further investigate the specificity of mRNA co-localization between BK and CaV1.3 channels. We acknowledge the importance of understanding ensemble trafficking dynamics and the functional role of pre-assembly at the plasma membrane, and we plan to explore these questions in future work. We look forward to submitting a revised manuscript that addresses the reviewers’ comments in detail.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Desingu et al. show that JEV infection reduces SIRT2 expression. Upon JEV infection, 10-day-old SIRT2 KO mice showed increased viral titer, more severe clinical outcomes, and reduced survival. Conversely, SIRT2 overexpression reduced viral titer, clinical outcomes, and improved survival. Transcriptional profiling shows dysregulation of NF-KB and expression of inflammatory cytokines. Pharmacological NF-KB inhibition reduced viral titer. The authors conclude that SIRT2 is a regulator of JEV infection.

This paper is novel because sirtuins have been primarily studied for aging, metabolism, stem cells/regeneration. Their role in infection has not been explored until recently. Indeed, Barthez et al. showed that SIRT2 protects aged mice from SARS-CoV-2 infection (Barthez, Cell Reports 2025). Therefore, this is a timely and novel research topic. Mechanistically, the authors showed that SIRT2 suppresses the NF-KB pathway. Interestingly, SIRT2 has also been shown recently to suppress other major inflammatory pathways, such as cGAS-STING (Barthez, Cell Reports 2025) and the NLRP3 inflammasome (He, Cell Metabolism 2020; Luo, Cell Reports 2019). Together, these findings support the emerging concept that SIRT2 is a master regulator of inflammation.

Weaknesses:

(1) Figures 2 and 3. Although SIRT2 KO mice showed increased viral titer, more severe clinical outcomes, and reduced survival upon JEV infection, the difference is modest because even WT mice exhibited very severe disease at this viral dose. The authors should perform the experiment using a sub-lethal viral dose for WT mice, to allow the assessment of increased clinical outcomes and reduced survival in KO mice.

(2) Figure 5K-N, the authors examined the expression of inflammatory cytokines in WT and SIRT2 KO cells upon JEV infection, in line with the dysregulation of NF-kB. It has been shown recently that SIRT2 also regulates the cGAS-STING pathway (Barthez, Cell Reports 2025) and the NLRP3 inflammasome (He, Cell Metabolism 2020; Luo, Cell Reports 2019). Do you also observe increased IFNb, IL1b, and IL18 in SIRT2 KO cells upon JEV infection? This may indicate that SIRT2 regulates systemic inflammatory responses and represents a potent protection upon viral infection. This is particularly important because in Figure 7F, the authors showed that SIRT2 overexpression reduced viral load even when NF-KB is inhibited, suggesting that NF-KB is not the only mediator of SIRT2 to suppress viral infection.

We thank the reviewer for the valuable recommendation. We are willing to conduct an experiment using a sub-lethal viral dose in wild-type (WT) mice to assess increased clinical outcomes and reduced survival in knockout (KO) mice, as recommended.

Furthermore, we acknowledge reviewers' comments that SIRT2 regulates systemic inflammatory responses and provides potent protection against viral infection. Additionally, NF-κB is not the only mediator of SIRT2's suppression of viral infection; other possible molecular mechanisms are also involved in this process.

Reviewer #2 (Public review):

The manuscript by Desingu et al., explores the role of SIRT2 in regulating Japanese Encephalitis Virus (JEV) replication and disease progression in rodent models. Using both an in vitro and an in vivo approach, the authors demonstrate that JEV infection leads to decreased SIRT2 expression, which they hypothesize is exploited by JEV for viral replication. To test this hypothesis, the authors utilize SIRT2 inhibition (via AGK2 or genetic knockout) and demonstrate that it leads to increased viral load and worsens clinical outcomes in JEV-infected mice. Conversely, SIRT2 overexpression via an AAV delivery system reduces viral replication and improves survival among infected mice. The study proposes a mechanism in which SIRT2 suppresses JEV-induced autophagy and inflammation by deacetylating NF-κB, thereby reducing Beclin-1 expression (an NF-κB-dependent gene) and autophagy, which the authors consider a pathway that JEV exploits for replication. Transcriptomic analysis further supports that SIRT2 deficiency leads to NF-κB-driven cytokine hyperactivation. Additionally, pharmacological inhibition of NF-κB using Bay 11 (an IKK inhibitor) results in reduced viral load and improved clinical pathology in WT and SIRT2 KO mice. Overall, the findings from Desingu et al. are generally supported by the data and suggest that targeting SIRT2 may serve as a promising therapeutic approach for JEV infection and potentially other RNA viruses that SIRT2 helps control. However, the paper does fall short in some areas. Please see below for our comments to help improve the paper.

We thank the reviewer for the valuable recommendation. We are willing to measure NF-kB acetylation in AdSIRT2 JEV-infected cells compared to WT-infected cells, to verify that the acetylation of NF-kB is truly linked to SIRT2 expression levels as per the reviewers' suggestion.

We are willing to conduct an experiment using a sub-lethal viral dose in wild-type (WT) mice to assess increased clinical outcomes and reduced survival in knockout (KO) mice, as recommended.

We are accepting the reviewer's suggestion that AGK2 can also inhibit other Sirtuins. Thus, to test the contribution of other Sirtuins, the experiment could be repeated using wild-type and Sirt2 KO mice. We are willing to conduct the AGK2 experiment using JEV-infected wild-type and Sirt2 knockout mice.

Author response:

Reviewer #1 (Public Review):

Fombellida-Lopez and colleagues describe the results of an ART intensification trial in people with HIV infection (PWH) on suppressive ART to determine the effect of increasing the dose of one ART drug, dolutegravir, on viral reservoirs, immune activation, exhaustion, and circulating inflammatory markers. The authors hypothesize that ART intensification will provide clues about the degree to which low-level viral replication is occurring in circulation and in tissues despite ongoing ART, which could be identified if reservoirs decrease and/or if immune biomarkers change. The trial design is straightforward and well-described, and the intervention appears to have been well tolerated. The investigators observed an increase in dolutegravir concentrations in circulation, and to a lesser degree in tissues, in the intervention group, indicating that the intervention has functioned as expected (ART has been intensified in vivo). Several outcome measures changed during the trial period in the intervention group, leading the investigators to conclude that their results provide strong evidence of ongoing replication on standard ART. The results of this small trial are intriguing, and a few observations in particular are hypothesis-generating and potentially justify further clinical trials to explore them in depth. However, I am concerned about over-interpretation of results that do not fully justify the authors' conclusions.

We thank Reviewer #1 for their thoughtful and constructive comments, which will help us clarify and improve the manuscript. Below, we address each of the reviewer’s points and describe the changes that we intend to implement in the revised version. We acknowledge the reviewer’s concern regarding potential over-interpretation of certain findings, and we will take particular care to ensure that all conclusions are supported by the data and framed within the exploratory nature of the study.

(1) Trial objectives: What was the primary objective of the trial? This is not clearly stated. The authors describe changes in some reservoir parameters and no changes in others. Which of these was the primary outcome? No a priori hypothesis / primary objective is stated, nor is there explicit justification (power calculations, prior in vivo evidence) for the small n, unblinded design, and lack of placebo control. In the abstract (line 36, "significant decreases in total HIV DNA") and conclusion (lines 244-246), the authors state that total proviral DNA decreased as a result of ART intensification. However, in Figures 2A and 2E (and in line 251), the authors indicate that total proviral DNA did not change. These statements are confusing and appear to be contradictory. Regarding the decrease in total proviral DNA, I believe the authors may mean that they observed transient decrease in total proviral DNA during the intensification period (day 28 in particular, Figure 2A), however this level increases at Day 56 and then returns to baseline at Day 84, which is the source of the negative observation. Stating that total proviral DNA decreased as a result of the intervention when it ultimately did not is misleading, unless the investigators intended the day 28 timepoint as a primary endpoint for reservoir reduction - if so, this is never stated, and it is unclear why the intervention would then be continued until day 84? If, instead, reservoir reduction at the end of the intervention was the primary endpoint (again, unstated by the authors), then it is not appropriate to state that the total proviral reservoir decreased significantly when it did not.

We agree with the reviewer that the primary objective of the study was not explicitly stated in the submitted manuscript. We will clarify this in the revised manuscript. As registered on ClinicalTrials.gov (NCT05351684), the primary outcome was defined as “To evaluate the impact of treatment intensification at the level of total and replication-competent reservoir (RCR) in blood and in tissues”, with a time frame of 3 months. Accordingly, our aim was to explore whether any measurable reduction in the HIV reservoir (total or replication-competent) occurred during the intensification period, including at day 28, 56, or 84. The protocol did not prespecify a single time point for this effect to occur, and the exploratory design allowed for detection of transient or sustained changes within the intensification window.

We recognize that this scope was not clearly articulated in the original text and may have led to confusion in interpreting the transient drop in total HIV DNA observed at day 28. While total DNA ultimately returned to baseline by the end of intensification, the presence of a transient reduction during this 3-month window still fits within the framework of the study’s registered objective. Moreover, although the change in total HIV DNA was transient, it aligns with the consistent direction of changes observed across the multiple independent measures, including CA HIV RNA, RNA/DNA ratio and intact HIV DNA, collectively supporting a biological effect of intensification.

We would also like to stress that this is the first clinical trial ever, in which an ART intensification is performed not by adding an extra drug but by increasing the dosage of an existing drug. Therefore, we were more interested in the overall, cumulative, effect of intensification throughout the entire trial period, than in differences between groups at individual time points. We will clarify in the manuscript that this was a proof-of-concept phase 2 study, designed to generate biological signals rather than confirm efficacy in a powered comparison. The absence of a pre-specified statistical endpoint or sample size calculation reflects the exploratory nature of the trial.

(2) Intervention safety and tolerability: The results section lacks a specific heading for participant safety and tolerability of the intervention. I was wondering about clinically detectable viremia in the study. Were there any viral blips? Was the increased DTG well tolerated? This drug is known to cause myositis, headache, CPK elevation, hepatotoxicity, and headache. Were any of these observed? What is the authors' interpretation of the CD4:8 ratio change (line 198)? Is this a significant safety concern for a longer duration of intensification? Was there also a change in CD4% or only in absolute counts? Was there relative CD4 depletion observed in the rectal biopsy samples between days 0 and 84? Interestingly, T cells dropped at the same timepoints that reservoirs declined... how do the authors rule out that reservoir decline reflects transient T cell decline that is non-specific (not due to additional blockade of replication)?

We will improve the Methods section to clarify how safety and tolerability were assessed during the study. Safety evaluations were conducted on day 28 and day 84 and included a clinical examination and routine laboratory testing (liver function tests, kidney function, and complete blood count). Medication adherence was also monitored through pill counts performed by the study nurses.

No virological blips above 50 copies/mL were observed and no adverse events were reported by participants during the 3-month intensification period. Although CPK levels were not included in the routine biological monitoring, no participant reported muscle pain or other symptoms suggestive of muscle toxicity.

The CD4:CD8 ratio decrease noted during intensification was not associated with significant changes in absolute CD4 or CD8 counts, as shown in Figure 5. We interpret this ratio change as a transient redistribution rather than an immunological risk, therefore we do not consider it to represent a safety concern.

We would like to clarify that CD4⁺ T-cell counts did not significantly decrease in any of the treatment groups, as shown in Figure 5. The apparent decline observed concerns the CD4/CD8 ratio, which transiently dropped, but not the absolute number of CD4⁺ T cells.

(3) The investigators describe a decrease in intact proviral DNA after 84 days of ART intensification in circulating cells (Figure 2D), but no changes to total proviral DNA in blood or tissue (Figures 2A and 2E; IPDA does not appear to have been done on tissue samples). It is not clear why ART intensification would result in a selective decrease in intact proviruses and not in total proviruses if the source of these reservoir cells is due to ongoing replication. These reservoir results have multiple interpretations, including (but not limited to) the investigators' contention that this provides strong evidence of ongoing replication. However, ongoing replication results in the production of both intact and mutated/defective proviruses that both contribute to reservoir size (with defective proviruses vastly outnumbering intact proviruses). The small sample size and well-described heterogeneity of the HIV reservoir (with regard to overall size and composition) raise the possibility that the study was underpowered to detect differences over the 84-day intervention period. No power calculations or prior studies were described to justify the trial size or the duration of the intervention. Readers would benefit from a more nuanced discussion of reservoir changes observed here.

We sincerely thank the reviewer for this insightful comment. We fully agree that the reservoir dynamics observed in our study raise several possible interpretations, and that its complexity, resulting from continuous cycles of expansion and contraction, reflects the heterogeneity of the latent reservoir.

Total HIV DNA in PBMCs showed a transient decline during intensification (notably at day 28), ultimately returning to baseline by day 84. This biphasic pattern may reflect the combined effects of suppression of ongoing low-level replication by an increased DTG dosage, followed by the expansion of infected cell clones (mostly harboring defective proviruses). In other words, the transient decrease in total (intact + defective) DNA at day 28 may be due to an initial decrease in newly infected cells upon ART intensification, however at the subsequent time points this effect was masked by proliferation (clonal expansion) of infected cells with defective proviruses. This explains why the intact proviruses decreased, but the total proviruses did not change, between days 0 and 84.

Importantly, we observed a significant decrease in intact proviral DNA between day 0 and day 84 in the intensification group (Figure 2D). We will highlight this result more clearly in the revised manuscript, as it directly addresses the study’s primary objective: assessing the impact of intensification on the replication-competent reservoir. In comparison, as the reviewer rightly points out, total HIV DNA includes over 90% defective genomes, which limits its interpretability as a biomarker of biologically relevant reservoir changes.

In addition, other reservoir markers, such as cell-associated unspliced RNA and RNA/DNA ratios, also showed consistent trends supporting a modest but biologically relevant effect of intensification. Even in the absence of sustained changes in total HIV DNA, the coherence across these independent measures suggests a signal indicative of ongoing replication in at least some individuals, and at specific timepoints.

Regarding tissue reservoirs, the lack of substantial change in total HIV DNA between days 0 and 84 is also in line with the predominance of defective sequences in these compartments. Moreover, the limited increase in rectal tissue dolutegravir levels during intensification (from 16.7% to 20% of plasma concentrations) may have limited the efficacy of the intervention in this site.

As for the IPDA on rectal biopsies, we attempted the assay using two independent DNA extraction methods (Promega Reliaprep and Qiagen Puregene), but both yielded high DNA Shearing Index values, and intact proviral detection was successful in only 3 of 40 samples. Given the poor DNA integrity and weak signals, these results were not interpretable.

That said, we fully acknowledge the limitations of our study, especially the small sample size, and we agree with the reviewer that caution is needed when interpreting these findings. In the revised manuscript, we will adopt a more measured tone in the discussion, clearly stating that these observations are exploratory and hypothesis-generating, and require confirmation in larger, more powered studies. Nonetheless, we believe that the convergence of multiple reservoir markers pointing in the same direction constitutes a potentially meaningful biological signal that deserves further investigation.

(4) While a few statistically significant changes occurred in immune activation markers, it is not clear that these are biologically significant. Lines 175-186 and Figure 3: The change in CD4 cells + for TIGIT looks as though it declined by only 1-2%, and at day 84, the confidence interval appears to widen significantly at this timepoint, spanning an interquartile range of 4%. The only other immune activation/exhaustion marker change that reached statistical significance appears to be CD8 cells + for CD38 and HLA-DR, however, the decline appears to be a fraction of a percent, with the control group trending in the same direction. Despite marginal statistical significance, it is not clear there is any biological significance to these findings; Figure S6 supports the contention that there is no significant change in these parameters over time or between groups. With most markers showing no change and these two showing very small changes (and the latter moving in the same direction as the control group), these results do not justify the statement that intensifying DTG decreases immune activation and exhaustion (lines 38-40 in the abstract and elsewhere).

We agree with the reviewer that the observed changes in immune activation and exhaustion markers were modest. We will revise the manuscript to reflect this more accurately. We will also note that these differences, while statistically significant (e.g., in TIGIT+ CD4+ T cells and CD38+HLA-DR+ CD8+ T cells), were limited in magnitude. We will explicitly acknowledge these limitations and interpret the findings with appropriate caution.

(5) There are several limitations of the study design that deserve consideration beyond those discussed at line 327. The study was open-label and not placebo-controlled, which may have led to some medication adherence changes that confound results (authors describe one observation that may be evidence of this; lines 146-148). Randomized/blinded / cross-over design would be more robust and help determine signal from noise, given relatively small changes observed in the intervention arm. There does not seem to be a measurement of key outcome variables after treatment intensification ceased - evidence of an effect on replication through ART intensification would be enhanced by observing changes once intensification was stopped. Why was intensification maintained for 84 days? More information about the study duration would be helpful. Table 1 indicates that participants were 95% male. Sex is known to be a biological variable, particularly with regard to HIV reservoir size and chronic immune activation in PWH. Worldwide, 50% of PWH are women. Research into improving management/understanding of disease should reflect this, and equal participation should be sought in trials. Table 1 shows differing baseline reservoir sizes between the control and intervention groups. This may have important implications, particularly for outcomes where reservoir size is used as the denominator.

We will expand the limitations section to address several key aspects raised by the reviewer: the absence of blinding and placebo control, the predominantly male study population, and the lack of post-intervention follow-up. While we acknowledge that open-label designs can introduce behavioral biases, including potential changes in adherence, we will now explicitly state that placebo-controlled, blinded trials would provide a more robust assessment and are warranted in future research.

The 84-day duration of intensification was chosen based on previous studies and provided sufficient time for observing potential changes in viral transcription and reservoir dynamics. However, we agree that including post-intervention follow-up would have strengthened the conclusions, and we will highlight this limitation and future direction in the revised manuscript.

The sex imbalance is now clearly acknowledged as a limitation in the revised manuscript, and we fully support ongoing efforts to promote equitable recruitment in HIV research. We would like to add that, in our study, rectal biopsies were coupled with anal cancer screening through HPV testing. This screening is specifically recommended for younger men who have sex with men (MSM), as outlined in the current EACS guidelines (see: https://eacs.sanfordguide.com/eacs-part2/cancer/cancer-screening-methods). As a result, MSM participants had both a clinical incentive and medical interest to undergo this procedure, which likely contributed to the higher proportion of male participants in the study.

Lastly, although baseline total HIV DNA was higher in the intensified group, our statistical approach is based on a within-subject (repeated-measures) design, in which the longitudinal change of a parameter within the same participant during the study was the main outcome. In other words, we are not comparing absolute values of any marker between the groups, we are looking at changes of parameters from baseline within participants, and these are not expected to be affected by baseline imbalances.

(6) Figure 1: the increase in DTG levels is interesting - it is not uniform across participants. Several participants had lower levels of DTG at the end of the intervention. Though unlikely to be statistically significant, it would be interesting to evaluate if there is a correlation between change in DTG concentrations and virologic / reservoir / inflammatory parameters. A positive relationship between increasing DTG concentration and decreased cell-associated RNA, for example, would help support the hypothesis that ongoing replication is occurring.

We agree with the reviewer that assessing correlations between DTG concentrations and virological, immunological, or inflammatory markers would be highly informative. In fact, we initially explored this question in a preliminary way by examining whether individuals who showed a marked increase in DTG levels after intensification also demonstrated stronger changes in the viral reservoir. While this exploratory analysis did not reveal any clear associations, we would like to emphasize that correlating biological effects with DTG concentrations measured at a single timepoint may have limited interpretability. A more comprehensive understanding of the relationship between drug exposure and reservoir dynamics would ideally require multiple pharmacokinetic measurements over time, including pre-intensification baselines. This is particularly important given that DTG concentrations vary across individuals and over time, depending on adherence, metabolism, and other individual factors. We will clarify these points in the revised manuscript.

(7) Figure 2: IPDA in tissue- was this done? scRNA in blood (single copy assay) - would this be expected to correlate with usCaRNA? The most unambiguous result is the decrease in cell-associated RNA - accompanying results using single-copy assay in plasma would be helpful to bolster this result.

As mentioned in our response to point 3, we attempted IPDA on tissue samples, but technical limitations prevented reliable detection of intact proviruses. Regarding residual viremia, we did perform ultra-sensitive plasma HIV RNA quantification but due to a technical issue (an inadvertent PBMC contamination during plasma separation) that affected the reliability of the results we felt uncomfortable including these data in the manuscript.

The use of the US RNA / Total DNA ratio is not helpful/difficult to interpret since the control and intervention arms were unmatched for total DNA reservoir size at study entry.

We respectfully disagree with this comment. The US RNA / Total DNA ratio is commonly used to assess the relative transcriptional activity of the viral reservoir, rather than its absolute size. While we acknowledge that the total HIV-1 DNA levels differed at baseline between the two groups, the US RNA / Total DNA ratio specifically reflects the relationship between transcriptional activity and reservoir size within each individual, and is therefore not directly confounded by baseline differences in total DNA alone.

Moreover, our analyses focus on within-subject longitudinal changes from baseline, not on direct between-group comparisons of absolute marker values. As such, the observed changes in the US RNA / Total DNA ratio over time are interpreted relative to each participant's baseline, mitigating concerns related to baseline imbalances between groups.

Reviewer #2 (Public Review):

Summary:

An intensification study with a double dose of 2nd generation integrase inhibitor with a background of nucleoside analog inhibitors of the HIV retrotranscriptase in 2, and inflammation is associated with the development of co-morbidities in 20 individuals randomized with controls, with an impact on the levels of viral reservoirs and inflammation markers. Viral reservoirs in HIV are the main impediment to an HIV cure, and inflammation is associated with co-morbidities.

Strengths:

The intervention that leads to a decrease of viral reservoirs and inflammation is quite straightforward forward as a doubling of the INSTI is used in some individuals with INSTI resistance, with good tolerability.

This is a very well documented study, both in blood and tissues, which is a great achievement due to the difficulty of body sampling in well-controlled individuals on antiretroviral therapy. The laboratory assays are performed by specialists in the field with state-of-the art quantification assays. Both the introduction and the discussion are remarkably well presented and documented.

The findings also have a potential impact on the management of chronic HIV infection.

Weaknesses:

I do not think that the size of the study can be considered a weakness, nor the fact that it is open-label either.

We thank Reviewer #2 for their constructive and supportive comments. We appreciate their positive assessment of the study design, the translational relevance of the intervention, and the technical quality of the assays. We also take note of their perspective regarding sample size and study design, which supports our positioning of this trial as an exploratory, hypothesis-generating phase 2 study.

Reviewer #3 (Public Review):

The introduction does a very good job of discussing the issue around whether there is ongoing replication in people with HIV on antiretroviral therapy. Sporadic, non-sustained replication likely occurs in many PWH on ART related to adherence, drug interactions and possibly penetration of antivirals into sanctuary areas of replication and as the authors point out proving it does not occur is likely not possible and proving it does occur is likely very dependent on the population studied and the design of the intervention. Whether the consequences of this replication in the absence of evolution toward resistance have clinical significance challenging question to address.

It is important to note that INSTI-based therapy may have a different impact on HIV replication events that results in differences in virus release for specific cell type (those responsible for "second phase" decay) by blocking integration in cells that have completed reverse transcription prior to ART initiation but have yet to be fully activated. In a PI or NNRTI-based regimen, those cells will release virus, whereas with an INSTI-based regimen, they will not.

Given the very small sample size, there is a substantial risk of imbalance between the groups in important baseline measures. Unfortunately, with the small sample size, a non-significant P value is not helpful when comparing baseline measures between groups. One suggestion would be to provide the full range as opposed to the inter-quartile range (essentially only 5 or 6 values). The authors could also report the proportion of participants with baseline HIV RNA target not detected in the two groups.

We thank Reviewer #3 for their thoughtful and balanced review. We are grateful for the recognition of the strength of the Introduction, the complexity of evaluating residual replication, and the technical execution of the assays. We also appreciate the insightful suggestions for improving the clarity and transparency of our results and discussion.

We will revise the manuscript to address several of the reviewer’s key concerns. We agree that the small sample size increases the risk of baseline imbalances. We will acknowledge these limitations in the revised manuscript. We will provide both the full range and the IQR in Table 1 in the revised manuscript.

A suggestion that there is a critical imbalance between groups is that the control group has significantly lower total HIV DNA in PBMC, despite the small sample size. The control group also has numerically longer time of continuous suppression, lower unspliced RNA, and lower intact proviral DNA. These differences may have biased the ability to see changes in DNA and US RNA in the control group.

We acknowledge the significant baseline difference in total HIV DNA between groups, which we have clearly reported. However, the other variables mentioned, duration of continuous viral suppression, unspliced RNA levels, and intact proviral DNA, did not differ significantly between groups at baseline, despite differences in the median values. These numerical differences do not necessarily indicate a critical imbalance.

Notably, there was no significant difference in the change in US RNA/DNA between groups (Figure 2C).

The nonsignificant difference in the change in US RNA/DNA between groups is not unexpected, given the significant between-group differences for both US RNA and total DNA changes. Since the ratio combines both markers, it is likely to show attenuated between-group differences compared to the individual components. However, while the difference did not reach statistical significance (p = 0.09), we still observed a trend towards a greater reduction in the US RNA/Total DNA ratio in the intervention group.

The fact that the median relative change appears very similar in Figure 2C, yet there is a substantial difference in P values, is also a comment on the limits of the current sample size.

Although we surely agree that in general, the limited sample size impacts statistical power, we would like to point out that in Figure 2C, while the medians may appear similar, the ranges do differ between groups. At days 56 and 84, the median fold changes from baseline are indeed close but the full interquartile range in the DTG group stays below 1, while in the control group, the interquartile range is wider and covers approximately equal distance above and below 1. This explains the difference in p values between the groups.

The text should report the median change in US RNA and US RNA/DNA when describing Figures 2A-2C.

These data are already reported in the Results section (lines 164–166): "By day 84, US RNA and US RNA/total DNA ratio had decreased from day 0 by medians (IQRs) of 5.1 (3.3–6.4) and 4.6 (3.1–5.3) fold, respectively (p = 0.016 for both markers)."

This statistical comparison of changes in IPDA results between groups should be reported. The presentation of the absolute values of all the comparisons in the supplemental figures is a strength of the manuscript.

In the assessment of ART intensification on immune activation and exhaustion, the fact that none of the comparisons between randomized groups were significant should be noted and discussed.

We would like to point out that a statistically significant difference between the randomized groups was observed for the frequency of CD4⁺ T cells expressing TIGIT, as shown in Figure 3A and reported in the Results section (p = 0.048).

The changes in CD4:CD8 ratio and sCD14 levels appear counterintuitive to the hypothesis and are commented on in the discussion.

Overall, the discussion highlights the significant changes in the intensified group, which are suggestive. There is limited discussion of the comparisons between groups where the results are less convincing.

We will temper the language accordingly and add commentary on the limited and modest nature of these changes. Similarly, we will expand our discussion of counterintuitive findings such as the CD4:CD8 ratio and sCD14 changes.

The limitations of the study should be more clearly discussed. The small sample size raises the possibility of imbalance at baseline. The supplemental figures (S3-S5) are helpful in showing the differences between groups at baseline, and the variability of measurements is more apparent. The lack of blinding is also a weakness, though the PK assessments do help (note 3TC levels rise substantially in both groups for most of the time on study (Figure S2).

The many assays and comparisons are listed as a strength. The many comparisons raise the possibility of finding significance by chance. In addition, if there is an imbalance at baseline outcomes, measuring related parameters will move in the same direction.

We agree that the multiple comparisons raise the possibility of chance findings but would like to stress that in an exploratory study like this it is very important to avoid a type II error. In addition, the consistent directionality of the most relevant outcomes (US RNA and intact DNA) lends biological plausibility to the observed effects.

The limited impact on activation and inflammation should be addressed in the discussion, as they are highlighted as a potentially important consequence of intermittent, not sustained replication in the introduction.

The study is provocative and well executed, with the limitations listed above. Pharmacokinetic analyses help mitigate the lack of blinding. The major impact of this work is if it leads to a much larger randomized, controlled, blinded study of a longer duration, as the authors point out.

Finally, we fully endorse the reviewer’s suggestion that the primary contribution of this study lies in its value as a proof-of-concept and foundation for future randomized, blinded trials of greater scale and duration. We will highlight this more clearly in the revised Discussion.

Author response:

We thank the editors and the reviewers for their positive comments regarding our manuscript and the methodological approach we have taken to understand the historical demographic response of endemic island birds to climate change. We acknowledge the issues of uneven sample sizes and plan to include additional species of island endemic birds for which genomic data is now available. As requested by reviewer 1, we will also address the issues related to the PSMC analysis in the revised version of the manuscript.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors present an interesting study using RL and Bayesian modelling to examine differences in learning rate adaptation in conditions of high and low volatility and noise respectively. Through "lesioning" an optimal Bayesian model, they reveal that apparently a suboptimal adaptation of learning rates results from incorrectly detecting volatility in the environment when it is not in fact present.

Strengths:

The experimental task used is cleverly designed and does a good job of manipulating both volatility and noise. The modelling approach takes an interesting and creative approach to understanding the source of apparently suboptimal adaptation of learning rates to noise, through carefully "lesioning" and optimal Bayesian model to determine which components are responsible for this behaviour.

We thank the reviewer for this assessment.

Weaknesses:

The study has a few substantial weaknesses; the data and modelling both appear robust and informative, and it tackles an interesting question. The model space could potentially have been expanded, particularly with regard to the inclusion of alternative strategies such as those that estimate latent states and adapt learning accordingly.

We thank the reviewer for this suggestion. We agree that it would be interesting to assess the ability of alternative models to reproduce the sub-optimal choices of participants in this study. The Bayesian Observer Model described in the paper is a form of Hierarchical Gaussian Filter, so we will assess the performance of a different class of models that are able to track uncertainty-- RL based models that are able to capture changes of uncertainty (the Kalman filter, and the model described by Cochran and Cisler, Plos Comp Biol 2019). We will assess the ability of the models to recapitulate the core behaviour of participants (in terms of learning rate adaption) and, if possible, assess their ability to account for the pupillometry response.

Reviewer #2 (Public review):

Summary:

In this study, the authors aimed to investigate how humans learn and adapt their behavior in dynamic environments characterized by two distinct types of uncertainty: volatility (systematic changes in outcomes) and noise (random variability in outcomes). Specifically, they sought to understand how participants adjust their learning rates in response to changes in these forms of uncertainty.

To achieve this, the authors employed a two-step approach:

(1) Reinforcement Learning (RL) Model: They first used an RL model to fit participants' behavior, revealing that the learning rate was context-dependent. In other words, it varied based on the levels of volatility and noise. However, the RL model showed that participants misattributed noise as volatility, leading to higher learning rates in noisy conditions, where the optimal strategy would be to be less sensitive to random fluctuations.

(2) Bayesian Observer Model (BOM): To better account for this context dependency, they introduced a Bayesian Observer Model (BOM), which models how an ideal Bayesian learner would update their beliefs about environmental uncertainty. They found that a degraded version of the BOM, where the agent had a coarser representation of noise compared to volatility, best fit the participants' behavior. This suggested that participants were not fully distinguishing between noise and volatility, instead treating noise as volatility and adjusting their learning rates accordingly.

The authors also aimed to use pupillometry data (measuring pupil dilation) as a physiological marker to arbitrate between models and understand how participants' internal representations of uncertainty influenced both their behavior and physiological responses. Their objective was to explore whether the BOM could explain not just behavioral choices but also these physiological responses, thereby providing stronger evidence for the model's validity.

Overall, the study sought to reconcile approximate rationality in human learning by showing that participants still follow a Bayesian-like learning process, but with simplified internal models that lead to suboptimal decisions in noisy environments.

Strengths:

The generative model presented in the study is both innovative and insightful. The authors first employ a Reinforcement Learning (RL) model to fit participants' behavior, revealing that the learning rate is context-dependent-specifically, it varies based on the levels of volatility and noise in the task. They then introduce a Bayesian Observer Model (BOM) to account for this context dependency, ultimately finding that a degraded BOM - in which the agent has a coarser representation of noise compared to volatility - provides the best fit for the participants' behavior. This suggests that participants do not fully distinguish between noise and volatility, leading to the misattribution of noise as volatility. Consequently, participants adopt higher learning rates even in noisy contexts, where an optimal strategy would involve being less sensitive to new information (i.e., using lower learning rates). This finding highlights a rational but approximate learning process, as described in the paper.

We thank the reviewer for their assessment of the paper.

Weaknesses:

While the RL and Bayesian models both successfully predict behavior, it remains unclear how to fully reconcile the two approaches. The RL model captures behavior in terms of a fixed or context-dependent learning rate, while the BOM provides a more nuanced account with dynamic updates based on volatility and noise. Both models can predict actions when fit appropriately, but the pupillometry data offers a promising avenue to arbitrate between the models. However, the current study does not provide a direct comparison between the RL framework and the Bayesian model in terms of how well they explain the pupillometry data. It would be valuable to see whether the RL model can also account for physiological markers of learning, such as pupil responses, or if the BOM offers a unique advantage in this regard. A comparison of the two models using pupillometry data could strengthen the argument for the BOM's superiority, as currently, the possibility that RL models could explain the physiological data remains unexplored.

We thank the reviewer for this suggestion. In the current version of the paper, we use an extremely simple reinforcement learning model to simply measure the learning rate in each task block (as this is the key behavioural metric we are interested in). As the reviewer highlights, this simple model doesn’t estimate uncertainty or adapt to it. Given this, we don’t think we can directly compare this model to the Bayesian Observer Model—for example, in the current analysis of the pupillometry data we classify individual trials based on the BOM’s estimate of uncertainty and show that participants adapt their learning rate as expected to the reclassified trials, this analysis would not be possible with our current RL model. However, there are more complex RL based models that do estimate uncertainty (as discussed above in response to Reviewer #1) and so may more directly be compared to the BOM. We will attempt to apply these models to our task data and describe their ability to account for participant behaviour and physiological response as suggested by the Reviewer.

The model comparison between the Bayesian Observer Model and the self-defined degraded internal model could be further enhanced. Since different assumptions about the internal model's structure lead to varying levels of model complexity, using a formal criterion such as Bayesian Information Criterion (BIC) or Akaike Information Criterion (AIC) would allow for a more rigorous comparison of model fit. Including such comparisons would ensure that the degraded BOM is not simply favored due to its flexibility or higher complexity, but rather because it genuinely captures the participants' behavioral and physiological data better than alternative models. This would also help address concerns about overfitting and provide a clearer justification for using the degraded BOM over other potential models.

Thank you, we will add this.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

For clarity, the methods would benefit from further detail of task framing to participants. I.e. were there explicit instructions regarding volatility/task contingencies? Or were participants told nothing?

We have added in the following explanatory text to the methods section (page 20), clarifying the limited instructions provided to participants:

“Participants were informed that the task would be split into 6 blocks, that they had to learn which was the best option to choose, and that this option may change over time. They were not informed about the different forms of uncertainty we were investigating or of the underlying structure of the task (that uncertainty varied between blocks).”

In the results, it would be useful to report the general task behavior of participants to get a sense of how they performed across different parts of the task. Also, were participants excluded if they didn't show evidence of learning adaptation to volatility?

We have added the following text reporting overall performance to the results (page 6):

“Participants were able to learn the best option to choose in the task, selecting the most highly rewarded option on an average of 71% of trials (range 65% - 74%).”

And the following text to the methods, confirming that participants were not excluded if they didn’t respond to volatility/noise (the failure in this adaptation is the focus of the current study) (page 19):

“No exclusion criteria related to task performance were used.”

The results would benefit from a more intuitive explanation of what the lesioning is trying to recapitulate; this can get quite technical and the objective is not necessarily clear, especially for the less computationally-minded reader.

We have amended the relevant section of the results to clarify this point (page 9):

“Having shown that an optimal learner adjusts its learning rate to changes in volatility and noise as expected, we next sought to understand the relative noise insensitivity of participants. In these analyses we “lesion” the BOM, to reduce its performance in some way, and then assess whether doing so recapitulates the pattern of learning rate adaptation observed for participants (Fig 3e). In other words, we damage the model so it performs less well and then assess whether this damage makes the behaviour of the BOM (shown in Fig 3f) more closely resemble that seen in participants (Fig 3e).”

The modelling might be improved by the inclusion of another class of model. Specifically, models that adapt learning rates in response to the estimation of latent states underlying the current task outcomes would be very interesting to see. In a sense, these are also estimating volatility through changeability of latent states, and it would be interesting to explore whether the findings could also be explained by an incorrect assumption that the latent state has changed when outcomes are noisy.

Thank you for this suggestion. We have added additional sections to the supplementary materials in which we use a general latent state model and a simple RL model to try to recapitulate the behaviour of participants (and to compare with the BOM). These additional sections are extensive, so are not reproduced here. We have also added in a section to the discussion in the main paper covering this interesting question in which we confirm that we were unable to reproduce participant behaviour (or the normative effect of the lesioned BOMs) using these models but suggest that alternative latent state formulations would be interesting to explore in future work (page 18):

“A related question is whether other, non-Bayesian model formulations may be able to account for participants’ learning adaptation in response to volatility and noise. Of note, the reinforcement learning model used to measure learning rates in separate blocks does not achieve this goal—as this model is fitted separately to each block rather than adapting between blocks (NB the simple reinforcement learning model that is fitted across all blocks does not capture participant behaviour, see supplementary information). One candidate class of model that has potential here is latent-state models (Cochran & Cisler, 2019), in which the variance and unexpected changes in the process being learned (which have a degree of similarity with noise and volatility respectively) is estimated and used to alter the model’s rates of updating as well as the estimated number of states being considered. Using the model described by Cochran and Cisler, we were unable to replicate the learning rate adaptation demonstrated by participants in the current study (see supplementary information) although it remains possible that other latent state formulations may be more successful. “

The discussion may benefit from a little more discussion of where this work leads us - what is the next step?

As above, we have added in a suggestion about future modelling work. We have also added in a section about the outstanding interesting questions concerning the neural representation of these quantities, reproduced in response to the suggestion by reviewer #2 below.

Reviewer #2 (Recommendations for the authors):

The study presents an opportunity to explore potential neural coding models that could account for the cognitive processes underlying the task. In the field of neural coding, noise correlation is often measured to understand how a population of neurons responds to the same stimulus, which could be related to the noise signal in this task. Since the brain likely treats the stimulus as the same, with noise representing minor changes, this aspect could be linked to the participants' difficulty distinguishing noise from volatility. On the other hand, signal correlation is used to understand how neurons respond to different stimuli, which can be mapped to the volatility signal in the task. It would be highly beneficial if the authors could discuss how these established concepts from neural population coding might relate to the Bayesian behavior model used in the study. For instance, how might neurons encode the distinction between noise and volatility at a population level? Could noise correlation lead to the misattribution of noise as volatility at a neural level, mirroring the behavioral findings? Discussing possible neural models that could explain the observed behavior and relating it to the existing literature on neural population coding would significantly enrich the discussion. It would also open up avenues for future research, linking these behavioral findings to potential neural mechanisms.

We thank the reviewer for this interesting suggestion. We have added in the following paragraph to the discussion section which we hope does justice to this interesting questions (page 18):

Previous work examining the neural representations of uncertainty have tended to report correlations between brain activity and some task-based estimate of one form of uncertainty at a time (Behrens et al., 2007; Walker et al., 2020, 2023). We are not aware of work that has, for example, systematically varied volatility and noise and reported distinct correlations for each. An interesting possibility as to how different forms of uncertainty may be encoded is suggested by parallels with the neuronal decoding literature. One question addressed by this literature is how the brain decodes changes in the world from the distributed, noisy neural responses to those changes, with a particular focus on the influence of different forms of between-neuron correlation (Averbeck et al., 2006; Kohn et al., 2016). Specifically, signal-correlation, the degree to which different neurons represent similar external quantities (required to track volatility) is distinguished from, and often limited by, noise-correlation, the degree to which the activity of different neurons covaries independently of these external quantities. One possibility relevant to the current study, which resembles the underlying logic of the BOM, is that a population of neurons represents the estimated mean of the generative process that produces task outcomes. In this case, volatility would be tracked as the signal-correlation across this population, whereas noise would be analogous to the noise-correlation and, crucially, misestimation of noise as volatility might arise as misestimation of these two forms of correlation. While the current study clearly cannot adjudicate on the neural representation of these processes, our finding of distinct behavioural and physiological responses to the two forms of uncertainty, does suggest that separable neural representations of uncertainty are maintained. “

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This useful work extends a prior study from the authors to observe distance changes within the CNBD domains of a full-length CNG channel based on changes in single photon lifetimes due to tmFRET between a metal at an introduced chelator site and a fluorescent non-canonical amino acid at another site. The data are excellent and convincingly support the authors' conclusions. The methodology is of general use for other proteins. The authors also show that coupling of the CNBDs to the rest of the channel stabilizes the CNBDs in their active state, relative to an isolated CNBD construct.

Strengths:

The manuscript is very well written and clear.

Reviewer #2 (Public review):

The manuscript "Domain Coupling in Allosteric Regulation of SthK Measured Using Time-Resolved Transition Metal Ion FRET" by Eggan et al. investigates the energetics of conformational transitions in the cyclic nucleotide-gated (CNG) channel SthK. This lab pioneered transition metal FRET (tmFRET), which has previously provided detailed insights into ion channel conformational changes. Here, the authors analyze tmFRET fluorescence lifetime measurements in the time domain, yielding detailed insights into conformational transitions within the cyclic nucleotide binding domains (CNBDs) of the channel. The integration of tmFRET with time-correlated single-photon counting (TCSPC) represents an advancement of this technique.

The results summarize known conformational transitions of the C-helix and provide distance distributions that agree with predicted values based on available structures. The authors first validated their TCSPC approach using the isolated CNBD construct previously employed for similar experiments. They then study the more complex fulllength SthK channel protein. The findings agree with earlier results from this group, demonstrating that the C-helix is more mobile in the closed state than static structures reflect. Upon adding the activating ligand cAMP, the C-helix moves closer to the bound ligand, as indicated by a reduced fluorescence lifetime, suggesting a shorter distance between the donor and acceptor. The observed effects depend on the cAMP concentration, with affinities comparable to functional measurements. Interestingly, a substantial amount of CNBDs appear to be in the activated state even in the absence of cAMP (Figure 6E and F, fA2 ~ 0.4).

This may be attributed to cooperativity among the CNBDs, which the authors could elaborate on further. In this context, the major limitation of this study is that distance distributions are observed only in one domain. While inter-subunit FRET is detected and accounted for, the results focus exclusively on movements within one domain. Thus, the resulting energetic considerations must be assessed with caution. In the absence of the activator, the closed state is favored, while the presence of cAMP favors the open state. This quantifies the standard assumption; otherwise, an activator would not effectively activate the channel. However, the numerical values of approximately 3 kcal/mol are limited by the fact that only one domain is observed in the experiment, and only one distance (C- helix relative to the CNBD) is probed. Additional conformational changes leading to pore opening (including rotation and upward movement of the CNBD, and radial dilation of the tetrameric assembly) are not captured by the current experiments. These limitations should be taken into account when interpreting the results.

We agree that these are important limitations to consider in interpreting our results. These limitations and future directions are now largely covered in our discussion. We believe measurements in individual domains provide unique insights into the contributions of different parts of the protein and future work will continue to address conformational energetics in other parts of the protein and subunit cooperativity. 

Reviewer #3 (Public review):

Summary:

This is a lucidly written manuscript describing the use of transition-metal FRET to assess distance changes during functional conformational changes in a CNG channel.

The experiments were performed on an isolated C-terminal nucleotide binding domain

(CNBD) and on a purified full-length channel, with FRET partners placed at two

positions in the CNBD.

Strengths:

The data and quantitative analysis are exemplary, and they provide a roadmap for use of this powerful approach in other proteins.

Weaknesses/Comments:

A ~3x lower Kd for nucleotide is seen for the detergent-solubilized full-length channel, compared to electrophysiological experiments. This is worth a comment in the Discussion, particularly in the context of the effect of the pore domain on the CNBD energetics.

We are cautious to interpret our K_D values given the high affinity for cAMP and the challenges of accurately determining the total protein concentrations in our experiments. We now state this explicitly in the manuscript.  

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The manuscript is very well written and clear. Congrats to the authors.

Minor comment: In "Measuring tmFRET in Full-Length SthK", 3rd paragraph: "... FRET model with both intersubunit and intersubunit FRET." Should read "intersubunit and intrasubunit".

Thank you for the comment, this is now corrected.  

Reviewer #2 (Recommendations for the authors):

Overall, the manuscript is well-written and clearly explained. However, I recommend that the authors discuss the limitations more critically.

The revised manuscript now largely addresses these limitations. Additional comments are addressed in short below:  

A) Only one distance is measured.

We believe validating a single distance as an important first step in determining the use of this technique and beginning to quantify the allosteric mechanism in SthK. Future studies aim to make additional measurements.

B) Measurements are confined to a single domain in the cooperative tetrameric assembly.

Isolating conformational changes in individual domains, allows us to determine how different parts of the protein contribute to the activation upon ligand binding.  

C) The change in distance upon activation mirrors what is observed in the closed state, which casts doubt on whether these conformational changes actually lead to channel opening or merely reflect the upward swinging of the C-helix that contributes to coordinating cAMP in the binding pocket.

Future studies aim to detect conformational changes in the pore and other parts of the protein.

D) Rigid body movements, rotations, and dilations are not captured by the measurements. 

Our measurements combine energetic information with some, although more limited, structural information.   

E) Cooperativity is not considered in the interpretation of the results.

It is currently unclear where in SthK cooperativity arises upon ligand activation (ie. at the level of the CNBD, C-Linker or pore). Our results do not provide evidence of cooperativity in the CNBD upon ligand binding. 

Additionally, the authors directly correlate their results with the functional states of SthK previously reported, but it remains open whether the modified protein for tmFRET behaves similarly to WT SthK. Functional experiments with the protein used for tmFRET, which demonstrate comparable open probabilities and cAMP potency, would considerably strengthen the manuscript.

Further optimization is needed to express the full-length protein used in tmFRET experiments in spheroplasts to enable electrophysiological recordings from these constructs. 

Reviewer #3 (Recommendations for the authors):

In the final paragraph of the Discussion, the sentence "In our experiments, we assumed that deleting the pore and transmembrane domains eliminates the coupling of these regions to the CNBD" seems trivial. Perhaps it would help to add "simply" before eliminates?

We have taken the advice and added ‘simply’ in this sentence.  

Can a statement be made about the magnitude of the effect in the C-terminal deletion experiments in refs 27-29?

Due to the different channels used in the C-terminal deletion experiments in refs 27-29 (HCN1 and spHCN), compared to the channel we used (SthK), it is challenging to compare the magnitude of energetic changes between these studies. Additionally, the HCN experiments measured changes in the pore domain, compared to the conformational changes in the CNBD domain measured here.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this useful narrative, the authors attempt to capture their experience of the success of team projects for the scientific community.

Strengths:

The authors are able to draw on a wealth of real-life experience reviewing, funding, and administering large team projects, and assessing how well they achieve their goals.

Weaknesses:

The utility of the RCR as a measure is questionable. I am not sure if this really makes the case for the success of these projects. The conclusions do not depend on Figure 1.

We respectfully disagree about the utility of the RCR, particularly because it is metric that is normalized by both year and topical area. We have added a more detailed description of how the RCR is calculated on page 6-7. Please note that figure 1 is aimed to highlight the funding opportunities, investments and number of awards associated with small lab (exploratory) versus team (elaborated, mature) research rather than a description of publication metrics.

Reviewer #2 (Public review):

Summary:

The authors review the history of the team projects within the Brain initiative and analyze their success in progression to additional rounds of funding and their bibliographic impact.

Strengths:

The history of the team projects and the fact that many had renewed funding and produced impactful papers is well documented.

Weaknesses:

The core bibliographic and funding impact results have largely been reported in the companion manuscript and so represent "double dipping" I presume the slight disagreement in the number of grants (by one) represents a single grant that was not deemed to address systems/computational neuroscience. The single figure is relatively uninformative. The domains of study are sufficiently large and overlapping that there seems to be little information gained from the graphic and the Sankey plot could be simply summarized by rates of competing success.

While we sincerely appreciate the feedback, we chose to retain these plots on domains and models to provide a sense of the broad spectrum of research topics contained in our TeamBCP awards. Further details on the awards can be derived from the award links provided in the text. Additionally, we retained the Sankey plots because these are a visual depiction of how awards transition from one mechanism to another, evolve in their funding sources, and advance in their research trajectories. The plot is an example of our continuity analysis which is only reported in the text and not visually shown for the remaining BCP programs.

Recommendations for the authors:

Editorial note:

In the discussion, the reviewers agreed that the present manuscript does not make a sufficient independent contribution and so would be more profitably combined with the companion manuscript. Both reviewers noted that there was not much insight that relied on the single figure. Since neither manuscript is long, and they have overlapping authors (including the same first and last authors), this should not be a difficult merger to achieve.

Thank you for the recommendation to merge. We have combined both manuscripts into one in this version.

Reviewer #1 (Recommendations for the authors):

The jargon of the grant programs could be described as a nightmare. Wellcome is spelled wrong.

We have attempted to limit the use of jargon and to define acronyms in this version. We have corrected the spelling of Wellcome.

Reviewer #2 (Recommendations for the authors):

I suggest that the two manuscripts be combined into a single paper. Although the other manuscript could stand on its own, this one does not.

The idea of culture change surrounding teams is useful but really forms more of a policy- focused opinion piece than a quantitative analysis of funding impact.

If the authors insist on keeping these separate, it is critical to remove the team data from the other manuscript.

We have combined both manuscripts and decided to retain the description of culture change but have edited and condensed this section and will use the supplemental report for qualitative assessments.

Author response:

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

Taber et al report the biochemical characterization of 7 mutations in PHD2 that induce erythrocytosis.

Their goal is to provide a mechanism for how these mutations cause the disease. PHD2 hydroxylates HIF1a in the presence of oxygen at two distinct proline residues (P564 and P402) in the "oxygen degradation domain" (ODD). This leads to the ubiquitylation of HIF1a by the VHL E3 ligase and its subsequent degradation. Multiple mutations have been reported in the EGLN1 gene (coding for PHD2), which are associated with pseudohypoxic diseases that include erythrocytosis. Furthermore, 3 mutations in PHD2 also cause pheochromocytoma and paraganglioma (PPGL), a neuroendocrine tumour. These mutations likely cause elevated levels of HIF1a, but their mechanisms are unclear. Here, the authors analyze mutations from 152 case reports and map them on the crystal structure. They then focus on 7 mutations, which they clone in a plasmid and transfect into PHD2-KO to monitor HIF1a transcriptional activity via a luciferase assay. All mutants show impaired activation. Some mutants also impaired stability in pulse chase turnover assays (except A228S, P317R, and F366L). In vitro purified PHD2 mutants display a minor loss in thermal stability and some propensity to aggregate. Using MST technology, they show that P317R is strongly impaired in binding to HIF1a and HIF2a, whereas other mutants are only slightly affected. Using NMR, they show that the PHD2 P317R mutation greatly reduces hydroxylation of P402 (HIF1a NODD), as well as P562 (HIF1a CODD), but to a lesser extent. Finally, BLI shows that the P317R mutation reduces affinity for CODD by 3-fold, but not NODD.  

Strengths: 

(1) Simple, easy-to-follow manuscript. Generally well-written. 

(2) Disease-relevant mutations are studied in PHD2 that provide insights into its mechanism of action. 

(3) Good, well-researched background section. 

Weaknesses: 

(1) Poor use of existing structural data on the complexes of PHD2 with HIF1a peptides and various metals and substrates. A quick survey of the impact of these mutations (as well as analysis by Chowdhury et al, 2016) on the structure and interactions between PHD2 peptides of HIF1a shows that the P317R mutation interferes with peptide binding. By contrast, F366L will affect the hydrophobic core, and A228S is on the surface, and it's not obvious how it would interfere with the stability of the protein. 

Thank you for the comment.  We will further analyze the mutations on the available PHD2 crystal structures in complex with HIFa to discern how these substitution mutations may impact PHD2 structure and function.  

(2) To determine aggregation and monodispersity of the PHD2 mutants using size-exclusion chromatography (SEC), equal quantities of the protein must be loaded on the column. This is not what was done. As an aside, the colors used for the SEC are very similar and nearly indistinguishable. 

Agreed.  We will perform additional experiment as suggested by the reviewer to further assess aggregation and hydrodynamic size.  The colors used in the graph will be changed for a clearer differentiation between samples.

(3) The interpretation of some mutants remains incomplete. For A228S, what is the explanation for its reduced activity? It is not substantially less stable than WT and does not seem to affect peptide hydroxylation. 

We agree with the reviewer that the causal mechanism for some of the tested disease-causing mutants remain unclear.  The negative findings also raise the notion, perhaps considered controversial, that there may be other substrates of PHD2 that are impacted by certain mutations, which contribute to disease pathogenesis.  We will expand our discussion accordingly. 

(4) The interpretation of the NMR prolyl hydroxylation is tainted by the high concentrations used here. First of all, there is a likely a typo in the method section; the final concentration of ODD is likely 0.18 mM, and not 0.18 uM (PNAS paper by the same group in 2024 reports using a final concentration of 230 uM). Here, I will assume the concentration is 180 uM. Flashman et al (JBC 2008) showed that the affinity of the NODD site (P402; around 10 uM) for PHD2 is 10-fold weaker than CODD (P564, around 1 uM). This likely explains the much faster kinetics of hydroxylation towards the latter. Now, using the MST data, let's say the P317R mutation reduces the affinity by 40-fold; the affinity becomes 400 uM for NODD (above the protein concentration) and 40 uM for CODD (below the protein concentration). Thus, CODD would still be hydroxylated by the P317R mutant, but not NODD. 

The HIF1α concentration was indeed an oversight, which will be corrected to 0.18 mM.  The study by Flashman et al.[1] showing PHD2 having a lower affinity to the NODD than CODD likely contributes to the differential hydroxylation rates via PHD2 WT.  We showed here via MST that PHD2 P317R had Kd of 320 ± 20 uM for HIF1αCODD, which should have led to a severe enzymatic defect, even at the high concentrations used for NMR (180 uM).  However, we observed only a subtle reduction in hydroxylation efficiency in comparison to PHD2 WT.  Thus, we performed another binding method using BLI that showed a mild binding defect on CODD by PHD2 P317R, consistent with NMR data.  The perplexing result is the WT-like binding to the NODD by PHD2 P317R, which appears inconsistent with the severe defect in NODD hydroxylation via PHD2 P317R as measured via NMR.  These results suggest that there are supporting residues within the PHD2/NODD interface that help maintain binding to NODD but compromise the efficiency of NODD hydroxylation upon PHD2 P317R mutation. We will perform additional binding experiments to further interrogate and validate the binding affinity of PHD2 P317R to NODD and CODD.

(5) The discrepancy between the MST and BLI results does not make sense, especially regarding the P317R mutant. Based on the crystal structures of PHD2 in complex with the ODD peptides, the P317R mutation should have a major impact on the affinity, which is what is reported by MST. This suggests that the MST is more likely to be valid than BLI, and the latter is subject to some kind of artefact. Furthermore, the BLI results are inconsistent with previous results showing that PHD2 has a 10-fold lower affinity for NODD compared to CODD. 

The reviewer’s structural prediction that P317R mutation should cause a major binding defect, while agreeable with our MST data, is incongruent with our NMR and the data from Chowdhury et al.[2] that showed efficient hydroxylation of CODD via PHD2 P317R.  Moreover, we have attempted to model NODD and CODD on apo PHD2 P317R structure and found that the mutation had no major impact on CODD while the mutated residue could clash with NODD, causing a shifting of peptide positioning on the protein.  However, these modeling predictions, like any in silico projections, would need experimental validation.  As mentioned in our preceding response, we also performed BLI, which showed that PHD2 P317R had a minor binding defect for CODD, consistent with the NMR results and findings by Chowdhury et al[2].  NODD binding was also measured with BLI as purified NODD peptides were not amenable for soluble-based MST assay, which showed similar K_d’s for PHD2 WT and P317R.  Considering the absence of NODD hydroxylation via PHD2 P317R as measured by NMR and modeling on apo PHD2 P317R, we posit that P317R causes deviation of NODD from its original orientation that may not affect binding due to the other interactions from the surrounding elements but unfortunately disallows NODD from turnover.  Further study would be required to validate such notion, which we feel is beyond the scope of this manuscript.  However, we will perform additional binding experiments to further interrogate PHD2 P317R binding to NODD.   

(6) Overall, the study provides some insights into mutants inducing erythrocytosis, but the impact is limited. Most insights are provided on the P317R mutant, but this mutant had already been characterized by Chowdhury et al (2016). Some mutants affect the stability of the protein in cells, but then no mechanism is provided for A228S or F366L, which have stabilities similar to WT, yet have impaired HIF1a activation. 

We thank the reviewer for raising these and other limitations.  We will expand on the shortcomings of the present study but would like to underscore that the current work using the recently described NMR assay along with other biophysical analyses suggests a previously under-appreciated role of NODD hydroxylation in the normal oxygen-sensing pathway.  

Reviewer #2 (Public review): 

Summary: 

Mutations in the prolyl hydroxylase, PHD2, cause erythrocytosis and, in some cases, can result in tumorigenesis. Taber and colleagues test the structural and functional consequences of seven patientderived missense mutations in PHD2 using cell-based reporter and stability assays, and multiple biophysical assays, and find that most mutations are destabilizing. Interestingly, they discover a PHD2 mutant that can hydroxylate the C-terminal ODD, but not the N-terminal ODD, which suggests the importance of N-terminal ODD for biology. A major strength of the manuscript is the multidisciplinary approach used by the authors to characterize the functional and structural consequences of the mutations. However, the manuscript had several major weaknesses, such as an incomplete description of how the NMR was performed, a justification for using neighboring residues as a surrogate for looking at prolyl hydroxylation directly, or a reference to the clinical case studies describing the phenotypes of patient mutations. Additionally, the experimental descriptions for several experiments are missing descriptions of controls or validation, which limits their strength in supporting the claims of the authors. 

Strengths: 

(1) This manuscript is well-written and clear. 

(2) The authors use multiple assays to look at the effects of several disease-associated mutations, which support the claims. 

(3) The identification of P317R as a mutant that loses activity specifically against NODD, which could be a useful tool for further studies in cells. 

Weaknesses: 

Major: 

(1) The source data for the patient mutations (Figure 1) in PHD2 is not referenced, and it's not clear where this data came from or if it's publicly available. There is no section describing this in the methods.

Clinical and patient information on disease-causing PHD2 mutants was compiled from various case reports and summarized in an excel sheet found in the Supplementary Information.  The case reports are cited in this excel file.  A reference to the supplementary data will be added to the Figure 1 legend and in the introduction.

(2) The NMR hydroxylation assay. 

A. The description of these experiments is really confusing. The authors have published a recent paper describing a method using 13C-NMR to directly detect proly-hydroxylation over time, and they refer to this manuscript multiple times as the method used for the studies under review. However, it appears the current study is using 15N-HSQC-based experiments to track the CSP of neighboring residues to the target prolines, so not the target prolines themselves. The authors should make this clear in the text, especially on page 9, 5th line, where they describe proline cross-peaks and refer to the 15N-HSQC data in Figure 5B. 

As the reviewer mentioned, the assay that we developed directly measures the target proline residues.  This assay is ideal when mutations near the prolines are studied, such as A403, Y565 (He et al[3]).  In this previous work, we observed that the shifting of the target proline cross-peaks due to change in electronegativity on the pyrrolidine ring of proline in turn impacted the neighboring residues[3], which meant that the neighboring residues can be used as reporter residues for certain purposes.  In this study, we focused on investigating the mutations on PHD2 while leaving the sequence of the HIF-1α unchanged by using solely 15N-HSQC-based experiments without the need for double-labeled samples.  Nonetheless, we thank the reviewer for pointing out the confusion in the text and we will correct and clarify our description of this assay.

B. The authors are using neighboring residues as reporters for proline hydroxylation, without validating this approach. How well do CSPs of A403 and I566 track with proline hydroxylation? Have the authors confirmed this using their 13C-NMR data or mass spec? 

For previous studies, we performed intercalated 15N-HSQC and 13C-CON experiments for the kinetic measurements of wild-type HIF-1α and mutants.  We observed that the shifting pattern of A403 and I566 in the 15N-HSQC spectra aligned well with the ones of P402 and P564, respectively, in the 13C-CON spectra.  Representative data will be added to Supplemental Data.

C. Peak intensities. In some cases, the peak intensities of the end point residue look weaker than the peak intensities of the starting residue (5B, PHD2 WT I566, 6 ct lines vs. 4 ct lines). Is this because of sample dilution (i.e., should happen globally)? Can the authors comment on this? 

This is an astute observation by the reviewer.  We checked and confirmed that for all kinetic datasets, the peak intensities of the end point residue are always slightly lower than the ones of the starting.  This includes the cases for PHD2 A228S and P317R in 5B, although not as obvious as the one of PHD2 WT.  We agree with the reviewer that the sample dilution is a factor as a total volume of 16 microliters of reaction components was added to the solution to trigger the reaction after the first spectrum was acquired.  It is also likely that rate of prolyl hydroxylation becomes extremely slow with only a low amount of substrate available in the system.  Therefore, the reaction would not be 100% complete which was detected by the sensitive NMR experimentation.

(3) Data validating the CRISPR KO HEK293A cells is missing. 

We thank the reviewer for noting this oversight.  Western blots validating PHD2 KO in HEK293A cells will be added to the Supplementary Data file.

(4) The interpretation of the SEC data for the PHD2 mutants is a little problematic. Subtle alterations in the elution profiles may hint at different hydrodynamic radii, but as the samples were not loaded at equal concentrations or volumes, these data seem more anecdotal, rather than definitive. Repeating this multiple times, using matched samples, followed by comparison with standards loaded under identical buffer conditions, would significantly strengthen the conclusions one could make from the data. 

Agreed.  We will perform additional experiments as suggested with equal volume and concentration of each PHD2 construct loaded onto the SEC column for better assessment of aggregation.

Minor: 

(1) Justification for picking the seven residues is not clearly articulated. The authors say they picked 7 mutants with "distinct residue changes", but no further rationale is provided. 

Additional justification for the selection of the mutants will be added to the ‘Mutations across the PHD2 enzyme induce erythrocytosis’ section.  Briefly, some mutants were chosen based on their frequency in the clinical data and their presence in potential mutational hot spots.  Various mutations were noted at W334 and R371, while F366L was identified in multiple individuals.  Additionally, 9 cases of PHD2-driven disease were reported to be caused from mutations located between residues 200 to 210 while 13 cases were reported between residues 369-379, so G206C and R371H were chosen to represent potential hot spots.  To examine a potential genotype-phenotype relationship, two of the mutants responsible for neuroendocrine tumor development, A228S and H374R, were also selected.  Finally, mutations located close or on catalytic core residues (P317R, R371H, and H374R) were chosen to test for suspected defects.   

(2) A major finding of the paper is that a disease-associated mutation, P317R, can differentially affect HIF1 prolyhydroxylation, however, additional follow-up studies have not been performed to test this in cells or to validate the mutant in another method. Is it the position of the proline within the catalytic core, or the identity of the mutation that accounts for the selectivity? 

This is the very question that we are currently addressing but as a part of a follow-up study.  Indeed, one thought is that the preferential defect observed could be the result of the loss of proline, an exceptionally rigid amino acid that makes contact with the backbone twice, or the addition of a specific amino acid, namely arginine, a flexible amino acid with an added charge at this site.  Although beyond the scope of this manuscript, we will investigate whether such and other characteristics in this region of PHD2/HIF1α interface contribute to the differential hydroxylation. 

Reviewer #3 (Public review): 

Summary: 

This is an interesting and clinically relevant in vitro study by Taber et al., exploring how mutations in PHD2 contribute to erythrocytosis and/or neuroendocrine tumors. PHD2 regulates HIFα degradation through prolyl-hydroxylation, a key step in the cellular oxygen-sensing pathway. 

Using a time-resolved NMR-based assay, the authors systematically analyze seven patient-derived PHD2 mutants and demonstrate that all exhibit structural and/or catalytic defects. Strikingly, the P317R variant retains normal activity toward the C-terminal proline but fails to hydroxylate the N-terminal site. This provides the first direct evidence that N-terminal prolyl-hydroxylation is not dispensable, as previously thought. 

The findings offer valuable mechanistic insight into PHD2-driven effects and refine our understanding of HIF regulation in hypoxia-related diseases. 

Strengths: 

The manuscript has several notable strengths. By applying a novel time-resolved NMR approach, the authors directly assess hydroxylation at both HIF1α ODD sites, offering a clear functional readout. This method allows them to identify the P317R variant as uniquely defective in NODD hydroxylation, despite retaining normal activity toward CODD, thereby challenging the long-held view that the N-terminal proline is biologically dispensable. The work significantly advances our understanding of PHD2 function and its role in oxygen sensing, and might help in the future interpretation and clinical management of associated erythrocytosis. 

Weaknesses: 

(1) There is a lack of in vivo/ex vivo validation. This is actually required to confirm whether the observed defects in hydroxylation-especially the selective NODD impairment in P317R-are sufficient to drive disease phenotypes such as erythrocytosis. 

We thank the reviewer for this comment, and while we agree with this statement, the objective of this study per se was to elucidate the structural and/or functional defect caused by the various diseaseassociated mutations on PHD2. The subsequent study would be to validate whether the identified defects, in particular the selective NODD impairment, would lead to erythrocytosis in vivo.  However, we feel that such study would be beyond the scope of this manuscript.

(2) The reliance on HRE-luciferase reporter assays may not reliably reflect the PHD2 function and highlights a limitation in the assessment of downstream hypoxic signaling. 

Agreed.  All experimental assays and systems have limitations. The HRE-luciferase assay used in the present manuscript also has limitations such as the continuous expression of exogenous PHD2 mutants driven via CMV promoter. Thus, we performed several additional biophysical methodologies to interrogate the disease-causing PHD2 mutants. The limitations of the luciferase assay will be expanded in the revised manuscript. 

(3) The study clearly documents the selective defect of the P317R mutant, but the structural basis for this selectivity is not addressed through high-resolution structural analysis (e.g., cryo-EM). 

We thank the reviewer for the comment.  While solving the structure of PHD2 P317R in complex with HIFα substrate is beyond the scope for this study, a structure of PHD2 P317R in complex with a clinically used inhibitor has been solved (PDB:5LAT).  In analyzing this structure and that of PHD2 WT in complex with NODD, Chowdhury et al[2] stated that P317 makes hydrophobic contacts with LXXLAP motif on HIFα and R317 is predicted to interact differently with this motif. While this analysis does not directly elucidate the reason for the preferential NODD defect, it supports the possibility that P317R substitution may be more detrimental for enzymatic activity on NODD than CODD. We will discuss this notion in the revised manuscript. 

(4) Given the proposed central role of HIF2α in erythrocytosis, direct assessment of HIF2α hydroxylation by the mutants would have strengthened the conclusions. 

We thank the reviewer for this comment, but we feel that such study would be beyond the scope of the present study. We observed that the PHD2 binding patterns to HIF1α and HIF2α were similar, and we have previously assigned >95% of the amino acids in HIF1α ODD for NMR study[3]. Thus, we first focused on the elucidation of possible defects on disease-associated PHD2 mutants using HIF1α as the substrate with the supposition that an identified deregulation on HIF1α could be extended to HIF2α paralog. 

However, we agree with the reviewer that future studies should examine the impact of PHD2 mutants directly on HIF2α.  

References:

(1) Flashman, E. et al. Kinetic rationale for selectivity toward N- and C-terminal oxygen-dependent degradation domain substrates mediated by a loop region of hypoxia-inducible factor prolyl hydroxylases. J Biol Chem 283, 3808-3815 (2008).

(2) Chowdhury, R. et al. Structural basis for oxygen degradation domain selectivity of the HIF prolyl hydroxylases. Nat Commun 7, 12673 (2016).

(3) He, W., Gasmi-Seabrook, G.M.C., Ikura, M., Lee, J.E. & Ohh, M. Time-resolved NMR detection of prolyl-hydroxylation in intrinsically disordered region of HIF-1alpha. Proc Natl Acad Sci U S A 121, e2408104121 (2024).

Author response:

Reviewer #1 (Public review):

Summary:

The authors have investigated the role of FMRP in the formation and function of RNA granules in mouse brain/cultured hippocampal neurons. Most of their results indicate that FMRP does not have a role in the formation or function of RNA granules with specific mRNAs, but may have some role in distal RNA granules in neurons and their response to synaptic stimulation. This is an important work (though the results are mostly negative) in understanding the composition and function of neuronal RNA granules. The last part of the work in cultured neurons is disjointed from the rest of the manuscript, and the results are neither convincing nor provide any mechanistic insight.

Strengths:

(1) The study is quite thorough, the methods and analysis used are robust, and the conclusion and interpretation are diligent.

(2) The comparative study of Rat and Mouse RNA granules is very helpful for future studies.

(3) The conclusion that the absence of FMRP does not affect the RNA granule composition and many of its properties in the system the authors have chosen to study is well supported by the results.

(4) The difference in the response to DHPG stimulation concerning RNA granules described here is very interesting and could provide a basis for further studies, though it has some serious technical issues.

Weaknesses:

(1) The system used for the study (P5 mouse brain or DIV 8-10 cultured neuron) is surprising, as the majority of defects in the absence of FMRP are reported in later stages (P30+ brain and DIV 14+ neurons). It is important to test if the conclusions drawn here hold good at different developmental stages.

(2) The term 'distal granules' is very vague. Since there is no structural or biochemical characterization of these granules, it is difficult to understand how they are different from the proximal granules and why FMRP has an effect only on these granules.

(3) Since the manuscript does not find any effect of FMRP on neuronal RNA granules, it does not provide any new molecular insight with respect to the function of FMRP

Thank you for your comments and for pointing out the strengths of the manuscript. Unfortunately, we will not be able to respond to point #1. The protocol for purification of the ribosomes from RNA granules does not work in older brains (See Khandjian et al, 2004 PNAS 101:13357), presumably due to the presence of large concentrations of myelin. While it would be possible to repeat our results later in culture, we have no expectation that it would be different since we do observe DHPG induction of elongation dependent, initiation independent mGLUR-LTD in later cultures (Graber et al, 2017 J. Neuroscience 37:9116)..We will strengthen this caveat in the discussion that our results are only at a snapshot of development and that it is certainly possible that different results may be seen at different times. We agree with point 2 that ‘distal granules’ is a vague term. We will remove the term and clarify that we only quantified granules larger than 50 microns from the cell soma. We do not know if these granules are distinct. We would respectfully disagree with point #3 that the study does not provide molecular insight into the function of FMRP, as disproving that FMRP is important for stalling and determining the position of stalling removes a major hypothesis about the function of FMRP, and showing that something is not true, is at least to me, providing insight.

Reviewer #2 (Public review):

In the present manuscript, Li et al. use biochemical fractionation of "RNA granules" from P5 wildtype and FMR1 knock-out mouse brains to analyze their protein/RNA content, determine a single particle cryo-EM structure of contained ribosomes, and perform ribo-seq analysis of ribosome-protected RNA fragments (RPFs). The authors conclude from these that neither the composition of the ribosome granules, nor the state of their contained ribosomes, nor the mRNA positions with high ribosome occupancy change significantly. Besides minor changes in mRNA occupancy, the one change the authors identified is a decrease in puromycylated punctae in distal neurites of cultured primary neurons of the same mice, and their enhanced resistance to different pharmacological treatments. These results directly build on their earlier work (Anadolu et al., 2023) using analogous preparations of rat brains; the authors now perform a very similar study using WT and FMR1-KO mouse brains. This is an important topic, aiming to identify the molecular underpinnings of the FMRP protein, which is the basis of a major neurological disease. Unfortunately, several limitations of this study prevent it from being more convincing in its present form.

In order to improve this study, our main suggestions are as follows:

(1) The authors equate their biochemically purified "RG" fraction with their imaging-based detection of puromycin-positive punctae. They claim essentially no differences in RGs, but detect differences in the latter (mostly their abundance and sensitivity to DHPG/HHT/Aniso). In the discussion the authors acknowledge the inconsistency between these two modalities: "An inconsistency in our findings is the loss of distal RPM puncta coupled with an increase in the immunoreactivity for S6 in the RG." and "Thus, it may be that the RG is not simply made up of ribosomes from the large liquid-liquid phase RNA granules."

How can the authors be sure that they are analysing the same entities in both modalities? A more parsimonious explanation of their results would be that, while there might be some overlap, two different entities are analyzed. Much of the main message rests on this equivalence, and I believe the authors should show its validity.

(2) The authors show that increased nuclease digestion (and magnesium concentration) led to a reduction of their RPF sizes down to levels also seen by other researchers. Analyzing these now properly digested RPFs, the authors state that the CDS coverage and periodicity drastically improved, and that spurious enrichments of secretory mRNAs, which made up one of the major fractions in their previous work, are now reduced. In my opinion, this would be more appropriately communicated as a correction to their previous work, not as a main Figure in another manuscript.

(3) The fold changes reported in Figure 7 (ranging between log2(-0.2) and log2(+0.25)) are all extremely small and in my opinion should not be used to derive claims such as "The loss of FMRP significantly affected the abundance and occupancy of FMRP-Clipped mRNAs in WT and FMR1-KO RG (Fig 7A, 7B), but not their enrichment between RG and RCs".

(4) Figure 8 / S8-1 - The authors show that ~2/3 of their reads stem from PCR duplicates, but that even after removing those, the majority of peaks remain unaltered. At the same time, Figure S8-1 shows the total number of peaks to be 615 compared with 1392 before duplicate removal. Can the authors comment on this discrepancy? In addition, the dataset with properly removed artefacts should be used for their main display item instead of the current Figure 8.

(5) Figure 9 / S9-1, the density of punctae in both WT and FMR1-KO actually increases after treatment of HHT or Anisomycin (Figure S9-1 B-C). Even if a large fraction would now be "resistant to run-off", there should not be an increase. While this effect is deemed not significant, a much smaller effect in Figure 9C is deemed significant. Can the authors explain this? Given how vastly different the sample sizes are (ranging from 23 neurites in Figures S9-1 to 5,171 neurites in Figure 9), the authors should (randomly) sample to the same size and repeat their statistical analysis again, to improve their credibility.

Thank you for your comments. We agree with the issue in point #1 that the equivalence of RPM puncta with the RG fraction is an issue and while we believe that we show in a number of ways that the two are related (anisomycin-resistant puromycylation, puromyclation only at high concentrations consistent with the hybrid state, etc), we would respectfully disagree that our main message results from the equivalence of the RPM-labeled RNA granules in neurites and the ribosomes isolated by sedimentation. We will make this point clearer in our revision. For point #2, we agree that the changes with increased nuclease is somewhat out of place in a narrative sense, but it is clearly relevant to this work. Whether or not one sees this as a ‘correction’ or an interesting point will depend on a better characterization of the structures of the stalled polysomes. My personal view is that the nuclease resistance of cleavage near the RNA entrance site is quite interesting. Since we reproduce our results with a similar nuclease treatment in mice, as reported in our previous publication, I believe the comparison could be of interest in the future and would like to retain it. We agree with point #3 and will temper these claims in our revised version. For point #4, we will determine more carefully why the number of peaks differs and switch the main and supplemental figures. We apologize for the typo in the figure legend in Figure 9, 171, not 5171. The box plot line shows the median not the average and the data is clearly skewed such that the median and average are different (i.e. there is a two-fold decrease in the average density of distal puncta between WT and FMRP, but the average density is actually slightly decreased with HHT and A, although the median increases slightly. We will now report the results in distinct modalities to clarify this, and we will reexamine the statistics to better address the skewed distribution of values in the revised version.

Summary:

Li et al describe a set of experiments to probe the role of FMRP in ribosome stalling and RNA granule composition. The authors are able to recapitulate findings from a previous study performed in rats (this one is in mice).

Strengths:

(1) The work addresses an important and challenging issue, investigating mechanisms that regulate stalled ribosomes, focusing on the role of FMRP. This is a complicated problem, given the heterogeneity of the granules and the challenges related to their purification. This work is a solid attempt at addressing this issue, which is widely understudied.

(2) The interpretation of the results could be interesting, if supported by solid data. The idea that FMRP could control the formation and release of RNA granules, rather than the elongation by stalled ribosomes is of high importance to the field, offering a fresh perspective into translational regulation by FMRP.

(3) The authors focused on recapitulating previous findings, published elsewhere (Anadolu et al., 2023) by the same group, but using rat tissue, rather than mouse tissue. Overall, they succeeded in doing so, demonstrating, among other findings, that stalled ribosomes are enriched in consensus mRNA motifs that are linked to FMRP. These interesting findings reinforce the role of FMRP in formation and stabilization of RNA granules. It would be nice to see extensive characterization of the mouse granules as performed in Figure 1 of Anadolu and colleagues, 2023.

(4) Some of the techniques incorporated aid in creating novel hypotheses, such as the ribopuromycilation assay and the cryo-EM of granule ribosomes.

Weaknesses:

(1) The RNA granule characterization needs to be more rigorous. Coomassie is not proper for this type of characterization, simply because protein weight says little about its nature. The enrichment of key proteins is not robust and seems to not reach significance in multiple instances, including S6 and UPF1. Furthermore, S6 is the only proxy used for ribosome quantification. Could the authors include at least 3 other ribosomal proteins (2 from small, 2 from large subunit)?

(2) Page 12-13 - The Gene Ontology analysis is performed incorrectly. First, one should not rank genes by their RPKM levels. It is well known that housekeeping genes such as those related to actin dynamics, molecular transport and translation are highly enriched in sequencing datasets. It is usually more informative when significantly different genes are ranked by p adjust or log2 Fold Change, then compared against a background to verify enrichment of specific processes. However, the authors found no DEGs. I would suggest the removal of this analysis, incorporation of a gene set enrichment analyses (ranked by p adjust). I further suggest that the authors incorporate a dimensionality reduction analysis to demonstrate that the lack of significance stems from biology and not experimental artifacts, such as poor reproducibility across biological replicates.

Thank you for your comments on the strengths of the manuscript. We agree with point #1 that the mouse RNA granule characterization needs to be more rigorous and we plan to accomplish this in our revised version. Similarly, we will incorporate the additional statistical analysis suggested by the reviewer in a revised version.

Author response:

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

Reviewer #1 (Public review):

Summary:

The authors report a study on how stimulation of receptive-field surround of V1 and LGN neurons affects their firing rates. Specifically, they examine stimuli in which a grey patch covers the classical RF of the cell and a stimulus appears in the surround. Using a number of different stimulus paradigms they find a long latency response in V1 (but not the LGN) which does not depend strongly on the characteristics of the surround grating (drifting vs static, continuous vs discontinuous, predictable grating vs unpredictable pink noise). They find that population responses to simple achromatic stimuli have a different structure that does not distinguish so clearly between the grey patch and other conditions and the latency of the response was similar regardless of whether the center or surround was stimulated by the achromatic surface. Taken together they propose that the surround-response is related to the representation of the grey surface itself. They relate their findings to previous studies that have put forward the concept of an ’inverse RF’ based on strong responses to small grey patches on a full-screen grating. They also discuss their results in the context of studies that suggest that surround responses are related to predictions of the RF content or figure-ground segregation. Strengths:

I find the study to be an interesting extension of the work on surround stimulation and the addition of the LGN data is useful showing that the surround-induced responses are not present in the feedforward path. The conclusions appear solid, being based on large numbers of neurons obtained through Neuropixels recordings. The use of many different stimulus combinations provides a rich view of the nature of the surround-induced responses.

Weaknesses:

The statistics are pooled across animals, which is less appropriate for hierarchical data. There is no histological confirmation of placement of the electrode in the LGN and there is no analysis of eye or face movements which may have contributed to the surround-induced responses. There are also some missing statistics and methods details which make interpretation more difficult.

We thank the reviewer for their positive and constructive comments, and have addressed these specific issues in response to the minor comments. For the statistics across animals, we refer to “Reviewer 1 recommendations” point 1. For the histological analysis, we refer to “Reviewer 1 recommendations point 2”. For the eye and facial movements, we refer to “Reviewer 1 recommendations point 5”. Concerning missing statistics and methods details, we refer to various responses to “Reviewer 1 recommendations”. We thoroughly reviewed the manuscript and included all missing statistical and methodological details.

Reviewer #2 (Public review):

Cuevas et al. investigate the stimulus selectivity of surround-induced responses in the mouse primary visual cortex (V1). While classical experiments in non-human primates and cats have generally demonstrated that stimuli in the surround receptive field (RF) of V1 neurons only modulate activity to stimuli presented in the center RF, without eliciting responses when presented in isolation, recent studies in mouse V1 have indicated the presence of purely surround-induced responses. These have been linked to prediction error signals. In this study, the authors build on these previous findings by systematically examining the stimulus selectivity of surround-induced responses.

Using neuropixels recordings in V1 and the dorsal lateral geniculate nucleus (dLGN) of head-fixed, awake mice, the authors presented various stimulus types (gratings, noise, surfaces) to the center and surround, as well as to the surround only, while also varying the size of the stimuli. Their results confirm the existence of surround-induced responses in mouse V1 neurons, demonstrating that these responses do not require spatial or temporal coherence across the surround, as would be expected if they were linked to prediction error signals. Instead, they suggest that surround-induced responses primarily reflect the representation of the achromatic surface itself.

The literature on center-surround effects in V1 is extensive and sometimes confusing, likely due to the use of different species, stimulus configurations, contrast levels, and stimulus sizes across different studies. It is plausible that surround modulation serves multiple functions depending on these parameters. Within this context, the study by Cuevas et al. makes a significant contribution by exploring the relationship between surround-induced responses in mouse V1 and stimulus statistics. The research is meticulously conducted and incorporates a wide range of experimental stimulus conditions, providing valuable new insights regarding center-surround interactions.

However, the current manuscript presents challenges in readability for both non-experts and experts. Some conclusions are difficult to follow or not clearly justified.

I recommend the following improvements to enhance clarity and comprehension:

(1) Clearly state the hypotheses being tested at the beginning of the manuscript.

(2) Always specify the species used in referenced studies to avoid confusion (esp. Introduction and Discussion).

(3) Briefly summarize the main findings at the beginning of each section to provide context.

(4) Clearly define important terms such as “surface stimulus” and “early vs. late stimulus period” to ensure understanding.

(5) Provide a rationale for each result section, explaining the significance of the findings.

(6) Offer a detailed explanation of why the results do not support the prediction error signal hypothesis but instead suggest an encoding of the achromatic surface.

These adjustments will help make the manuscript more accessible and its conclusions more compelling.

We thank the reviewer for their constructive feedback and for highlighting the need for improved clarity regarding the hypotheses and their relation to the experimental findings.

• We have strongly improved the Introduction and Discussion section, explaining the different hypotheses and their relation to the performed experiments.

• In the Introduction, we have clearly outlined each hypothesis and its predictions, providing a structured framework for understanding the rationale behind our experimental design. • In the Discussion, we have been more explicit in explaining how the experimental findings inform these hypotheses.

• We explicitly mentioned the species used in the referenced studies.

• We provided a clearer rationale for each experiment in the Results section.

We have also always clearly stated the species that previous studies used, both in the Introduction and Discussion section.

Reviewer #3 (Public review):

Summary:

This paper explores the phenomenon whereby some V1 neurons can respond to stimuli presented far outside their receptive field. It introduces three possible explanations for this phenomenon and it presents experiments that it argues favor the third explanation, based on figure/ground segregation.

Strengths:

I found it useful to see that there are three possible interpretations of this finding (prediction error, interpolation, and figure/ground). I also found it useful to see a comparison with LGN responses and to see that the effect there is not only absent but actually the opposite: stimuli presented far outside the receptive field suppress rather than drive the neurons. Other experiments presented here may also be of interest to the field.

Weaknesses:

The paper is not particularly clear. I came out of it rather confused as to which hypotheses were still standing and which hypotheses were ruled out. There are numerous ways to make it clearer.

We thank the reviewer for their constructive feedback and for highlighting the need for improved clarity regarding the hypotheses and their relation to the experimental findings.

• We have strongly improved the Introduction and Discussion section, explaining the different hypotheses and their relation to the performed experiments.

• In the Introduction, we have clearly outlined each hypothesis and its predictions, providing a structured framework for understanding the rationale behind our experimental design. • In the Discussion, we have been more explicit in explaining how the experimental findings inform these hypotheses.

** Recommendations for the Authors:**

Reviewer #1 (Recommendations for the Authors):

(1) Given the data is hierarchical with neurons clustered within 6 mice (how many recording sessions per animal?) I would recommend the use of Linear Mixed Effects models. Simply pooling all neurons increases the risk of false alarms.

To clarify: We used the standard method for analyzing single-unit recordings, by comparing the responses of a population of single neurons between two different conditions. This means that the responses of each single neuron were measured in the different conditions, and the statistics were therefore based on the pairwise differences computed for each neuron separately. This is a common and standard procedure in systems neuroscience, and was also used in the previous studies on this topic (Keller et al., 2020; Kirchberger et al., 2023). We were not concerned with comparing two groups of animals, for which hierarchical analyses are recommended. To address the reviewer’s concern, we did examine whether differences between baseline and the gray/drift condition, as well as the gray/drift compared to the grating condition, were consistent across sessions, which was indeed the case. These findings are presented in Supplementary Figure 6.

(2) Line 432: “The study utilized three to eight-month-old mice of both genders”. This is confusing, I assume they mean six mice in total, please restate. What about the LGN recordings, were these done in the same mice? Can the authors please clarify how many animals, how many total units, how many included units, how many recording sessions per animal, and whether the same units were recorded in all experiments?

We have now clarified the information regarding the animals used in the Methods section.

• We state that “We included female and male mice (C57BL/6), a total of six animals for V1 recordings between three and eight months old. In two of those animals, we recorded simultaneously from LGN and V1.”

• We state that“For each animal, we recorded around 2-3 sessions from each hemisphere, and we recorded from both hemispheres.”

• We noted that the number of neurons was not mentioned for each figure caption. We apologize for this omission. We have now added the number for all of the figures and protocols to the revised manuscript. We note that the same neurons were recorded for the different conditions within each protocol, however because a few sessions were short we recorded more units for the grating protocol. Note that we did not make statistical comparisons between protocols.

(3) I see no histology for confirmation of placement of the electrode in the LGN, how can they be sure they were recording from the LGN? There is also little description of the LGN experiments in the methods.

For better clarity, we have included a reconstruction of the electrode track from histological sections of one animal post-experiment (Figure S4). The LGN was targeted via stereotactical surgery, and the visual responses in this area are highly distinct. In addition, we used a flash protocol to identify the early-latency responses typical for the LGN, which is described in the Methods section: “A flash stimulus was employed to confirm the locations of LGN at the beginning of the recording sessions, similar to our previous work in which we recorded from LGN and V1 simultaneously (Schneider et al., 2023). This stimulus consisted of a 100 ms white screen and a 2 s gray screen as the inter-stimulus interval, designed to identify visually responsive areas. The responses of multi-unit activity (MUA) to the flash stimulus were extracted and a CSD analysis was then performed on the MUA, sampling every two channels. The resulting CSD profiles were plotted to identify channels corresponding to the LGN. During LGN recordings, simultaneous recordings were made from V1, revealing visually responsive areas interspersed with non-responsive channels.”

(4) Many statements are not backed up by statistics, for example, each time the authors report that the response at 90degree sign is higher than baseline (Line 121 amongst other places) there is no test to support this. Also Line 140 (negative correlation), Line 145, Line 180.

For comparison purposes, we only presented statistical analyses across conditions. However, we have now added information to the figure captions stating that all conditions show values higher than the baseline.

(5) As far as I can see there is no analysis of eye movements or facial movements. This could be an issue, for example, if the onset of the far surround stimuli induces movements this may lead to spurious activations in V1 that would be interpreted as surround-induced responses.

To address this point, we have included a supplementary figure analyzing facial movements across different sessions and comparing them between conditions (Supplementary Figure 5). A detailed explanation of this analysis has been added to the Methods section. Overall, we observed no significant differences in face movements between trials with gratings, trials with the gray patch, and trials with the gray screen presented during baseline. Animals exhibited similar face movements across all three conditions, supporting the conclusion that the observed neural firing rate increases for the gray-patch condition are not related to face movements.

(6) The experiments with the rectangular patch (Figure 3) seem to give a slightly different result as the responses for large sizes (75, 90) don’t appear to be above baseline. This condition is also perceptually the least consistent with a grey surface in the RF, the grey patch doesn’t appear to occlude the surface in this condition. I think this is largely consistent with their conclusions and it could merit some discussion in the results/discussion section.

While the effect is maybe a bit weaker, the total surround stimulated also covers a smaller area because of the large rectangular gray patch. Furthermore, the early responses are clearly elevated above baseline, and the responses up to 70 degrees are still higher than baseline. Hence we think this data point for 90 degrees does not warrant a strong interpretation.

Minor points:

(1) Figure 1h: What is the statistical test reported in the panel (I guess a signed rank based on later figures)? Figure 4d doesn’t appear to be significantly different but is reported as so. Perhaps the median can be indicated on the distribution?

We explained that we used a signed rank test for Figure 1h and now included the median of the distributions in Figure 4d.

(2) What was the reason for having the gratings only extend to half the x-axis of the screen, rather than being full-screen? This creates a percept (in humans at least) that is more consistent with the grey patch being a hole in the grating as the grey patch has the same luminance as the background outside the grating.

We explained in the Methods section that “We presented only half of the x-axis due to the large size of our monitor, in order to avoid over-stimulation of the animals with very large grating stimuli.”. Perceptually speaking, the gray patch appears as something occluding the grating, not as a “hole”.

(3) Line 103: “and, importantly, had less than 10degree sign (absolute) distance to the grating stimulus’ RF center.” Re-phrase, a stimulus doesn’t have an RF center.

We corrected this to “We included only single units into the analysis that met several criteria in terms of visual responses (see Methods) and, importantly, the RF center had less than 10(absolute) distance to the grating stimulus’ center. ”.

(4) Line 143: “We recorded single neurons LGN” - should be “single LGN neurons”.

We corrected this to “we recorded single LGN neurons”.

(5) Line 200: They could spell out here that the latency is consistent with the latency observed for the grey patch conditions in the previous experiments. (6) Line 465: This is very brief. What criteria did they use for single-unit assignation? Were all units well-isolated or were multi-units included?

We clarified in the Methods section that “We isolated single units with Kilosort 2.5 (Steinmetz et al., 2021) and manually curated them with Phy2 (Rossant et al., 2021). We included only single units with a maximum contamination of 10 percent.”

(7) Line 469: “The experiment was run on a Windows 10”. Typo.

We corrected this to “The experiment was run on Windows 10”.

(9) Line 481: “We averaged the response over all trials and positions of the screen”. What do they mean by ’positions of the screen’?

We changed this to “We computed the response for each position separately right, by averaging the response across all the trials where a square was presented at a given position.”

(9) Line 483: “We fitted an ellipse in the center of the response”. How?

We additionally explain how we preferred the detection of the RF using an ellipse fitting: “A heatmap of the response was computed. This heatmap was then smoothed, and we calculated the location of the peak response. From the heatmap we calculated the centroid of the response using the function regionprops.m that finds unique objects, we then selected the biggest area detected. Using the centroids provided as output. We then fitted an ellipse centered on this peak response location to the smoothed heatmap using the MATLAB function ellipse.m.“

(10) Line 485 “...and positioned the stimulus at the response peak previously found”. Unclear wording, do you mean the center of the ellipse fit to the MUA response averaged across channels or something else? (11) Line 487: “We performed a permutation test of the responses inside the RF detected vs a circle from the same area where the screen was gray for the same trials.”. The wording is a bit unclear here, can they clarify what they mean by the ’same trials’, what is being compared to what here?

We used a permutation test to compare the neuron’s responses to black and white squares inside the RF to the condition where there was no square in the RF (i.e. the RF was covered by the gray background).

(12) Was the pink noise background regenerated on each trial or as the same noise pattern shown on each trial?

We explain that “We randomly presented one of two different pink noise images”

(13) Line 552: “...used a time window of the Gaussian smoothing kernel from-.05 to .05”. Missing units.

We explained that “we used a time window of the Gaussian smoothing kernel from -.05 s to .05 s, with a standard deviation of 0.0125 s.”

(14) Line 565: “Additionally, for the occluded stimulus, we included patch sizes of 70 degree sign and larger.”. Not sure what they’re referring to here.

We changed this to: “For the population analyses, we analyzed the conditions in which the gray patch sizes were 70 degrees and 90 degrees”.

(15) Line 569: What is perplexity, and how does changing it affect the t-SNE embeddings?

Note that t-SNE is only used for visualization purposes. In the revised manuscript, we have expanded our explanation regarding the use of t-SNE and the choice of perplexity values. Specifically, we have clarified that we used a perplexity value of 20 for the Gratings with circular and rectangular occluders and 100 for the black-and-white condition. These values were empirically selected to ensure that the groups in the data were clearly separable while maintaining the balance between local and global relationships in the projected space. This choice allowed us to visually distinguish the different groups while preserving the meaningful structure encoded in the dissimilarity matrices. In particular, varying the perplexity values would not alter the conclusions drawn from the visualization, as t-SNE does not affect the underlying analytical steps of our study.

(16) Line 572: “We trained a C-Support Vector Classifier based on dissimilarity matrices”. This is overly brief, please describe the construction of the dissimilarity matrices and how the training was implemented. Was this binary, multi-class? What conditions were compared exactly?

In the revised manuscript, we have expanded our explanation regarding the construction of the dissimilarity matrices and the implementation of the C-Support Vector Classification (C-SVC) model (See Methods section).

The dissimilarity matrices were calculated using the Euclidean distance between firing rate vectors for all pairs of trials (as shown in Figure 6a-b). These matrices were used directly as input for the classifier. It is important to note that t-SNE was not used for classification but only for visualization purposes. The classifier was binary, distinguishing between two classes (e.g., Dr vs St). We trained the model using 60% of the data for training and used 40% for testing. The C-SVC was implemented using sklearn, and the classification score corresponds to the average accuracy across 20 repetitions.

Reviewer #2 (Recommendations for the Authors):

The relationship between the current paper and Keller et al. is challenging to understand. It seems like the study is critiquing the previous study but rather implicitly and not directly. I would suggest either directly stating the criticism or presenting the current study as a follow-up investigation that further explores the observed effect or provides an alternative function. Additionally, defining the inverse RF versus surround-induced responses earlier than in the discussion would be beneficial. Some suggestions:

(1) The introduction is well-written, but it would be helpful to clearly define the hypotheses regarding the function of surround-induced responses and revisit these hypotheses one by one in the results section.

Indeed, we have generally improved the Introduction of the manuscript, and stated the hypotheses and their relationships to the Experiments more clearly.

(2) Explicitly mention how you compare classic grating stimuli of varying sizes with gray patch stimuli. Do the patch stimuli all come with a full-field grating? For the full-field grating, you have one size parameter, while for the patch stimuli, you have two (size of the patch and size of the grating).

We now clearly describe how we compare grating stimuli of varying sizes with gray patch stimuli.

(3) The third paragraph in the introduction reads more like a discussion and might be better placed there.

We have moved content from the third paragraph of the Introduction to the Discussion, where it fits more naturally.

(4) Include 1-2 sentences explaining how you center RFs and detail the resolution of your method.

We have added an explanation to the Methods: “To center the visual stimuli during the recording session, we averaged the multiunit activity across the responsive channels and positioned the stimulus at the center of the ellipse fit to the MUA response averaged across channels.”.

(5) Motivate the use of achromatic stimuli. This section is generally quite hard to understand, so try to simplify it.

We explained better in the Introduction why we performed this particular experiment.

(6) The decoding analysis is great, but it is somewhat difficult to understand the most important results. Consider summarizing the key findings at the beginning of this section.

We now provide a clearer motivation at the start of the Decoding section.

Reviewer #3 (Recommendations for the Authors):

I have a few suggestions to improve the clarity of the presentation.

Abstract: it lists a series of observations and it ends with a conclusion (“based on these findings...”). However, it provides little explanation for how this conclusion would arise from the observations. It would be more helpful to introduce the reasoning at the top and show what is consistent with it.

We have improved the abstract of the paper incorporating this feedback.

To some extent, this applies to Results too. Sometimes we are shown the results of some experiment just because others have done a similar experiment. Would it be better to tell us which hypotheses it tests and whether the results are consistent with all 3 hypotheses or might rule one or more out? I came out of the paper rather confused as to which hypotheses were still standing and which hypotheses were ruled out.

We have strongly improved our explanation of the hypotheses and the relationships to the experiments in the Introduction.

It would be best if the Results section focused on the results of the study, without much emphasis on what previous studies did or did not measure. Here, instead, in the middle of Results we are told multiple times what Keller et al. (2020) did or did not measure, and what they did or did not find. Please focus on the questions and on the results. Where they agree or disagree with previous papers, tell us briefly that this is the case.

We have revised the Results section in the revised manuscript, and ensured that there is much less focus on what previous studies did in the Results. Differences to previous work are now discussed in the Discussion section.

The notation is extremely awkward. For instance “Gc” stands for two words (Gray center) but “Gr” stands for a single word (Grating). The double meaning of G is one of many sources of confusion.

This notation needs to be revised. Here is one way to make it simpler: choose one word for each type of stimulus (e.g. Gray, White, Black, Drift, Stat, Noise) and use it without abbreviations. To indicate the configuration, combine two of those words (e.g. Gray/Drift for Gray in the center and Drift in the surround).

We have corrected the notation in the figures and text to enhance readability and improve the reader’s understanding.

Figure 1e and many subsequent ones: it is not clear why the firing rate is shown in a logarithmic scale. Why not show it in a linear scale? Anyway, if the logarithmic scale is preferred for some reason, then please give us ticks at numbers that we can interpret, like 0.1,1,10,100... or 0.5,1,2,4... Also, please use the same y-scale across figures so we can compare.

To clarify: it is necessary to normalize the firing rates relative to baseline, in order to pool across neurons. However such a divisive normalization would be by itself problematic, as e.g. a change from 1 to 2 is the same as a change from 1 to 0.5, on a linear scale. Furthermore such division is highly outlier sensitive. For this reason taking the logarithm (base 10) of the ratio is an appropriate transformation. We changed the tick labels to 1, 2, 4 like the reviewer suggested.

Figure 3: it is not clear what “size” refers to in the stimuli where there is no gray center. Is it the horizontal size of the overall stimulus? Some cartoons might help. Or just some words to explain.

Figure 3: if my understanding of “size” above is correct, the results are remarkable: there is no effect whatsoever of replacing the center stimulus with a gray rectangle. Shouldn’t this be remarked upon?

We have added a paragraph under figure 3 and in the Methods section explaining that the sizes represent the varying horizontal dimensions of the rectangular patch. In this protocol, the classical condition (i.e. without gray patch) was shown only as full-field gratings, which is depicted in the plot as size 0, indicating no rectangular patch was present.

DETAILS The word “achromatic” appears many times in the paper and is essentially uninformative (all stimuli in this study are achromatic, including the gratings). It could be removed in most places except a few, where it is actually used to mean “uniform”. In those cases, it should be replaced by “uniform”.

Ditto for the word “luminous”, which appears twice and has no apparent meaning. Please replace it with “uniform”.

We have replaced the words achromatic and luminous with “uniform” stimuli to improve the clarity when we refer to only black or white stimuli.

Page 3, line 70: “We raise some important factors to consider when describing responses to only surround stimulation.” This sentence might belong in the Discussion but not in the middle of a paragraph of Results.

We removed this sentence.

Neuropixel - Neuropixels (plural)

“area LGN” - LGN

We corrected for misspellings.

References

Keller, A.J., Roth, M.M., Scanziani, M., 2020. Feedback generates a second receptive field in neurons of the visual cortex. Nature 582, 545–549. doi:10.1038/s41586-020-2319-4.

Kirchberger, L., Mukherjee, S., Self, M.W., Roelfsema, P.R., 2023. Contextual drive of neuronal responses in mouse V1 in the absence of feedforward input. Science Advances 9, eadd2498. doi:10. 1126/sciadv.add2498.

Rossant, C., et al., 2021. phy: Interactive analysis of large-scale electrophysiological data. https://github.com/cortex-lab/phy.

Schneider, M., Tzanou, A., Uran, C., Vinck, M., 2023. Cell-type-specific propagation of visual flicker. Cell Reports 42.

Steinmetz, N.A., Aydin, C., Lebedeva, A., Okun, M., Pachitariu, M., Bauza, M., Beau, M., Bhagat, J., B¨ohm, C., Broux, M., Chen, S., Colonell, J., Gardner, R.J., Karsh, B., Kloosterman, F., Kostadinov, D., Mora-Lopez, C., O’Callaghan, J., Park, J., Putzeys, J., Sauerbrei, B., van Daal,R.J.J., Vollan, A.Z., Wang, S., Welkenhuysen, M., Ye, Z., Dudman, J.T., Dutta, B., Hantman, A.W., Harris, K.D., Lee, A.K., Moser, E.I., O’Keefe, J., Renart, A., Svoboda, K., H¨ausser, M., Haesler, S., Carandini, M., Harris, T.D., 2021. Neuropixels 2.0: A miniaturized high-density probe for stable, long-term brain recordings. Science 372, eabf4588. doi:10.1126/science.abf4588.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This work aims to improve our understanding of the factors that influence female-on-female aggressive interactions in gorilla social hierarchies, using 25 years of behavioural data from five wild groups of two gorilla species. Researchers analysed aggressive interactions between 31 adult females, using behavioural observations and dominance hierarchies inferred through Elo-rating methods. Aggression intensity (mild, moderate, severe) and direction (measured as the rank difference between aggressor and recipient) were used as key variables. A linear mixed-effects model was applied to evaluate how aggression direction varied with reproductive state (cycling, trimester-specific pregnancy, or lactation) and sex composition of the group. This study highlights the direction of aggressive interactions between females, with most interactions being directed from higher- to lower-ranking adult females close in social rank. However, the results show that 42% of these interactions are directed from lower- to higher-ranking females. Particularly, lactating and pregnant females targeted higher-ranking individuals, which the authors suggest might be due to higher energetic needs, which increase risk-taking in lactating and pregnant females. Sex composition within the group also influenced which individuals were targeted. The authors suggest that male presence buffers female-on-female aggression, allowing females to target higher-ranking females than themselves. In contrast, females targeted lower-ranking females than themselves in groups with a larger ratio of females, which supposes a lower risk for the females since the pool of competitors is larger. The findings provide an important insight into aggression heuristics in primate social systems and the social and individual factors that influence these interactions, providing a deeper understanding of the evolutionary pressures that shape risk-taking, dominance maintenance, and the flexibility of social strategies in group-living species.

The authors achieved their aim by demonstrating that aggression direction in female gorillas is influenced by factors such as reproductive condition and social context, and their results support the broader claim that aggression heuristics are flexible. However, some specific interpretations require further support. Despite this, the study makes a valuable contribution to the field of behavioural ecology by reframing how we think about intra-sexual competition and social rank maintenance in primates.

Strengths:

One of the study's major strengths is the use of an extensive dataset that compiles 25 years of behavioural data and 6871 aggressive interactions between 31 adult females in five social groups, which allows for a robust statistical analysis. This study uses a novel approach to the study of aggression in social groups by including factors such as the direction and intensity of aggressive interactions, which offers a comprehensive understanding of these complex social dynamics. In addition, this study incorporates ecological and physiological factors such as the reproductive state of the females and the sex composition of the group, which allows an integrative perspective on aggression within the broader context of body condition and social environment. The authors successfully integrate their results into broader evolutionary and ecological frameworks, enriching discussions around social hierarchies and risk sensitivity in primates and other animals.

Thank you for the positive assessment of our work and the nice summary of the manuscript!

Weaknesses:

Although the paper has a novel approach by studying the effect of reproductive state and social environment on female-female aggression, the use of observational data without experimental manipulation limits the ability to establish causation. The authors suggest that the difference observed in female aggression direction between groups with different sex composition might be indicative of male presence buffering aggression, which seems speculative, as no direct evidence of male intervention or support was reported. Similarly, the use of reproductive state as a proxy for energetic need is an indirect measure and does not account for actual energy expenditure or caloric intake, which weakens the authors' claims that female energetic need induces risk-taking. Overall, this paper would benefit from stronger justification and empirical support to strengthen the conclusions of the study about the mechanisms driving female aggression in gorillas.

We agree that experimental manipulation would allow us to extend our work. Unfortunately, this is not possible with wild, endangered gorillas.

We have now added more references (Watts 1994; Watts 1997) and enriched our arguments regarding male presence buffering aggression. Previous research suggests that male gorillas may support lower-ranking females and they may intervene in female-female conflicts (Sicotte 2002). Unfortunately, our dataset did not allow us to test for male protection. We conduct proximity scans every 10 minutes and these scans are not associated to each interaction, meaning that we cannot reliably test if proximity to a male influence the likelihood to receive aggression.

We have now clearly stated that reproductive state is an indirect proxy for energetic needs. We agree with your point about energy intake and expenditure, but unfortunately, we do not have data on energy expenditure or caloric intake to allow us to delve into more fine-grained analyses.

Overall, we have tried to enrich the justification and empirical support to strengthen our conclusions by clarifying the text and adding more examples and references.

Reviewer #2 (Public review):

Summary:

The authors' aim in this study is to assess the factors that can shift competitive incentives against higher- or lower-ranking groupmates in two gorilla species.

Strengths:

This is a relevant topic, where important insights could be gained. The authors brought together a substantial dataset: a long-term behavioral dataset representing two gorilla species from five social groups.

Weaknesses:

The authors have not fully shown the data used in the model and explored the potential of the model. Therefore, I remain cautious about the current results and conclusions.

Some specific suggestions that require attention are

(1) The authors described how group size can affect aggression patterns in some species (line 54), using a whole paragraph, but did not include it as an explanation variable in their model, despite that they stated the overall group size can "conflate opposing effects of females and males" (line 85). I suggest underlining the effects of numbers of males or/and females here and de-emphasizing the effect of group size in the Introduction.

We did not use group size as a main predictor, as has been commonly done in other species, because of potentially conflating opposing effects of males and females. To further stress this point, we have specifically added in the introduction: “group size, the overall number of individuals in the group, might not be a good predictor of aggression heuristics, as it can conflate the effects of different kinds of individuals on aggression (see Smit & Robbins 2024 for an example of opposing effects of the number of females and number of males on female gorilla aggression).”

We also “ran our analysis testing for group size (number of weaned individuals in the group), instead of the numbers of females and males, [and] its influence on interaction score was not significant (estimate=-0.001, p-value=0.682).”

(2) There should be more details given about how the authors calculated individual Elo-ratings (line 98). It seems that authors pooled all avoidance/displacement behaviors throughout the study period. But how often was the Elo-rating they included in the model calculated? By the day or by the month? I guess it was by the day, as they "estimate female reproductive state daily" (line 123). If so, it should be made clear in the text.

We rephrased accordingly: “We used all avoidance and displacement interactions throughout the study period and we used the function elo.seq from R package EloRating to infer daily individual female Elo-scores”. We also clarified that “This method takes into account the temporal sequence of interactions and updates an individual’s Elo-scores each day the individual interacted with another...”

In addition, all groups were long-term studied, and the group composition seems fluctuant based on the Table 1 in Reference 11. When an individual enters/leaves the group with a stable hierarchy, it takes time before the hierarchy turns stable again. If the avoidance/displacement behaviors used for the rank relationship were not common, it would take a few days or maybe longer. Also, were the aggressive behaviors more common during rank fluctuations? In other words, if avoidance/displacement behaviors and aggressive behaviors occur simultaneously during rank fluctuations, how did the authors deal with it and take it into consideration in the analysis?

We have shown in Reference 25 (Smit & Robbins 2025) after Reference 11 (Smit & Robbins 2024) that females form highly stable hierarchies, and that dyadic dominance relationships are not influenced by dispersal or death of third individuals. Notably, new immigrant females usually start at and remain low ranking, without large fluctuations in rank. Therefore, the presence of any fluctuation periods have limited influence in the aggressive interactions in our study system.

The authors emphasized several times in the text that gorillas "form highly stable hierarchical relationships". Also, in Reference 25, they found very high stabilities of each group's hierarchy. However, the number of females involved in that analysis was different from that used here. They need to provide more basic info on each group's dominance hierarchy and verify their statement. I strongly suggest that the authors display Elo-rating trajectories and necessary relevant statistics for each group throughout the study period as part of the supplementary materials.

In fact, the females involved in the present analysis and the analysis of Smit & Robbins 2025 are the same. Our present analysis is based on the hierarchies of Smit & Robbins 2025. Note that female gorillas disperse and occasionally immigrate to another study group. This is why some females may appear in the hierarchies of more than one group, giving the impression that there are more females involved in the analysis of Smit & Robbins 2025 (e.g. by counting the lines in the Elo-rating plots). We now specifically state that “We present these interactions and hierarchies in detail in Smit & Robbins 2025”, to clarify that the hierarchies are the same.

(3) The authors stated why they differentiated the different stages based on female reproductive status. They also referred to the differences in energetic needs between stages of pregnancy and lactation (lines 127-128). However, in the mixed model, they only compared the interaction score between the female cycling stage and other stages. The model was not well explained, and the results could be expanded. I suggest conducting more pairwise comparisons in the model and presenting the statistics in the text, if there are significant results. If all three pregnancy stages differed significantly from cycling and lactating stages but not from each other, they may be merged as one pregnancy stage. More in-depth analysis would help provide better answers to the research questions.

Thank you for pointing this out. First, when we considered one pregnancy stage, pregnant females showed indeed a significantly greater interaction score than females in other reproductive stages. We have now included that in the manuscript. However, we still find relevant to test for the different stages of pregnancy, given the difference of energetic needs in these stages. We have now included the pairwise comparisons in a new table (Table 2).

Reviewer #3 (Public review):

Smit and Robbins' manuscript investigates the dynamics of aggression among female groupmates across five gorilla groups. The authors utilize longitudinal data to examine how reproductive state, group size, presence of males, and resource availability influence patterns of aggression and overall dominance rankings as measured by Elo scores. The findings underscore the important role of group composition and reproductive status, particularly pregnancy, in shaping dominance relationships in wild gorillas. While the study addresses a compelling and understudied topic, I have several comments and suggestions that may enhance clarity and improve the reader's experience.

(1) Clarification of longitudinal data - The manuscript states that 25 years of behavioral data were used, but this number appears unclear. Based on my calculations, the maximum duration of behavioral observation for any one group appears to be 18 years. Specifically:

• ATA: 6 years

• BIT: 8 years

• KYA: 18 years

• MUK: 6 years

• ORU: 8 years

I recommend that the authors clarify how the 25-year duration was derived.

Indeed none of the five study “groups” has been studied for 25 years in a row. However, MUK emerged from a fission of group KYA in early 2016. So, from the start of group KYA in October 1998 to the end of group MUK in December 2023, there are 25 years and 2 months. We have now rephrased to “...starting in 1998 in one of the mountain gorilla groups” in the introduction, and to “We use a long-term behavioural dataset on five wild groups of the two gorilla species, starting in 1998” in the abstract.

(2) Consideration of group size - The authors mention that group size was excluded from analyses to avoid conflating the opposing effects of female and male group members. While this is understandable, it may still be beneficial to explore group size effects in supplementary analyses. I suggest reporting statistics related to group size and potentially including a supplementary figure. Additionally, given that the study includes both mountain and wild gorillas, it would be helpful to examine whether any interspecies differences are apparent.

We have now added the suggested extra test: “When we ran our analysis testing for group size (number of weaned individuals in the group), instead of the numbers of females and males, its influence on interaction score was not significant (estimate=-0.001, p-value=0.682).”

Regarding species differences: In our analysis, we test for species (mountain vs western) and we find no significant differences between the two. This is stated in the results.

(3) Behavioral measures clarification - Lines 112-116 describe the types of aggressive behaviors observed. It would be helpful to clarify how these behaviors differ from those used to calculate Elo scores, or whether they overlap. A brief explanation would improve transparency regarding the methodology.

We now added short explanations into brackets for behaviours that are not obvious. We also added a sentence in the text to clarify the difference with the behaviours used to calculate Elo scores: “These two behaviours [avoidance and displacement] are ritualized, occurring in absence of aggression, they are considered a more reliable proxy of power relationships over aggression, and they are typically used to infer gorilla hierarchical relationships”.

(4) Aggression rates versus Elo scores - The manuscript uses aggression rates rather than dominance rank (as measured by Elo scores) as the main outcome variable, but there is no explanation on why. How would the results differ if aggression rates were replaced or supplemented with Elo scores? The current justification for prioritizing aggression rates over dominance rank needs to be more clearly supported.

The sentence we added above (“These two behaviours [avoidance and displacement] are ritualized, occurring in absence of aggression, they are considered a more reliable proxy of power relationships over aggression, and they are typically used to infer gorilla hierarchical relationships”) and the first paragraph of the results hopefully clarify that ritualized agonistic interactions are generally directionally consistent and more reliably capture the highly stable dominance relationships of female gorillas. This approach has been used to calculate dominance rank in gorillas in all studies that have considered it, dating back to the 1970s (namely in studies by Harcourt and Watts). On the other hand, aggression can be context dependent (we now clearly note that in the beginning of the Methods paragraph on aggressive interactions). Therefore, we use Eloscores inferred from ritualized interactions as base and a reliable proxy of power relationships; then we test if the direction of aggression within these relationships is driven also by energetic needs or the social environment.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aimed to elucidate the molecular mechanisms underlying HIV-1 persistence and host immune dysfunction in CD4+ T cells during early infection (<6 months). Using single-cell multi-omics technologies-including scRNA-seq, scATAC-seq, and single-cell multiome analyses-they characterized the transcriptional and epigenomic landscapes of HIV-1-infected CD4+ T cells. They identified key transcription factors (TFs), signaling pathways, and T cell subtypes involved in HIV-1 persistence, particularly highlighting KLF2 and Th17 cells as critical regulators of immune suppression. The study provides new insights into immune dysregulation during early HIV-1 infection and reveals potential epigenetic regulatory mechanisms in HIV-1-infected T cells.

Strengths:

The study excels through its innovative integration of single-cell multi-omics technologies, enabling detailed analysis of gene regulatory networks in HIV-1-infected cells. Focusing on early infection stages, it fills a crucial knowledge gap in understanding initial immune responses and viral reservoir establishment. The identification of KLF2 as a key transcription factor and Th17 cells as major viral reservoirs, supported by comprehensive bioinformatics analyses, provides robust evidence for the study's conclusions. These findings have immediate clinical relevance by identifying potential therapeutic targets for HIV-1 reservoir eradication.

We sincerely appreciate the reviewer’s positive evaluation of our work.

Weaknesses:

Despite its strengths, the study has several limitations. By focusing exclusively on CD4+ T cells, the study overlooks other relevant immune cells such as CD14+ monocytes, NK cells, and B cells. Additionally, while the authors generated their own single-cell datasets, they need to validate their findings using other publicly available single-cell data from HIV-1-infected PBMCs.

Thank you to Reviewer #1 for your feedback on our work. In response to this feedback, we have examined cell-cell interactions between HIV-1-infected CD4+ T cells and other innate immune cells, including monocytes and NK cells. We identified altered interaction signaling patterns (e.g., MIF, ICAM2, CCL5, CLEC2B) that contribute to immune dysfunction and viral persistence (page 9, Supplementary Fig. 5) In addition, we validated the expression of KLF2 and its target genes using a publicly available scRNA-seq dataset from HIV-1-infected PBMCs [1], which includes both healthy donors and individuals with chronic HIV-1 infection. The upregulation of key KLF2 targets in HIV-1-infected CD4+ T cells from this dataset supports the reproducibility of our findings. We have incorporated into the revised Results, Discussion, and Supplementary Materials (page 8, page 12 and Supplementary Fig. 4A).

Reviewer #2 (Public review):

Summary:

The authors observed gene ontologies associated with upregulated KLF2 target genes in HIV-1 RNA+ CD4 T Cells using scRNA-seq and scATAC-seq datasets from the PBMCs of early HIV-1-infected patients, showing immune responses contributing to HIV pathogenesis and novel targets for viral elimination.

Strengths:

The authors carried out detailed transcriptomics profiling with scRNA-seq and scATAC-seq datasets to conclude upregulated KLF2 target genes in HIV-1 RNA+ CD4 T Cells.

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

Weaknesses:

This key observation of up-regulation KLF2 associated genes family might be important in the HIV field for early diagnosis and viral clearance. However, with the limited sample size and in-vivo study model, it will be hard to conclude. I highly recommend increasing the sample size of early HIV-1-infected patients.

Thank you to Reviewer #2 for this important comment. We acknowledge the limitations of our modest sample size, which reflects the challenges of recruiting well-characterized individuals in early HIV-1 infection (<6 months) and obtaining high-quality PBMCs for single-cell multi-omic profiling. To strengthen our findings, we validated the upregulation of KLF2 target genes using a publicly available scRNA-seq dataset from HIV-1-infected PBMCs [1], which showed similar expression patterns in HIV-1 RNA+ CD4+ T cells (page 8 and Supplementary Fig. 4A).

Reviewer #3 (Public review):

Summary:

This manuscript studies intracellular changes and immune processes during early HIV-1 infection with an additional focus on the small CD4+ T cell subsets. The authors used single-cell omics to achieve high resolution of transcriptomic and epigenomic data on the infected cells which were verified by viral RNA expression. The results add to understanding of transcriptional regulation which may allow progression or HIV latency later in infected cells. The biosamples were derived from early HIV infection cases, providing particularly valuable data for the HIV research field.

Strengths:

The authors examined the heterogeneity of infected cells within CD4 T cell populations, identified a significant and unexpected difference between naive and effector CD4 T cells, and highlighted the differences in Th2 and Th17 cells. Multiple methods were used to show the role of the increased KLF2 factor in infected cells. This is a valuable finding of a new role for the major transcription factor in further disease progression and/or persistence.

The methods employed by the authors are robust. Single-cell RNA-Seq from PBMC samples was followed by a comprehensive annotation of immune cell subsets, 16 in total. This manuscript presents to the scientific community a valuable multi-omics dataset of good quality, which could be further analyzed in the context of larger studies.

We sincerely thank the reviewer for the insightful and concise summary of our work.

Weaknesses:

Methods and Supplementary materials

Some technical aspects could be described in more detail. For example, it is unclear how the authors filtered out cells that did not pass quality control, such as doublets and cells with low transcript/UMI content. Next, in cell annotation, what is the variability in cell types between donors? This information is important to include in the supplementary materials, especially with such a small sample size. Without this, it is difficult to determine, whether the differences between subsets on transcriptomic level, viral RNA expression level, and chromatin assessment are observed due to cell type variations or individual patient-specific variations. For the DEG analysis, did the authors exclude the most variable genes?

Thank you to Reviewer #3 for these detailed comments and observations. In the revised Methods section (page 16), we have added information on our quality control filtering process. Specifically, we excluded cells with fewer than 200 detected genes, high mitochondrial content (>30%), or low UMI counts. Doublets were identified and removed using DoubletFinder.

To address inter-donor variability, we included a new supplementary figure (Supplementary Fig. 1B) showing the distribution of major immune cell types across individual donors. While we observed some variation in cell-type composition between individuals, this likely reflects natural biological heterogeneity in early HIV-1 infection. Additionally, we applied fastMNN batch correction to mitigate donor-specific technical variation. After correction, the overall patterns of gene expression within each major CD4+ T cell subset were consistent across individuals (Supplementary Fig. 1C).

Regarding the DEG analysis, we used ‘FindMarkers’ function in Seurat (v.3.2.1), which does not exclude highly variable genes. These details have been clarified in the updated Methods section (page 18).

The annotation of 16 cell types from PBMC samples is impressive and of good quality, however, not all cell types get attention for further analysis. It’s natural to focus primarily on the CD4 T cells according to the research objectives. The authors also study potential interactions between CD4 and CD8 T cells by cell communication inference. It would be interesting to ask additional questions for other underexplored immune cell subsets, such as: 1) Could viral RNA be detected in monocytes or macrophages during early infection? 2) What are the inferred interactions between NK cells and infected CD4 T cells, are interactions similar to CD4-CD8 results? 3) What are the inferred interactions between monocytes or macrophages and infected CD4 T cells?

In line with our study objectives, we initially focused on CD4+ T cells as primary HIV-1 targets. However, in response to the reviewer’s comment, we examined the inferred communications between HIV-1-infected CD4+ T cells and other immune cells.

(1) With regard to the presence of viral RNA in monocytes or macrophages, we observed negligible HIV-1 RNA signal in these cell types in our dataset, consistent with their low permissiveness in early-stage infection [2]. However, we acknowledge the limitations of detecting rare infected cells at the single-cell level.

(2) We identified increased MIF and ICAM2 signaling between NK cells and HIV-1-infected CD4+ T cells, which are associated with KLF2-mediated immune modulation. These patterns are consistent with the CD4–CD8 interaction results observed in our dataset. (Supplementary Fig. 5A)

(3) Through the cell-cell interaction analysis with differential expression analysis, we inferred reduced CCL5 and CD55 signaling between monocytes and HIV-1-infected CD4+ T cells (Supplementary Fig. 5B). These reductions may potentially impair immune responses and antiviral defense.

We appreciate the reviewer’s suggestions and believe that the analysis of underexplored immune subsets strengthens the relevance of our findings. These results have been incorporated into the revised Results (page 9).

Discussion

It would be interesting to see more discussion of the observation of how naïve T cells produce more viral RNA compared to effector T cells. It seems counterintuitive according to general levels of transcriptional and translational activity in subsets.

Another discussion block could be added regarding the results and conclusion comparison with Ashokkumar et al. paper published earlier in 2024 (10.1093/gpbjnl/qzae003). This earlier publication used both a cell line-based HIV infection model and primary infected CD4 T cells and identified certain transcription factors correlated with viral RNA expression.

Thank you to Reviewer #3 for the insightful suggestions. We observed that the proportion of HIV-1-infected naïve CD4 T cells is higher compared to effector T cells. Although effector CD4 T cells are generally more active, previous studies have suggested that naïve CD4 T cells are susceptible to HIV-1 infection during early infection that may associate with initial expansion and rapid progression [3, 4]. This may be due to less restriction by antiviral signaling or more accessible chromatin states in resting cells. We have added this context and cited relevant papers to address this observation (page 11)

In addition, we have incorporated a comparative discussion with the recent study [5], which identified FOXP1 and GATA3 as transcriptional regulators associated with HIV-1 RNA expression. While these TFs were not significantly differentially expressed in our dataset, we discuss potential reasons for this discrepancy—including differences in infection model (in vitro vs. ex vivo), infection stage (latency vs. acute), and T cell subset composition—and emphasize that both studies highlight the importance of transcriptional regulation in HIV-1 persistence (page 12 and Supplementary Fig. 4B).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The study has several notable limitations.

First, it was restricted to early-stage HIV-1 infection (<6 months) without longitudinal data, preventing the authors from capturing temporal changes in immune cell populations, gene expression profiles, and epigenetic landscapes throughout disease progression.

Thank you to Reviewer #1 for this important limitation. As noted, our study focused exclusively on early-stage HIV-1 infection (<6 months) to capture the initial immune dysregulation and epigenetic alterations. We agree that longitudinal analysis would provide valuable insights into disease progression. However, due to the limited availability of early-infection patient samples suitable for performing multi-omics profiling, we prioritized capturing a detailed snapshot at this early stage. To address this limitation, future studies incorporating longitudinal sampling—including chronic infection and long-term non-progressors—will be essential to fully elucidate the temporal dynamics of HIV-1 pathogenesis.

Second, while the bioinformatic analysis compared "Uninfected" and "HIV-1-infected" cells from patients, the authors could have strengthened their findings by incorporating publicly available single-cell data from healthy donors and chronically infected HIV-1 patients to validate their arguments across all figures.

To support the robustness of our findings, we incorporated a publicly available single-cell RNA-seq dataset [1], which includes both healthy donors and individuals with chronic HIV-1 infection. In this dataset, we validated the upregulation of KLF2 and its target genes in HIV-1-infected CD4+ T cells and observed generally consistent expression patterns with those in our early-infection cohort (page 8; page 12 and Supplementary Fig. S4). While not all gene-level trends were identically reflecting differences in infection stage and immune activation status, this external comparison reinforces the reproducibility of key observations and highlights the unique transcriptional features associated with early HIV-1 infection.

Third, although the study focused on CD4+ T cells as primary HIV-1 targets, it overlooked other important immune cells such as CD8+ T cells, monocytes, and NK cells, which may contribute to viral persistence and immune dysfunction through cell-cell interactions.

In the revised manuscript, we expanded our analysis to include predicted ligand–receptor interactions between HIV-1-infected and uninfected CD4+ T cells with innate and cytotoxic immune cells using CellChat v.2.1.1. Specifically, we evaluated interactions with NK cells and monocytes and identified altered signaling pathways such as MIF, ICAM2, CCL5, and CLEC2B, which are associated with immune modulation (Supplementary Fig. 5A). We have added these results to the revised Results (page 9).

Lastly, comparing these findings with other chronic viral infections (e.g., HBV, HCV) would have positioned this work more effectively within the broader field of viral immunology and enhanced its impact.

We agree that broader comparisons with other chronic viral infections could enhance the impact of our findings. In the current discussion, we noted similarities in interferon signaling disruption with viruses such as HCV and HSV. (page 11). Our observation that HIV-1-infected CD4+ T cells exhibit impaired interferon responses is consistent with immune evasion mechanisms reported in HCV and HSV infections. These results underscore both the shared and specific features of immune modulation and persistence during HIV-1 early infection.

Reviewer #3 (Recommendations for the authors):

Supplementary Table S1 should indicate which technique was used for sequencing. However, the current version of the table marks no protocol applied to the majority of the samples, which is confusing and needs to be corrected.

Thank you to Reviewer #3 for pointing out this important oversight. We have revised Supplementary Table S1 to clearly indicate the sequencing method used for each sample. Separate columns for scRNA-seq, scATAC-seq, and sc-Multiome now specify whether each technique was applied (“Yes” or “No”) to improve clarity and transparency.

(1) Wang, S., et al., An atlas of immune cell exhaustion in HIV-infected individuals revealed by single-cell transcriptomics. Emerg Microbes Infect, 2020. 9(1): p. 2333-2347.

(2) Arfi, V., et al., Characterization of the early steps of infection of primary blood monocytes by human immunodeficiency virus type 1. J Virol, 2008. 82(13): p. 6557-65.

(3) Douek, D.C., et al., HIV preferentially infects HIV-specific CD4+ T cells. Nature, 2002. 417(6884): p. 95-8.

(4) Jiao, Y., et al., Higher HIV DNA in CD4+ naive T-cells during acute HIV-1 infection in rapid progressors. Viral Immunol, 2014. 27(6): p. 316-8.

(5) Ashokkumar, M., et al., Integrated Single-cell Multiomic Analysis of HIV Latency Reversal Reveals Novel Regulators of Viral Reactivation. Genomics Proteomics Bioinformatics, 2024. 22(1).

Author response:

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

Joint Public Review:

Summary:

The authors sought to elucidate the mechanism by which infections increase sleep in Drosophila. Their work is important because it further supports the idea that the blood-brain barrier is involved in brain-body communication, and because it advances the field of sleep research. Using knock-down and knock-out of cytokines and cytokine receptors specifically in the endocrine cells of the gut (cytokines) as well as in the glia forming the blood-brain barrier (BBB) (cytokines receptors), the authors show that cytokines, upd2 and upd3, secreted by entero-endocrine cells in response to infections increase sleep through the Dome receptor in the BBB. They also show that gut-derived Allatostatin (Alst) A promotes wakefulness by inhibiting Alst A signaling that is mediated by Alst receptors expressed in BBB glia. Their results suggest there may be additional mechanisms that promote elevated sleep during gut inflammation.

The authors suggest that upd3 is more critical than upd2, which is not sufficiently addressed or explained. In addition, the study uses the gut's response to reactive oxygen molecules as a proxy for infection, which is not sufficiently justified. Finally, further verification of some fundamental tools used in this paper would further solidify these findings making them more convincing.

Strengths:

(1) The work addresses an important topic and proposes an intriguing mechanism that involves several interconnected tissues. The authors place their research in the appropriate context and reference related work, such as literature about sickness-induced sleep, ROS, the effect of nutritional deprivation on sleep, sleep deprivation and sleep rebound, upregulated receptor expression as a compensatory mechanism in response to low levels of a ligand, and information about Alst A.

(2) The work is, in general, supported by well-performed experiments that use a variety of different tools, including multiple RNAi lines, CRISPR, and mutants, to dissect both signal-sending and receiving sides of the signaling pathway.

(3) The authors provide compelling evidence that shows that endocrine cells from the gut are the source of the upd cytokines that increase daytime sleep, that the glial cells of the BBB are the targets of these upds, and that upd action causes the downregulation of Alst receptors in the BBB via the Jak/Stat pathways.

We are pleased that the reviewers recognized the strength and significance of our findings describing a gut-to-brain cytokine signaling mechanism involving the blood-brain barrier (BBB) and its role in regulating sleep, and we thank them for their comments.

Weaknesses:

(1) There is a limited characterization of cell types in the midgut which are classically associated with upd cytokine production.

We thank the reviewer for raising this point. Although several midgut cell types (including the absorptive enterocytes) may indeed produce Unpaired (Upd) cytokines, our study specifically focused on enteroendocrine cells (EECs), which are well-characterized as secretory endocrine cells capable of exerting systemic effects. As detailed in our response to Results point #2 (please see below), we show that EEC-specific manipulation of Upd signaling is both necessary and sufficient to regulate sleep in response to intestinal oxidative stress. These findings support the role of EECs as a primary source of gut-derived cytokine signaling to the brain. To acknowledge the possible involvement of other source, we have also added a statement to the Discussion in the revised manuscript noting that other, non-endocrine gut cell types may contribute to systemic Unpaired signaling that modulates sleep.

(2) Some of the main tools used in this manuscript to manipulate the gut while not influencing the brain (e.g., Voilà and Voilà + R57C10-GAL80), are not directly shown to not affect gene expression in the brain. This is critical for a manuscript delving into intra-organ communication, as even limited expression in the brain may lead to wrong conclusions.

We agree with the reviewer that this is an important point. To address it, we performed additional validation experiments to assess whether the voilà-GAL4 driver in combination with R57C10-GAL80 (EEC>) influences upd2 or upd3 expression in the brain. Our results show that manipulation using EEC> alters upd2 and upd3 expression in the gut (Fig. 1a,b), with new data showing that this does not affect their expression levels in neuronal tissues (Fig. S1a), supporting the specificity of our approach. These new data are now included in the revised manuscript and described in the Results section. This additional validation strengthens our conclusion that the observed sleep phenotypes result from gut-specific cytokine signaling, rather than from effects on Unpaired cytokines produced in the brain.

(1) >(3) The model of gut inflammation used by the authors is based on the increase in reactive oxygen species (ROS) obtained by feeding flies food containing 1% H2O2. The use of this model is supported by the authors rather weakly in two papers (refs. 26 and 27 ): The paper by Jiang et al. (ref. 26) shows that the infection by Pseudomonas entomophila induces cytokine responses upd2 and 3, which are also induced by the Jnk pathway. In addition, no mention of ROS could be found in Buchon et al. (ref 27); this is a review that refers to results showing that ROS are produced by the NADPH oxidase DUOX as part of the immune response to pathogens in the gut. Thus, there is no strong support for the use of this model.

We thank the reviewer for raising this point. We agree that the references originally cited did not sufficiently justify the use of H₂O₂ feeding as a model of gut inflammation. To address this, we have revised the Results section to clarify that we use H₂O₂ feeding as a controlled method to elevate intestinal ROS levels, rather than as a general model of inflammation. This approach allows us to investigate the specific effects of ROS-induced cytokine signaling in the gut. We have also added additional citations to support the physiological relevance of this model. For instance, Tamamouna et al. (2021) demonstrated that H₂O₂ feeding induces intestinal stem-cell proliferation – a response also observed during bacterial infection – and Jiang et al. (2009) showed that enteric infections increase upd2 and upd3 expression, which we similarly observe following H₂O₂ feeding (Fig. 3a). These findings support the use of H₂O₂ as a tool to mimic specific ROS-linked responses in the gut. We believe this targeted and tractable model is a strength of our study, enabling us to dissect how intestinal ROS modulates systemic physiology through cytokine signaling

Additionally, we have included a statement in the Discussion acknowledging that ROS generated during infection may activate signaling mechanisms distinct from those triggered by chemically induced oxidative stress, and that exploring these differences in future studies may yield important insights into gut–brain communication. These revisions provide a stronger justification for our model while more accurately conveying both its relevance and its limitations.

(2) >(4) Likewise, there is no support for the use of ROS in the food instead a direct infection by pathogenic bacteria. Furthermore, it is known that ROS damages the gut epithelium, which in turn induces the expression of the cytokines studied. Thus the effects observed may not reflect the response to infection. In addition, Majcin Dorcikova et al. (2023). Circadian clock disruption promotes the degeneration of dopaminergic neurons in male Drosophila. Nat Commun. 2023 14(1):5908. doi: 10.1038/s41467-02341540-y report that the feeding of adult flies with H2O2 results in neurodegeneration if associated with circadian clock defects. Thus, it would be important to discuss or present controls that show that the feeding of H2O2 does not cause neuronal damage.

We thank the reviewer for this thoughtful follow-up point. We would like to clarify that we do not claim that the effects observed in our study directly reflect the full response to enteric infection. As outlined in our revised response to comment 3, we have updated the manuscript to more precisely describe the H₂O₂-feeding paradigm as a model that induces local intestinal ROS responses comparable to, but not equivalent to, those observed during pathogenic challenges. This revised framing highlights both the potential similarities and differences between chemically induced oxidative stress and infection-induced responses. Indeed, in the revised Discussion, we now explicitly acknowledge that ROS generated during infection may engage distinct signaling mechanisms compared to exogenous H₂O₂ and emphasize the value of future studies in delineating these pathways. We are currently pursuing this direction in an independent ongoing study investigating the effects of enteric infections. However, for the present work, we chose to focus on the effects of ROS-induced responses in isolation, as this provides a clean and well-controlled context to dissect the specific contribution of oxidative stress to cytokine signaling and sleep regulation.

To further address the reviewer’s concern, we have also included new data (a TUNEL stain for apoptotic DNA fragmentation) in the revised manuscript showing that H₂O₂ feeding does not damage neuronal tissues under our experimental conditions (Fig. S3f,g). This addresses the point raised regarding the potential neurotoxicity of H₂O₂, as described by Majcin Dorcikova et al. (2023), and supports the specificity of the sleep phenotypes observed in our study. We believe these revisions and clarifications strengthen the manuscript and make our interpretation more precise.

(3) >(5) The novelty of the work is difficult to evaluate because of the numerous publications on sleep in Drosophila. Thus, it would be very helpful to read from the authors how this work is different and novel from other closely related works such as: Li et al. (2023) Gut AstA mediates sleep deprivation-induced energy wasting in Drosophila. Cell Discov. 23;9(1):49. doi: 10.1038/s41421-023-00541-3.

Our work highlights a distinct role for gut-derived AstA in sleep regulation compared to findings by Lin et al. (Cell Discovery, 2023)[1], who showed that gut AstA mediates energy wasting during sleep deprivation. Their study focused on the metabolic consequences of sleep loss, proposing that sleep deprivation increases ROS in the gut, which then promotes the release of the glucagon-like hormone adipokinetic hormone (AKH) through gut AstA signaling, thereby triggering energy expenditure.

In contrast, our study addresses the inverse question – how ROS in the gut influences sleep. In our model, intestinal ROS promotes sleep, raising the intriguing possibility – cleverly pointed out by the reviewers – that ROS generated during sleep deprivation might promote sleep by inducing Unpaired cytokine signaling in the gut. According to our findings, this suppresses wake-promoting AstA signaling in the BBB, providing a mechanism to promote sleep as a restorative response to gut-derived oxidative stress and potentially limiting further ROS accumulation. Importantly, our findings support a wakepromoting role for EEC-derived AstA, demonstrated by several lines of evidence. First, EEC-specific knockdown of AstA increases sleep. Second, activation of AstA⁺ EECs using the heat-sensitive cation channel Transient Receptor Potential A1 (TrpA1) reduces sleep, and this effect is abolished by simultaneous knockdown of AstA, indicating that the sleep-suppressing effect is mediated by AstA and not by other peptides or secreted factors released by these cells. Third, downregulation of AstA receptor expression in BBB glial cells increases sleep, further supporting the existence of a functional gut AstA– glia arousal pathway. We have now included new data in the revised manuscript showing that AstA release from EECs is downregulated during intestinal oxidative stress (Fig. 7k,l,m). This suggests that this wake-promoting signal is suppressed both at its source (the gut endocrine cells), by unknown means, and at its target, the BBB, via Unpaired cytokine signaling that downregulates AstA receptor expression. This coordinated downregulation may serve to efficiently silence this arousal-promoting pathway and facilitate sleep during intestinal stress. These new data, along with an expanded discussion, provide further mechanistic insight into gut-derived AstA signaling and strengthen our proposed model.

This contrasts with the interpretation by Lin et al., who observed increased AstA peptide levels in EECs after antioxidant treatment and interpreted this as peptide retention. However, peptide accumulation may result from either increased production or decreased release, and peptide levels alone are insufficient to distinguish between these possibilities. To resolve this, we examined AstA transcript levels, which can serve as a proxy for production. Following oxidative stress (24 h of 1% H₂O₂ feeding and the following day), when animals show increased sleep (Fig. 7e), we observed a decrease in AstA transcript levels followed by an increase in peptide levels (Fig. 7k,l,m), suggesting that oxidative stress leads to reduced gut AstA production and release. Furthermore, we recently found that a class of EECs that produce the hormone Tachykinin (Tk) and are distinct from the AstA⁺ EECs express the ROSsensitive cation channel TrpA1 (Ahrentløv et al., 2025, Nature Metabolism2). In these Tk⁺ EECs, TrpA1 mediates ROS-induced Tk hormone release. In contrast, single-cell RNA-seq data[3] do not support TrpA1 expression in AstA⁺ EECs, consistent with our findings that ROS does not promote AstA release – an effect that would be expected if TrpA1 were functionally expressed in AstA⁺ EECs. This contradicts the findings of Lin et al., who reported TrpA1 expression in AstA⁺ EECs. We have now included relevant single-cell data in the revised manuscript (Fig. S6f) showing that TrpA1 is specifically expressed in Tk⁺ EECs, but not in AstA⁺ EECs, and we have expanded the discussion to address discrepancies in TrpA1 expression and AstA regulation.

Taken together, our results reveal a dual-site regulatory mechanism in which Unpaired cytokines released from the gut act at the BBB to downregulate AstA receptor expression, while AstA release from EECs is simultaneously suppressed. We thank the reviewers for raising this important point. We have also included a discussion the other point raised by the reviewers – the possibility that ROS generated during sleep deprivation may engage the same signaling pathways described here, providing a mechanistic link between sleep deprivation, intestinal stress, and sleep regulation.

Recommendations for the authors:

A- Material and Methods:

(1) Feeding Assay: The cited publication (doi.org:10.1371/journal.pone.0006063) states: "For the amount of label in the fly to reflect feeding, measurements must therefore be confined to the time period before label egestion commences, about 40 minutes in Drosophila, a time period during which disturbance of the flies affects their feeding behavior. There is thus a requirement for a method of measuring feeding in undisturbed conditions." Was blue fecal matter already present on the tube when flies were homogenized at 1 hour? If so, the assay may reflect gut capacity rather than food passage (as a proxy for food intake). In addition, was the variability of food intake among flies in the same tube tested (to make sure that 1-2 flies are a good proxy for the whole population)?

We agree that this is an important point for feeding experiments. We are aware of the methodological considerations highlighted in the cited study and have extensive experience using a range of feeding assays in Drosophila, including both short- and long-term consumption assays (e.g., dye-based and CAFE assays), as well as automated platforms such as FLIC and FlyPAD (Nature Communications, 2022; Nature Metabolism, 2022; and Nature Metabolism, 2025)[2,4,5].

For the dye-based assay, we carefully selected a 1-hour feeding window based on prior optimization. Since animals were not starved prior to the assay, shorter time points (e.g., 30 minutes) typically result in insufficient ingestion for reliable quantification. A 1-hour period provides a robust readout while remaining within the timeframe before significant label excretion occurs under our experimental conditions. To support the robustness of our findings, we complemented the dye-based assay with data from FLIC, which enables automated, high-resolution monitoring of feeding behavior in undisturbed animals over extended periods. The FLIC results were consistent with the dye-based data, strengthening our confidence in the conclusions. To minimize variability and ensure consistency across experiments, all feeding assays were performed at the same circadian time – Zeitgeber Time 0 (ZT0), corresponding to 10:00 AM when lights are turned on in our incubators. This time point coincides with the animals' natural morning feeding peak, allowing for reproducible comparisons across conditions. Regarding variability among flies within tubes, each biological replicate in the dye assay consisted of 1–2 flies, and results were averaged across multiple replicates. We observed good consistency across samples, suggesting that these small groups reliably reflect group-level feeding behavior under our conditions.

(2) Biological replicates: whereas the number of samples is clearly reported in each figure, the number of biological replicates is not indicated. Please include this information either in Material and methods or in the relevant figure legends. Please also include a description of what was considered a biological replicate.

We have now clarified in the Materials and Methods section under Statistics that all replicates represent independent biological samples, as suggested by the reviewers.

(3) Control Lines: please indicate which control lines were used instead of citing another publication. If preferred, this information could be supplied as a supplementary table.

We now provide a clear description of the control lines used in the Materials and Methods section. Specifically, all GAL4 and GAL80 lines used in this study were backcrossed for several generations into a shared w¹¹¹⁸ background and then crossed to the same w¹¹¹⁸ strain used as the genetic background for the UAS-RNAi, <i.CRISPR, or overexpression lines. This approach ensures, to a strong approximation, that the only difference between control and experimental animals is the presence or absence of the UAS transgene.

(4) Statistical analyses: for some results (e.g., those shown in Figure 3d), it could be useful to test the interaction between genotype and treatment.

We thank the reviewer for this helpful suggestion. In response, we have now performed two-way ANOVA analyses to assess genotype × treatment (diet) interaction effects for the relevant data, including those shown in Figure 3d as well as additional panels where animals were exposed to oxidative stress and sleep phenotypes were measured. We have added the corresponding interaction p-values in the updated figure legends for Figures 3d, 3k, 5a–c, 5f, 5h, 5i, 6c, 6e, and 7e. All of these tests revealed significant interaction effects, supporting the conclusion that the observed differences in sleep phenotypes are specifically dependent on the interaction between genetic manipulation (e.g., cytokine or receptor knockdown) and oxidative stress. These additions reinforce the interpretation that Unpaired cytokine signaling, glial JAK-STAT pathway activity, and AstA receptor regulation functionally interact with intestinal ROS exposure to modulate sleep. We thank the reviewer for suggesting this improvement.

(5) Reporting of p values. Some are reported as specific values whereas others are reported as less than a specific value. Please make this reporting consistent across different figures.

All p-values reported in the manuscript are exact, except in cases where values fall below p < 0.0001. In those instances, we use the inequality because the Prism software package (GraphPad, version 10), which was used for all statistical analyses, does not report more precise values. We believe this reporting approach reflects standard practice in the field.

(6) Please include the color code used in each figure, either in the figure itself or in the legend.

We have now clarified the color coding in all relevant figures. In particular, we acknowledge that the meaning of the half-colored circles used to indicate H₂O₂ treatment was not previously explained. These have now been clearly labeled in each figure to indicate treatment conditions.

(7) The scheme describing the experimental conditions and the associated chart is confusing. Please improve.

We have improved the schematic by replacing “ROS” with “H₂O₂” to more clearly indicate the experimental condition used. Additionally, we have added the corresponding circle annotations so that they now also appear consistently above the relevant charts. This revised layout enhances clarity and helps readers more easily interpret the experimental conditions. We believe these changes address the reviewer’s concern and make the figure significantly more intuitive.

8) Please indicate which line was used for upd-Gal4 and the evidence that it faithfully reflects upd3 expression.

We have now clarified in the Materials and Methods section that the upd3-GAL4 line used in our study is Bloomington stock #98420, which drives GAL4 expression under the control of approximately 2 kb of sequence upstream of the upd3 start codon. This line has previously been used as a transcriptional reporter for upd3 activity. The only use of this line was to illustrate reporter expression in the EECs. To support this aspect of Upd3 expression, we now include new data in the revised manuscript using fluorescent in situ hybridization (FISH) against upd3, which confirms the presence of upd3 transcripts in prospero-positive EECs of the adult midgut (Fig. S1b). Additionally, we show that upd3 transcript levels are significantly reduced in dissected midguts following EEC-specific knockdown using multiple independent RNAi lines driven by voilà-GAL4, both alone and in combination with R57C10-GAL80, consistent with endogenous expression in these cells (Fig. 1a,b).

To further address the reviewer’s concern and provide additional support for the endogenous expression of upd3 in EECs, we performed targeted knockdown experiments focusing on molecularly defined EEC subpopulations. The adult Drosophila midgut contains two major EEC subtypes characterized by their expression of Allatostatin C (AstC) or Tachykinin (Tk), which together encompass the vast majority of EECs. To selectively manipulate these populations, we used AstC-GAL4 and Tk-GAL4 drivers – both knock-in lines in which GAL4 is inserted at the respective endogenous hormone loci. This design enables precise GAL4 expression in AstC- or Tk-expressing EECs based on their native transcriptional profile. To eliminate confounding neuronal expression, we combined these drivers with R57C10GAL80, restricting GAL4 activity to the gut and generating AstC^Gut> and Tk^Gut> drivers. Using these tools, we knocked down upd2 and upd3 selectively in the AstC- or Tk-positive EECs. Knockdown of either cytokine in AstC-positive EECs significantly increased sleep under homeostatic conditions, recapitulating the phenotype observed with knockdown in all EECs (Fig. 1m-o). In contrast, knockdown of upd2 or upd3 in Tk-positive EECs had no effect on sleep (Fig. 1p-r). Furthermore, we show in the revised manuscript that selective knockdown of upd2 or upd3 in AstC-positive EECs abolishes the H₂O₂-induced increase in sleep (Fig. 3f–h). These findings demonstrate that Unpaired cytokine signaling from AstC-positive EECs is essential for mediating the sleep response to intestinal oxidative stress, highlighting this specific EEC subtype as a key source of cytokine-driven regulation in this context. These new results indicate that AstC-positive EECs are a primary source of the Unpaired cytokines that regulate sleep, while Tk-positive EECs do not appear to contribute to this function. Importantly, upd3 transcript levels were significantly reduced in dissected midguts following AstC^Gut driven knockdown (Fig. S1r), further confirming that upd3 is endogenously expressed in AstC-positive EECs. Thus we have bolstered our confidence that upd3 is indeed expressed in EECs, as illustrated by the reporter line, through several means.

(9) Please indicate which GFP line was used with upd-Gal4 (CD8, NLS, un-tagged, etc). The Material and Methods section states that it was "UAS-mCD8::GFP (#5137);", however, the stain does not seem to match a cell membrane pattern but rather a nuclear or cytoplasmic pattern. This information would help the interpretation of Figure 1C.

We confirm that the GFP reporter line used with upd3-GAL4 was obtained from Bloomington stock #98420. As noted by the Bloomington Drosophila Stock Center, “the identity of the UAS-GFP transgene is a guess,” and the subcellular localization of the GFP fusion is therefore uncertain. We agree with the reviewer that the signal observed in Figure 1c does not display clear membrane localization and instead appears diffuse, consistent with cytoplasmic or partially nuclear localization. In any case, what we find most salient is the reporter’s labeling of Prospero-positive EECs in the adult midgut, consistent with upd3 expression in these cells. This conclusion is further supported by multiple lines of evidence presented in the revised manuscript, as mentioned above in response to question #8: (1) fluorescent in situ hybridization (FISH) for upd3 confirms expression in EECs (Fig. S1b), (2) EEC-specific RNAi knockdown of upd3 reduces transcript levels in dissected midguts, and (3) publicly available single-cell RNA sequencing datasets[3] also indicate that upd3 is expressed at low levels in a subset of adult midgut EECs under normal conditions. We have also clarified in the revised Materials and Methods section that GFP localization is undefined in the upd3-GAL4 line, to guide interpretation of the reporter signal.

B- Results

(1) Figure 1: According to previous work (10.1016/j.celrep.2015.06.009, http://flygutseq.buchonlab.com/data?gene=upd3%0D%0A), in basal conditions upd3 is expressed as following: ISC (35 RPKM), EB (98 RPKM), EC (57 RPKM), and EEC (8 RPKM). Accordingly, even complete KO in EECs should eliminate only a small fraction of upd3 from whole guts, even less considering the greater abundance of other cell types such as ECs compared to EECs. It would be useful to understand where this discrepancy comes from, in case it is affecting the conclusion of the manuscript. While this point per se does not affect the main conclusions of the manuscript, it makes the interpretation of the results more difficult.

We acknowledge the previously reported low expression of upd3 in EECs. However, the FlyGut-seq site appears to be no longer available, so we could not directly compare other related genes. Nonetheless, our data – based on in situ hybridization, reporter expression, and multiple RNAi knockdowns – consistently support upd3 expression in EECs. These complementary approaches strengthen the conclusion that EECs are an important source of systemic upd3 under the conditions tested.

(2) Figure 1: The upd2-3 mutants show sleep defects very similar to those of EEC>RNAi and >Cas9. It would thus be helpful to try to KO upd3 with other midgut drivers (An EC driver like Myo1A or 5966GS and a progenitor driver like Esg or 5961GS) to validate these results. Such experiments might identify precisely which cells are involved in the gut-brain signaling reported here.

We appreciate the reviewer’s suggestion and agree that exploring other potential sources of Upd3 in the gut is an interesting direction. In this study, we have focused on EECs, which are the primary hormone-secreting cells in the intestine and thus the most likely candidates for mediating systemic effects such as gut-to-brain signaling. While it is possible that other gut cell types – such as enterocytes (e.g., Myo1A⁺) or intestinal progenitors (e.g., Esg⁺) – also contribute to Upd3 production, these cells are not typically endocrine in nature. Demonstrating their involvement in gutto-brain communication would therefore require additional, extensive validation beyond the scope of the current study. Importantly, our data show that manipulating Upd3 specifically in EECs is both necessary and sufficient to modulate sleep in response to intestinal ROS, strongly supporting the conclusion that EEC-derived cytokine signaling underlies the observed phenotype. In contrast, manipulating cytokines in other gut cells could produce indirect effects – such as altered proliferation, epithelial integrity, or immune responses – that complicate the interpretation of behavioral outcomes like sleep. For these reasons, we chose to focus on EECs as the source of endocrine signals mediating gut-to-brain communication. However, to address this point raised by the reviewer, we have now included a statement in the Discussion acknowledging that other non-endocrine gut cell types may also contribute to the systemic Unpaired signaling that modulates sleep in response to intestinal oxidative stress.

(3) Figure 3: "This effect mirrored the upregulation observed with EEC-specific overexpression of upd3, indicating that it reflects physiologically relevant production of upd3 by the gut in response to oxidative stress." Please add (Figure 3a) at the end of this sentence.

We have now added “(Figure 3a)” at the end of the sentence to clearly reference the relevant data.

(4) For Figure 3b, do you have data showing that the increased amount of sleep was due to the addition of H2O2 per se, rather than the procedure of adding it?

We have added new data to address this point. To ensure that the observed sleep increase was specifically due to the presence of H₂O₂ and not an effect of the food replacement procedure, we performed a control experiment in which animals were fed standard food prepared using the same protocol and replaced daily, but without H₂O₂. These animals did not exhibit increased sleep, confirming that the sleep effect is attributable to intestinal ROS rather than the supplementation procedure itself (Fig. S3a). Thanks for the suggestion.

(5) In the text it is stated that "Since 1% H2O2 feeding induced robust responses both in upd3 expression and in sleep behavior, we asked whether gut-derived Unpaired signaling might be essential for the observed ROS-induced sleep modulation. Indeed, EEC-specific RNAi targeting upd2 or upd3 abolished the sleep response to 1% H2O2 feeding." While it is indeed true that there is no additional increase in sleep time due to EEC>upd3 RNAi, it is also true that EEC>upd3 RNAi flies, without any treatment, have already increased their sleep in the first place. It is then possible that rather than unpaired signaling being essential, an upper threshold for maximum sleep allowed by manipulation of these processes was reached. It would be useful to discuss this point.

Several findings argue against a ceiling effect and instead support a requirement for Unpaired signaling in mediating ROS-induced sleep. Animals with EEC-specific upd2 or upd3 knockdown or null mutation not only fail to increase sleep following H₂O₂ treatment but actually exhibit reduced sleep during oxidative stress (Fig. 3e, k, l; Fig. 5e, f), suggesting that Unpaired signaling is required to sustain sleep under these conditions. Similarly, animals with glial dome knockdown also show reduced sleep under oxidative stress, closely mirroring the phenotype of EEC-specific upd3 RNAi animals (Fig. 5a–c, g–i). These results support the conclusion that gut-to-glia Unpaired cytokine signaling is necessary for maintaining elevated sleep during oxidative stress. In the absence of this signaling, animals exhibit increased wakefulness. We identify AstA as one such wake-promoting signal that is suppressed during intestinal stress. We present new data showing that this pathway is downregulated not only via Unpaired-JAK/STAT signaling in glial cells but also through reduced AstA release from the gut in the revised manuscript. This model, in which Unpaired cytokines promote sleep during intestinal stress by suppressing arousal pathways, is discussed throughout the manuscript to address the reviewer’s point.

(6) In Figure 3k, the dots highlighting the experiment show an empty profile, a full one, and a half one. Please define what the half dots represent.

We have now clarified the color coding in all relevant figures. Specifically, we acknowledge that the meaning of the half-colored circles indicating H₂O₂ treatment was not previously defined – it indicates washout or recovery time. In the revised version, these symbols are now clearly labeled in each figure to indicate the treatment condition, ensuring consistent and intuitive interpretation across all panels.

(7) The authors used appropriate GAL4 and RNAi lines to the knockdown dome, a upd2/3 JAK-STATlinked receptor, specifically in neurons and glia, respectively, in order to identify the CNS targets of upd2/3 cytokines produced by enteroendocrine cells (EECs). Pan-neuronal dome knockdown did not alter daytime sleep in adult females, yet pan-glial dome knockdown phenocopied effects of upd2/3 knockdown in EECs. They also observed that EEC-specific knockdown of upd2 and upd3 led to a decrease in JAK-STAT reporter activity in repo-positive glial cells. This supports the authors' conclusion that glial cells, not neurons, are the targets by which unpaired cytokines regulate sleep via JAK-STAT signaling. However, they do not show nighttime sleep data of pan-neuronal and pan-glial dome knockdowns. It would strengthen their conclusion if the nighttime sleep of pan-glial dome knockdown phenocopied the upd2/3 knockdowns as well, provided the pan-neuronal dome knockdown did not alter nighttime sleep.

We have now added nighttime sleep data for both pan-glial and pan-neuronal domeless knockdowns in the revised manuscript (Fig. 2a). Glial knockdown increased nighttime sleep, similar to EEC-specific upd2/3 knockdown, while neuronal knockdown had no effect. These results further support the glial cells’ being the relevant target of gut-derived Unpaired signaling.

(8) The authors only used one method to induce oxidative stress (hydrogen peroxide feeding). It would strengthen their argument to test multiple methods of inducing oxidative stress, such as lipopolysaccharide (LPS) feeding. In addition, it would be useful to use a direct bacterial infection to confirm that in flies, the infection promotes sleep. Additionally, flies deficient in Dome in the BBB and infected should not be affected in their sleep by the infection. These experiments would provide direct support for the mechanism proposed. Finally, the authors should add a primary reference for using ROS as a model of bacterial infection and justify their choice better.

We agree that directly comparing different models of intestinal stress, such as bacterial infection or LPS feeding, would provide valuable insight into how gut-derived signals influence sleep in response to infection. As noted in our detailed responses above, we now include an expanded rationale for our use of H₂O₂ feeding as a controlled and well-established method for inducing intestinal ROS – one of the key physiological responses to enteric infection and inflammation. In the revised Discussion, we explicitly acknowledge that pathogenic infections – which trigger both intestinal ROS and additional immune pathways – may engage distinct or complementary mechanisms compared to chemically induced oxidative stress. We emphasize the importance of future studies aimed at dissecting these differences. In fact, we are actively pursuing this direction in ongoing work examining sleep responses to enteric infection. For the purposes of the present study, however, we chose to focus on a tractable and specific model of ROS-induced stress to define the contribution of Unpaired cytokine signaling to gut-brain communication and sleep regulation. This approach allowed us to isolate the effect of oxidative stress from other confounding immune stimuli and identify a glia-mediated signaling mechanism linking gut epithelial stress to changes in sleep behavior.

(9) To confirm that animals lacking EEC Unpaired signaling are not more susceptible to ROS-induced damage, the authors assessed the survival of upd2 and upd3 knockdowns on 1% H2O2 and concluded they display no additional sensitivity to oxidative stress compared to controls. It may be useful to include other tests of sensitivity to oxidative stress, in addition to survival.

We appreciate the reviewer’s suggestion. In our view, survival is a highly informative and stringent readout, as it reflects the overall physiological capacity of the animal to withstand oxidative stress. Importantly, our data show that animals lacking EEC-derived Unpaired signaling do not exhibit reduced survival following H₂O₂ exposure, indicating that their oxidative stress resistance is not compromised. Furthermore, we previously confirmed that feeding behavior is unaffected in these animals, suggesting that their ability to ingest food (and thus the stressor) is not impaired. As a molecular complement to these assays in response to this point and others, we have also performed an assessment of neuronal apoptosis (a TUNEL assay, Fig. S3f,g). This assay did not identify an increase in cell death in the brains of animals fed peroxide-containing medium. Thus, gross neurological health, behavior, and overall survival appear to be resilient to the environmental treatment regime we apply here, suggesting that the outcomes we observe arise from signaling per se.

(10) The authors confirmed that animals lacking EEC-derived upd3 displayed sleep suppression similar to controls in response to starvation. These results led the authors to conclude that there is a specific requirement for EEC-derived Unpaired signaling in responding to intestinal oxidative stress. However, they previously showed that EEC-specific knockdown of upd3 and upd2 led to increased daytime sleep under normal feeding conditions. Their interpretations of their data are inconsistent.

We appreciate the reviewer’s comment. While animals lacking EEC-derived Unpaired signaling show increased baseline sleep under normal feeding conditions, they still exhibit a robust reduction in sleep when subjected to starvation – comparable to that of control animals (Fig. S3h–j). This demonstrates that they retain the capacity to appropriately modulate sleep in response to metabolic stress. Thus, the sleep-promoting phenotype under normal conditions does not reflect a generalized inability to adjust sleep behavior. Rather, it highlights a specific role for Unpaired signaling in mediating sleep responses to intestinal oxidative stress, not in broadly regulating all sleep-modulating stimuli.

(11) The authors report a significant increase in JAK-STAT activity in surface glial cells at ZT0 in animals fed 1% H2O2-containing food for 20 hours. This response was abolished in animals with EECspecific knockdown of upd2 or upd3. The authors confirmed there were no unintended neuronal effects on upd2 or upd3 expression in the heads. They also observed an upregulation of dome transcript levels in the heads of animals with EEC-specific knockdown of upd3 fed 1% H2O2-containing food for 15 hours, which they interpret to be a compensatory mechanism in response to low levels of the ligand. This assay is inconsistent with previous experiments in which animals were fed hydrogen peroxide for 20 hours.

We thank the reviewer for identifying this discrepancy. The inconsistency arose from a labeling error in the manuscript. Both the JAK-STAT reporter assays in glial cells and the dome expression measurements were performed following 15 hours of H₂O₂ feeding, not 20 hours as previously stated. We have now corrected this in the revised manuscript.

(12) The authors show that animals with glia-specific dome knockdown did not have decreased survival on H2O2-containing food, and displayed normal rebound sleep in the morning following sleep deprivation. These results potentially undermine the significance of the paper. If the normal sleep response to oxidative stress is an important protective mechanism, why would oxidative stress not decrease survival in dome knockdown flies (that don't have the normal sleep response to oxidative stress)? This suggests that the proposed mechanism is not important for survival. The authors conclude that Dome-mediated JAK-STAT signaling in the glial cells specifically regulates ROS-induced sleep responses, which their results support.

We agree that our survival data show that glial dome knockdown does not reduce survival under continuous oxidative stress. However, we believe this does not undermine the importance of the sleep response as an adaptive mechanism. In our survival assay, animals were continuously exposed to 1% H₂O₂ without the opportunity to recover. In contrast, under natural conditions, oxidative stress is likely to be intermittent, and the ability to mount a sleep response may be particularly important for promoting recovery and maintaining homeostasis during or after transient stress episodes. Thus, while the JAK-STAT-mediated sleep response may not directly enhance survival under constant oxidative challenge, it likely plays a critical role in adaptive recovery under natural conditions.

(13) Altogether, the authors conclude that enteric oxidative stress induces the release of Unpaired cytokines which activate the JAK-STAT pathway in subperineurial glia of the BBB, which leads to the glial downregulation of receptors for AstA, which is a wake-promoting factor also released by EECs. This mechanism is supported by their results, however, this research raises some intriguing questions, such as the role of upd2 versus upd3, the role of AstA-R1 versus AstA-R2, the importance of this mechanism in terms of survival, the sex-specific nature of this mechanism, and the role that nutritional availability plays in the dual functionality of Unpaired cytokine signaling in regards to sleep.

We thank the reviewer for highlighting these important questions. Our data suggest that Upd2 and Upd3, while often considered partially redundant, both contribute to sleep regulation, with stronger effects observed for Upd3. This is consistent with prior studies indicating overlapping but non-identical roles for these cytokines. Similarly, although AstA-R1 and AstA-R2 can both be activated by AstA, knockdown of AstA-R2 consistently produces more robust sleep phenotypes, suggesting a predominant role in mediating this effect. The possibility of sex-specific regulation is indeed compelling. While our study focused on females, many gut hormones show sex-dependent activity, and we recognize this as an important avenue for future research. Finally, we have included new data in the revised manuscript showing that gut-derived AstA is downregulated under oxidative stress, further supporting our model in which Unpaired signaling suppresses arousal pathways during intestinal stress

(14)Data Availability: It is indicated that: "Reasonable data requests will be fulfilled by the lead author". However, eLife's guidelines for data sharing require that all data associated with an article to be made freely and widely available.

We thank the reviewer for pointing this out. We have revised the Data Availability section of the manuscript to clarify that all data will be made freely available from the lead contact without restriction, in accordance with eLife’s open data policy.

References

(1) Li, Y., Zhou, X., Cheng, C., Ding, G., Zhao, P., Tan, K., Chen, L., Perrimon, N., Veenstra, J.A., Zhang, L., and Song, W. (2023). Gut AstA mediates sleep deprivaPon-induced energy wasPng in Drosophila. Cell Discov 9, 49. 10.1038/s41421-023-00541-3. (2) Ahrentlov, N., Kubrak, O., Lassen, M., Malita, A., Koyama, T., Frederiksen, A.S., Sigvardsen, C.M., John, A., Madsen, P., Halberg, K.A., et al. (2025). Protein-responsive gut hormone Tachykinin directs food choice and impacts lifespan. Nature Metabolism. 10.1038/s42255-025-01267-0.

(3) Li, H., Janssens, J., De Waegeneer, M., Kolluru, S.S., Davie, K., Gardeux, V., Saelens, W., David, F.P.A., Brbic, M., Spanier, K., et al. (2022). Fly Cell Atlas: A single-nucleus transcriptomic atlas of the adult fruit fly. Science 375, eabk2432. 10.1126/science.abk2432.

(4) Kubrak, O., Koyama, T., Ahrentlov, N., Jensen, L., Malita, A., Naseem, M.T., Lassen, M., Nagy, S., Texada, M.J., Halberg, K.V., and Rewitz, K. (2022). The gut hormone AllatostaPn C/SomatostaPn regulates food intake and metabolic homeostasis under nutrient stress. Nature communicaPons 13, 692. 10.1038/s41467-022-28268-x.

(5) Malita, A., Kubrak, O., Koyama, T., Ahrentlov, N., Texada, M.J., Nagy, S., Halberg, K.V., and Rewitz, K. (2022). A gut-derived hormone suppresses sugar appePte and regulates food choice in Drosophila. Nature Metabolism 4, 1532-1550. 10.1038/s42255-022-00672-z.

Author response:

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

Reviewer #1 (Public Review)>

Summary:

This research group has consistently performed cutting-edge research aiming to understand the role of hormones in the control of social behaviors, specifically by utilizing the genetically tractable teleost fish, medaka, and the current work is no exception. The overall claim they make, that estrogens modulate social behaviors in males and females is supported, with important caveats. For one, there is no evidence these estrogens are generated by "neurons" as would be assumed by their main claim that it is NEUROestrogens that drive this effect. While indeed the aromatase they have investigated is expressed solely in the brain, in most teleosts, brain aromatase is only present in glial cells (astrocytes, radial glia). The authors should change this description so as not to mislead the reader. Below I detail more specific strengths and weaknesses of this manuscript.

We thank the reviewer for this very positive evaluation of our work and greatly appreciate their helpful comments and suggestions for improving the manuscript. We agree with the comment that the term “neuroestrogens” is misleading. Therefore, we have replaced “neuroestrogens” with “brain-derived estrogens” or “brain estrogens” throughout the manuscript, including the title.

In the following sections, “neuroestrogens” has been revised to align with the surrounding context.

Line 21: “in the brain, also known as neuroestrogens,” → “in the brain.”

Line 28: “neuroestrogens” → “these estrogens.”

Line 30: “mechanism of action of neuroestrogens” → “mode of action of brain-derived estrogens.”

Line 43: “brain-derived estrogens, also called neuroestrogens,” → “estrogens.”

Line 74: “neuroestrogen synthesis is selectively impaired while gonadal estrogen synthesis remains intact” → “estrogen synthesis in the brain is selectively impaired while that in the gonads remains intact.”

Line 77: “neuroestrogens” → “these estrogens.”

Line 335: “levels of neuroestrogens” → “brain estrogen levels.”

Line 338: “neuroestrogens” → “these estrogens.”

Line 351: “neuroestrogens” → “these estrogens.”

Line 357: “neuroestrogen action” → “the action of brain-derived estrogens.”

Line 359: “neuroestrogens” → “estrogen synthesis in the brain.”

Line 390: “active synthesis of neuroestrogens” → “active estrogen synthesis in the brain.”

Line 431: “neuroestrogens” → “estrogens in the brain.”

Line 431: “neuroestrogen action” → “the action of brain-derived estrogens.”

Line 433: “neuroestrogen action” → “their action.”

Strengths:

Excellent use of the medaka model to disentangle the control of social behavior by sex steroid hormones.

The findings are strong for the most part because deficits in the mutants are restored by the molecule (estrogens) that was no longer present due to the mutation.

Presentation of the approach and findings are clear, allowing the reader to make their own inferences and compare them with the authors'.

Includes multiple follow-up experiments, which lead to tests of internal replication and an impactful mechanistic proposal.

Findings are provocative not just for teleost researchers, but for other species since, as the authors point out, the data suggest mechanisms of estrogenic control of social behaviors may be evolutionarily ancient.

We again thank the reviewer for their positive evaluation of our work.

Weaknesses:

(1) As stated in the summary, the authors attribute the estrogen source to neurons and there isn't evidence this is the case. The impact of the findings doesn't rest on this either.

As noted in Response to reviewer #1’s summary comment, we have replaced “neuroestrogens” with “brain-derived estrogens” or “brain estrogens” throughout the manuscript.

Line 63: We have also added the text “In teleost brains, including those of medaka, aromatase is exclusively localized in radial glial cells, in contrast to its neuronal localization in rodent brains (18– 20).” Following this addition, “This observation suggests” in the subsequent sentence has been replaced with “These observations suggest.”

The following references (#18–20), cited in the newly added text above, have been included in the reference list, with other references renumbered accordingly:

P. M. Forlano, D. L. Deitcher, D. A. Myers, A. H. Bass, Anatomical distribution and cellular basis for high levels of aromatase activity in the brain of teleost fish: aromatase enzyme and mRNA expression identify glia as source. J. Neurosci. 21, 8943–8955 (2001).

N. Diotel, Y. Le Page, K. Mouriec, S. K. Tong, E. Pellegrini, C. Vaillant, I. Anglade, F. Brion, F. Pakdel, B. C. Chung, O. Kah, Aromatase in the brain of teleost fish: expression, regulation and putative functions. Front. Neuroendocrinol. 31, 172–192 (2010).

A. Takeuchi, K. Okubo, Post-proliferative immature radial glial cells female-specifically express aromatase in the medaka optic tectum. PLoS One 8, e73663 (2013).

(2) The d4 versus d8 esr2a mutants showed different results for aggression. The meaning and implications of this finding are not discussed, leaving the reader wondering.

Line 282: As the reviewer correctly noted, circles were significantly reduced in mutant males of the Δ8 line, whereas no significant reduction was observed in those of the Δ4 line. However, a tendency toward reduction was evident in the Δ4 line (P = 0.1512), and both lines showed significant differences in fin displays. Based on these findings, we believe our conclusion that esr2a^−/− males exhibit reduced aggression remains valid. To clarify this point and address potential reader concerns, we have revised the text as follows: “esr2a^−/− males from both the Δ8 and Δ4 lines exhibited significantly fewer fin displays than their wildtype siblings (P = 0.0461 and 0.0293, respectively). Circles followed a similar pattern, with a significant reduction in the Δ8 line (P = 0.0446) and a comparable but non-significant decrease in the Δ4 line (P = 0.1512) (Fig. 5L; Fig. S8E), showing less aggression.”

(3) Lack of attribution of previously published work from other research groups that would provide the proper context of the present study.

In response to this and other comments from this reviewer, we have revised the Introduction and Discussion sections as follows.

Line 56: “solely responsible” in the Introduction has been modified to “largely responsible”.

Line 57: “This is consistent with the recent finding in medaka fish (Oryzias latipes) that estrogens act through the ESR subtype Esr2b to prevent females from engaging in male-typical courtship (10)” has been revised to “This is consistent with recent observations in a few teleost species that genetic ablation of AR severely impairs male-typical behaviors (13–16) and with findings in medaka fish (Oryzias latipes) that estrogens act through the ESR subtype Esr2b to prevent females from engaging in maletypical courtship (12)” to include previous studies on the behavior of AR mutant fish (Yong et al., 2017; Alward et al., 2020; Ogino et al., 2023; Nishiike and Okubo, 2024) in the Introduction.

Line 65: “It is worth mentioning that systemic administration of estrogens and an aromatase inhibitor increased and decreased male aggression, respectively, in several teleost species, potentially reflecting the behavioral effects of brain-derived estrogens (21–24)” has been added to the Introduction. This addition provides an overview of previous studies on the effects of estrogens and aromatase on male fish aggression (Hallgren et al., 2006; O’Connell and Hofmann, 2012; Huffman et al., 2013; Jalabert et al., 2015).

Line 367: “treatment of males with an aromatase inhibitor reduces their male-typical behaviors (31– 33)” has been edited to read “treatment of males with an aromatase inhibitor reduces their male-typical behaviors, while estrogens exert the opposite effect (21–24).”

After the revisions described above, the following references (#13, 14, and 22) have been added to the reference list, with other references renumbered accordingly:

L. Yong, Z. Thet, Y. Zhu, Genetic editing of the androgen receptor contributes to impaired male courtship behavior in zebrafish. J. Exp. Biol. 220, 3017–3021 (2017).

B. A. Alward, V. A. Laud, C. J. Skalnik, R. A. York, S. A. Juntti, R. D. Fernald, Modular genetic control of social status in a cichlid fish. Proc. Natl. Acad. Sci. U.S.A. 117, 28167–28174 (2020).

L. A. O’Connell, H. A. Hofmann, Social status predicts how sex steroid receptors regulate complex behavior across levels of biological organization. Endocrinology 153, 1341–1351 (2012).

(4) There are a surprising number of citations not included; some of the ones not included argue against the authors' claims that their findings were "contrary to expectation".

Line 68: As detailed in Response to reviewer #1’s comment 3 on weaknesses, we have cited previous studies on the effects of estrogens and aromatase on male fish aggression (Hallgren et al., 2006; O’Connell and Hofmann, 2012; Huffman et al., 2013; Jalabert et al., 2015) in the Introduction.

The following revisions have also been made to avoid phrases such as “contrary to expectation” and “unexpected.”

Line 76: “Contrary to our expectations” → “Remarkably.”

Line 109: “Contrary to this expectation, however” → “Nevertheless.”

Line 135: “Again, contrary to our expectation, cyp19a1b^−/− males” → “cyp19a1b^−/− males.”

Line 333: “unexpected” → “noteworthy.”

Line 337: “unexpected” → “notable.”

(5) The experimental design for studying aggression in males has flaws. A standard test like a resident intruder test should be used.

We agree that the resident-intruder test is the most commonly used method for assessing aggression. However, medaka form shoals and lack strong territoriality, and even slight dominance differences between the resident and the intruder can increase variability in the results, compromising data consistency. Therefore, in this study, we adopted an alternative approach: placing four unfamiliar males together in a tank and quantifying aggressive interactions in total. This method allows for the assessment of aggression regardless of territorial tendencies, making it more appropriate for our investigation.

(6) While they investigate males and females, there are fewer experiments and explanations for the female results, making it feel like a small addition or an aside.

We agree that the data and discussion for females are less extensive than for males. However, we have previously elucidated the mechanism by which estrogen/Esr2b signaling promotes female mating behavior (Nishiike et al., 2021, Curr Biol, 1699–1710). Accordingly, it follows that the new insights into female behavior gained from the cyp19a1b knockout model are more limited than those for males. Nevertheless, when combined with our prior findings, the female data in this study offer valuable insights, and the overall mechanism through which estrogens promote female mating behavior is becoming clearer. Therefore, we do not consider the female data in this study to be incomplete or merely supplementary.

(7) The statistics comparing "experimental to experimental" and "control to experimental" aren't appropriate.

The reviewer raises concerns about the statistical analysis used for Figures 4C and 4E, suggesting that Bonferroni’s test should be used instead of Dunnett’s test. However, Dunnett’s test is commonly used to compare treatment groups to a reference group that receives no treatment, as in our study. Since we do not compare the treated groups with each other, we believe Dunnett’s test is the most appropriate choice.

Line 619: The reviewer’s concern may have arisen from the phrase “comparisons between control and experimental groups” in the Materials and Methods. We have revised it to “comparisons between untreated and E2-treated groups in Fig. 4, C and D” for clarity.

Reviewer #2 (Public Review):

Summary:

The novelty of this study stems from the observations that neuro-estrogens appear to interact with brain androgen receptors to support male-typical behaviors. The study provides a step forward in clarifying the somewhat contradictory findings that, in teleosts and unlike other vertebrates, androgens regulate male-typical behaviors without requiring aromatization, but at the same time estrogens appear to also be involved in regulating male-typical behaviors. They manipulate the expression of one aromatase isoform, cyp19a1b, that is purported to be brain-specific in teleosts. Their findings are important in that brain estrogen content is sensitive to the brain-specific cyp19a1b deficiency, leading to alterations in both sexual behavior and aggressive behavior. Interestingly, these males have relatively intact fertility rates, despite the effects on the brain.

We thank this reviewer for their positive evaluation of our work and constructive comments, which we found very helpful in improving the manuscript.

That said, the framing of the study, the relevant context, and several aspects of the methods and results raise concerns. Two interpretations need to be addressed/tempered:

(1) that the rescue of cyp19a1b deficiency by tank-applied estradiol is not necessarily a brain/neuroestrogen mode of action, and

Line 155: cyp19a1b-deficient males exhibited a severe reduction in brain E2 levels, yet their peripheral E2 levels remained comparable to those in wild-type males. Given this hormonal milieu and the lack of behavioral change in wild-type males following E2 treatment, the observed recovery of mating behavior in cyp19a1b-deficient males following E2 treatment can be best explained by the restoration of brain E2 levels. However, as the reviewer pointed out, we cannot rule out the possibility that bath-immersed E2 influenced behavior through an indirect peripheral mechanism. To address this concern, we have modified the text as follows: “These results suggest that reduced E2 in the brain is the primary cause of the mating defects, highlighting a pivotal role of brain-derived estrogens in male mating behavior. However, caution is warranted, as an indirect peripheral effect of bath-immersed E2 on behavior cannot be ruled out, although this is unlikely given the comparable peripheral E2 levels in cyp19a1b-deficient and wild-type males. In contrast to mating.”

(2) the large increases in peripheral and brain androgen levels in the cyp19a1b deficient animals imply some indirect/compensatory effects of lifelong cyp19a1b deficiency.

As stated in line 151, androgen/AR signaling has a strong facilitative effect on male-typical behaviors in teleosts. If increased androgen levels in the periphery and brain affected behavior, the expected effect would be facilitative. However, cyp19a1b-deficient males exhibited impaired male-typical behaviors, suggesting that elevated androgen levels were unlikely to be responsible. Although chronic androgen elevation could cause androgen receptor desensitization, which could lead to behavioral suppression, our long-term androgen treatments have consistently promoted, rather than inhibited, male-typical behaviors (e.g., Nishiike et al., Proc Natl Acad Sci USA 121:e2316459121). Hence, this possibility is also highly unlikely.

Reviewer #3 (Public Review):

Summary:

Taking advantage of the existence in fish of two genes coding for estrogen synthase, the enzyme aromatase, one mostly expressed in the brain (Cyp19a1b) and the other mostly found in the gonads (Cyp19a1a), this study investigates the role of neuro-estrogens in the control of sexual and aggressive behavior in teleost fish. The constitutive deletion of Cyp19a1b reduced brain estrogen content by 87% in males and about 50% in females. It led to reduced sexual and aggressive behavior in males and reduced sexual behavior in females. These effects are reversed by adult treatment with estradiol thus indicating that they are activational in nature. The deletion of Cyp19a1b is associated with a reduced expression of the genes coding for the two androgen receptors, ara, and arb, in brain regions involved in the regulation of social behavior. The analysis of the gene expression and behavior of mutants of estrogen receptors indicates that these effects are likely mediated by the activation of the esr1 and esr2a isoforms. These results provide valuable insight into the role of neuro-estrogens in social behavior in the most abundant vertebrate taxa. While estrogens are involved in the organization of the brain and behavior of some birds and rodents, neuro-estrogens appear to play an activational role in fish through a facilitatory action of androgen signaling.

We thank this reviewer for their positive evaluation of our work and comments that have improved the manuscript.

Strengths:

Evaluation of the role of brain "specific" Cyp19a1 in male teleost fish, which as a taxa are more abundant and yet proportionally less studied than the most common birds and rodents. Therefore, evaluating the generalizability of results from higher vertebrates is important. This approach also offers great potential to study the role of brain estrogen production in females, an understudied question in all taxa.

Results obtained from multiple mutant lines converge to show that estrogen signaling drives aspects of male sexual behavior.

The comparative discussion of the age-dependent abundance of brain aromatase in fish vs mammals and its role in organization vs activation is important beyond the study of the targeted species.

We again thank the reviewer for their positive evaluation of our work.

Weaknesses:

(1) The new transgenic lines are under-characterized. There is no evaluation of the mRNA and protein products of Cyp19a1b and ESR2a.

We did not directly assess the function of cyp19a1b and esr2a in our mutant fish. However, the observed reduction in brain E2 levels, with no change in peripheral E2 levels, in cyp19a1b-deficient fish strongly supports the loss of cyp19a1b function. This is stated in the Results section (line 97) as follows: “These results show that cyp19a1b-deficient fish have reduced estrogen levels coupled with increased androgen levels in the brain, confirming the loss of cyp19a1b function.”

Line 473: A previous study reported that female medaka lacking esr2a fail to release eggs due to oviduct atresia (Kayo et al., 2019, Sci Rep 9:8868). Similarly, in this study, some esr2a-deficient females exhibited spawning behavior but were unable to release eggs, although the sample size was limited (Δ8 line: 2/3; Δ4 line: 1/1). In contrast, this was not observed in wild-type females (Δ8 line: 0/12; Δ4 line: 0/11). These results support the effective loss of esr2a function. To incorporate this information into the manuscript, the following text has been added to the Materials and Methods: “A previous study reported that esr2a-deficient female medaka cannot release eggs due to oviduct atresia (59). Likewise, some esr2a-deficient females generated in this study, despite the limited sample size, exhibited spawning behavior but were unable to release eggs (Δ8 line: 2/3; Δ4 line: 1/1), while such failure was not observed in wild-type females (Δ8 line: 0/12; Δ4 line: 0/11). These results support the effective loss of esr2a function.”

The following reference (#59), cited in the newly added text above, have been included in the reference list:

D. Kayo, B. Zempo, S. Tomihara, Y. Oka, S. Kanda, Gene knockout analysis reveals essentiality of estrogen receptor β1 (Esr2a) for female reproduction in medaka. Sci. Rep. 9, 8868 (2019).

(2) The stereotypic sequence of sexual behavior is poorly described, in particular, the part played by the two sexual partners, such that the conclusions are not easily understandable, notably with regards to the distinction between motivation and performance.

Line 103: To provide a more detailed description of medaka mating behavior, we have revised the text from “The mating behavior of medaka follows a stereotypical pattern, wherein a series of followings, courtship displays, and wrappings by the male leads to spawning” to “The mating behavior of medaka follows a stereotypical sequence. It begins with the male approaching and closely following the female (following). The male then performs a courtship display, rapidly swimming in a circular pattern in front of the female. If the female is receptive, the male grasps her with his fins (wrapping), culminating in the simultaneous release of eggs and sperm (spawning).”

(3) The behavior of females is only assessed from the perspective of the male, which raises questions about the interpretation of the reduced behavior of the males.

In medaka, female mating behavior is largely passive, except for rejecting courtship attempts and releasing eggs. Therefore, its analysis relies on measuring the latency to receive following, courtship displays, or wrappings from the male and the frequency of courtship rejection or wrapping refusal. We understand the reviewer’s perspective that cyp19a1b-deficient females might not be less receptive but instead less attractive to males, potentially leading to reduced male mating efforts. However, since these females are approached and followed by males at levels comparable to wild-type females, this possibility appears unlikely. Moreover, cyp19a1b-deficient females tend to avoid males and exhibit a slightly female-oriented sexual preference. While these traits are closely associated with reduced sexual receptivity, they do not readily align with reduced sexual attractiveness. Therefore, it is more plausible to conclude that these females have decreased receptivity rather than being less attractive to males.

(4) At no point do the authors seem to consider that a reduced behavior of one sex could result from a reduced sensory perception from this sex or a reduced attractivity or sensory communication from the other sex.

Line 112: As noted above, the impaired mating behavior of cyp19a1b-deficient females is unlikely to be due to reduced attractiveness to males. Similarly, mating behavior tests using esr2b-deficient females as stimulus females suggest that the impaired mating behavior of cyp19a1b-deficient males cannot be attributed to reduced attractiveness to females. However, the possibility that their impaired mating behavior could be attributed to altered cognition or sexual preference cannot be ruled out. To reflect this in the manuscript, we have revised the text “, suggesting that they are less motivated to mate” to “. These results suggest that they are less motivated to mate, though an alternative interpretation that their cognition or sexual preference may be altered cannot be dismissed.”

(5) Aspects of the methods are not detailed enough to allow proper evaluation of their quality or replication of the data.

In response to this and other specific comments from this reviewer, we have revised the Materials and Methods section to include more detailed descriptions of the methods.

Line 469: The following text has been added to describe the method for domain identification in medaka Esr2a: “The DNA- and ligand-binding domains of medaka Esr2a were identified by sequence alignment with yellow perch (Perca flavescens) Esr2a, for which these domain locations have been reported (58).”

The following reference (#58), cited in the newly added text above, have been included in the reference list:

S. G. Lynn, W. J. Birge, B. S. Shepherd, Molecular characterization and sex-specific tissue expression of estrogen receptor α (esr1), estrogen receptor βa (esr2a) and ovarian aromatase (cyp19a1a) in yellow perch (Perca flavescens). Comp. Biochem. Physiol. B Biochem. Mol. Biol. 149, 126–147 (2008).

Line 540: The text “, and the total area of signal in each brain nucleus was calculated using Olyvia software (Olympus)” has been revised to include additional details on the single ISH method as follows: “. The total area of signal across all relevant sections, including both hemispheres, was calculated for each brain nucleus using Olyvia software (Olympus). Images were converted to a 256-level intensity scale, and pixels with intensities from 161 to 256 were considered signals. All sections used for comparison were processed in the same batch, without corrections between samples.”

Line 596: The following text has been added to include additional details on the double ISH method: “Cells were identified as coexpressing the two genes when Alexa Fluor 555 and fluorescein signals were clearly observed in the cytoplasm surrounding DAPI-stained nuclei, with intensities markedly stronger than the background noise.”

(6) It seems very dangerous to use the response to a mutant abnormal behavior (ESR2-KO females) as a test, given that it is not clear what is the cause of the disrupted behavior.

esr2b-deficient females have fully developed ovaries, a normal sex steroid milieu, and sexual attractiveness to males comparable to wild-type females, yet they are completely unreceptive to male courtship (Nishiike et al., 2021, Curr Biol, 1699–1710). Although, as the reviewer noted, the detailed mechanisms underlying this phenotype remain unclear, it is evident that the loss of estrogen/Esr2b signaling in the brain severely impairs sexual receptivity. Therefore, using esr2b-deficient females as stimulus females in the mating behavior test eliminates the influence of female sexual receptivity and male attractiveness to females, enabling the exclusive assessment of male mating motivation. This rationale is already presented in the Results section (lines 116–120), and we believe this experimental design offers a robust framework for assessing male mating motivation.

Additionally, the mating behavior test with esr2b-deficient females complemented the test with wildtype females, and its results were not the sole basis for our discussion of the male mating behavior phenotype. The results of both tests were largely concordant, and we believe that the conclusions drawn from them are highly reliable.

Meanwhile, in the test with esr2b-deficient females, cyp19a1b-deficient males were courted more frequently by these females than wild-type males. As the reviewer noted, this may suggest an anomaly in the test. Accordingly, we have confined our discussion to the possibility that “Perhaps cyp19a1b^−/− males are misidentified as females by esr2b-deficient females because they are reluctant to court or they exhibit some female-like behavior” (line 131).

(7) Most experiments are weakly powered (low sample size) and analyzed by multiple T-tests while 2 way ANOVA could have been used in several instances. No mention of T or F values, or degrees of freedom.

Histological analysis was conducted with a relatively small sample size, as our previous experience suggested that interindividual variability in the results would not be substantial. As significant differences were detected in many analyses, further increasing the sample size is unnecessary.

Although two-way ANOVA could be used instead of multiple T-tests for analyzing the data in Figures 4D, 4F, 6D, S4A, and S4B, we applied the Bonferroni–Dunn correction to control for multiple pairwise comparisons in multiple T-tests. As this comparison method is equivalent to the post hoc test following two-way ANOVA, the statistical results are identical regardless of whether T-tests or two-way ANOVA are used.

For the data in Figures 4D, 4F, S4A, and S4B, the primary focus is on whether relative luciferase activity differs between E2-treated and untreated conditions for each mutant construct. Therefore, two-way ANOVA is not particularly relevant, as assessing the main effect of construct type or its interaction with E2 treatment does not provide meaningful insights. Similarly, in Figure 6D, the focus is solely on whether wild-type and mutant females differ in time spent at each distance. Given this, two-way ANOVA is unnecessary, as analyzing the main effect of distance is not meaningful.

Accordingly, two-way ANOVA was not employed in this study, and therefore, its corresponding F values were not included. As the figure legends specify the sample sizes for all analyses, specifying degrees of freedom separately was deemed unnecessary.

(8) The variability of the mRNA content for the same target gene between experiments (genotype comparison vs E2 treatment comparison) raises questions about the reproducibility of the data (apparent disappearance of genotype effect).

As the reviewer pointed out, the overall area of ara expression is larger in Figure 2J than in Figure 2F. However, the relative area ratios of ara expression among brain nuclei are consistent between the two figures, indicating the reproducibility of the results. Thus, this difference is unlikely to affect the conclusions of this study.

Additionally, the differences in ara expression in pPPp and arb expression in aPPp between wild-type and cyp19a1b-deficient males appear less pronounced in Figures 2J and 2K than in Figures 2F and 2H. This is likely attributable to the smaller sample size used in the experiments for Figures 2J and 2K, resulting in less distinct differences. However, as the same genotype-dependent trends are observed in both sets of figures, the conclusion that ara and arb expression is reduced in cyp19a1b-deficient male brains remains valid.

(9) The discussion confuses the effects of estrogens on sexual differentiation (developmental programming = permanent) and activation (= reversible activation of brain circuits in adulthood) of the brain and behavior. Whether sex differences in the circuits underlying social behaviors exist is not clear.

We recognize that the effects of adult steroids are sometimes not considered to be sexual differentiation, as they do not differentiate the neural substrate, but rather transiently activate the already masculinized or feminized substrate. Arnold (2017, J Neurosci Res 95:291–300) contends that all factors that cause sex differences, including the transient effects of adult steroids, should be incorporated into a theory of sexual differentiation, and indeed, these effects may be the most potent proximate factors that make males and females different. We concur with this perspective and have adopted it as a foundation for our manuscript.

In teleosts, early developmental exposure to steroids has minimal impact, and sexual differentiation relies primarily on steroid action in adulthood (Okubo et al., 2022, Spectrum of Sex, pp. 111–133). This is evidenced by the effective reversal of sex-typical behaviors through experimental hormonal manipulation in adult teleosts and the absence of transient early-life steroid surges observed in mammals and birds. Accordingly, our discussion on brain sexual differentiation, including the statement in line 347, “This variation among species may represent the activation of neuroestrogen synthesis at life stages critical for sexual differentiation of behavior that are unique to each species”, remains well-supported. Additionally, given these considerations, while sex differences in neural circuit activation are evident in teleosts, substantial structural differences in these circuits are unlikely.

(10) Overall, the claims regarding the activational role of neuro-estrogens on male sexual behavior are supported by converging evidence from multiple mutant lines. The role of neuroestrogens on gene expression in the brain is mostly solid too. The data for females are comparatively weaker. Conclusions regarding sexual differentiation should be considered carefully.

We agree that the data for females are less extensive than for males. However, we have previously elucidated the mechanism by which estrogen/Esr2b signaling promotes female mating behavior (Nishiike et al., 2021). Accordingly, it follows that the new insights into female behavior gained from the cyp19a1b knockout model are more limited than those for males. Nevertheless, when integrated with our prior findings, the data on females in this study provide significant insights, and the overall mechanism through which estrogens promote female mating behavior is becoming clearer. Therefore, we do not consider the female data in this study to be incomplete or merely supplementary.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

The authors set out to answer an intriguing question regarding the hormonal control of innate social behaviors in medaka. Specifically, they wanted to test the effects of cyp19a1b mutation on mating and aggression in males. They also test these effects in females. Their approach takes them down several distinct experimental pathways, including one investigating how cyp19a1a function is related to androgen receptor expression and how estrogens themselves may act on the androgen receptor to modulate its expression, as well as how different esr genes may be involved. The study and its results are valuable and a clear, general conclusion of a pathway from brain aromatase>estrogens>esr genes> androgen receptor can be made. This is important, novel, and impactful. However, there are issues with how the study logic is set up, the approach for assessing certain behaviors, the statistics used, the interpretation of findings, and placing the findings in the proper context based on previous work, which manifests as a general issue where previous work is not properly attributed to.

Thank you for your thoughtful review. We have carefully addressed each specific comment, as detailed below.

Major comments:

(1) The background for the rationale of the current study is misleading and lacks proper context. The authors root the logic of their experiment in determining whether estrogens regulate male-typical behaviors because the current assumption is androgens are "solely responsible" for male-typical behaviors in teleosts. This is not the case. Previous studies have shown aromatase/estrogens are involved in male-typical aggression in teleosts. For example, to name a couple:

Huffman, L. S., O'Connell, L. A., & Hofmann, H. A. (2013). Aromatase regulates aggression in the African cichlid fish Astatotilapia burtoni. Physiology & behavior, 112, 77-83.

O'Connell, L. A., & Hofmann, H. A. (2012). Social status predicts how sex steroid receptors regulate complex behavior across levels of biological organization. Endocrinology, 153(3), 1341-1351.

And even a recent paper sheds light on a possible AR>aromatase.estradiol hypothesis of male typical behaviors:

Lopez, M. S., & Alward, B. A. (2024). Androgen receptor deficiency is associated with reduced aromatase expression in the ventromedial hypothalamus of male cichlids. Annals of the New York Academy of Sciences.

Interestingly, the authors cite Hufmann et al in the discussion, so I don't understand why they make the claims they do about estrogens and male-typical behavior.

Related to this, is an issue of proper attribution to published work. Indeed, missing are key references from lab groups using AR mutant teleosts. Here are a couple:

Yong, L., Thet, Z., & Zhu, Y. (2017). Genetic editing of the androgen receptor contributes to impaired male courtship behavior in zebrafish. Journal of Experimental Biology, 220(17), 3017-3021.

Alward, B. A., Laud, V. A., Skalnik, C. J., York, R. A., Juntti, S. A., & Fernald, R. D. (2020). Modular genetic control of social status in a cichlid fish. Proceedings of the National Academy of Sciences, 117(45), 28167-28174.

Ogino, Y., Ansai, S., Watanabe, E., Yasugi, M., Katayama, Y., Sakamoto, H., ... & Iguchi, T. (2023). Evolutionary differentiation of androgen receptor is responsible for sexual characteristic development in a teleost fish. Nature communications, 14(1), 1428.

As noted in Response to reviewer #1’s comment 3 on weaknesses, we have revised the Introduction and Discussion sections as follows.

Line 56: “solely responsible” in the Introduction has been modified to “largely responsible”.

Line 57: The text “This is consistent with the recent finding in medaka fish (Oryzias latipes) that estrogens act through the ESR subtype Esr2b to prevent females from engaging in male-typical courtship (10)” has been revised to “This is consistent with recent observations in a few teleost species that genetic ablation of AR severely impairs male-typical behaviors (13–16) and with findings in medaka fish (Oryzias latipes) that estrogens act through the ESR subtype Esr2b to prevent females from engaging in male-typical courtship (12)” to include previous studies on the behavior of AR mutant fish (Yong et al., 2017; Alward et al., 2020; Ogino et al., 2023; Nishiike and Okubo, 2024) in the Introduction.

Line 65: “It is worth mentioning that systemic administration of estrogens and an aromatase inhibitor increased and decreased male aggression, respectively, in several teleost species, potentially reflecting the behavioral effects of brain-derived estrogens (21–24)” has been added to the Introduction, providing an overview of previous studies on the effects of estrogens and aromatase on male fish aggression (Hallgren et al., 2006; O’Connell and Hofmann, 2012; Huffman et al., 2013; Jalabert et al., 2015).

Line 367: “treatment of males with an aromatase inhibitor reduces their male-typical behaviors (31– 33)” has been edited to read “treatment of males with an aromatase inhibitor reduces their male-typical behaviors, while estrogens exert the opposite effect (21–24).”

After the revisions described above, the following references (#13, 14, and 22) have been added to the reference list:

L. Yong, Z. Thet, Y. Zhu, Genetic editing of the androgen receptor contributes to impaired male courtship behavior in zebrafish. J. Exp. Biol. 220, 3017–3021 (2017).

B. A. Alward, V. A. Laud, C. J. Skalnik, R. A. York, S. A. Juntti, R. D. Fernald, Modular genetic control of social status in a cichlid fish. Proc. Natl. Acad. Sci. U.S.A. 117, 28167–28174 (2020).

L. A. O’Connell, H. A. Hofmann, Social status predicts how sex steroid receptors regulate complex behavior across levels of biological organization. Endocrinology 153, 1341–1351 (2012).

While Lopez and Alward (2024) provide valuable insights into the regulation of cyp19a1b expression by androgens, our study focuses specifically on the functional aspects of cyp19a1b. Expanding the discussion to include expression regulation would divert from the primary focus of our manuscript. For this reason, we have opted not to cite this reference.

(2) As it is now, the authors are only citing a book chapter/review from their own group. This is a serious issue as it does not provide the proper context for the work. The authors need to fix their issues of attribution to previously published work and the proper interpretation of the work that they are aware of as it pertains to ideas proposed on the roles of androgens and estrogens in the control of male-typical behaviors. This is also important to get the citations right because the common use of "contrary to expectations" when describing their results is actually not correct. Many of the observations are expected to a degree. However, this doesn't take away from a generally stellar experimental design and mostly clear results. The authors do not need to rely on enhancing the impact of their paper by making false claims of unexpected findings. The depth and clarity of your findings are where the impact of your work is.

As detailed in Response to reviewer #1’s comment 3 on weaknesses, we have cited previous studies on the effects of estrogens and aromatase on male fish aggression (Hallgren et al., 2006; O’Connell and Hofmann, 2012; Huffman et al., 2013; Jalabert et al., 2015) in the Introduction.

Additionally, as noted in Response to reviewer #1’s comment 4 on weaknesses, we have made the following revisions to avoid phrases such as “contrary to expectation” and “unexpected.”

Line 76: “Contrary to our expectations” → “Remarkably.”

Line 109: “Contrary to this expectation, however” → “Nevertheless.”

Line 135: “Again, contrary to our expectation, cyp19a1b^−/− males” → “cyp19a1b^−/− males.”

Line 333: “unexpected” → “noteworthy.”

Line 337: “unexpected” → “notable.”

(3) The experimental design for studying aggression in males has flaws. A standard test like a residentintruder test should be used. An assay in which only male mutants are housed together? I do not understand the logic there and the logic for the approach isn't even explained. Too many confounds that are not controlled for. It makes it seem like an aspect of the study that was thrown in as an aside.

As noted in Response to reviewer #1’s comment 5 on weaknesses, medaka form shoals and lack strong territoriality. As a result, even slight differences in dominance between the resident and intruder can substantially impact the outcomes of the resident-intruder test. Therefore, we adopted an alternative approach in this study.

(4) Hormonal differences in the mutants seem to vary based on sex, and the meaning of these differences, or how they affect interpreting the findings, wasn't discussed. There was no acknowledegment of the fact that female central E2 was still at 50%, meaning the "rescue" experiments using peripheral injections are not given the proper context. For example, this is different than giving a fish with only 16% of their normal central E2 an E2 injection. Missing as well is a clear hypothesis for why E2 injections did not rescue aggression deficits in cyp19a1b mutant males.

Line 385: As the reviewer pointed out, the degree of brain estrogen reduction in cyp19a1b-deficient fish differs greatly between males and females. This is likely because females receive a large supply of estrogens from the ovaries. Given that estrogen levels in cyp19a1b-deficient females were 50% of those in wild-type females, it can be inferred that half of their brain estrogens are synthesized locally, while the other half originates from the ovaries. This is an important finding, and we have already noted in the Discussion that “females have higher brain levels of estrogens, half of which are synthesized locally in the brain (i.e., neuroestrogens)” However, as this explanation was not sufficiently clear, we have revised it to “females have higher brain levels of estrogens, with half being synthesized locally and the other half supplied by the ovaries.”

The reviewer raised a concern that conducting the estrogen rescue experiment in females, where 50% of brain estrogens remain, might be inappropriate. However, as this experiment was conducted exclusively in males, this concern is not applicable.

Line 377: As noted in the reviewer’s subsequent comment, the failure of aggression recovery in E2treated cyp19a1b-deficient males could be due to insufficient induction of ara/arb expression in aggression-relevant brain regions. To address this concern, we have inserted the following statement into the Discussion after “the development of male behaviors may require moderate neuroestrogen levels that are sufficient to induce the expression of ara and arb, but not esr2b, in the underlying neural circuitry”: “This may account for the lack of aggression recovery in E2-treated cyp19a1b-deficient males in this study.”

(5) In relation to that, the "null" results may have some of the most interesting implications, but they are barely discussed. For example, what does it mean that E2 didn't restore aggression in male cyp19 mutants? Is this a brain region factor? Could this relate to findings from Lopez et al NYAS, where male and female Ara mutants show different effects on brain-region-specific aromatase expression? And maybe this relates to the different impact of estrogens on ar expression. Were the different effects impacted in aggression areas? Maybe this is why E2 injection didn't retore aggression in males. You could make the argument that: (1) E2 doesn't restore ar expression in aggression regions and that's why there was no rescue. Or (2) that the circuits in adulthood that regulate aggression are NOT dependent on aggression but in early development they are. Another null finding not expanded on is why the two esr2a mutant lines showed differences. There is no reason to trust one line over the other, meaning we still don't know whether esr2a is required for latency to follow.

As stated in our response to the previous comment, we have added the following text to the Discussion (line 377): “This may account for the lack of aggression recovery in E2-treated cyp19a1b-deficient males in this study.” Meanwhile, as discussed in lines 341–342, it is highly unlikely that the neural circuits regulating aggression are primarily influenced by early-life estrogen exposure, because androgen administration in adulthood alone is sufficient to induce high levels of aggression in both sexes. This notion is further supported by previous observations that cyp19a1b expression in the brain is minimal during embryonic development (Okubo et al., 2011, J Neuroendocrinol, 23:412–423).

The findings of Lopez and Alward (2024) pertain to the regulation of cyp19a1b expression by androgen receptors. While this represents an important aspect of neuroendocrine regulation, it does not appear to be directly relevant to our discussion on cyp19a1b-mediated regulation of androgen receptor expression.

To ensure the reliability of behavioral analyses in mutant fish, we consider a phenotype valid only when it is consistently observed in two independent mutant lines. In the mating behavior test examining esr2adeficient males using esr2b-deficient females as stimulus females, Δ8 line males exhibited a shorter latency to initiate following than wild-type males, whereas Δ4 line males did not. This discrepancy led us to refrain from drawing conclusions about the role of esr2a in mating behavior, even though the mating behavior test using wild-type females as stimulus females yielded consistent results in the Δ8 and Δ4 lines. Therefore, we do not consider the reviewer’s concern to be a significant issue.

(6) Not sure what's going on with the statistics, but it is not appropriate here to treat a "control" group as special. All groups are "experimental" groups. There is nothing special about the control group in this context. all should be Bonferroni post-hoc tests.

Line 619: As detailed in Response to reviewer #1’s comment 7 on weaknesses, we consider Dunnett’s test the most appropriate choice for the experiments presented in Figures 4C and 4E. We acknowledge that the reviewer’s concern may stem from the phrase “comparisons between control and experimental groups” in the Materials and Methods section. To clarify this point, we have revised it to “comparisons between untreated and E2-treated groups in Fig. 4, C and D” for clarity.

Minor comments:

Line 47: then how can you say the aromatization hypothesis is "correct"? it only applies to a few species so far. Need to change the framing, not state so strongly such a vague thing as a hypothesis being "correct".

Line 45: To address this concern, we have modified “widely accepted as correct” to “widely acknowledged”, ensuring a more precise characterization.

Figure 1: looks like a dosage effect in males but not females. this should be discussed at some point, even if just to mention a dosage effect exists and put it in context.

Line 91: We have revised the sentence “In males, brain E2 in heterozygotes (cyp19a1b+/−) was also reduced to 45% of the level in wild-type siblings (P = 0.0284) (Fig. 1A)” by adding “, indicating a dosage effect of cyp19a1b mutation” to make this point explicit.

Were male cyp19 KO aggressive towards females?

We have not observed cyp19a1b-deficient males exhibiting aggressive behavior towards females in our experiments. Therefore, we do not consider them aggressive toward females.

Please explain how infertility would lead to reduced mating.

Line 142: As the reviewer has questioned, even if cyp19a1b-deficient males exhibit infertility due to efferent duct obstruction, it is difficult to imagine that this directly leads to reduced mating. However, the inability to release sperm could indirectly affect behavior. To address this, we have added “, possibly due to the perception of impaired sperm release” after “If this is also the case in medaka, the observed behavioral defects might be secondary to infertility.”

Describe something about the timing of the treatment here. How can peripheral E2 injections restore it when peripheral levels are normal? Did these injections restore central levels? This needs to be shown experimentally.

Line 517: As described in the Materials and Methods, E2 treatment was conducted by immersing fish in E2-containing water for 4 days. However, we had not explicitly stated that the water was changed daily to maintain the nominal concentration. To clarify this and address reviewer #2’s comment 9, we have revised “males were treated with 1 ng/ml of E2 (Fujifilm Wako Pure Chemical, Osaka, Japan) or vehicle (ethanol) alone by immersion in water for 4 days” to “males were treated with 1 ng/ml of E2 (Fujifilm Wako Pure Chemical, Osaka, Japan), which was first dissolved in 100% ethanol (vehicle), or with the vehicle alone by immersion in water for 4 days, with daily water changes to maintain the nominal concentration.”

Line 522: The treatment effectively restored mating activity and ara/arb expression in the brain, suggesting a sufficient increase in brain E2 levels. However, we did not measure the actual increase, and its extent remains uncertain. To reflect this in the manuscript, we have now added the following sentence: “Although the exact increase in brain E2 levels following E2 treatment was not quantified, the observed positive effects on behavior and gene expression suggest that it was sufficient.”

I know the nomenclature differs among those who study teleosts, but it's ARa and then gene is ar1 (as an example; arb would be ar2). You're recommended the following citation to remain consistent:

Munley, K. M., Hoadley, A. P., & Alward, B. A. (2023). A phylogenetics-based nomenclature system for steroid receptors in teleost fishes. General and Comparative Endocrinology, 114436.

Paralogous genes resulting from the third round of whole-genome duplication in teleosts are typically designated by adding the suffixes “a” and “b” to their gene symbols. This convention also applies to the two androgen receptor genes, commonly referred to as ara and arb. While the alternative names ar1 and ar2 may gain broader acceptance in the future, ara and arb remain more widely used at present. Therefore, we have chosen to retain ara and arb in this manuscript.

Line 268: how is this "suggesting" less aggression? They literally showed fewer aggressive displays, so it doesn't suggest it - it literally shows it.

Line 285: Following this thoughtful suggestion, we have changed “suggesting less aggression” to “showing less aggression.”

Line 317: how can you still call it the primary driver?

The stimulatory effects of aromatase/estrogens on male-typical behaviors are exerted through the potentiation of androgen/AR signaling. Thus, we still believe that androgens—specifically 11KT in teleosts—serve as the primary drivers of these behaviors.

Line 318: not all deficits, like aggression, were rescued.

Line 334: To address this comment, “These behavioral deficits were rescued by estrogen administration, indicating that reduced levels of neuroestrogens are the primary cause of the observed phenotypes: in other words, neuroestrogens are pivotal for male-typical behaviors in teleosts” has been modified and now reads “Deficits in mating were rescued by estrogen administration, indicating that reduced brain estrogen levels are the primary cause of the observed mating impairment; in other words, brain-derived estrogens are pivotal at least for male-typical mating behaviors in teleosts.”

Line 324: what do you mean by "sufficient"? To show that, you'd have to castrate the male and only give estrogen back. the authors continue to overstate virtually every aspect of their study, seemingly in an unnecessary manner.

Line 341: Our intention was to convey that brain-derived estrogens early in life are not essential for the expression of male-typical behaviors in teleosts. However, we recognize that the term “sufficient” could be misinterpreted as implying that estrogens alone are adequate, without contributions from other factors such as androgens. To clarify this, we have revised the text from “neuroestrogen activity in adulthood is sufficient for the execution of male-typical behaviors, while that in early in life is not requisite. Thus, while” to “brain-derived estrogens early in life is not essential for the execution of male-typical behaviors. While.”

Line 329: so? in adult mice, amygdala aromatase neurons still regulate aggression. The amount in adulthood seems less important compared to site-specific functions.

Line 346: We do not intend to suggest that brain aromatase activity in adulthood plays a negligible role in male behaviors in rodents, as we have already acknowledged its necessity in the Introduction (lines 42–43). To enhance clarity and prevent misinterpretation, we have added “, although it remains important for male behavior in adulthood” to the end of the sentence: “brain aromatase activity in rodents reaches its peak during the perinatal period and thereafter declines with age.”

Line 351: This contradicts what you all have been saying.

Line 65: As mentioned in Response to reviewer #1’s comment 3 on weaknesses, the following text has been added to the Introduction: “It is worth mentioning that systemic administration of estrogens and an aromatase inhibitor increased and decreased male aggression, respectively, in several teleost species, potentially reflecting the behavioral effects of brain-derived estrogens (21–24)”, providing an overview of previous studies on the effects of estrogens and aromatase on male fish aggression (Hallgren et al., 2006; O’Connell and Hofmann, 2012; Huffman et al., 2013; Jalabert et al., 2015). With this revision, we believe the inconsistency has been addressed.

Line 367: Additionally, we have revised the sentence from “treatment of males with an aromatase inhibitor reduces their male-typical behaviors (31–33)” to “treatment of males with an aromatase inhibitor reduces their male-typical behaviors, while estrogens exert the opposite effect (21–24).”

Line 360: change to "...possibility that is not mutually exclusive,"

Line 378: We have revised the phrase as suggested from “Another possibility, not mutually exclusive,” to “Another possibility that is not mutually exclusive.”

Line 363: but it didn't rescue aggression

Line 381: In response, we have revised the sentence from “This possibility is supported by the present observation that estrogen treatment facilitated mating behavior in cyp19a1b-deficient males but not in their wild-type siblings” to “This possibility is at least likely for mating behavior, as estrogen treatment facilitated mating behavior in cyp19a1b-deficient males but not in their wild-type siblings.”

Line 367: on average

To explain the sex differences in the role of aromatase, what about the downstream molecular or neural targets? In mammals, hodology is related to sex differences. there could be convergent sex differences in regulating the same type of behaviors as well.

Our findings demonstrate that brain-derived estrogens promote the expression of ara, arb, and their downstream target genes vt and gal in males, while enhancing the expression of npba, a downstream target of Esr2b signaling, in females. The identity of additional target genes and their roles in specific neural circuits remain to be elucidated, and we aim to address these in future research.

Lines 378-382: this doesn't logically follow. pgf2a could be the target of estrogens which in the intact animal do regulate female sexual receptivity. And how can you say this given that your lab has shown in esr2b mutants females don't mate?

We agree that PGF2α signaling may be activated by estrogen signaling, as stated in lines 404–407: “the present finding provides a likely explanation for this apparent contradiction, namely, that neuroestrogens, rather than or in addition to ovarian-derived circulating estrogens, may function upstream of PGF2α signaling to mediate female receptivity.” The observation that esr2b-deficient females do not accept male courtship is also stated in lines 401–403: “we recently challenged it by showing that female medaka deficient for esr2b are completely unreceptive to males, and thus estrogens play a critical role in female receptivity.”

Line 396-397: or the remaining estrogens are enough to activate esr2b-dependent female-typical mating behaviors.

We agree that cyp19a1b deficiency did not completely preclude female mating behavior, most likely because residual estrogens in the brains of cyp19a1b-deficient females enable weak activation of Esr2b signaling. However, the relevant section in the Discussion is not focused on examining why mating behavior persisted, but rather on considering the implications of this finding for the neural circuits regulating mating behavior. Therefore, incorporating the suggested explanation here would shift the focus and would not be appropriate.

Line 420-421: this is a lot of variation. Was age controlled for?

The time required for medaka to reach sexual maturity varies with rearing density and food availability. Due to space constraints, we adjust these parameters as needed, which led to variation in the ages of the experimental fish. However, since all experiments were conducted using sibling fish of the same age that had just reached sexual maturity, we believe this does not affect our conclusions.

Line 457: have these kits been validated in medaka?

Although we have not directly validated its applicability in medaka, its extensive use in this species suggests that it us unlikely to pose any issues (e.g., Ussery et al., 2018, Aquat Toxicol, 205:58–65; Lee et al., 2019, Ecotoxicol Environ Saf, 173:174–181; Kayo et al., 2020, Gen Comp Endocrinol, 285:113272; Fischer et al., 2021, Aquat Toxicol, 236:105873; Royan et al., 2023, Endocrinology, 164:bqad030).

Line 589, re fish that spawned: how many times did this happen? Please note it is based on genotype and experiment. This could be important.

Line 627: In response to this comment, we have added the following details: “Specifically, 7/18 cyp19a1b^+/+, 11/18 cyp19a1b^+/−, and 6/18 cyp19a1b^−/− males were excluded in Fig. 1D; 6/10 cyp19a1b^+/+, 3/10 cyp19a1b^+/−, and 6/10 cyp19a1b^−/− females were excluded in Fig. 6B; 2/23 esr1+/+ and 5/24 esr1−/− males were excluded in Fig. S7; 2/24 esr2a+/+ and 3/23 esr2a^−/− males were excluded in Fig. S8A; 0/23 esr2a+/+ and 0/23 esr2a^−/− males were excluded in Fig. S8B.”

Reviewer #2 (Recommendations For The Authors):

Abstract:

(A1) The framing of neuroestrogens being important for male-typical rodents, and not for other vertebrate lineages, does not account for other groups (birds) in which this is true (the authors can consult their cited work by Balthazart (Reference 6) for extensive accounting of this). This makes the novelty clause in the abstract "indicating that neuro-estrogens are pivotal for male-typical behaviors even in nonrodents" less surprising and should be acknowledged by the authors by amending or omitting this novelty clause. The findings regarding androgen receptor transcription (next sentence) are more important and pertinent.

Line 27: We recognize that the aromatization hypothesis applies to some birds, including zebra finches, as stated in the Introduction (lines 48–49) and Discussion (lines 432–433). However, this was not reflected in the Abstract. Following the reviewer’s suggestion, we have changed “in non-rodents” to “in teleosts.”

(A2) The medaka line that has been engineered to have aromatase absent in the brain is presented briefly in the abstract, but can be misinterpreted as naturally occurring. This should be amended, by including something like "engineered" or "directed mutant" before 'male medaka fish'.

Line 24: We have added “mutagenesis-derived” before “male medaka fish” in response to this comment.

Introduction:

(I1) The paragraph on teleost brain aromatase should acknowledge that while the capacity for estrogen synthesis in the brain is 100-1000 fold higher in teleosts as compared to rodents and other vertebrates, the majority of this derives from glial and not neural sources. This can be confusing for readers since the term 'neuroestrogens' often refers to the neuronal origin and signalling. And this observation includes the exclusive radial glial expression of cyp19a1b in medaka (Diotel et al., 2010), and first discovered in midshipman (Forlano et al., 2001), each of which should also be cited here. In addition, the authors expend much text comparing teleosts and rodents, but it is worth expanding these kinds of comparisons, especially by pointing out that parts of the primate brain are found to densely express aromatase (see work by Ei Terasawa and others).

In response to this comment and a similar comment from reviewer #1, we have replaced “neuroestrogens” with “brain-derived estrogens” or “brain estrogens” throughout the manuscript.

Line 63: We have also added the text “In teleost brains, including those of medaka, aromatase is exclusively localized in radial glial cells, in contrast to its neuronal localization in rodent brains (18– 20).” As a result of this addition, we have changed “This observation suggests” to “These observations suggest” in the subsequent sentence.

Line 51: Additionally, to include information on aromatase in the primate brain, we have added the following text: “In primates, the hypothalamic aromatization of androgens to estrogens plays a central role in female gametogenesis (10) but is not essential for male behaviors (7, 8).”

The following references (#10 and 18–20), cited in the newly added text above, have been included in the reference list, with other references renumbered accordingly:

E. Terasawa, Neuroestradiol in regulation of GnRH release. Horm. Behav. 104, 138–145 (2018).

P. M. Forlano, D. L. Deitcher, D. A. Myers, A. H. Bass, Anatomical distribution and cellular basis for high levels of aromatase activity in the brain of teleost fish: aromatase enzyme and mRNA expression identify glia as source. J. Neurosci. 21, 8943–8955 (2001).

N. Diotel, Y. Le Page, K. Mouriec, S. K. Tong, E. Pellegrini, C. Vaillant, I. Anglade, F. Brion, F. Pakdel, B. C. Chung, O. Kah, Aromatase in the brain of teleost fish: expression, regulation and putative functions. Front. Neuroendocrinol. 31, 172–192 (2010).

A. Takeuchi, K. Okubo, Post-proliferative immature radial glial cells female-specifically express aromatase in the medaka optic tectum. PLoS One 8, e73663 (2013).

(I2) It is difficult to resolve from the introduction and work cited how restricted cyp19a1b is to the medaka brain. Important for the results of this study, it is not clear whether it is more of a bias in the brain vs other tissues, or if the cyp19a1b deficiency is restricted to the brain, and gonadal/peripheral cyp19 expression persists. The authors need to improve their consideration of the alternatives, i.e., that this manipulation is not somehow affecting: 1) peripheral aromatase expression (either cyp19a1a or cyp19a1b) in the gonad or elsewhere, 2) compensatory processes, such as other steroidogenic genes (are androgen synthesizing enzymes increasing?).

Our previous study demonstrated that cyp19a1b is expressed in the gonads, but at levels tens to hundreds of times lower than those in the brain (Okubo et al., 2011, J Neuroendocrinol 23:412–423). Additionally, a separate study in medaka reported that cyp19a1b expression in the ovary is considerably lower than that of cyp19a1a (Nakamoto et al., 2018, Mol Cell Endocrinol 460:104–122). Given these observations, any potential effect of cyp19a1b knockout on peripheral estrogen synthesis is likely negligible. Indeed, Figures S1C and S1D confirm that cyp19a1b knockout does not alter peripheral E2 levels.

Line 72: To incorporate this information into the Introduction and address the following comment, we have added the following text: “In medaka, cyp19a1b is also expressed in the gonads, but only at a level tens to hundreds of times lower than in the brain and substantially lower than that of cyp19a1a (26, 27).”

The following references (#26 and 27), cited in the newly added text above, have been included in the reference list, with other references renumbered accordingly:

K. Okubo, A. Takeuchi, R. Chaube, B. Paul-Prasanth, S. Kanda, Y. Oka, Y. Nagahama, Sex differences in aromatase gene expression in the medaka brain. J. Neuroendocrinol. 23, 412–423 (2011).

M. Nakamoto, Y. Shibata, K. Ohno, T. Usami, Y. Kamei, Y. Taniguchi, T. Todo, T. Sakamoto, G. Young, P. Swanson, K. Naruse, Y. Nagahama, Ovarian aromatase loss-of-function mutant medaka undergo ovary degeneration and partial female-to-male sex reversal after puberty. Mol. Cell. Endocrinol. 460, 104–122 (2018).

We have not assessed whether the expression of other steroidogenic enzymes is altered in cyp19a1bdeficient fish, and this may be investigated in future studies.

(I3) Related, there are documented sex differences in the brain expression of cyp19a1b especially in adulthood (Okubo et al 2011) and this study should be cited here for context.

Line 72: As stated in our previous response, we have cited Okubo et al. (2011) by adding the following sentence: “In medaka, cyp19a1b is also expressed in the gonads, but only at a level tens to hundreds of times lower than in the brain and substantially lower than that of cyp19a1a (26, 27).”

Methods

(M1) The rationale is unclear as presented for using mutagen screening for cype19a1b while using CRISPR for esr2a. Are there methodological/biochemical reasons why the authors chose to not use the same method for both?

At the time we generated the cyp19a1b knockouts, genome editing was not yet available, and the TILLING-based screening was the only method for obtaining mutants in medaka. In contrast, by the time we generated the esr2a knockouts, CRISPR/Cas9 had become available, enabling a more efficient and convenient generation of knockout lines. This is why the two knockout lines were generated using different methods.

(M2) Measurement of steroids in biological matrices is not straightforward, and it is good that the authors use multiple extraction steps (organic followed by C18 columns) before loading samples on the ELISA plates, which are notoriously sensitive. Even though these methods have been published before by this group of authors previously, the quality control and ELISA performance values (recovery, parallelism, etc.) should be presented for readers to evaluate.

Thank you for appreciating our sample purification method. Unfortunately, we have not evaluated the recovery rate or parallelism, but we recognize this a subject for future studies.

(M3) Mating behavior - E2 treated males were not co-housed with social partners for the full 24 hr before testing, but instead a few hours (?) prior to testing. The rationale for this should be spelled out explicitly.

Line 494: In response to this comment, we have added “to ensure the efficacy of E2 treatment” to the end of the sentence “The set-up was modified for E2-treated males, which were kept on E2 treatment and not introduced to the test tanks until the day of testing.”

(M4) The E2 treatment is listed as 1ng/ml vs. vehicle (ethanol). Is the E2 dissolved in 100% ethanol for administration to the tank water? Clarification is needed.

Line 517: As the reviewer correctly assumed, E2 was first dissolved in 100% ethanol before being added to the tank water. To provide this information and address reviewer #1’s minor comment 5, we have revised “males were treated with 1 ng/ml of E2 (Fujifilm Wako Pure Chemical, Osaka, Japan) or vehicle (ethanol) alone by immersion in water for 4 days” to “males were treated with 1 ng/ml of E2 (Fujifilm Wako Pure Chemical, Osaka, Japan), which was first dissolved in 100% ethanol (vehicle), or with the vehicle alone by immersion in water for 4 days, with daily water changes to maintain the nominal concentration.”

(M5) The authors exclude fish from the analysis of courtship display behavior for those individuals that spawned immediately at the start of the testing (and therefore it was impossible to register courtship display behaviors). How often did fish in the various treatment groups exhibit this "fast spawning" behavior? Was the occurrence rate different by treatment group? It is unlikely that these omissions from the data set drove large-scale patterns, but an indication of how often this occurred would be reassuring.

Line 627: In response to this comment, we have included the following details: “Specifically, 7/18 cyp19a1b^+/+, 11/18 cyp19a1b<sup+/−</sup>, and 6/18 cyp19a1b^−/− males were excluded in Fig. 1D; 6/10 cyp19a1b+/+, 3/10 cyp19a1b+/−, and 6/10 cyp19a1b^−/− females were excluded in Fig. 6B; 2/23 esr1+/+ and 5/24 esr1−/− males were excluded in Fig. S7; 2/24 esr2a+/+ and 3/23 esr2a^−/− males were excluded in Fig. S8A; 0/23 esr2a+/+ and 0/23 esr2a^−/− males were excluded in Fig. S8B.” These data indicate that the proportion of excluded males is nearly constant within each trial and is independent of the genotype of the focal fish.

Results

(R1) It is striking to see the genetic-'dose' dependent suppression of brain E2 content by heterozygous and homozygous cyp19a1b deficiency, indicating that, as the authors point out, the majority of E2 in the male medaka brain (and 1/2 in the female brain) have a brain-derived origin. It is important also for the interpretation that there are large compensatory increases in brain levels of androgens, when E2 levels drop in the cyp19a1b mutant homozygotes. This latter point should receive more attention.

Also, there are large increases in peripheral androgen levels in the homozygote mutants for cyp19a1b in both males and females. This indicates a peripheral effect in addition to the clear brain knockdown of E2 synthesis. These nuances need to be addressed.

In response to this comment, we have revised the Results section as follows:

Line 91: “, indicating a dosage effect of cyp19a1b mutation” has been added to the end of the sentence “In males, brain E2 in heterozygotes (cyp19a1b^+/−) was also reduced to 45% of the level in wild-type siblings (P = 0.0284) (Fig. 1A).”

Line 94: To draw more attention to the increase in brain androgen levels caused by cyp19a1b deficiency, “Brain levels of testosterone” has been modified to “Strikingly, brain levels of testosterone.”

Line 100: “Their peripheral 11KT levels also increased 3.7- and 1.8-fold, respectively (P = 0.0789, males; P = 0.0118, females) (Fig. S1, C and D)” has been modified and now reads “In addition, peripheral 11KT levels in cyp19a1b^−/− males and females increased 3.7- and 1.8-fold, respectively (P = 0.0789, males; P = 0.0118, females) (Fig. S1, C and D), indicating peripheral influence in addition to central effects.”

(R2) The interpretation on page 4 that cyp19a1b deficient males are 'less motivated' to mate is premature, given the behavioral measures used in this study. There are several competing explanations for these findings (e.g., alterations in motivation, sensory discrimination, preference, etc.) that could be followed up in future work, but the current results are not able to distinguish among these possibilities.

Line 112: We agree that the possibility of altered cognition or sexual preference cannot be dismissed. To incorporate this perspective, we have revised the text “, suggesting that they are less motivated to mate” to “These results suggest that they are less motivated to mate, though an alternative interpretation that their cognition or sexual preference may be altered cannot be dismissed.”

(R3) On page 5, the authors present that peripheral E2 manipulation (delivery to the fish tank) restores courtship behavior in males, and then go on to erroneously conclude that this demonstrates "that reduced E2 in the brain was the primary cause of the mating defects, indicating a pivotal role of neuroestrogens in male mating behavior." Because this is a peripheral E2 treatment, there can be manifold effects on gonadal physiology or other endocrine events that can have indirect effects on the brain and behavior. Without manipulation of E2 directly to the brain to 'rescue' the cyp19a1b deficiency, the authors cannot conclude that these effects are directly on the central nervous system. Tellingly, the tank E2 treatment did not rescue aggressive behavior, suggestive of the potential for indirect effects.

Line 155: As detailed in Response to reviewer #2’s specific comment 1, we have revised the text from “These results demonstrated that reduced E2 in the brain was the primary cause of the mating defects, indicating a pivotal role of neuroestrogens in male mating behavior. In contrast” to “These results suggest that reduced E2 in the brain is the primary cause of the mating defects, highlighting a pivotal role of brain-derived estrogens in male mating behavior. However, caution is warranted, as an indirect peripheral effect of bath-immersed E2 on behavior cannot be ruled out, although this is unlikely given the comparable peripheral E2 levels in cyp19a1b-deficient and wild-type males. In contrast to mating.”

(R4) The downregulation of androgen-dependent gene expression (vasotocin in pNVT and galanin in pPMp) in the cyp19a1b deficient males (Figure 3) could be due to exceedingly high levels of brain androgens in the cyp19a1b deficient males. The best way to test the idea that estrogens can restore the expression to be more wild-type directly (like what is happening for ara and arb) is to look at these same markers (vasotocin and galanin) in these same brain areas in the brains of E2-treated males. The authors should have these brains from Figure 2. Unless I missed something, those experiments were not performed/reported here. It is clear that the ara and arb receptors have EREs and are 'rescued' by E2 treatment, but in principle, there could be indirect actions for reasons stated above for the behavior due to the peripheral E2 tank application.

Thank you for your insightful comment. We agree that the current results cannot exclude the possibility that excessive androgen levels caused the downregulation of vt and gal. However, our previous studies showed that excessive 11KT administration to gonadectomized males and females increased the expression of these genes to levels comparable to wild-type males (Yamashita et al., 2020, eLife, 9:e59470; Kawabata-Sakata et al., 2024, Mol Cell Endocrinol 580:112101), making this scenario unlikely. That said, testing whether estrogen treatment restores vt and gal expression in cyp19a1bdeficient males would be informative, and we see this as an important direction for future research.

Discussion

(D1) The authors need to clarify whether EREs are found in other vertebrate AR introns, or is this unique to the teleost genome duplication?

We have identified multiple ERE-like sequences within intron 1 of the mouse AR gene. However, sequence data alone do not provide sufficient evidence of their functionality, rendering this information of limited relevance. Therefore, we have chosen not to include this discussion in the current paper.

Reviewer #3 (Recommendations For The Authors):

(1) The authors are strongly encouraged to report information regarding the effect of Cyp19a1b deletion on the brain content of aromatase protein (ideally both isoforms investigated separately) as the two isoforms are mostly but not completely brain vs gonad specific. The analysis of other tissues would also strengthen the characterization of this model.

We agree that measuring aromatase protein levels in the brain of our fish would be valuable for confirming the loss of cyp19a1b function. However, as no suitable method is currently available, this issue will need to be addressed in future studies. While this constitutes indirect evidence, the observed reduction in brain E2 levels, with no change in peripheral E2 levels, in cyp19a1b-deficient fish strongly suggests the loss of cyp19a1b function, as noted in Response to reviewer #3’s comment 1 on weaknesses.

(2) As presented, this study reads as niche work. A better description of the behavior and reproductive significance of the different aspects of the behavioral sequence would allow a better understanding of the results and would thus allow the non-specialist to appreciate the significance of the observations.

Line 103: In response to this comment and Reviewer #3’s comment 2 on weaknesses, we have revised the sentence from “The mating behavior of medaka follows a stereotypical pattern, wherein a series of followings, courtship displays, and wrappings by the male leads to spawning” to “The mating behavior of medaka follows a stereotypical sequence. It begins with the male approaching and closely following the female (following). The male then performs a courtship display, rapidly swimming in a circular pattern in front of the female. If the female is receptive, the male grasps her with his fins (wrapping), culminating in the simultaneous release of eggs and sperm (spawning)” in order to provide a more detailed description of medaka mating behavior.

(3) The data regarding female behavior are limited and incomplete. It is suggested to keep this for another manuscript unless data on the behavior of the female herself is added. Indeed, analyzing female's behavior from the male's perspective complicates the interpretation of the results while a description of what the females do would provide valuable and interpretable information.

We thank the reviewer for this thoughtful suggestion and agree that the data and discussion for females are less extensive than for males. However, we have previously elucidated the mechanism by which estrogen/Esr2b signaling promotes female mating behavior (Nishiike et al., 2021). Accordingly, it follows that the new insights into female behavior gained from the cyp19a1b knockout model are more limited than those for males. Nevertheless, when combined with our prior findings, the female data in this study offer valuable insights, and the overall mechanism through which estrogens promote female mating behavior is becoming clearer. Therefore, we do not consider the female data in this study to be incomplete or merely supplementary.

(4) In Figure 2, the validity to run multiple T-tests rather than a two-way ANOVA comparing TRT and genotype is questionable. Moreover, why are the absolute values in CTL higher than in the initial experiment comparing genotypes for ara in PPa, pPPp, and NVT as well as for arb in aPPp. More importantly, these graphs do not seem to reproduce the genotype effects for ara in pPPp and NVT and for arb in aPPp.

The data in Figures 2J and 2K were analyzed with an exclusive focus on the difference between vehicletreated and E2-treated males, without considering genotype differences. Therefore, the use of T-tests for significance testing is appropriate.

As the reviewer noted, the overall ara expression area is larger in Figure 2J than in Figure 2F. However, as detailed in Response to reviewer #3’s comment 8 on weaknesses, the relative area ratios of ara expression among brain nuclei are consistent between the two figures, indicating the reproducibility of the results. Thus, we consider this difference unlikely to affect the conclusions of this study.

Additionally, the differences in ara expression in pPPp and arb expression in aPPp between wild-type and cyp19a1b-deficient males appear smaller in Figures 2J and 2K compared to Figures 2F and 2H. This is likely due to the smaller sample size used in the experiments for Figures 2J and 2K, which makes the differences less distinct. However, since the same genotype-dependent trends are observed in both sets of figures, the conclusion that ara and arb expression is reduced in cyp19a1b-deficient male brains remains valid.

(5) More information is required regarding the analysis of single ISH - How was the positive signal selected from the background in the single ISH analyses? How was this measure standardized across animals? How many sections were imaged per region? Do the values represent unilateral or bilateral analysis?

Line 540: Following this comment, we have provided additional details on the single ISH method in the manuscript. Specifically, “, and the total area of signal in each brain nucleus was calculated using Olyvia software (Olympus)” has been revised to “The total area of signal across all relevant sections, including both hemispheres, was calculated for each brain nucleus using Olyvia software (Olympus). Images were converted to a 256-level intensity scale, and pixels with intensities from 161 to 256 were considered signals. All sections used for comparison were processed in the same batch, without corrections between samples.”

(6) More information should be provided in the methods regarding the image analysis of double ISH. In particular, what were the criteria to consider a cell as labeled are not clear. This is not clear either from the representative images.

Line 596: To provide additional details on the single ISH method in the manuscript, we have added the following sentence: “Cells were identified as coexpressing the two genes when Alexa Fluor 555 and fluorescein signals were clearly observed in the cytoplasm surrounding DAPI-stained nuclei, with intensities markedly stronger than the background noise.”

(7) There is no description of the in silico analyses run on ESR2a in the methods.

The method for identifying estrogen-responsive element-like sequences in the esr2a locus is described in line 549: “Each nucleotide sequence of the 5′-flanking region of ara and arb was retrieved from the Ensembl medaka genome assembly and analyzed for potential canonical ERE-like sequences using Jaspar (version 5.0_alpha) and Match (public version 1.0) with default settings.”

However, the method for domain identification in Esr2a was not described. Therefore, we have added the following text in line 469: “The DNA- and ligand-binding domains of medaka Esr2a were identified by sequence alignment with yellow perch (Perca flavescens) Esr2a, for which these domain locations have been reported (58).”

The following reference (#58), cited in the newly added text above, have been included in the reference: S. G. Lynn, W. J. Birge, B. S. Shepherd, Molecular characterization and sex-specific tissue expression of estrogen receptor α (esr1), estrogen receptor βa (esr2a) and ovarian aromatase (cyp19a1a) in yellow perch (Perca flavescens). Comp. Biochem. Physiol. B Biochem. Mol. Biol. 149, 126–147 (2008).

(8) Information about the validation steps of the EIA that were carried out as well as the specificity of the antibody the steroids and the extraction efficacy should be provided.

We have not directly validated the applicability of the EIA kit, but its extensive use in medaka suggests that it us unlikely to pose any issues (e.g., Ussery et al., 2018, Aquat Toxicol, 205:58–65; Lee et al., 2019, Ecotoxicol Environ Saf, 173:174–181; Kayo et al., 2020, Gen Comp Endocrinol, 285:113272; Fischer et al., 2021, Aquat Toxicol, 236:105873; Royan et al., 2023, Endocrinology, 164:bqad030).

The specificity (cross-reactivity) of the antibodies is detailed as follows.

(1) Estradiol ELISA kits: estradiol, 100%; estrone, 1.38%; estriol, 1.0%; 5α-dihydrotestosterone, 0.04%; androstenediol, 0.03%; testosterone, 0.03%; aldosterone, <0.01%; cortisol, <0.01%; progesterone, <0.01%.

(2) Testosterone ELISA kits: testosterone, 100%; 5α-dihydrotestosterone, 27.4%; androstenedione, 3.7%; 11-ketotestosterone, 2.2%; androstenediol, 0.51%; progesterone, 0.14%; androsterone, 0.05%; estradiol, <0.01%.

(3) 11-Keto Testosterone ELISA kits: 11-ketotestosterone, 100%; adrenosterone, 2.9%; testosterone, <0.01%.

As this information is publicly available on the manufacturer’s website, we deemed it unnecessary to include it in the manuscript.

Unfortunately, we have not evaluated the extraction efficacy of the samples, but we recognize this a subject for future studies.

(9) I wonder whether the evaluation of the impact of the mutation by comparing the behavior of a group of wild-type males to a group of mutated males is the most appropriate. Justifying this approach against testing the behavior of one mutated male facing one or several wild-type males would be appreciated.

We agree that the resident-intruder test, in which a single focal resident is confronted with one or more stimulus intruders, is the most commonly used method for assessing aggression. However, medaka form shoals and lack strong territoriality, and even slight dominance differences between the resident and the intruder can increase variability in the results, compromising data consistency. Therefore, in this study, we adopted an alternative approach: placing four unfamiliar males together in a tank and quantifying aggressive interactions in total. This method allows for the assessment of aggression regardless of territorial tendencies, making it more appropriate for our investigation.

(10) Lines 329-331: this sentence should be rephrased as it contributes to the confusion between sexual differentiation and activation of circuits. The restoration of sexual behavior by adult estrogen treatment pleads in favor of an activational role of neuro-estrogens on behavior rather than an organizational role. Therefore, referring to sexual differentiation is misleading, even more so that the study never compares sexes.

As detailed in Response to reviewer #3’s comment 9 on weaknesses, we consider that all factors that cause sex differences, including the transient effects of adult steroids, need to be incorporated into a theory of sexual differentiation. In teleosts, since steroids during early development have little effect and sexual differentiation primarily relies on steroid action in adulthood, our discussion on brain sexual differentiation remains valid, including the statement in line 347: “This variation among species may represent the activation of neuroestrogen synthesis at life stages critical for sexual differentiation of behavior that are unique to each species.”

(11) Lines 384-386: I may have missed something but I do not see data supporting the notion that neuroestrogens may function upstream of PGF2a signaling to mediate female receptivity.

Line 403: We acknowledge that our explanation was insufficient and apologize for any confusion. To clarify this point, “Given that estrogen/Esr2b signaling feminizes the neural substrates that mediate mating behavior, while PGF2α signaling triggers female sexual receptivity,” has been added before the sentence “The present finding provides a likely explanation for this apparent contradiction, namely, that neuroestrogens, rather than or in addition to ovarian-derived circulating estrogens, may function upstream of PGF2α signaling to mediate female receptivity.”

Additional alteration

Reference list (line 682): a preprint article has now been published in a peer-reviewed journal, and the information has been updated accordingly as follows: “bioRxiv doi: 10.1101/2024.01.10.574747 (2024)” to “Proc. Natl. Acad. Sci. U.S.A. 121, e2316459121 (2024).”

Author response:

eLife Assessment

Alignment and sequencing errors are a major concern in molecular evolution, and this valuable study represents a welcome improvement for genome-wide scans of positive selection. This new method seems to perform well and is generally convincing, although the evidence could be made more direct and more complete through additional simulations to determine the extent to which alignment errors are being properly captured.

We thank the editors for their positive assessment and for highlighting the core strength and a key area for improvement. The main request (also echoed by both reviewers) is for us to conduct additional simulation studies where true alignment errors are known and assess the performance of BUSTED-E. We plan to conduct several simulations (on the order of 100,000 individual alignments in total) in response to that request, with the caveat that we are not aware of any tools that simulate realistic alignment errors, so these simulations are likely only a pale reflection of biological reality.

(1) Ad hoc small local edits of alignments similar to what was implemented in the HMMCleaner paper. These local edits would include operations like replacement of codons or small stretches of sequences with random data, local transposition, inversion.

(a) Using parametrically simulated alignments (under BUSTED models).

(b) Using empirical alignments.

(2) Simulations under model misspecification, specifically to address the point of reviewer 2. For example, we would simulate under models that allow for multi-nucleotide substitutions, and then apply error filtering under models which do not.

We will also run several new large-scale screens of existing alignments, to directly and indirectly address the reviewers comments. These will include

(a) A drosophila dataset (from https://academic.oup.com/mbe/article/42/4/msaf068/8092905)

(b) Current Selectome data (https://selectome.org/), both filtered and unfiltered. Here the filtering procedure refers to what Selectome does to obtain what its authors think are high quality alignments.

(c) Current OrthoMam data, both (https://orthomam.mbb.cnrs.fr/) filtered and unfiltered. Here the filtering procedure refers to what OrthoMam does to obtain what its authors think are high quality alignments.

Reviewer #1:

We are grateful to Reviewer #1 for their positive and encouraging review. We are pleased they found our analyses convincing and recognized BUSTED-E as a "simple, efficient, and computationally fast" improvement for evolutionary scans.

Strengths:

As a side note, I found it particularly interesting how the authors tested the statistical support for the new method compared to the simpler version without the error class. In many cases, the simpler model could not be statistically rejected in favor of the more complex model, despite producing biologically incorrect results in terms of parameter inference. This highlights a broader issue in molecular evolution and phylogenomics, where model selection often relies too heavily on statistical tests, potentially at the expense of biological realism.

We agree that this observation touches upon a critical issue in phylogenomics. A statistically "good" fit does not always equate to a biologically accurate model. We believe our work serves as a useful case study in this regard. We will add discussion of the importance of considering biological realism alongside statistical adequacy in model selection.

Weaknesses:

Regarding the structure of the manuscript, the text could be clearer and more precise.

We appreciate this feedback. We will perform a thorough revision of the entire manuscript to improve its clarity, flow, and precision. We will focus on streamlining the language and ensuring that our methodological descriptions and results are as unambiguous as possible.

Clear, practical recommendations for users could also be provided in the Results section.

To make our method more accessible and its application more straightforward, we will add a new section that provides clear, practical recommendations for users. This includes guidance on when to apply BUSTED-E, how to interpret its output, and best practices for distinguishing potential errors from strong selection.

Additionally, the simulation analyses could be further developed to include scenarios with both alignment errors and positive selection, in order to better assess the method's performance.

Additional simulations will be conducted (see above)

Finally, the model is evaluated only in the context of site models, whereas the widely used branch-site model is mentioned as possible but not assessed.

BUSTED class models support branch-site variation in dN/dS, so technically all of our analyses are already branch-site. However, we interpret the reviewer’s comment as describing use cases when a method is used to test for selection on a subset of tree branches (as opposed to the entire tree). BUSTED-E already supports this ability, and we will add a section in the manuscript describing how this type of testing can be done, including examples. However, we do not plan to conduct additional extensive data analyses or simulations, as this would probably bloat the manuscript too much.

Reviewer #2:

We thank Reviewer #2 for their detailed and thought-provoking comments, and for their enthusiasm for modeling alignment issues directly within the codon modeling framework. The criticisms raised are challenging and we will work on improving the justification, testing, and contextualization of our method.

Weaknesses:

The definition of alignment error by a very large ω is not justified anywhere in the paper... I would suggest characterising a more specific error model. E.g., radical amino-acid "changes" clustered close together in the sequence, proximity to gaps in the alignment, correlation of apparent ω with genome quality... Also concerning this high ω, how sensitive is its detection to computational convergence issues?

This is a fundamental point that we are grateful to have the opportunity to clarify. Our intention with the high ω category is not to provide a mechanistic or biological definition of an alignment error. Rather, its purpose is to serve as a statistical "sink" for codons exhibiting patterns of divergence so extreme that they are unlikely to have resulted from a typical selective process. It is phenomenological and ad hoc. The reviewer makes sensible suggestions for other ad hoc/empirical approaches to alignment quality filtering, but most of those have already been implemented in existing (excellent) alignment filtering tools. BUSTED-E is never meant to replace them, but rather to catch what is left over. Importantly, error detection is not even the primary goal of BUSTED-E; errors are treated as a statistical nuisance. With all due respect, all of the reviewers suggestions are similarly ad hoc -- there is no rigorous quantitative justification for any of them, but they are all sensible and plausible, and usually work in practice.

Computational convergence issues can never be fully dismissed, but we do not consider this to be a major issue. Our approach already pays careful attention to proper initialization, does convergence checks, considers multiple initial starting points. We also don’t need to estimate large ω with any degree of precision, it just needs to be “large”.

The authors should clarify the relation between the "primary filter for gross or large-scale errors" and the "secondary filter" (this method). Which sources of error are expected to be captured by the two scales of filters?

We will add discussion and examples to explicitly define the distinct and complementary roles of these filtering stages.

The benchmarking of the method could be improved both for real and simulated data... I suggest comparing results with e.g. Drosophila genomes... For simulations, the authors should present simulations with or without alignment errors... and with or without positive selection... I also recommend simulating under more complex models, such as multinucleotide mutations or strong GC bias...

We will add more simulations as suggested (see above). We will also analyze a drosophila gene alignment from previously published papers.

It would be interesting to compare to results from the widely used filtering tool GUIDANCE, as well as to the Selectome database pipeline... Moreover, the inconsistency between BUSTED-E and HMMCleaner, and BMGE is worrying and should be better explained.

Some of the alignments we have analyzed had already been filtered by GUIDANCE. We’ll also run the Selectome data through BUSTED-E: both filtered and unfiltered. We consider it beyond the scope of this manuscript to conduct detailed filtering pipeline instrumentation and side-by-side comparison.

For a new method such as this, I would like to see p-value distributions and q-q plots, to verify how unbiased the method is, and how well the chi-2 distribution captures the statistical value.

We will report these values for new null simulations.

I disagree with the motivation expressed at the beginning of the Discussion... Our goal should not be to find a few impressive results, but to measure accurately natural selection, whether it is frequent or rare.

That’s a philosophical point; at some level, given enough time, every single gene likely experiences some positive selection at some point in the evolutionary past. The practically important question is how to improve the sensitivity of the methods while controlling for ubiquitous noise. We do agree with the sentiment that the ultimate goal is to “measure accurately natural selection, whether it is frequent or rare”. However, we also must be pragmatic about what is possible with dN/dS methods on available genomic data.

Author response:

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

We thank all reviewers for the highly detailed review and the time and effort which has been invested in this review. It is clear from the reviews that we’ve had the privilege to have our work extensively and thoroughly checked by knowledgeable experts, for which we are very grateful. We have read their perspectives, questions and suggested improvements with great interest. We have reflected on the public review in detail and have included detailed responses below. First, we would like to respond to four main issues pointed out by the editor and reviewers:

(1) Lack of yield data in the manuscript: Yield data has been collected in most of the sites and years of our study, and these have already been published and cited in our manuscript. In the appendix of our manuscript, we included a table with yield data for the sites and years in which the beetle diversity was studied. These data show that strip cropping does not cause a systematic yield reduction.

(2) Sampling design clarification: Our paper combines data from trials conducted at different locations and years. On the one hand this allows an analysis of a comprehensive dataset, but on the other hand in some cases this resulted in variations in how data were collected or processed (e.g. taxonomic level of species identification). We have added more details to the sections on sampling design and data analysis to increase clarity and transparency.

(3) Additional data analysis: In the revised manuscript we present an analysis on the responses of abundances of the 12 most common ground beetle genera to strip cropping. This gives better insight in the variation of responses among ground beetle taxa.

(4) Restrict findings to our system: We nuanced our findings further and focused more on the implications of our data on ground beetle communities, rather than on agrobiodiversity in a broader sense.

Below we also respond to the editor and reviewers in more detail.

Reviewing Editor Comments:

(1) You only have analyzed ground beetle diversity, it would be important to add data on crop yields, which certainly must be available (note that in normal intercropping these would likely be enhanced as well).

Most yield data have been published in three previous papers, which we already cited or cite now (one was not yet published at the time of submission). Our argumentation is based on these studies. We had also already included a table in the appendix that showed the yield data that relates specifically to our locations and years of measurement. The finding that strip cropping does not majorly affect yield is based on these findings. We revised the title of our manuscript to remove the explicit focus on yield.

(2) Considering the heterogeneous data involving different experiments it is particularly important to describe the sampling design in detail and explain how various hierarchical levels were accounted for in the analysis.

We agree that some important details to our analysis were not described in sufficient detail. Especially reviewer 2 pointed out several relevant points that we did account for in our analyses, but which were not clear from the text in the methods section. We are convinced that our data analyses are robust and that our conclusions are supported by the data. We revised the methods section to make our approach clearer and more transparent.

(3) In addition to relative changes in richness and density of ground beetles you should also present the data from which these have been derived. Furthermore, you could also analyze and interpret the response of the different individual taxa to strip cropping.

With our heterogeneous dataset it was quite complicated to show overall patterns of absolute changes in ground beetle abundance and richness, especially for the field-level analyses. As the sampling design was not always the same and occasionally samples were missing, the number of year series that made up a datapoint were different among locations and years. However, we always made sure that for the comparison of a paired monoculture and strip cropping field, the number of year series was always made equal through rarefaction. That is, the number of ground beetle(s) (species) are always expressed as the number per 2 to 6 samples. Therefore, we prefer to stick to relative changes as we are convinced that this gives a fairer representation of our complex dataset.

We agree with the second point that both the editor and several reviewers pointed out. The indicator species analyses that we used were biased by rare species, and we now omit this analysis. Instead, we included a GLM analysis on the responses of abundances of the 12 most common ground beetle genera to strip cropping. We chose for genera here (and not species) as we could then include all locations and years within the analyses, and in most cases a genus was dominated by a single species (but notable exceptions were Amara and Harpalus, which were often made up of several species). We illustrate these analyses still in a similar fashion as we did for the indicator species analysis.

(4) Keep to your findings and don't overstate them but try to better connect them to basic ecological hypotheses potentially explaining them.

After careful consideration of the important points that reviewers point out, we decided to nuance our reasoning about biodiversity conservation along two key lines: (1) the extent to which ground beetles can be indicators of wider biodiversity changes; and (2) our findings that are not as straightforward positive as our narrative suggests. We still believe that strip cropping contributes positively to carabid communities, and have carefully checked the text to avoid overstatements.

Reviewer #1 (Public review):

Summary:

This study demonstrates that strip cropping enhances the taxonomic diversity of ground beetles across organically-managed crop systems in the Netherlands. In particular, strip cropping supported 15% more ground beetle species and 30% more individuals compared to monocultures.

Strengths:

A well-written study with well-analyzed data of a complex design. The data could have been analyzed differently e.g. by not pooling samples, but there are pros and cons for each type of analysis and I am convinced this will not affect the main findings. A strong point is that data were collected for 4 years. This is especially strong as most data on biodiversity in cropping systems are only collected for one or two seasons. Another strong point is that several crops were included.

We thank reviewer 1 for their kind words and agree with this strength of the paper. The paper combines data from trials conducted at different locations and years. On the one hand this allows an analysis of a comprehensive dataset, but on the other hand in some cases there were slight variations in how data were collected or processed (e.g. taxonomic level of species identification).

Weaknesses:

This study focused on the biodiversity of ground beetles and did not examine crop productivity. Therefore, I disagree with the claim that this study demonstrates biodiversity enhancement without compromising yield. The authors should present results on yield or, at the very least, provide a stronger justification for this statement.

We acknowledge that we indeed did not formally analyze yield in our study, but we have good reason for this. The claim that strip cropping does not compromise yield comes from several extensive studies (Juventia & van Apeldoorn, 2024; Ditzler et al., 2023; Carillo-Reche et al., 2023) that were conducted in nearly all the sites and years that we included in our study. We chose not to include formal analyses of productivity for two key reasons: (1) a yield analysis would duplicate already published analyses, and (2) we prefer to focus more on the ecology of ground beetles and the effect of strip cropping on biodiversity, rather than diverging our focus also towards crop productivity. Nevertheless, we have shown the results on yield in Table S6 and refer extensively to the studies that have previously analyzed this data (line 203-207, 217-221).

Reviwer #1 (Recommendations for the authors):

This is a well-written study on the effects of strip cropping on ground-beetle diversity. As stated above the study is well analyzed, presented, and written but you should not pretend that you analyzed yield e.g. lines 25-27 "We show that strip cropping...enhance ground beetle biodiversity without incurring major yield loss.

We understand the confusion caused by this sentence, and it was never our intention to give the impression that we analyzed yield losses. These findings were based on previous research by ourselves and colleagues, and we have now changed the sentence to reflect this (line 25-27).

I think you assume that yield does not differ between strip cropping and monoculture. I am not sure this is correct as one crop might attract pests or predators spilling over to the other crop. I am also not sure if the sowing and harvest of the crop will come with the same costs. So if you assume this, you should only do it in the main manuscript and not the abstract, to justify this better.

With three peer-reviewed papers on the same fields as we studied, we can convincingly state that strip cropping in organic agriculture generally does not result in major yield loss, although exceptions exist, which we refer to in the discussion.

In the introduction lines 28-43, you refer to insect biomass decline. I wonder if you would like to add the study of Loboda et al. 2017 in Ecography. It seems not fitting as it is from the Artic but also the other studies you cite are not only coming from agricultural landscapes and this study is from the same time as the Hallmann et al. 2017 study and shows a decline in flies of 80%

We have removed the sentence that this comment refers to, to streamline the introduction more.

Lines 50-51. You only have one citation for biodiversity strategies in agricultural systems. I suggest citing Mupepele et al. 2021 in TREE. This study refers to management but also the policies and societal pressures behind it.

We have added this citation and a recent paper by Cozim-Melges et al. (2024) here (line 49-52).

In the methods, I am missing a section on species identifications. This would help to understand why you used "taxonomic richness".

Thanks for pointing this out. We have now included a new section on ground beetle identification (line 304-309 in methods).

Figure 1 is great and I like that you separated the field and crop-level data, although there is no statistical power for the crop-specific data. I personally would move k to the supplements. It is very detailed and small and therefore hard to read

We chose to keep figure 1k, as in our view it gives a good impression of the scale of the experiment, the number of crops included and the absolute numbers of caught species.

Reviewer #2 (Public review):

Summary:

The authors aimed to investigate the effects of organic strip cropping on carabid richness and density as well as on crop yields. They find on average higher carabid richness and density in strip cropping and organic farming, but not in all cases.

We did not intend to investigate the effect of strip cropping on crop yields, but rather place our work in the framework of earlier studies that already studied yield. All the monocultures and strip cropping fields were organic farms. Our findings thus compare crop diversity effects within the context of organic farming.

Strengths:

Based on highly resolved species-level carabid data, the authors present estimates for many different crop types, some of them rarely studied, at the same time. The authors did a great job investigating different aspects of the assemblages (although some questions remain concerning the analyses) and they present their results in a visually pleasing and intuitive way.

We appreciate the kind words of reviewer 2 and their acknowledgement of the extensiveness of our dataset. In our opinion, the inclusion of many different crops is indeed a strength, rarely seen in similar studies; and we are happy that the figures are appreciated.

Weaknesses:

The authors used data from four different strip cropping experiments and there is no real replication in space as all of these differed in many aspects (different crops, different areas between years, different combinations, design of the strip cropping (orientation and width), sampling effort and sample sizes of beetles (differing more than 35 fold between sites; L 100f); for more differences see L 237ff). The reader gets the impression that the authors stitched data from various places together that were not made to fit together. This may not be a problem per se but it surely limits the strength of the data as results for various crops may only be based on small samples from one or two sites (it is generally unclear how many samples were used for each crop/crop combination).

The paper indeed combines data from trials conducted at different locations and years. On the one hand this allows an analysis of a comprehensive dataset, but on the other hand in some cases there were slight differences in the experimental design. At the time that we did our research, there were only a handful of farmers that were employing strip cropping within the Netherlands, which greatly reduced the number of fields for our study. Therefore, we worked in the sites that were available and studied as many crops on these sites. Since there was variation in the crops grown in the sites, for some crops we have limited replication. In the revision we have explained this more clearly (line 297-300).

One of my major concerns is that it is completely unclear where carabids were collected. As some strips were 3m wide, some others were 6m and the monoculture plots large, it can be expected that carabids were collected at different distances from the plot edge. This alone, however, was conclusively shown to affect carabid assemblages dramatically and could easily outweigh the differences shown here if not accounted for in the models (see e.g. Boetzl et al. (2024) or Knapp et al. (2019) among many other studies on within field-distributions of carabids).

Point well taken. Samples were always taken at least 10 meters into the field, and always in the middle of the strip. This would indeed mean that there is a small difference between the 3- and 6m wide strips regarding distance from another strip, but this was then only a difference of 1.5 to 3 meters from the edge. A difference that, based on our own extensive experience with ground beetle communities, will not have a large impact on the findings of ground beetles. The distance from field/plot edges was similar between monocultures and strip cropped fields. We present a more detailed description of the sampling design in the methods of the revised manuscript (line 294-297).

The authors hint at a related but somewhat different problem in L 137ff - carabid assemblages sampled in strips were sampled in closer proximity to each other than assemblages in monoculture fields which is very likely a problem. The authors did not check whether their results are spatially autocorrelated and this shortcoming is hard to account for as it would have required a much bigger, spatially replicated design in which distances are maintained from the beginning. This limitation needs to be stated more clearly in the manuscript.

To be clear, this limitation relates to the comparison that we did for the community compositions of ground beetles in two crops either in strip cropping or monocultures. In this case, it was impossible to avoid potential autocorrelation due to our field design. We also acknowledge this limitation in the results section (line 130-133). However, for our other analyses we corrected for spatial autocorrelation by including variables per location, year and crop. This grouped samples that were spatially autocorrelated. Therefore, we don’t see this as a discrepancy of our other analyses.

Similarly, we know that carabid richness and density depend strongly on crop type (see e.g. Toivonen et al. (2022)) which could have biased results if the design is not balanced (this information is missing but it seems to be the case, see e.g. Celeriac in Almere in 2022).

We agree and acknowledge that crop type can influence carabid richness and density, which is why we have included variables to account for differences caused by crops. However, we did not observe consistent differences between crops in how strip cropping affected ground beetle richness and density. Therefore, we don’t think that crop types would have influenced our conclusions on the overall effect of strip cropping.

A more basic problem is that the reader neither learns where traps were located, how missing traps were treated for analyses how many samples there were per crop or crop combination (in a simple way, not through Table S7 - there has to have been a logic in each of these field trials) or why there are differences in the number of samples from the same location and year (see Table S7). This information needs to be added to the methods section.

Point well taken. We have clarified this further in the revised manuscript (line 294-301, 318-322). As we combined data from several experimental designs that originally had slightly different research questions, this in part caused differences between numbers of rounds or samples per crop, location or year.

As carabid assemblages undergo rapid phenological changes across the year, assemblages that are collected at different phenological points within and across years cannot easily be compared. The authors would need to standardize for this and make sure that the assemblages they analyze are comparable prior to analyses. Otherwise, I see the possibility that the reported differences might simply be biased by phenology.

We agree and we dealt with this issue by using year series instead of using individual samples of different rounds. This approach allowed us to get a good impression of the entire ground beetle community across seasons. For our analyses we had the choice to only include data from sampling rounds that were conducted at the same time, or to include all available data. We chose to analyze all data, and made sure that the number of samples between strip cropping and monoculture fields per location, year and crop was always the same by pooling and rarefaction.

Surrounding landscape structure is known to affect carabid richness and density and could thus also bias observed differences between treatments at the same locations (lower overall richness => lower differences between treatments). Landscape structure has not been taken into account in any way.

We did not include landscape structure as there are only 4 sites, which does not allow a meaningful analysis of potential effects landscape structure. Studying how landscape interacts with strip cropping to influence insect biodiversity would require at least, say 15 to 20 sites, which was not feasible for this study. However, such an analysis may be possible in an ongoing project (CropMix) which includes many farms that work with strip cropping.

In the statistical analyses, it is unclear whether the authors used estimated marginal means (as they should) - this needs to be clarified.

In the revised manuscript we further clarified this point (line 365-366, 373-374).

In addition, and as mentioned by Dr. Rasmann in the previous round (comment 1), the manuscript, in its current form, still suffers from simplified generalizations that 'oversell' the impact of the study and should be avoided. The authors restricted their analyses to ground beetles and based their conclusions on a design with many 'heterogeneities' - they should not draw conclusions for farmland biodiversity but stick to their system and report what they found. Although I understand the authors have previously stated that this is 'not practically feasible', the reason for this comment is simply to say that the authors should not oversell their findings.

In the revised manuscript, we nuanced our findings by explaining that strip cropping is a potentially useful tool to support ground beetle biodiversity in agricultural fields (line 33-35).

Reviewer #2 (Recommendations for the authors):

In addition to the points stated under 'Weaknesses' above, I provide smaller comments and recommendations:

Overall comments:

(i) The carabid images used in the figures were created by Ortwin Bleich and are copyrighted. I could not find him accredited in the acknowledgements; the figure legends simply state that the images were taken from his webpage. Was his permission obtained? This should be stated.

We have received written permission from Ortwin Bleich for using his pictures in our figures, and have accredited him for this in the acknowledgements (line 455-456).

(ii) There is a great confusion in the field concerning terminology. The authors here use intercropping and strip cropping, a specific form of intercropping, interchangeably. I advise the authors to stick to strip cropping as it is more precise and avoids confusion with other forms of intercropping.

We agree with the definitions given by reviewer 2 and had already used them as such in the text. We defined strip cropping in the first paragraph of the introduction and do not use the term “intercropping” after this definition to avoid confusion.

Comments to specific lines:

Line 19: While this is likely true, there is so far not enough compelling evidence for such a strong statement blaming agriculture. Please rephrase.

Changed the sentence to indicate more clearly that it is one of the major drivers, but that the “blame” is not solely on agriculture (line 18-19).

Line 22: Is this the case? I am aware of strip cropping being used in other countries, many of them in Europe. Why the focus on 'Dutch'?

Indeed, strip cropping is now being pioneered by farmers throughout Europe. However in the Netherlands, some farmers have been pioneering strip cropping already since 2014. We have added this information to indicate that our setting is in the Netherlands, and as in our opinion it gives a bit more context to our manuscript.

Line 24: I would argue that carabids are actually not good indicators for overall biodiversity in crop fields as they respond in a very specific way, contrasting with other taxa. It is commonly observed that carabids prefer more disturbed habitats and richness often increases with management intensity and in more agriculturally dominated landscapes - in stark contrast to other taxa like wild bees or butterflies.

We have reworded this sentence to reflect that they are not necessarily indicators of wide agricultural biodiversity, but that they do hold keystone positions within food webs in agricultural systems (line 23-25).

Line 31: This statement here is also too strong - carabids are not overall biodiversity and patterns found for carabids likely differ strongly from patterns that would be observed in other taxa. This study is on carabids and the conclusion should thus also refer to these in order to avoid such over-simplified generalizations.

We agree and have nuanced this sentence to indicate that our findings are only on ground beetles (line 33-35). However, we would like to point out that the statement that “patterns found for carabids likely differ strongly from patterns that would be observed in other taxa” assumes a disassociation between carabids and other taxa.

Line 41: I am sure the authors are aware of the various methodological shortcomings of the dataset used in Hallmann et al. (2017) which likely led to an overestimation of the actual decline. Analysing the same data, Müller et al. (2023) found that weather can explain fluctuations in biomass just as well as time. I thus advise not putting too much focus on these results here as they seem questionable.

We have removed this sentence to streamline the introduction, thus no longer mentioning the percentages given by Hallmann et al. (2017).

Line 46: Surely likely but to my knowledge this is actually remarkably hard to prove. Instead of using the IPBES report here that simply states this as a fact, it would be better to see some actual evidence referenced.

We removed IPBES as a source and changed this for Dirzo et al. (2014), a review that shows the consequences of biodiversity decline on a range of different ecosystem services and ecological functions (line 45-47).

Line 52ff: I am not sure whether this old land-sparing vs. land-sharing debate is necessary here. The authors could simply skip it and directly refer to the need of agricultural areas, the dominating land-use in many regions, to become more biodiversity-friendly. It can be linked directly to Line 61 in my opinion which would result in a more concise and arguably stronger introduction.

After reconsidering, we agree with reviewer 2 that this section was redundant and we have removed the lines on land-sparing vs land-sharing.

Line 59: Just a note here: this argument is not meaningful when talking about strip cropping in the Netherlands as there is virtually no land left that could be converted (if anything, agricultural land is lost to construction). The debate on land-use change towards agriculture is nowadays mostly focused on the tropics and the Global South.

We argue that strip cropping could play an important role as a measure that does not necessarily follow the trade-off between biodiversity and agriculture for a context beyond the Netherlands (line 52-58).

Line 69: Does this statement really need 8 references?

Line 71: ... and this one 5 additional ones?

We have removed excess references in these two lines (line 62-66).

Line 74: But also likely provides the necessary crop continuity for many crop pests - the authors should keep in mind that when practitioners read agricultural biodiversity, they predominantly think of weeds and insect pests.

We agree with reviewer 2 that agricultural biodiversity is still a controversial topic. However, as the focus in this manuscript is more on biodiversity conservation, rather than pest management, we prefer to keep this sentence as is. In other published papers and future work we focus more on the role of strip cropping for pest management.

Line 83: Consider replacing 'moments' maybe - phenological stages or development stages?

Although we understand the point of reviewer 2, we prefer to keep it at moments, as we did not focus on phenological stages and we only wanted to say that we set pitfall traps at several moments throughout the year. However, by placing the pitfall traps at several moments throughout the year, we did capture several phenological stages.

Line 86: Not only farming practices - there are also massive fluctuations between years in the same crop with the same management due to effects of the weather in the previous reproductive season. Interpreting carabid assemblage changes is therefore not straightforward.

We absolutely agree that interpreting carabid assemblage is not straightforward, but as we did not study year or crop legacy effects we chose to keep this sentence to maintain focus on our research goals.

Line 88: 'ecolocal'?

Typo, should have been ecological. Changed (line 81).

Line 90: 'As such, they are often used as indicator group for wider insect diversity in agroecosystems' - this is the third repetition of this statement and the second one in this paragraph - please remove. Having worked on carabids extensively myself, I also think that this is not the true reason - they are simply easy to collect passively.

We agree with the reviewer and have removed this sentence.

Line 141: I have doubts about the value of the ISA looking at the results. Anchomenus dorsalis is a species extremely common in cereal monoculture fields in large parts of Europe, especially in warmer and drier conditions (H. griseus was likely only returned as it is generally rare and likely only occurred in few plots that, by chance, were strip-cropped). It can hardly be considered an indicator for diverse cropping systems but it was returned as one here (which I do not doubt). This often happens with ISA in my experience as they are very sensitive to the specific context of the data they are run on. The returned species are, however, often not really useable as indicators in other contexts. I thus believe they actually have very limited value. Apart from this, we see here that both monocultures and strip cropping have their indicators, as would likely all crop types. I wonder what message we would draw from this ...

On close reconsideration, we agree with the reviewer that the ISAs might have been too sensitive to rare species that by chance occur in one of two crop configurations. To still get an idea on what happens with specific ground beetle groups, we chose to replace the ISAs with analyses on the 12 most common ground beetle genera. For this purpose we have added new sections to the methods (line 368-374) and results (line 135-143), replaced figure 2 and table S5, and updated the discussion (line 182-200).

Line 165: Carabid activity is high when carabids are more active. Carabids can be more active either when (i) there are simply more carabid individuals or /and (ii) when they are starved and need to search more for prey. More carabid activity does thus not necessarily indicate more individuals, it can indicate that there is less prey. This aspect is missing here and should be discussed. It is also not true that crop diversification always increases prey biomass - especially strip cropping has previously been shown to decrease pest densities (Alarcón-Segura et al., 2022). Of course, this is a chicken-egg problem (less pests => less carabids or more carabids => less pests ?) ... this should at least be discussed.

We have rewritten this paragraph to further discuss activity density in relation to food availability (line 175-185).

Line 178: These species are not exclusively granivorous - this speculation may be too strong here.

Line 185: true for all but C. melanocephalus - this species is usually more associated with hedgerows, forests etc.

After removing the ISA’s, we also chose to remove this paragraph and replace it with a paragraph that is linked to the analyses on the 12 most common genera (line 182-200).

Line 202: These statements are too strong for my taste - the authors should add an 'on average' here. The data show that they likely do not always enhance richness by 15 % and as the authors state, some monocultures still had higher richness and densities.

“on average” added (line 211)

Line 203: 'can lead' - the authors cannot tell based on their results if this is always true for all taxa.

Changed to “can lead” (line 213)

Line 205: What is 'diversification' here?

This concerns measures like hedgerows or flower strips. We altered the sentence to make this clearer (line 215-216).

Line 208: Does this statement need 5 references? (as in the introduction, the reader gets the impression the authors aimed to increase the citation count of other articles here).

We have removed excess references (line 219-221).

Line 222: How many are 'a few'? Maybe state a proportion.

We only found two species, we’ve changed the sentence accordingly (line 232-233).

Line 224: As stated above, I would not overstress the results of the ISAs - the authors stated themselves that the result for A. dorsalis is likely only based on one site ...

We removed this sentence after removing the ISAs.

Line 305: I think there is an additional nested random level missing - the transect or individual plot the traps were located in (or was there only one replicate for each crop/strip in each experiment)? Hard to tell as the authors provide no information on the actual sample sizes.

Indeed, there was one field or plot per cropping system per crop per location per year from which all the samples were taken. Therefore the analysis does not miss a nested random level. We provided information on sample sizes in Table S7.

Line 314ff: The authors describe that they basically followed a (slightly extended) Chao-Hill approach (species richness, Shannon entropy & inverse Simpson) without the sampling effort / sample completeness standardization implemented in this approach and as a reader I wonder why they did not simply just use the customary Chao-Hill approach.

We were not aware of the Chao-Hill approach, and we see it as a compliment that we independently came up with an approach similar to a now accepted approach.

Line 329: Unclear what was nested in what here - location / year / crop or year / location / crop ?

For the crop-level analyses, the nested structure was location > year > crop. This nested structure was chosen as every location was sampled across different years and (for some locations) the crops differed among years. However, as we pooled the samples from the same field in the field-level analyses, using the same random structure would have resulted in each individual sampling unit being distinguished as a group. Therefore, the random structure here was only location > year. We explain this now more clearly in lines 329 and 355-357.

Line 334: I can see why the authors used these distributions but it is presented here without any justification. As a side note: Gamma (with log link) would likely be better for the Shannon model as well (I guess it cannot be 0 or negative ...).

We explain this now better in lines 360-364.

Line 341: Why Hellinger and not simply proportions?

We used Hellinger transformation to give more weight to rarer species. Our pitfall traps were often dominated by large numbers of a few very abundant / active species. If we had used proportions, these species would have dominated the community analyses. We clarified this in the text (line 379-381).

Line 348: An RDA is constrained by the assumptions / model the authors proposed and "forces" the data into a spatial ordination that resembles this model best. As the authors previously used an unconstrained PERMANOVA, it would be better to also use an NMDS that goes along with the PERMANOVA.

The initial goal of the RDA was not to directly visualize the results of the PERMANOVA, but to show whether an overall crop configuration effect occurred, both for the whole dataset and per location. We have now added NMDS figures to link them to the PERMANOVA and added these to the supplementary figures (fig S6-S8). We also mention this approach in the methods section (line 387-390).

Line 355f: This is also a clear indication of the strong annual fluctuations in carabid assemblages as mentioned above.

Indeed.

Line 361: 'pairwise'.

Typo, we changed this.

Line 362: reference missing.

Reference added (line 405)

References

Alarcón-Segura, V., Grass, I., Breustedt, G., Rohlfs, M., Tscharntke, T., 2022. Strip intercropping of wheat and oilseed rape enhances biodiversity and biological pest control in a conventionally managed farm scenario. J. Appl. Ecol. 59, 1513-1523.

Boetzl, F.A., Sponsler, D., Albrecht, M., Batáry, P., Birkhofer, K., Knapp, M., Krauss, J., Maas, B., Martin, E.A., Sirami, C., Sutter, L., Bertrand, C., Baillod, A.B., Bota, G., Bretagnolle, V., Brotons, L., Frank, T., Fusser, M., Giralt, D., González, E., Hof, A.R., Luka, H., Marrec, R., Nash, M.A., Ng, K., Plantegenest, M., Poulin, B., Siriwardena, G.M., Tscharntke, T., Tschumi, M., Vialatte, A., Van Vooren, L., Zubair-Anjum, M., Entling, M.H., Steffan-Dewenter, I., Schirmel, J., 2024. Distance functions of carabids in crop fields depend on functional traits, crop type and adjacent habitat: a synthesis. Proceedings of the Royal Society B: Biological Sciences 291, 20232383.

Hallmann, C.A., Sorg, M., Jongejans, E., Siepel, H., Hofland, N., Schwan, H., Stenmans, W., Müller, A., Sumser, H., Hörren, T., Goulson, D., de Kroon, H., 2017. More than 75 percent decline over 27 years in total flying insect biomass in protected areas. PLoS One 12, e0185809.

Knapp, M., Seidl, M., Knappová, J., Macek, M., Saska, P., 2019. Temporal changes in the spatial distribution of carabid beetles around arable field-woodlot boundaries. Scientific Reports 9, 8967.

Müller, J., Hothorn, T., Yuan, Y., Seibold, S., Mitesser, O., Rothacher, J., Freund, J., Wild, C., Wolz, M., Menzel, A., 2023. Weather explains the decline and rise of insect biomass over 34 years. Nature.

Toivonen, M., Huusela, E., Hyvönen, T., Marjamäki, P., Järvinen, A., Kuussaari, M., 2022. Effects of crop type and production method on arable biodiversity in boreal farmland. Agriculture, Ecosystems & Environment 337, 108061.

Reviewer #3 (Public review):

Summary:

In this paper, the authors made a sincere effort to show the effects of strip cropping, a technique of alternating crops in small strips of several meters wide, on ground beetle diversity. They state that strip cropping can be a useful tool for bending the curve of biodiversity loss in agricultural systems as strip cropping shows a relative increase in species diversity (i.e. abundance and species richness) of the ground beetle communities compared to monocultures. Moreover, strip cropping has the added advantage of not having to compromise on agricultural yields.

Strengths:

The article is well written; it has an easily readable tone of voice without too much jargon or overly complicated sentence structure. Moreover, as far as reviewing the models in depth without raw data and R scripts allows, the statistical work done by the authors looks good. They have well thought out how to handle heterogenous, yet spatially and temporarily correlated field data. The models applied and the model checks performed are appropriate for the data at hand. Combining RDA and PCA axes together is a nice touch.

We thank reviewer 3 for their kind words and appreciation for the simple language and analysis that we used.

Weaknesses:

The evidence for strip cropping bringing added value for biodiversity is mixed at best. Yes, there is an increase in relative abundance and species richness at the field level, but it is not convincingly shown this difference is robust or can be linked to clear structural and hypothesised advantages of the strip cropping system. The same results could have been used to conclude that there are only very limited signs of real added value of strip cropping compared to monocultures.

Point well taken. We agree that the effect of strip cropping on carabid beetle communities are subtle and we nuanced the text in the revised version to reflect this. See below for more details on how we revised the manuscript to reflect this point.

There are a number of reasons for this:

(1) Significant differences disappear at crop level, as the authors themselves clearly acknowledge, meaning that there are no differences between pairs of similar crops in the strip cropping fields and their respective monoculture. This would mean the strips effectively function as "mini-monocultures".

This is indeed in line with our conclusions. Based on our data and results, the advantages of strip cropping seem mostly to occur because crops with different communities are now on the same field, rather than that within the strips you get mixtures of communities related to different crops. We discussed this in the first paragraph of the discussion in the original submission (line 161-164).

The significant relative differences at the field level could be an artifact of aggregation instead of structural differences between strip cropping and monocultures; with enough data points things tend to get significant despite large variance. This should have been elaborated further upon by the authors with additional analyses, designed to find out where differences originate and what it tells about the functioning of the system. Or it should have provided ample reason for cautioning in drawing conclusions about the supposed effectiveness of strip cropping based on these findings.

We believe that this is a misunderstanding of our approach. In the field-level analyses we pooled samples from the same field (i.e. pseudo-replicates were pooled), resulting in a relatively small sample size of 50 samples. We revised the methods section to better explain this (line 318-322). Therefore, the statement “with enough data points things tend to get significant” is not applicable here.

(2) The authors report percentages calculated as relative change of species richness and abundance in strip cropping compared to monocultures after rarefaction. This is in itself correct, however, it can be rather tricky to interpret because the perspective on actual species richness and abundance in the fields and treatments is completely lost; the reported percentages are dimensionless. The authors could have provided the average cumulative number of species and abundance after rarefaction. Also, range and/or standard error would have been useful to provide information as to the scale of differences between treatments. This could provide a new perspective on the magnitude of differences between the two treatments which a dimensionless percentage cannot.

We agree that this would be the preferred approach if we would have had a perfectly balanced dataset. However, this approach is not feasible with our unbalanced design and differences in sampling effort. While we acknowledge the limitation of the interpretation of percentages, it does allow reporting relative changes for each combination of location, year and crop. The number of samples on which the percentages were based were always kept equal (through rarefaction) between the cropping systems (for each combination of location, year and crop), but not among crops, years and location. This approach allowed us to make a better estimation whenever more samples were available, as we did not always have an equal number of samples available between both cropping systems. For example, sometimes we had 2 samples from a strip cropped field and 6 from the monoculture, here we would use rarefaction up to 2 samples (where we would just have a better estimation from the monoculture). In other cases, we had 4 samples in both strip cropped and monoculture fields, and we chose to use rarefaction to 4 samples to get a better estimation altogether. Adding a value for actual richness or abundance to the figures would have distorted these findings, as the variation would be huge (as it would represent the number of ground beetle(s) species per 2 to 6 pitfall samples). Furthermore, the dimension that reviewer 3 describes would thus be “The number of ground beetle species / individuals per 2 to 6 samples”, not a very informative unit either.

(3) The authors appear to not have modelled the abundance of any of the dominant ground beetle species themselves. Therefore it becomes impossible to assess which important species are responsible (if any) for the differences found in activity density between strip cropping and monocultures and the possible life history traits related reasons for the differences, or lack thereof, that are found. A big advantage of using ground beetles is that many life history traits are well studied and these should be used whenever there is reason, as there clearly is in this case. Moreover, it is unclear which species are responsible for the difference in species richness found at the field level. Are these dominant species or singletons? Do the strip cropping fields contain species that are absent in the monoculture fields and are not the cause of random variation or sampling? Unfortunately, the authors do not report on any of these details of the communities that were found, which makes the results much less robust.

Thank you for raising this point. We have reconsidered our indicator species analysis and found that it is rather sensitive for rare species and insensitive to changes in common species. Therefore, we have replaced the indicator species analyses with a GLM analysis for the 12 most common genera of ground beetles in the revised manuscript. This will allow us to go more in depth on specific traits of the genera which abundances change depending on the cropping system. In the revised manuscript, we will also discuss these common genera more in depth, rather than focusing on rarer species (line 135-143, 182-200 in discussion). Furthermore, we have added information on rarity and habitat preference to the table that shows species abundances per location (Table S2), and mention these aspects briefly in the results (line 145-153).

(4) In the discussion they conclude that there is only a limited amount of interstrip movement by ground beetles. Otherwise, the results of the crop-level statistical tests would have shown significant deviation from corresponding monocultures. This is a clear indication that the strips function more like mini-monocultures instead of being more than the sum of its parts.

This is in line with our point in the first paragraph of the discussion and an important message of our manuscript.

(5) The RDA results show a modelled variable of differences in community composition between strip cropping and monoculture. Percentages of explained variation of the first RDA axis are extremely low, and even then, the effect of location and/or year appear to peak through (Figure S3), even though these are not part of the modelling. Moreover, there is no indication of clustering of strip cropping on the RDA axis, or in fact on the first principal component axis in the larger RDA models. This means the explanatory power of different treatments is also extremely low. The crop level RDA's show some clustering, but hardly any consistent pattern in either communities of crops or species correlations, indicating that differences between strip cropping and monocultures are very small.

We agree and we make a similar point in the first paragraph of the discussion (line 160-162).

Furthermore, there are a number of additional weaknesses in the paper that should be addressed:

The introduction lacks focus on the issues at hand. Too much space is taken up by facts on insect decline and land sharing vs. land sparing and not enough attention is spent on the scientific discussion underlying the statements made about crop diversification as a restoration strategy. They are simply stated as facts or as hypotheses with many references that are not mentioned or linked to in the text. An explicit link to the results found in the large number of references should be provided.

We revised the introduction by omitting the land sharing vs. land sparing topic and better linking references to our research findings.

The mechanistic understanding of strip cropping is what is at stake here. Does strip cropping behave similarly to intercropping, a technique that has been proven to be beneficial to biodiversity because of added effects due to increased resource efficiency and greater plant species richness? This should be the main testing point and agenda of strip cropping. Do the biodiversity benefits that have been shown for intercropping also work in strip cropping fields? The ground beetles are one way to test this. Hypotheses should originate from this and should be stated clearly and mechanistically.

We agree with the reviewer and clarified this research direction clearer in the introduction of the revised manuscript (line 66-72).

One could question how useful indicator species analysis (ISA) is for a study in which predominantly highly eurytopic species are found. These are by definition uncritical of their habitat. Is there any mechanistic hypothesis underlying a suspected difference to be found in preferences for either strip cropping or monocultures of the species that were expected to be caught? In other words, did the authors have any a priori reasons to suspect differences, or has this been an exploratory exercise from which unexplained significant results should be used with great caution?

Point well taken. We agree that the indicator species analysis has limitations and therefore now replaced this with GLM analysis for the 12 most common ground beetle genera.

However, setting these objections aside there are in fact significant results with strong species associations both with monocultures and strip cropping. Unfortunately, the authors do not dig deeper into the patterns found a posteriori either. Why would some species associate so strongly with strip cropping? Do these species show a pattern of pitfall catches that deviate from other species, in that they are found in a wide range of strips with different crops in one strip cropping field and therefore may benefit from an increased abundance of food or shelter? Also, why would so many species associate with monocultures? Is this in any way logical? Could it be an artifact of the data instead of a meaningful pattern? Unfortunately, the authors do not progress along these lines in the methods and discussion at all.

We thank reviewer 3 for these valuable perspectives. In the revised manuscript, we further explored the species/genera that respond to cropping systems and discuss these findings in more detail in the revised manuscript (line 182-200 in discussion).

A second question raised in the introduction is whether the arable fields that form part of this study contain rare species. Unfortunately, the authors do not elaborate further on this. Do they expect rare species to be more prevalent in the strip cropping fields? Why? Has it been shown elsewhere that intercropping provides room for additional rare species?

The answer is simply no, we did not find more rare species in strip cropping. In the revised manuscript, we added a column for rarity (according to waarneming.nl) in the table showing abundances of species per location (table S2). We only found two rare species, one of which we only found a single individual and one that was more related to the open habitat created by a failed wheat field. We discuss this more in depth in the revised results (line 145-153).

Considering the implications the results of this research can have on the wider discussion of bending the curve and the effects of agroecological measures, bold claims should be made with extreme restraint and be based on extensive proof and robust findings. I am not convinced by the evidence provided in this article that the claim made by the authors that strip cropping is a useful tool for bending the curve of biodiversity loss is warranted.

We believe that strip cropping can be a useful tool because farmers readily adopt it and it can result in modest biodiversity gains without yield loss. However, strip cropping is indeed not a silver bullet (which we also don’t claim). We nuanced the implications of our study in the revised manuscript (line 30-35, 232-237).

Reviewer #3 (Recommendations for the authors):

General comments:

(1) I am missing the R script and data files in the manuscript. This is a serious drawback in assessing the quality of the work.

Datasets and R scripts will be made available upon completion of the manuscript.

(2) I have doubts about the clarity of the title. It more or less states that strip cropping is designed in order to maintain productivity. However, the main objective of strip cropping is to achieve ecological goals without losing productivity. I suggest a rethink of the title and what it is the authors want to convey.

As the title lead to false expectations for multiple reviewers regarding analyses on yield, we chose to alter the title and removed any mention of yield in the title.

(3) Line 22: I would add something along the lines of: "As an alternative to intercropping, strip cropping is pioneerd by Dutch farmers... " This makes the distinction and the connection between the two more clear.

In our opinion, strip cropping is a form of intercropping. We have changed this sentence to reflect this point better. (line 21-22)

(4) Line 24: "these" should read "they"

After changing this sentence, this typo is no longer there (line 24).

(5) Line 34-48. I think this introduction is too long. The paper is not directly about insect decline, so the authors could consider starting with line 43 and summarising 34-42 in one or two sentences.

Removed a sentence on insect declines here to make the introduction more streamlined.

(6) Line 51-59. I am not convinced the land sparing - land sharing idea adds anything to the paper. It is not used in the discussion and solicits much discussion in and of itself unnecessary in this paper. The point the authors want to make is not arable fields compared to natural biodiversity, but with increases in biodiversity in an already heavily degraded ecosystem; intensive agriculture. I think the introduction should focus on that narrative, instead of the land sparing-sharing dichotomy, especially because too little attention is spent on this narrative.

We removed the section on land-sparing vs land-sharing as it was indeed off-topic.

(7) Line 85. Dynamics is not correctly used here. It should read Ground beetle communities are sensitive.

Changed accordingly (line 78-79).

(8) Line 90-91. Here, it should be added that ground beetles are used as indicators for ground-dwelling insect diversity, not wider insect diversity in agricultural systems. In fact, Gerlach et al., the reference included, clearly warn against using indicator groups in a context that is too wide for a single indicator group to cover and Van Klink (2022) has recently shown in a meta-analysis that the correlation between trends in insect groups is often rather poor.

We removed the sentence that claimed ground beetles to be indicators of general biodiversity, and have focused the text in general more on ground beetle biodiversity, rather than general biodiversity.

(9) Line 178: was there a high weed abundance measured in the stripcropping fields? Or has there been reports on higher weed abundance in general? The references provided do not appear to support this claim.

To our knowledge, there is only one paper on the effect of strip cropping on weeds (Ditzler et al., 2023). This paper shows strip cropping (and more diverse cropping systems) reduce weed cover, but increase weed richness and diversity. We mistakenly mentioned that crop diversification increases weed seed biomass, but have changed this accordingly to weed seed richness. The paper from Carbonne et al. (2022) indeed doesn’t show an effect of crop diversification on weeds. However, it does show a positive relation between weed seed richness and ground beetle activity density. We have moved this citation to the right place in the sentence (line 172-175).

(10) Line 279-288. The description of sampling with pitfalls is inadequate. Please follow the guidelines for properly incorporating sufficient detail on pitfall sampling protocols as described in Brown & Matthews 2016,

We were sadly not aware of this paper prior to the experiments, but have at least added information on all characteristics of the pitfall traps as mentioned in the paper (line 290-294).

(11) Lines 307-310. What reasoning lies behind the choice to focus on the most beetle-rich monocultures? Do the authors have references for this way of comparing treatments? Is there much variation in the monocultures that solicits this approach? It would be preferable if the authors could elaborate on why this method is used, provide references that it is a generally accepted statistical technique and provide additional assesments of the variation in the data so it can be properly related to more familiar exploratory data analysis techniques.

We ran two analyses for the field-level richness and abundance. First we used all combinations of monocultures and strip cropping. However, as strip cropping is made up of (at least) 2 crops, we had 2 constituent monocultures. As we would count a comparison with the same strip cropped field twice when we included both monocultures, we also chose to run the analyses again with only those monocultures that had the highest richness and abundance. This choice was done to get a conservative estimate of ground beetle richness increases through strip cropping. We explained this methodology further in the statistical analysis section (line 329-335).

In Figure S6 the order of crop combinations is altered between 2021 on the left and 2022 on the right. This is not helpful to discover any possible patterns.

We originally chose this order as it represented also the crop rotations, but it is indeed not helpful without that context. Therefore, we chose to change the order to have the same crop combinations within the rows.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Recent work has demonstrated that the hummingbird hawkmoth, Macroglossum stellatarum, like many other flying insects, use ventrolateral optic flow cues for flight control. However, unlike other flying insects, the same stimulus presented in the dorsal visual field, elicits a directional response. Bigge et al., use behavioral flight experiments to set these two pathways in conflict in order to understand whether these two pathways (ventrolateral and dorsal) work together to direct flight and if so, how. The authors characterize the visual environment (the amount of contrast and translational optic flow) of the hawkmoth and find that different regions of the visual field are matched to relevant visual cues in their natural environment and that the integration of the two pathways reflects a prioritization for generating behavior that supports hawkmoth safety rather than the prevalence for a particular visual cue that is more prevalent in the environment.

Strengths:

This study creatively utilizes previous findings that the hawkmoth partitions their visual field as a way to examine parallel processing. The behavioral assay is well-established and the authors take the extra steps to characterize the visual ecology of the hawkmoth habitat to draw exciting conclusions about the hierarchy of each pathway as it contributes to flight control.

Reviewer #2 (Public review):

Summary

Bigge and colleagues use a sophisticated free-flight setup to study visuo-motor responses elicited in different parts of the visual field in the hummingbird hawkmoth. Hawkmoths have been previously shown to rely on translational optic flow information for flight control exclusively in the ventral and lateral parts of their visual field. Dorsally presented patterns, elicit a formerly completely unknown response - instead of using dorsal patterns to maintain straight flight paths, hawkmoths fly, more often, in a direction aligned with the main axis of the pattern presented (Bigge et al, 2021). Here, the authors go further and put ventral/lateral and dorsal visual cues into conflict. They found that the different visuomotor pathways act in parallel, and they identified a 'hierarchy': the avoidance of dorsal patterns had the strongest weight and optic flow-based speed regulation the lowest weight. The authors linked their behavioral results to visual scene statistics in the hawkmoths' natural environment. The partition of ventral and dorsal visuomotor pathways is well in line with differences in visual cue frequencies. The response hierarchy, however, seems to be dominated by dorsal features, that are less frequent, but presumably highly relevant for the animals' flight safety.

Strengths

The data are very interesting and unique. The manuscript provides a thorough analysis of free-flight behavior in a non-model organism that is extremely interesting for comparative reasons (and on its own). These data are both difficult to obtain and very valuable to the field.

Weaknesses

While the present manuscript clearly goes beyond Bigge et al, 2021, the advance could have perhaps been even stronger with a more fine-grained investigation of the visual responses in the dorsal visual field. Do hawkmoths, for example, show optomotor responses to rotational optic flow in the dorsal visual field?

I find the majority of the data, which are also the data supporting the main claims of the paper, compelling. However, the measurements of flight height are less solid than the rest and I think these data should be interpreted more carefully.

Reviewer #3 (Public review):

The authors have significantly improved the paper in revising to make its contributions distinct from their prior paper. They have also responded to my concerns about quantification and parameter dependency of the integration conclusion. While I think there is still more that could be done in this capacity, especially in terms of the temporal statistics and quantification of the conflict responses, they have a made a case for the conclusions as stated. The paper still stands as an important paper with solid evidence a bit limited by these concerns.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The edits have significantly improved the clarity of the manuscript. A few small notes:

Figure 2B legend - describe what the orange dashed line represents

We added a description.

Figure 2B legend - references Table 1 but I believe this should reference Table S1. There are other places in the manuscript where Table 1 is referenced and it should reference S1

We changed this for all instances in the main paper and supplement, where the reference was wrong.

Figure S1 legend - some figure panel letters are in parentheses while others are not

We unified the notation to not use parentheses for any of the panel letters.

Reviewer #2 (Recommendations for the authors):

I couldn't find the l, r, d, v indications in Fig. 1a. This was just a suggestion, but since you wrote you added them, I was wondering if this is the old figure version.

We added them to what is now Fig. 2, which was originally part of Fig. 1. After restructuring, we did indeed not add an additional set to Fig. 1, which we have now adjusted.

Fig. 2: Adding 'optic flow' and 'edges' to the y-axis in panels E and F, would make it faster for me to parse the figure. Maybe also add the units for the magnitudes? Same for Figure 6B

We added 'optic flow' and 'edges' to the panels E and F in Fig. 2 and Fig. 6.

Fig. 2: Very minor - could you use the same pictograms in D and E&F (i.e. all circles for example, instead of switching to "tunnels" in EF)?

We used the tunnel pictograms, because we associated those with the short notations for the different conditions summarised in Table S1. Because we wanted to keep this consistent across the paper, we used the “tunnel” pictograms here too.

In the manuscript, you still draw lots of conclusions based on these area measurements (L132-142, L204-209 etc). This does not fully reflect what you wrote in your reply to the reviewers. If you think of these measurements as qualitative rather than quantitative, I would say so in the manuscript and not use quantitative statistics etc. My suggestion would be to be more specific about potential issues that can influence the measurement (you mentioned body size, image contrast, motion blur, pitch across conditions etc) and give that data not the same weight as the rest of the measurements.

We do express explicit caution with this measure in the methods section (l. 657-659) and the results section (l. 135-137). Nevertheless, as the trends in the data are consistent with optic flow responses in the other planes, and with responses reported in the literature, we felt that it is valuable to report the data, as well as the statistics for all readers, who can – given out cautionary statement – assess the data accordingly.

The area measurements suggest that moths fly lower with unilateral vertical gratings (Fig. S1, G1 and G2 versus the rest). If you leave the data in can you speculate why that would be? (Sorry if I missed that)

We agree, this seems quite consistent, but we do not have a good explanation for this observation. It would certainly require some additional experiments and variable conditions to understand what causes this phenomenon.

Fig.4 - is panel B somehow flipped? Shouldn't the flight paths start out further away from the grating and then be moved closer to midline (as in A). That plot shows the opposite.

Absolutely right, thank you for spotting this, it was indeed an intermediate and not the final figure which was uploaded to the manuscript. It also had outdated letter-number identifiers, which we now updated.

L198 - should be "they avoided"